the nurse comes telling the couple that lady capulet is approaching as romeo is desending the windows juliet had a vision of romeo looking like a corpse

Reviewer #1 (Public review):

Summary:

This manuscript follows up previous work from this group using a conditional TCF4 mouse where Cre-expression turns "on" expression of TCF4 to investigate whether postnatal re-expression of TCF4 is effective to correct phenotypes related to Pitt-Hopkins Syndrome (PTHS) in humans. Results may inform gene therapy human PTHS gene therapy efforts on effective developmental windows for gene therapy. The authors demonstrate that re-expression of TCF4, induced by retro-orbital (RO) AAV-PHP.eB-Cre, during 2-4th postnatal week, does not rescue brain or body weight, anxiety-like or nest-building behaviors, but rescues an object location memory task, a measure of cognition. These results are novel and interesting in that they reveal distinct developmental roles for TCF4 in distinct behaviors and suggest that TCF4 plays a role in the mature brain in hippocampal and memory-related plasticity. Results may inform gene therapy design in PTHS.

Strengths:

The results are rigorous and high quality. Multiple methods are used to assess AAV-mediated re-expression of Cre, reactivation of TCF4, and the developmental time course of expression. Multiple behavioral phenotypes and molecular rescue are assessed. Most behavioral phenotypes are reproducible and robust, and it is clear whether a rescue was observed.

Weaknesses:

(1) Although the authors demonstrate the time course and spatial extent of Cre and a Cre-reporter (TdTom) in the brain with the AAV-Cre, it is unclear how many cells are transduced. Similarly, the authors do not measure TCF4 levels with immunohistochemistry or western blot. So the level of protein reactivation is unknown. A possible reason the rescue is incomplete is that the TCF4 protein is not induced in a large % of neurons in specific brain regions that mediate specific behaviors, such as the hippocampus vs. the striatum.

(2) The authors perform bulk qPCR to demonstrate a 20% increase in TCF4 RNA with Cre-mediated activation. It is unclear why the full gene reactivation is not observed. An alternative interpretation of the incomplete rescue of the phenotypes is that full TCF4 expression is required at later developmental time points.

This argument can definitely be backed by my own prior experiences. Whether it’s Gone Home or other similar games that I've played and seen–some with horror and mystery aspects–I never truly explored the environments simply for the sake of exploring my surroundings. Rather, I was always driven by a sense of curiosity to unfold the mysteries surrounding my character and the others around me.

Reviewer #2 (Public review):

Summary and overall evaluation:

The authors assessed how visual discrimination of stimuli in the foveola changes before, during, and after small instructed eye movements (in the "micro" range). Consistent with (and advancing) related prior work, their main finding regards a pre-saccadic modulation of visual performance at the saccade target vs. the opposite location. This pre-saccadic modulation in foveal vision peaks ~70 ms prior to the instructed small saccade.

Strengths:

The study uses an impressive, technically advanced set-up and zooms in on peri-saccadic modulations in visual acuity at the micro scale. The findings build on related prior findings from the literature on smaller and larger eye movements and add temporal granularity over prior work from the same lab. The writing is easy to follow, and the figures are clear.

Weaknesses:

At the same time, the findings remain relatively empirical in nature and do not profoundly advance theoretical understanding beyond adding valuable granularity to existing knowledge. Relevant prior literature could be better introduced and acknowledged. In addition, there remain concerns regarding potential cue-driven attentional influences that may confound the reported effects (leaving the possibility that the reported effects may be related to cue-driven attention, rather than saccade planning/execution per se). There are also some issues regarding specific statistical inferences. I detail these points below.

Major Points:

(1) Novelty framing and introduction of relevant prior literature

At times, this study is introduced as if no prior study explored the time course of changes in visual perception surrounding small (micro) saccades. Yet, it appears that a prior study from the same lab, using a very similar task, already showed a time course (Figure 5 in Shelchkova & Poletti, 2020). While this study is discussed in the introduction, it is not mentioned that at least some pre-saccade time course was already reported there, albeit a more crude one than the one in the current article. Moreover, the 2013 study by Hafed also specifically looked at "peri-microsaccade modulation in visual perception" and also already showed a temporal modulation that peaked ~50 ms before microsaccade onset. I appreciate how the current study differs in a number of ways (focusing on visual acuity in the foveola), but I was nevertheless surprised to see the first reference to this relevant prior finding in the discussion (and without any elaboration). Though more recent, the same could be argued for the 2025 study by Bouhnik et al. on pre-microsaccade modulations in visual processing in V1, which, like the Hafed study, is first mentioned only in the discussion. Perhaps these studies could be introduced in the paragraph starting at line 48, or in the next paragraph, to do better justice to the existing literature on this topic when motivating the study. This would likely also help to better point out the major advances provided by the current study.

Relatedly, in Shelchkova & Poletti (PNAS, 2020), an apparently similar congruency effect on performance was reported >200 ms milliseconds before saccade onset, as evident from Fig 5 in that article. How should readers rhyme this with the current findings? Ideally, the authors would not only acknowledge that such a time course was already reported previously, but also discuss the discrepancies between these findings further: why may the performance effects appear much earlier in this prior study compared to in the current study, where the congruency effect emerges only ~100 ms prior to the instructed small saccade?

(2) Saccade- or cue-driven? (assumption that attention is unaltered in failed saccade trials)

Because the authors used a cue to instruct saccade direction, it remains a possibility that the reported modulations in visual performance may be driven directly by the spatial cue (cue-related attentional allocation), rather than the instructed small saccade per se. While the authors are clearly aware of this potential confound, questions remain regarding the convincingness of the presented control analyses. In my view, a more compelling control would require an additional experiment.

The central argument against a cue-locked (purely attentional) modulation is the absence of a performance modulation in so-called "failed" saccade trials. However, a key assumption here is that putative cue-driven attention was unaltered in these trials. This is never verified and, in my opinion, highly unlikely. Rather, trials with failed microsaccades could very well be the result of failing to process the cue in the first place (indeed, if the task is to make a saccade to the cue, failure to make a saccade equates failure to perform the task). In such trials, any putative cue-driven influences over spatial attention would also be expected to be substantially reduced. Accordingly, just because failed saccade trials show little performance modulation does not rule out cue-driven attention effects, because attention may also have "failed" in these failed saccade trials. The control for potential cue-driven attention effects would be more convincing if the authors included a condition with the same cues, where participants are simply not instructed to make any saccades to the cues. Unfortunately, such an experimental condition appears not to have been included here. The author may still consider adding such a control experiment.

Another argument against a cue-driven effect is that the authors found no interaction with time in the cue-locked data, whereas they did find such an interaction in the saccade-locked data. However, the lack of significance in the cue-locked data but significance in the saccade-locked data is not strong evidence against a cue-driven influence. Statistically, there is no direct comparison here, and more importantly, with longer delays, the cue-locked data may also start to show a dip (this could potentially be tested by the authors if they have enough trials available to extend their cue-locked analysis further in time). Indeed, exogenous attention, that may have been automatically evoked by the spatial cue, is known to be transient and to eventually even reverse after a brief initial facilitation (see e.g., Klein TiCS, 2000).

Finally, the authors consistently refer to "endogenous" attention (starting at line 221) when addressing potential cue-driven attention confounds. However, because the cue is not predictive, but is a spatial cue that differs in a bottom-up manner between left and right cues, "exogenous" attention is a more likely confound here in my view. Specifically, the spatial cue may automatically trigger attention in the direction of the target location it points to (and such exogenous effects would be expected even for unpredictive cues).

(3) Benefit and cost, or just cost?

Line 151 states that no statistically significant benefit for the saccade target was found compared to the neutral baseline. Yet, the claim throughout the article is distinct, such as in line 159: "These results show that approximately 100 milliseconds before microsaccade onset, discrimination rapidly improved at the intended target location". I do not question the robustness of the congruency effect, but the authors should be more careful when inferring "improved" perception at the target location because, as far as I could tell (as well as in the authors' own writing in line 151), this is not substantiated statistically when compared to the neutral baseline.

Related to this point, in Figure 3B, it would be informative to also see the average performance in the neutral cue condition (for example, as a straight line as in some other figures). This would help to better appreciate the relative benefits and/or costs compared to the neutral condition, also in the time-resolved data.

(4) Statistical inference for the comparison between failed and non-failed trials

Currently, the lack of modulation in the failed saccade trials hinges on a null effect. It would be stronger to support the claims with a significant difference in the congruency effect between failed and non-failed trials. Indeed, lack of significance in failed saccade trials does by itself not constitute valid evidence that the congruency effect is larger in saccade compared to failed saccade trials. For this, a significant interaction between saccade-trial-type (failed/non-failed) and congruency (congruent/incongruent) should be established (see e.g., Nieuwenhuis et al., Nat Neurosci, 2011).

(5) Time window justification

While the authors nicely depict their data across the full time axis, all statistics are currently performed on data extracted from specific time windows. How exactly were these time windows determined and justified? Likewise, how were the specific times picked for visualizing and statistically quantifying the data in e.g., Figures 3D and E? It would be reassuring to add justification for these specific time windows and/or to verify (using follow-up analyses) that the presented results are robust when different time windows are chosen.

(6) Microsaccade definition

Microsaccades are explicitly defined as being below half a degree. This appears rather arbitrary and rigid. Does the size of saccades not ultimately depend on the task and stimulus (e.g., Otero-Millan et al., PNAS, 2013) rather than being a fixed biological property? Perhaps this could be stated less rigidly, such as by stating how microsaccades are often observed below 0.5 degrees.

(Relatedly, one may wonder whether the type of instructed saccades that the authors studied here involves the same type of eye movements as the type of fixational microsaccades that have been the focus of ample prior studies. However, I recognize that this specific reflection may open a debate that is beyond the scope of this article.

Reviewer #1 (Public review):

Summary:

Jeay-Bizot and colleagues investigate the neural correlates of the preparation of, and commitment to, a self-initiated motor action. In their introduction, they differentiate between theoretical proposals relating to the timing of such neural correlates relative to the time of a recorded motor action (e.g., a keypress). These are categorised into 'early' and 'late' timing accounts. The authors advocate for 'late' accounts based on several arguments that align well with contemporary models of decision-making in other domains (for example, evidence accumulation models applied to perceptual decisions). They also clearly describe prevalent methodological issues related to the measurement of event-related potentials (ERPs) and time-frequency power to gauge the timing of the commitment to making a motor action. These methodological insights are communicated clearly and denote potentially important limitations on the inferences that can be drawn from a large body of existing work.

To attempt to account for such methodological concerns, the authors devise an innovative experiment that includes an experimental condition whereby participants make a motor action (a right-hand keypress) to make an image disappear. They also include a condition whereby the stimulus presentation program automatically proceeds at a set time that is matched to the response timing in a previous trial. In this latter condition, no motor action is required by the participant. The authors then attempt to determine the times at which they can differentiate between these two conditions (motor action vs no motor action) based on EEG and MEG data, using event-related potential analyses, time-frequency analyses, and multivariate classifiers. They also apply analysis techniques based on comparing M/EEG amplitudes at different time windows (as used in previous work) to compare these results to those of their key analyses.

When using multivariate classifiers to discriminate between conditions, they observed very high classification performance at around -100ms from the time of the motor response or computer-initiated image transition, but lower classification performance and a lack of statistically significant effects across analyses for earlier time points. Based on this, they make the key claim that measured M/EEG responses at the earlier time points (i.e., earlier than around -100ms from the motor action) do not reliably correlate with the execution of a motor action (as opposed to no such action being prepared or made). This is argued to favour 'late' accounts of motor action commitment, aligning with the well-made theoretical arguments in favour of these accounts in the introduction. Although the exact time window related to 'late' accounts is not concretely specified, an effect that occurs around -100ms from response onset is assumed here to fall within that window.

Importantly, this claim relies on accepting the null hypothesis of zero effect for the time points preceding around -100ms based on a somewhat small sample of n=15 and some additional analyses of individual participant datasets. Although the authors argue that their classifiers are sensitive to detecting relevant effects, and the study appears well-powered to detect the (likely to be large magnitude) M/EEG signal differences occurring around the time of the response or computer-initiated image transition, there is no guarantee that the study is adequately sensitive to detect earlier differences in M/EEG signals. These earlier effects are likely to be more subtle and exhibit lower signal-to-noise ratios, but would still be relevant to the 'early' vs 'late' debate framed in the manuscript. This, along with some observed patterns in the data, may substantially reduce the confidence one may have in the key claim about the onset timing of M/EEG signal differences.

Notably, there is some indication of above-chance (above 0.5 AUC) classification performance at time points earlier than -100ms from the response, as visible in Figure 3A for the task-based EEG analyses (EEG OC dataset, blue line). While this was not statistically significantly above chance for their n=15 sample, these results do not appear to be clear evidence in favour of a zero-effect null-hypothesis. In Figures 2A-B, there are also visible differences in the ERPs across conditions, from around the time that motor action-related components have been previously observed (around -500ms from the response). The plotted standard errors in the data are large enough to indicate that the study may not have been adequately powered to differentiate between the conditions.

Although the authors acknowledge this limitation in the discussion section of their manuscript, their counter-argument is that the classifiers could reliably differentiate between conditions at time points very close to the motor response, and in the time-based analyses where substantive confounds are likely to be present, as demonstrated in a set of analyses. Based on this data, the authors imply that the study is sufficiently powered to detect effects across the range of time points used in the analyses. While it's commendable that these extra analyses were run, they do not provide convincing evidence that the study is necessarily sensitive to detecting more subtle effects that may occur at earlier time points. In other words, the ability of classifiers (or other analysis methods) to detect what are likely to be very prominent, large effects around the time of the motor response does not guarantee that such analyses will detect smaller magnitude effects at other time points.

In summary, the authors develop some very important lines of argument for why existing work may have misestimated the timing of neural signals that precede motor actions. This in itself is an important contribution to the field. However, their attempt to better estimate the timing of such signals is limited by a reliance on accepting the null hypothesis based on non-statistically significant results, and arguably a limited degree of sensitivity to detect subtle but meaningful effects.

Strengths:

This manuscript provides compelling reasons why existing studies may have misestimated the timing of the neural correlates of motor action preparation and execution. They provide additional analyses as evidence of the relevant confounds and provide simulations to back up their claims. This will be important to consider for many in the field. They also endeavoured to collect large numbers of trials per participant to also examine effects in individuals, which is commendable and arguably better aligned with contemporary theory (which pertains to how individuals make decisions to act, rather than groups of people).

The innovative control condition in their experiment may also be very useful for providing complementary evidence that can better characterise the neural correlates of motor action preparation and commitment. The method for matching image durations across active and passive conditions is particularly well thought-out and provides a nice control for a range of potential confounding factors.

Weaknesses:

There is a mismatch between the stated theoretical phenomenon of interest (commitment to making a motor action) and what is actually tested in the study (differences in neural responses when an action is prepared and made compared to when no action is required). The assumed link between these concepts could be made more explicit for readers, particularly because it is argued in the manuscript that neural correlates of motor action preparation are not necessarily correlates of motor action commitment.

As mentioned in the summary, the main issue is the strong reliance on accepting the null hypothesis of no differences between motor action and computer initiation conditions based on a lack of statistically significant results from the modest (n=15) sample. Although a larger sample will increase measurement precision at the group level, there are some EEG data processing changes that could increase the signal-to-noise ratio of the analysed data and produce more precise estimates of effects, which may improve the ability to detect more subtle effects, or at least provide more confidence in the claims of null effects.

First, it is stated in the EEG acquisition and preprocessing section that the 64-channel Biosemi EEG data were recorded with a common average reference applied. Unless some non-standard acquisition software was used (of which we are not aware exists), Biosemi systems do not actually apply this reference at recording (it is for display purposes only, but often mistaken to be the actual reference applied). As stated in the Biosemi online documentation, a reference should be subsequently applied offline; otherwise, there is a substantial decrease in the signal-to-noise ratio of the EEG data, and a large portion of ambient alternating current noise is retained in the recordings. This can be easily fixed by applying a referencing scheme (e.g., the common average reference) offline as one of the first steps of data processing. If this was, in fact, done offline, it should be clearly communicated in the manuscript.

In addition, the data is downsampled using a non-integer divisor of the original sampling rate (a 2,048 Hz dataset is downsampled to 500 Hz rather than 512 Hz). Downsampling using a non-integer divisor is not recommended and can lead to substantial artefacts in raw data as a result, as personally observed by this Reviewer in Biosemi data. Finally, although a 30 Hz low-pass filter is applied for visualisation purposes of ERPs, no such filter is applied prior to analyses, and no method is used to account for alternating current noise that is likely to be in the data. As noted above, much of the alternating current noise will be retained when an offline reference is not applied, and this is likely to further degrade the quality of the data and reduce one's ability to identify subtle patterns in EEG signals. Changes in data processing to address these issues would likely lead to more precise estimates of EEG signals (and by extension differences across conditions).

With regard to possible effects extending hundreds of milliseconds before the response, it would be helpful for the authors to more precisely clarify the time windows associated with 'early' and 'late' theories in this case. The EEG data that would be required to support 'early' theories is also not made sufficiently clear. For example, even quite early neural correlates of motor actions in this task (e.g., around -500ms from the response, or earlier) could still be taken as evidence for the 'late' theories if these correlates simply reflect the accumulation of evidence toward making a decision and associated motor action, as implied by the Leaky Stochastic Accumulator model described by the authors. In other words, even observations of neural correlates of motor action preparation that occur much earlier than the response would not constitute clear evidence against the 'late' account if this neural activity represents an antecedent to a decision and action (rather than commitment to the action), as the authors point out in the introduction.

In addition, there is some discrepancy regarding the data that is used by the classifiers to differentiate between the conditions in the EEG data and the claims about the timing of neural responses that differentiate between conditions. Unless we reviewers are mistaken, the Sliding Window section of the methods states that the AUC scores in Figure 3 are based on windows of EEG data that extend from the plotted time point until 0.5 seconds into the past. In other words, an AUC value at -100ms from the response is based on classifiers applied to data ranging from -600 to -100 milliseconds relative to the response. In this case, the range of data used by the classifiers extends much earlier than the time points indicated by Figure 3, and it is difficult to know whether the data at these earlier time points may have contributed (even in subtle ways) to the success of the classifiers. This may undermine the claim that neural responses only become differentiable from around -100ms from response onset. The spans of these windows used for classification could be made more explicit in Figure 3, and classification windows that are narrower could be included in a subset of analyses to ensure that classifiers only using data in a narrow window around the response show the high degree of classification performance in the dataset. If we are mistaken, then perhaps these details could be clarified in the method and results sections.

id = identité et href = hypertext reference.

Pour faire le dièse sur Windows: Alt GR + touche 3 du clavier central.

Si on mets une étiquette "Fr" mais que c'est écrit avec un alphabet bizarre que personne ne peut lire, l'étiquette ne sert à rien. Enregistrer en UTF-8, c'est choisir le bon alphabet au moment de cliquer sur "Enregistrer".

L'encodage est un réglage de l'éditeur de texte (VS Code, Sublime Text, Notepad++, etc.).

Dans VS Code : Tout en bas à droite de la fenêtre, dans la barre bleue. C'est écrit "UTF-8". Si c'est écrit"Windows-1252" ou "Western", c'est qu'il y a un blème !

Par Les "é" deviennent des é

Si les accents bugguent malgré la balise meta :

Ouvrir le fichier dans l'éditeur.

Cliquer sur l'encodage en bas à droite (souvent "UTF-8" ou "Win1252"). "Save with Encoding" (Enregistrer avec l'encodage).

Sélectionner UTF-8.

Guide de Référence Solidatech : Solutions Numériques pour les Associations

Synthèse Opérationnelle

Solidatech est un programme de solidarité numérique créé en 2008, porté par les Ateliers du Bocage, une coopérative d'utilité sociale membre d'Emmaüs. Sa mission principale est de renforcer l'impact des associations, fondations et fonds de dotation par le biais du numérique.

Le programme repose sur deux piliers stratégiques : permettre aux structures de réaliser des économies significatives sur leurs équipements (logiciels et matériel) et les accompagner dans leur montée en compétences.

Avec plus de 45 000 structures accompagnées, Solidatech s'impose comme un intermédiaire clé entre le secteur technologique et le monde associatif.

Le programme traverse actuellement une phase de transition importante suite à la fin de son partenariat historique avec le réseau international TechSoup, entraînant une restructuration interne et une autonomisation de son catalogue de solutions.

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1. Identité et Gouvernance de Solidatech

L'organisation se distingue par son ancrage dans l'économie sociale et solidaire (ESS).

• Structure porteuse : Les Ateliers du Bocage, une entreprise d'insertion et entreprise adaptée située dans les Deux-Sèvres (79).

• Affiliation : Membre du mouvement Emmaüs.

• Écosystème : Accompagne environ 45 000 associations, fonds de dotation et fondations reconnues d'utilité publique.

• Accessibilité : L'inscription au programme est entièrement gratuite pour les structures éligibles.

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2. Le Pilier Économique : Équipements et Logiciels

Solidatech facilite l'accès à des ressources technologiques à tarifs préférentiels via une boutique en ligne dédiée.

Solutions Logicielles

Le catalogue est en cours de reconstruction pour privilégier des solutions françaises, sécurisées et, de plus en plus, issues du logiciel libre.

• Domaines couverts : Travail collaboratif, communication, sécurité informatique, comptabilité et gestion.

• Modèle tarifaire : Les associations s'acquittent d'un coupon (frais de gestion) auprès de Solidatech pour obtenir des remises importantes (souvent 30 % à 50 %) sur les abonnements annuels ou mensuels des partenaires.

• Exemples d'offres : AssoConnect (gestion associative), Kaspersky (sécurité).

Matériel Informatique

Le matériel est majoritairement reconditionné en France, au sein des Ateliers du Bocage.

• Gamme "Les Cabossés" : Une offre spécifique de matériel présentant des défauts esthétiques mineurs (rayures) mais parfaitement fonctionnel, proposée à des tarifs encore plus réduits.

• Diversité des équipements : Ordinateurs portables, unités centrales, écrans, tablettes, smartphones et accessoires.

• Garantie : Tout le matériel est garanti 1 an, avec une option d'extension d'un an supplémentaire.

• Systèmes d'exploitation : Possibilité d'équiper les machines avec Windows, Linux (dont PrimTux pour les enfants) ou ChromeOS Flex.

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3. Le Pilier Compétences : Formation et Accompagnement

Au-delà de l'équipement, Solidatech propose un écosystème de services pour professionnaliser les usages numériques.

Formation Professionnelle

• Certification : Organisme certifié Qualiopi, permettant le financement des formations via les crédits OPCO (équivalent du CPF pour les structures employeuses).

• Thématiques : Intelligence Artificielle (IA), Canva, Microsoft 365, RGPD, communication digitale et outils de travail collaboratif.

Accompagnement et Diagnostic

• Diagnostic Numérique : Un outil gratuit d'auto-évaluation basé sur sept piliers de maturité numérique pour identifier les priorités d'action.

• Services de Migration : Aide au passage vers des environnements Cloud (Microsoft 365, Google Workspace) pour sécuriser les données et favoriser la collaboration.

• Prestatech : Une plateforme répertoriant des prestataires de confiance sélectionnés par Solidatech, pratiquant souvent des tarifs solidaires pour les associations.

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4. Évolutions Stratégiques et Changements Structurels

Le paysage opérationnel de Solidatech a été modifié de manière significative à la fin de l'année 2023.

| Aspect | Ancienne Situation | Situation Actuelle (Post-31/12/2023) | | --- | --- | --- | | Partenariat majeur | TechSoup Global (depuis 2008) | Fin du partenariat (décision de TechSoup) | | Support utilisateur | Équipe support interne dédiée | Suppression de l'équipe support (6 départs) | | Gestion des licences | Centralisée via TechSoup | Directe via les partenaires ou le nouveau catalogue Solidatech | | Catalogue | Partagé internationalement | Catalogue autonome en cours de repeuplement |

Conséquence pour les utilisateurs : Pour les licences historiques acquises via TechSoup (ex: anciennes licences Microsoft ou Adobe), les associations doivent désormais s'adresser directement à TechSoup Europe (basé en Pologne) ou aux éditeurs concernés, Solidatech n'ayant plus accès aux données de ces anciens comptes.

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5. Ressources et Pilotage de la Maturité Numérique

Solidatech produit et diffuse des connaissances pour éclairer le secteur associatif.

• Étude Nationale : Publication triennale de l'enquête "La place du numérique dans le projet associatif" (5ème édition disponible), coproduite avec Recherches & Solidarités.

• Centre de Ressources : Articles conseils, replays de webinaires et guides pratiques (ex: alternatives libres à la suite Adobe).

• Veille et Information : Une newsletter mensuelle et des webinaires réguliers (format court d'une heure) sur des enjeux d'actualité comme LinkedIn ou l'IA.

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6. Modalités Pratiques d'Inscription

Pour bénéficier des services, une structure doit suivre un processus simple :

1. Inscription sur solidatech.fr : Nécessite le téléchargement des documents officiels de l'association.

2. Création de compte boutique : Une étape unique pour accéder au catalogue matériel et logiciel.

3. Mise à jour des contacts : Il est recommandé de renseigner plusieurs contacts pour assurer la continuité des échanges malgré le turn-over associatif.

Solidatech encourage activement les associations à faire remonter leurs besoins spécifiques via des questionnaires pour orienter les futurs partenariats du catalogue en reconstruction.

Reviewer #1 (Public review):

Summary:

This manuscript by Lin et al. presents a timely, technically strong study that builds patient-specific midbrain-like organoids (MLOs) from hiPSCs carrying clinically relevant GBA1 mutations (L444P/P415R and L444P/RecNcil). The authors comprehensively characterize nGD phenotypes (GCase deficiency, GluCer/GluSph accumulation, altered transcriptome, impaired dopaminergic differentiation), perform CRISPR correction to produce an isogenic line, and test three therapeutic modalities (SapC-DOPS-fGCase nanoparticles, AAV9-GBA1, and SRT with GZ452). The model and multi-arm therapeutic evaluation are important advances with clear translational value.

My overall recommendation is that the work undergo a major revision to address the experimental and interpretive gaps listed below.

Strengths:

(1) Human, patient-specific midbrain model: Use of clinically relevant compound heterozygous GBA1 alleles (L444P/P415R and L444P/RecNcil) makes the model highly relevant to human nGD and captures patient genetic context that mouse models often miss.

(2) Robust multi-level phenotyping: Biochemical (GCase activity), lipidomic (GluCer/GluSph by UHPLC-MS/MS), molecular (bulk RNA-seq), and histological (TH/FOXA2, LAMP1, LC3) characterization are thorough and complementary.

(3) Use of isogenic CRISPR correction: Generating an isogenic line (WT/P415R) and demonstrating partial rescue strengthens causal inference that the GBA1 mutation drives many observed phenotypes.

(4) Parallel therapeutic testing in the same human platform: Comparing enzyme delivery (SapC-DOPS-fGCase), gene therapy (AAV9-GBA1), and substrate reduction (GZ452) within the same MLO system is an elegant demonstration of the platform's utility for preclinical evaluation.

(5) Good methodological transparency: Detailed protocols for MLO generation, editing, lipidomics, and assays allow reproducibility

Weaknesses:

(1) Limited genetic and biological replication

(a) Single primary disease line for core mechanistic claims. Most mechanistic data derive from GD2-1260 (L444P/P415R); GD2-10-257 (L444P/RecNcil) appears mainly in therapeutic experiments. Relying primarily on one patient line risks conflating patient-specific variation with general nGD mechanisms.

(b) Unclear biological replicate strategy. It is not always explicit how many independent differentiations and organoid batches were used (biological replicates vs. technical fields of view).

(c) A significant disadvantage of employing brain organoids is the heterogeneity during induction and potential low reproducibility. In this study, it is unclear how many independent differentiation batches were evaluated and, for each test (for example, immunofluorescent stain and bulk RNA-seq), how many organoids from each group were used. Please add a statement accordingly and show replicates to verify consistency in the supplementary data.

(d) Isogenic correction is partial. The corrected line is WT/P415R (single-allele correction); residual P415R complicates the interpretation of "full" rescue and leaves open whether the remaining pathology is due to incomplete correction or clonal/epigenetic effects.

(e) The authors tested week 3, 4, 8, 15, and 28 old organoids in different settings. However, systematic markers of maturation should be analyzed, and different maturation stages should be compared, for example, comparing week 8 organoids to week 28 organoids, with immunofluorescent marker staining and bulk RNAseq.

(f) The manuscript frequently refers to Wnt signaling dysregulation as a major finding. However, experimental validation is limited to transcriptomic data. Functional tests, such as the use of Wnt agonist/inhibitor, are needed to support this claim (see below).

(g) Suggested fixes/experiments

Add at least one more independent disease hiPSC line (or show expanded analysis from GD2-10-257) for key mechanistic endpoints (lipid accumulation, transcriptomics, DA markers)

Generate and analyze a fully corrected isogenic WT/WT clone (or a P415R-only line) if feasible; at minimum, acknowledge this limitation more explicitly and soften claims.

Report and increase independent differentiations (N = biological replicates) and present per-differentiation summary statistics.

(2) Mechanistic validation is insufficient

(a) RNA-seq pathways (Wnt, mTOR, lysosome) are not functionally probed. The manuscript shows pathway enrichment and some protein markers (p-4E-BP1) but lacks perturbation/rescue experiments to link these pathways causally to the DA phenotype.

(b) Autophagy analysis lacks flux assays. LC3-II and LAMP1 are informative, but without flux assays (e.g., bafilomycin A1 or chloroquine), one cannot distinguish increased autophagosome formation from decreased clearance.

(c) Dopaminergic dysfunction is superficially assessed. Dopamine in the medium and TH protein are shown, but no neuronal electrophysiology, synaptic marker co-localization, or viability measures are provided to demonstrate functional recovery after therapy.

(d) Suggested fixes/experiments

Perform targeted functional assays:

(i) Wnt reporter assays (TOP/FOP flash) and/or treat organoids with Wnt agonists/antagonists to test whether Wnt modulation rescues DA differentiation.

(ii)Test mTOR pathway causality using mTOR inhibitors (e.g., rapamycin) or 4E-BP1 perturbation and assay effects on DA markers and autophagy.

Include autophagy flux assessment (LC3 turnover with bafilomycin), and measure cathepsin activity where relevant.

Add at least one functional neuronal readout: calcium imaging, MEA recordings, or synaptic marker quantification (e.g., SYN1, PSD95) together with TH colocalization.

(3) Therapeutic evaluation needs greater depth and standardization

(a) Short windows and limited durability data. SapC-DOPS and AAV9 experiments range from 48 hours to 3 weeks; longer follow-up is needed to assess durability and whether biochemical rescue translates into restored neuronal function.

(b) Dose-response and biodistribution are under-characterized. AAV injection sites/volumes are described, but transduction efficiency, vg copies per organoid, cell-type tropism quantification, and SapC-DOPS penetration/distribution are not rigorously quantified.

(c) Specificity controls are missing. For SapC-DOPS, inclusion of a non-functional enzyme control (or heat-inactivated fGCase) would rule out non-specific nanoparticle effects. For AAV, assessment of off-target expression and potential cytotoxicity is needed.

(d) Comparative efficacy lacking. It remains unclear which modality is most effective in the long term and in which cellular compartments.

(e) Suggested fixes/experiments

Extend follow-up (e.g., 6+ weeks) after AAV/SapC dosing and evaluate DA markers, electrophysiology, and lipid levels over time.

Quantify AAV transduction by qPCR for vector genomes and by cell-type quantification of GFP+ cells (neurons vs astrocytes vs progenitors).

Include SapC-DOPS control nanoparticles loaded with an inert protein and/or fluorescent cargo quantitation to show distribution and uptake kinetics.

Provide head-to-head comparative graphs (activity, lipid clearance, DA restoration, and durability) with statistical tests.

(4) Model limitations not fully accounted for in interpretation

(a) Absence of microglia and vasculature limits recapitulation of neuroinflammatory responses and drug penetration, both of which are important in nGD. These absences could explain incomplete phenotypic rescues and must be emphasized when drawing conclusions about therapeutic translation.

(b) Developmental vs degenerative phenotype conflation. Many phenotypes appear during differentiation (patterning defects). The manuscript sometimes interprets these as degenerative mechanisms; the distinction must be clarified.

(c) Suggested fixes

Tone down the language throughout (Abstract/Results/Discussion) to avoid overstatement that MLOs fully recapitulate nGD neuropathology.

Add plans or pilot data (if available) for microglia incorporation or vascularization to indicate how future work will address these gaps.

(5) Statistical and presentation issues

(a) Missing or unclear sample sizes (n). For organoid-level assays, report the number of organoids and the number of independent differentiations.

(b) Statistical assumptions not justified. Tests assume normality; where sample sizes are small, consider non-parametric tests and report exact p-values.

(c) Quantification scope. Many image quantifications appear to be from selected fields of view, which are then averaged across organoids and differentiations.

(d) RNA-seq QC and deposition. Provide mapping rates, batch correction details, and ensure the GEO accession is active. Include these in Methods/Supplement.

(e) Suggested fixes

Add a table summarizing biological replicates, technical replicates, and statistical tests used for each figure panel.

Recompute statistics where appropriate (non-parametric if N is small) and report effect sizes and confidence intervals.

(6) Minor comments and clarifications

(a) The authors should validate midbrain identity further with additional regional markers (EN1, OTX2) and show absence/low expression of forebrain markers (FOXG1) across replicates.

(b) Extracellular dopamine ELISA should be complemented with intracellular dopamine or TH+ neuron counts normalized per organoid or per total neurons.

(c) For CRISPR editing: the authors should report off-target analysis (GUIDE-seq or targeted sequencing of predicted off-targets) or at least in-silico off-target score and sequencing coverage of the edited locus.

(d) It should be clarified as to whether lipidomics normalization is to total protein per organoid or per cell, and include representative LC-MS chromatograms or method QC.

(e) Figure legends should be improved in order to state the number of organoids, the number of differentiations, and the exact statistical tests used (including multiple-comparison corrections).

(f) In the title, the authors state "reveal disease mechanisms", but the studies mainly exhibit functional changes. They should consider toning down the statement.

(7) Recommendations

This reviewer recommends a major revision. The manuscript presents substantial novelty and strong potential impact but requires additional experimental validation and clearer, more conservative interpretation. Key items to address are:

(a) Strengthening genetic and biological replication (additional lines or replicate differentiations).

(b) Adding functional mechanistic validation for major pathways (Wnt/mTOR/autophagy) and providing autophagy flux data.

(c) Including at least one neuronal functional readout (calcium imaging/MEA/patch) to demonstrate functional rescue.

(d) Deepening therapeutic characterization (dose, biodistribution, durability) and including specificity controls.

(e) Improving statistical reporting and explicitly stating biological replicate structure.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript by Lin et al. presents a timely, technically strong study that builds patientspecific midbrain-like organoids (MLOs) from hiPSCs carrying clinically relevant GBA1 mutations (L444P/P415R and L444P/RecNcil). The authors comprehensively characterize nGD phenotypes (GCase deficiency, GluCer/GluSph accumulation, altered transcriptome, impaired dopaminergic differentiation), perform CRISPR correction to produce an isogenic line, and test three therapeutic modalities (SapC-DOPS-fGCase nanoparticles, AAV9GBA1, and SRT with GZ452). The model and multi-arm therapeutic evaluation are important advances with clear translational value.

My overall recommendation is that the work undergo a major revision to address the experimental and interpretive gaps listed below.

Strengths:

(1) Human, patient-specific midbrain model: Use of clinically relevant compound heterozygous GBA1 alleles (L444P/P415R and L444P/RecNcil) makes the model highly relevant to human nGD and captures patient genetic context that mouse models often miss.

(2) Robust multi-level phenotyping: Biochemical (GCase activity), lipidomic (GluCer/GluSph by UHPLC-MS/MS), molecular (bulk RNA-seq), and histological (TH/FOXA2, LAMP1, LC3) characterization are thorough and complementary.

(3) Use of isogenic CRISPR correction: Generating an isogenic line (WT/P415R) and demonstrating partial rescue strengthens causal inference that the GBA1 mutation drives many observed phenotypes.

(4) Parallel therapeutic testing in the same human platform: Comparing enzyme delivery (SapC-DOPS-fGCase), gene therapy (AAV9-GBA1), and substrate reduction (GZ452) within the same MLO system is an elegant demonstration of the platform's utility for preclinical evaluation.

(5) Good methodological transparency: Detailed protocols for MLO generation, editing, lipidomics, and assays allow reproducibility

Weaknesses:

(1) Limited genetic and biological replication

(a) Single primary disease line for core mechanistic claims. Most mechanistic data derive from GD2-1260 (L444P/P415R); GD2-10-257 (L444P/RecNcil) appears mainly in therapeutic experiments. Relying primarily on one patient line risks conflating patient-specific variation with general nGD mechanisms.

We thank the reviewer for highlighting the importance of genetic and biological replication. An additional patient-derived iPSC line was included in the manuscript, therefore, our study includes two independent nGD patient-derived iPSC lines, GD2-1260 (GBA1^L444P/P415R) and GD2-10-257 (GBA1^{L444P/RecNcil}), both of which carry the severe mutations associated with nGD. These two lines represent distinct genetic backgrounds and were used to demonstrate the consistency of key disease phenotypes (reduced GCase activity, elevated substrate, impaired dopaminergic neuron differentiation, etc.) across different patient’s MLOs. Major experiments (e.g., GCase activity assays, substrate, immunoblotting for DA marker TH, and therapeutic testing with SapC-DOPS-fGCase, AAV9-GBA1) were performed using both patient lines, with results showing consistent phenotypes and therapeutic responses (see Figs. 2-6, and Supplementary Figs. 4-5). To ensure clarity and transparency, a new Supplementary Table 2 summarizes the characterization of both the GD2-1260 and GD2-10-257 lines.

(b) Unclear biological replicate strategy. It is not always explicit how many independent differentiations and organoid batches were used (biological replicates vs. technical fields of view).

Biological replication was ensured in our study by conducting experiments in at least 3 independent differentiations per line, and technical replicates (multiple organoids/fields per batch) were averaged accordingly. We have clarified biological replicates and differentiation in the figure legends. 

(c) A significant disadvantage of employing brain organoids is the heterogeneity during induction and potential low reproducibility. In this study, it is unclear how many independent differentiation batches were evaluated and, for each test (for example, immunofluorescent stain and bulk RNA-seq), how many organoids from each group were used. Please add a statement accordingly and show replicates to verify consistency in the supplementary data.

In the revision, we have clarified biological replicates and differentiation in the figure legend in Fig.1E; Fig.2B,2G; Fig.3F, 3G; Fig.4B-C,E,H-J, M-N; Fig.6D; and Fig.7A-C, I.

(d) Isogenic correction is partial. The corrected line is WT/P415R (single-allele correction); residual P415R complicates the interpretation of "full" rescue and leaves open whether the remaining pathology is due to incomplete correction or clonal/epigenetic effects.

We attempted to generate an isogenic iPSC line by correcting both GBA1 mutations (L444P and P415R). However, this was not feasible because GBA1 overlaps with a highly homologous pseudogene (PGBA), which makes precise editing technically challenging. Consequently, only the L444P mutation was successfully corrected, and the resulting isogenic line retains the P415R mutation in a heterozygous state. Because Gaucher disease is an autosomal recessive disorder, individuals carrying a single GBA1 mutation (heterozygous carriers) do not develop clinical symptoms. Therefore, the partially corrected isogenic line, which retains only the P415R allele, represents a clinically relevant carrier model. Consistent with this, our results show that GCase activity was restored to approximately 50% of wild-type levels (Fig.4B-C), supporting the expected heterozygous state. These findings also make it unlikely that the remaining differences observed are due to clonal variation or epigenetic effects.

(e) The authors tested week 3, 4, 8, 15, and 28 old organoids in different settings. However, systematic markers of maturation should be analyzed, and different maturation stages should be compared, for example, comparing week 8 organoids to week 28 organoids, with immunofluorescent marker staining and bulk RNAseq.

We agree that a systematic analysis of maturation stages is essential for validating the MLO model. Our data integrated a longitudinal comparison across multiple developmental windows (Weeks 3 to 28) to characterize the transition from progenitors to mature/functional states for nGD phenotyping and evaluation of therapeutic modalities: 1) DA differentiation (Wks 3 and 8 in Fig. 3): qPCR analysis demonstrated the progression of DA-specific programs. We observed a steady increase in the mature DA neuron marker TH and ASCL1. This was accompanied by a gradual decrease in early floor plate/progenitor markers FOXA2 and PLZF, indicating a successful differentiation path from progenitors to differentiated/mature DA neurons. 2) Glycosphingolipid substrates accumulation (Wks 15 and 28 in Fig 2): To assess late-stage nGD phenotyping, we compared GluCer and GluSph at Week 15 and Week 28. This comparison highlights the progressive accumulation of substrates in nGD MLOs, reflecting the metabolic consequences of the disease at different mature stage. 3) Organoid growth dynamics (Wks 4, 8, and 15 in new Fig. 4): The new Fig. 4 tracks physical maturation through organoid size and growth rates across three key time points, providing a macro-scale verification of consistent development between WT and nGD groups. By comparing these early (Wk 3-8) and late (Wk 15-28) stages, we confirmed that our MLOs transition from a proliferative state to a post-mitotic, specialized neuronal state, satisfied the requirement for comparing distinct maturation stages.

(f) The manuscript frequently refers to Wnt signaling dysregulation as a major finding. However, experimental validation is limited to transcriptomic data. Functional tests, such as the use of Wnt agonist/inhibitor, are needed to support this claim (see below).

We agree that the suggested experiments could provide additional mechanistic insights into this study and will consider them in future work.

(g) Suggested fixes / experiments

Add at least one more independent disease hiPSC line (or show expanded analysis from GD2-10-257) for key mechanistic endpoints (lipid accumulation, transcriptomics, DA markers).

Additional line iPSC GD2-10-257 derived MLO was included in the manuscript. This was addressed above [see response to Weaknesses (1)-a]. 

Generate and analyze a fully corrected isogenic WT/WT clone (or a P415R-only line) if feasible; at minimum, acknowledge this limitation more explicitly and soften claims.

We attempted to generate an isogenic iPSC line by correcting both GBA1 mutations (L444P and P415R). However, this was unsuccessful because the GBA1 gene overlaps with a pseudogene (PGBA) located 16 kb downstream of GBA1, which shares 96-98% sequence similarity with GBA1 (Ref#1, #2), which complicates precise editing. GBA1 is shorter (~5.7 kb) than PGBA (~7.6 kb). The primary exonic difference between GBA1 and PGBA is a 55-bp deletion in exon 9 of the pseudogene. As a result, the isogenic line we obtained carries only the P415R mutation, and L444P was corrected to the normal sequence. We have included this limitation in the Methods as “This gene editing strategy is expected to also target the GBA1 pseudogene due to the identical target sequence, which limits the gene correction on certain mutations (e.g., P415R)”. 

References:

(1) Horowitz M., Wilder S., Horowitz Z., Reiner O., Gelbart T., Beutler E. The human glucocerebrosidase gene and pseudogene: structure and evolution. Genomics (1989). 4, 87–96. doi:10.1016/0888-7543(89)90319-4

(2) Woo EG, Tayebi N, Sidransky E. Next-Generation Sequencing Analysis of GBA1: The Challenge of Detecting Complex Recombinant Alleles. Front Genet. (2021). 12:684067. doi:10.3389/fgene.2021.684067. PMCID: PMC8255797.

Report and increase independent differentiations (N = biological replicates) and present per-differentiation summary statistics.

This was addressed above [see response to Weaknesses (1)-b, (1)-c]. 

(2) Mechanistic validation is insufficient

(a) RNA-seq pathways (Wnt, mTOR, lysosome) are not functionally probed. The manuscript shows pathway enrichment and some protein markers (p-4E-BP1) but lacks perturbation/rescue experiments to link these pathways causally to the DA phenotype.

(b) Autophagy analysis lacks flux assays. LC3-II and LAMP1 are informative, but without flux assays (e.g., bafilomycin A1 or chloroquine), one cannot distinguish increased autophagosome formation from decreased clearance.

(c) Dopaminergic dysfunction is superficially assessed. Dopamine in the medium and TH protein are shown, but no neuronal electrophysiology, synaptic marker co-localization, or viability measures are provided to demonstrate functional recovery after therapy.

(d) Suggested fixes/experiments

Perform targeted functional assays:

(i) Wnt reporter assays (TOP/FOP flash) and/or treat organoids with Wnt agonists/antagonists to test whether Wnt modulation rescues DA differentiation.

(ii) Test mTOR pathway causality using mTOR inhibitors (e.g., rapamycin) or 4E-BP1 perturbation and assay effects on DA markers and autophagy.

Include autophagy flux assessment (LC3 turnover with bafilomycin), and measure cathepsin activity where relevant.

Add at least one functional neuronal readout: calcium imaging, MEA recordings, or synaptic marker quantification (e.g., SYN1, PSD95) together with TH colocalization.

We thank the reviewer for these valuable suggestions. We agree that the suggested experiments could provide additional mechanistic insights into this study and will consider them in future work. Importantly, the primary conclusions of our manuscript, that GBA1 mutations in nGD MLOs resulted in nGD pathologies such as diminished enzymatic function, accumulation of lipid substrates, widespread transcriptomic changes, and impaired dopaminergic neuron differentiation, which can be corrected by several therapeutic strategies in this study, are supported by the evidence presented. The suggested experiments represent an important direction for future research using brain organoids.

(3) Therapeutic evaluation needs greater depth and standardization

(a) Short windows and limited durability data. SapC-DOPS and AAV9 experiments range from 48 hours to 3 weeks; longer follow-up is needed to assess durability and whether biochemical rescue translates into restored neuronal function.

We agree with the reviewer. Because this is a proof-of-principle study, the treatment was designed within a short time window. Long-term studies with more comprehensive outcome assessments will be conducted in future work.

(b) Dose-response and biodistribution are under-characterized. AAV injection sites/volumes are described, but transduction efficiency, vg copies per organoid, cell-type tropism quantification, and SapC-DOPS penetration/distribution are not rigorously quantified.

We appreciate the reviewer’s concerns. This study was intended to demonstrate the feasibility and initial response of MLOs to AAV therapy. A comprehensive evaluation of AAV biodistribution will be considered in future studies.

The penetration and distribution of SapC-DOPS have been extensively characterized in prior studies. In vivo biodistribution of SapC–DOPS coupled CellVue Maroon, a fluorescent cargo, was examined in mice bearing human tumor xenografts using real-time fluorescence imaging, where CellVue Maroon fluorescence in tumor remained for 48 hours (Ref. #3: Fig. 4B, mouse 1), 100 hours (Ref. #4: Fig. 5), up to 216 hours (Ref. #5: Fig. 3). Uptake kinetics were also demonstrated in cells, with flow cytometry quantification showing that fluorescent cargo coupled SapC-DOPS nanovesicles, were incorporated into human brain tumor cell membranes within minutes and remained stably incorporated into the cells for up to one hour (Ref. # 6: Fig. 1a and Fig. 1b). Building on these findings, the present study focuses on evaluating the restoration of GCase function rather than reexamining biodistribution and uptake kinetics.

References:

(3) X. Qi, Z. Chu, Y.Y. Mahller, K.F. Stringer, D.P. Witte, T.P. Cripe. Cancer-selective targeting and cytotoxicity by liposomal-coupled lysosomal saposin C protein. Clin. Cancer Res. (2009) 15, 5840-5851. PMID: 19737950.

(4) Z. Chu, S. Abu-Baker, M.B. Palascak, S.A. Ahmad, R.S. Franco, and X. Qi. Targeting and cytotoxicity of SapC-DOPS nanovesicles in pancreatic cancer. PLOS ONE (2013) 8, e75507. PMID: 24124494.

(5) Z. Chu, K. LaSance, V.M. Blanco, C.-H. Kwon, B., Kaur, M., Frederick, S., Thornton, L., Lemen, and X. Qi. Multi-angle rotational optical imaging of brain tumors and arthritis using fluorescent SapC-DOPS nanovesicles. J. Vis. Exp. (2014) 87, e51187, 17. PMID: 24837630.

(6) J. Wojton, Z. Chu, C-H. Kwon, L.M.L. Chow, M. Palascak, R. Franco, T. Bourdeau, S. Thornton, B. Kaur, and X. Qi. Systemic delivery of SapC-DOPS has antiangiogenic and antitumor effects against glioblastoma. Mol. Ther. (2013) 21, 1517-1525. PMID: 23732993.

(c) Specificity controls are missing. For SapC-DOPS, inclusion of a non-functional enzyme control (or heat-inactivated fGCase) would rule out non-specific nanoparticle effects. For AAV, assessment of off-target expression and potential cytotoxicity is needed.

Including inactive fGCase would confound the assessment of fGCase in MLOs by immunoblot and immunofluorescence; therefore, saposin C–DOPS was used as the control instead. 

We agree that assessment of Off-target expression and potential cytotoxicity for AAV is important; this will be included in future studies.

(d) Comparative efficacy lacking. It remains unclear which modality is most effective in the long term and in which cellular compartments.

To address this comment, we have added a new table (Supplementary Table 2) comparing the four therapeutic modalities and summarizing their respective outcomes. While this study focused on short-term responses as a proof-of-principle, future work will explore long-term therapeutic effects. 

(e) Suggested fixes/experiments

Extend follow-up (e.g., 6+ weeks) after AAV/SapC dosing and evaluate DA markers, electrophysiology, and lipid levels over time.

We appreciate the reviewer’s suggestions. The therapeutic testing in patient-derived MLOs was designed as a proof-of-principle study to demonstrate feasibility and the primary response (rescue of GCase function) to the treatment. A comprehensive, long-term therapeutic evaluation of AAV and SapC-DOPS-fGCase is indeed important for a complete assessment; however, this represents a separate therapeutic study and is beyond the scope of the current work.

Quantify AAV transduction by qPCR for vector genomes and by cell-type quantification of GFP+ cells (neurons vs astrocytes vs progenitors).

For the AAV-treated experiments, we agree that measuring AAV copy number and GFP expression would provide additional information. However, the primary goal of this study was to demonstrate the key therapeutic outcome, rescue of GCase function by AAV-delivered normal GCase, which is directly relevant to the treatment objective.

Include SapC-DOPS control nanoparticles loaded with an inert protein and/or fluorescent cargo quantitation to show distribution and uptake kinetics.

As noted above [see response to Weakness (3)-c], using inert GCase would confound the assessment of fGCase uptake in MLOs; therefore, it was not suitable for this study. See response above for the distribution and uptake kinetics of SapC-DOPS [see response to Weaknesses (3)-b].

Provide head-to-head comparative graphs (activity, lipid clearance, DA restoration, and durability) with statistical tests.

We have added a new table (Supplementary Table 2) providing a head-to-head comparison of the treatment effects. 

(4) Model limitations not fully accounted for in interpretation

(a) Absence of microglia and vasculature limits recapitulation of neuroinflammatory responses and drug penetration, both of which are important in nGD. These absences could explain incomplete phenotypic rescues and must be emphasized when drawing conclusions about therapeutic translation.

We agree that the absence of microglia and vasculature in midbrain-like organoids represents a limitation, as we have discussed in the manuscript. In this revision, we highlighted this limitation in the Discussion section and clarified that it may contribute to incomplete phenotyping and phenotypic rescue observed in our therapeutic experiments. Additionally, we have outlined future directions to incorporate microglia and vascularization into the organoid system to better recapitulate the in vivo environment and improve translational relevance (see 7th paragraph in the Discussion).

(b) Developmental vs degenerative phenotype conflation. Many phenotypes appear during differentiation (patterning defects). The manuscript sometimes interprets these as degenerative mechanisms; the distinction must be clarified.

We appreciate the reviewer’s comments. In the revised manuscript, we have clarified that certain abnormalities, such as patterning defects observed during early differentiation, likely reflect developmental consequences of GBA1 mutations rather than degenerative processes. Conversely, phenotypes such as substrate accumulation, lysosomal dysfunction, and impaired dopaminergic maturation at later stages are interpreted as degenerative features. We have updated the Results and Discussion sections to avoid conflating developmental defects with neurodegenerative mechanisms.

(c) Suggested fixes

Tone down the language throughout (Abstract/Results/Discussion) to avoid overstatement that MLOs fully recapitulate nGD neuropathology.

The manuscript has been revised to avoid overstatements.

Add plans or pilot data (if available) for microglia incorporation or vascularization to indicate how future work will address these gaps.

The manuscript now includes further plans to address the incorporation of microglia and vascularization, described in the last two paragraphs in the Discussion. Pilot study of microglia incorporation will be reported when it is completed.

(5) Statistical and presentation issues

(a) Missing or unclear sample sizes (n). For organoid-level assays, report the number of organoids and the number of independent differentiations.

We have clarified biological replicates and differentiation in the figure legend [see response to Weaknesses (1)-b, (1)-c]. 

(b) Statistical assumptions not justified. Tests assume normality; where sample sizes are small, consider non-parametric tests and report exact p-values.

We have updated Statistical analysis in the methods as described below:

“For comparisons between two groups, data were analyzed using unpaired two-tailed Student’s t-tests when the sample size was ≥6 per group and normality was confirmed by the Shapiro-Wilk test. When the normality assumption was not met or when sample sizes were small (n < 6), the non-parametric Mann-Whitney U test was used instead. For comparisons involving three or more groups, one-way ANOVA followed by Tukey’s multiple comparison test was applied when data were normally distributed; otherwise, the nonparametric Dunn’s multiple comparison test was used. Exclusion of outliers was made based on cut-offs of the mean ±2 standard deviations. All statistical analyses were performed using GraphPad Prism 10 software. Exact p-values are reported throughout the manuscript and figures where feasible. A p-value < 0.05 was considered statistically significant.”

(c) Quantification scope. Many image quantifications appear to be from selected fields of view, which are then averaged across organoids and differentiations.

In this work, quantitative immunofluorescence analyses (e.g., cell counts for FOXP1+, FOXG1+, SOX2+ and Ki67+ cells, as well as marker colocalization) were performed on at least 3–5 randomly selected non-overlapping fields of view (FOVs) per organoid section, with a minimum of 3 organoids per differentiation batch. Each FOV was imaged at consistent magnification (60x) and z-stack depth to ensure comparable sampling across conditions. Data from individual FOVs were first averaged within each organoid to obtain an organoid-level mean, and then biological replicates (independent differentiations, n ≥ 3) were averaged to generate the final group mean ± SEM. This multilevel averaging approach minimizes bias from regional heterogeneity within organoids and accounts for variability across differentiations. Representative confocal images shown in the figures were selected to accurately reflect the quantified data. We believe this standardized quantification strategy ensures robust and reproducible results while appropriately representing the 3D architecture of the organoids.

In the revision, we have clarified the method used for image analysis of sectioned MLOs as below:

“Quantitative immunofluorescence analyses (e.g., cell counts for FOXP1+, FOXG1+, SOX2+ and Ki67+ cells, as well as marker colocalization) were performed using ImageJ (NIH) on at least 3–5 randomly selected non-overlapping fields of view (FOVs) per organoid section, with a minimum of 3 organoids per differentiation batch. Each FOV was imaged at consistent magnification (60x) and z-stack depth to ensure comparable sampling across conditions. Data from individual FOVs were first averaged within each organoid to obtain an organoid-level mean, and then biological replicates (independent differentiations, n ≥ 3) were averaged to generate the final group mean ± SEM.”

(d) RNA-seq QC and deposition. Provide mapping rates, batch correction details, and ensure the GEO accession is active. Include these in Methods/Supplement.

RNA-seq data are from the same batch. The mapping rate is >90%. GEO accession will be active upon publication. These were included in the Methods.

(e) Suggested fixes

Add a table summarizing biological replicates, technical replicates, and statistical tests used for each figure panel.

We have revised the figure legends to include replicates for each figure and statistical tests [see response in weaknesses (1)-b, (1)-c].

Recompute statistics where appropriate (non-parametric if N is small) and report effect sizes and confidence intervals.

Statistical analysis method is provided in the revision [see response in Weaknesses (5)-b].

(6) Minor comments and clarifications

(a) The authors should validate midbrain identity further with additional regional markers (EN1, OTX2) and show absence/low expression of forebrain markers (FOXG1) across replicates.

We validated the MLO identity by 1) FOXG1 and 2) EN1. FOXG1 was barely detectable in Wk8 75.1_MLO but highly present in ‘age-matched’ cerebral organoid (CO), suggesting our culturing method is midbrain region-oriented. In nGD MLO, FOXG1 expression is significantly higher than 75.1_MLO, indicating that there was aberrant anterior-posterior brain specification, consistent with the transcriptomic dysregulation observed in our RNA-seq data.

To further confirm midbrain identity, we examined the expression of EN1, an established midbrain-specific marker. Quantitative RT-PCR analysis demonstrated that EN1 expression increased progressively during differentiation in both WT-75.1 and nGD2-1260 MLOs at weeks 3 and 8 (Author response image 1). EN1 reached 34-fold and 373-fold higher levels than in WT-75.1 iPSCs at weeks 3 and 8, respectively, in WT-75.1 MLOs. In nGD MLOs, although EN1 expression showed a modest reduction at week 8, the levels were not significantly different from those observed in age-matched WT-75.1 MLOs (p > 0.05, ns).

Author response image 1.

qRT-PCR quantification of midbrain progenitor marker EN1 expression in WT-75.1 and GD2-1260 MLOs at Wk3 and Wk8. Data was normalized to WT-75.1 hiPSC cells and presented as mean ± SEM (n = 3-4 MLOs per group).ns, not significant.<br />

(b) Extracellular dopamine ELISA should be complemented with intracellular dopamine or TH+ neuron counts normalized per organoid or per total neurons.

We quantified TH expression at both the mRNA level (Fig. 3F) and the protein level (Fig. 3G/H) from whole-organoid lysates, which provides a more consistent and integrative measure across samples. These TH expression levels correlated well with the corresponding extracellular (medium) dopamine concentrations for each genotype. In contrast, TH⁺ neuron counts may not reliably reflect total cellular dopamine levels because the number of cells captured on each organoid section varies substantially, making normalization difficult. Measuring intracellular dopamine is an alternative approach that will be considered in future studies.

(c) For CRISPR editing: the authors should report off-target analysis (GUIDE-seq or targeted sequencing of predicted off-targets) or at least in-silico off-target score and sequencing coverage of the edited locus. (off-target analysis (GUIDE-seq or targeted sequencing of predicted off-targets) or at least in-silico off-target score and sequencing coverage of the edited locus). 

The off-target effect was analyzed during gene editing and the chance to target other off-targets is low due to low off-target scores ranked based on the MIT Specificity Score analysis. The related method was also updated as stated below:

“The chance to target other Off-targets is low due to low Off-target scores ranked based on the MIT Specificity Score analysis (Hsu, P., Scott, D., Weinstein, J. et al. DNA targeting specificity of RNA-guided Cas9 nucleases. Nat Biotechnol 31, 827–832 (2013).https://doi.org/10.1038/nbt.2647).”

(d) It should be clarified as to whether lipidomics normalization is to total protein per organoid or per cell, and include representative LC-MS chromatograms or method QC.

The normalization was to the protein of the organoid lysate. This was clarified in the Methods section in the revision as stated below:

“The GluCer and GluSph levels in MLO were normalized to total MLO protein (mg) that were used for glycosphingolipid analyses. Protein mass was determined by BCA assay and glycosphingolipid was expressed as pmol/mg protein. Additionally, GluSph levels in the culture medium were quantified and normalized to the medium volume (pmol/mL).”

Representative LC-MS chromatograms for both normal and GD MLOs have been included in a new figure, Supplementary Figure 2.

(e) Figure legends should be improved in order to state the number of organoids, the number of differentiations, and the exact statistical tests used (including multiplecomparison corrections).

This was addressed above [see response to Weaknesses (1)-b and (5)-b].

(f) In the title, the authors state "reveal disease mechanisms", but the studies mainly exhibit functional changes. They should consider toning down the statement.

The title was revised to: Patient-Specific Midbrain Organoids with CRISPR Correction Recapitulate Neuronopathic Gaucher Disease Phenotypes and Enable Evaluation of Novel Therapies

(7) Recommendations

This reviewer recommends a major revision. The manuscript presents substantial novelty and strong potential impact but requires additional experimental validation and clearer, more conservative interpretation. Key items to address are:

(a) Strengthening genetic and biological replication (additional lines or replicate differentiations).

This was addressed above [see response to Weaknesses (1)-a, (1)-b, (1)-c].

(b) Adding functional mechanistic validation for major pathways (Wnt/mTOR/autophagy) and providing autophagy flux data.

(c) Including at least one neuronal functional readout (calcium imaging/MEA/patch) to demonstrate functional rescue.

As addressed above [see response to Weaknesses (2)], the suggested experiments in b) and c) would provide additional insights into this study and we will consider them in future work. 

(d) Deepening therapeutic characterization (dose, biodistribution, durability) and including specificity controls.

This was addressed above [see response to Weaknesses (3)-a to e].

(e) Improving statistical reporting and explicitly stating biological replicate structure.

This was addressed above [see response to Weaknesses (1)-b, (5)-b].

Reviewer #2 (Public review):

Sun et al. have developed a midbrain-like organoid (MLO) model for neuronopathic Gaucher disease (nGD). The MLOs recapitulate several features of nGD molecular pathology, including reduced GCase activity, sphingolipid accumulation, and impaired dopaminergic neuron development. They also characterize the transcriptome in the MLO nGD model. CRISPR correction of one of the GBA1 mutant alleles rescues most of the nGD molecular phenotypes. The MLO model was further deployed in proof-of-principle studies of investigational nGD therapies, including SapC-DOPS nanovesicles, AAV9-mediated GBA1 gene delivery, and substrate-reduction therapy (GZ452). This patient-specific 3D model provides a new platform for studying nGD mechanisms and accelerating therapy development. Overall, only modest weaknesses are noted.

We thank the reviewer for the supportive remarks.

Reviewer #3 (Public review):

Summary:

In this study, the authors describe modeling of neuronopathic Gaucher disease (nGD) using midbrain-like organoids (MLOs) derived from hiPSCs carrying GBA1 L444P/P415R or L444P/RecNciI variants. These MLOs recapitulate several disease features, including GCase deficiency, reduced enzymatic activity, lipid substrate accumulation, and impaired dopaminergic neuron differentiation. Correction of the GBA1 L444P variant restored GCase activity, normalized lipid metabolism, and rescued dopaminergic neuronal defects, confirming its pathogenic role in the MLO model. The authors further leveraged this system to evaluate therapeutic strategies, including: (i) SapC-DOPS nanovesicles for GCase delivery, (ii) AAV9-mediated GBA1 gene therapy, and (iii) GZ452, a glucosylceramide synthase inhibitor. These treatments reduced lipid accumulation and ameliorated autophagic, lysosomal, and neurodevelopmental abnormalities.

Strengths:

This manuscript demonstrates that nGD patient-derived MLOs can serve as an additional platform for investigating nGD mechanisms and advancing therapeutic development.

Comments:

(1) It is interesting that GBA1 L444P/P415R MLOs show defects in midbrain patterning and dopaminergic neuron differentiation (Figure 3). One might wonder whether these abnormalities are specific to the combination of L444P and P415R variants or represent a 

general consequence of GBA1 loss. Do GBA1 L444P/RecNciI (GD2-10-257) MLOs also exhibit similar defects?

We observed reduced dopaminergic neuron marker TH expression in GBA1 L444P/RecNciI (GD2-10-257) MLOs, suggesting that this line also exhibits defects in dopaminergic neuron differentiation. These data are provided in a new Supplementary Fig. 4E, and are summarized in new Supplementary Table 2 in the revision.

(2) In Supplementary Figure 3, the authors examined GCase localization in SapC-DOPSfGCase-treated nGD MLOs. These data indicate that GCase is delivered to TH⁺ neurons, GFAP⁺ glia, and various other unidentified cell types. In fruit flies, the GBA1 ortholog, Gba1b, is only expressed in glia (PMID: 35857503; 35961319). Neuronally produced GluCer is transferred to glia for GBA1-mediated degradation. These findings raise an important question: in wild-type MLOs, which cell type(s) normally express GBA1? Are they dopaminergic neurons, astrocytes, or other cell types?

All cell types in wild-type MLOs are expected to express GBA1, as it is a housekeeping gene broadly expressed across neurons, astrocytes, and other brain cell types. Its lysosomal function is essential for cellular homeostasis and is therefore not restricted to any specific lineage. (https://www.proteinatlas.org/ENSG00000177628GBA1/brain/midbrain). 

(3) The authors may consider switching Figures 2 and 3 so that the differentiation defects observed in nGD MLOs (Figure 3) are presented before the analysis of other phenotypic abnormalities, including the various transcriptional changes (Figure 2).

We appreciate the reviewer’s suggestion; however, we respectfully prefer to retain the current order of Figures 2 and 3, as we believe this structure provides the clearest narrative flow. Figure 2 establishes the core biochemical hallmarks: reduced GCase activity, substrate accumulation, and global transcriptomic dysregulation (1,429 DEGs enriched in neural development, WNT signaling, and lysosomal pathways), which together provide essential molecular context for studying the specific cellular differentiation defects presented in Figure 3. Presenting the broader disease landscape first creates a coherent mechanistic link to the subsequent analyses of midbrain patterning and dopaminergic neuron impairment.

To enhance readability, we have added a brief transitional sentence at the start of the Figure 3 paragraph: “Building on the molecular and transcriptomic hallmarks of GCase deficiency observed in nGD MLOs (Figure 2), we next investigated the impact on midbrain patterning and dopaminergic neuron differentiation (Figure 3).”

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"Personalized Mobile Conputing"

all about Personal Knowledge Work interchangeably on Desktop and Mobile Devices (Palm and Windows Mobile)

Doing DocBook Structure without the complexity of MarkDown

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Extensible Augmented Morphic Writing

Rendering was slow, 10 years ahead of the capabilities

The hidden goal was to eventually go from Peronal Learning Networks

towards Personal first, Autonomous InterPersonal InerPlanetary Mutual Learning Networks

Indy Learning Commons

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #2 (Public review):

In this valuable manuscript, Lin et al attempt to examine the role of long non coding RNAs (lncRNAs) in human evolution, through a set of population genetics and functional genomics analyses that leverage existing datasets and tools. Although the methods are incomplete and at times inadequate, the results nonetheless point towards a possible contribution of long non coding RNAs to shaping humans, and suggest clear directions for future, more rigorous study.

Comments on revisions:

I thank the authors for their revision and changes in response to previous rounds of comments. As before, I appreciate the changes made in response to my comments, and I think everyone is approaching this in the spirit of arriving at the best possible manuscript, but we still have some deep disagreements on the nature of the relevant statistical approach and defining adequate controls. I highlight a couple of places that I think are particularly relevant, but note that given the authors disagree with my interpretation, they should feel free to not respond!

(1) On the subject of the 0.034 threshold, I had previously stated: "I do not agree with the rationale for this claim, and do not agree that it supports the cutoff of 0.034 used below."

In their reply to me, the authors state:

"What we need is a gene number, which (a) indicates genes that effectively differentiate humans from chimpanzees, (b) can be used to set a DBS sequence distance cutoff. Since this study is the first to systematically examine DBSs in humans and chimpanzees, we must estimate this gene number based on studies that identify differentially expressed genes in humans and chimpanzees. We choose Song et al. 2021 (Song et al. Genetic studies of human-chimpanzee divergence using stem cell fusions. PNAS 2021), which identified 5984 differentially expressed genes, including 4377 genes whose differential expression is due to trans-acting differences between humans and chimpanzees. To the best of our knowledge, this is the only published data on trans-acting differences between humans and chimpanzees, and most HS lncRNAs and their DBSs/targets have trans-acting relationships (see Supplementary Table 2). Based on these numbers, we chose a DBS sequence distance cutoff of 0.034, which corresponds to 4248 genes (the top 20%), slightly fewer than 4377."

I have some notes here. First, Agoglia et al, Nature, 2021, also examined the nature of cis vs trans regulatory differences between human and chimps using a very similar set up to Song et al; their Supplementary Table 4 enables the discovery of genes with cis vs trans effects although admittedly this is less straightforward than the Song et al data. Second, I can't actually tell how the 4377 number is arrived at. From Song et al, "Of 4,671 genes with regulatory changes between human-only and chimpanzee-only iPSC lines, 44.4% (2,073 genes) were regulated primarily in cis, 31.4% (1,465 genes) were regulated primarily in trans, and the remaining 1,133 genes were regulated both in cis and in trans (Fig. 2C). This final category was further broken down into a cis+trans category (cis- and transregulatory changes acting in the same direction) and a cis-trans category (cis- and trans-regulatory changes acting in opposite directions)." Even when combining trans-only and cis&trans genes that gives 2,598 genes with evidence for some trans regulation. I cannot find 4,377 in the main text of the Song et al paper.

Elsewhere in their response, the authors respond to my comment that 0.034 is an arbitrary threshold by repeating the analyses using a cutoff of 0.035. I appreciate the sentiment here, but I would not expect this to make any great difference, given how similar those numbers are! A better approach, and what I had in mind when I mentioned this, would be to test multiple thresholds, ranging from, eg,0.05 to 0.01 <DBS dist =0.01 -> 0.034 -> 0.05> at some well-defined step size.

(1) We sincerely thank the reviewer for this critical point. Our initial purpose, based on DBS distances from the human genome to chimpanzee genome and archaic genomes, was that genes with large DBS distances may have contributed more to human evolution. However, our ORA (overrepresentation analysis) explored only genes with large DBS distances (the legend of old Figure 2 was “1256 target genes whose DBSs have the largest distances from modern humans to chimpanzees and Altai Neanderthals are enriched in different Biological Processes GO terms”), with the use of the cutoff (threshold) of 0.034 for defining large distance. The cutoff is not totally unreasonable (as our new results and the following sensitivity analysis indicate), but this approach was indirect and flawed.

(2) We have now performed ORA using two methods. The first uses only DBS distances. Instead of using a cutoff, we now sort genes by DBS distance (human-chimpanzee distances and human-Altai Neanderthal distance, respectively, see Supplementary Table 5) and use the top 25% and bottom 25% of genes to perform ORA. This directly examines whether DBS distances along indicate that genes with large DBS distances contribute more to human evolution than genes with small DBS distances. The second also explores the ASE genes (allele-specific expression, genes undergoing human/chimpanzee-specific regulation in the tetraploid human–chimpanzee hybrid iPS) reported by Agoglia et al. 2021. We select the top 50% and bottom 50% of genes with large and small DBS distances, intersect them with ASE genes from Agoglia et al. 2021 (their Supplementary Table 4), and apply ORA to the intersections. Both the results are that: (a) more GO terms are obtained from genes with large DBS distances, (b) more human evolution-related GO terms are obtained from genes with large DBS distances (Supplementary Table 5,6,7; Figure 2; Supplementary Fig. 15). These results directly suggest that genes with large DBS distances contribute more to human evolution than genes with small DBS distances, which is a key theme of the study.

(3) Regarding Song et al 2021, the statement of “we differentiated…allotetraploid (H1C1a, H1C1b, H2C2a, H2C2b) lines into ectoderm, mesoderm, and endoderm” made us assume that their differentiated hybrid cell lines cover more tissue types than those of Agoglia et al. 2021. Now, upon re-examining Supplementary Table 5 of Song et al. and Supplementary Table 4 of Agoglia et al. 2021, we find that the latter more clearly indicates significant ASE genes (p-adj<0.01 and |LFC>0.5| in GRCh38 and PanTro5).

(4) We have also performed two additional analyses in response to the suggestion of “test multiple thresholds, ranging from, eg, 0.05 to 0.01 <DBS dist =0.01 -> 0.034 -> 0.05> at some well-defined step size”. First, we performed a multi-threshold sensitivity analysis using a spectrum of cutoffs (0.03, 0.034, 0.04, 0.05), and tracked the number of genes identified and the enrichment significance of key GO terms (e.g., "neuron projection development," "behavior") across these thresholds. The result confirms that while the absolute number of genes varies with the cutoffs, the core biological conclusion (specifically, the significant enrichment of target genes in neurodevelopmental and cognitive functions) remains stable and significant. For instance, "behavior" maintains strong statistical significance (FDR<0.01) in both the human-chimpanzee and human-Altai Neanderthal comparisons across all tested cutoffs, and "Neuron projection development" also remains significant across three (0.03, 0.034, 0.04) of the four cutoffs in the Altai comparison. This pattern suggests that our core findings regarding neurodevelopmental functions are robust across a range of cutoffs. Nevertheless, we did not extend the analysis to smaller cutoffs (e.g., 0.01 or 0.02) because such values would identify an excessively large number of genes (>10000) for ORA, which would render the GOterm enrichment analysis less meaningful due to a loss of specificity.

Second, we have performed an additional validation to directly evaluate whether the 0.034 cutoff itself represents a stringent and biologically meaningful value. We sought to empirically determine how often a DBS sequence distance of 0.034 or greater might occur by chance in promoter regions, thereby testing its significance as a marker of potential evolutionary divergence. We randomly sampled 10,000 windows from annotated promoter regions across the hg38 genome, each with a size matching the average length of DBSs (147 bp). We then calculated the per-base sequence distances for these random windows between modern humans and chimpanzees, as well as between modern humans and the three archaic humans (Altai, Denisovan, Vindija). The analysis reveals that a distance of ≥0.034 is a rare event in random promoter sequences: for Human-Chimp, Human-Altai, HumanDenisovan, and Human-Vindija, 5.49% (549/10000), 0.31% (31/10000), 4.47% (447/10000), and0.03% (3/10000) of random windows reach this distance. This empirical evidence suggests that 0.034 is a sufficiently strong cutoff for defining large DBS distance, it would occur very unlikely in a random genomic background (P<0.1 for Chimpanzee and P<0.05 for the archaic humans), and DBSs exceeding this cutoff are significantly enriched for sequences that have undergone substantial evolutionary change instead of being random neutral variations.  

(5) We present new Figure 2, Supplementary Table 5,6,7, and Supplementary Fig. 15. We have substantially revised section 2.3, related sections in Results, Supplementary Note 3, and Supplementary Table 8. We have removed related descriptions and explanations in the main text and Supplementary Notes. The results of the above two analyses are presented here as two Author response images.

Author response table 1.

Sensitivity analysis of GO-term enrichment across different DBS sequence distance cutoffs. The table shows the numbers of target genes identified and the false discovery rates (FDR) for the enrichment of three selected GO terms at four different distance cutoffs. Note that, unlike in the old Figure 2, the results for chimpanzees and Altai Neanderthals are not directly comparable here, as the numbers of target genes used for the enrichment analysis differ between them at each cutoff.

Author response image 1.

Distribution of per-base sequence distances for DBS size-matched random genomic windows in Ensembl-annotated promoter regions, calculated between modern humans and (A) chimpanzee, (B) Altai Neanderthal, (C) Denisovan, and (D) Vindija Neanderthal genomes.

(2) The authors have introduced a new TFBS section, as a control for their lncRNAs - this is welcome, though again I would ask for caution when interpreting results. For instance, in their reply to me the authors state: "The number of HS TFs and HS lncRNAs (5 vs 66) <HS TF vs all HS lncRNAs> alone lends strong evidence suggesting that HS lncRNAs have contributed more significantly to human evolution than HS TFs (note that 5 is the union of three intersections between <many2zero + one2zero> and the three <human TF list>)."

But this assumes the denominator is the same! There are 35899 lncRNAs according to the current GENCOVE build; 66/35899 = 0.0018, so, 0.18% of lncRNAs are HS. The authors compare this to 5 TFs. There are 19433 protein coding genes in the current GENCOVE build, which naively (5/19433) gives a big depletion (0.026%) relative to the lnc number. However, this assumes all protein coding genes are TFs, which is not the case. A quick search suggests that ~2000 protein coding genes are TFs (see, eg, https://pubmed.ncbi.nlm.nih.gov/34755879/); which gives an enrichment (although I doubt it is a statistically significant one!) of HS TFs over HS lncRNAs (5/2000 = 0.0025). Hence my emphasis on needing to be sure the controls are robust and valid throughout!

We thank the reviewer for this comment. While 5 vs 66 reveals a difference, a direct comparison is too simplified. The real take-home message of the new TFBS section is not the numbers but the distributions of HS TFs’ targets and HS lncRNAs’ targets across GTEx organs and tissues (Figure 3 and Supplementary Figures 24, 25) - correlated HS lncRNA-target transcript pairs are highly enriched in brain regions, but correlated HS TF-target transcript pairs are distributed broadly across GTEx tissues and organs. We have now removed the simple comparison of “5 vs 66” and more carefully explained our comparison in section 2.6.

(3) In my original review I said: line 187: "Notably, 97.81% of the 105141 strong DBSs have counterparts in chimpanzees, suggesting that these DBSs are similar to HARs in evolution and have undergone human-specific evolution." I do not see any support for the inference here. Identifying HARs and acceleration relies on a far more thorough methodology than what's being presented here. Even generously, pairwise comparison between two taxa only cannot polarise the direction of differences; inferring human-specific change requires outgroups beyond chimpanzee.

In their reply to me, the authors state:

Here, we actually made an analogy but not an inference; therefore, we used such words as "suggesting" and "similar" instead of using more confirmatory words. We have revised the latter half sentence, saying "raising the possibility that these sequences have evolved considerably during human evolution".

Is the aim here to draw attention to the ~2.2% of DBS that do not have a counterpart? In that case, it would be better to rewrite the sentence to emphasise those, not the ones that are shared between the two species? I do appreciate the revised wording, though.

(1) Our original phrasing may be misleading, and we agree entirely that “pairwise comparison between two taxa only cannot polarise the direction of differences; inferring human-specific change requires outgroups beyond chimpanzee”. As explained in that reply, we know and think that DBSs and HARs are two different classes of sequences, and indeed, identifying HARs and acceleration relies on a far more thorough methodology. Yet, three factors prompted us to compare them. First, both suggest the importance of sequences outside genes. Second, both are quite “old” sequences and have undergone considerable evolution recently (although the references are different). Third, both have contributed greatly to human brain evolution.  

(2) Here, our stress is 97.81% but not 2.2%, and we have made this analogy more clearly and cautiously. Relevant revisions have been made in the Results, Discussion, and Methods sections.   

(3) We also have further determined whether the 2.2% DBSs are human-specific gains by analyzing them using the UCSC Multiz Alignments of 100 Vertebrates. The result confirms that all 2248 DBSs are present in the human genome but are absent from the chimpanzee genome and all other aligned vertebrate genomes. We add this result into the manuscript.

(4) Finally, Line 408: "Ensembl-annotated transcripts (release 79)" Release 79 is dated to March 2015, which is quite a few releases and genome builds ago. Is this a typo? Both the human and the chimpanzee genome have been significantly improved since then!

(1) We thank the reviewer for this comment, which prompts us to provide further explanation and additional data. First, we began predicting HS lncRNAs’ DBSs when Ensembl release 79 was available, but did not re-predict DBSs when new Ensembl releases were published because (a) these new Ensembl releases are based also on hg38, (b) we did not find any fault in the LongTarget program during our use, nor received any one from users, (c) predicting lncRNAs’ DBSs using the LongTarget program is highly time-consuming.  

(2) Second, to assess the influence of newer Ensembl releases, we compared the promoters annotated in release 79 and in release 115. We found that the vast majority (87.3%) of promoters newly annotated in release 115 belong to non-coding genes. Thus, using release 115 may predict more DBSs in non-coding genes, but downstream analyses based on protein-coding genes would be essentially the same (meaning that all figures and tables would be the same).

(3) Third, a key element of this study is GTEx data analysis, and these data were also published years ago.  

(4) Finally, some lncRNA genes have new gene symbols in new Ensembl releases. To allow researchers to use our data conveniently, we have added a new column titled "Gene symbol (Ensembl release115)" to Supplementary Tables 2A and 2B.  

Summary:

Major changes based on Reviewer’s comments:

(1) The following revisions are made to address the comment on “the 0.034 threshold”: (a) Section 2.3, section 2.4, Supplementary Note 3, and related contents in Discussion and Methods are revised, (b) new Figure 2, Supplementary Figure 15, new Supplementary Table 5,6,7, (c) Table 2 and Supplementary Table 8 are revised.

(2) To address the comment on “new TFBS section”, section 2.6 and section 4.13 are revised.  

(3) To address the comment on “97.81% and 2.2% of DBSs”, section 2.3 is revised.

(4) The following revisions are made to address the comment on “release 79”: (a) the old Supplementary Table 2, 3 are merged to Supplementary Table 2AB, and the new column "Gene symbol (Ensembl release115)" is added to Supplementary Table 2AB, (b) accordingly, Supplementary Table 4,5 are renamed to Supplementary Table 3,4.

Additional revisions:

(1) Section 2.5 “Young weak DBSs may have greatly promoted recent human evolution” is moved into Supplementary Note 3 (which now has the subtitle “Target genes with specific DBS features are enriched in specific functions”), because this section is short and lacking sufficient cross-validation.

(2) Considerable minor revisions of sentences have been made.

(3) Since there are many supplementary figures, the main text now cites only Supplementary Notes, as the reader can easily access supplementary figures in Supplementary Notes.

This passage makes me think a lot about art and how one can go about making a painting, or a sculpture, etc. I think it's cool to think of literature this way as well because it is art that is really just expressed more through words.

I like this passage because it encourages the idea that movement and routine can come naturally through your experiences. I personally never have a set routine but I think everyone, whether they realize it or not, have some sort of unconscious routine and pattern

This passage made me think about how form can emerge from lived experience rather than being imposed afterward. Alison’s description of movement becoming structure suggests that narrative, like architecture, can grow organically from daily life instead of following a pre-set formula. It reframes writing as something embodied rather than abstract.

Schleswig-Holstein is still using Windows, taking it step by step. MS Office to LibreOffice, Thunderbird w Open-Xchange for mail, calendar, contacts, Element/Matrix for chat, Nextcloud for collab.

If only it weren't 25+ years later (and the PowerShell folks hadn't regressed on Windows).

the conversation shift too romeo and lady montaque is asking benvolioo where he is and is explained by montaque that he is always withdrawn and sad

Author response:

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

Reviewer #1

Chen et al. engineered and characterized a suite of next-generation GECIs for the Drosophila NMJ that allow for the visualization of calcium dynamics within the presynaptic compartment, at presynaptic active zones, and in the postsynaptic compartment. These GECIs include ratiometric presynaptic Scar8m (targeted to synaptic vesicles), ratiometric active zone localized Bar8f (targeted to the scaffold molecule BRP), and postsynaptic SynapGCaMP8m. The authors demonstrate that these new indicators are a large improvement on the widely used GCaMP6 and GCaMP7 series GECIs, with increased speed and sensitivity. They show that presynaptic Scar8m accurately captures presynaptic calcium dynamics with superior sensitivity to the GCaMP6 and GCaMP7 series and with similar kinetics to chemical dyes. The active-zone targeted Bar8f sensor was assessed for the ability to detect release-site-specific nanodomain changes, but the authors concluded that this sensor is still too slow to accurately do so. Lastly, the use of postsynaptic SynapGCaMP8m was shown to enable the detection of quantal events with similar resolution to electrophysiological recordings. Finally, the authors developed a Python-based analysis software, CaFire, that enables automated quantification of evoked and spontaneous calcium signals. These tools will greatly expand our ability to detect activity at individual synapses without the need for chemical dyes or electrophysiology.

We thank this Reviewer for the overall positive assessment of our manuscript and for the incisive comments.

(1) The role of Excel in the pipeline could be more clearly explained. Lines 182-187 could be better worded to indicate that CaFire provides analysis downstream of intensity detection in ImageJ. Moreover, the data type of the exported data, such as .csv or .xlsx, should be indicated instead of 'export to graphical program such as Microsoft Excel'.

We thank the Reviewer for these comments, many of which were shared by the other reviewers. In response, we have now 1) more clearly explained the role of Excel in the CaFire pipeline (lines 677-681), 2) revised the wording in lines 676-679 to indicate that CaFire provides analysis downsteam of intensity detection in ImageJ, and 3) Clarified the exported data type to Excel (lines 677-681). These efforts have improved the clarity and readability of the CaFire analysis pipeline.

(2) In Figure 2A, the 'Excel' step should either be deleted or included as 'data validation' as ImageJ exports don't require MS Excel or any specific software to be analysed. (Also, the graphic used to depict Excel software in Figure 2A is confusing.)

We thank the reviewer for this helpful suggestion. In the Fig. 2A, we have changed the Excel portion and clarified the processing steps in the revised methods. Specifically, we now indicate that ROIs are first selected in Fiji/ImageJ and analyzed to obtain time-series data containing both the time information and the corresponding imaging mean intensity values. These data are then exported to a spreadsheet file (e.g., Excel), which is used to organize the output before being imported into CaFire for subsequent analysis. These changes can be found in the Fig. 2A and methods (lines 676-681).

(3) Figure 2B should include the 'Partition Specification' window (as shown on the GitHub) as well as the threshold selection to give the readers a better understanding of how the tool works.

We absolutely agree with this comment, and have made the suggested changes to the Fig. 2B. In particular, we have replaced the software interface panels and now include windows illustrating the Load File, Peak Detection, and Partition functions. These updated screenshots provide a clearer view of how CaFire is used to load the data, detect events, and perform partition specification for subsequent analysis. We agree these changes will give the readers a better understanding of how the tool works, and we thank the reviewer for this comment.

(4) The presentation of data is well organized throughout the paper. However, in Figure 6C, it is unclear how the heatmaps represent the spatiotemporal fluorescence dynamics of each indicator. Does the signal correspond to a line drawn across the ROI shown in Figure 6B? If so, this should be indicated.

We apologize that the heatmaps were unclear in Fig panel 6C (Fig. 7C in the Current revision). Each heatmap is derived from a one-pixel-wide vertical line within a miniature-event ROI. These heatmaps correspond to the fluorescence change in the indicated SynapGCaMP variant of individual quantal events and their traces shown in Fig. 7C, with a representative image of the baseline and peak fluorescence shown in Fig. 7B. Specifically, we have added the following to the revised Fig. 7C legend:

The corresponding heatmaps below were generated from a single vertical line extracted from a representative miniature-event ROI, and visualize the spatiotemporal fluorescence dynamics (ΔF/F) along that line over time.

(5) In Figure 6D, the addition of non-matched electrophysiology recordings is confusing. Maybe add "at different time points" to the end of the 6D legend, or consider removing the electrophysiology trace from Figure 6D and referring the reader to the traces in Figure 7A for comparison (considering the same point is made more rigorously in Figure 7).

This is a good point, one shared with another reviewer. We apologize this was not clear, and have now revised this part of the figure to remove the electrophysiological traces in what is now Fig. 7 while keeping the paired ones still in what is now Fig. 8A as suggested by the reviewer. We agree this helps to clarify the quantal calcium transients.

(6) In GitHub, an example ImageJ Script for analyzing the images and creating the inputs for CaFire would be helpful to ensure formatting compatibility, especially given potential variability when exporting intensity information for two channels. In the Usage Guide, more information would be helpful, such as how to select ∆R/R, ideally with screenshots of the application being used to analyze example data for both single-channel and two-channel images.

We agree that additional details added to the GitHub would be helpful for users of CaFire. In response, we have now added the following improvements to the GitHub site: 

- ImageJ operation screenshots

Step-by-step illustrations of ROI drawing and Multi Measure extraction.

- Example Excel file with time and intensity values

Demonstrates the required data format for CaFire import, including proper headers.

- CaFire loading screenshots for single-channel and dual-channel imaging

Shows how to import GCaMP into Channel 1 and mScarlet into Channel 2.

- Peak Detection and Partition setting screenshots

Visual examples of automatic peak detection, manual correction, and trace partitioning.

- Instructions for ROI Extraction and CaFire Analysis

A written guide describing the full workflow from ROI selection to CaFire data export.

These changes have improved the usability and accessibility of CaFire, and we thank the reviewer for these points.

Reviewer #2

Calcium ions play a key role in synaptic transmission and plasticity. To improve calcium measurements at synaptic terminals, previous studies have targeted genetically encoded calcium indicators (GECIs) to pre- and postsynaptic locations. Here, Chen et al. improve these constructs by incorporating the latest GCaMP8 sensors and a stable red fluorescent protein to enable ratiometric measurements. In addition, they develop a new analysis platform, 'CaFire', to facilitate automated quantification. Using these tools, the authors demonstrate favorable properties of their sensors relative to earlier constructs. Impressively, by positioning postsynaptic GCaMP8m near glutamate receptors, they show that their sensors can report miniature synaptic events with speed and sensitivity approaching that of intracellular electrophysiological recordings. These new sensors and the analysis platform provide a valuable tool for resolving synaptic events using all-optical methods.

We thank the Reviewer for their overall positive evaluation and comments.

Major comments:

(1) While the authors rigorously compared the response amplitude, rise, and decay kinetics of several sensors, key parameters like brightness and photobleaching rates are not reported. I feel that including this information is important as synaptically tethered sensors, compared to freely diffusible cytosolic indicators, can be especially prone to photobleaching, particularly under the high-intensity illumination and high-magnification conditions required for synaptic imaging. Quantifying baseline brightness and photobleaching rates would add valuable information for researchers intending to adopt these tools, especially in the context of prolonged or high-speed imaging experiments.

This is a good point made by the reviewer, and one we agree will be useful for researchers to be aware. First, it is important to note that the photobleaching and brightness of the sensors will vary depending on the nature of the user’s imaging equipment, which can vary significantly between widefield microscopes (with various LED or halogen light sources for illumination), laser scanning systems (e.g., line scans with confocal systems), or area scanning systems using resonant scanners (as we use in our current study). Under the same imaging settings, GCaMP8f and 8m exhibit comparable baseline fluorescence, whereas GCaMP6f and 6s are noticeably dimmer; because our aim is to assess each reagent’s potential under optimal conditions, we routinely adjust excitation/camera parameters before acquisition to place baseline fluorescence in an appropriate dynamic range. As an important addition to this study, motivated by the reviewer’s comments above, we now directly compare neuronal cytosolic GCaMP8m expression with our Scar8m sensor, showing higher sensitivity with Scar8m (now shown in the new Fig. 3F-H).

Regarding photobleaching, GCaMP signals are generally stable, while mScarlet is more prone to bleaching: in presynaptic area scanned confocal recordings, the mScarlet channel drops by ~15% over 15 secs, whereas GCaMP6s/8f/8m show no obvious bleaching over the same window (lines 549-553). In contrast, presynaptic widefield imaging using an LED system (CCD), GCaMP8f shows ~8% loss over 15 secs (lines 610-611). Similarly, for postsynaptic SynapGCaMP6f/8f/8m, confocal resonant area scans show no obvious bleaching over 60 secs, while widefield shows ~2–5% bleaching over 60 secs (lines 634-638). Finally, in active-zone/BRP calcium imaging (confocal), mScarlet again bleaches by ~15% over 15 s, while GCaMP8f/8m show no obvious bleaching. The mScarlet-channel bleaching can be corrected in Huygens SVI (Bleaching correction or via the Deconvolution Wizard), whereas we avoid applying bleaching correction to the green GCaMP channel when no clear decay is present to prevent introducing artifacts. This information is now added to the methods (lines 548-553).

(2) In several places, the authors compare the performance of their sensors with synthetic calcium dyes, but these comparisons are based on literature values rather than on side-by-side measurements in the same preparation. Given differences in imaging conditions across studies (e.g., illumination, camera sensitivity, and noise), parameters like indicator brightness, SNR, and photobleaching are difficult to compare meaningfully. Additionally, the limited frame rate used in the present study may preclude accurate assessment of rise times relative to fast chemical dyes. These issues weaken the claim made in the abstract that "...a ratiometric presynaptic GCaMP8m sensor accurately captures .. Ca²⁺ changes with superior sensitivity and similar kinetics compared to chemical dyes." The authors should clearly acknowledge these limitations and soften their conclusions. A direct comparison in the same system, if feasible, would greatly strengthen the manuscript.

We absolutely agree with these points made the reviewer, and have made a concerted effort to address them through the following:

We have now directly compared presynaptic calcium responses on the same imaging system using the chemical dye Oregon Green Bapta-1 (OGB-1), one of the primary synthetic calcium indicators used in our field. These experiments reveal that Scar8f exhibits markedly faster kinetics and an improved signal-to-noise ratio compared to OGB-1, with higher peak fluorescence responses (Scar8f: 0.32, OGB-1: 0.23). The rise time constants of the two indicators are comparable (both ~3 msecs), whereas the decay of Scar8f is faster than that of OGB-1 (Scar8f: ~40, OGB-1: ~60), indicating more rapid signal recovery. These results now directly demonstrate the superiority of the new GCaMP8 sensors we have engineered over conventional synthetic dyes, and are now presented in the new Fig. 3A-E of the manuscript.

We agree with the reviewer that, in the original submission, the relatively slow resonant area scans (~115 fps) limited the temporal resolution of our rise time measurements. To address this, we have re-measured the rise time using higher frame-rate line scans (kHz). For Scar8f, the rise time constant was 6.736 msec at ~115 fps resonant area scanned, but shortened to 2.893 msec when imaged at ~303 fps, indicating that the original protocol underestimated the true kinetics. In addition, for Bar8m, area scans at ~118 fps yielded a rise time constant of 9.019 msec, whereas line scans at ~1085 fps reduced the rise time constant to 3.230 msec. These new measurements are now incorporated into the manuscript ( Figs. 3,4, and 6) to more accurately reflect the fast kinetics of these indicators.

(3) The authors state that their indicators can now achieve measurements previously attainable with chemical dyes and electrophysiology. I encourage the authors to also consider how their tools might enable new measurements beyond what these traditional techniques allow. For example, while electrophysiology can detect summed mEPSPs across synapses, imaging could go a step further by spatially resolving the synaptic origin of individual mEPSP events. One could, for instance, image MN-Ib and MN-Is simultaneously without silencing either input, and detect mEPSP events specific to each synapse. This would enable synapse-specific mapping of quantal events - something electrophysiology alone cannot provide. Demonstrating even a proof-of-principle along these lines could highlight the unique advantages of the new tools by showing that they not only match previous methods but also enable new types of measurements.

These are excellent points raised by the reviewer. In response, we have done the following: 

We have now included a supplemental video as “proof-of-principle” data showing simultaneous imaging of SynapGCaMP8m quantal events at both MN-Is and -Ib, demonstrating that synapse-specific spatial mapping of quantal events can be obtained with this tool (see new Supplemental Video 1). 

We have also included an additional discussion of the potential and limitations of these tools for new measurements beyond conventional approaches. This discussion is now presented in lines 419-421 in the manuscript.

(4) For ratiometric measurements, it is important to estimate and subtract background signals in each channel. Without this correction, the computed ratio may be skewed, as background adds an offset to both channels and can distort the ratio. However, it is not clear from the Methods section whether, or how, background fluorescence was measured and subtracted.

This is a good point, and we agree more clarification about how ratiometric measurements were made is needed. In response, we have now added the following to the Methods section (lines 548-568):

Time-lapse videos were stabilized and bleach-corrected prior to analysis, which visibly reduced frame-toframe motion and intensity drift. In the presynaptic and active-zone mScarlet channel, a bleaching factor of ~1.15 was observed during the 15 sec recording. This bleaching can be corrected using the “Bleaching correction” tool in Huygens SVI. For presynaptic and active-zone GCaMP signals, there was minimal bleaching over these short imaging periods. Therefore, the bleaching correction step for GCaMP was skipped. Both GCaMP and mScarlet channels were processed using the default settings in the Huygens SVI “Deconvolution Wizard” (with the exception of the bleaching correction option). Deconvolution was performed using the CMLE algorithm with the Huygens default stopping criterion and a maximum of 30 iterations, such that the algorithm either converged earlier or, if convergence was not reached, was terminated at this 30iteration limit; no other iteration settings were used across the GCaMP series. ROIs were drawn on the processed images using Fiji ImageJ software, and mean fluorescence time courses were extracted for the GCaMP and mScarlet channels, yielding F_GCaMP(t) and F_mScarlet(t). F(t)s were imported into CaFire with GCaMP assigned to Channel #1 (signal; required) and mScarlet to Channel #2 (baseline/reference; optional). If desired, the mScarlet signal could be smoothed in CaFire using a user-specified moving-average window to reduce high-frequency noise. In CaFire’s ΔR/R mode, the per-frame ratio was computed as R(t)=F_GCaMP(t) and F_mScarlet(t); a baseline ratio R0 was estimated from the pre-stimulus period, and the final response was reported as ΔR/R(t)=[R(t)−R0]/R0, which normalizes GCaMP signals to the co-expressed mScarlet reference and thereby reduces variability arising from differences in sensor expression level or illumination across AZs.

(5) At line 212, the authors claim "... GCaMP8m showing 345.7% higher SNR over GCaMP6s....(Fig. 3D and E) ", yet the cited figure panels do not present any SNR quantification. Figures 3D and E only show response amplitudes and kinetics, which are distinct from SNR. The methods section also does not describe details for how SNR was defined or computed.

This is another good point. We define SNR operationally as the fractional fluorescence change (ΔF/F). Traces were processed with CaFire, which estimates a per-frame baseline F₀(t) with a user-configurable sliding window and percentile. In the Load File panel, users can specify both the length of the moving baseline window and the desired percentile; the default settings are a 50-point window and the 30th percentile, representing a 101-point window centered on each time point (previous 50 to next 50 samples) and took the lower 30% of values within that window to estimate F₀(t). The signal was then computed as ΔF/F=[F(t)−F0(t)]/F0(t). This ΔF/F value is what we report as SNR throughout the manuscript and is now discussed explicitly in the revised methods (lines 686-693).

(6) Lines 285-287 "As expected, summed ΔF values scaled strongly and positively with AZ size (Fig. 5F), reflecting a greater number of Cav2 channels at larger AZs". I am not sure about this conclusion. A positive correlation between summed ΔF values and AZ size could simply reflect more GCaMP molecules in larger AZs, which would give rise to larger total fluorescence change even at a given level of calcium increase.

The reviewer makes a good point, one that we agree should be clarified. The reviewer is indeed correct that larger active zones should have more abundant BRP protein, which in turn will lead to a higher abundance of the Bar8f sensor, which should lead to a higher GCaMP response simply by having more of this sensor. However, the inclusion of the ratiometric mScarlet protein should normalize the response accurately, correcting for this confound, in which the higher abundance of GCaMP should be offset (normalized) by the equally (stoichiometric) higher abundance of mScarlet. Therefore, when the ∆R/R is calculated, the differences in GCaMP abundance at each AZ should be corrected for the ratiometric analysis. We now use an improved BRP::mScarlet3::GCaMP8m (Bar8m) and compute ΔR/R with R(t)=F_GCaMP8m/F_mScarlet3. ROIs were drawn over individual AZs (Fig. 6B). CaFire estimated R0 with a sliding 101-point window using the lowest 10% of values, and responses were reported as ΔR/R=[R−R0]/R0. Area-scan examples (118 fps) show robust ΔR/R transients (peaks ≈1.90 and 3.28; tau rise ≈9.0–9.3 ms; Fig. 6C, middle).

We have now made these points more clearly in the manuscript (lines 700-704) and moved the Bar8f intensity vs active zone size data to Table S1. Together, these revisions improve the indicator-abundance confound (via mScarlet normalization). 

(6) Lines 313-314: "SynapGCaMP quantal signals appeared to qualitatively reflect the same events measured with electrophysiological recordings (Fig. 6D)." This statement is quite confusing. In Figure 6D, the corresponding calcium and ephys traces look completely different and appear to reflect distinct sets of events. It was only after reading Figure 7 that I realized the traces shown in Figure 6D might not have been recorded simultaneously. The authors should clarify this point.

Yes, we absolutely agree with this point, one shared by Reviewer 1. In response, we have removed the electrophysiological traces in Fig. 6 to clarify that just the calcium responses are shown, and save the direct comparison for the Fig. 7 data (now revised Fig. 8).

(8) Lines 310-313: "SynapGCaMP8m .... striking an optimal balance between speed and sensitivity", and Lines 314-316: "We conclude that SynapGCaMP8m is an optimal indicator to measure quantal transmission events at the synapse." Statements like these are subjective. In the authors' own comparison, GCaMP8m is significantly slower than GCaMP8f (at least in terms of decay time), despite having a moderately higher response amplitude. It is therefore unclear why GCaMP8m is considered 'optimal'. The authors should clarify this point or explain their rationale for prioritizing response amplitude over speed in the context of their application.

This is another good point that we agree with, as the “optimal” sensor will of course depend on the user’s objectives. Hence, we used the term “an optimal sensor” to indicate it is what we believed to be the best one for our own uses. However, this point should be clarified and better discussed. In response, we have revised the relevant sections of the manuscript to better define why we chose the 8m sensors to strike an optimal balance of speed and sensitivity for our uses, and go on to discuss situations in which other sensor variants might be better suited. These are now presented in lines 223-236 in the revised manuscript, and we thank the reviewer for making these comments, which have improved our study.

Minor comments

(1)  Please include the following information in the Methods section:

(a) For Figures 3 and 4, specify how action potentials were evoked. What type of electrodes were used, where were they placed, and what amount of current or voltage was applied?

We apologize for neglecting to include this information in the original submission. We have now added this information to the revised Methods section (lines 537-543).

(b) For imaging experiments, provide information on the filter sets used for each imaging channel, and describe how acquisition was alternated or synchronized between the green and red channels in ratiometric measurements. Additionally, please report the typical illumination intensity (in mW/mm²) for each experimental condition.

We thank the reviewer for this helpful comment. We have now added detailed information about the imaging configuration to the Methods (lines 512-528) with the following:

Ca2+ imaging was conducted using a Nikon A1R resonant scanning confocal microscope equipped with a 60x/1.0 NA water-immersion objective (refractive index 1.33). GCaMP signals were acquired using the FITC/GFP channel (488-nm laser excitation; emission collected with a 525/50-nm band-pass filter), and mScarlet/mCherry signals were acquired using the TRITC/mCherry channel (561-nm laser excitation; emission collected with a 595/50-nm band-pass filter). ROIs focused on terminal boutons of MN-Ib or -Is motor neurons. For both channels, the confocal pinhole was set to a fixed diameter of 117.5 µm (approximately three Airy units under these conditions), which increases signal collection while maintaining adequate optical sectioning. Images were acquired as 256 × 64 pixel frames (two 12-bit channels) using bidirectional resonant scanning at a frame rate of ~118 frames/s; the scan zoom in NIS-Elements was adjusted so that this field of view encompassed the entire neuromuscular junction and was kept constant across experiments. In ratiometric recordings, the 488-nm (GCaMP) and 561-nm (mScarlet) channels were acquired in a sequential dual-channel mode using the same bidirectional resonant scan settings: for each time point, a frame was first collected in the green channel and then immediately in the red channel, introducing a small, fixed frame-to-frame temporal offset while preserving matched spatial sampling of the two channels.

Directly measuring the absolute laser power at the specimen plane (and thus reporting illumination intensity in mW/mm²) is technically challenging on this resonant-scanning system, because it would require inserting a power sensor into the beam path and perturbing the optical alignment; consequently, we are unable to provide reliable absolute mW/mm² values. Instead, we now report all relevant acquisition parameters (objective, numerical aperture, refractive index, pinhole size, scan format, frame rate, and fixed laser/detector settings) and note that laser powers were kept constant within each experimental series and chosen to minimize bleaching and phototoxicity while maintaining an adequate signal-to-noise ratio. We have now added the details requested in the revised Methods section (lines 512-535), including information about the filter sets, acquisition settings, and typical illumination intensity.

(2) Please clarify what the thin versus thick traces represent in Figures 3D, 3F, 4C, and 4E. Are the thin traces individual trials from the same experiment, or from different experiments/animals? Does the thick trace represent the mean/median across those trials, a fitted curve, or a representative example?

We apologize this was not more clear in the original submission. Thin traces are individual stimulus-evoked trials (“sweeps”) acquired sequentially from the same muscle/NMJ in a single preparation; the panel is shown as a representative example of recordings collected across animals. The thick colored trace is the trialaveraged waveform (arithmetic mean) of those thin traces after alignment to stimulus onset and baseline subtraction (no additional smoothing beyond what is stated in Methods). The thick black curve over the decay phase is a single-exponential fit used to estimate τ. Specifically, we fit the decay segment by linear regression on the natural-log–transformed baseline-subtracted signal, which is equivalent to fitting y = y_peak·e^−t/τdecay over the decay window (revised Fig.4D and Fig.5C legends).

(3) Please clarify what the reported sample size (n) represents. Does it indicate the number of experimental repeats, the number of boutons or PSDs, or the number of animals?

Again, we apologize this was not clear. (n) refers to the number of animals (biological replicates), which is reported in Supplementary Table 1. All imaging was performed at muscle 6, abdominal segment A3. Per preparation, we imaged 1-2 NMJs in total, with each imaging targeting 2–3 terminal boutons at the target NMJ and acquired 2–3 imaging stacks choosing different terminal boutons per NMJ. For the standard stimulation protocol, we delivered 1 Hz stimulation for 1ms and captured 14 stimuli in a 15s time series imaging (lines 730-736).

Reviewer #3

Genetically encoded calcium indicators (GECIs) are essential tools in neurobiology and physiology. Technological constraints in targeting and kinetics of previous versions of GECIs have limited their application at the subcellular level. Chen et al. present a set of novel tools that overcome many of these limitations. Through systematic testing in the Drosophila NMJ, they demonstrate improved targeting of GCaMP variants to synaptic compartments and report enhanced brightness and temporal fidelity using members of the GCaMP8 series. These advancements are likely to facilitate more precise investigation of synaptic physiology.

This is a comprehensive and detailed manuscript that introduces and validates new GECI tools optimized for the study of neurotransmission and neuronal excitability. These tools are likely to be highly impactful across neuroscience subfields. The authors are commended for publicly sharing their imaging software.

This manuscript could be improved by further testing the GECIs across physiologically relevant ranges of activity, including at high frequency and over long imaging sessions. The authors provide a custom software package (CaFire) for Ca2+ imaging analysis; however, to improve clarity and utility for future users, we recommend providing references to existing Ca2+ imaging tools for context and elaborating on some conceptual and methodological aspects, with more guidance for broader usability. These enhancements would strengthen this already strong manuscript.

We thank the Reviewer for their overall positive evaluation and comments. 

Major comments:

(1) Evaluation of the performance of new GECI variants using physiologically relevant stimuli and frequency. The authors took initial steps towards this goal, but it would be helpful to determine the performance of the different GECIs at higher electrical stimulation frequencies (at least as high as 20 Hz) and for longer (10 seconds) (Newman et al, 2017). This will help scientists choose the right GECI for studies testing the reliability of synaptic transmission, which generally requires prolonged highfrequency stimulation.

We appreciate this point by the reviewer and agree it would be of interest to evaluate sensor performance with higher frequency stimulation and for a longer duration. In response, we performed a variety of stimulation protocols at high intensities and times, but found the data to be difficult to separate individual responses given the decay kinetics of all calcium sensors. Hence, we elected not to include these in the revised manuscript. However, we have now included an evaluation of the sensors with 20 Hz electrical stimulation for ~1 sec using a direct comparison of Scar8f with OGB-1. These data are now presented in a new Fig. 3D,E and discussed in the manuscript (lines 396-403).

(2) CaFire.

The authors mention, in line 182: 'Current approaches to analyze synaptic Ca2+ imaging data either repurpose software designed to analyze electrophysiological data or use custom software developed by groups for their own specific needs.' References should be provided. CaImAn comes to mind (Giovannucci et al., 2019, eLife), but we think there are other software programs aimed at analyzing Ca2+ imaging data that would permit such analysis.

Thank you for the thoughtful question. At this stage, we’re unable to provide a direct comparison with existing analysis workflows. In surveying prior studies that analyze Drosophila NMJ Ca²⁺ imaging traces, we found that most groups preprocess images in Fiji/ImageJ and then rely on their own custom-made MATLAB or Python scripts for downstream analysis (see Blum et al. 2021; Xing and Wu 2018). Because these pipelines vary widely across labs, a standardized head-to-head evaluation isn’t currently feasible. With CaFire, our goal is to offer a simple, accessible tool that does not require coding experience and minimizes variability introduced by custom scripts. We designed CaFire to lower the barrier to entry, promote reproducibility, and make quantal event analysis more consistent across users. We have added references to the sentence mentioned above.

Regarding existing software that the reviewer mentioned – CaImAn (Giovannucci et al. 2019): We evaluated CaImAn, which is a powerful framework designed for large-scale, multicellular calcium imaging (e.g., motion correction, denoising, and automated cell/ROI extraction). However, it is not optimized for the per-event kinetics central to our project - such as extracting rise and decay times for individual quantal events at single synapses. Achieving this level of granularity would typically require additional custom Python scripting and parameter tuning within CaImAn’s code-centric interface. This runs counter to CaFire’s design goals of a nocode, task-focused workflow that enables users to analyze miniature events quickly and consistently without specialized programming expertise.

Regarding Igor Pro (WaveMetrics), (Müller et al. 2012): Igor Pro is another platform that can be used to analyze calcium imaging signals. However, it is commercial (paid) software and generally requires substantial custom scripting to fit the specific analyses we need. In practice, it does not offer a simple, open-source, point-and-click path to per-event kinetic quantification, which is what CaFire is designed to provide.

The authors should be commended for making their software publicly available, but there are some questions:

How does CaFire compare to existing tools?

As mentioned above, we have not been able to adapt the custom scripts used by various labs for our purposes, including software developed in MatLab (Blum et al. 2021), Python (Xing and Wu 2018), and Igor (Müller et al. 2012). Some in the field do use semi-publically available software, including Nikon Elements (Chen and Huang 2017) and CaImAn (Giovannucci et al. 2019). However, these platforms are not optimized for the per-event kinetics central to our project - such as extracting rise and decay times for individual quantal events at single synapses. We have added more details about CaFire, mainly focusing on the workflow and measurements, highlighting the superiority of CaFire, showing that CaFire provides a no-code, standardized pipeline with automated miniature-event detection and per-event metrics (e.g., amplitude, rise time τ, decay time τ), optional ΔR/R support, and auto-partition feature. Collectively, these features make CaFire simpler to operate without programming expertise, more transparent and reproducible across users, and better aligned with the event-level kinetics required for this project.

Very few details about the Huygens deconvolution algorithms and input settings were provided in the methods or text (outside of MLE algorithm used in STED images, which was not Ca2+ imaging). Was it blind deconvolution? Did the team distill the point-spread function for the fluorophores? Were both channels processed for ratiometric imaging? Were the same settings used for each channel? Importantly, please include SVI Huygens in the 'Software and Algorithms' Section of the methods.

We thank the reviewer for raising this important point. We have now expanded the Methods to describe our use of Huygens in more detail and have added SVI Huygens Professional (Scientific Volume Imaging, Hilversum, The Netherlands) to the “Software and Algorithms” section. For Ca²⁺ imaging data, time-lapse stacks were processed in the Huygens Deconvolution Wizard using the standard estimation algorithm (CMLE). This is not a blind deconvolution procedure. Instead, Huygens computes a theoretical point-spread function (PSF) from the full acquisition metadata (objective NA, refractive index, voxel size/sampling, pinhole, excitation/emission wavelengths, etc.); if refractive index values are provided and there is a mismatch, the PSF is adjusted to account for spherical aberration. We did not experimentally distill PSFs from bead measurements, as Huygens’ theoretical PSFs are sufficient for our data.

Both green (GCaMP) and red (mScarlet) channels were processed for ratiometric imaging using the same workflow (stabilization, optional bleaching correction, and deconvolution within Huygens). For each channel, the PSF, background, and SNR were estimated automatically by the same built-in algorithms, so the underlying procedures were identical even though the numerical values differ between channels because of their distinct wavelengths and noise characteristics. Importantly, Huygens normalizes each PSF to unit total intensity, such that the deconvolution itself does not add or remove signal and therefore preserves intensity ratios between channels; only background subtraction and bleaching correction can change absolute fluorescence values. For the mScarlet channel, where we observed modest bleaching (~1.10 over 15 sec), we applied Huygens’ bleaching correction and visually verified that similar structures maintained comparable intensities after correction. For presynaptic GCaMP signals, bleaching over these short recordings was negligible, so we omitted the bleaching-correction step to avoid introducing multiplicative artifacts. This workflow ensures that ratiometric ΔR/R measurements are based on consistently processed, intensity-conserving deconvolved images in both channels.

The number of deconvolution iterations could have had an effect when comparing GCAMP series; please provide an average number of iterations used for at least one experiment. For example, Figure 3, Syt::GCAMP6s, Scar8f & Scar8m, and, if applicable, the maximum number of permissible iterations.

We thank the reviewer for this comment. For all Ca²⁺ imaging datasets, deconvolution in Huygens was performed using the recommended default settings of the CMLE algorithm with a maximum of 30 iterations. The stopping criterion was left at the Huygens default, so the algorithm either converged earlier or, if convergence was not reached, terminated at this 30-iteration limit. No other iteration settings were used across the GCaMP series (lines 555-559).

Please clarify if the 'Express' settings in Huygens changed algorithms or shifted input parameters.

We appreciate the reviewer’s question regarding the Huygens “Express” settings. For clarity, we note that all Ca²⁺ imaging data reported in this manuscript were deconvolved using the “Deconvolution Wizard”, not the “Deconvolution Express” mode. In the Wizard, we explicitly selected the CMLE algorithm (or GMLE in a few STED-related cases as recommended by SVI), using the recommended maximum of 30 iterations, and other recommended settings while allowing Huygens to auto-estimate background and SNR for each channel.Bleaching correction was toggled manually per channel (applied to mScarlet when bleaching was evident, omitted for GCaMP when bleaching was negligible), as described in the revised Methods (lines 553-559).

By contrast, the Deconvolution Express tool in Huygens is a fully automated front-end that can internally adjust both the choice of deconvolution algorithm (e.g., CMLE vs. GMLE/QMLE) and key input parameters such as SNR, number of iterations, and quality threshold based on the selected “smart profile” and the image metadata. In preliminary tests on our datasets, Express sometimes produced results that were either overly smoothed or showed subtle artifacts, so we did not use it for any data included in this study. Instead, we relied exclusively on the Wizard with explicitly controlled settings to ensure consistency and transparency across all GCaMP series and ratiometric analyses.

We suggest including a sample data set, perhaps in Excel, so that future users can beta test on and organize their data in a similar fashion.

We agree that this would be useful, a point shared by R1 above. In response, we have added a sample data set to the GitHub site and included sample ImageJ data along with screenshots to explain the analysis in more detail. These improvements are discussed in the manuscript (lines 705-708).

(3) While the challenges of AZ imaging are mentioned, it is not discussed how the authors tackled each one. What is defined as an active zone? Active zones are usually identified under electron microscopy. Arguably, the limitation of GCaMP-based sensors targeted to individual AZs, being unable to resolve local Ca2+ changes at individual boutons reliably, might be incorrect. This could be a limitation of the optical setup being used here. Please discuss further. What sensor performance do we need to achieve this performance level, and/or what optical setup would we need to resolve such signals?

We appreciate the reviewer’s thoughtful comments and agree that the technical challenges of active zone (AZ) Ca²⁺ imaging merit further clarification. We defined AZs, as is the convention in our field, as individual BRP puncta at NMJs. These BRP puncta co-colocalize with individual puncta of other AZ components, including CAC, RBP, Unc13, etc. ROIs were drawn tightly over individual BRP puncta and only clearly separable spots were included.

To tackle the specific obstacles of AZ imaging (small signal volume, high AZ density, and limited photon budget at high frame rates), we implemented both improved sensors and optimized analysis (Fig. 6). First, we introduced a ratiometric AZ-targeted indicator, BRP::mScarlet3::GCaMP8m (Bar8m), and computed ΔR/R with ΔR/R with R(t)=F_GCaMP8m/F_mScarlet3. ROIs were drawn over individual AZs (Fig. 6B). Under our standard resonant area-scan conditions (~118 fps), Bar8m produces robust ΔR/R transients at individual AZs (example peaks ≈ 3.28; τ_rise≈9.0 ms; Fig. 6C, middle), indicating that single-AZ signals can be detected reproducibly when AZs are optically resolvable.

Second, we increased temporal resolution using high-speed Galvano line-scan imaging (~1058 fps), which markedly sharpened the apparent kinetics (τ_rise≈3.23 ms) and revealed greater between-AZ variability (Fig. 6C, right; 6D–E). Population analyses show that line scans yield much faster rise times than area scans (Fig. 6D) and a dramatically higher fraction of significantly different AZ pairs (8.28% and 4.14% in 8f and 8m areascan vs 78.62% in 8m line-scan, lines 721-725), uncovering pronounced AZ-to-AZ heterogeneity in Ca²⁺ signals. Together, these revisions demonstrate that under our current confocal configuration, AZ-targeted GCaMP8m can indeed resolve local Ca²⁺ changes at individual, optically isolated boutons.

We have revised the Discussion to clarify that our original statement about the limitations of AZ-targeted GCaMPs refers specifically to this combination of sensor and optical setup, rather than an absolute limitation of AZ-level Ca²⁺ imaging. In our view, further improvements in baseline brightness and dynamic range (ΔF/F or ΔR/R per action potential), combined with sub-millisecond kinetics and minimal buffering, together with optical configurations that provide smaller effective PSFs and higher photon collection (e.g., higher-NA objectives, optimized 2-photon or fast line-scan modalities, and potentially super-resolution approaches applied to AZ-localized indicators), are likely to be required to achieve routine, high-fidelity Ca²⁺ measurements at every individual AZ within a neuromuscular junction.

(4) In Figure 5: Only GCAMP8f (Bar8f fusion protein) is tested here. Consider including testing with GCAMP8m. This is particularly relevant given that GCAMP8m was a more successful GECI for subcellular post-synaptic imaging in Figure 6.

We appreciate this point and request by Reviewer 3. The main limitation for detecting local calcium changes at AZs is the speed of the calcium sensor, and hence we used the fastest available (GCaMP8f) to test the Bar8f sensor. While replacing GCaMP8f with GCaMP8m would indeed be predicted to enhance sensitivity (SNR), since GCaMP8m does not have faster kinetics relative to GCaMP8f, it is unlikely to be a more successful GECI for visualizing local calcium differences at AZs. 

That being said, we agree that the Bar8m tool, including the improved mScarlet3 indicator, would likely be of interest and use to the field. Fortunately, we had engineered the Bar8m sensor while this manuscript was in review, and just recently received transgenic flies. We have evaluated this sensor, as requested by the reviewer, and included our findings in Fig. 1 and 6. In short, while the sensitivity is indeed enhanced in Bar8m compared to Bar8f, the kinetics remain insufficient to capture local AZ signals. These findings are discussed in the revised manuscript (lines 424-442, 719-730), and we appreciate the reviewer for raising these important points.

In earlier experiments, Bar8f yielded relatively weak fluorescence, so we traded frame rate for image quality during resonant area scans (~60 fps). After switching to Bar8m, the signal was bright enough to restore our standard 118 fps area-scan setting. Nevertheless, even with dual-channel resonant area scans and ratiometric (GCaMP/mScarlet) analysis, AZ-to-AZ heterogeneity remained difficult to resolve. Because Ca²⁺ influx at individual active zones evolves on sub-millisecond timescales, we adopted a high-speed singlechannel Galvano line-scan (~1 kHz) to capture these rapid transients. We first acquired a brief area image to localize AZ puncta, then positioned the line-scan ROI through the center of the selected AZ. This configuration provided the temporal resolution needed to uncover heterogeneity that was under-sampled in area-scan data. Consistent with this, Bar8m line-scan data showed markedly higher AZ heterogeneity (significant AZ-pair rate ~79%, vs. ~8% for Bar8f area scans and ~4% for Bar8m area scans), highlighting Bar8m’s suitability for quantifying AZ diversity. We have updated the text, Methods, and figure legend accordingly (tell reviewer where to find everything).

(5) Figure 5D and associated datasets: Why was Interquartile Range (IQR) testing used instead of ZScoring? Generally, IQR is used when the data is heavily skewed or is not normally distributed. Normality was tested using the D'Agostino & Pearson omnibus normality test and found that normality was not violated. Please explain your reasoning for the approach in statistical testing. Correlation coefficients in Figures 5 E & F should also be reported on the graph, not just the table. In Supplementary Table 1. The sub-table between 4D-F and 5E-F, which describes the IQR, should be labeled as such and contain identifiers in the rows describing which quartile is described. The table description should be below. We would recommend a brief table description for each sub-table.

Thank you for this helpful suggestion. We have updated the analysis in two complementary ways. First, we now perform paired two-tailed t-tests between every two AZs within the same preparation (pairwise AZ–AZ comparisons of peak responses). At α<0.05, the fraction of significant AZ pairs is ~79% for Bar8m line-scan data versus ~8% for Bar8f area-scan data, indicating markedly greater AZ-to-AZ diversity when measured at high temporal resolution. Second, for visually marking the outlying AZs, we re-computed the IQR (Q1–Q3) based on the individual values collected from each AZs(15 data points per AZ, 30 AZs for each genotype), and marked AZs whose mean response falls above Q3 or below Q1; IQR is used here solely as a robust dispersion reference rather than for hypothesis testing. Both analyses support the same observation: Bar8m line-scan data reveal substantially higher AZ heterogeneity than Bar8f and Bar8m area-scan data. We have revised the Methods, figure panels, and legends accordingly (t-test details; explicit “IQR (Q1–Q3)” labeling; significant AZ-pair rates reported on the plots) (lines 719-730).

(6) Figure 6 and associated data. The authors mention: ' SynapGCaMP quantal signals appeared to qualitatively reflect the same events measured with electrophysiological recordings (Fig. 6D).' If that was the case, shouldn't the ephys and optical signal show some sort of correlation? The data presented in Figure 6D show no such correlation. Where do these signals come from? It is important to show the ROIs on a reference image.

We apologize this was not clear, as similar points were raised by R1 and R2. We were just showing separate (uncorrelated) sample traces of electrophysiological and calcium imaging data. Given how confusing this presentation turned out to be, and the fact that we show the correlated ephys and calcium imaging events in Fig. 7, we have elected to remove the uncorrelated electrophysiological events in Fig. 6 to just focus on the calcium imaging events (now Figures 7 and 8).

Figure 7B: Were Ca2+ transients not associated with mEPSPs ever detected? What is the rate of such events?

This is an astute question. Yes indeed, during simultaneous calcium imaging and current clamp electrophysiology recordings, we occasionally observed GCaMP transients without a detectable mEPSP in the electrophysiological trace. This may reflect the detection limit of electrophysiology for very small minis; with our noise level and the technical limitation of the recording rig, events < ~0.2 mV cannot be reliably detected, whereas the optical signal from the same quantal event might still be detected. The fraction of calcium-only events was ~1–10% of all optical miniature events, depending on genotype (higher in lines with smaller average minis). These calcium-only detections were low-amplitude and clustered near the optical threshold (lines 361-365).

Minor comments

(1) It should be mentioned in the text or figure legend whether images in Figure 1 were deconvolved, particularly since image pre-processing is only discussed in Figure 2 and after.

We thank the reviewer for pointing this out. Yes, the confocal images shown in Figure 1 were also deconvolved in Huygens using the CMLE-based workflow described in the revised Methods. We applied deconvolution to improve contrast, reduce out-of-focus blur, and better resolve the morphology of presynaptic boutons, active zones, and postsynaptic structures, so that the localization of each sensor is more clearly visualized. We have now explicitly stated in the Fig. 1 legend and Methods (lines 575-577) that these images were deconvolved prior to display. 

(2) The abbreviation, SNR, signal-to-noise ratio, is not defined in the text.

We have corrected this error and thank the reviewer for pointing this out.

(3) Please comment on the availability of fly stocks and molecular constructs.

We have clarified that all fly stocks and molecular constructs will be shared upon request (lines 747-750). We are also in the process of depositing the new Scar8f/m, Bar8f/m, and SynapGCaMP sensors to the Bloomington Drosophila Stock Center for public dissemination.

(4) Please add detection wavelengths and filter cube information for live imaging experiments for both confocal and widefield.

We thank the reviewer for this helpful suggestion. We have now added the detection wavelengths and filter cube configurations for both confocal and widefield live imaging to the Methods.

For confocal imaging, GCaMP signals were acquired on a Nikon A1R system using the FITC/GFP channel (488-nm laser excitation; emission collected with a 525/50-nm band-pass filter), and mScarlet signals were acquired using the TRITC/mCherry channel (561-nm laser excitation; emission collected with a 595/50-nm band-pass filter). Both channels were detected with GaAsP detectors under the same pinhole and scan settings described above (lines 512-517).

For widefield imaging, GCaMP was recorded using a GFP filter cube (LED excitation ~470/40 nm; emission ~525/50 nm), which is now explicitly described in the revised Methods section (lines 632-633).

(5) Please include a mini frequency analysis in Supplemental Figure S1.

We apologize for not including this information in the original submission. This is now included in the Supplemental Figure S1.

(6) In Figure S1B, consider flipping the order of EPSP (currently middle) and mEPSP (currently left), to easily guide the reader through the quantification of Figure S1A (EPSPs, top traces & mEPSPs, bottom traces).

We agree these modifications would improve readability and clarity. We have now re-ordered the electrophysiological quantifications in Fig. S1B as requested by the reviewer.

(7) Figure 6C: Consider labeling with sensor name instead of GFP.

We agree here as well, and have removed “GFP” and instead added the GCaMP variant to the heatmap in Fig. 7C.

(8) Figure 6E, 7B, 7E: Main statistical differences highlighting sensor performance should be represented on the figures for clarity.

We did not show these differences in the original submission in an effort to keep the figures “clean” and for clarity, putting the detailed statistical significance in Table S1. However, we agree with the reviewer that it would be easier to see these in the Fig. 6E and 7B,E graphs. This information has now been added the Figs. 7 and 8.

(9) Please report if the significance tested between the ephys mini (WT vs IIB-/-, WT vs IIA-/-, IIB-/- vs IIA-/-) is the same as for Ca2+ mini (WT vs IIB-/-, WT vs IIA-/-, IIB-/- vs IIA-/-). These should also exhibit a very high correlation (mEPSP (mV) vs Ca2+ mini deltaF/F). These tests would significantly strengthen the final statement of "SynapGCaMP8m can capture physiologically relevant differences in quantal events with similar sensitivity as electrophysiology."

We agree that adding the more detailed statistical analysis requested by the reviewer would strengthen the evidence for the resolution of quantal calcium imaging using SynapGCaMP8m. We have included the statistical significance between the ephys and calcium minis in Fig. 8 and included the following in the revised methods (lines 358-361), the Fig. 8 legend and Table S1:

Using two-sample Kolmogorov–Smirnov (K–S) tests, we found that SynapGCaMP8m Ca²⁺ minis (ΔF/F, Fig. 8E) differ significantly across all genotype pairs (WT vs IIB^-/-, WT vs IIA^-/-, IIB^-/- vs IIA^-/-; all p < 0.0001). The genotype rank order of the group means (±SEM) is IIB^-/- > WT > IIA^-/- (0.967 ± 0.036; 0.713 ± 0.021; 0.427 ± 0.017; n=69, 65, 59). For electrophysiological minis (mEPSP amplitude, Fig. 8F), K–S tests likewise show significant differences for the same comparisons (all p < 0.0001) with D statistics of 0.1854, 0.3647, and 0.4043 (WT vs IIB^-/-, WT vs IIA^-/-, IIB^-/- vs IIA^-/-, respectively). Group means (±SEM) again follow IIB^-/- > WT > IIA^-/- (0.824 ± 0.017 mV; 0.636 ± 0.015 mV; 0.383 ± 0.007 mV; n=41 each). These K–S results demonstrate identical significance and rank order across modalities, supporting our conclusion that SynapGCaMP8m resolves physiologically relevant quantal differences with sensitivity comparable to electrophysiology.

References

Blum, Ian D., Mehmet F. Keleş, El-Sayed Baz, Emily Han, Kristen Park, Skylar Luu, Habon Issa, Matt Brown, Margaret C. W. Ho, Masashi Tabuchi, Sha Liu, and Mark N. Wu. 2021. 'Astroglial Calcium Signaling Encodes Sleep Need in Drosophila', Current Biology, 31: 150-62.e7.

Chen, Y., and L. M. Huang. 2017. 'A simple and fast method to image calcium activity of neurons from intact dorsal root ganglia using fluorescent chemical Ca(2+) indicators', Mol Pain, 13: 1744806917748051.

Giovannucci, Andrea, Johannes Friedrich, Pat Gunn, Jérémie Kalfon, Brandon L. Brown, Sue Ann Koay, Jiannis Taxidis, Farzaneh Najafi, Jeffrey L. Gauthier, Pengcheng Zhou, Baljit S. Khakh, David W. Tank, Dmitri B. Chklovskii, and Eftychios A. Pnevmatikakis. 2019. 'CaImAn an open source tool for scalable calcium imaging data analysis', eLife, 8: e38173.

Müller, M., K. S. Liu, S. J. Sigrist, and G. W. Davis. 2012. 'RIM controls homeostatic plasticity through modulation of the readily-releasable vesicle pool', J Neurosci, 32: 16574-85.

Wu, Yifan, Keimpe Wierda, Katlijn Vints, Yu-Chun Huang, Valerie Uytterhoeven, Sahil Loomba, Fran Laenen, Marieke Hoekstra, Miranda C. Dyson, Sheng Huang, Chengji Piao, Jiawen Chen, Sambashiva Banala, Chien-Chun Chen, El-Sayed Baz, Luke Lavis, Dion Dickman, Natalia V. Gounko, Stephan Sigrist, Patrik Verstreken, and Sha Liu. 2025. 'Presynaptic Release Probability Determines the Need for Sleep', bioRxiv: 2025.10.16.682770.

Xing, Xiaomin, and Chun-Fang Wu. 2018. 'Unraveling Synaptic GCaMP Signals: Differential Excitability and Clearance Mechanisms Underlying Distinct Ca²⁺ Dynamics in Tonic and Phasic Excitatory, and Aminergic Modulatory Motor Terminals in Drosophila', eneuro, 5: ENEURO.0362-17.2018.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript addresses an important question: how do circadian clocks adjust to a complex rhythmic environment with multiple daily rhythms? The focus is on the temperature and light cycles (TC and LD) and their phase relationship. In nature, TC usually lags the LD cycle, but the phase delay can vary depending on seasonal and daily weather conditions. The authors present evidence that circadian behavior adjusts to different TC/LD phase relationships, that temperature-sensitive tim splicing patterns might underlie some of these responses, and that artificial selection for preferential evening or morning eclosion behavior impacts how flies respond to different LD/TC phase relationship

Strength:

Experiments are conducted on control strains and strains that have been selected in the laboratory for preferential morning or evening eclosion phenotypes. This study is thus quite unique as it allows us to probe whether this artificial selection impacted how animals respond to different environmental conditions, and thus gives hints on how evolution might shape circadian oscillators and their entrainment. The authors focused on circadian locomotor behavior and timeless (tim) splicing because warm and cold-specific transcripts have been described as playing an important role in determining temperature-dependent circadian behavior. Not surprisingly, the results are complex, but there are interesting observations. In particular, the "late" strain appears to be able to adjust more efficiently its evening peak in response to changes in the phase relationship between temperature and light cycles, but the morning peak seems less responsive in this strain. Differences in the circadian pattern of expression of different tim mRNA isoforms are found under specific LD/TC conditions.

We sincerely thank the reviewer for this generous assessment and for recognizing several key strengths of our study. We are particularly gratified that the reviewer values our use of long-term laboratory-selected chronotype lines (350+ generations), which provide a unique evolutionary perspective on how artificial selection reshapes circadian responses to complex LD/TC phase relationships—precisely our core research question.

Weaknesses:

These observations are interesting, but in the absence of specific genetic manipulations, it is difficult to establish a causative link between tim molecular phenotypes and behavior. The study is thus quite descriptive. It would be worth testing available tim splicing mutants, or mutants for regulators of tim splicing, to understand in more detail and more directly how tim splicing determines behavioral adaptation to different phase relationships between temperature and light cycles. Also, I wonder whether polymorphisms in or around tim splicing sites, or in tim splicing regulators, were selected in the early or late strains.

We thank the reviewer for this insightful comment. We agree that our current data do not establish a direct causal link between tim splicing (or Psi) and behaviour, and we appreciate that some of our wording (e.g. “linking circadian gene splicing to behavioural plasticity” or describing tim splicing as a “pivotal node”) may have suggested unintended causal links. In the revision, we will (i) explicitly state in the Abstract, Introduction, and early Discussion that the main aim was to test whether selection for timing of eclosion is accompanied by correlated evolution of temperature‑dependent tim splicing patterns and evening activity plasticity under complex LD/TC regimes, and (ii) consistently describe the molecular findings as correlational and hypothesis‑generating rather than causal. We will also add phrases throughout the text to point the reader more clearly to existing passages where we already emphasize “correlated evolution” and explicitly label our mechanistic ideas as “we speculate” / “we hypothesize” and as future experiments.

We fully agree that studies using tim splicing mutants or manipulations of splicing regulators under in‑sync and out‑of‑sync LD/TC regimes will be essential to ascertain what role tim variants play under such environmental conditions, and we will highlight this as a key future direction. At the same time, we emphasize that the long‑term selection lines provide a complementary perspective to classical mutant analyses by revealing how behavioural and molecular phenotypes can exhibit correlated evolution under a specific, chronobiologically relevant selection pressure (timing of emergence).

Finally, we appreciate the suggestion regarding polymorphisms. Whole‑genome analyses of these lines in a PhD thesis from our group (Ghosh, 2022, unpublished, doctoral dissertation) reveal significant SNPs in intronic regions of timeless in both Early and Late populations, as well as SNPs in CG7879, a gene implicated in alternative mRNA splicing, in the Late line. Because these analyses are ongoing and not yet peer‑reviewed, we do not present them as main results.

I also have a major methodological concern. The authors studied how the evening and morning phases are adjusted under different conditions and different strains. They divided the daily cycle into 12h morning and 12h evening periods, and calculated the phase of morning and evening activity using circular statistics. However, the non-circadian "startle" responses to light or temperature transitions should have a very important impact on phase calculation, and thus at least partially obscure actual circadian morning and evening peak phase changes. Moreover, the timing of the temperature-up startle drifts with the temperature cycles, and will even shift from the morning to the evening portion of the divided daily cycle. Its amplitude also varies as a function of the LD/TC phase relationship. Note that the startle responses and their changes under different conditions will also affect SSD quantifications.

We thank the reviewer for this perceptive methodological concern, which we had anticipated and systematically quantified but had not included in the original submission. The reviewer is absolutely correct that non-circadian startle responses to zeitgeber transitions could confound both circular phase (CoM) calculations and SSD quantifications, particularly as TC drift creates shifting startle locations across morning/evening windows.

We will be including startle response quantification (previously conducted but unpublished) as new a Supplementary figure, systematically measuring SSD in 1-hour windows immediately following each of the four environmental transitions (lights-ON, lights-OFF, temperature rise and temperature fall) across all six LDTC regimes (2-12hr TC-LD lags) for all 12 selection lines (early_1-4, control_1-4, late_1-4).

Author response image 1.

Startle responses in selection lines under LDTC regimes: SSD calculated to assess startle response to each of the transitions (1-hour window after the transition used for calculations). Error bars are 95% Tukey’s confidence intervals for the main effect of selection in a two-factor ANOVA design with block as a random factor. Non-overlapping error bars indicate significant differences among the values. SSD values between in-sync and out-of-sync regimes for a range of phase relationships between LD and TC cycles (A) LDTC 2-hr, (B) LDTC 4-hr, (C) LDTC 6-hr, (D) LDTC 8-hr, (E) LDTC 10-hr, (F) LDTC 12-hr.

Key findings directly addressing the reviewer's concerns:

(1) Morning phase advances in LDTC 8-12hr regimes are explained by quantified nocturnal startle activity around temperature rise transitions occurring within morning windows. Critically, these startles show no selection line differences, confirming they represent equivalent non-circadian confounds across lines.

(2) Early selection lines exhibit significantly heightened startle responses specifically to temperature rise in LDTC 4hr and 6hr regimes (early > control ≥ late), demonstrating that startle responses themselves exhibit correlated evolution with emergence timing—an important novel finding that strengthens our evolutionary story.

(3) Startle responses differed among selection lines only for the temperature rise transition under two of the regimes used, LDTC 4 hr and 6 hr regimes. Under LDTC 4 hr, temperature rise transition falls in the morning window and despite early having significantly greater startle than late, the overall morning SSD (over 12 hours morning window) did not differ significantly among the selection lines for this regime. Thus, eliminating the startle window would make the selection lines more similar to one another. On the other hand, under LDTC 6 hour regime, the startle response to temperature rise falls in the evening 12 hour window. In this case too, early showed higher startle than control and late. A higher startle in early would thus, contribute to the observed differences among selection lines. We agree with the reviewer that eliminating this startle peak would lead to a clearer interpretation of the change in circadian evening activity.

We deliberately preserved all behavioural data without filtering out startle windows since it would require arbitrary cutoffs like 1 hr, 2 hr or 3 hours post transitions or until the startle peaks declines in different selection lines under different regimes. In the revised version, we will add complementary analyses excluding the startle windows to obtain mean phase and SSD values which are unaffected by the startle responses.

For the circadian phase, these issues seem, for example, quite obvious for the morning peak in Figure 1. According to the phase quantification on panel D, there is essentially no change in the morning phase when the temperature cycle is shifted by 6 hours compared to the LD cycle, but the behavior trace on panel B clearly shows a phase advance of morning anticipation. Comparison between the graphs on panels C and D also indicates that there are methodological caveats, as they do not correlate well.

Because of the various masking effects, phase quantification under entrainment is a thorny problem in Drosophila. I would suggest testing other measurements of anticipatory behavior to complement or perhaps supersede the current behavior analysis. For example, the authors could employ the anticipatory index used in many previous studies, measure the onset of morning or evening activity, or, if more reliable, the time at which 50% of anticipatory activity is reached. Termination of activity could also be considered. Interestingly, it seems there are clear effects on evening activity termination in Figure 3. All these methods will be impacted by startle responses under specific LD/TC phase relationships, but their combination might prove informative.

We agree that phase quantification under entrained conditions in Drosophila is challenging and that anticipatory indices, onset/offset measures, and T50 metrics each have particular strengths and weaknesses. In designing our analysis, we chose to avoid metrics that require arbitrary or subjective criteria (e.g. defining activity thresholds or durations for anticipation, or visually marking onset/offset), because these can substantially affect the estimated phase and reduce comparability across regimes and genotypes. Instead, we used two fully quantitative, parameter-free measures applied to the entire waveform within defined windows: (i) SSD to capture waveform change in shape/amplitude and (ii) circular mean phase of activity (CoM) restricted to the 12 h morning and 12 h evening windows. By integrating over the entire window, these measures are less sensitive to the exact choice of threshold and to short-lived, high-amplitude startles at transitions, and they treat all bins within the window in a consistent, reproducible way across all LDTC regimes and lines. Panels C (SSD) and D (CoM) are intentionally complementary, not redundant: SSD reflects how much the waveform changes in shape and amplitude, whereas CoM reflects the timing of the center of mass of activity. Under conditions where masking alters amplitude and introduces short-lived bouts without a major shift of the main peak, it is expected that SSD and CoM will not correlate linearly across regimes.

We will be including a detailed calculation of how CoM is obtained in our methods for the revised version.  

Reviewer #2 (Public review):

Summary:

The authors aimed to dissect the plasticity of circadian outputs by combining evolutionary biology with chronobiology. By utilizing Drosophila strains selected for "Late" and "Early" adult emergence, they sought to investigate whether selection for developmental timing co-evolves with plasticity in daily locomotor activity. Specifically, they examined how these diverse lines respond to complex, desynchronized environmental cues (temperature and light cycles) and investigated the molecular role of the splicing factor Psi and timeless isoforms in mediating this plasticity.

Major strengths and weaknesses:

The primary strength of this work is the novel utilization of long-term selection lines to address fundamental questions about how organisms cope with complex environmental cues. The behavioral data are compelling, clearly demonstrating that "Late" and "Early" flies possess distinct capabilities to track temperature cycles when they are desynchronized from light cycles.

We sincerely thank the reviewer for this enthusiastic recognition of our study's core strengths. We are particularly gratified that the reviewer highlights our novel use of long-term selection lines (350+ generations) as the primary strength, enabling us to address fundamental evolutionary questions about circadian plasticity under complex environmental cues. We thank them for identifying our behavioral data as compelling (Figs 1, 3), which robustly demonstrate selection-driven divergence in temperature cycle tracking.

However, a significant weakness lies in the causal links proposed between the molecular findings and these behavioral phenotypes. The molecular insights (Figures 2, 4, 5, and 6) rely on mRNA extracted from whole heads. As head tissue is dominated by photoreceptor cells and glia rather than the specific pacemaker neurons (LNv, LNd) driving these behaviors, this approach introduces a confound. Differential splicing observed here may reflect the state of the compound eye rather than the central clock circuit, a distinction highlighted by recent studies (e.g., Ma et al., PNAS 2023).

We thank the reviewer for highlighting this important methodological consideration. We fully agree that whole-head extracts do not provide spatial resolution to distinguish central pacemaker neurons (~100-200 total) from compound eyes and glia, and that cell-type-specific profiling represents the critical next experimental step. As mentioned in our response to Reviewer 1, we appreciate the issue with our phrasing and will be revising it accordingly to more clearly describe that we do not claim any causal connections between expression of the tim splice variants in particular circadian neurons and their contribution of the phenotype observed.

We chose whole-head extracts for practical reasons aligned with our study's specific goals:

(1) Fly numbers: Our artificially selected populations are maintained at large numbers (~1000s per line). Whole-head extracts enabled sampling ~150 flies per time point = ~600 flies per genotype per environmental, providing means to faithfully sample the variation that may exist in such randomly mating populations.

(2) Established method for characterizing splicing patterns: The majority of temperature-dependent period/timeless splicing studies have successfully used whole-head extracts (Majercak et al., 1999; Shakhmantsir et al., 2018; Martin Anduaga et al., 2019) to characterize splicing dynamics under novel conditions.

(3) Novel environmental regimes: Our primary molecular contribution was documenting timeless splicing patterns under previously untested LDTC phase relationships (TC 2-12hr lags relative to LD) and testing whether these exhibit selection-dependent differences consistent with behavioral divergence.

Furthermore, while the authors report that Psi mRNA loses rhythmicity under out-of-sync conditions, this correlation does not definitively prove that Psi oscillation is required for the observed splicing patterns or behavioral plasticity. The amplitude of the reported Psi rhythm is also low (~1.5 fold) and variable, raising questions about its functional significance in the absence of manipulation experiments (such as constitutive expression) to test causality.

We thank the reviewer for this insightful comment and appreciate that our phrasing has been misleading. We will especially pay attention to this issue, raised by two reviewers, and clearly highlight our results as correlated evolution and hypothesis-generating.

We appreciate the reviewer highlighting these points and would like to draw attention to the following points in our Discussion section:

“Psi and levels of tim-cold and tim-sc (Foley et al., 2019). We observe that this correlation is most clearly upheld under temperature cycles wherein tim-medium and Psi peak in-phase while the cold-induced transcripts start rising when Psi falls (Figure 8A1&2). Under LDTC in-sync conditions this relationship is weaker, even though Psi is rhythmic, potentially due to light-modulated factors influencing timeless splicing (Figure 8B1&2). This is in line with Psi’s established role in regulating activity phasing under TC 12:12 but not LD 12:12 (Foley et al., 2019). This is also supported by the fact that while tim-medium and tim-cold are rhythmic under LD 12:12 (Shakhmantsir et al., 2018), Psi is not (datasets from Kuintzle et al., 2017; Rodriguez et al., 2013). Assuming this to be true across genetic backgrounds and sexes and combined with our similar findings for these three transcripts under LDTC out-of-sync (Figure 2B3, D3&E3), we speculate that Psi rhythmicity may not be essential for tim-medium or tim-cold rhythmicity especially under conditions wherein light cycles are present along with temperature cycles (Figure 8C1&2). Our study opens avenues for future experiments manipulating PSI expression under varying light-temperature regimes to dissect its precise regulatory interactions. We hypothesize that flies with Psi knocked down in the clock neurons should exhibit a less pronounced shift of the evening activity under the range LDTC out-of-sync conditions for which activity is assayed in our study. On the other hand, its overexpression should cause larger delays in response to delayed temperature cycles due to the increased levels of tim-medium translating into delay in TIM protein accumulation.”

Appraisal of aims and conclusions:

The authors successfully demonstrate the co-evolution of emergence timing and activity plasticity, achieving their aim on the behavioral level. However, the conclusion that the specific molecular mechanism involves the loss of Psi rhythmicity driving timeless splicing changes is not yet fully supported by the data. The current evidence is correlative, and without spatial resolution (specific clock neurons) or causal manipulation, the mechanistic model remains speculative.

This study is likely to be of significant interest to the chronobiology and evolutionary biology communities as it highlights the "enhanced plasticity" of circadian clocks as an adaptive trait. The findings suggest that plasticity to phase lags - common in nature where temperature often lags light - may be a key evolutionary adaptation. Addressing the mechanistic gaps would significantly increase the utility of these findings for understanding the molecular basis of circadian plasticity.

Thank you for this thoughtful appraisal affirming our successful demonstration of co-evolution between emergence timing and circadian activity plasticity.

Reviewer #3 (Public review):

Summary:

This study attempts to mimic in the laboratory changing seasonal phase relationships between light and temperature and determine their effects on Drosophila circadian locomotor behavior and on the underlying splicing patterns of a canonical clock gene, timeless. The results are then extended to strains that have been selected over many years for early or late circadian phase phenotypes.

Strengths:

A lot of work, and some results showing that the phasing of behavioural and molecular phenotypes is slightly altered in the predicted directions in the selected strains.

We thank the reviewer for acknowledging the substantial experimental effort across 7 environmental regimes (6 LDTC phase relationships + LDTC in-phase), 12 replicate populations (early_1-4, control_1-4, late_1-4), and comprehensive behavioural + molecular phenotyping.

Weaknesses:

The experimental conditions are extremely artificial, with immediate light and temperature transitions compared to the gradual changes observed in nature. Studies in the wild have shown how the laboratory reveals artifacts that are not observed in nature. The behavioural and molecular effects are very small, and some of the graphs and second-order analyses of the main effects appear contradictory. Consequently, the Discussion is very speculative as it is based on such small laboratory effects.

We thank the reviewer for these important points regarding ecological validity, effect sizes, and interpretation scope.

(1) Behavioural effects are robust across population replicates in selection lines (not small/weak)

Our study assayed 12  populations total (4 replicate populations each of early, control, and late selection lines) under 7 LDTC regimes. Critically, selection effects were consistent across all 4 replicate populations within each selection line for every condition tested. In these randomly mating large populations, the mixed model ANOVA reveals highly significant selection×regime interactions [F(5,45)=4.1, p=0.003; Fig 3E, Table S2], demonstrating strong, replicated evolutionary divergence in evening temperature sensitivity.

(2) Molecular effects test critical evolutionary hypothesis

As stated in our Introduction, "selection can shape circadian gene splicing and temperature responsiveness" (Low et al., 2008, 2012). Our laboratory-selected chronotype populations—known to exhibit evolved temperature responsiveness (Abhilash et al., 2019, 2020; Nikhil et al., 2014; Vaze et al., 2012)—provide an apt system to test whether selection for temporal niche leads to divergence in timeless splicing. With ~600 heads per environmental regime per selection line, we detect statistically robust, selection line-specific temporal profiles [early4 advanced timeless phase (Fig 4A4); late4 prolonged tim-cold (Fig 5A4); significant regime×selection×time interactions (Tables S3-S5)], providing initial robust evidence of correlated molecular evolution under novel LDTC regimes.

(3) Systematic design fills critical field gap

Artificial conditions like LD/DD have been useful in revealing fundamental zeitgeber principles. Our systematic 2-12hr TC-LD lags directly implement Pittendrigh & Bruce (1959) + Oda & Friesen (2011) validated design, which discuss how such experimental designs can provide a more comprehensive understanding of zeitgeber integration compared to studies with only one phase jump between two zeitgebers.

(4) Ramping regimes as essential next step

Gradual ramping regimes better mimic nature and represent critical future experiments. New Discussion addition in the revised version: "Ramping LDTC regimes can test whether selection-specific zeitgeber hierarchy persists under naturalistic gradients." While ramping experiments are essential, we would like to emphasize that we aimed to use this experimental design as a tool to test if evening activity exhibits greater temperature sensitivity and if this property of the circadian system can undergo correlated evolution upon selection for timing of eclosion/emergence.

(5) New startle quantification addresses masking

Our startle quantification (which will be added as a new supplementary figure) confirms circadian evening tracking persists despite quantified, selection-independent masking in most of the regimes.

Reviewer #3 (Public review):

Summary:

The work by Azur and colleagues makes use of the TEMPO (Temporal Encoding and Manipulation in a Predefined Order) methodology to trace cortical neurogenesis in combination with overexpression of Imp1. Imp1 is a mammalian homologue of the Drosophila Imp, which has been shown to control temporal identity in a stem cell context. In their work, they show that overexpression of Imp1 in radial glia, which generate neurons and macroglia in a sequential manner during cortical development, leads to a disruption of faithful neuron/glia generation. They show that continuous overexpression leads to a distinct phenotypic outcome when compared to paradigms where Imp1 was specifically overexpressed in defined temporal windows, enabled by the unique TEMPO approach. Interestingly, the observed phenotype with 'ectopic' generation of mainly lower cortical layer neurons appears not to be due to migration deficits. Strikingly, the overexpression of Imp1 specifically at later stages also leads to ectopic glia-like foci throughout the developing cortical plate. Altogether, the new data provide new insights regarding the role of the post-transcriptional Imp1 regulator in controlling temporal fate in radial glia for the faithful generation of neurons and glia during cortical development.

Strengths:

The TEMPO approach provides excellent experimental access to probe Imp1 gene function at defined temporal windows. The data is very robust and convincing. The overexpression paradigm and its associated phenotypes match very well the expected outcome based on Imp1 loss-of-function. Overall, the study contributes significantly to our understanding of the molecular cues that are associated with the temporal progression of radial glia fate potential during cortical development.

Weaknesses:

The authors provide some experimental evidence, including live imaging, that deficits related to Imp1 overexpression and subsequent overabundance of lower-layer neurons, or accumulation at the subplate, appear to evolve independently of neuronal migration deficits. However, the analysis at the population level might not suffice to make the claim robust. To analyze neuronal migration in more depth, the authors could trace individual neurons and establish speed and directional parameters for comparison.

In their analysis, the authors mainly rely on temporal parameters/criteria to associate the generation of certain neuron fates. While two markers were used to identify the neuronal fate, the variance seems quite high. The authors could consider utilizing an antibody against Satb2, which would provide additional data points that could help to establish statistical significance in some of the analyses.

The analysis of glia was done at postnatal day 10, although gliogenesis and, in particular, astrocyte maturation last at least until postnatal day 28. The authors could consider extending their analysis to capture the full spectrum of their astrocyte phenotype.

The author baiscally supports his point by describing his experience working across many operating systems. This shows that the issues he mentions come from actual technical experience.

Reviewer #2 (Public review):

Summary:

Tan et al. examined how multivoxel patterns shift in time windows surrounding event boundaries caused by both prediction errors and prediction uncertainty. They observed that some regions of the brain show earlier pattern shifts than others, followed by periods of increased stability. The authors combine their recent computational model to estimate event boundaries that are based on prediction error vs. uncertainty and use this to examine the moment-to-moment dynamics of pattern changes. I believe this is a meaningful contribution that will be of interest to memory, attention, and complex cognition research.

Strengths:

The authors have shown exceptional transparency in terms of sharing their data, code, and stimuli which is beneficial to the field for future examinations and to the reproduction of findings. The manuscript is well written with clear figures. The study starts from a strong theoretical background to understand how the brain represents events and have used a well-curated set of stimuli. Overall, the authors extend the event segmentation theory beyond prediction error to include prediction uncertainty which is an important theoretical shift that has implications in episodic memory encoding, use of semantic and schematic knowledge and to attentional processing.

Weaknesses:

(1) I am not fully satisfied with the author's explanation of pattern shifts occurring 11.9s prior to event boundaries. The average length of time for an event was 21.4 seconds. The window around the identified event boundaries was 20 seconds on either side. The earliest identified pattern shift peaks occur at 11.9s prior to the actual event boundary. This would mean on average, a pattern shift is occurring approximately at the midway point of the event (11.9s prior to a boundary of a 21.4s event is approx. the middle of an event). The authors offer up an explanation in which top down regions signal an update that propagates to lower order regions closer to the boundary. To make this interpretation concrete, they added an example: "in a narrative where a goal is reached midway-for instance, a mystery solved before the story formally ends-higher-order regions may update the event representation at that point, and this updated model then cascades down to shape processing in lower-level regions". This might make sense in a one-off case of irregular storytelling, but it is odd to think this would generalize. If an event is occurring and a given collection of regions represent that event, it doesn't follow the accepted convention of multivariate representational analysis that that set of regions would undergo such a large shift in patterns in the middle of an event. The stabilization of these patterns taking so long is also odd to me. I suspect some of these findings may be due to the stimuli used in this experiment and I am not confident this would generalize and invite the authors to disagree and explain. In the case of the exercise routine video, I try to imagine going from the push-up event to the jumping jack event. The actor stops doing pushups, stands up, and moves minimally for 16 seconds (these lulls are not uncommon). At that point they start doing jumping jacks. It is immediately evident from that moment on that jumping jacks will be the kind of event you are perceiving which may explain the long delay in event pattern stabilisation. Then about 11.9s prior to the end of the event, when the person is still performing jumping jacks (at this point they have been performing jumping jacks for 6 seconds), I would expect the brain to still be expecting this " jumping jacks event". For some reason at this point multivariate patterns in higher order regions shift. I do not understand what kind of top down processing is happening here and the reviewers need to be more concrete in their explanation because as of right now it is ill-defined. I also recognize that being specific to jumping jacks is maybe unfair, but this would apply to the push-ups, granola bar eating, or table cleaning events in the same manner. I suspect one possibility is that the participants realize that the stereotyped action of jumping jacks is going to continue and, thus, mindwander to other thoughts while waiting for novel, informative information to be presented. This explanation would challenge the more active top down processing assumed by the authors.

I had provided a set of concerns to the authors that were not part of the public review and were not addressed. I was unaware of the exact format of the eLife approach, but I think they are worth open discussion so I am adding them here for consideration. Apologies for any confusion.

(2) Why did the authors not examine event boundary activity magnitude differences from the uncertainty vs error boundaries? I see that the authors have provided the data on the openneuro. However, it seems like the difference in activity maps would not only provide extra contextualization of the findings, but also be fairly trivial. Just by eye-balling the plots, it appears as though there may be activity differences in the mPFC occurring shortly after a boundary between the two. Given this regions role in prediction error and schema, it would be important to understand whether this difference is merely due to thresholding effects or is statistically meaningful.

(3) Further, the authors omitted all subcortical regions some of which would be especially interesting such as the hippocampus, basal ganglia, ventral tegmental area. These regions have a rich and deep background in event boundary activity, and prediction error. Univariate effects in these regions may provide interesting effects that might contextualize some of the pattern shifts in the cortex.

(3) I see that field maps were collected, but the fmriprep methods state that susceptibility distortion correction was not performed. Is there a reason to omit this?

(4) How many events were present in the stimuli?

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This paper investigates the control signals that drive event model updating during continuous experience. The authors apply predictions from previously published computational models to fMRI data acquired while participants watched naturalistic video stimuli. They first examine the time course of BOLD pattern changes around human-annotated event boundaries, revealing pattern changes preceding the boundary in anterior temporal and then parietal regions, followed by pattern stabilization across many regions. The authors then analyze time courses around boundaries generated by a model that updates event models based on prediction error and another that uses prediction uncertainty. These analyses reveal overlapping but partially distinct dynamics for each boundary type, suggesting that both signals may contribute to event segmentation processes in the brain.

Strengths:

(1) The question addressed by this paper is of high interest to researchers working on event cognition, perception, and memory. There has been considerable debate about what kinds of signals drive event boundaries, and this paper directly engages with that debate by comparing prediction error and prediction uncertainty as candidate control signals.

(2) The authors use computational models that explain significant variance in human boundary judgments, and they report the variance explained clearly in the paper.

(3) The authors' method of using computational models to generate predictions about when event model updating should occur is a valuable mechanistic alternative to methods like HMM or GSBS, which are data-driven.

(4) The paper utilizes an analysis framework that characterizes how multivariate BOLD pattern dissimilarity evolves before and after boundaries. This approach offers an advance over previous work focused on just the boundary or post-boundary points.

We appreciate this reviewer’s recognition of the significance of this research problem, and of the value of the approach taken by this paper.

Weaknesses:

(1) While the paper raises the possibility that both prediction error and uncertainty could serve as control signals, it does not offer a strong theoretical rationale for why the brain would benefit from multiple (empirically correlated) signals. What distinct advantages do these signals provide? This may be discussed in the authors' prior modeling work, but is left too implicit in this paper.

We added a brief discussion in the introduction highlighting the complementary advantages of prediction error and prediction uncertainty, and cited prior theoretical work that elaborates on this point. Specifically, we now note that prediction error can act as a reactive trigger, signaling when the current event model is no longer sufficient (Zacks et al., 2007). In contrast, prediction uncertainty is framed as proactive, allowing the system to prepare for upcoming changes even before they occur (Baldwin & Kosie, 2021; Kuperberg, 2021). Together, this makes clearer why these two signals could each provide complementary benefits for effective event model updating.

"One potential signal to control event model updating is prediction error—the difference between the system’s prediction and what actually occurs. A transient increase in prediction error is a valid indicator that the current model no longer adequately captures the current activity. Event Segmentation Theory (EST; Zacks et al., 2007) proposes that event models are updated when prediction error increases beyond a threshold, indicating that the current model no longer adequately captures ongoing activity. A related but computationally distinct proposal is that prediction uncertainty (also termed "unpredictability") can serve as a control signal (Baldwin & Kosie, 2021). The advantage of relying on prediction uncertainty to detect event boundaries is that it is inherently proactive: the cognitive system can start looking for cues about what might come next before the next event starts (Baldwin & Kosie, 2021; Kuperberg, 2021). "

(2) Boundaries derived from prediction error and uncertainty are correlated for the naturalistic stimuli. This raises some concerns about how well their distinct contributions to brain activity can be separated. The authors should consider whether they can leverage timepoints where the models make different predictions to make a stronger case for brain regions that are responsive to one vs the other.

We addressed this concern by adding an analysis that explicitly tests the unique contributions of prediction error– and prediction uncertainty–driven boundaries to neural pattern shifts. In the revised manuscript, we describe how we fit a combined FIR model that included both boundary types as predictors and then compared this model against versions with only one predictor. This allowed us to identify the variance explained by each boundary type over and above the other. The results revealed two partially dissociable sets of brain regions sensitive to error- versus uncertainty-driven boundaries (see Figure S1), strengthening our argument that these signals make distinct contributions.

"To account for the correlation between uncertainty-driven boundaries and error-driven boundaries, we also fitted a FIR model that predicted pattern dissimilarity from both types of boundaries (combined FIR) for each parcel. Then, we performed two likelihood ratio tests: combined FIR to error FIR, which measures the unique contribution of uncertainty boundaries to pattern dissimilarity, and combined FIR to uncertainty FIR, which measures the unique contribution of error boundaries to pattern dissimilarity. The analysis also revealed two dissociable sets of brain regions associated with each boundary type (see Figure S1)."

(3) The authors refer to a baseline measure of pattern dissimilarity, which their dissimilarity measure of interest is relative to, but it's not clear how this baseline is computed. Since the interpretation of increases or decreases in dissimilarity depends on this reference point, more clarity is needed.

We clarified how the FIR baseline is estimated in the methods section. Specifically, we now explain that the FIR coefficients should be interpreted relative to a reference level, which reflects the expected dissimilarity when timepoints are far from an event boundary. This makes it clear what serves as the comparison point for observed increases or decreases in dissimilarity.

"The coefficients from the FIR model indicate changes relative to baseline, which can be conceptualized as the expected value when far from event boundaries."

(4) The authors report an average event length of ~20 seconds, and they also look at +20 and -20 seconds around each event boundary. Thus, it's unclear how often pre- and post-boundary timepoints are part of adjacent events. This complicates the interpretations of the reported time courses.

This is related to reviewer's 2 comment, and it will be addressed below.

(5) The authors describe a sequence of neural pattern shifts during each type of boundary, but offer little setup of what pattern shifts we might expect or why. They also offer little discussion of what cognitive processes these shifts might reflect. The paper would benefit from a more thorough setup for the neural results and a discussion that comments on how the results inform our understanding of what these brain regions contribute to event models.

We thank the reviewer for this advice on how better to set the context for the different potential outcomes of the study. We expanded both the introduction and discussion to better set up expectations for neural pattern shifts and to interpret what these shifts may reflect. In the introduction, we now describe prior findings showing that sensory regions tend to update more quickly than higher-order multimodal regions (Baldassano et al., 2017; Geerligs et al., 2021, 2022), and we highlight that it remains unclear whether higher-order updates precede or follow those in lower-order regions. We also note that our analytic approach is well-suited to address this open question. In the discussion, we then interpret our results in light of this framework. Specifically, we describe how we observed early shifts in higher-order areas such as anterior temporal and prefrontal cortex, followed by shifts in parietal and dorsal attention regions closer to event boundaries. This pattern runs counter to the traditional bottom-up temporal hierarchy view and instead supports a model of top-down updating, where high-level representations are updated first and subsequently influence lower-level processing (Friston, 2005; Kuperberg, 2021). To make this interpretation concrete, we added an example: in a narrative where a goal is reached midway—for instance, a mystery solved before the story formally ends—higher-order regions may update the event representation at that point, and this updated model then cascades down to shape processing in lower-level regions. Finally, we note that the widespread stabilization of neural patterns after boundaries may signal the establishment of a new event model.

Excerpt from Introduction:

“More recently, multivariate approaches have provided insights into neural representations during event segmentation. One prominent approach uses hidden Markov models (HMMs) to detect moments when the brain switches from one stable activity pattern to another (Baldassano et al., 2017) during movie viewing; these periods of relative stability were referred to as "neural states" to distinguish them from subjectively perceived events. Sensory regions like visual and auditory cortex showed faster transitions between neural states. Multi-modal regions like the posterior medial cortex, angular gyrus, and intraparietal sulcus showed slower neural state shifts, and these shifts aligned with subjectively reported event boundaries. Geerligs et al. (2021, 2022) employed a different analytical approach called Greedy State Boundary Search (GSBS) to identify neural state boundaries. Their findings echoed the HMM results: short-lived neural states were observed in early sensory areas (visual, auditory, and somatosensory cortex), while longer-lasting states appeared in multi-modal regions, including the angular gyrus, posterior middle/inferior temporal cortex, precuneus, anterior temporal pole, and anterior insula. Particularly prolonged states were found in higher-order regions such as lateral and medial prefrontal cortex.

The previous evidence about evoked responses at event boundaries indicates that these are dynamic phenomena evolving over many seconds, with different brain areas showing different dynamics (Ben-Yakov & Henson, 2018; Burunat et al., 2024; Kurby & Zacks, 2018; Speer et al., 2007; Zacks, 2010). Less is known about the dynamics of pattern shifts at event boundaries (e.g. whether shifts observed in higher-order regions precedes or follow shifts observed in lower-level regions), because the HMM and GSBS analysis methods do not directly provide moment-by-moment measures of pattern shifts. Both the spatial and temporal aspects of evoked responses and pattern shifts at event boundaries have the potential to provide evidence about two potential control processes (error-driven and uncertainty-driven) for event model updating.”

Excerpt from Discussion:

“We first characterized the neural signatures of human event segmentation by examining both univariate activity changes and multivariate pattern changes around subjectively identified event boundaries. Using multivariate pattern dissimilarity, we observed a structured progression of neural reconfiguration surrounding human-identified event boundaries. The largest pattern shifts were observed near event boundaries (~4.5s before) in dorsal attention and parietal regions; these correspond with regions identified by Geerligs et. al as shifting their patterns on a fast to intermediate timescale (2022). We also observed smaller pattern shifts roughly 12 seconds prior to event boundaries in higher-order regions within anterior temporal cortex and prefrontal cortex, and these are slow-changing regions identified by Geerligs et. al (2022). This is puzzling. One prevalent proposal, based on the idea of a cortical hierarchy of increasing temporal receptive windows (TRWs), suggests that higher-order regions should update representations after lower-order regions do (Chang et al., 2021). In this view, areas with shorter TRWs (e.g., word-level processors) pass information upward, where it is integrated into progressively larger narrative units (phrases, sentences, events). This proposal predicts neural shifts in higher-order regions to follow those in lower-order regions. By contrast, our findings indicate the opposite sequence. Our findings suggest that the brain might engage in top-down event representation updating, with changes in coarser-grain representations propagating downward to influence finer-grain representations. (Friston, 2005; Kuperberg, 2021). For example, in a narrative where the main goal is achieved midway—such as a detective solving a mystery before the story formally ends—higher-order regions might update the overarching event representation at that point, and this updated model could then cascade down to reconfigure how lower-level regions process the remaining sensory and contextual details. In the period after a boundary (around +12 seconds), we found widespread stabilization of neural patterns across the brain, suggesting the establishment of a new event model. Future work could focus on understanding the mechanisms behind the temporal progression of neural pattern changes around event boundaries.”

Reviewer #2 (Public review):

Summary:

Tan et al. examined how multivoxel patterns shift in time windows surrounding event boundaries caused by both prediction errors and prediction uncertainty. They observed that some regions of the brain show earlier pattern shifts than others, followed by periods of increased stability. The authors combine their recent computational model to estimate event boundaries that are based on prediction error vs. uncertainty and use this to examine the moment-to-moment dynamics of pattern changes. I believe this is a meaningful contribution that will be of interest to memory, attention, and complex cognition research.

Strengths:

The authors have shown exceptional transparency in terms of sharing their data, code, and stimuli, which is beneficial to the field for future examinations and to the reproduction of findings. The manuscript is well written with clear figures. The study starts from a strong theoretical background to understand how the brain represents events and has used a well-curated set of stimuli. Overall, the authors extend the event segmentation theory beyond prediction error to include prediction uncertainty, which is an important theoretical shift that has implications in episodic memory encoding, the use of semantic and schematic knowledge, and attentional processing.

We thank the reader for their support for our use of open science practices, and for their appreciation of the importance of incorporating prediction uncertainty into models of event comprehension.

Weaknesses:

The data presented is limited to the cortex, and subcortical contributions would be interesting to explore. Further, the temporal window around event boundaries of 20 seconds is approximately the length of the average event (21.4 seconds), and many of the observed pattern effects occur relatively distal from event boundaries themselves, which makes the link to the theoretical background challenging. Finally, while multivariate pattern shifts were examined at event boundaries related to either prediction error or prediction uncertainty, there was no exploration of univariate activity differences between these two different types of boundaries, which would be valuable.

The fact that we observed neural pattern shifts well before boundaries was indeed unexpected, and we now offer a more extensive interpretation in the discussion section. Specifically, we added text noting that shifts emerged in higher-order anterior temporal and prefrontal regions roughly 12 seconds before boundaries, whereas shifts occurred in lower-level dorsal attention and parietal regions closer to boundaries. This sequence contrasts with the traditional bottom-up temporal hierarchy view and instead suggests a possible top-down updating mechanism, in which higher-order representations reorganize first and propagate changes to lower-level areas (Friston, 2005; Kuperberg, 2021). (See excerpt for Reviewer 1’s comment #5.)

With respect to univariate activity, we did not find strong differences between error-driven and uncertainty-driven boundaries. This makes the multivariate analyses particularly informative for detecting differences in neural pattern dynamics. To support further exploration, we have also shared the temporal progression of univariate BOLD responses on OpenNeuro (BOLD_coefficients_brain_animation_pe_SEM_bold.html and BOLD_coefficients_brain_animation_uncertainty_SEM_bold.html in the derivatives/figures/brain_maps_and_timecourses/ directory; https://doi.org/10.18112/openneuro.ds005551.v1.0.4) for interested researchers.

Reviewer #3 (Public review):

Summary:

The aim of this study was to investigate the temporal progression of the neural response to event boundaries in relation to uncertainty and error. Specifically, the authors asked (1) how neural activity changes before and after event boundaries, (2) if uncertainty and error both contribute to explaining the occurrence of event boundaries, and (3) if uncertainty and error have unique contributions to explaining the temporal progression of neural activity.

Strengths:

One strength of this paper is that it builds on an already validated computational model. It relies on straightforward and interpretable analysis techniques to answer the main question, with a smart combination of pattern similarity metrics and FIR. This combination of methods may also be an inspiration to other researchers in the field working on similar questions. The paper is well written and easy to follow. The paper convincingly shows that (1) there is a temporal progression of neural activity change before and after an event boundary, and (2) event boundaries are predicted best by the combination of uncertainty and error signals.

We thank the reviewer for their thoughtful and supportive comments, particularly regarding the use of the computational model and the analysis approaches.

Weaknesses:

(1) The current analysis of the neural data does not convincingly show that uncertainty and prediction error both contribute to the neural responses. As both terms are modelled in separate FIR models, it may be that the responses we see for both are mostly driven by shared variance. Given that the correlation between the two is very high (r=0.49), this seems likely. The strong overlap in the neural responses elicited by both, as shown in Figure 6, also suggests that what we see may mainly be shared variance. To improve the interpretability of these effects, I think it is essential to know whether uncertainty and error explain similar or unique parts of the variance. The observation that they have distinct temporal profiles is suggestive of some dissociation,but not as convincing as adding them both to a single model.

We appreciate this point. It is closely related to Reviewer 1's comment 2; please refer to our response above.

(2) The results for uncertainty and error show that uncertainty has strong effects before or at boundary onset, while error is related to more stabilization after boundary onset. This makes me wonder about the temporal contribution of each of these. Could it be the case that increases in uncertainty are early indicators of a boundary, and errors tend to occur later?

We also share the intuition that increases in uncertainty are early indicators of a boundary, and errors tend to occur later. If that is the case, we would expect some lags between prediction uncertainty and prediction error. We examined lagged correlation between prediction uncertainty and prediction error, and the optimal lag is 0 for both uncertainty-driven and error-driven models. This indicates that when prediction uncertainty rises, prediction error also simultaneously rises.

Author response image 1.

(3) Given that there is a 24-second period during which the neural responses are shaped by event boundaries, it would be important to know more about the average distance between boundaries and the variability of this distance. This will help establish whether the FIR model can properly capture a return to baseline.

We have added details about the distribution of event lengths. Specifically, we now report that the mean length of subjectively identified events was 21.4 seconds (median 22.2 s, SD 16.1 s). For model-derived boundaries, the average event lengths were 28.96 seconds for the uncertainty-driven model and 24.7 seconds for the error-driven model.

" For each activity, a separate group of 30 participants had previously segmented each movie to identify fine-grained event boundaries (Bezdek et al., 2022). The mean event length was 21.4 s (median 22.2 s, SD 16.1 s). Mean event lengths for uncertainty-driven model and error-driven model were 28.96s, and 24.7s, respectively (Nguyen et al., 2024)."

(4) Given that there is an early onset and long-lasting response of the brain to these event boundaries, I wonder what causes this. Is it the case that uncertainty or errors already increase at 12 seconds before the boundaries occur? Or if there are other makers in the movie that the brain can use to foreshadow an event boundary? And if uncertainty or errors do increase already 12 seconds before an event boundary, do you see a similar neural response at moments with similar levels of error or uncertainty, which are not followed by a boundary? This would reveal whether the neural activity patterns are specific to event boundaries or whether these are general markers of error and uncertainty.

We appreciate this point; it is similar to reviewer 2’s comment 2. Please see our response to that comment above.

(5) It is known that different brain regions have different delays of their BOLD response. Could these delays contribute to the propagation of the neural activity across different brain areas in this study?

Our analyses use ±20 s FIR windows, and the key effects we report include shifts ~12s before boundaries in higher-order cortex and ~4.5s pre-boundary in dorsal attention/parietal areas. Given the literature above, region-dependent BOLD delays are much smaller (~1–2s) than the temporal structure we observe (Taylor et al., 2018), making it unlikely that HRF lag alone explains our multi-second, region-specific progression.

(6) In the FIR plots, timepoints -12, 0, and 12 are shown. These long intervals preclude an understanding of the full temporal progression of these effects.

For page length purposes, we did not include all timepoints. We uploaded a brain animation of all timepoints and coefficients for each parcel in Openneuro (PATTERN_coefficients_brain_animation_human_fine_pattern.html and PATTERN_coefficients_lines_human_fine.html in the derivatives/figures/brain_maps_and_timecourses/ directory; https://doi.org/10.18112/openneuro.ds005551.v1.0.4) for interested researchers.

References

Taylor, A. J., Kim, J. H., & Ress, D. (2018). Characterization of the hemodynamic response function across the majority of human cerebral cortex. NeuroImage, 173, 322–331. https://doi.org/10.1016/j.neuroimage.2018.02.061

Reviewer #2 (Public review):

This study uses monkey single-unit recordings to examine the role of the STN in combining noisy sensory information with reward bias during decision-making between saccade directions. Using multiple linear regressions and k-means clustering approaches, the authors overall show that a highly heterogeneous activity in the STN reflects almost all aspects of the task, including choice direction, stimulus coherence, reward context and expectation, choice evaluation, and their interactions. The authors report in particular how, here too, in a very heterogeneous way, four classes of neurons map to different decision processes evaluated via the fitting of a drift-diffusion model. Overall, the study provides evidence for functionally diverse populations of STN neurons, supporting multiple roles in perceptual and reward-based decision-making.

This study follows up on work conducted in previous years by the same team and complements it. Extracellular recordings in monkeys trained to perform a complex decision-making task remain a remarkable achievement, particularly in brain structures that are difficult to target, such as the subthalamic nucleus. The authors conducted numerous rigorous and systematic analyses of STN activities, using sophisticated statistical approaches and functional computational modeling.

One criticism I would make is that the authors sometimes seem to assume that readers are familiar with their previous work. Indeed, the motivation and choices behind some analyses are not clearly explained. It might be interesting to provide a little more context and insight into these methodological choices. The same is true for the description of certain results, such as the behavioral results, which I find insufficiently detailed, especially since the two animals do not perform exactly the same way in the task.

Another criticism is the difficulty in following and absorbing all the presented results, given their heterogeneity. This heterogeneity stems from analytical choices that include defining multiple time windows over which activities are studied, multiple task-related or monkey behavioral factors that can influence them, multiple parameters underlying the decision-making phenomena to be captured, and all this without any a priori hypotheses. The overall impression is of an exploratory description that is sometimes difficult to digest, from which it is hard to extract precise information beyond the very general message that multiple subpopulations of neurons exist and therefore that the STN is probably involved in multiple roles during decision-making.

It would also have been interesting to have information regarding the location of the different identified subpopulations of neurons in the STN and their level of segregation within this nucleus. Indeed, since the STN is one of the preferred targets of electrical stimulation aimed at improving the condition of patients suffering from various neurological disorders, it would be interesting to know whether a particular stimulation location could preferentially affect a specific subpopulation of neurons, with the associated specific behavioral consequences.

Therefore, this paper is interesting because it complements other work from the same team and other studies that demonstrate the likely important role of the STN in decision-making. This will be of interest to the decision-making neuroscience community, but it may leave a sense of incompleteness due to the difficulty in connecting the conclusions of these different studies. For example, in the discussion section, the authors attempt to relate the different neuronal populations identified in their study and describe some relatively consistent results, but others less so.

Reviewer #3 (Public review):

Summary:

In their study McDermott et al. investigate the neurocomputational mechanism underlying sensory prediction errors. They contrast two accounts: representational sharpening and dampening. Representational sharpening suggests that predictions increase the fidelity of the neural representations of expected inputs, while representational dampening suggests the opposite (decreased fidelity for expected stimuli). The authors performed decoding analyses on EEG data, showing that first expected stimuli could be better decoded (sharpening), followed by a reversal during later response windows where unexpected inputs could be better decoded (dampening). These results are interpreted in the context of opposing process theory (OPT), which suggests that such a reversal would support perception to be both veridical (i.e., initial sharpening to increase the accuracy of perception) and informative (i.e., later dampening to highlight surprising, but informative inputs).

Strengths:

The topic of the present study is of significant relevance for the field of predictive processing. The experimental paradigm used by McDermott et al. is well designed, allowing the authors to avoid common confounds in investigating predictions, such as stimulus familiarity and adaptation. The introduction provides a well written summary of the main arguments for the two accounts of interest (sharpening and dampening), as well as OPT. Overall, the manuscript serves as a good overview of the current state of the field.

Weaknesses:

In my opinion the study has a few weaknesses. Some method choices appear arbitrary (e.g., binning). Additionally, not all results are necessarily predicted by OPT. Finally, results are challenging to reconcile with previous studies. For example, while I agree with the authors that stimulus familiarity is a clear difference compared to previous designs, without a convincing explanation why this would produce the observed pattern of results, I find the account somewhat unsatisfying.

"Create Space"<br /> the biggest EMF sources in notebooks are the CPU and GPU, located directly under the keyboard.<br /> fix: use external keyboard and mouse

generally:<br /> buy an EMF meter for about 20 euros, and measure all the things.<br /> in an electric car, measure at your feet, the EMF meter will go "out of range"...

touchscreens/touchpads are especially bad, because of the capacitive coupling between your fingers and the device.<br /> worst case: prolonged use of a touchscreen device connected to a battery charger.<br /> at some point, your hands will start to "burn" (painful cramping)

insect suicide:<br /> again and again, i see insects (ladybirds, bees, ...) deliberately sitting on my notebook keyboard,<br /> directly over the CPU, with the most radiation.<br /> they sit there for a few minutes, until they are dead.<br /> i guess that these insects are so stressed-out by the EMF radiation in my appartment<br /> (power grid harmonics, switched-mode power supplies, wifi, 5G, CPUs, ...),<br /> so when they find no way to exit my appartment (all windows closed),<br /> then they switch to "suicide mode" and land on my notebook keyboard...

ECS Instance Storage: - way to mount volume storage to ec2 instance - provides persistance storagae even after termination - different types - temporary, and file system 30 GB for free tier (general pupose) Elastic Block Storage, - volume storage. dddd - discount for different types Elastic File System - network file sysem - can mount 100s of ec2 instance - has a high thought(read/ write) capabiliteis - - can be used for muiltiple OS - windows vs linux - others

Briefing : L'émancipation de l'Éducation nationale face au monopole de Microsoft

Ce document synthétise les enjeux de la dépendance technologique de l'Éducation nationale française envers Microsoft et l'émergence d'une alternative structurée autour du logiciel libre et de la collaboration enseignante.

Résumé Exécutif

L'Éducation nationale française fait face à une dépendance coûteuse et structurelle vis-à-vis des solutions propriétaires, principalement Microsoft.

Le passage imposé de Windows 10 à Windows 11 illustre cette vulnérabilité : l'obsolescence logicielle pourrait coûter jusqu'à un milliard d'euros à l'échelle nationale pour le renouvellement du parc informatique.

Face à ce constat, une "guérilla" de l'open source s'organise. Portée par la Direction du numérique pour l'éducation (DNE) et des initiatives comme « La Forge », cette dynamique mobilise désormais 10 000 enseignants-développeurs.

L'objectif est de substituer aux licences onéreuses des « communs numériques » (Linux, BigBlueButton, NextCloud), garantissant la souveraineté des données, la pérennité des investissements publics et une pédagogie adaptée aux besoins réels du terrain.

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1. Le constat d'une dépendance critique : Le "cas d'école" Microsoft

La relation entre l'institution scolaire et Microsoft est décrite comme une forme d'addiction budgétaire et technique.

Le coût de l'obsolescence imposée

• L'exemple des Hauts-de-France : Suite à une cyberattaque par ransomware, la région a dû envisager la migration vers Windows 11.

Un membre de la DSI a estimé à 100 millions d'euros le coût pour renouveler 30 000 PC incapables de supporter cette mise à jour.

• Extrapolation nationale : Les Hauts-de-France représentant environ 10 % de l'éducation nationale, le coût total pour la mise à jour forcée du parc (300 000 machines) est estimé à 1 milliard d'euros.

• La vente liée : Le monopole s'appuie sur le mécanisme de la vente liée, où le système d'exploitation est pré-installé sans distinction de prix entre le matériel et le logiciel, imposant une solution "clé en main" qui freine l'adoption d'alternatives.

Limites des services propriétaires

• Coûts récurrents : Des dizaines de millions d'euros sont versés chaque année en licences.

• Failles systémiques : La crise du Covid-19 a révélé les carences du système numérique éducatif, notamment sa dépendance à des solutions propriétaires onéreuses et son manque de cohérence globale.

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2. La stratégie de rupture par le Logiciel Libre

Face au monopole, des solutions basées sur Linux et l'open source prouvent leur viabilité sur le terrain.

Distributions Linux dédiées à l'éducation

Il existe des alternatives robustes permettant d'adapter l'ordinateur aux besoins pédagogiques :

• PrimTux : Système d'exploitation spécifique pour les écoles primaires.

• ND (Numérique Inclusif, Responsable et Durable) : Distribution destinée au secondaire.

Obstacles et leviers d'adoption

| Obstacle | État des lieux | Perspectives | | --- | --- | --- | | Logiciels métiers | Certains éditeurs (SVT, physique, techno) ne développent que pour Windows. | Pression par la masse : l'augmentation du parc Linux doit forcer les éditeurs à s'adapter. | | Logiciels de vie scolaire | Pronote dispose d'un client Windows complet mais d'une version web dégradée sous Linux. | Nécessité d'une évolution des clients vers des standards interopérables. | | Résilience | En cas d'attaque (ransomware), les systèmes sous Windows ont été paralysés. | Des lycées sous Linux (ex: Lycée Carnot à Bruay-la-Buissière) ont pu proposer leur aide et leurs outils. |

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3. « La Forge » : L'industrialisation de l'innovation enseignante

« La Forge » représente un changement de paradigme : passer de l'enseignant "bricoleur" isolé à une communauté structurée de développeurs au sein de l'État.

Un modèle collaboratif massif

• Effectifs : 10 000 enseignants inscrits.

• Volume : 6 500 projets (dépôts de code) enregistrés.

• Fonctionnement : Outil de travail collaboratif (basé sur le modèle GitHub) permettant de fédérer, tester et partager des codes sources et des ressources pédagogiques.

Exemples de projets emblématiques

• MindStory : Alternative open source à Minecraft, permettant aux élèves de collaborer sur des constructions sans dépendre d'un compte Microsoft payant.

• Philo GPT : Interface permettant de dialoguer avec des simulations de grands philosophes.

• Execubot : Outil d'apprentissage de la programmation via un robot virtuel.

• Créa-appli : Outil utilisant l'IA pour aider les profs à générer des prototypes d'applications (HTML/JS) via le "vibe coding" (codage par prompt).

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4. Souveraineté, Communs Numériques et Commande Publique

L'enjeu n'est pas seulement technique, il est politique et financier : assurer que l'argent public finance des biens publics.

La notion de "Communs Numériques"

Un commun numérique repose sur trois piliers : une ressource, une communauté et une gouvernance. L'idée est que l'amélioration d'un logiciel par le ministère bénéficie à tous.

Les services souverains déjà déployés

Le ministère opère et héberge ses propres instances de logiciels libres pour s'affranchir des GAFAM :

• BigBlueButton : Alternative à Zoom/Meet pour la visioconférence (participation financière du ministère au développement du projet global).

• Apps.education.fr : Portail regroupant des outils comme Tube (alternative à YouTube basée sur PeerTube) ou NextCloud (alternative à Google Drive).

Critique du modèle traditionnel de commande publique

Par le passé, l'État stimulait les start-ups ("EdTech") via des marchés publics sans exiger la propriété intellectuelle :

1. Les entreprises conservaient le code source et les données.

2. L'État devait payer des abonnements pour continuer à utiliser ce qu'il avait financé.

3. Résultat : Aucune capitalisation sur le long terme.

La nouvelle approche privilégie la pérennité : Investir dans l'open source permet à l'institution de conserver la maîtrise de ses outils, même après la fin d'un contrat avec un prestataire.

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Citations Clés

« L'éducation nationale est accro à Microsoft. Chaque année, des dizaines de millions d'euros s'envolent en licences. »

« Le slogan de la forge c'est : "L'union fait la forge". »

« On a oublié que nos profs étaient aussi capables de fabriquer leurs propres ressources... On a passé des marchés avec ces EdTech où on n'exigeait rien en termes de propriété intellectuelle. Les boîtes repartaient avec l'ensemble du code. »

« Un milliard pour faire une mise à jour de système d'exploitation qui était imposée par Microsoft parce que Microsoft a déclaré qu'ils arrêtent le support de Windows 10. »

Author response:

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

Reviewer #4 (Public review):

Summary:

The authors demonstrate a computational rational design approach for developing RNA aptamers with improved binding to the Receptor Binding Domain (RBD) of the SARS-CoV-2 spike protein. They demonstrate the ability of their approach to improve binding affinity using a previously identified RNA aptamer, RBD-PB6-Ta, which binds to the RBD. They also computationally estimate the binding energies of various RNA aptamers with the RBD and compare against RBD binding energies for a few neutralizing antibodies from the literature. Finally, experimental binding affinities are estimated by electrophoretic mobility shift assays (EMSA) for various RNA aptamers and a single commercially available neutralizing antibody to support the conclusions from computational studies on binding. The authors conclude that their computational framework, CAAMO, can provide reliable structure predictions and effectively support rational design of improved affinity for RNA aptamers towards target proteins. Additionally, they claim that their approach achieved design of high affinity RNA aptamer variants that bind to the RBD as well or better than a commercially available neutralizing antibody.

Strengths:

The thorough computational approaches employed in the study provide solid evidence of the value of their approach for computational design of high affinity RNA aptamers. The theoretical analysis using Free Energy Perturbation (FEP) to estimate relative binding energies supports the claimed improvement of affinity for RNA aptamers and provides valuable insight into the binding model for the tested RNA aptamers in comparison to previously studied neutralizing antibodies. The multimodal structure prediction in the early stages of the presented CAAMO framework, combined with the demonstrated outcome of improved affinity using the structural predictions as a starting point for rational design, provide moderate confidence in the structure predictions.

We thank the reviewer for this accurate summary and for recognizing the strength of our integrated computational–experimental workflow in improving aptamer affinity.

Weaknesses:

The experimental characterization of RBD affinities for the antibody and RNA aptamers in this study present serious concerns regarding the methods used and the data presented in the manuscript, which call into question the major conclusions regarding affinity towards the RBD for their aptamers compared to antibodies. The claim that structural predictions from CAAMO are reasonable is rational, but this claim would be significantly strengthened by experimental validation of the structure (i.e. by chemical footprinting or solving the RBD-aptamer complex structure).

The conclusions in this work are somewhat supported by the data, but there are significant issues with experimental methods that limit the strength of the study's conclusions.

(1) The EMSA experiments have a number of flaws that limit their interpretability. The uncropped electrophoresis images, which should include molecular size markers and/or positive and negative controls for bound and unbound complex components to support interpretation of mobility shifts, are not presented. In fact, a spliced image can be seen for Figure 4E, which limits interpretation without the full uncropped image.

Thank you for your valuable comments and careful review.

In response to your suggestion, we will provide all uncropped electrophoresis raw images corresponding to the results in the main figures and supplementary figures (Figure 2F, 3D, 3E, 4E, S9A and S10 of the original manuscript) in the revised version. Regarding the spliced image in Figure 4E, the uncropped raw gel image clearly shows that the two C23U samples were run on an adjacent lane of the same gel due to the total number of samples exceeding the well capacity of a single lane. All samples were electrophoresed and signal-detected under identical experimental conditions in one single experiment, ensuring the validity of direct signal intensity comparison across all samples. These complete uncropped raw images will be supplemented in the revised manuscript as Figure S12 (also see Author response image 1).

Author response image 1.

Uncropped electrophoresis images corresponding to Figures 2F, 3D, 3E, 4E, S9A and S10 of the original manuscript.

Additionally, he volumes of EMSA mixtures are not presented when a mass is stated (i.e. for the methods used to create Figure 3D), which leaves the reader without the critical parameter, molar concentration, and therefore leaves in question the claim that the tested antibody is high affinity under the tested conditions.

Thank you for your valuable comment on this oversight.

For the EMSA assay in Figure 3D, the reaction mixture (10 μL total volume) contained 3 μg of RBD protein and 3 μg of antibody (40592-R001), either individually or in combination, with incubation at room temperature for 20 minutes. Based on the molecular weights (35 kDa for RBD and 150 kDa for the IgG antibody), the corresponding molar concentrations in the mixture were calculated as 8.57 μM for RBD and 2 μM for the antibody. To ensure consistency, clarity and provide the critical molar concentration parameter, we will revise the legend of Figure 3D, replacing the mass values with the calculated molar concentrations as you suggested in the revised manuscript.

Additionally, protein should be visualized in all gels as a control to ensure that lack of shifts is not due to absence/aggregation/degradation of the RBD protein. In the case of Figure 3E, for example, it can be seen that there are degradation products included in the RBD-only lane, introducing a reasonable doubt that the lack of a shift in RNA tests (i.e. Figure 2F) is conclusively due to a lack of binding.

We sincerely appreciate your careful evaluation of our work, which helps us further clarify the experimental details and data reliability.

First, we would like to clarify the nature of the gel electrophoresis in Figure 3E: the RBD protein was separated by native-PAGE rather than denaturing SDS-PAGE. The RBD protein used in all experiments was purchased from HUABIO (Cat. No. HA210064) with guaranteed quality, and its integrity and purity were independently verified in our laboratory via denaturing SDS-PAGE (see Author response image 2), which showed a single, intact band without any degradation products. The ladder-like bands observed in the RBD-only lane of the native-PAGE gel are not a result of protein degradation. Instead, they arise from two well-characterized properties of recombinant SARS-CoV-2 Spike RBD protein expressed in human cells: intrinsic conformational heterogeneity (the RBD domain exists in multiple dynamic conformations due to its structural flexibility) (Cai et al., Science, 2020; Wrapp et al., Science, 2020) and heterogeneity in N-glycosylation modification (variable glycosylation patterns at the conserved N-glycosylation sites of RBD) (Casalino et al., ACS Cent. Sci., 2020; Ives et al., eLife, 2024), both of which could cause distinct migration bands in native-PAGE under non-denaturing conditions.

Second, to ensure the reliability of the RNA-binding results, the EMSA experiments for determining the binding affinity (K_d) of RBD to Ta, Tc and Ta variants were performed with three independent biological replicates (the original manuscript includes all replicate data in Figure 2F and S9). Consistent results were obtained across all replicates, which effectively rules out false-negative outcomes caused by accidental absence or loss of functional RBD protein in the reaction system. In addition, our gel images (Figure 2F and S9 in the original manuscript) and uncropped raw images of all EMSA gels (see Author response image 1) show no significant signal accumulation in the sample wells, confirming the absence of RBD protein aggregation in the binding reactions—an issue that would otherwise interfere with RNA-protein interaction and band shift detection.

New results for RBD analysis by denaturing SDS-PAGE, along with the associated discussion, will be added to the revised manuscript as Figure S10 (also see Author response image 2).

Author response image 2.

SDS-PAGE analysis of the SARS-CoV-2 Spike RBD protein, neutralizing antibody (40592-R001) and BSA reference. This gel validates the high purity and structural integrity of the commercially sourced RBD protein and neutralizing antibody used in this study.

References

Cai, Y. et al. Distinct conformational states of SARS-CoV-2 spike proteins. Science 369, 1586-1592 (2020).

Casalino, L. et al. Beyond shielding: the roles of glycans in the SARS-CoV-2 spike protein. ACS Cent. Sci. 6, 1722-1734 (2020).

Ives, C.M. et al. Role of N343 glycosylation on the SARS-CoV-2 S RBD structure and co-receptor binding across variants of concern. eLife 13, RP95708 (2024).

Wrapp, D. et al. Cryo-EM structure of the 2019-nCoV spike in the prefusion conformation. Science 367, 1260-1263 (2020).

Finally, there is no control for nonspecific binding, such as BSA or another non-target protein, which fails to eliminate the possibility of nonspecific interactions between their designed aptamers and proteins in general. A nonspecific binding control should be included in all EMSA experiments.

Thank you for this constructive comment.

Following your recommendation, we are currently supplementing the EMSA assays with BSA as a non-target protein control to rigorously exclude potential non-specific binding between our designed aptamers (Ta and Ta variants) and exogenous proteins. These additional experiments are designed to directly assess whether the aptamers exhibit unintended interactions with unrelated proteins and to further validate the protein specificity of the RBD–aptamer interaction observed in our study.

The resulting nonspecific binding control data will be formally incorporated into the revised manuscript as Figure S11, and the corresponding Results and Discussion sections will be updated accordingly to reflect this critical validation once the experiments are completed.

(2) The evidence supporting claims of better binding to RBD by the aptamer compared to the commercial antibody is flawed at best. The commercial antibody product page indicates an affinity in low nanomolar range, whereas the fitted values they found for the aptamers in their study are orders of magnitude higher at tens of micromolar. Moreover, the methods section is lacking in the details required to appropriately interpret the competitive binding experiments. With a relatively short 20-minute equilibration time, the order of when the aptamer is added versus the antibody makes a difference in which is apparently bound. The issue with this becomes apparent with the lack of internal consistency in the presented results, namely in comparing Fig 3E (which shows no interference of Ta binding with 5uM antibody) and Fig 5D (which shows interference of Ta binding with 0.67-1.67uM antibody). The discrepancy between these figures calls into question the methods used, and it necessitates more details regarding experimental methods used in this manuscript.

Thank you for your insightful comments, which have helped us refine the rigor of our study. We address each of your concerns in detail below:

First, we agree with your observation that the commercial neutralizing antibody (Sino Biological, Cat# 40592-R001) is reported to bind Spike RBD with low nanomolar affinity on its product page. However, this discrepancy in affinity values (nanomolar vs. micromolar) stems from the use of distinct analytical methods. The product page affinity was determined via the Octet RED System, a technique analogous to Surface Plasmon Resonance (SPR) that offers high sensitivity for kinetic and affinity measurements. In contrast, our study employed EMSA, a method primarily optimized for semi-quantitative assessment of binding interactions. The inherent differences in sensitivity and principle between these two techniques—with Octet RED System enabling real-time monitoring of biomolecular interactions and EMSA relying on gel separation—account for the observed variation in affinity values.

Second, regarding the competitive binding experiments, we appreciate your note on the critical role of reagent addition order and equilibration time. To eliminate potential biases from sequential addition, we clarify that Cy3-labeled RNAs, RBD proteins, and the neutralizing antibody were added simultaneously to the reaction system. We will revise the Methods section in the revised manuscript to provide a detailed protocol for the EMSA experiments, to ensure full reproducibility and appropriate interpretation of the results.

Third, we acknowledge and apologize for a critical error in the figure legends of Figure 3E: the concentrations reported (5 μM aptamer and antibody 40592-R001) refer to stock solutions, not the final concentrations in the EMSA reaction mixture. The correct final concentrations are 0.5 μM for aptamer Ta, and 0.5 μM for the antibody. This correction resolves the apparent inconsistency between Figure 3E and Figure 5D, as the final antibody concentration in Figure 3E is now consistent with the concentration range used in Figure 5D. We will update the figure legends for Figure 3E and revise the Methods section to explicitly distinguish between stock and final reaction concentrations, ensuring clarity and internal consistency of the results.

We sincerely thank you for highlighting these issues, which will prompt important revisions to improve the clarity, accuracy, and rigor of our manuscript.

(3) The utility of the approach for increasing affinity of RNA aptamers for their targets is well supported through computational and experimental techniques demonstrating relative improvements in binding affinity for their G34C variant compared to the starting Ta aptamer. While the EMSA experiments do have significant flaws, the observations of relative relationships in equilibrium binding affinities among the tested aptamer variants can be interpreted with reasonable confidence, given that they were all performed in a consistent manner.

We sincerely appreciate your valuable concerns and constructive feedback, which have greatly facilitated the improvement of our manuscript. Regarding the flaws of the EMSA experiments you pointed out, we have provided a detailed response to clarify the related issues and supplemented necessary experimental details to enhance the rigor and reproducibility of our work (see corresponding response above). It is worth noting that EMSA remains a classic and widely used technique for studying biomolecular interactions, and its reliability in qualitative and semi-quantitative analysis of binding events has been well recognized in the field. Furthermore, we fully agree with and are grateful for your view that, since all tested aptamer variants were analyzed using a consistent experimental protocol, the observations on the relative relationships of their equilibrium binding affinities can be interpreted with reasonable confidence. This recognition reinforces the validity of the relative affinity improvements we observed for the G34C variant compared to the parental Ta aptamer, which is a key finding of our study.

(4) The claim that the structure of the RBD-Aptamer complex predicted by the CAAMO pipeline is reliable is tenuous. The success of their rational design approach based on the structure predicted by several ensemble approaches supports the interpretation of the predicted structure as reasonable, however, no experimental validation is undertaken to assess the accuracy of the structure. This is not a main focus of the manuscript, given the applied nature of the study to identify Ta variants with improved binding affinity, however the structural accuracy claim is not strongly supported without experimental validation (i.e. chemical footprinting methods).

We thank the reviewer for this comment and agree that experimental validation would be required to establish the structural accuracy of the predicted RBD–aptamer complex. We note, however, that the primary aim of this study is not structural determination, but the development of a general computational framework for aptamer affinity maturation. In most practical applications, experimentally resolved structures of aptamer–protein complexes are unavailable. Accordingly, CAAMO is designed to operate under such conditions, using computationally generated binding models as working hypotheses to guide rational optimization rather than as definitive structural descriptions. In this context, the predicted structure is evaluated by its utility for affinity improvement, rather than by direct structural validation. We will revise the manuscript accordingly to further clarify this scope.

(5) Throughout the manuscript, the phrasing of "all tested antibodies" was used, despite there being only one tested antibody in experimental methods and three distinct antibodies in computational methods. While this concern is focused on specific language, the major conclusion that their designed aptamers are as good or better than neutralizing antibodies in general is weakened by only testing only three antibodies through computational binding measurements and a fourth single antibody for experimental testing. The contact residue mapping furthermore lacks clarity in the number of structures that were used, with a vague description of structures from the PDB including no accession numbers provided nor how many distinct antibodies were included for contact residue mapping.

We thank the reviewer for this important comment regarding language precision, experimental scope, and clarity of the antibody dataset used in this study. We agree that the phrase “all tested antibodies” was imprecise and could lead to overgeneralization. We will carefully revise the manuscript to use more accurate and explicit wording throughout, clearly distinguishing between experimentally tested antibodies, computationally analyzed antibodies, and antibody structures used for large-scale contact analysis.

Specifically, the experimental comparison in this study was performed using one commercially available SARS-CoV-2 neutralizing antibody, whereas free energy–based computational analyses were conducted on three representative neutralizing antibodies with available structural data. We will revise the manuscript to explicitly state these distinctions and avoid general statements referring to neutralizing antibodies as a class.

Importantly, the residue-level contact frequency analysis was not based solely on these individual antibodies. Instead, this analysis leveraged a comprehensive set of experimentally resolved SARS-CoV-2 RBD–antibody complex structures curated from the Coronavirus Antibody Database (CoV-AbDab), a publicly available and actively maintained resource developed by the Oxford Protein Informatics Group. CoV-AbDab aggregates all published coronavirus-binding antibodies with associated PDB structures and provides a systematic and unbiased structural foundation for antibody–RBD interaction analysis. All available high-resolution RBD–antibody complex structures indexed in CoV-AbDab at the time of analysis were included to compute contact residue frequencies across the structural ensemble. We will explicitly state this data source, clarify the number and nature of structures used, and add the appropriate citation (Raybould et al., Bioinformatics, 2021, doi: 10.1093/bioinformatics/btaa739).

Finally, we will revise the conclusions to avoid claims that extend beyond the scope of the data. The comparison between aptamers and antibodies is now framed in terms of representative antibodies and consensus interaction patterns derived from a large structural ensemble, rather than as a general statement about all neutralizing antibodies. These revisions will improve the clarity, rigor, and reproducibility of the manuscript, while preserving the core conclusion that the CAAMO framework enables effective structure-guided affinity maturation of RNA aptamers.

Overall, the manuscript by Yang et al presents a valuable tool for rational design of improved RNA aptamer binding affinity toward target proteins, which the authors call CAAMO. Notably, the method is not intended for de novo design, but rather as a tool for improving aptamers that have been selected for binding affinity by other methods such as SELEX. While there are significant issues in the conclusions made from experiments in this manuscript, the relative relationships of observed affinities within this study provide solid evidence that the CAAMO framework provides a valuable tool for researchers seeking to use rational design approaches for RNA aptamer affinity maturation.

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this study, the authors attempt to devise general rules for aptamer design based on structure and sequence features. The main system they are testing is an aptamer targeting a viral sequence.

Strengths:

The method combines a series of well-established protocols, including docking, MD, and a lot of system-specific knowledge, to design several new versions of the Ta aptamer with improved binding affinity.

We thank the reviewer for this accurate summary and for recognizing the strength of our integrated computational–experimental workflow in improving aptamer affinity.

Weaknesses:

The approach requires a lot of existing knowledge and, importantly, an already known aptamer, which presumably was found with SELEX. In addition, although the aptamer may have a stronger binding affinity, it is not clear if any of it has any additional useful properties such as stability, etc.

Thanks for these critical comments.

(1) On the reliance on a known aptamer: We agree that our CAAMO framework is designed as a post-SELEX optimization platform rather than a tool for de novo discovery. Its primary utility lies in rationally enhancing the affinity of existing aptamers that may not yet be sequence-optimal, thereby complementing experimental technologies such as SELEX. The following has been added to “Introduction” of the revised manuscript. (Page 5, line 108 in the revised manuscript)

‘Rather than serving as a de novo aptamer discovery tool, CAAMO is designed as a post-SELEX optimization platform that rationally improves the binding capability of existing aptamers.’

(2) On stability and developability: We also appreciate the reviewer’s important reminder that affinity alone is not sufficient for therapeutic development. We acknowledge that the present study has focused mainly on affinity optimization, and properties such as nuclease resistance, structural stability, and overall developability were not evaluated. The following has been added to “Discussion and conclusion” of the revised manuscript. (Page 25, line 595 in the revised manuscript)

‘While the present study primarily focused on affinity optimization, we acknowledge that other key developability traits—such as nuclease resistance, structural and thermodynamic stability, and in vivo persistence—are equally critical for advancing aptamers toward therapeutic applications. These properties were not evaluated here but will be systematically addressed in future iterations of the CAAMO framework to enable comprehensive optimization of aptamer candidates.’

Reviewer #2 (Public review):

Summary:

This manuscript proposes a workflow for discovering and optimizing RNA aptamers, with application in the optimization of a SARS-CoV-2 RBD. The authors took a previously identified RNA aptamer, computationally docked it into one specific RBD structure, and searched for variants with higher predicted affinity. The variants were subsequently tested for RBD binding using gel retardation assays and competition with antibodies, and one was found to be a stronger binder by about three-fold than the founding aptamer.

Overall, this would be an interesting study if it were performed with truly high-affinity aptamers, and specificity was shown for RBD or several RBD variants.

Strengths:

The computational workflow appears to mostly correctly find stronger binders, though not de novo binders.

We thank the reviewer for the clear summary and for acknowledging that our workflow effectively prioritizes stronger binders.

Weaknesses:

(1) Antibody competition assays are reported with RBD at 40 µM, aptamer at 5 µM, and a titration of antibody between 0 and 1.2 µg. This approach does not make sense. The antibody concentration should be reported in µM. An estimation of the concentration is 0-8 pmol (from 0-1.2 µg), but that's not a concentration, so it is unknown whether enough antibody molecules were present to saturate all RBD molecules, let alone whether they could have displaced all aptamers.

Thanks for your insightful comment. We have calculated that 0–1.2 µg antibody corresponds to a final concentration range of 0–1.6 µM (see Author response image 1). In practice, 1.2 µg was the maximum amount of commercial antibody that could be added under the conditions of our assay. In the revised manuscript, all antibody amounts previously reported in µg have been converted to their corresponding molar concentrations in Fig. 1F and Fig. 5D. In addition, the exact antibody concentrations used in the EMSA assays are now explicitly stated in the Materials and Methods section under “EMSA experiments.” The following has been added to “EMSA experiments” of the revised manuscript. (Page 30 in the revised manuscript)

‘For competitive binding experiments, 40 μM of RBP proteins, 5 μM of annealed Cy3-labelled RNAs and increasing concentrations of SARS-CoV-2 neutralizing antibody 40592-R001 (0–1.67 μM) were mixed in the EMSA buffer and incubated at room temperature for 20 min.’

Author response image 1.

Estimation of antibody concentration. Assuming a molecular weight of 150 kDa, dissolving 1.2 µg of antibody in a 5 µL reaction volume results in a final concentration of 1.6 µM.

As shown in Figure 5D, the purpose of the antibody–aptamer competition assay was not to achieve full saturation but rather to compare the relative competitive binding of the optimized aptamer (Ta^G34C) versus the parental aptamer (Ta). Molecular interactions at this scale represent a dynamic equilibrium of binding and dissociation. While the antibody concentration may not have been sufficient to saturate all available RBD molecules, the experimental results clearly reveal the competitive binding behavior that distinguishes the two aptamers. Specifically, two consistent trends emerged:

(1) Across all antibody concentrations, the free RNA band for Ta was stronger than that of Ta^G34C, while the RBD–RNA complex band of the latter was significantly stronger, indicating that Ta^G34C bound more strongly to RBD.

(2) For Ta, increasing antibody concentration progressively reduced the RBD–RNA complex band, consistent with antibody displacing the aptamer. In contrast, for Ta^G34C, the RBD–RNA complex band remained largely unchanged across all tested antibody concentrations, suggesting that the antibody was insufficient to displace Ta^G34C from the complex.

Together, these observations support the conclusion that Ta^G34C exhibits markedly stronger binding to RBD than the parental Ta aptamer, in line with the predictions and objectives of our CAAMO optimization framework.

(2) These are not by any means high-affinity aptamers. The starting sequence has an estimated (not measured, since the titration is incomplete) K_d of 110 µM. That's really the same as non-specific binding for an interaction between an RNA and a protein. This makes the title of the manuscript misleading. No high-affinity aptamer is presented in this study. If the docking truly presented a bound conformation of an aptamer to a protein, a sub-micromolar K_d would be expected, based on the number of interactions that they make.

In fact, our starting sequence (Ta) is a high-affinity aptamer, and then the optimized sequences (such as Ta^G34C) with enhanced affinity are undoubtedly also high-affinity aptamers. See descriptions below:

(1) Origin and prior characterization of Ta. The starting aptamer Ta (referred to as RBD-PB6-Ta in the original publication by Valero et al., PNAS 2021, doi:10.1073/pnas.2112942118) was selected through multiple positive rounds of SELEX against SARS-CoV-2 RBD, together with counter-selection steps to eliminate non-specific binders. In that study, Ta was reported to bind RBD with an IC₅₀ of ~200 nM as measured by biolayer interferometry (BLI), supporting its high affinity and specificity. The following has been added to “Introduction” of the revised manuscript. (Page 4 in the revised manuscript)

‘This aptamer was originally identified through SELEX and subsequently validated using surface plasmon resonance (SPR) and biolayer interferometry (BLI), which confirmed its high affinity (sub-nanomolar) and high specificity toward the RBD. Therefore, Ta provides a well-characterized and biologically relevant starting point for structure-based optimization.’

(2) Methodological differences between EMSA and BLI measurements. We acknowledge that the discrepancy between our obtained binding affinity (K_d = 110 µM) and the previously reported one (IC₅₀ ~ 200 nM) for the same Ta sequence arises primarily from methodological and experimental differences between EMSA and BLI. Namely, different experimental measurement methods can yield varied binding affinity values. While EMSA may have relatively low measurement precision, its relatively simple procedures were the primary reason for its selection in this study. Particularly, our framework (CAAMO) is designed not as a tool for absolute affinity determination, but as a post-SELEX optimization platform that prioritizes relative changes in binding affinity under a consistent experimental setup. Thus, the central aim of our work is to demonstrate that CAAMO can reliably identify variants, such as Ta^G34C, that bind more strongly than the parental sequence under identical assay conditions. The following has been added to “Discussion and conclusion” of the revised manuscript. (Page 24 in the revised manuscript)

‘Although the absolute K_d values determined by EMSA cannot be directly compared with surface-based methods such as SPR or BLI, the relative affinity trends remain highly consistent. While EMSA provides semi-quantitative affinity estimates, the close agreement between experimental EMSA trends and FEP-calculated ΔΔG values supports the robustness of the relative affinity changes reported here. In future studies, additional orthogonal biophysical techniques (e.g., filter-binding, SPR, or BLI) will be employed to further validate and refine the protein–aptamer interaction models.’

(3) Evidence of specific binding in our assays. We emphasize that the binding observed in our EMSA experiments reflects genuine aptamer–protein interactions. As shown in Figure 2G, a control RNA (Tc) exhibited no detectable binding to RBD, whereas Ta produced a clear binding curve, confirming that the interaction is specific rather than non-specific.

(3) The binding energies estimated from calculations and those obtained from the gel-shift experiments are vastly different, as calculated from the K_d measurements, making them useless for comparison, except for estimating relative affinities.

Author Reply: We thank the reviewer for raising this important point. CAAMO was developed as a post-SELEX optimization tool with the explicit goal of predicting relative affinity changes (ΔΔG) rather than absolute binding free energies (ΔG). Empirically, CAAMO correctly predicted the direction of affinity change for 5 out of 6 designed variants (e.g., ΔΔG < 0 indicates enhanced binding free energy relative to WT); such predictive power for relative ranking is highly valuable for prioritizing candidates for experimental testing. Our prior work on RNA–protein interactions likewise supports the reliability of relative affinity predictions (see: Nat Commun 2023, doi:10.1038/s41467-023-39410-8). The following has been added to “Discussion and conclusion” of the revised manuscript. (Page 24 in the revised manuscript)

‘While EMSA provides semi-quantitative affinity estimates, the close agreement between experimental EMSA trends and FEP-calculated ΔΔG values supports the robustness of the relative affinity changes reported here.’

Recommendations for the Authors:

Reviewer #1 (Recommendations for the authors)

(1) Overall, the paper is well-written and, in the opinion of this reviewer, could remain as it is.

We thank the reviewer for the positive evaluation and supportive comments regarding our manuscript. We are grateful for the endorsement of its quality and suitability for publication.

Reviewer #2 (Recommendations for the authors)

(1) All molecules present in experiments need to be reported with their final concentrations (not µg).

We thank the reviewer for raising this important point. In the revised manuscript, all antibody amounts previously reported in µg have been converted to their corresponding molar concentrations in Fig. 1F and Fig. 5D. In addition, the exact antibody concentrations used in the EMSA assays are now explicitly stated in the Materials and Methods section under “EMSA experiments.” The following has been added to “EMSA experiments” of the revised manuscript. (Page 30 in the revised manuscript)

‘For competitive binding experiments, 40 μM of RBP proteins, 5 μM of annealed Cy3-labelled RNAs and increasing concentrations of SARS-CoV-2 neutralizing antibody 40592-R001 (0–1.67 μM) were mixed in the EMSA buffer and incubated at room temperature for 20 min.’

(2) An independent K_d measurement, for example, using a filter binding assay, would greatly strengthen the results.

We thank the reviewer for this constructive suggestion and agree that an orthogonal biophysical measurement (e.g., a filter-binding assay, SPR or BLI) would further strengthen confidence in the reported dissociation constants. Unfortunately, all available SARS-CoV-2 RBD protein used in this study has been fully consumed and, due to current supply limitations, we were unable to perform new orthogonal binding experiments for the revised manuscript. We regret this limitation and have documented it in the Discussion as an item for future work.

Importantly, although we could not perform a new filter-binding experiment at this stage, we have multiple independent lines of evidence that support the reliability of the EMSA-derived affinity trends reported in the manuscript:

(1) Rigorous EMSA design and reproducibility. All EMSA binding curves reported in the manuscript (e.g., Figs. 2F–G, 4E–F, 5A and Fig. S9) are derived from three independent biological replicates and include standard deviations; the measured binding curves show good reproducibility across replicates.

(2) Appropriate positive and negative controls. Our gel assays include clear internal controls. The literature-reported strong binder Ta forms a distinct aptamer–RBD complex band under our conditions, whereas the negative-control aptamer Tc shows no detectable binding under identical conditions (see Fig. 2F). These controls demonstrate that the EMSA system discriminates specific from non-binding sequences with high sensitivity.

(3) Orthogonal computational validation (FEP) that agrees with experiment. The central strength of the CAAMO framework is the integration of rigorous physics-based calculations with experiments. We performed FEP calculations for the selected single-nucleotide mutations and computed ΔΔG values for each mutant. The direction and rank order of binding changes predicted by FEP are in good agreement with the EMSA measurements: five of six FEP-predicted improved mutants (Ta^G34C, Ta^G34U, Ta^G34A, Ta^C23A, Ta^C23U) were experimentally confirmed to have stronger apparent affinity than wild-type Ta (see Fig. 4D–F, Table S2), yielding a success rate of 83%. The concordance between an independent, rigorous computational method and our experimental measurements provides strong mutual validation.

(4) Independent competitive binding experiments. We additionally performed competitive EMSA assays against a commercial neutralizing monoclonal antibody (40592-R001). These competition experiments show that Ta^G34C–RBD complexes are resistant to antibody displacement under conditions that partially displace the wild-type Ta–RBD complex (see Fig. 5D). This result provides an independent, functionally relevant line of evidence that Ta^G34C binds RBD with substantially higher affinity and specificity than WT Ta under our assay conditions.

Given these multiple, independent lines of validation (rigorous EMSA replicates and controls, FEP agreement, and antibody competition assays), we are confident that the relative affinity improvements reported in the manuscript are robust, even though the absolute K_d values measured by EMSA are not directly comparable to surface-based methods (EMSA typically reports larger apparent K_d values than SPR/BLI due to methodological differences). The following has been added to “Discussion and conclusion” of the revised manuscript. (Page 24 in the revised manuscript)

‘Although the absolute K_d values determined by EMSA cannot be directly compared with surface-based methods such as SPR or BLI, the relative affinity trends remain highly consistent. While EMSA provides semi-quantitative affinity estimates, the close agreement between experimental EMSA trends and FEP-calculated ΔΔG values supports the robustness of the relative affinity changes reported here. In future studies, additional orthogonal biophysical techniques (e.g., filter-binding, SPR, or BLI) will be employed to further validate and refine the protein–aptamer interaction models.’

(3) The project would really benefit from a different aptamer-target system. Starting with a 100 µM aptamer is really not adequate.

We thank the reviewer for this important suggestion and for highlighting the value of testing the CAAMO framework in additional aptamer–target systems.

First, we wish to clarify the rationale for selecting the Ta–RBD system as the proof-of-concept. The Ta aptamer is not an arbitrary or weak binder: it was originally identified by independent SELEX experiments and subsequently validated by rigorous biophysical assays (SPR and BLI) (see: Proc. Natl. Acad. Sci. 2021, doi: 10.1073/pnas.2112942118). That study confirmed that Ta exhibits high-affinity and high-specificity binding to the SARS-CoV-2 RBD, which is why it serves as a well-characterized and biologically relevant system for method validation and optimization. We have added a brief clarification to the “Introduction” to emphasize these points. The following has been added to “Introduction” of the revised manuscript. (Page 4 in the revised manuscript)

‘This aptamer was originally identified through SELEX and subsequently validated using surface plasmon resonance (SPR) and biolayer interferometry (BLI), which confirmed its high affinity and high specificity toward the RBD. Therefore, Ta provides a well-characterized and biologically relevant starting point for structure-based optimization.’

Second, we agree that apparent discrepancies in absolute K_d values can arise from different experimental platforms. Surface-based methods (SPR/BLI) and gel-shift assays (EMSA) have distinct measurement principles; EMSA yields semi-quantitative, solution-phase, apparent K_d values that are not directly comparable in absolute magnitude to surface-based measurements. Crucially, however, our study focuses on relative affinity change. EMSA is well suited for parallel, comparative measurements across multiple variants when all samples are assayed under identical conditions, and thus provides a reliable readout for ranking and validating designed mutations. We have added a short statement in the “Discussion and conclusion”. The following has been added to “Discussion and conclusion” of the revised manuscript. (Page 24 in the revised manuscript)

‘Although the absolute K_d values determined by EMSA cannot be directly compared with surface-based methods such as SPR or BLI, the relative affinity trends remain highly consistent. While EMSA provides semi-quantitative affinity estimates, the close agreement between experimental EMSA trends and FEP-calculated ΔΔG values supports the robustness of the relative affinity changes reported here. In future studies, additional orthogonal biophysical techniques (e.g., filter-binding, SPR, or BLI) will be employed to further validate and refine the protein–aptamer interaction models.’

Third, and importantly, CAAMO is inherently generalizable. In addition to the Ta–RBD application presented here, we have already begun applying CAAMO to other aptamer–target systems. In particular, we have successfully deployed the framework in preliminary optimization studies of RNA aptamers targeting the epidermal growth factor receptor (EGFR) (see: Gastroenterology 2021, doi: 10.1053/j.gastro.2021.05.055) (see Author response image 2). These preliminary results support the transferability of the CAAMO pipeline beyond the SARS-CoV-2 RBD system. We have added a short statement in the “Discussion and conclusion”. The following has been added to “Discussion and conclusion” of the revised manuscript. (Page 259 in the revised manuscript)

‘In addition to the Ta–RBD system, the CAAMO framework itself is inherently generalizable. More work is currently underway to apply CAAMO to optimize aptamers targeting other therapeutically relevant proteins, such as the epidermal growth factor receptor (EGFR) [45], in order to further explore its potential for broader aptamer engineering.’

Author response image 2.

Overview of the predicted binding model of the EGFR–aptamer complex generated using the CAAMO framework.

(4) Several RBD variants should be tested, as well as other proteins, for specificity. At such weak affinities, it is likely that these are non-specific binders.

We thank the reviewer for this important concern. Below we clarify the basis for selecting Ta and its engineered variants, summarize the experimental controls that address specificity, and present the extensive in silico variant analysis we performed to assess sensitivity and breadth of binding.

(1) Origin and validation of Ta. As noted in our response to “Comment (3)”, the Ta aptamer was not chosen arbitrarily. Ta was identified by independent SELEX with both positive and negative selection and subsequently validated using surface-based biophysical assays (SPR and BLI), which reported low-nanomolar affinity and high specificity for the SARS-CoV-2 RBD. Thus, Ta is a well-characterized, experimentally validated starting lead for method development and optimization.

(2) Experimental specificity controls. We appreciate the concern that weak apparent affinities can reflect non-specific binding. As noted in our response to “Comment (2)”, we applied multiple experimental controls that argue against non-specificity: (i) a literature-reported weak binder (Tc) was used as a negative control and produced no detectable complex under identical EMSA conditions (see Figs. 2F–G), demonstrating the assay’s ability to discriminate non-binders from specific binders; (ii) competitive EMSA assays with a commercial neutralizing monoclonal antibody (40592-R001) show that both Ta and Ta^G34C engage the same or overlapping RBD site as the antibody, and that Ta^G34C is substantially more resistant to antibody displacement than WT Ta (see Figs. 3D–E, 5D). Together, these wet-lab controls support that the observed aptamer-RBD bands reflect specific interactions rather than general, non-specific adsorption.

(3) Variant and specificity analysis by rigorous FEP calculations. To address the reviewer’s request to evaluate variant sensitivity, we performed extensive free energy perturbation combined with Hamiltonian replica-exchange molecular dynamics (FEP/HREX) for improved convergence efficiency and increased simulation time to estimate relative binding free energy changes (ΔΔG) of both WT Ta and the optimized Ta^G34C against a panel of RBD variants. Results are provided in Tables S4 and S5. Representative findings include: For WT Ta versus early lineages, FEP reproduces the experimentally observed trends: Alpha (B.1.1.7; N501Y) yields ΔΔG_FEP = −0.42 ± 0.07 kcal/mol (ΔΔG_exp = −0.24), while Beta (B.1.351; K417N/E484K/N501Y) gives ΔΔG_FEP = 0.64 ± 0.25 kcal/mol (ΔΔG_exp = 0.36) (see Table S4). The agreement between the computational and experimental results supports the fidelity of our computational model for variant assessment. For the engineered Ta^G34C, calculations across a broad panel of variants indicate that Ta^G34C retains or improves binding (ΔΔG < 0) for the majority of tested variants, including Alpha, Beta, Gamma and many Omicron sublineages. Notable examples: BA.1 (ΔΔG = −3.00 ± 0.52 kcal/mol), BA.2 (ΔΔG = −2.54 ± 0.60 kcal/mol), BA.2.75 (ΔΔG = −5.03 ± 0.81 kcal/mol), XBB (ΔΔG = −3.13 ± 0.73 kcal/mol) and XBB.1.5 (ΔΔG = −2.28 ± 0.96 kcal/mol). A minority of other Omicron sublineages (e.g., BA.4 and BA.5) show modest positive ΔΔG values (2.11 ± 0.67 and 2.27 ± 0.68 kcal/mol, respectively), indicating a predicted reduction in affinity for those specific backgrounds. Overall, these data indicate that the designed Ta^G34C aptamer can maintain its binding ability with most SARS-CoV-2 variants, showing potential for broad-spectrum antiviral activity (see Table S5). The following has been added to “Results” of the revised manuscript. (Page 22 in the revised manuscript)

‘2.6 Binding performance of Ta and Ta^G34C against SARS-CoV-2 RBD variants

To further evaluate the binding performance and specificity of the designed aptamer Ta^G34C toward various SARS-CoV-2 variants [39], we conducted extensive free energy perturbation combined with Hamiltonian replica-exchange molecular dynamics (FEP/HREX) [40–42] for both the wild-type aptamer Ta and the optimized Ta^G34C against a series of RBD mutants. The representative variants include the early Alpha (B.1.1.7) and Beta (B.1.351) lineages, as well as a panel of Omicron sublineages (BA.1–BA.5, BA.2.75, BQ.1, XBB, XBB.1.5, EG.5.1, HK.3, JN.1, and KP.3) carrying multiple mutations within the RBD region (residues 333–527). For each variant, mutations within 5 Å of the bound aptamer were included in the FEP to accurately estimate the relative binding free energy change (ΔΔG).

For the wild-type Ta aptamer, the FEP-predicted binding affinities toward the Alpha and Beta RBD variants were consistent with the previous experimental results, further validating the reliability of our model (see Table S4). Specifically, Ta maintained comparable or slightly enhanced binding to the Alpha variant and showed only marginally reduced affinity for the Beta variant.

In contrast, the optimized aptamer Ta^G34C exhibited markedly improved and broad-spectrum binding capability toward most tested variants (see Table S5). For early variants such as Alpha, Beta, and Gamma, Ta^G34C maintained enhanced affinities (ΔΔG < 0). Notably, for multiple Omicron sublineages—including BA.1, BA.2, BA.2.12.1, BA.2.75, XBB, XBB.1.5, XBB.1.16, XBB.1.9, XBB.2.3, EG.5.1, XBB.1.5.70, HK.3, BA.2.86, JN.1 and JN.1.11.1—the calculated binding free energy changes ranged from −1.89 to −7.58 kcal/mol relative to the wild-type RBD, indicating substantially stronger interactions despite the accumulation of multiple mutations at the aptamer–RBD interface. Only in a few other Omicron sublineages, such as BA.4, BA.5, and KP.3, a slight reduction in binding affinity was observed (ΔΔG > 0).

These computational findings demonstrate that the Ta^G34C aptamer not only preserves high affinity for the RBD but also exhibits improved tolerance to the extensive mutational landscape of SARS-CoV-2. Collectively, our results suggest that Ta^G34C holds promise as a high-affinity and potentially cross-variant aptamer candidate for targeting diverse SARS-CoV-2 spike protein variants, showing potential for broad-spectrum antiviral activity.’

The following has been added to “Materials and Methods” of the revised manuscript. (Page 29 in the revised manuscript)

‘4.7 FEP/HREX

To evaluate the binding sensitivity of the optimized aptamer Ta^G34C toward SARS-CoV-2 RBD variants, we employed free energy perturbation combined with Hamiltonian replica-exchange molecular dynamics (FEP/HREX) simulations for enhanced sampling efficiency and improved convergence. The relative binding free energy changes (ΔΔG) upon RBD mutations were estimated as:

ΔΔ𝐺 = Δ𝐺_bound − Δ𝐺_free

where ΔG_bound and ΔG_free represent the RBD mutations-induced free energy changes in the complexed and unbound states, respectively. All simulations were performed using GROMACS 2021.5 with the Amber ff14SB force field. For each mutation, dual-topology structures were generated in a pmx-like manner, and 32 λ-windows (0.0, 0.01, 0.02, 0.03, 0.06, 0.09, 0.12, 0.16, 0.20, 0.24, 0.28, 0.32, 0.36, 0.40, 0.44, 0.48, 0.52, 0.56, 0.60, 0.64, 0.68, 0.72, 0.76, 0.80, 0.84, 0.88, 0.91, 0.94, 0.97, 0.98, 0.99, 1.0) were distributed uniformly between 0.0 and 1.0. To ensure sufficient sampling, each window was simulated for 5 ns, with five independent replicas initiated from distinct velocity seeds. Replica exchange between adjacent λ states was attempted every 1 ps to enhance phase-space overlap and sampling convergence. The van der Waals and electrostatic transformations were performed simultaneously, employing a soft-core potential (α = 0.3) to avoid singularities. For each RBD variant system, this setup resulted in an accumulated simulation time of approximately 1600 ns (5 ns × 32 windows × 5 replicas × 2 states). The Gromacs bar analysis tool was used to estimate the binding free energy changes.’

Tables S4 and S5 have been added to Supplementary Information of the revised manuscript.

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Reviewer #2 (Public review):

Summary

In this manuscript, the authors combine an automated touchscreen-based trial-unique nonmatching-to-location (TUNL) task with activity-dependent labeling (TRAP/c-Fos) and birth-dating of adult-born dentate granule cells (abDGCs) to examine how cognitive demand modulates dentate gyrus (DG) activity patterns. By varying spatial separation between sample and choice locations, the authors operationally increase task difficulty and show that higher demand is associated with increased mature granule cell (mGC) activity and an amplified suprapyramidal (SB) versus infrapyramidal (IB) blade bias. Using chemogenetic inhibition, they further demonstrate dissociable contributions of abDGCs and mGCs to task performance and DG activation patterns.

The combination of behavioral manipulation, spatially resolved activity tagging, and temporally defined abDGC perturbations is a strength of the study and provides a novel circuit-level perspective on how adult neurogenesis modulates DG function. In particular, the comparison across different abDGC maturation windows is well designed and narrows the functionally relevant population to neurons within the critical period (~4-7 weeks). The finding that overall mGC activity levels, in addition to spatially biased activation patterns, are required for successful performance under high cognitive demand is intriguing.

Major Comments

(1) Individual variability and the relationship between performance and DG activation.

The manuscript reports substantial inter-animal variability in the number of days required to reach the criterion, particularly during large-separation training. Given this variability, it would be informative to examine whether individual differences in performance correlate with TRAP+ or c-Fos+ density and/or spatial bias metrics. While the authors report no correlation between success and TRAP+ density in some analyses, a more systematic correlation across learning rate, final performance, and DG activation patterns (mGC vs abDGC, SB vs IB) could strengthen the interpretation that DG activity reflects task engagement rather than performance only.

(2) Operational definition of "cognitive demand".

The distinction between low (large separation) and high (small separation) cognitive demand is central to the manuscript, yet the definition remains somewhat broad. Reduced spatial separation likely alters multiple behavioral variables beyond cognitive load, including reward expectation, attentional demands, confidence, engagement, and potentially motivation. The authors should more explicitly acknowledge these alternative interpretations and clarify whether "cognitive demand" is intended as a composite construct rather than a strictly defined cognitive operation.

(3) Potential effects of task engagement on neurogenesis.

Given the extensive behavioral training and known effects of experience on adult neurogenesis, it remains unclear whether the task itself alters the size or maturation state of the abDGC population. Although the focus is on activity and function rather than cell number, it would be useful to clarify whether neurogenesis rates were assessed or controlled for, or to explicitly state this as a limitation.

(4) Temporal resolution of activity tagging.

TRAP and c-Fos labeling provide a snapshot of neural activity integrated over a temporal window, making it difficult to determine which task epochs or trial types drive the observed activation patterns. This limitation is partially acknowledged, but the conclusions occasionally imply trial-specific or demand-specific encoding. The authors should more clearly distinguish between sustained task engagement and moment-to-moment trial processing, and temper interpretations accordingly. While beyond the scope of the current study, this also motivates future experiments using in vivo recording approaches.

(5) Interpretation of altered spatial patterns following abDGC inhibition.

In the abDGC inhibition experiments, Cre+ DCZ animals show delayed learning relative to controls. As a result, when animals are sacrificed, they may be at an intermediate learning stage rather than at an equivalent behavioral endpoint. This raises the possibility that altered DG activation patterns reflect the learning stage rather than a direct circuit effect of abDGC inhibition. Additional clarification or analysis controlling for the learning stage would strengthen the causal interpretation.

(6) Relationship between c-Fos density and behavioral performance.

The study reports that abDGC inhibition increases c-Fos density while impairing performance, whereas mGC inhibition decreases c-Fos density and also impairs performance. This raises an important conceptual question regarding the relationship between overall activity levels and task success. The authors suggest that both sufficient activity and appropriate spatial patterning are required, but the manuscript would benefit from a more explicit discussion of how different perturbations may shift the identity, composition, or coordination of the active neuronal ensemble rather than simply altering total activity levels.

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Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Weaknesses:

The technical approach is strong and the conceptual framing is compelling, but several aspects of the evidence remain incomplete. In particular, it is unclear whether the reported changes in connectivity truly capture causal influences, as the rank metrics remain correlational and show discrepancies with the manipulation results.

We agree that our functional connectivity ranking analyses cannot establish causal influences. As discussed in the manuscript, besides learning-related activity changes, the functional connectivity may also be influenced by neuromodulatory systems and internal state fluctuations. In addition, the spatial scope of our recordings is still limited compared to the full network implicated in visual discrimination learning, which may bias the ranking estimates. In future, we aim to achieve broader region coverage and integrate multiple complementary analyses to address the causal contribution of each region.

The absolute response onset latencies also appear slow for sensory-guided behavior in mice, and it is not clear whether this reflects the method used to define onset timing or factors such as task structure or internal state.

We believe this may be primarily due to our conservative definition of onset timing. Specifically, we required the firing rate to exceed baseline (t-test, p < 0.05) for at least 3 consecutive 25-ms time windows. This might lead to later estimates than other studies, such as using the latency to the first spike after visual stimulus onset (Siegle et al., 2021) or the time to half-max response (Goldbach, Akitake, Leedy, & Histed, 2021).

The estimation of response onset latency in our study may also be affected by potential internal state fluctuations of the mice. We used the time before visual stimulus onset as baseline firing, since firing rates in this period could be affected by trial history, we acknowledge this may increase the variability of the baseline, thus increase the difficulty to statistically detect the onset of response.

Still, we believe these concerns do not affect the observation of the formation of compressed activity sequence in CR trials during learning.

Furthermore, the small number of animals, combined with extensive repeated measures, raises questions about statistical independence and how multiple comparisons were controlled.

We agree that a larger sample size would strengthen the robustness of the findings. However, as noted above, the current dataset has inherent limitations in both the number of recorded regions and the behavioral paradigm. Given the considerable effort required to achieve sufficient unit yields across all targeted regions, we wish to adjust the set of recorded regions, improve behavioral task design, and implement better analyses in future studies. This will allow us to both increase the number of animals and extract more precise insights into mesoscale dynamics during learning.

The optogenetic experiments, while intended to test the functional relevance of rank increasing regions, leave it unclear how effectively the targeted circuits were silenced. Without direct evidence of reliable local inhibition, the behavioral effects or lack thereof are difficult to interpret.

We appreciate this important point. Due to the design of the flexible electrodes and the implantation procedure, bilateral co-implantation of both electrodes and optical fibers was challenging, which prevented us from directly validating the inhibition effect in the same animals used for behavior. In hindsight, we could have conducted parallel validations using conventional electrodes, and we will incorporate such controls in future work to provide direct evidence of manipulation efficacy.

Details on spike sorting are limited.

We have provided more details on spike sorting in method section, including the exact parameters used in the automated sorting algorithm and the subsequent manual curation criteria.

Reviewer #2 (Public review):

Weaknesses:

I had several major concerns:

(1) The number of mice was small for the ephys recordings. Although the authors start with 7 mice in Figure 1, they then reduce to 5 in panel F. And in their main analysis, they minimize their analysis to 6/7 sessions from 3 mice only. I couldn't find a rationale for this reduction, but in the methods they do mention that 2 mice were used for fruitless training, which I found no mention in the results. Moreover, in the early case, all of the analysis is from 118 CR trials taken from 3 mice. In general, this is a rather low number of mice and trial numbers. I think it is quite essential to add more mice.

We apologize for the confusion. As described in the Methods section, 7 mice (Figure 1B) were used for behavioral training without electrode array or optical fiber implants to establish learning curves, and an additional 5 mice underwent electrophysiological recordings (3 for visual-based decision-making learning and 2 for fruitless learning).

As we noted in our response to Reviewer #1, the current dataset has inherent limitations in both the number of recorded regions and the behavioral paradigm. Given the considerable effort required to achieve high-quality unit yields across all targeted regions, we wish to adjust the set of recorded regions, improve behavioral task design, and implement better analyses in future studies. These improvements will enable us to collect data from a larger sample size and extract more precise insights into mesoscale dynamics during learning.

(2) Movement analysis was not sufficient. Mice learning a go/no-go task establish a movement strategy that is developed throughout learning and is also biased towards Hit trials. There is an analysis of movement in Figure S4, but this is rather superficial. I was not even sure that the 3 mice in Figure S4 are the same 3 mice in the main figure. There should be also an analysis of movement as a function of time to see differences. Also for Hits and FAs. I give some more details below. In general, most of the results can be explained by the fact that as mice gain expertise, they move more (also in CR during specific times) which leads to more activation in frontal cortex and more coordination with visual areas. More needs to be done in terms of analysis, or at least a mention of this in the text.

Due to the limitation in the experimental design and implementation, movement tracking was not performed during the electrophysiological recordings, and the 3 mice shown in Figure S4 (now S5) were from a separate group. We have carefully examined the temporal profiles of mouse movements and found it did not fully match the rank dynamics for all regions, and we have added these results and related discussion in the revised manuscript. However, we acknowledge the observed motion energy pattern could explain some of the functional connection dynamics, such as the decrease in face and pupil motion energy could explain the reduction in ranks for striatum.

Without synchronized movement recordings in the main dataset, we cannot fully disentangle movement-related neural activity from task-related signals. We have made this limitation explicit in the revised manuscript and discuss it as a potential confound, along with possible approaches to address it in future work.

(3) Most of the figures are over-detailed, and it is hard to understand the take-home message. Although the text is written succinctly and rather short, the figures are mostly overwhelming, especially Figures 4-7. For example, Figure 4 presents 24 brain plots! For rank input and output rank during early and late stim and response periods, for early and expert and their difference. All in the same colormap. No significance shown at all. The Δrank maps for all cases look essentially identical across conditions. The division into early and late time periods is not properly justified. But the main take home message is positive Δrank in OFC, V2M, V1 and negative Δrank in ThalMD and Str. In my opinion, one trio map is enough, and the rest could be bumped to the Supplementary section, if at all. In general, the figure in several cases do not convey the main take home messages. See more details below.

We thank the reviewer for this valuable critique. The statistical significance corresponding to the brain plots (Figure 4 and Figure 5) was presented in Figure S3 and S5 (now Figure S5 and S7 in the revised manuscript), but we agree that the figure can be simplified to focus on the key results.

In the revised manuscript, we have condensed these figures to focus on the most important comparisons to make the visual presentation more concise and the take-home message clearer.

(4) The analysis is sometimes not intuitive enough. For example, the rank analysis of input and output rank seemed a bit over complex. Figure 3 was hard to follow (although a lot of effort was made by the authors to make it clearer). Was there any difference between the output and input analysis? Also, the time period seems redundant sometimes. Also, there are other network analysis that can be done which are a bit more intuitive. The use of rank within the 10 areas was not the most intuitive. Even a dimensionality reduction along with clustering can be used as an alternative. In my opinion, I don't think the authors should completely redo their analysis, but maybe mention the fact that other analyses exist

We appreciate the reviewer’s comment. In brief, the input- and output-rank analyses yielded largely similar patterns across regions in CR trials, although some differences were observed in certain areas (e.g., striatum) in Hit trials, where the magnitude of rank change was not identical between input and output measures. We have condensed the figures to only show averaged rank results, and the colormap was updated to better covey the message.

We did explore dimensionality reduction applied to the ranking data. However, the results were not intuitive as well and required additional interpretation, which did not bring more insights. Still, we acknowledge that other analysis approaches might provide complementary insights.

Reviewer #3 (Public review):

Weaknesses:

The weakness is also related to the strength provided by the method. It is demonstrated in the original method that this approach in principle can track individual units for four months (Luan et al, 2017). The authors have not showed chronically tracked neurons across learning. Without demonstrating that and taking advantage of analyzing chronically tracked neurons, this approach is not different from acute recording across multiple days during learning. Many studies have achieved acute recording across learning using similar tasks. These studies have recorded units from a few brain areas or even across brain-wide areas.

We appreciate the reviewer’s important point. We did attempt to track the same neurons across learning in this project. However, due to the limited number of electrodes implanted in each brain region, the number of chronically tracked neurons in each region was insufficient to support statistically robust analyses. Concentrating probes in fewer regions would allow us to obtain enough units tracked across learning in future studies to fully exploit the advantages of this method.

Another weakness is that major results are based on analyses of functional connectivity that is calculated using the cross-correlation score of spiking activity (TSPE algorithm). Functional connection strengthen across areas is then ranked 1-10 based on relative strength. Without ground truth data, it is hard to judge the underlying caveats. I'd strongly advise the authors to use complementary methods to verify the functional connectivity and to evaluate the mesoscale change in subnetworks. Perhaps the authors can use one key information of anatomy, i.e. the cortex projects to the striatum, while the striatum does not directly affect other brain structures recorded in this manuscript

We agree that the functional connectivity measured in this study relies on statistical correlations rather than direct anatomical connections. We plan to test the functional connection data with shorter cross-correlation delay criteria to see whether the results are consistent with anatomical connections and whether the original findings still hold.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The small number of mice, each contributing many sessions, complicates the  interpretation of the data. It is unclear how statistical analyses accounted for the small  sample size, repeated measures, and non-independence across sessions, or whether  multiple comparisons were adequately controlled.

We realized the limitation from the small number of animal subjects, yet the difficulty to achieve sufficient unit yields across all regions in the same animal restricted our sample size. Though we agree that a larger sample size would strengthen the robustness of the findings, however, as noted below the current dataset has inherent limitations in both the scope of recorded regions and the behavioral paradigm.

Given the considerable effort required to achieve sufficient unit yields across all targeted regions, we wish to adjust the set of recorded regions, improve behavioral task design, and implement better analyses in future studies. This will allow us to both increase the number of animals and extract more precise insights into mesoscale dynamics during learning.

(2) The ranking approach, although intuitive for visualizing relative changes in  connectivity, is fundamentally descriptive and does not reflect the magnitude or  reliability of the connections. Converting raw measures into ordinal ranks may obscure  meaningful differences in strength and can inflate apparent effects when the underlying  signal is weak.

We agree with this important point. As stated in the manuscript, our motivation in taking the ranking approach was that the differences in firing rates might bias cross-correlation between spike trains, making raw accounts of significant neuron pairs difficult to compare across conditions, but we acknowledge the ranking measures might obscure meaningful differences or inflate weak effects in the data.

We added the limitations of ranking approach in the discussion section and emphasized the necessity in future studies for better analysis approaches that could provide more accurate assessment of functional connection dynamics without bias from firing rates.

(3) The absolute response onset latencies also appear quite slow for sensory-guided  behavior in mice, and it remains unclear whether this reflects the method used to  determine onset timing or factors such as task design, sensorimotor demands, or  internal state. The approach for estimating onset latency by comparing firing rates in  short windows to baseline using a t-test raises concerns about robustness, as it may  be sensitive to trial-to-trial variability and yield spurious detections.

We agree this may be primarily due to our conservative definition of onset timing. Specifically, we required the firing rate to exceed baseline (t-test, p < 0.05) for at least 3 consecutive 25-ms time windows. This might lead to later estimates than other studies, such as using the latency to the first spike after visual stimulus onset (Siegle et al., 2021) or the time to half-max response (Goldbach, Akitake, Leedy, & Histed, 2021).

The estimation of response onset latency in our study may also be affected by potential internal state fluctuations of the mice. We used the time before visual stimulus onset as baseline firing, since firing rates in this period could be affected by trial history, we acknowledge this may increase the variability of the baseline, thus increase the difficulty to statistically detect the onset of response.

Still, we believe these concerns do not affect the observation of the formation of compressed activity sequence in CR trials during learning.

(4) Details on spike sorting are very limited. For example, defining single units only by  an interspike interval threshold above one millisecond may not sufficiently rule out  contamination or overlapping clusters. How exactly were neurons tracked across days  (Figure 7B)?

We have added more details on spike sorting, including the processing steps and important parameters used in the automated sorting algorithm. Only the clusters well isolated in feature space were accepted in manual curation.

We attempted to track the same neurons across learning in this project. However, due to the limited number of electrodes implanted in each brain region, the number of chronically tracked neurons in each region was insufficient to support statistically robust analyses.

This is now stated more clearly in the discussion section.

(5) The optogenetic experiments, while designed to test the functional relevance of  rank-increasing regions, also raise questions. The physiological impact of the inhibition  is not characterized, making it unclear how effectively the targeted circuits were  actually silenced. Without clearer evidence that the manipulations reliably altered local  activity, the interpretation of the observed or absent behavioral effects remains  uncertain.

We appreciate this important point. Due to the design of the flexible electrodes and the implantation procedure, bilateral co-implantation of both electrodes and optical fibers was challenging, which prevented us from directly validating the inhibition effect in the same animals used for behavior. In hindsight, we could have conducted parallel validations using conventional electrodes, and we will incorporate such controls in future work to provide direct evidence of manipulation efficacy. 

(6) The task itself is relatively simple, and the anatomical coverage does not include  midbrain or cerebellar regions, limiting how broadly the findings can be generalized to more flexible or ethologically relevant forms of decision-making.

We appreciate this advice and have expanded the existing discussion to more explicitly state that the relatively simple task design and anatomical coverage might limit the generalizability of our findings.

(7) The abstract would benefit from more consistent use of tense, as the current mix of  past and present can make the main findings harder to follow. In addition, terms like  "mesoscale network," "subnetwork," and "functional motif" are used interchangeably in  places; adopting clearer, consistent terminology would improve readability.

We have changed several verbs in abstract to past form, and we now adopted a more consistent terminology by substituting “functional motif” as “subnetwork”. We still feel the use of

“mesoscale network” and “subnetwork” could emphasize different aspects of the results according to the context, so these words are kept the same.

(8) The discussion could better acknowledge that the observed network changes may  not reflect task-specific learning alone but could also arise from broader shifts in  arousal, attention, or motivation over repeated sessions.

We have expanded the existing discussion to better acknowledge the possible effects from broader shifts in arousal, attention, or motivation over repeated sessions.

(9) The figures would also benefit from clearer presentation, as several are dense and  not straightforward to interpret. For example, Figure S8 could be organized more  clearly to highlight the key comparisons and main message

We have simplified the over-detailed brain plots in Figure 4-5, and the plots in Figure 6 and S8 (now S10 in the revised manuscript).

(10) Finally, while the manuscript notes that data and code are available upon request,  it would strengthen the study's transparency and reproducibility to provide open access  through a public repository, in line with best practices in the field.

The spiking data, behavior data and codes for the core analyses in the manuscript are now shared in pubic repository (Dryad). And we have changed the description in the Data Availability secition accordingly.

Reviewer #2 (Recommendations for the authors):

(A) Introduction:

(1) "Previous studies have implicated multiple cortical and subcortical regions in visual  task learning and decision-making". No references here, and also in the next sentence.

The references were in the following introduction and we have added those references here as well.

We also added one review on cortical-subcortical neural correlates in goal-directed behavior (Cruz et al., 2023).

(2) Intro: In general, the citation of previous literature is rather minimal, too minimal.  There is a lot of studies using large scale recordings during learning, not necessarily  visual tasks. An example for brain-wide learning study in subcortical areas is Sych et  al. 2022 (cell reports). And for wide-field imaging there are several papers from the  Helmchen lab and Komiyama labs, also for multi-area cortical imaging.

We appreciate this advice. We included mainly visual task learning literature to keep a more focused scope around the regions and task we actually explored in this study. We fear if we expand the intro to include all the large-scale imaging/recording studies in learning field, the background part might become too broad.

We have included (Sych, Fomins, Novelli, & Helmchen, 2022) for its relevance and importance in the field.

(3) In the intro, there is only a mention of a recording of 10 brain regions, with no  mention of which areas, along with their relevance to learning. This is mentioned in the  results, but it will be good in the intro.

The area names are now added in intro.

(B) Results:

(1) Were you able to track the same neurons across the learning profile? This is not  stated clearly.

We did attempt to track the same neurons across learning in this project. However, due to the limited number of electrodes implanted in each brain region, the number of chronically tracked neurons in each region was insufficient to support statistically robust analyses.

We now stated this more clearly in the discussion section.

(2) Figure 1 starts with 7 mice, but only 5 mice are in the last panel. Later it goes down  to 3 mice. This should be explained in the results and justified.

We apologize for the confusion. As described in the Methods section, 7 mice (Figure 1B) were used for behavioral training without electrode array or optical fiber implants to establish learning curves, and an additional 5 mice underwent electrophysiological recordings (3 for visual-based decision-making learning and 2 for fruitless learning).

(3) I can't see the electrode tracks in Figure 1d. If they are flexible, how can you make  sure they did not bend during insertion? I couldn't find a description of this in the  methods also.

The electrode shanks were ultra-thin (1-1.5 µm) and it was usually difficult to recover observable tracks or electrodes in section.

The ultra-flexible probes could not penetrate brain on their own (since they are flexible), and had to be shuttled to position by tungsten wires through holes designed at the tip of array shanks. The tungsten wires were assembled to the electrode array before implantation; this was described in the section of electrode array fabrication and assembly. We also included the description about the retraction of the guiding tungsten wires in the surgery section to avoid confusion.

As an further attempt to verify the accuracy of implantation depth, we also measured the repeatability of implantation in a group of mice and found a tendency for the arrays to end in slightly deeper location in cortex (142.1 ± 55.2 μm, n = 7 shanks), and slightly shallower location in subcortical structure (-122.6 ± 71.7 μm, n = 7 shanks). We added these results as new Figure S1 to accompany Figure 1.

(4) In the spike rater in 1E, there seems to be ~20 cells in V2L, for example, but in 1F,  the number of neurons doesn't go below 40. What is the difference here? 

We checked Figure 1F, the plotted dots do go below 40 to ~20. Perhaps the file that reviewer received wasn’t showing correctly?

(5) The authors focus mainly on CR, but during learning, the number of CR trials is  rather low (because they are not experts). This can also be seen in the noisier traces  in Figure 2a. Do the authors account for that (for example by taking equal trials from  each group)? 

We accounted this by reconstructing bootstrap-resampled datasets with only 5 trials for each session in both the early stage and the expert stage. The mean trace of the 500 datasets again showed overall decrease in CR trial firing rate during task learning, with highly similar temporal dynamics to the original data.

The figure is now added to supplementary materials (as Figure S3 in the revised manuscript).

(6) From Figure 2a, it is evident that Hit trials increase response when mice become  experts in all brain areas. The authors have decided to focus on the response onset  differences in CRs, but the Hit responses display a strong difference between naïve  and expert cases.

Judged from the learning curve in this task the mice learned to inhibit its licking action when the No-Go stimuli appeared, which is the main reason we focused on these types of trials.

The movement effects and potential licking artefacts in Hit trials also restricted our interpretation of these trials.

(7) Figure 3 is still a bit cumbersome. I wasn't 100% convinced of why there is a need  to rank the connection matrix. I mean when you convert to rank, essentially there could  be a meaningful general reduction in correlation, for example during licking, and this  will be invisible in the ranking system. Maybe show in the supp non-ranked data, or  clarify this somehow

We agree with this important point. As stated in the manuscript and response to Reviewer #1, our motivation in taking the ranking approach was that the differences in firing rates could bias cross-correlation between spike trains, making raw accounts of significant neuron pairs difficult to compare across conditions, but we acknowledge the ranking measures might obscure meaningful differences or inflate weak effects in the data.

We added the limitations of ranking approach in the discussion section and emphasized the necessity in future studies for better analysis approaches that could provide more accurate assessment of functional connection dynamics without bias from firing rates.

(8) Figure 4a x label is in manuscript, which is different than previous time labels,  which were seconds.

We now changed all time labels from Figure 2 to milliseconds.

(9) Figure 4 input and output rank look essentially the same.

We have compressed the brain plots in Figures 4-5 to better convey the take-home message.

(10) Also, what is the late and early stim period? Can you mark each period in panel A? Early stim period is confusing with early CR period. Same for early respons and late response.

The definition of time periods was in figure legends. We now mark each period out to avoid confusion.

(11) Looking at panel B, I don't see any differences between delta-rank in early stim,  late stim, early response, and late response. Same for panel c and output plots.

The rankings were indeed relatively stable across time periods. The plots are now compressed and showed a mean rank value.

(12) Panels B and C are just overwhelming and hard to grasp. Colors are similar both  to regular rank values and delta-rank. I don't see any differences between all  conditions (in general). In the text, the authors report only M2 to have an increase in  rank during the response period. Late or early response? The figure does not go well  with the text. Consider minimizing this plot and moving stuff to supplementary.

The colormap are now changed to avoid confusion, and brain plots are now compressed.

(13) In terms of a statistical test for Figure 4, a two-way ANOVA was done, but over  what? What are the statistics and p-values for the test? Is there a main effect of time  also? Is their a significant interaction? Was this done on all mice together? How many  mice? If I understand correctly, the post-hoc statistics are presented in the  supplementary, but from the main figure, you cannot know what is significant and what  is not.

For these figures we were mainly concerned with the post-hoc statistics which described the changes in the rankings of each region across learning.

We have changed the description to “t-test with Sidak correction” to avoid the confusion.

(14) In the legend of Figure 4, it is reported that 610 expert CR trials from 6 sessions,  instead of 7 sessions. Why was that? Also, like the previous point, why only 3 mice?

Behavior data of all the sessions used were shown in Figure S1. There were only 3 mice used for the learning group, the difficulty to achieve sufficient unit yields across all regions in the same animal restricted our sample size

(15) Body movement analysis: was this done in a different cohort of mice? Only now  do I understand why there was a division into early and late stim periods. In supp 4,  there should be a trace of each body part in CR expert versus naïve. This should also  be done for Hit trials as a sanity check. I am not sure that the brightness difference  between consecutive frames is the best measure. Rather try to calculate frame-to frame correlation. In general, body movement analysis is super important and should  be carefully analyzed.

Due to the limitation in the experimental design and implementation, movement tracking was not performed during the electrophysiological recordings, and the 3 mice shown in Figure S4 (now S5) were from a separate group. We have carefully examined the temporal profiles of mouse movements and found it did not fully match the rank dynamics for all regions, and we have added these results and related discussion in the revised manuscript. However, we acknowledge the observed motion energy pattern could explain some of the functional connection dynamics, such as the decrease in face and pupil motion energy could explain the reduction in ranks for striatum.

Without synchronized movement recordings in the main dataset, we cannot fully disentangle movement-related neural activity from task-related signals. We have made this limitation explicit in the revised manuscript and discuss it as a potential confound, along with possible approaches to address it in future work.

(16) For Hit trials, in the striatum, there is an increase in input rank around the  response period, and from Figure S6 it is clear that this is lick-related. Other than that,  the authors report other significant changes across learning and point out to Figure 5b,c. I couldn't see which areas and when it occurred.

We did naturally expect the activity in striatum to be strongly related to movement.

With Figure S6 (now S7) we wished to show that the observed rank increase for striatum could not simply be attributed to changes in time of lick initiation.

As some readers may argue that during learning the mice might have learned to only intensely lick after response signal onset, causing the observed rise of input rank after response signal, we realigned the spikes in each trial to the time of the first lick, and a strong difference could still be observed between early training stage and expert training stage.

We still cannot fully rule out the effects from more subtle movement changes, as the face motion energy did increase in early response period. This result and related discussion has been added to the results section of revised manuscript.

(17) Figure 6, again, is rather hard to grasp. There are 16 panels, spread over 4 areas,  input and output, stim and response. What is the take home message of all this?  Visually, it's hard to differentiate between each panel. For me, it seems like all the  panels indicate that for all 4 areas, both in output and input, frontal areas increase in  rank. This take-home message can be visually conveyed in much less tedious ways.  This simpler approach is actually conveyed better in the text than in the figures  themselves. Also, the whole explanation on how this analysis was done, was not clear  from the text. If I understand it, you just divided and ranked the general input (or  output) into individual connections? If so, then this should be better explained.

We appreciate this advice and we have compressed the figures to better convey the main message.The rankings for Figure 6 and Figure S8 (now Figure S9) was explained in the left panel of Figure 3C. Each non-zero element in the connection matrix was ranked to value from 1-10, with a value of 10 represented the 10% strongest non-zero elements in the matrix.

We have updated the figure legends of Figure 3, and we have also updated the description in methods (Connection rank analyses) to give a clearer description of how the analyses were applied in subsequent figures.

(18) Figure 7: Here, the authors perform a ROC analysis between go and no-go  stimuli. They balance between choice, but there is still an essential difference between  a hit and a FA in terms of movement and licks. That is maybe why there is a big  difference in selective units during the response period. For example, during a Hit trial  the mouse licks and gets a reward, resulting in more licking and excitement. In FAs,the mouse licks, but gets punished, which causes a reduction in additional licking and  movements. This could be a simple explanation why the ROC was good in the late  response period. Body movement analysis of Hit and FA should be done as in Figure  S4.

We appreciate this insightful advice.

Though we balanced the numbers of basic trial types, we couldn’t rule out the difference in the intrinsic movement amount difference in FA trials and Hit trials, which is likely the reason of large proportion of encoding neurons in response period.

We have added this discussion both in result section and discussion section along with the necessity of more carefully designed behavior paradigm to disentangle task information.

(19) The authors also find selective neurons before stimulus onset, and refer to trial  history effects. This can be directly checked, that is if neurons decode trial history.

We attempted encoding analyses on trial history, but regrettably for our dataset we could not find enough trials to construct a dataset with fully balanced trial history, visual stimulus and behavior choice.

(20) Figure 7e. What is the interpretation for these results? That areas which peaked  earlier had more input and output with other areas? So, these areas are initiating  hubs? Would be nice to see ACC vs Str traces from B superimposed on each other.  Having said this, the Str is the only area to show significant differences in the early  stim period. But is also has the latest peak time. This is a bit of a discrepancy.

We appreciate this important point.

The limitation in the anatomical coverage of brain regions restricted our interpretation about these findings. They could be initiating hubs or earlier receiver of the true initiating hubs that were not monitored in our study.

The Str trace was in fact above the ACC trace, especially in the response period. This could be explained by the above advice 18: since we couldn’t rule out the difference in the intrinsic movement amount difference in FA trials and Hit trials, and considering striatum activity is strongly related to movement, the Str trace may reflect more in the motion related spike count difference between FA trials and Hit trials, instead of visual stimulus related difference.

This further shows the necessity of more carefully designed behavior paradigm to disentangle task information.

The striatum trace also in fact didn’t show a true double peak form as traces in other regions, it ramped up in the stimulus region and only peaked in response period. This description is now added to the results section.

In the early stim period, the Striatum did show significant differences in average percent of encoding neurons, as the encoding neurons were stably high in expert stage. The striatum activity is more directly affected Still the percentage of neurons only reached peak in late stimulus period.

(21) For the optogenetic silencing experiments, how many mice were trained for each  group? This is not mentioned in the results section but only in the legend of Figure 8. This part is rather convincing in terms of the necessity for OFC and V2M

We have included the mice numbers in results section as well.

(C) Discussion

(1) There are several studies linking sensory areas to frontal networks that should be  mentioned, for example, Esmaeili et a,l 2022, Matteucci et al., 2022, Guo et a,l 2014,Gallero Salas et al, 2021, Jerry Chen et al, 2015. Sonja Hofer papers, maybe. Probably more.

We appreciate this advice. We have now included one of the mentioned papers (Esmaeili et al., 2022) in the results section and discussion section for its direct characterization of the enhanced coupling between somatosensory region and frontal (motor) region during sensory learning.The other studies mentioned here seem to focus more on the differences in encoding properties between regions along specific cortical pathways, rather than functional connection or interregional activity correlation, and we feel they are not directly related to the observations discussed.

(2) The reposted reorganization of brain-wide networks with shifts in time is best  described also in Sych et al. 2021.

We regret we didn’t include this important research and we have now cited this in discussion section.

(3) Regarding the discussion about more widespread stimulus encoding after learning,  the results indicate that the striatum emerges first in decoding abilities (Figure 7c left  panel), but this is not discussed at all.

We briefly discussed this in the result section. We tend to attribute this to trial history signal in striatum, but since the structure of our data could not support a direct encoding analysis on trial history, we felt it might be inappropriate to over-interpret the results.

(4) An important issue which is not discussed is the contribution of movement which  was shown to have a strong effect on brain-wide dynamics (Steinmetz et al 2019;  Musall et al 2019; Stringer et al 2019; Gilad et al 2018) The authors do have some movement analysis, but this is not enough. At least a discussion of the possible effects of movement on learning-related dynamics should be added.

We have included these studies in discussion section accordingly. Since the movement analyses were done in a separate cohort of mice, we have made our limitation explicit in the revised manuscript and discuss it as a potential confound, along with possible approaches to address it in future work.

(D) Methods

(1) How was the light delivery of the optogenetic experiments done? Via fiber  implantation in the OFC? And for V2M? If the red laser was on the skull, how did it get  to the OFC?

The fibers were placed on cortex surface for V2M group, and were implanted above OFC for OFC manipulation group. These were described in the viral injection part of the methods section.

(2) No data given on how electrode tracking was done post hoc

As noted in our response to the advice 3 in results section, the electrode shanks were ultra-thin (1-1.5 µm) and it was usually difficult to recover observable tracks or electrodes in section.

As an attempt to verify the accuracy of implantation depth, we measured the repeatability of implantation in a group of mice and found a tendency for the arrays to end in slightly deeper location in cortex (142.1 ± 55.2 μm, n = 7 shanks), and slightly shallower location in subcortical structure (-122.6 ± 71.7 μm, n = 7 shanks). We added these results as new Figure S1 to accompany Figure 1.

Reviewer #3 (Recommendations for the authors):

(1) The manuscript uses decision-making in the title, abstract and introduction.  However, nothing is related to decision learning in the results section. Mice simply  learned to suppress licking in no-go trials. This type of task is typically used to study behavioral inhibition. And consistent with this, the authors mainly identified changes  related to network on no-go trials. I really think the title and main message is  misleading. It is better to rephrase it as visual discrimination learning. In the  introduction, the authors also reviewed multiple related studies that are based on  learning of visual discrimination tasks.

We do view the Go/No-Go task as a specific genre of decision-making task, as there were literature that discussed this task as decision-making task under the framework of signal detection theory or updating of item values (Carandini & Churchland, 2013; Veling, Becker, Liu, Quandt, & Holland, 2022).

We do acknowledge the essential differences between the Go/No-Go task and the tasks that require the animal to choose between alternatives, and since we have now realized some readers may not accept this task as a decision task, we have changed the title to visual discrimination task as advised.

(2) Learning induced a faster onset on CR trials. As the no-go stimulus was not  presented to mice during early stages of training, this change might reflect the  perceptual learning of relevant visual stimulus after repeated presentation. This further  confirms my speculation, and the decision-making used in the title is misleading. 

We have changed the title to visual discrimination task accordingly.

(3) Figure 1E, show one hit trial. If the second 'no-go stimulus' is correct, that trial  might be a false alarm trial as mice licked briefly. I'd like to see whether continuous  licking can cause motion artifacts in recording. 

We appreciate this important point. There were indeed licking artifacts with continuous licking in Hit trials, which was part of the reason we focused our analyses on CR trials. Opto-based lick detectors may help to reduce the artefacts in future studies.

(4) What is the rationale for using a threshold of d' < 2 as the early-stage data and d'>3  as expert stage data?

The thresholds were chosen as a result from trade-off based on practical needs to gather enough CR trials in early training stage, while maintaining a relatively low performance.

Assume the mice showed lick response in 95% of Go stimulus trials, then d' < 2 corresponded to the performance level at which the mouse correctly rejected less than 63.9% of No-Go stimulus trials, and d' > 3 corresponded to the performance level at which the mouse correctly rejected more than 91.2% of No-Go stimulus trials.

(5) Figure 2A, there is a change in baseline firing rates in V2M, MDTh, and Str. There  is no discussion. But what can cause this change? Recording instability, problem in  spiking sorting, or learning?

It’s highly possible that the firing rates before visual stimulus onset is affected by previous reward history and task engagement states of the mice. Notably, though recorded simultaneously in same sessions, the changes in CR trials baseline firing rates in the V2M region were not observed in Hit trials.

Thus, though we cannot completely rule out the possibility in recording instability, we see this as evidence of the effects on firing rates from changes in trial history or task engagement during learning.

References:

Carandini, M., & Churchland, A. K. (2013). Probing perceptual decisions in rodents. Nat Neurosci, 16(7), 824-831. doi:10.1038/nn.3410.

Cruz, K. G., Leow, Y. N., Le, N. M., Adam, E., Huda, R., & Sur, M. (2023).Cortical-subcortical interactions in goal-directed behavior. Physiol Rev, 103(1), 347-389. doi:10.1152/physrev.00048.2021

Esmaeili, V., Oryshchuk, A., Asri, R., Tamura, K., Foustoukos, G., Liu, Y., Guiet, R., Crochet, S., & Petersen, C. C. H. (2022). Learning-related congruent and incongruent changes of excitation and inhibition in distinct cortical areas. PLOS Biology, 20(5), e3001667. doi:10.1371/journal.pbio.3001667

Goldbach, H. C., Akitake, B., Leedy, C. E., & Histed, M. H. (2021). Performance in even a simple perceptual task depends on mouse secondary visual areas. Elife, 10, e62156. doi:10.7554/eLife.62156.

Siegle, J. H., Jia, X., Durand, S., Gale, S., Bennett, C., Graddis, N., Heller, G.,Ramirez, T. K., Choi, H., Luviano, J. A., Groblewski, P. A., Ahmed, R., Arkhipov, A., Bernard, A., Billeh, Y. N., Brown, D., Buice, M. A., Cain, N.,Caldejon, S., Casal, L., Cho, A., Chvilicek, M., Cox, T. C., Dai, K., Denman, D.J., de Vries, S. E. J., Dietzman, R., Esposito, L., Farrell, C., Feng, D., Galbraith, J., Garrett, M., Gelfand, E. C., Hancock, N., Harris, J. A., Howard, R., Hu, B.,Hytnen, R., Iyer, R., Jessett, E., Johnson, K., Kato, I., Kiggins, J., Lambert, S., Lecoq, J., Ledochowitsch, P., Lee, J. H., Leon, A., Li, Y., Liang, E., Long, F., Mace, K., Melchior, J., Millman, D., Mollenkopf, T., Nayan, C., Ng, L., Ngo, K., Nguyen, T., Nicovich, P. R., North, K., Ocker, G. K., Ollerenshaw, D., Oliver, M., Pachitariu, M., Perkins, J., Reding, M., Reid, D., Robertson, M., Ronellenfitch, K., Seid, S., Slaughterbeck, C., Stoecklin, M., Sullivan, D., Sutton, B., Swapp, J., Thompson, C., Turner, K., Wakeman, W., Whitesell, J. D., Williams, D., Williford, A., Young, R., Zeng, H., Naylor, S., Phillips, J. W., Reid, R. C., Mihalas, S., Olsen, S. R., & Koch, C. (2021). Survey of spiking in the mouse visual system reveals functional hierarchy. Nature, 592(7852), 86-92. doi:10.1038/s41586-020-03171-x

Sych, Y., Fomins, A., Novelli, L., & Helmchen, F. (2022). Dynamic reorganization of the cortico-basal ganglia-thalamo-cortical network during task learning. Cell Rep, 40(12), 111394. doi:10.1016/j.celrep.2022.111394

Veling, H., Becker, D., Liu, H., Quandt, J., & Holland, R. W. (2022). How go/no-go training changes behavior: A value-based decision-making perspective. Current Opinion in Behavioral Sciences, 47,101206.

doi:https://doi.org/10.1016/j.cobeha.2022.101206.

Author response:

The following is the authors’ response to the previous reviews

eLife Assessment

This valuable study combines a computational language model, i.e., HM-LSTM, and temporal response function (TRF) modeling to quantify the neural encoding of hierarchical linguistic information in speech, and addresses how hearing impairment affects neural encoding of speech. The analysis has been significantly improved during the revision but remain somewhat incomplete - The TRF analysis should be more clearly described and controlled. The study is of potential interest to audiologists and researchers who are interested in the neural encoding of speech.

We thank the editors for the updated assessment. In the revised manuscript, we have added a more detailed description of the TRF analysis on p. of the revised manuscript. We have also updated Figure 1 to better visualize the analyses pipeline. Additionally, we have included a supplementary video to illustrate the architecture of the HM-LSTM model, the ridge regression methods using the model-derived features, and mTRF analysis using the acoustic envelop and the binary rate models.

Public Reviews:

Reviewer #1 (Public review):

About R squared in the plots:

The authors have used a z-scored R squared in the main ridge regression plots. While this may be interpretable, it seems non-standard and overly complicated. The authors could use a simple Pearson r to be most direct and informative (and in line with similar work, including Goldstein et al. 2022 which they mentioned). This way the sign of the relationships is preserved.

We did not use Pearson’s r as in Goldstein et al. (2022) because our analysis did not involve a train-test split, which was a key aspect of their approach. Specifically, Goldstein et al. (2022) divided their data into training and testing sets, trained a ridge regression model on the training set, and then used the trained model to predict neural responses on the test set. They calculated Pearson’s r to assess the correlation between the predicted and observed neural responses, making the correlation coefficient (r) their primary measure of model performance. In contrast, our analysis focused on computing the model fitting performance (R²) of the ridge regression model for each sensor and time point for each subject. At the group level, we conducted one-sample t-tests with spatiotemporal cluster-based correction on the R² values to identify sensors and time windows where R² values were significantly greater than baseline. We established the baseline by normalizing the R² values using Fisher z-transformation across sensors within each subject. We have added this explanation on p.13 of the revised manuscript.

About the new TRF analysis:

The new TRF analysis is a necessary addition and much appreciated. However, it is missing the results for the acoustic regressors, which should be there analogous to the HM-LSTM ridge analysis. The authors should also specify which software they have utilized to conduct the new TRF analysis. It also seems that the linguistic predictors/regressors have been newly constructed in a way more consistent with previous literature (instead of using the HM-LSTM features); these specifics should also be included in the manuscript (did it come from Montreal Forced Aligner, etc.?). Now that the original HM-LSTM can be compared to a more standard TRF analysis, it is apparent that the results are similar.

We used the Python package Eelbrain (https://eelbrain.readthedocs.io/en/r0.39/auto_examples/temporal-response-functions/trf_intro.html) to conduct the multivariate temporal response function (mTRF) analyses. As we previously explained in our response to R3, we did not apply mTRF to the acoustic features due to the high dimensionality of the input. Specifically, our acoustic representation consists of a 130-dimensional vector sampled every 10 ms throughout the speech stimuli (comprising a 129-dimensional spectrogram and a 1dimensional amplitude envelope). This led to interpreting the 130-dimensional TRF estimation difficult to interpret. A similar constraint applied to the hidden-layer activations from our HMLSTM model for the five linguistic features. After dimensionality reduction via PCA, each still resulted in 150-dimensional vectors. To address this, we instead used binary predictors marking the offset of each linguistic unit (phoneme, syllable, word, phrase, sentence). Since our speech stimuli were computer-synthesized, the phoneme and syllable boundaries were automatically generated. The word boundaries were manually annotated by a native Mandarin as in Li et al. (2022). The phrase boundaries were automatically annotated by the Stanford parser and manually checked by a native Mandarin speaker. These rate models are represented as five distinct binary time series, each aligned with the timing of the corresponding linguistic unit, making them well-suited for mTRF analysis. Although the TRF results from the 1-dimensional rate predictors and the ridge regression results from the high-dimensional HM-LSTM-derived features are similar, they encode different things: The rate regressors only encode the timing of linguistic unit boundaries, while the model-derived features encode the representational content of the linguistic input. Therefore, we do not consider the mTRF analyses to be analogous to the ridge regression analyses. Rather, these results complement each other and both provide informative results into the neural tracking of linguistic structures at different levels for the attended and unattended speech.

Since the TRF result for the continuous acoustic features also concerns R2, we have added an mTRF analysis where we fitted the one-dimensional speech envelope to the EEG. We extracted the envelope at 10 ms intervals for both attended and unattended speech and computed mTRFs independently for each subject and sensor using a basis of 50 ms Hamming windows spanning –100 ms to 300 ms relative to envelope onset. The results showed that in hearing-impaired participants, attended speech elicited a significant cluster in the bilateral temporal regions from 270 to 300 ms post-onset (t = 2.40, p = 0.01, Cohen’s d = 0.63). Unattended speech elicited an early cluster in right temporal and occipital regions from –100 ms to –80 ms (t = 3.07, p = 0.001, d = 0.83). Normal-hearing participants showed significant envelope tracking in the left temporal region at 280–300 ms after envelope onset (t = 2.37, p = 0.037, d = 0.48), with no significant cluster for unattended speech. These results further suggest that hearing-impaired listeners may have difficulty suppressing unattended streams. We have added the new TRF results for envelope to Figure S3 and the “mTRF results for attended and unattended speech” on p.7 and the “mTRF analysis” in Material and Methods of the revised manuscript.

The authors' wording about this suggests that these new regressors have a nonzero sample at each linguistic event's offset, not onset. This should also be clarified. As the authors know, the onset would be more standard, and using the offset has implications for understanding the timing of the TRFs, as a phoneme has a different duration than a word, which has a different duration from a sentence, etc.

In our rate‐model mTRF analyses, we initially labelled linguistic boundaries as “offsets” because our ridge‐regression with HM-LSTM features was aligned to sentence offsets rather than onsets. However, since each offset coincides with the next unit’s onset—and our regressors simply mark these transition points as 1—the “offset” and “onset” models yield identical mTRFs. To avoid confusion, we have relabeled “offset” as “boundary” in Figure S2.

As discussed in our prior responses, this design was based on the structure of our input to the HM-LSTM model, where each input consists of a pair of sentences encoded in phonemes, such as “t a_1 n əŋ_2 f ei_1 <sep> zh ə_4 sh iii_4 f ei_1 j ii_1” (“It can fly <sep> This is an airplane”). The two sentences are separated by a special <sep> token, and the model’s objective is to determine whether the second sentence follows the first, similar to a next-sentence prediction task. Since the model processes both sentences in full before making a prediction, the neural activations of interest should correspond to the point at which the entire sentence has been processed by humans. To enable a fair comparison between the model’s internal representations and brain responses, we aligned our neural analyses with the sentence offsets, capturing the time window after the sentence has been fully perceived by the participant. Thus, we extracted epochs from -100 to +300 ms relative to each sentence offset, consistent with our model-informed design.

We understand that phonemes, syllables, words, phrases, and sentences differ in their durations. However, the five hidden activity vectors extracted from the model are designed to capture the representations of these five linguistic levels across the entire sentence. Specifically, for a sentence pair such as “It can fly <sep> This is an airplane,” the first 2048-dimensional vector represents all the phonemes in the two sentences (“t a_1 n əŋ_2 f ei_1 <sep> zh ə_4 sh iii_4 f ei_1 j ii_1”), the second vector captures all the syllables (“ta_1 nəŋ_2 fei_1 <sep> zhə_4 shiii_4 fei_1jii_1”), the third vector represents all the words, the fourth vector captures the phrases, and the fifth vector represents the sentence-level meaning. In our dataset, input pairs consist of adjacent sentences from the stimuli (e.g., Sentence 1 and Sentence 2, Sentence 2 and Sentence 3, and so on), and for each pair, the model generates five 2048-dimensional vectors, each corresponding to a specific linguistic level. To identify the neural correlates of these model-derived features—each intended to represent the full linguistic level across a complete sentence—we focused on the EEG signal surrounding the completion of the second sentence rather than on incremental processing. Accordingly, we extracted epochs from -100 ms to +300 ms relative to the offset of the second sentence and performed ridge regression analyses using the five model features (reduced to 150 dimensions via PCA) at every 50 ms across the epoch. We have added this clarification on p.12 of the revised manuscript.

About offsets:

TRFs can still be interpretable using the offset timings though; however, the main original analysis seems to be utilizing the offset times in a different, more confusing way. The authors still seem to be saying that only the peri-offset time of the EEG was analyzed at all, meaning the vast majority of the EEG trial durations do not factor into the main HM-LSTM response results whatsoever. The way the authors describe this does not seem to be present in any other literature, including the papers that they cite. Therefore, much more clarification on this issue is needed. If the authors mean that the regressors are simply time-locked to the EEG by aligning their offsets (rather than their onsets, because they have varying onsets or some such experimental design complexity), then this would be fine. But it does not seem to be what the authors want to say. This may be a miscommunication about the methods, or the authors may have actually only analyzed a small portion of the data. Either way, this should be clarified to be able to be interpretable.

We hope that our response in RE4, along with the supplementary video, has helped clarify this issue. We acknowledge that prior studies have not used EEG data surrounding sentence offsets to examine neural responses at the phoneme or syllable levels. However, this is largely due to a lack of model that represent all linguistic levels across an entire sentence. There is abundant work comparing model predictors with neural data time-locked to offsets because they mark the point at which participants has already processed the relevant information (Brennan, 2016; Brennan et al., 2016; Gwilliams et al., 2024, 2025). Similarly, in our model– brain alignment study, our goal is to identify neural correlates for each model-derived feature. If we correlate model activity with EEG data aligned to sentence onsets, we would be examining linguistic representations at all levels (from phoneme to sentence) of the whole sentence at the time when participants have not heard the sentence yet. Although this limits our analysis to a subset of the data (143 sentences × 400 ms windows × 4 conditions), it targets the exact moment when full-sentence representations emerge against background speech, allowing us to examine each model-derived feature onto its neural signature. We have added this clarification on p.12 of the revised manuscript.

Reviewer #2 (Public review):

This study presents a valuable finding on the neural encoding of speech in listeners with normal hearing and hearing impairment, uncovering marked differences in how attention to different levels of speech information is allocated, especially when having to selectively attend to one speaker while ignoring an irrelevant speaker. The results overall support the claims of the authors, although a more explicit behavioural task to demonstrate successful attention allocation would have strengthened the study. Importantly, the use of more "temporally continuous" analysis frameworks could have provided a better methodology to assess the entire time course of neural activity during speech listening. Despite these limitations, this interesting work will be useful to the hearing impairment and speech processing research community. The study compares speech-in-quiet vs. multi-talker scenarios, allowing to assess within-participant the impact that the addition of a competing talker has on the neural tracking of speech. Moreover, the inclusion of a population with hearing loss is useful to disentangle the effects of attention orienting and hearing ability. The diagnosis of high-frequency hearing loss was done as part of the experimental procedure by professional audiologists, leading to a high control of the main contrast of interest for the experiment. Sample size was big, allowing to draw meaningful comparisons between the two populations.

We thank you very much for your appreciation of our research and we have now added a more description of the mTRF analyses on p.13-14 of the revised manuscript.

An HM-LSTM model was employed to jointly extract speech features spanning from the stimulus acoustics to word-level and phrase-level information, represented by embeddings extracted at successive layers of the model. The model was specifically expanded to include lower level acoustic and phonetic information, reaching a good representation of all intermediate levels of speech. Despite conveniently extracting all features jointly, the HMLSTM model processes linguistic input sentence-by-sentence, and therefore only allows to assess the corresponding EEG data at sentence offset. If I understood correctly, while the sentence information extracted with the HM-LSTM reflects the entire sentence - in terms of its acoustic, phonetic and more abstract linguistic features - it only gives a condensed final representation of the sentence. As such, feature extraction with the HM-LSTM is not compatible with a continuous temporal mapping on the EEG signal, and this is the main reason behind the authors' decision to fit a regression at nine separate time points surrounding sentence offsets.

Yes, you are correct. As explained in RE4, the model generates five hidden-layer activity vectors, each intended to represent all the phonemes, syllables, words, phrases within the entire sentence (“a condensed final representation”). This is the primary reason we extract EEG data surrounding the sentence offsets—this time point reflects when the full sentence has been processed by the human brain. We assume that even at this stage, residual neural responses corresponding to each linguistic level are still present and can be meaningfully analyzed.

While valid and previously used in the literature, this methodology, in the particular context of this experiment, might be obscuring important attentional effects impacted by hearing-loss. By fitting a regression only around sentence-final speech representations, the method might be overlooking the more "online" speech processing dynamics, and only assessing the permanence of information at different speech levels at sentence offset. In other words, the acoustic attentional bias between Attended and Unattended speech might exist even in hearing-impaired participants but, due to a lower encoding or permanence of acoustic information in this population, it might only emerge when using methodologies with a higher temporal resolution, such as Temporal Response Functions (TRFs). If a univariate TRF fit simply on the continuous speech envelope did not show any attentional bias (different trial lengths should not be a problem for fitting TRFs), I would be entirely convinced of the result. For now, I am unsure on how to interpret this finding.

We agree and we have added the mTRF results using the rate models for the 5 linguistic levels in the prior revision. The rate model aligns with the boundaries of each linguistic unit at each level. As explained in RE3, the rate regressors encode the timing of linguistic unit boundaries, while the model-derived features encode the representational content of the linguistic input. The mTRF results showed similar patterns to those observed using features from our HM-LSTM model with ridge regression (see Figure S2). These results complement each other and both provide informative results into the neural tracking of linguistic structures at different levels for the attended and unattended speech.

We have also added TRF results fitting the envelope of attended and unattended speech at every 10 ms to the whole 10-minute EEG data at every 10 ms. Our results showed that in hearing-impaired participants, attended speech elicited a significant cluster in the bilateral temporal regions from 270 to 300 ms post-onset (t = 2.40, p = 0.01, Cohen’s d = 0.63). Unattended speech elicited an early cluster in right temporal and occipital regions from –100 ms to –80 ms (t = 3.07, p = 0.001, d = 0.83). Normal-hearing participants showed significant envelope tracking in the left temporal region at 280–300 ms after envelope onset (t = 2.37, p = 0.037, d = 0.48), with no significant cluster for unattended speech. These results further suggest that hearing-impaired listeners may have difficulty suppressing unattended streams. We have added the new TRF results for envelope to Figure S3 and the “mTRF results for attended and unattended speech” on p.7 and the “mTRF analysis” in Material and Methods of the revised manuscript.

Despite my doubts on the appropriateness of condensed speech representations and singlepoint regression for acoustic features in particular, the current methodology allows the authors to explore their research questions, and the results support their conclusions. This work presents an interesting finding on the limits of attentional bias in a cocktail-party scenario, suggesting that fundamentally different neural attentional filters are employed by listeners with highfrequency hearing loss, even in terms of the tracking of speech acoustics. Moreover, the rich dataset collected by the authors is a great contribution to open science and will offer opportunities for re-analysis.

We sincerely thank you again for your encouraging comments regarding the impact of our study.

Reviewer #3 (Public review):

Summary:

The authors aimed to investigate how the brain processes different linguistic units (from phonemes to sentences) in challenging listening conditions, such as multi-talker environments, and how this processing differs between individuals with normal hearing and those with hearing impairments. Using a hierarchical language model and EEG data, they sought to understand the neural underpinnings of speech comprehension at various temporal scales and identify specific challenges that hearing-impaired listeners face in noisy settings.

Strengths:

Overall, the combination of computational modeling, detailed EEG analysis, and comprehensive experimental design thoroughly investigates the neural mechanisms underlying speech comprehension in complex auditory environments. The use of a hierarchical language model (HM-LSTM) offers a data-driven approach to dissect and analyze linguistic information at multiple temporal scales (phoneme, syllable, word, phrase, and sentence). This model allows for a comprehensive neural encoding examination of how different levels of linguistic processing are represented in the brain. The study includes both single-talker and multi-talker conditions, as well as participants with normal hearing and those with hearing impairments. This design provides a robust framework for comparing neural processing across different listening scenarios and groups.

Weaknesses:

The analyses heavily rely on one specific computational model, which limits the robustness of the findings. The use of a single DNN-based hierarchical model to represent linguistic information, while innovative, may not capture the full range of neural coding present in different populations. A low-accuracy regression model-fit does not necessarily indicate the absence of neural coding for a specific type of information. The DNN model represents information in a manner constrained by its architecture and training objectives, which might fit one population better than another without proving the non-existence of such information in the other group. It is also not entirely clear if the DNN model used in this study effectively serves the authors' goal of capturing different linguistic information at various layers. More quantitative metrics on acoustic/linguistic-related downstream tasks, such as speaker identification and phoneme/syllable/word recognition based on these intermediate layers, can better characterize the capacity of the DNN model.

We agree that, before aligning model representations with neural data, it is essential to confirm that the model encodes linguistic information at multiple hierarchical levels. This is the purpose of our validation analysis: We evaluated the model’s representations across five layers using a test set of 20 four-syllable sentences in which every syllable shares the same vowel—e.g., “mā ma mà mǎ” (mother scolds horse), “shū shu shǔ shù” (uncle counts numbers; see Table S1). We hypothesized that the activity in the phoneme and syllable layer would be more similar than other layers for same-vowel sentences. The results confirmed our hypothesis: Hidden-layer activity for same-vowel sentences exhibited much more similar distributions at the phoneme and syllable levels compared to those at the word, phrase and sentence levels Figure 3C displays the scatter plot of the model activity at the five linguistic levels for each of the 20 4-syllable sentences, post dimension reduction using multidimensional scaling (MDS). We used color-coding to represent the activity of five hidden layers after dimensionality reduction. Each dot on the plot corresponds to one test sentence. Only phonemes are labeled because each syllable in our test sentences contains the same vowels (see Table S1).The plot reveals that model representations at the phoneme and syllable levels are more dispersed for each sentence, while representations at the higher linguistic levels—word, phrase, and sentence—are more centralized. Additionally, similar phonemes tend to cluster together across the phoneme and syllable layers, indicating that the model captures a greater amount of information at these levels when the phonemes within the sentences are similar.

Apart from the DNN model, we also included the rate models which simply mark 1 at each unit boundaries across the 5 levels. We performed mTRF analyses with these rate models and found similar patterns to our ridge‐regression results with the DNN: (see Figure S2). This provides further evidence that the model reliably captures information across all five hierarchical levels.

Since EEG measures underlying neural activity in near real-time, it is expected that lower-level acoustic information, which is relatively transient, such as phonemes and syllables, would be distributed throughout the time course of the entire sentence. It is not evident if this limited time window effectively captures the neural responses to the entire sentence, especially for lower-level linguistic features. A more comprehensive analysis covering the entire time course of the sentence, or at least a longer temporal window, would provide a clearer understanding of how different linguistic units are processed over time.

We agree that lower-level linguistic features may be distributed throughout the whole sentence, however, using the entire sentence duration was not feasible, as the sentences in the stimuli vary in length, making statistical analysis challenging. Additionally, since the stimuli consist of continuous speech, extending the time window would risk including linguistic units from subsequent sentences. This would introduce ambiguity as to whether the EEG responses correspond to the current or the following sentence. Additionally, our model activity represents a “condensed final representation” at the five linguistic levels for the whole sentence, rather than incrementally during the sentence. We think the -100 to 300 ms time window relative to each sentence offset targets the exact moment when full-sentence representations are comprehended and a “condensed final representation” for the whole sentence across five linguistic level have been formed in the brain. We have added this clarification on p.13 of the revised manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Here are some specifics and clarifications of my public review:

Initially I was interpreting the R squared as a continuous measure of predicted EEG relative to actual EEG, based on an encoding model, but this does not appear to be correct. Thank you for pointing out that the y axis is z-scored R squared in your main ridge regression plots. However, I am not sure why/how you chose to represent this that way. It seems to me that a simple Pearson r would be most informative here (and in line with similar work, including Goldstein et al. 2022 that you mentioned). That way you preserve the sign of the relationships between the regressors and the EEG. With R squared, we have a different interpretation, which is maybe also ok, but I also don't see the point of z-scoring R squared. Another possibility is that when you say "z-transformed" you are referring to the Fisher transformation; is that the case? In the plots you say "normalized", so that sounds like a z-score, but this needs to be clarified; as I say, a simple Pearson r would probably be best.

We did not use Pearson’s r, as in Goldstein et al. (2022), because our analysis did not involve a train-test split, which was central to their approach. In their study, the data were divided into training and testing sets, and a ridge regression model was trained on the training set. They then used the trained model to predict neural responses on the held-out test set, and calculated Pearson’s r to assess the correlation between the predicted and observed neural responses. As a result, their final metric of model performance was the correlation coefficient (r). In contrast, our analysis is more aligned with standard temporal response function (TRF) approaches. We did not perform a train-test split; instead, we computed the model fitting performance (R²) of the ridge regression model at each sensor and time point for each subject. At the group level, we conducted one-sample t-tests with spatiotemporal cluster-based correction on the R² values to determine which sensors and time windows showed significantly greater R² values than baseline. To establish a baseline, we z-scored the R² values across sensors and time points, effectively centering the distribution around zero. This normalization allowed us to interpret deviations from the mean R² as meaningful increases in model performance and provided a suitable baseline for the statistical tests. We have added this clarification on p.13 of the revised manuscript.

Thank you for doing the TRF analysis, but where are the acoustic TRFs, analogous to the acoustic results for your HM-LSTM ridge analyses? And what tools did you use to do the TRF analysis? If it is something like the mTRF MATLAB toolbox, then it is also using ridge regression, as you have already done in your original analysis, correct? If so, then it is pretty much the same as your original analysis, just with more dense timepoints, correct? This is what I meant by referring to TRFs originally, because what you have basically done originally was to make a 9-point TRF (and then the plots and analyses are contrasts of pairs of those), with lags between -100 and 300 ms relative to the temporal alignment between the regressors and the EEG, I think (more on this below).

Also with the new TRF analysis, you say that the regressors/predictors had "a value of 1 at each unit boundary offset". So this means you re-made these predictors to be discrete as I and reviewer 3 were mentioning before (rather than using the HM-LSTM model layer(s)), and also, that you put each phoneme/word/etc. marker at its offset, rather than its onset? I'm also confused as to why you would do this rather than the onset, but I suppose it doesn't change the interpretation very much, just that the TRFs are slid over by a small amount.

We used the Python package Eelbrain (https://eelbrain.readthedocs.io/en/r0.39/auto_examples/temporal-response-functions/trf_intro.html) to conduct the multivariate temporal response function (mTRF) analyses. As we previously explained in our response to Reviewer 3, we did not apply mTRF to the acoustic features due to the high dimensionality of the input. Specifically, our acoustic representation consists of a 130-dimensional vector sampled every 10 ms throughout the speech stimuli (comprising a 129-dimensional spectrogram and a 1-dimensional amplitude envelope). This renders the 130 TRF weights to the acoustic features uninterpretable. However, we have now added TRF results from the 1- dimension envelope to the attended and unattended speech at every 10 ms.

A similar constraint applied to the hidden-layer activations from our HM-LSTM model for the five linguistic features. After dimensionality reduction via PCA, each still resulted in 150-dimensional vectors, further preventing their use in mTRF analyses. To address this, we instead used binary predictors marking the offset of each linguistic unit (phoneme, syllable, word, phrase, sentence). These rate models are represented as five distinct binary time series, each aligned with the timing of the corresponding linguistic unit, making them well-suited for mTRF analysis. It is important to note that these rate predictors differ from the HM-LSTMderived features: They encode only the timing of linguistic unit boundaries, not the content or representational structure of the linguistic input. Therefore, we do not consider the mTRF analyses to be equivalent to the ridge regression analyses based on HM-LSTM features

For onset vs. offset, as explained RE4, we labelled them “offsets” because our ridge‐regression with HM-LSTM features was aligned to sentence offsets rather than onsets (see RE4 and RE15 below for the rationale of using sentence offset). However, since each unit offset coincides with the next unit’s onset—and the rate model simply mark these transition points as 1—the “offset” and “onset” models yield identical mTRFs. To avoid confusion, we have relabeled “offset” as “boundary” in Figure S2.

I'm still confused about offsets generally. Does this maybe mean that the EEG, and each predictor, are all aligned by aligning their endpoints, which are usually/always the ends of sentences? So e.g. all the phoneme activity in the phoneme regressor actually corresponds to those phonemes of the stimuli in the EEG time, but those regressors and EEG do not have a common starting time (one trial to the next maybe?), so they have to be aligned with their ends instead?

We chose to use sentence offsets rather than onsets based on the structure of our input to the HM-LSTM model, where each input consists of a pair of sentences encoded in phonemes, such as “t a_1 n əŋ_2 f ei_1 <sep> zh ə_4 sh iii_4 f ei_1 j ii_1” (“It can fly <sep> This is an airplane”). The two sentences are separated by a special <sep> token, and the model’s objective is to determine whether the second sentence follows the first, similar to a next-sentence prediction task. Since the model processes both sentences in full before making a prediction, the neural activations of interest should correspond to the point at which the entire sentence has been processed. To enable a fair comparison between the model’s internal representations and brain responses, we aligned our neural analyses with the sentence offsets, capturing the time window after the sentence has been fully perceived by the participant. Thus, we extracted epochs from -100 to +300 ms relative to each sentence offset, consistent with our modelinformed design. If we align model activity with EEG data aligned to sentence onsets, we would be examining linguistic representations at all levels (from phoneme to sentence) of the whole sentence at the time when participants have not heard the sentence yet. By contrast, aligning to sentence offsets ensures that participants have constructed a full-sentence representation.

We understand that it is a bit confusing why the regressor of each level is not aligned to their own offsets in the data. The hidden-layer activations of the HM-LSTM model corresponding to the five linguistic levels (phoneme, syllable, word, phrase, sentence) are consistently 150-dimensional vectors after PCA reduction. As a result, for each input sentence pair, the model produces five distinct hidden-layer activations, each capturing the representational content associated with one linguistic level for the whole sentence. We believe our -100 to 300 ms time window relative to sentence offset reflects a meaningful period during which the brain integrates and comprehends information across multiple linguistic levels.

Being "time-locked to the offset of each sentence at nine latencies" is not something I can really find in any of the references that you mentioned, regarding the offset aspect of this method. Can you point me more specifically to what you are trying to reference with that, or further explain? You said that "predicting EEG signals around the offset of each sentence" is "a method commonly employed in the literature", but the example you gave of Goldstein 2022 is using onsets of words, which is indeed much more in line with what I would expect (not offsets of sentences).

You are correct that Goldstein (2022) aligned model predictions to onsets rather than offsets; however, many studies in the literature also align model predictions with unit offsets. typically because they mark the point at which participants has already processed the relevant information (Brennan, 2016; Brennan et al., 2016; Gwilliams et al., 2024, 2025). Similarly, in our study, we aim to identify neural correlates for each model-derived feature. If we correlate model activity with EEG data aligned to sentence onsets, we would be examining linguistic representations at all levels (from phoneme to sentence) of the whole sentence at the time when participants have not heard the sentence yet. By contrast, aligning to sentence offsets ensures that participants have constructed a full-sentence representation. Although this limits our analysis to a subset of the data (143 sentences × 400 ms windows × 4 conditions), it targets the exact moment when full-sentence representations emerge against background speech, allowing us to examine each model-derived feature onto its neural signature. We have added this clarification on p.12 of the revised manuscript.

This new sentence does not make sense to me: "The regressors are aligned to sentence offsets because all our regressors are taken from the hidden layer of our HM-LSTM model, which generates vector representations corresponding to the five linguistic levels of the entire sentence".

Thank you for the suggestion. We hope our responses in RE4, 15 and 16, along with our supplementary video have now clarified the issue. We have deleted the sentence and provided a more detailed explanation on p.12 of the revised manuscript: The regressors are aligned to sentence offsets because our goal is to identify neural correlates for each model-derived feature of a whole sentence. If we align model activity with EEG data time-locked to sentence onsets, we would be finding neural responses to linguistic levels (from phoneme to sentence) of the whole sentence at the time when participants have not processed the sentence yet. By contrast, aligning to sentence offsets ensures that participants have constructed a full-sentence representation. Although this limits our analysis to a subset of the data (143 sentences × 2 sections × 400 ms windows), it targets the exact moment when full-sentence representations emerge against background speech, allowing us to examine each model-derived feature onto its neural signature. We understand that phonemes, syllables, words, phrases, and sentences differ in their durations. However, the five hidden activity vectors extracted from the model are designed to capture the representations of these five linguistic levels across the entire sentence Specifically, for a sentence pair such as “It can fly <sep> This is an airplane,” the first 2048dimensional vector represents all the phonemes in the two sentences (“t a_1 n əŋ_2 f ei_1 <sep> zh ə_4 sh iii_4 f ei_1 j ii_1”), the second vector captures all the syllables (“ta_1 nəŋ_2 fei_1 <sep> zhə_4 shiii_4 fei_1jii_1”), the third vector represents all the words, the fourth vector captures the phrases, and the fifth vector represents the sentence-level meaning. In our dataset, input pairs consist of adjacent sentences from the stimuli (e.g., Sentence 1 and Sentence 2, Sentence 2 and Sentence 3, and so on), and for each pair, the model generates five 2048dimensional vectors, each corresponding to a specific linguistic level. To identify the neural correlates of these model-derived features—each intended to represent the full linguistic level across a complete sentence—we focused on the EEG signal surrounding the completion of the second sentence rather than on incremental processing. Accordingly, we extracted epochs from -100 ms to +300 ms relative to the offset of the second sentence and performed ridge regression analyses using the five model features (reduced to 150 dimensions via PCA) at every 50 ms across the epoch.

More on the issue of sentence offsets: In response to reviewer 3's question about -100 - 300 ms around sentence offset, you said "Using the entire sentence duration was not feasible, as the sentences in the stimuli vary in length, making statistical analysis challenging. Additionally, since the stimuli consist of continuous speech, extending the time window would risk including linguistic units from subsequent sentence." This does not make sense to me, so can you elaborate? It sounds like you are actually saying that you only analyzed 400 ms of each trial, but that cannot be what you mean.

Yes, we analyzed only the 400 ms window surrounding each sentence offset. Although this represents just a subset of our data (143 sentences × 400 ms × 4 conditions), it precisely captures when full-sentence representations emerge against background speech. Because our model produces a single, condensed representation for each linguistic level over the entire sentence—rather than incrementally—we think it is more appropriate to align to the period surrounding sentence offsets. Additionally, extending the window (e.g. to 2 seconds) would risk overlapping adjacent sentences, since sentence lengths vary. Our focus is on the exact period when integrated, level-specific information for each sentence has formed in the brain, and our results already demonstrate different response patterns to different linguistic levels for the two listener groups within this interval. We have added this clarification on p.13 of the revised manuscript.

In your mTRF analysis, you are now saying that the discrete predictors have "a value of 1" at each of the "boundary offsets", and those TRFs look very similar to your original plots. It sounds to me like you should not be referring to time zero in your original ridge analysis as "sentence offset". If what you mean is that sentence offset time is merely how you aligned the regressors and EEG in time, then your time zero still has a standard, typical TRF interpretation. It is just the point in time, or lag, at which the regressor(s) and EEG are aligned. So activity before zero is "predictive" and activity after zero is "reactive", to think of it crudely. So also in the text, when you say things like "50-150 ms after the sentence offsets", I think this is not really what you mean. I think you are referring to the lags of 50 - 150 ms, relative to the alignment of the regressor and the EEG.

Thank you very much for the explanation. We agree that, in our ridge‐regression time course, pre zero lags index “predictive” processing and post-zero lags index “reactive” processing. Unlike TRF analysis, we applied ridge regression to our high-dimensional model features at nine discrete lags around the sentence offset. At each lag, we tested whether the regression score exceeded a baseline defined as the mean regression score across all lags. For example, finding a significantly higher regression score between 50 and 150 ms suggests that our regressor reliably predicted EEG activity in that time window. So here time zero refers to the precise moment of the sentence offset—not the the alignment of the regressor and the EEG.

I look forward to discussing how much of my interpretation here makes sense or doesn't, both with the authors and reviewers.

Thank you very much for these very constructive feedback and we hope that we have addressed all your questions.

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It Refers to current OSs such as Windows, Linux, and macOS that provide advanced multitasking and concurrency features.

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Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In the manuscript submission by Zhao et al. entitled, "Cardiac neurons expressing a glucagon-like receptor mediate cardiac arrhythmia induced by high-fat diet in Drosophila" the authors assert that cardiac arrhythmias in Drosophila on a high fat diet is due in part to adipokinetic hormone (Akh) signaling activation. High fat diet induces Akh secretion from activated endocrine neurons, which activate AkhR in posterior cardiac neurons. Silencing or deletion of Akh or AkhR blocks arrhythmia in Drosophila on high fat diet. Elimination of one of two AkhR expressing cardiac neurons results in arrhythmia similar to high fat diet.

Strengths:

The authors propose a novel mechanism for high fat diet induced arrhythmia utilizing the Akh signaling pathway that signals to cardiac neurons.

Comments on revisions:

The authors have addressed my other concerns. The only outstanding issue is in regard to the following comment:

The authors state that "HFD led to increased heartbeat and an irregular rhythm." In representative examples shown, HFD resulted in pauses, slower heart rate, and increased irregularity in rhythm but not consistently increased heart rate (Figures 1B, 3A, and 4C). Based on the cited work by Ocorr et al (https://doi.org/10.1073/pnas.0609278104), Drosophila heart rate is highly variable with periods of fast and slow rates, which the authors attributed to neuronal and hormonal inputs. Ocorr et al then describe the use of "semi-intact" flies to remove autonomic input to normalize heart rate. Were semi-intact flies used? If not, how was heart rate variability controlled? And how was heart rate "increase" quantified in high fat diet compared to normal fat diet? Lastly, how does one measure "arrhythmia" when there is so much heart rate variability in normal intact flies?

The authors state that 8 sec time windows were selected at the discretion of the imager for analysis. I don't know how to avoid bias unless the person acquiring the imaging is blinded to the condition and the analysis is also done blind. Can you comment whether data acquisition and analysis was done in a blinded fashion? If not, this should be stated as a limitation of the study.

Drosophila heart rate is highly variable. During the recording, we were biased to choose a time window when heartbeat was fairly stable. This is a limitation of the study, which we mentioned in the revised version. We chose to use intact over “semi-intact” flies with an intention to avoid damaging the cardiac neurons. 

Reviewer #3 (Public review):

Zhao et al. provide new insights into the mechanism by which a high-fat diet (HFD) induces cardiac arrhythmia employing Drosophila as a model. HFD induces cardiac arrhythmia in both mammals and Drosophila. Both glucagon and its functional equivalent in Drosophila Akh are known to induce arrhythmia. The study demonstrates that Akh mRNA levels are increased by HFD and both Akh and its receptor are necessary for high-fat diet-induced cardiac arrhythmia, elucidating a novel link. Notably, Zhao et al. identify a pair of AKH receptor-expressing neurons located at the posterior of the heart tube. Interestingly, these neurons innervate the heart muscle and form synaptic connections, implying their roles in controlling the heart muscle. The study presented by Zhao et al. is intriguing, and the rigorous characterization of the AKH receptor-expressing neurons would significantly enhance our understanding of the molecular mechanism underlying HFD-induced cardiac arrhythmia.

Many experiments presented in the manuscript are appropriate for supporting the conclusions while additional controls and precise quantifications should help strengthen the authors' arguments. The key results obtained by loss of Akh (or AkhR) and genetic elimination of the identified AkhR-expressing cardiac neurons do not reconcile, complicating the overall interpretation.

We thank the reviewer for the positive comments. We believe that more signaling pathways are active in the AkhR neurons and regulate rhythmic heartbeat. We are current searching for the molecules and pathways that act on the AkhR cardiac neurons to regulate the heartbeat. Thus, AkhR neuron x shall have a more profound effect. Loss of AkhR is not equivalent to AkhR neuron ablation. 

The most exciting result is the identification of AkhR-expressing neurons located at the posterior part of the heart tube (ACNs). The authors attempted to determine the function of ACNs by expressing rpr with AkhR-GAL4, which would induce cell death in all AkhRexpressing cells, including ACNs. The experiments presented in Figure 6 are not straightforward to interpret. Moreover, the conclusion contradicts the main hypothesis that elevated Akh is the basis of HFD-induced arrhythmia. The results suggest the importance of AkhR-expressing cells for normal heartbeat. However, elimination of Akh or AkhR restores normal rhythm in HFD-fed animals, suggesting that Akh and AkhR are not important for maintaining normal rhythms. If Akh signaling in ACNs is key for HFD-induced arrhythmia, genetic elimination of ACNs should unalter rhythm and rescue the HFD-induced arrhythmia. An important caveat is that the experiments do not test the specific role of ACNs. ACNs should be just a small part of the cells expressing AkhR. Specific manipulation of ACNs will significantly improve the study. Moreover, the main hypothesis suggests that HFD may alter the activity of ACNs in a manner dependent on Akh and AkhR. Testing how HFD changes calcium, possibly by CaLexA (Figure 2) and/or GCaMP, in wild-type and AkhR mutant could be a way to connect ACNs to HFD-induced arrhythmia. Moreover, optogenetic manipulation of ACNs may allow for specific manipulation of ACNs.

We thank the reviewer for suggesting the detailed experiments and we believe that address these points shall consolidate the results. As AkhR-Gal4 also expresses in the fat body, we set out to build a more specific driver. We planned to use split-Gal4 system (Luan et al. 2006. PMID: 17088209). The combination of pan neuronal Elav-Gal4.DBD and AkhRp65.AD shall yield AkhR neuron specific driver. We selected 2580 bp AkhR upstream DNA and cloned into pBPp65ADZpUw plasmid (Addgene plasmid: #26234). After two rounds of injection, however, we were not able to recover a transgenic line.

We used GCaMP to record the calcium signal in the AkhR neurons. AkhR-Gal4>GCaMP has extremely high levels of fluorescence in the cardiac neurons under normal condition.

We are screening Gal4 drivers, trying to find one line that is specific to the cardiac neurons and has a lower level of driver activity.   

Interestingly, expressing rpr with AkhR-GAL4 was insufficient to eliminate both ACNs. It is not clear why it didn't eliminate both ACNs. Given the incomplete penetrance, appropriate quantifications should be helpful. Additionally, the impact on other AhkR-expressing cells should be assessed. Adding more copies of UAS-rpr, AkhR-GAL4, or both may eliminate all ACNs and other AkhR-expressing cells. The authors could also try UAS-hid instead of UASrpr.

We quantified the AkhR neuron ablation and found that about 69% (n=28) showed a single ACN in AkhR-Gal4>rpr flies. It is more challenging to quantify other AkhR-expressing cells, as they are wide-spread distributed. We tried to add more copies of UAS-rpr or AkhR-Gal4, which caused developmental defects (pupa lethality). Thus, as mentioned above, we are trying to find a more specific driver for targeting the cardiac neurons.

Recommendations for the authors:

Reviewer #3 (Recommendations for the authors):

The authors refer 'crop' as the functional equivalent of the human stomach. Considering the difference in their primary functions, this cannot be justified.

In Drosophila, the crop functions analogously to the stomach in vertebrates. It is a foregut storage and preliminary processing organ that regulates food passage into the midgut. It’s more than a simple reservoir. Crop engages in enzymatic mixing, neural control, and active motility.

Line 163 and 166, APCs are not neurons.

Akh-producing cells (APCs) in Drosophila are neuroendocrine cells, residing in the corpora cardiaca (CC). While they produce and secrete the hormone AKH (akin to glucagon), they are not brain interneurons per se. APCs share many neuronal features (vesicular release, axon-like projections) and receive neural inputs, effectively functioning as a peripheral endocrine center.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

One possible remaining conceptual concern that might require future work is determining whether STN primarily mediates higher-level cognitive avoidance or if its activation primarily modulates motor tone.

Our results using viral and electrolytic lesions (Fig. 11) and optogenetic inhibition of STN neurons (Fig. 10) show that signaled active avoidance is virtually abolished, and this effect is reproduced when we selectively inhibit STN fibers in the midbrain (Fig. 12). Inhibition of STN projections in either the substantia nigra pars reticulata (SNr) or the midbrain reticular tegmentum (mRt) eliminates cued avoidance responses while leaving escape responses intact. Importantly, mice continue to escape during US presentation after lesions or during photoinhibition, demonstrating that basic motor capabilities and the ability to generate rapid defensive actions are preserved.

These findings argue against the idea that STN’s role in avoidance reflects a nonspecific suppression or facilitation of motor tone, even if the STN also contributes to general movement control. Instead, they show that STN output is required for generating “cognitively” guided cued actions that depend on interpreting sensory information and applying learned contingencies to decide when to act. Thus, while STN activity can modulate movement parameters, the loss-of-function results point to a more selective role in supporting cued, goal-directed avoidance behavior rather than a general adjustment of motor tone.

Reviewer #2 (Public review):

All previous weaknesses have been addressed. The authors should explain how inhibition of the STN impairing active avoidance is consistent with the STN encoding cautious action. If 'caution' is related to avoid latency, why does STN lesion or inhibition increase avoid latency, and therefore increase caution? Wouldn't the opposite be more consistent with the statement that the STN 'encodes cautious action'?

The reviewer’s interpretation treats any increase in avoidance latency as evidence of “more caution,” but this holds only when animals are performing the avoidance behavior normally. In our intact animals, avoidance rates remain high across AA1 → AA2 → AA3, and the active avoidance trials (CS1) used to measure latency are identical across tasks (e.g., in AA2 the only change is that intertrial crossings are punished). Under these conditions, changes in latency genuinely reflect adjustments in caution, because the behavior itself is intact, actions remain tightly coupled to the cue, and the trials are identical.

This logic does not apply when STN function is disrupted. STN inhibition or lesions reduce avoidance to near chance levels; the few crossings that do occur are poorly aligned to the CS and many likely reflect random movement rather than a cued avoidance response. Once performance collapses, latency can no longer be assumed to reflect the same cognitive process. Thus, interpreting longer latencies during STN inactivation as “more caution” would be erroneous, and we never make that claim.

A simple analogy may help clarify this distinction. Consider a pedestrian deciding when to cross the street after a green light. If the road is deserted (like AA1), the person may step off the curb quickly. If the road is busy with many cars that could cause harm (like AA2), they may wait longer to ensure that all cars have stopped. This extra hesitation reflects caution, not an inability to cross. However, if the pedestrian is impaired (e.g., cannot clearly see the light, struggles to coordinate movements, or cannot reliably make decisions), a delayed crossing would not indicate greater caution—it would reflect a breakdown in the ability to perform the behavior itself. The same principle applies to our data: we interpret latency as “caution” only when animals are performing the active avoidance behavior normally, success rates remain high, and the trial rules are identical. Under STN inhibition or lesion, when active avoidance collapses, the latency of the few crossings that still occur can no longer be interpreted as reflecting caution. We have added these points to the Discussion.

Reviewer #3 (Public review):

Original Weaknesses:

I found the experimental design and presentation convoluted and some of the results over-interpreted.

We appreciate the reviewer’s comment, but the concern as stated is too general for us to address in a concrete way. The revised manuscript has been substantially reorganized, with simplified terminology, streamlined figures, and removal of an entire set of experiments to avoid over-interpretation. We are confident that the experimental design and results are now presented clearly and without extrapolation beyond the data. If there are specific points the reviewer finds convoluted or over-interpreted, we would be happy to address them directly.

As presented, I don't understand this idea that delayed movement is necessarily indicative of cautious movements. Is the distribution of responses multi-modal in a way that might support this idea; or do the authors simply take a normal distribution and assert that the slower responses represent 'caution'? Even if responses are multi-modal and clearly distinguished by 'type', why should readers think this that delayed responses imply cautious responding instead of say: habituation or sensitization to cue/shock, variability in attention, motivation, or stress; or merely uncertainty which seems plausible given what I understand of the task design where the same mice are repeatedly tested in changing conditions. This relates to a major claim (i.e., in the title).

We appreciate the reviewer’s question and address each component directly.

(1) What we mean by “caution” and how it is operationalized

In our study, caution is defined operationally as a systematic increase in avoidance latency when the behavioral demand becomes higher, while the trial structure and required response remain unchanged. Specifically, CS1 trials are identical in AA1, AA2, and AA3. Thus, when mice take longer to initiate the same action under more demanding contexts, the added time reflects additional evaluation before acting—consistent with longestablished interpretations of latency shifts in cognitive psychology (see papers by Donders, Sternberg, Posner) and interpretations of deliberation time in speed-accuracy tradeoff literature.

(2) Why this interpretation does not rely on multi-modal response distributions We do not claim that “cautious” responses form a separate mode in the latency distribution. The distributions are unimodal, and caution is inferred from conditiondependent shifts in these distributions across identical trials, not from the existence of multiple peaks (see Zhou et al, 2022). Latency shifts across conditions with identical trial structure are widely used as behavioral indices of deliberation or caution.

(3) Why alternative explanations (habituation/sensitization, motivation, attention, stress, uncertainty) do not account for these latency changes

Importantly, nothing changes in CS1 trials between AA1 and AA2 with respect to the cue, shock, or required response. Therefore:

- Habituation/sensitization to the cue or shock cannot explain the latency shift (the stimuli and trial type are unchanged). We have previously examined cue-evoked orienting responses and their habituation in detail (Zhou et al., 2023), and those measurements are dissociable from the latency effects described here.

- Motivation or attention are unlikely to change selectively for identical CS1 trials when the task manipulation only adds a contingency to intertrial crossings.

- Uncertainty also does not increase for CS1 trials, they remain fully predictable and unchanged between conditions.

- Stress is too broad a construct to be meaningful unless clearly operationalized; moreover, any stress differences that arise from task structure would covary with caution rather than replace the interpretation.

(4) Clarifying “types” of responses

The reviewer’s question about “response types” appears to conflate behavioral latencies with the neuronal response “types” defined in the manuscript. The term “type” in this paper refers to neuronal activation derived from movement-based clustering, not to distinct behavioral categories of avoidance, which we term modes.

In sum, we interpret increased CS1 latency as “caution” only when performance remains intact and trial structure is identical between conditions; under those criteria, latency reliably reflects additional cognitive evaluation before acting, rather than nonspecific changes in sensory processing, motivation, etc.

Related to the last, I'm struggling to understand the rationale for dividing cells into 'types' based their physiological responses in some experiments.

There is longstanding precedent in systems neuroscience for classifying neurons by their physiological response patterns, because neurons that respond similarly often play similar functional roles. For example, place cells, grid cells, direction cells, in vivo, and regular spiking, burst firing, and tonic firing in vitro are all defined by characteristic activity patterns in response to stimuli rather than anatomy or genetics alone. In the same spirit, our classifications simply reflect clusters of neurons that exhibit similar ΔF/F dynamics around behaviorally relevant events, such as movement sensitivity or avoidance modes. This is a standard analytic approach used in many studies. Thus, our rationale is not arbitrary: the “classes” and “types” arise from data-driven clustering of physiological responses, consistent with widespread practice, and they help reveal functional distinctions within the STN that would otherwise remain obscured.

In several figures the number of subjects used was not described. This is necessary. Also necessary is some assessment of the variability across subjects.

All the results described include the number of animals. To eliminate uncertainty, we now also include this information in figure legends.

The only measure of error shown in many figures relates trial-to-trial or event variability, which is minimal because in many cases it appears that hundreds of trials may have been averaged per animal, but this doesn't provide a strong view of biological variability (i.e., are results consistent across animals?).

The concern appears to stem from a misunderstanding of what the mixed-effects models quantify. The figure panels often show session-averaged traces for clarity, all statistical inferences in the paper are made at the level of animals, not trials. Mixed-effects modeling is explicitly designed for hierarchical datasets such as ours, where many trials are nested within sessions, which are themselves nested within animals.

In our models, animal is the clustering (random) factor, and sessions are nested within animals, so variability across animals is directly estimated and used to compute the population-level effects. This approach is not only appropriate but is the most stringent and widely recommended method for analyzing behavioral and neural data with repeated measures. In other words, the significance tests and confidence intervals already fully incorporate biological variability across animals.

Thus, although hundreds of trials per animal may be illustrated for visualization, the inferences reflect between-animal consistency, not within-animal trial repetition. The fact that the mixed-effects results are robust across animals supports the biological reliability of the findings.

It is not clear if or how spread of expression outside of target STN was evaluated, and if or how or how many mice were excluded due to spread or fiber placements. Inadequate histological validation is presented and neighboring regions that would be difficult to completely avoid, such as paraSTN may be contributing to some of the effects.

The STN is a compact structure with clear anatomical boundaries, and our injections were rigorously validated to ensure targeting specificity. As detailed in the Methods, every mouse underwent histological verification, and injections were quantified using the Brain Atlas Analyzer app (available on OriginLab), which we developed to align serial sections to the Allen Brain Atlas. This approach provides precise, slice-by-slice confirmation of viral spread. We have performed thousands of AAV injections and probe implants in our lab, incorporating over the years highly reliable stereotaxic procedures with multiple depth and angle checks and tools. For this study specifically, fewer than 10% of mice were excluded due to off-target expression or fiber/lesion placement. None of the included cases showed spread into adjacent structures.

Regarding paraSTN: anatomically, paraSTN is a very small extension contiguous with STN. Our study did not attempt to dissociate subregions within STN, and the viral expression patterns we report fall within the accepted boundaries of STN. Importantly, none of our photometry probes or miniscope lenses sampled paraSTN, so contributions from that region are extremely unlikely to account for any of our neural activity results.

Finally, our paper employs five independent loss-of-function approaches—optogenetic inhibition of STN neurons, selective inhibition of STN projections to the midbrain (in two sites: SNr and mRt), and STN lesions (electrolytic and viral). All methods converge on the same conclusion, providing strong evidence that the effects we report arise from manipulation of STN itself rather than from neighboring regions.

Raw example traces are not provided.

We do not think raw traces are useful here. All figures contain average traces to reflect the average activity of the estimated populations, which are already clustered per classes and types.

The timeline of the spontaneous movement and avoidance sessions were not clear, nor the number of events or sessions per animal and how this was set. It is not clear if there was pre-training or habituation, if many or variable sessions were combined per animal, or what the time gaps between sessions was, or if or how any of these parameters might influence interpretation of the results.

As noted, we have enhanced the description of the sessions, including the number of animals and sessions, which are daily and always equal per animals in each group of experiments. The sessions are part of the random effects in the model. In addition, we now include schematics to facilitate understanding of the procedures.  

Comments on revised version:

The authors removed the optogenetic stimulation experiments, but then also added a lot of new analyses. Overall the scope of their conclusions are essentially unchanged. Part of the eLife model is to leave it to the authors discretion how they choose to present their work. But my overall view of it is unchanged. There are elements that I found clear, well executed, and compelling. But other elements that I found difficult to understand and where I could not follow or concur with their conclusions.

We respectfully disagree with the assertion that the scope of our conclusions remains unchanged. The revised manuscript differs in several fundamental ways:

(1) Removal of all optogenetic excitation experiments

These experiments were a substantial portion of the original manuscript, and their removal eliminated an entire set of claims regarding the causal control of cautious responding by STN excitation. The revised manuscript no longer makes these claims.

(2) Addition of analyses that directly address the reviewers’ central concerns The new analyses using mixed-effects modeling, window-specific covariates, and movement/baseline controls were added precisely because reviewers requested clearer dissociation of sensory, motor, and task-related contributions. These additions changed not only the presentation but the interpretation of the neural signals. We now conclude that STN encodes movement, caution, and aversive signals in separable ways—not that it exclusively or causally regulates caution.

(3) Clear narrowing of conclusions

Our current conclusions are more circumscribed and data-driven than in the original submission. For example, we removed all claims that STN activation “controls caution,” relying instead on loss-of-function data showing that STN is necessary for performing cued avoidance—not for generating cautious latency shifts. This is a substantial conceptual refinement resulting directly from the review process.

(4) Reorganization to improve clarity

Nearly every section has been restructured, including terminology (mode/type/class), figure organization, and explanations of behavioral windows. These revisions were implemented to ensure that readers can follow the logic of the analyses.

We appreciate the reviewer’s recognition that several elements were clear and compelling. For the remaining points they found difficult to understand, we have addressed each one in detail in the response and revised the manuscript accordingly. If there are still aspects that remain unclear, we would welcome explicit identification of those points so that we can clarify them further.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Show individual data points on bar plots

- partially addressed. Individual data points are still not shown.

Wherever feasible, we display individual data points (e.g., Figures 1 and 2) to convey variability directly. However, in cases where figures depict hundreds of paired (repeatedmeasures) data points, showing all points without connecting them would not be appropriate, while linking them would make the figures visually cluttered and uninterpretable. All plots and traces include measures of variability (SEM), and the raw data will be shared on Dryad. When error bars are not visible, they are smaller than the trace thickness or bar line—for example, in Figure 5B, the black circles and orange triangles include error bars, but they are smaller than the symbol size.

Also, to minimize visual clutter, only a subset of relevant comparisons is highlighted with asterisks, whereas all relevant statistical results, comparisons, and mouse/session numbers are fully reported in the Results section, with statistical analyses accounting for the clustering of data within subjects and sessions.

(2) The active avoidance experiments are confusing when they are introduced in the results section. More explanation of what paradigms were used and what each CS means at the time these are introduced would add clarity. For example AA1, AA2 etc are explained only with references to other papers, but a brief description of each protocol and a schematic figure would really help.

- partially addressed. A schematic figure showing the timeline would still be helpful.

As suggested, we have added an additional panel to Fig. 5A with a schematic describing

AA1-3 tasks. In addition, the avoidance protocols are described briefly but clearly in the Results section (second paragraph of “STN neurons activate during goal-directed avoidance contingencies”) and in greater detail in the Methods section. As stated, these tasks were conducted sequentially, and mice underwent the same number of sessions per procedure, which are indicated. All relevant procedural information has been included in these sections. Mice underwent daily sessions and learnt these tasks within 1-2 sessions, progressing sequentially across tasks with an equal number of sessions per task (7 per task), and the resulting data were combined and clustered by mouse/session in the statistical models.

(3) How do the Class 1, 2, 3 avoids relate to Class 1 , 2, 3 neural types established in Figure 3? It seems like they are not related, and if that is the case they should be named something different from each other to avoid confusion.

-not sufficiently addressed. The new naming system of neural 'classes' and 'types' helps with understanding that these are completely different ways of separating subpopulations within the STN. However, it is still unclear why the authors re-type the neurons based on their relation to avoids, when they classify the neurons based on their relationship to speed earlier. And it is unclear whether these neural classes and neural types have anything to do with each other. Are the neural Types related to the neural classes in any way? and what is the overlap between neural types vs classes? Which separation method is more useful for functionally defining STN populations?

The remaining confusion stems from treating several independent analyses as if they were different versions of the same classification. In reality, each analysis asks a distinct question, and the resulting groupings are not expected to overlap or correspond. We clarify this explicitly below.

- Movement onset neuron classes (Class A, B, C; Fig. 3):

These classes categorize neurons based on how their ΔF/F changes around spontaneous movement onset. This analysis identifies which neurons encode the initiation and direction of movement. For instance, Class B neurons (15.9%) were inhibited as movement slowed before onset but did not show sharp activation at onset, whereas Class C neurons (27.6%) displayed a pronounced activation time-locked to movement initiation. Directional analyses revealed that Class C neurons discharged strongly during contraversive turns, while Class B neurons showed a weaker ipsiversive bias. Because neurons were defined per session and many of these recordings did not include avoidance-task sessions, these movement-onset classes were not used in the avoidance analyses.

- Movement-sensitivity neuron classes (Class 1, 2, 3, 4; Fig. 7):

These classes categorize neurons based on the cross-correlation between ΔF/F and head speed, capturing how each neuron’s activity scales with movement features across the entire recording session. This analysis identifies neurons that are strongly speed-modulated, weakly speed-modulated, or largely insensitive to movement. These movement-sensitivity classes were then carried forward into the avoidance analyses to ask how neurons with different kinematic relationships participate during task performance; for example, whether neurons that are insensitive to movement nonetheless show strong activation during avoidance actions.

- Avoidance modes (Mode 1, 2, 3; Fig. 8)

Here we classify actions, not neurons. K-means clustering is applied to the movementspeed time series during CS1 active avoidance trials only, which allows us to identify distinct action modes or variants—fast-onset versus delayed avoidance responses. This action-based classification ensures that we compare neural activity across identical movements, eliminating a major confound in studies that do not explicitly separate action variants. First, we examine how population activity differs across these avoidance modes, reflecting neural encoding of the distinct actions themselves. Second, within each mode, we then classify neurons into “types,” which simply describes how different neurons activate during that specific avoidance action (as noted next).

- Neuron activation types within each mode (Type a, b, c; Fig.9)

This analysis extends the mode-based approach by classifying neuronal activation patterns only within each specific avoidance mode. For each mode, we apply k-means clustering to the ΔF/F time series to identify three activation types—e.g., neurons showing little or no response, neurons showing moderate activation, and neurons showing strong or sharply timed activation. Because all trials within a mode have identical movement profiles, these activation types capture the variability of neural responses to the same avoidance behavior. Importantly, these activation “types” (a, b,

c) are not global neuron categories. They do not correspond to, nor are they intended to map onto, the movement-based neuron classes defined earlier. Instead, they describe how neurons differ in their activation during a particular behavioral mode—that is, within a specific set of behaviorally matched trials. Because modes are defined at the trial level, the neurons contributing to each mode can differ: some neurons have trials belonging to one mode, others to two or all three. Thus, Type a/b/c groupings are not fixed properties of neurons. To prevent confusion, we refer to them explicitly as neuronal activation types, emphasizing that they characterize mode-specific response patterns rather than global cell identities.

In conclusion, the categorizations serve entirely different analytical purposes and should not be interpreted as competing classifications. The mode-specific “types” do not reclassify or replace the movement-sensitivity classes; they capture how neurons differ within a single, well-defined avoidance action, while the movement classes reflect how neurons relate to movements in general. Each classification relates to different set of questions and overlap between them is not expected.

To make this as clear as possible we added the following paragraph to the Results:  

“To avoid confusion between analyses, it is important to note that the movement-sensitivity classes defined here (Class 1–4; Fig. 7) are conceptually distinct from both the movementonset classes (Class A–C; Fig. 3) and the neuronal activation “types” introduced later in the avoidance-mode analysis. The Class 1–4 grouping reflects how neurons relate to movement across the entire session, based on their cross-correlation with speed. The onset classes A–C capture neural activity specifically around spontaneous movement initiation during general exploration. In contrast, the later activation “types” are derived within each avoidance mode and describe how neurons differ in their activation patterns during identical CS1 avoidance responses. These classifications answer different questions about STN function and are not intended to correspond to one another.”

(4) Similarly having 3 different cell types (a,b,c) in the active avoidance seems unrelated to the original classification of cell types (1,2,3), and these are different for each class of avoid. This is very confusing and it is unclear how any of these types relate to each other. Presumable the same mouse has all three classes of avoids, so there are recording from each cell during each type of avoid. So the authors could compare one cell during each avoid and determine whether it relates to movement or sound or something else. It is interesting that types a,b,c have the exact same proportions in each class of avoid, and really makes it important to investigate if these are the exact same cells or not. Also, these mice could be recorded during open field so the original neural classification (class 1, 2,3) could be applied to these same cells and then the authors can see whether each cell type defined in the open field has different response to the different avoid types. As it stands, the paper simply finds that during movement and during avoidance behaviors different cells in the STN do different things. - Similarly, the authors somewhat addressed the neural types issue, but figure 9 still has 9 different neural types and it is unclear whether the same cells that are type 'a' in mode 1 avoids are also type 'a' in mode 2 avoids, or do some switch to type b? Is there consistency between cell types across avoid modes? The authors show that type 'c' neurons are differentially elevated in mode 3 vs 2, but also describes neurons as type '2c' and statistically compare them to type '1c' neurons. Are these the same neurons? or are type 2c neurons different cells vs type 1c neurons? This is still unclear and requires clarification to be interpretable.

We believe the remaining confusion arises from treating the different classification schemes as if they were alternative labels applied to the same neurons, when in fact they serve entirely separate analytical purposes and may not include the same neurons (see previous point). Because these classifications answer different questions, they are not expected to overlap, nor is overlap required for the interpretations we draw. It is therefore not appropriate to compare a neuron’s “type” in one avoidance mode to its movement class, or to ask whether types a/b/c across different modes are “the same cells,” since modes are defined by trial-level movement clustering rather than by neuron identity. Importantly, Types a/b/c are not intended as a new global classification of neurons; they simply summarize the variability of neuronal responses within each behaviorally matched mode. We agree that future studies could expand our findings, but that is beyond the already wide scope of the present paper. Our current analyses demonstrate a key conceptual point: when movement is held constant (via modes), STN neurons still show heterogeneous, outcome- and caution-related patterns, indicating encoding that cannot be reduced to movement alone.

Relatedly, was the association with speed used to define each neural "class" done in the active avoidance context or in a separate (e.g. open field) experiment? This is not clear in the text.

The cross-correlation classes were derived from the entire recording session, which included open-field and avoidance tasks recordings. The tasks include long intertrial periods with spontaneous movements. We found no difference in classes when we include only a portion of the session, such as the open field or if we exclude the avoidance interval where actions occur.

Finally, in figure 7, why is there a separate avoid trace for each neural class? With the GRIN lens, the authors are presumably getting a sample of all cell types during each avoid, so why do the avoids differ depending on the cell type recorded?

The entire STN population is not recorded within a single session; each session contributes only a subset of neurons to the dataset. Consequently, each neural class is composed of neurons drawn from partially non-overlapping sets of sessions, each with its own movement traces. For this reason, we plot avoidance traces separately for each neural class to maintain strict within-session correspondence between neural activity and the behavior collected in the same sessions. This prevents mixing behavioral data across sessions that did not contribute neurons to that class and ensures that all neural– behavioral comparisons remain appropriately matched. We have clarified this rationale in the revised manuscript. We note that averaging movement across classes—as is often done—would obscure these distinctions and would not preserve the necessary correspondence between neural activity and behavior. This is also clarified in Results.

(5) The use of the same colors to mean two different things in figure 9 is confusing. AA1 vs AA2 shouldn't be the same colors as light-naïve vs light signaling CS.

-addressed, but the authors still sometimes use the same colors to mean different things in adjacent figures (e.g. the red, blue, black colors in figure 1 and figure 2 mean totally different things) and use different colors within the same figure to represent the same thing (Figure 9AB vs Figure 9CD). This is suboptimal.

Following the reviewer’s suggestion, in Figure 2, we changed the colors, so readers do not assume they are related to Fig. 1.

In Figure 9, we changed the colors in C,D to match the colors in A,B.

(6) The exact timeline of the optogenetics experiments should be presented as a schematic for understandability. It is not clear which conditions each mouse experienced in which order. This is critical to the interpretation of figure 9 and the reduction of passive avoids during STN stimulation. Did these mice have the CS1+STN stimulation pairing or the STN+US pairing prior to this experiment? If they did, the stimulation of the STN could be strongly associated with either punishment or with the CS1 that predicts punishment. If that is the case, stimulating the STN during CS2 could be like presenting CS1+CS2 at the same time and could be confusing. The authors should make it clear whether the mice were naïve during this passive avoid experiment or whether they had experienced STN stimulation paired with anything prior to this experiment.

-addressed

(7) Similarly, the duration of the STN stimulation should be made clear on the plots that show behavior over time (e.g. Figure 9E).

-addressed

(8) There is just so much data and so many conditions for each experiment here. The paper is dense and difficult to read. It would really benefit readability if the authors put only the key experiments and key figure panels in the main text and moved much of the repetative figure panels to supplemental figures. The addition of schematic drawings for behavioral experiment timing and for the different AA1, AA2, AA3 conditions would also really improve clarity.

-partially addressed. The paper is still dense and difficult to read. No experimental schematics were added.

As suggested, we now added the schematic to Fig. 5A.  

New Comments:

(9) Description of the animals used and institutional approval are missing from the methods.

The information on animal strains and institutional approval is already included in the manuscript. The first paragraph of the Methods section states:

“… All procedures were reviewed and approved by the institutional animal care and use committee and conducted in adult (>8 weeks) male and female mice. …”

Additionally, the next subsection, “Strains and Adeno-Associated Viruses (AAVs),” fully specifies all mouse lines used. We therefore believe that the required descriptions of animals and institutional approval are already present and meet standard reporting.

We are already used to this from way before in the late 1990s, w corporate thin clients. afaict that has peaked some time ago already, and offices now tend to have hardware again (laptops usually)?

Author response:

Point-by-point description of the revisions:

Reviewer #1 (Evidence, reproducibility and clarity):

Summary

In this article, the authors used the synthetic TALE DNA binding proteins, tagged with YFP, which were designed to target five specific repeat elements in Trypanosoma brucei genome, including centromere and telomeres-associated repeats and those of a transposon element. This is in order to detect and identified, using YFP-pulldown, specific proteins that bind to these repetitive sequences in T. brucei chromatin. Validation of the approach was done using a TALE protein designed to target the telomere repeat (TelR-TALE) that detected many of the proteins that were previously implicated with telomeric functions. A TALE protein designed to target the 70 bp repeats that reside adjacent to the VSG genes (70R-TALE) detected proteins that function in DNA repair and the protein designed to target the 177 bp repeat arrays (177R-TALE) identified kinetochore proteins associated T. brucei mega base chromosomes, as well as in intermediate and mini-chromosomes, which imply that kinetochore assembly and segregation mechanisms are similar in all T. brucei chromosome.

Major comments:

Are the key conclusions convincing?

The authors reported that they have successfully used TALE-based affinity selection of proteinassociated with repetitive sequences in the T. brucei genome. They claimed that this study has provided new information regarding the relevance of the repetitive region in the genome to chromosome integrity, telomere biology, chromosomal segregation and immune evasion strategies. These conclusions are based on high-quality research, and it is, basically, merits publication, provided that some major concerns, raised below, will be addressed before acceptance for publication.

(1) The authors used TALE-YFP approach to examine the proteome associated with five different repetitive regions of the T. brucei genome and confirmed the binding of TALE-YFP with Chip-seq analyses. Ultimately, they got the list of proteins that bound to synthetic proteins, by affinity purification and LS-MS analysis and concluded that these proteins bind to different repetitive regions of the genome. There are two control proteins, one is TRF-YFP and the other KKT2-YFP, used to confirm the interactions. However, there are no experiment that confirms that the analysis gives some insight into the role of any putative or new protein in telomere biology, VSG gene regulation or chromosomal segregation. The proteins, which have already been reported by other studies, are mentioned. Although the author discovered many proteins in these repetitive regions, their role is yet unknown. It is recommended to take one or more of the new putative proteins from the repetitive elements and show whether or not they (1) bind directly to the specific repetitive sequence (e.g., by EMSA); (2) it is recommended that the authors will knockdown of one or a small sample of the new discovered proteins, which may shed light on their function at the repetitive region, as a proof of concept.

The main request from Referee 1 is for individual evaluation of protein-DNA interaction for a few candidates identified in our TALE-YFP affinity purifications, particularly using EMSA to identify binding to the DNA repeats used for the TALE selection. In our opinion, such an approach would not actually provide the validation anticipated by the reviewer. The power of TALE-YFP affinity selection is that it enriches for protein complexes that associate with the chromatin that coats the target DNA repetitive elements rather than only identifying individual proteins or components of a complex that directly bind to DNA assembled in chromatin.

The referee suggests we express recombinant proteins and perform EMSA for selected candidates, but many of the identified proteins are unlikely to directly bind to DNA – they are more likely to associate with a combination of features present in DNA and/or chromatin (e.g. specific histone variants or histone post-translational modifications). Of course, a positive result would provide some validation but only IF the tested protein can bind DNA in isolation – thus, a negative result would be uninformative.

In fact, our finding that KKT proteins are enriched using the 177R-TALE (minichromosome repeat sequence) identifies components of the trypanosome kinetochore known (KKT2) or predicted (KKT3) to directly bind DNA (Marciano et al., 2021; PMID: 34081090), and likewise the TelR-TALE identifies the TRF component that is known to directly associate with telomeric (TTAGGG)n repeats (Reis et al 2018; PMID: 29385523). This provides reassurance on the specificity of the selection, as does the lack of cross selectivity between different TALEs used (see later point 3 below). The enrichment of the respective DNA repeats quantitated in Figure 2B (originally Figure S1) also provides strong evidence for TALE selectivity.

It is very likely that most of the components enriched on the repetitive elements targeted by our TALE-YFP proteins do not bind repetitive DNA directly. The TRF telomere binding protein is an exception – but it is the only obvious DNA binding protein amongst the many proteins identified as being enriched in our TelR-TALE-YFP and TRF-YFP affinity selections.

The referee also suggests that follow up experiments using knockdown of the identified proteins found to be enriched on repetitive DNA elements would be informative. In our opinion, this manuscript presents the development of a new methodology previously not applied to trypanosomes, and referee 2 highlights the value of this methodological development which will be relevant for a large community of kinetoplastid researchers. In-depth follow-up analyses would be beyond the scope of this current study but of course will be pursued in future. To be meaningful such knockdown analyses would need to be comprehensive in terms of their phenotypic characterisation (e.g. quantitative effects on chromosome biology and cell cycle progression, rates and mechanism of recombination underlying antigenic variation, etc) – simple RNAi knockdowns would provide information on fitness but little more. This information is already publicly available from genome-wide RNAi screens (www.tritrypDB.org), with further information on protein location available from the genome-wide protein localisation resource (Tryptag.org). Hence basic information is available on all targets selected by the TALEs after RNAi knock down but in-depth follow-up functional analysis of several proteins would require specific targeted assays beyond the scope of this study.

(2) NonR-TALE-YFP does not have a binding site in the genome, but YFP protein should still be expressed by T. brucei clones with NLS. The authors have to explain why there is no signal detected in the nucleus, while a prominent signal was detected near kDNA (see Fig.2). Why is the expression of YFP in NonR-TALE almost not shown compared to other TALE clones?

The NonR-TALE-YFP immunolocalisation signal indeed is apparently located close to the kDNA and away from the nucleus. We are not sure why this is so, but the construct is sequence validated and correct. However, we note that artefactual localisation of proteins fused to a globular eGFP tag, compared to a short linear epitope V5 tag, near to the kinetoplast has been previously reported (Pyrih et al, 2023; PMID: 37669165).

The expression of NonR-TALE-YFP is shown in Supplementary Fig. S2 in comparison to other TALE proteins. Although it is evident that NonR-TALE-YFP is expressed at lower levels than other TALEs (the different TALEs have different expression levels), it is likely that in each case the TALE proteins would be in relative excess.

It is possible that the absence of a target sequence for the NonR-TALE-YFP in the nucleus affects its stability and cellular location. Understanding these differences is tangential to the aim of this study.

However, importantly, NonR-TALE-YFP is not the only control for used for specificity in our affinity purifications. Instead, the lack of cross-selection of the same proteins by different TALEs (e.g. TelR-TALE-YFP, 177R-TALE-YFP) and the lack of enrichment of any proteins of interest by the well expressed ingiR-TALE-YFP or 147R-TALE-YFP proteins each provide strong evidence for the specificity of the selection using TALEs, as does the enrichment of similar protein sets following affinity purification of the TelR-TALE-YFP and TRF-YFP proteins which both bind telomeric (TTAGGG)n repeats. Moreover, control affinity purifications to assess background were performed using cells that completely lack an expressed YFP protein which further support specificity (Figure 6).

We have added text to highlight these important points in the revised manuscript:

Page 8:

“However, the expression level of NonR-TALE-YFP was lower than other TALE-YFP proteins; this may relate to the lack of DNA binding sites for NonR-TALE-YFP in the nucleus.”

Page 8:

“NonR-TALE-YFP displayed a diffuse nuclear and cytoplasmic signal; unexpectedly the cytoplasmic signal appeared to be in the vicinity the kDNA of the kinetoplast (mitochrondria). We note that artefactual localisation of some proteins fused to an eGFP tag has previously been observed in T. brucei (Pyrih et al, 2023).”

Page 10:

Moreover, a similar set of enriched proteins was identified in TelR-TALE-YFP affinity purifications whether compared with cells expressing no YFP fusion protein (No-YFP), the NonR-TALE-YFP or the ingiR-TALE-YFP as controls (Fig. S7B, S8A; Tables S3, S4). Thus, the most enriched proteins are specific to TelR-TALE-YFP-associated chromatin rather than to the TALE-YFP synthetic protein module or other chromatin.

(3) As a proof of concept, the author showed that the TALE method determined the same interacting partners enrichment in TelR-TALE as compared to TRF-YFP. And they show the same interacting partners for other TALE proteins, whether compared with WT cells or with the NonR-TALE parasites. It may be because NonR-TALE parasites have almost no (or very little) YFP expression (see Fig. S3) as compared to other TALE clones and the TRF-YFP clone. To address this concern, there should be a control included, with proper YFP expression.

See response to point 2, but we reiterate that the ingi-TALE -YFP and 147R-TALE-YFP proteins are well expressed (western original Fig. S3 now Fig. S2) but few proteins are detected as being enriched or correspond to those enriched in TelR-TALE-YFP or TRF-YFP affinity purifications (see Fig. S9). Therefore, the ingi-TALE -YFP and 147R-TALE-YFP proteins provide good additional negative controls for specificity as requested. To further reassure the referee we have also included additional volcano plots which compare TelR-TALE-YFP, 70R-TALE-YFP or 177R-TALE-YFP to the ingiR-TALE-YFP affinity selection (new Figure S8). As with No-YFP or NonR-TALE-YFP controls, the use of ingiR-TALE-YFP as a negative control demonstrates that known telomere associated proteins are enriched in TelR-TALE-YFP affinity purification, RPA subunits enriched with 70R-TALE-YFP and Kinetochore KKT poroteins enriched with 177RTALE-YFP. These analyses demonstrate specificity in the proteins enriched following affinity purification of our different TALE-YFPs and provide support to strengthen our original findings.

We now refer to use of No-YFP, NonR-TALE-YFP, and ingiR-TALE -YFP as controls for comparison to TelR-TALE-YFP, 70R-TALE-YFP or 177R-TALE-YFP in several places:

Page10:

“Moreover, a similar set of enriched proteins was identified in TelR-TALE-YFP affinity purifications whether compared with cells expressing no YFP fusion protein (No-YFP), the NonR-TALE-YFP or the ingiR-TALE-YFP as controls (Fig. S7B, S8A; Tables S3, S4).”

Page 11:

“Thus, the nuclear ingiR-TALE-YFP provides an additional chromatin-associated negative control for affinity purifications with the TelR-TALE-YFP, 70R-TALE-YFP and 177R-TALE-YFP proteins (Fig. S8).”

“Proteins identified as being enriched with 70R-TALE-YFP (Figure 6D) were similar in comparisons with either the No-YFP, NonR-TALE-YFP or ingiR-TALE-YFP as negative controls.”

Top Page 12:

“The same kinetochore proteins were enriched regardless of whether the 177R-TALE proteomics data was compared with No-YFP, NonR-TALE or ingiR-TALE-YFP controls.”

Discussion Page 13:

“Regardless, the 147R-TALE and ingiR-TALE proteins were well expressed in T. brucei cells, but their affinity selection did not significantly enrich for any relevant proteins. Thus, 147R-TALE and ingiR-TALE provide reassurance for the overall specificity for proteins enriched TelR-TALE, 70R-TALE and 177R-TALE affinity purifications.”

(4) After the artificial expression of repetitive sequence binding five-TALE proteins, the question is if there is any competition for the TALE proteins with the corresponding endogenous proteins? Is there any effect on parasite survival or health, compared to the control after the expression of these five TALEs YFP protein? It is recommended to add parasite growth curves, for all the TALE proteins expressing cultures.

Growth curves for cells expressing TelR-TALE-YFP, 177R-TALE-YFP and ingiR-TALE-YFP are now included (New Fig S3A). No deficit in growth was evident while passaging 70R-TALE-YFP, 147R-TALE-YFP, NonR-TALE-YFP cell lines (indeed they grew slightly better than controls).

The following text has been added page 8:

“Cell lines expressing representative TALE-YFP proteins displayed no fitness deficit (Fig. S3A).”

(5) Since the experiments were performed using whole-cell extracts without prior nuclear fractionation, the authors should consider the possibility that some identified proteins may have originated from compartments other than the nucleus. Specifically, the detection of certain binding proteins might reflect sequence homology (or partial homology) between mitochondrial DNA (maxicircles and minicircles) and repetitive regions in the nuclear genome. Additionally, the lack of subcellular separation raises the concern that cytoplasmic proteins could have been co-purified due to whole cell lysis, making it challenging to discern whether the observed proteome truly represents the nuclear interactome.

In our experimental design, we confirmed bioinformatically that the repeat sequences targeted were not represented elsewhere in the nuclear or mitochondrial genome (kDNA). The absence of subcellular fractionation could result in some cytoplasmic protein selection, but this is unlikely since each TALE targets a specific DNA sequence but is otherwise identical such that cross-selection of the same contaminating protein set would be anticipated if there was significant non-specific binding. We have previously successfully affinity selected 15 chromatin modifiers and identified associated proteins without major issues concerning cytoplasmic protein contamination (Staneva et al 2021 and 2022; PMID: 34407985 and 36169304). Of course, the possibility that some proteins are contaminants will need to be borne in mind in any future follow-up analysis of proteins of interest that we identified as being enriched on specific types of repetitive element in T. brucei. Proteins that are also detected in negative control, or negative affinity selections such as No-YFP, NoR-YFP, IngiR-TALE or 147R-TALE must be disregarded.

(6) Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

As mentioned earlier, the author claimed that this study has provided new information concerning telomere biology, chromosomal segregation mechanisms, and immune evasion strategies. But there are no experiments that provides a role for any unknown or known protein in these processes. Thus, it is suggested to select one or two proteins of choice from the list and validate their direct binding to repetitive region(s), and their role in that region of interaction.

As highlighted in response to point 1 the suggested validation and follow up experiments may well not be informative and are beyond the scope of the methodological development presented in this manuscript. Referee 2 describes the study in its current form as “a significant conceptual and technical advancement” and “This approach enhances our understanding of chromatin organization in these regions and provides a foundation for investigating the functional roles of associated proteins in parasite biology.”

The Referee’s phrase ‘validate their direct binding to repetitive region(s)’ here may also mean to test if any of the additional proteins that we identified as being enriched with a specific TALE protein actually display enrichment over the repeat regions when examined by an orthogonal method. A key unexpected finding was that kinetochore proteins including KKT2 are enriched in our affinity purifications of the 177R-TALE-YFP that targets 177bp repeats (Figure 6F). By conducting ChIP-seq for the kinetochore specific protein KKT2 using YFP-KKT2 we confirmed that KKT2 is indeed enriched on 177bp repeat DNA but not flanking DNA (Figure 7). Moreover, several known telomere-associated proteins are detected in our affinity selections of TelRTALE-YFP (Figure 6B, FigS6; see also Reis et al, 2018 Nuc. Acids Res. PMID: 29385523; Weisert et al, 2024 Sci. Reports PMID: 39681615).

Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

The answer for this question depends on what the authors want to present as the achievements of the present study. If the achievement of the paper was is the creation of a new tool for discovering new proteins, associated with the repeat regions, I recommend that they add a proof for direct interactions between a sample the newly discovered proteins and the relevant repeats, as a proof of concept discussed above, However, if the authors like to claim that the study achieved new functional insights for these interactions they will have to expand the study, as mentioned above, to support the proof of concept.

See our response to point 1 and the point we labelled ‘6’ above.

Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

I think that they are realistic. If the authors decided to check the capacity of a small sample of proteins (which was unknown before as a repetitive region binding proteins) to interacts directly with the repeated sequence, it will substantially add of the study (e.g., by EMSA; estimated time: 1 months). If the authors will decide to check the also the function of one of at least one such a newly detected proteins (e.g., by KD), I estimate the will take 3-6 months.

As highlighted previously the proposed EMSA experiment may well be uninformative for protein complex components identified in our study or for isolated proteins that directly bind DNA in the context of a complex and chromatin. RNAi knockdown data and cell location data (as well as developmental expression and orthology data) is already available through tritrypDB.org and trtyptag.org

Are the data and the methods presented in such a way that they can be reproduced? Yes

Are the experiments adequately replicated, and statistical analysis adequate?

The authors did not mention replicates. There is no statistical analysis mentioned.

The figure legends indicate that all volcano plots of TALE affinity selections were derived from three biological replicates. Cutoffs used for significance: P < 0.05 (Student's t-test).

For ChiP-seq two biological replicates were analysed for each cell line expressing the specific YFP tagged protein of interest (TALE or KKT2). This is now stated in the relevant figure legends – apologies for this oversight. The resulting data are available for scrutiny at GEO: GSE295698.

Minor comments:

Specific experimental issues that are easily addressable.

The following suggestions can be incorporated:

(1) Page 18, in the material method section author mentioned four drugs: Blasticidine, Phleomycin and G418, and hygromycin. It is recommended to mention the purpose of using these selective drugs for the parasite. If clonal selection has been done, then it should also be mentioned.

We erroneously added information on several drugs used for selection in our labaoratory. In fact all TALE-YFP construct carry the Bleomycin resistance genes which we select for using Phleomycin. Also, clones were derived by limiting dilution immediately after transfection. We have amended the text accordingly:

Page 17/18:

“Cell cultures were maintained below 3 x 106 cells/ml. Pleomycin 2.5 µg/ml was used to select transformants containing the TALE construct BleoR gene.”

“Electroporated bloodstream cells were added to 30 ml HMI-9 medium and two 10-fold serial dilutions were performed in order to isolate clonal Pleomycin resistant populations from the transfection. 1 ml of transfected cells were plated per well on 24-well plates (1 plate per serial dilution) and incubated at 37°C and 5% CO2 for a minimum of 6 h before adding 1 ml media containing 2X concentration Pleomycin (5 µg/ml) per well.”

(2) In the method section the authors mentioned that there is only one site for binding of NonR-TALE in the parasite genome. But in Fig. 1C, the authors showed zero binding site. So, there is one binding site for NonR-TALE-YFP in the genome or zero?

We thank the reviewer for pointing out this discrepancy. We have checked the latest Tb427v12 genome assembly for predicted NonR-TALE binding sites and there are no exact matches. We have corrected the text accordingly.

Page 7:

“A control NonR-TALE protein was also designed which was predicted to have no target sequence in the T. brucei genome.”

Page 17:

“A control NonR-TALE predicted to have no recognised target in the T. brucei geneome was designed as follows: BLAST searches were used to identify exact matches in the TREU927 reference genome. Candidate sequences with one or more match were discarded.”

(3) The authors used two different anti-GFP antibodies, one from Roche and the other from Thermo Fisher. Why were two different antibodies used for the same protein?

We have found that only some anti-GFP antibodies are effective for affinity selection of associated proteins, whereas others are better suited for immunolocalisation. The respective suppliers’ antibodies were optimised for each application.

(4) Page 6: in the introduction, the authors give the number of total VSG genes as 2,634. Is it known how many of them are pseudogenes?

This value corresponds to the number reported by Consentino et al. 2021 (PMID: 34541528) for subtelomeric VSGs, which is similar to the value reported by Muller et al 2018 (PMID: 30333624) (2486), both in the same strain of trypanosomes as used by us. Based on the earlier analysis by Cross et al (PMID: 24992042), 80% of the identified VSGs in their study (2584) are pseudogenes. This approximates to the estimation by Consentino of 346/2634 (13%) being fully functional VSG genes at subtelomeres, or 17% when considering VSGs at all genomic locations (433/2872).

(5) I found several typos throughout the manuscript.

Thank you for raising this, we have read through the manuscipt several times and hopefully corrected all outstanding typos.

(6) Fig. 1C: Table: below TOTAL 2nd line: the number should be 1838 (rather than 1828)

Corrected- thank you.

- Are prior studies referenced appropriately? Yes

- Are the text and figures clear and accurate? Yes

- Do you have suggestions that would help the authors improve the presentation of their data and conclusions? Suggested above

Reviewer #1 (Significance):

Describe the nature and significance of the advance (e.g., conceptual, technical, clinical) for the field:

This study represents a significant conceptual and technical advancement by employing a synthetic TALE DNA-binding protein tagged with YFP to selectively identify proteins associated with five distinct repetitive regions of T. brucei chromatin. To the best of my knowledge, it is the first report to utilize TALE-YFP for affinity-based isolation of protein complexes bound to repetitive genomic sequences in T. brucei. This approach enhances our understanding of chromatin organization in these regions and provides a foundation for investigating the functional roles of associated proteins in parasite biology. Importantly, any essential or unique interacting partners identified could serve as potential targets for therapeutic intervention.

- Place the work in the context of the existing literature (provide references, where appropriate). I agree with the information that has already described in the submitted manuscript, regarding its potential addition of the data resulted and the technology established to the study of VSGs expression, kinetochore mechanism and telomere biology.

- State what audience might be interested in and influenced by the reported findings. These findings will be of particular interest to researchers studying the molecular biology of kinetoplastid parasites and other unicellular organisms, as well as scientists investigating chromatin structure and the functional roles of repetitive genomic elements in higher eukaryotes.

- (1) Define your field of expertise with a few keywords to help the authors contextualize your point of view. Protein-DNA interactions/ chromatin/ DNA replication/ Trypanosomes

- (2) Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate. None

Reviewer #2 (Evidence, reproducibility and clarity):

Summary

Carloni et al. comprehensively analyze which proteins bind repetitive genomic elements in Trypanosoma brucei. For this, they perform mass spectrometry on custom-designed, tagged programmable DNA-binding proteins. After extensively verifying their programmable DNA-binding proteins (using bioinformatic analysis to infer target sites, microscopy to measure localization, ChIP-seq to identify binding sites), they present, among others, two major findings: 1) 14 of the 25 known T. brucei kinetochore proteins are enriched at 177bp repeats. As T. brucei's 177bp repeatcontaining intermediate-sized and mini-chromosomes lack centromere repeats but are stable over mitosis, Carloni et al. use their data to hypothesize that a 'rudimentary' kinetochore assembles at the 177bp repeats of these chromosomes to segregate them. 2) 70bp repeats are enriched with the Replication Protein A complex, which, notably, is required for homologous recombination. Homologous recombination is the pathway used for recombination-based antigenic variation of the 70bp-repeat-adjacent variant surface glycoproteins.

Major Comments

None. The experiments are well-controlled, claims well-supported, and methods clearly described. Conclusions are convincing.

Thank you for these positive comments.

Minor Comments

(1) Fig. 2 - I couldn't find an uncropped version showing multiple cells. If it exists, it should be linked in the legend or main text; Otherwise, this should be added to the supplement.

The images presented represent reproducible analyses, and independently verified by two of the authors. Although wider field of view images do not provide the resolution to be informative on cell location, as requested we have provided uncropped images in new Fig. S4 for all the cell lines shown in Figure 2A.

In addition, we have included as supplementary images (Fig. S3B) additional images of TelRTALE-YFP, 177R-TALE-YFP and ingiR-TALE YFP localisation to provide additional support their observed locations presented in Figure 1. The set of cells and images presented in Figure 2A and in Fig S3B were prepared and obtained by a different authors, independently and reproducibly validating the location of the tagged protein.

(2) I think Suppl. Fig. 1 is very valuable, as it is a quantification and summary of the ChIP-seq data. I think the authors could consider making this a panel of a main figure. For the main figure, I think the plot could be trimmed down to only show the background and the relevant repeat for each TALE protein, leaving out the non-target repeats. (This relates to minor comment 6.) Also, I believe, it was not explained how background enrichment was calculated.

We are grateful for the reviewer’s positive view of original Fig. S1 and appreciate the suggestion. We have now moved these analysis to part B of main Figure 2 in the revised manuscript – now Figure 2B. We have also provided additional details in the Methods section on the approaches used to assess background enrichment.

Page 19:

“Background enrichment calculation

The genome was divided into 50 bp sliding windows, and each window was annotated based on overlapping genomic features, including CIR147, 177 bp repeats, 70 bp repeats, and telomeric (TTAGGG)n repeats. Windows that did not overlap with any of these annotated repeat elements were defined as "background" regions and used to establish the baseline ChIP-seq signal. Enrichment for each window was calculated using bamCompare, as log₂(IP/Input). To adjust for background signal amongst all samples, enrichment values for each sample were further normalized against the corresponding No-YFP ChIP-seq dataset.”

Note: While revising the manuscript we also noticed that the script had a nomalization error. We have therefore included a corrected version of these analyses as Figure 2B (old Fig. S1)

(3) Generally, I would plot enrichment on a log2 axis. This concerns several figures with ChIP-seq data.

Our ChIP-seq enrichment is calculated by bamCompare. The resulting enrichment values are indeed log2 (IP/Input). We have made this clear in the updated figures/legends.

(4) Fig. 4C - The violin plots are very hard to interpret, as the plots are very narrow compared to the line thickness, making it hard to judge the actual volume. For example, in Centromere 5, YFP-KKT2 is less enriched than 147R-TALE over most of the centromere with some peaks of much higher enrichment (as visible in panel B), however, in panel C, it is very hard to see this same information. I'm sure there is some way to present this better, either using a different type of plot or by improving the spacing of the existing plot.

We thank the reviewer for this suggestion; we have elected to provide a Split-Violin plot instead. This improves the presentation of the data for each centromere. The original violin plot in Figure 4C has been replaced with this Split-Violin plot (still Figure 4C).

(5) Fig. 6 - The panels are missing an x-axis label (although it is obvious from the plot what is displayed).

Maybe the "WT NO-YFP vs" part that is repeated in all the plot titles could be removed from the title and only be part of the x-axis label?

In fact, to save space the X axis was labelled inside each volcano plot but we neglected to indicate that values are a log2 scale indicating enrichment. This has been rectified – see Figure 6, and Fig. S7, S8 and S9.

(6) Fig. 7 - I would like to have a quantification for the examples shown here. In fact, such a quantification already exists in Suppl. Figure 1. I think the relevant plots of that quantification (YFPKKT2 over 177bp-repeats and centromere-repeats) with some control could be included in Fig. 7 as panel C. This opportunity could be used to show enrichment separated out for intermediate-sized, mini-, and megabase-chromosomes. (relates to minor comment 2 & 8)

The CIR147 sequence is found exclusively on megabase-sized chromosomes, while the 177 bp repeats are located on intermediate- and mini-sized chromosomes. Due to limitations in the current genome assembly, it is not possible to reliably classify all chromosomes into intermediate- or mini- sized categories based on their length. Therefore, original Supplementary Fig. S1 presented the YFP-KKT2 enrichment over CIR147 and 177 bp repeats as a representative comparison between megabase chromosomes and the remaining chromosomes (corrected version now presented as main Figure 2B). Additionally, to allow direct comparison of YFP-KKT2 enrichment on CIR147 and 177 bp repeats we have included a new plot in Figure 7C which shows the relative enrichment of YFP-KKT2 on these two repeat types.

We have added the following text , page 12:

“Taking into account the relative to the number of CIR147 and 177 bp repeats in the current T.brucei genome (Cosentino et al., 2021; Rabuffo et al., 2024), comparative analyses demonstrated that YFP-KKT2 is enriched on both CIR147 and 177 bp repeats (Figure 7C).”

(7) Suppl. Fig. 8 A - I believe there is a mistake here: KKT5 occurs twice in the plot, the one in the overlap region should be KKT1-4 instead, correct?

Thanks for spotting this. It has been corrected

(8) The way that the authors mapped ChIP-seq data is potentially problematic when analyzing the same repeat type in different regions of the genome. The authors assigned reads that had multiple equally good mapping positions to one of these mapping positions, randomly.

This is perfectly fine when analysing repeats by their type, independent of their position on the genome, which is what the authors did for the main conclusions of the work.

However, several figures show the same type of repeat at different positions in the genome. Here, the authors risk that enrichment in one region of the genome 'spills' over to all other regions with the same sequence. Particularly, where they show YFP-KKT2 enrichment over intermediate- and mini-chromosomes (Fig. 7) due to the spillover, one cannot be sure to have found KKT2 in both regions.

Instead, the authors could analyze only uniquely mapping reads / read-pairs where at least one mate is uniquely mapping. I realize that with this strict filtering, data will be much more sparse. Hence, I would suggest keeping the original plots and adding one more quantification where the enrichment over the whole region (e.g., all 177bp repeats on intermediate-/mini-chromosomes) is plotted using the unique reads (this could even be supplementary). This also applies to Fig. 4 B & C.

We thank the reviewer for their thoughtful comments. Repetitive sequences are indeed challenging to analyze accurately, particularly in the context of short read ChIP-seq data. In our study, we aimed to address YFP-KKT2 enrichment not only over CIR147 repeats but also on 177 bp repeats, using both ChIP-seq and proteomics using synthetic TALE proteins targeted to the different repeat types. We appreciate the referees suggestion to consider uniquely mapped reads, however, in the updated genome assembly, the 177 bp repeats are frequently immediately followed by long stretches of 70 bp repeats which can span several kilobases. The size and repetitive nature of these regions exceeds the resolution limits of ChIP-seq. It is therefore difficult to precisely quantify enrichment across all chromosomes.

Additionally, the repeat sequences are highly similar, and relying solely on uniquely mapped reads would result in the exclusion of most reads originating from these regions, significantly underestimating the relative signals. To address this, we used Bowtie2 with settings that allow multi-mapping, assigning reads randomly among equivalent mapping positions, but ensuring each read is counted only once. This approach is designed to evenly distribute signal across all repetitive regions and preserve a meaningful average.

Single molecule methods such as DiMeLo (Altemose et al. 2022; PMID: 35396487) will need to be developed for T. brucei to allow more accurate and chromosome specific mapping of kinetochore or telomere protein occupancy at repeat-unique sequence boundaries on individual chromosomes.

Reviewer #2 (Significance):

This work is of high significance for chromosome/centromere biology, parasitology, and the study of antigenic variation. For chromosome/centromere biology, the conceptual advancement of different types of kinetochores for different chromosomes is a novelty, as far as I know. It would certainly be interesting to apply this study as a technical blueprint for other organisms with minichromosomes or chromosomes without known centromeric repeats. I can imagine a broad range of labs studying other organisms with comparable chromosomes to take note of and build on this study. For parasitology and the study of antigenic variation, it is crucial to know how intermediate- and mini-chromosomes are stable through cell division, as these chromosomes harbor a large portion of the antigenic repertoire. Moreover, this study also found a novel link between the homologous repair pathway and variant surface glycoproteins, via the 70bp repeats. How and at which stages during the process, 70bp repeats are involved in antigenic variation is an unresolved, and very actively studied, question in the field. Of course, apart from the basic biological research audience, insights into antigenic variation always have the potential for clinical implications, as T. brucei causes sleeping sickness in humans and nagana in cattle. Due to antigenic variation, T. brucei infections can be chronic.

Thank you for supporting the novelty and broad interest of our manuscript

My field of expertise / Point of view:

I'm a computer scientist by training and am now a postdoctoral bioinformatician in a molecular parasitology laboratory. The laboratory is working on antigenic variation in T. brucei. The focus of my work is on analyzing sequencing data (such as ChIP-seq data) and algorithmically improving bioinformatic tools.

Very active and detailed!

Author response:

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

Public reviews:

Reviewer #1 (Public review):

Summary: 

The authors provide a resource to the systems neuroscience community, by offering their Python-based CLoPy platform for closed-loop feedback training. In addition to using neural feedback, as is common in these experiments, they include a capability to use real-time movement extracted from DeepLabCut as the control signal. The methods and repository are detailed for those who wish to use this resource. Furthermore, they demonstrate the efficacy of their system through a series of mesoscale calcium imaging experiments. These experiments use a large number of cortical regions for the control signal in the neural feedback setup, while the movement feedback experiments are analyzed more extensively.

Strengths:

The primary strength of the paper is the availability of their CLoPy platform. Currently, most closed-loop operant conditioning experiments are custom built by each lab and carry a relatively large startup cost to get running. This platform lowers the barrier to entry for closed-loop operant conditioning experiments, in addition to making the experiments more accessible to those with less technical expertise.

Another strength of the paper is the use of many different cortical regions as control signals for the neurofeedback experiments. Rodent operant conditioning experiments typically record from the motor cortex and maybe one other region. Here, the authors demonstrate that mice can volitionally control many different cortical regions not limited to those previously studied, recording across many regions in the same experiment. This demonstrates the relative flexibility of modulating neural dynamics, including in non-motor regions.

Finally, adapting the closed-loop platform to use real-time movement as a control signal is a nice addition. Incorporating movement kinematics into operant conditioning experiments has been a challenge due to the increased technical difficulties of extracting real-time kinematic data from video data at a latency where it can be used as a control signal for operant conditioning. In this paper they demonstrate that the mice can learn the task using their forelimb position, at a rate that is quicker than the neurofeedback experiments.

Weaknesses:

There are several weaknesses in the paper that diminish the impact of its strengths. First, the value of the CLoPy platform is not clearly articulated to the systems neuroscience community. Similarly, the resource could be better positioned within the context of the broader open-source neuroscience community. For an example of how to better frame this resource in these contexts, I recommend consulting the pyControl paper. Improving this framing will likely increase the accessibility and interest of this paper to a less technical neuroscience audience, for instance by highlighting the types of experimental questions CLoPy can enable.

We appreciate the editor’s feedback regarding the clarity of the CLoPy platform's value and its positioning within the broader neuroscience community. We agree and understand the importance of effectively communicating the utility of CLoPy to both the systems neuroscience field and the wider open-source neuroscience community.

To address this, we have revised the introduction and discussion sections of the manuscript to more clearly articulate the unique contributions of the CLoPy platform. Specifically:

(1) We have emphasized how CLoPy can address experimental questions in systems neuroscience by highlighting its ability to enable real-time closed-loop experiments, such as investigating neural dynamics during behavior or studying adaptive cortical reorganization after injury. These examples are aimed at demonstrating its practical utility to the neuroscience audience.

(2) We have positioned CLoPy within the broader open-source neuroscience ecosystem, drawing comparisons to similar resources like pyControl. We describe how CLoPy complements existing tools by focusing on real-time optical feedback and integration with genetically encoded indicators, which are becoming increasingly popular in systems neuroscience. We also emphasize its modularity and ease of adoption in experimental settings with limited resources.

(3) To make the manuscript more accessible to a less technically inclined audience, we have restructured certain sections to focus on the types of experiments CLoPy enables, rather than the technical details of the implementation.

We have consulted the pyControl paper, as suggested, and have used it as a reference point to improve the framing of our resource. We believe these changes will increase the accessibility and appeal of the paper to a broader neuroscience audience.

While the dataset contains an impressive amount of animals and cortical regions for the neurofeedback experiment, and an analysis of the movement-feedback experiments, my excitement for these experiments is tempered by the relative incompleteness of the dataset, as well as its description and analysis in the text. For instance, in the neurofeedback experiment, many of these regions only have data from a single mouse, limiting the conclusions that can be drawn. Additionally, there is a lack of reporting of the quantitative results in the text of the document, which is needed to better understand the degree of the results. Finally, the writing of the results section could use some work, as it currently reads more like a methods section.

Thank you for your thoughtful and constructive feedback on our manuscript. We appreciate the time and effort you took to review our work and provide detailed suggestions for improvement. Below, we address the key points raised in your review:

(1) Dataset Completeness: We acknowledge that some of the neurofeedback experiments include data from only a single mouse for some cortical regions while for some cortical regions, there are several animals. This was due to practical constraints during the study, and we understand the limitations this poses for drawing broad conclusions. We felt it was still important to include these data sets with smaller sample sizes as they might be useful for others pursuing this direction in the future. To address this, we have revised the text to explicitly acknowledge these limitations and clarify that the results for some regions are exploratory in nature. We believe our flexible tool will provide a means for our lab and others include more animals representing additional cortical regions in future studies. Importantly, we have included all raw and processed data as well as code for future analysis.

(2) Quantitative Results: We recognize the importance of reporting quantitative results in the text for better clarity and interpretation. In response, we have added more detailed description of the quantitative findings from both the neurofeedback and movement-feedback experiments. This will include effect sizes, statistical measures, and key numerical results to provide a clearer understanding of the degree and significance of the observed effects.

(3) Results Section Writing: We appreciate your observation that parts of the results section read more like a methods section. To improve clarity and focus, we have restructured the results section to present the findings in a more concise and interpretative manner, while moving overly detailed descriptions of experimental procedures to the methods section.

Suggestions for improved or additional experiments, data or analyses:

Not necessary for this paper, but it would be interesting to see if the CLNF group could learn without auditory feedback.

This is a great suggestion and certainly something that could be done in the future.

There are no quantitative results in the results section. I would add important results to help the reader better interpret the data. For example, in: "Our results indicated that both training paradigms were able to lead mice to obtain a significantly larger number of rewards over time," You could show a number, with an appropriate comparison or statistical test, to demonstrate that learning was observed.

Thank you for pointing this out. We have mentioned quantification values in the results now, along with being mentioned in the figure legends, and we are quoting it in following sentences. “A ΔF/F0 threshold value was calculated from a baseline session on day 0 that would have allowed 25% performance. Starting from this basal performance of around 25% on day 1, mice (CLNF No-rule-change, N=23, n=60 and CLNF Rule-change, N=17, n=60) were able to discover the task rule and perform above 80% over ten days of training (Figure 4A, RM ANOVA p=2.83e-5), and Rule-change mice even learned a change in ROIs or rule reversal (Figure 4A, RM ANOVA p=8.3e-10, Table 5 for different rule changes). There were no significant differences between male and female mice (Supplementary Figure 3A).”

For: "Performing this analysis indicated that the Raspberry Pi system could provide reliable graded feedback within ~63 {plus minus} 15 ms for CLNF experiments." The LED test shows the sending of the signal, but the actual delay for the audio generation might be longer. This is also longer than the 50 ms mentioned in the abstract.

We appreciate the reviewer’s insightful comment. The latency reported (~63ms) was measured using the LED test, which captures the time from signal detection to output triggering on the Raspberry Pi GPIO. We agree that the total delay for auditory feedback generation could include an additional latency component related to the digital-to-analog conversion and speaker response. In our setup, we employ a fast Audiostream library written in C to generate the audio signal and expect the delay contribution to be negligible compared to the GPIO latency. Though we did not do this, it can be confirmed by an oscilloscope-based pilot measurement (for additional delay calculation). We have updated the manuscript to clarify that the 63 ± 15 ms value reflects the GPIO-triggered output latency, and we have revised the abstract to accurately state the delay as “~63 ms” rather than 50 ms. This ensures consistency and avoids underestimation of the latency. We have corrected the LED latency for CLNF and CLMF experiments in the abstract as well.

It could be helpful to visualize an individual trial for each experiment type, for instance how the audio frequency changes as movement speed / calcium activity changes.

We have added Supplementary Figure 8 that contains this data where you can see the target cortical activity trace, target paw speed, rewards, along with the audio frequency generated.

The sample sizes are small (n=1) for a few groups. I am excited by the variety of regions recorded, so it could be beneficial for the authors to collect a few more animals to beef up the sample sizes.

We've acknowledged that some of the sample sizes are small. Importantly, we have included raw and processed data as well as code for future analysis. We felt it was still important to still include these data sets with smaller sample sizes as they might be useful for others pursuing this direction in the future.

I am curious as to why 60 trials sessions were used. Was it mostly for the convenience of a 30 min session, or were the animals getting satiated? If the former, would learning have occurred more rapidly with longer sessions?

This is a great observation and the answer is it was mostly due to logistical reasons. We tried to not keep animals headfixed for more than 45 minutes in each session as they become less engaged with long duration headfixed sessions. After headfixing them, it takes about 15 minutes to get the experiment going and therefore 30 - 40 minutes long recorded sessions seemed appropriate before they stop being engaged or before they get satiated in the task. We provided supplemental water after the sessions and we observed that they consumed water after the sessions so they were not fully satiated during the sessions even when they performed well in the task and got maximum rewards. We also had inter-trial rest periods of 10s that elongated the session duration. We think it would be interesting to explore the relationship between session duration(number of trials) and task learning progression over the days in a separate study.

Figure 4E is interesting, it seems like the changes in the distribution of deltaF was in both positive and negative directions, instead of just positive. I'd be curious as to the author's thoughts as to why this is the case. Relatedly, I don't see Figure 4E, and a few other subplots, mentioned in the text. As a general comment, I would address each subplot in the text.

We have split Figure 4 into two to keep the figures more readable. Previous Figure 4E-H are now Figure 5A-D in the revised manuscript. The online real-time CLNF sessions were using a moving window average to calculate ΔF/F₀  and the figures were generated by averaging the whole recorded sessions. We have added text in Methods under “Online ΔF/F₀calculation” and “Offline ΔF/F₀ calculation” sections making it clear about how we do our ΔF/F₀ normalization based on average fluorescence over the entire session. Using this method of normalization does increase the baseline so that some peaks appear to be below zero. Additionally, it is unclear what strategy animals are employing to achieve the rule specific target activity. The task did not constrain them to have a specific strategy for cortical activation - they were rewarded as long as they crossed the threshold in target ROI(s). For example, in 2-ROI experiments, to increase ROI1-ROI2 target activity, they could increase activity of ROI1 relative to ROI2 or decreased activity of ROI1 relative to ROI1 - both would have led to a reward as long as the result crossed the threshold.

We have now addressed and added reference to the figures in the text in Results under “Mice can explore and learn an arbitrary task, rule, and target conditions” and “Mice can rapidly adapt to changes in the task rule” sections - thanks for pointing this out.

For: "In general, all ROIs assessed that encompassed sensory, pre-motor, and motor areas were capable of supporting increased reward rates over time," I would provide a visual summary showing the learning curves for the different types of regions.

We have rewritten this section to emphasize that these conclusions were based on pooled data from multiple regions of interest. The sample sizes for each type of region are different and some are missing. We believe it would be incomplete and not comparable to present this as a regular analysis since the sample sizes were not balanced. We would be happy to dive deeper into this and point to the raw and processed dataset if anyone would like to explore this further by GitHub or other queries.

Relatedly, I would further explain the fast vs slow learners, and if they mapped onto certain regions.

Mice were categorized into fast or slow learners based on the slope of learning over days (reward progression over the days) as shown in Supplementary Figure 3C,D. Our initial aim was not to probe cortical regions that led to fast vs slow learning but this was a grouping we did afterwards. Based on the analysis we did, the fast learners included the sensory (V1), somatosensory (BC, HL), and motor (M1, M2) areas, while the slow learners included the motor (M1, M2), and higher order (TR, RL) cortical areas. Testing all dorsal cortical areas would be prudent to establish their role in fast or slow learning and it is an interesting future direction.

Also I would make the labels for these plots (e.g. Supp Fig3) more intuitive, versus the acronyms currently used.

We have made more expressive labels and explained the acronyms below the Supplementary Figure 3.

The CLMF animals showed a decrease in latency across learning, what about the CLNF animals? There is currently no mention in the text or figures.

We have now incorporated the CLNF task latency data into both the Results text and Figure 4C. Briefly, task latency decreased as performance improved, increased following a rule change, and then decreased again as the animals relearned the task. The previous Figure 4C has been updated to Figure 4D, and the former Figure 4D has been moved to Supplementary Figure 4E.

Reviewer #2 (Public review):

Summary:

In this work, Gupta & Murphy present several parallel efforts. On one side, they present the hardware and software they use to build a head-fixed mouse experimental setup that they use to track in "real-time" the calcium activity in one or two spots at the surface of the cortex. On the other side, the present another setup that they use to take advantage of the "real-time" version of DeepLabCut with their mice. The hardware and software that they used/develop is described at length, both in the article and in a companion GitHub repository. Next, they present experimental work that they have done with these two setups, training mice to max out a virtual cursor to obtain a reward, by taking advantage of auditory tone feedback that is provided to the mice as they modulate either (1) their local cortical calcium activity, or (2) their limb position.

Strengths:

This work illustrates the fact that thanks to readily available experimental building blocks, body movement and calcium imaging can be carried using readily available components, including imaging the brain using an incredibly cheap consumer electronics RGB camera (RGB Raspberry Pi Camera). It is a useful source of information for researchers that may be interested in building a similar setup, given the highly detailed overview of the system. Finally, it further confirms previous findings regarding the operant conditioning of the calcium dynamics at the surface of the cortex (Clancy et al. 2020) and suggests an alternative based on deeplabcut to the motor tasks that aim to image the brain at the mesoscale during forelimb movements (Quarta et al. 2022).

Weaknesses:

This work covers 3 separate research endeavors: (1) The development of two separate setups, their corresponding software. (2) A study that is highly inspired from the Clancy et al. 2020 paper on the modulation of the local cortical activity measured through a mesoscale calcium imaging setup. (3) A study of the mesoscale dynamics of the cortex during forelimb movements learning. Sadly, the analyses of the physiological data appears uncomplete, and more generally the paper tends to offer overstatements regarding several points:

In contrast to the introductory statements of the article, closed-loop physiology in rodents is a well-established research topic. Beyond auditory feedback, this includes optogenetic feedback (O'Connor et al. 2013, Abbasi et al. 2018, 2023), electrical feedback in hippocampus (Girardeau et al. 2009), and much more.

We have included and referenced these papers in our introduction section (quoted below) and rephrased the part where our previous text indicated there are fewer studies involving closed-loop physiology.

“Some related studies have demonstrated the feasibility of closed-loop feedback in rodents, including hippocampal electrical feedback to disrupt memory consolidation (Girardeau et al.2009), optogenetic perturbations of somatosensory circuits during behavior (O'Connor et al.2013), and more recent advances employing targeted optogenetic interventions to guide behavior (Abbasi et al. 2023).”

The behavioral setups that are presented are representative of the state of the art in the field of mesoscale imaging/head fixed behavior community, rather than a highly innovative design. In particular, the closed-loop latency that they achieve (>60 ms) may be perceived by the mice. This is in contrast with other available closed-loop setups.

We thank the reviewer for this thoughtful comment and fully agree that our closed-loop latency is larger than that achieved in some other contemporary setups. Our primary aim in presenting this work, however, is not to compete with the lowest possible latencies, but to provide an open-source, accessible, and flexible platform that can be readily adopted by a broad range of laboratories. By building on widely available and lower-cost components, our design lowers the barrier of entry for groups that wish to implement closed-loop imaging and behavioral experiments, while still achieving latencies well within the range that can support many biologically meaningful applications.

For example, our latency (~60 ms) remains compatible with experimental paradigms such as:

Motor learning and skill acquisition, where sensorimotor feedback on the scale of tens to hundreds of milliseconds is sufficient to modulate performance.

Operant conditioning and reward-based learning, in which reinforcement timing windows are typically broader and not critically dependent on sub-20 ms latencies.

Cortical state dependent modulation, where feedback linked to slower fluctuations in brain activity (hundreds of milliseconds to seconds) can provide valuable insight.

Studies of perception and decision-making, in which stimulus response associations often unfold on behavioral timescales longer than tens of milliseconds.

We believe that emphasizing openness, affordability, and flexibility will encourage widespread adoption and adaptation of our setup across laboratories with different research foci. In this way, our contribution complements rather than competes with ultra-low-latency closed-loop systems, providing a practical option for diverse experimental needs.

Through the paper, there are several statements that point out how important it is to carry out this work in a closed-loop setting with an auditory feedback, but sadly there is no "no feedback" control in cortical conditioning experiments, while there is a no-feedback condition in the forelimb movement study, which shows that learning of the task can be achieved in the absence of feedback.

We fully agree that such a control would provide valuable insight into the contribution of feedback to learning in the CLNF paradigm. In designing our initial experiments, we envisioned multiple potential control conditions, including No-feedback and Random-feedback. However, our first and primary objective was to establish whether mice could indeed learn to modulate cortical ROI activation through auditory feedback, and to further investigate this across multiple cortical regions. For this reason, we focused on implementing the CLNF paradigm directly, without the inclusion of these additional control groups. To broaden the applicability of the system, we subsequently adapted the platform to the CLMF experiments, where we did incorporate a No-feedback group. These results, as the reviewer notes, strengthen the evidence for the role of feedback in shaping task performance. We agree that the inclusion of a No-feedback control group in the CLNF paradigm will be crucial in future studies to further dissect the specific contribution of feedback to cortical conditioning.

The analysis of the closed-loop neuronal data behavior lacks controls. Increased performance can be achieved by modulating actively only one of the two ROIs, this is not clearly analyzed (for instance looking at the timing of the calcium signal modulation across the two ROIs. It seems that overall ROIs1 and 2 covariate, in contrast to Clancy et al. 2020. How can this be explained?

We agree that the possibility of increased performance being driven by modulation of a single ROI is an important consideration. Our study indeed began with 1-ROI closed-loop experiments. In those early experiments, while we did observe animals improving performance across days, we realized that daily variability in ongoing cortical GCaMP activity could lead to fluctuations in threshold-crossing events. The 2-ROI design was subsequently introduced to reduce this variability, as the target activity was defined as the relative activity between the two ROIs (e.g., ROI1 – ROI2). This approach offered a more stable signal by normalizing ongoing fluctuations. In our analysis of the early 2-ROI experiments, we observed that animals adopted diverging strategies to achieve threshold crossings. Specifically, some animals increased activity in ROI1 relative to ROI2, while others decreased activity in ROI2 to accomplish the same effect. Once discovered, each animal consistently adhered to its chosen strategy throughout subsequent training sessions. This was an early and intriguing observation, but as the experiments were not originally designed to systematically test this effect, we limited our presentation to the analysis of a small number of animals (shown in Figure 11). We have added details about this observation in our Results section as well, quoted below-

“In the 2-ROI experiment where the task rule required “ROI1 - ROI2” activity to cross a threshold for reward delivery, mice displayed divergent strategies. Some animals predominantly increased ROI1 activity, whereas others reduced ROI2 activity, both approaches leading to successful threshold crossing (Figure 11)”.

We hope this clarifies how the use of two ROIs helps explain the apparent covariation of the signals, and why some divergence from the observations of Clancy et al. (2020) may be expected.

Reviewer #3 (Public review):

Summary:

The study demonstrates the effectiveness of a cost-effective closed-loop feedback system for modulating brain activity and behavior in head-fixed mice. Authors have tested real-time closed-loop feedback system in head-fixed mice two types of graded feedback: 1) Closed-loop neurofeedback (CLNF), where feedback is derived from neuronal activity (calcium imaging), and 2) Closed-loop movement feedback (CLMF), where feedback is based on observed body movement. It is a python based opensource system, and authors call it CLoPy. The authors also claim to provide all software, hardware schematics, and protocols to adapt it to various experimental scenarios. This system is capable and can be adapted for a wide use case scenario.

Authors have shown that their system can control both positive (water drop) and negative reinforcement (buzzer-vibrator). This study also shows that using the close loop system mice have shown better performance, learnt arbitrary task and can adapt to change in the rule as well. By integrating real-time feedback based on cortical GCaMP imaging and behavior tracking authors have provided strong evidence that such closed-loop systems can be instrumental in exploring the dynamic interplay between brain activity and behavior.

Strengths:

Simplicity of feedback systems designed. Simplicity of implementation and potential adoption.

Weaknesses:

Long latencies, due to slow Ca2+ dynamics and slow imaging (15 FPS), may limit the application of the system.

We appreciate the reviewer’s comment and agree that latency is an important factor in our setup. The latency arises partly from the inherent slow kinetics of calcium signaling and GCaMP6s, and partly from the imaging rate of 15 FPS (every 66 ms). These limitations can be addressed in several ways: for example, using faster calcium indicators such as GCaMP8f, or adapting the system to electrophysiological signals, which would require additional processing capacity. In our implementation, image acquisition was fixed at 15 FPS to enable real-time frame processing (256 × 256 resolution) on Raspberry Pi 4B devices. With newer hardware, such as the Raspberry Pi 5, substantially higher acquisition and processing rates are feasible (although we have not yet benchmarked this extensively). More powerful platforms such as Nvidia Jetson or conventional PCs would further support much faster data acquisition and processing.

Major comments:

(1) Page 5 paragraph 1: "We tested our CLNF system on Raspberry Pi for its compactness, general-purpose input/output (GPIO) programmability, and wide community support, while the CLMF system was tested on an Nvidia Jetson GPU device." Can these programs and hardware be integrated with windows-based system and a microcontroller (Arduino/ Tency). As for the broad adaptability that's what a lot of labs would already have (please comment/discuss)?

While we tested our CLNF system on a Raspberry Pi (chosen for its compactness, GPIO programmability, and large user community) and our CLMF system on an Nvidia Jetson GPU device (to leverage real-time GPU-based inference), the underlying software is fully written in Python. This design choice makes the system broadly adaptable: it can be run on any device capable of executing Python scripts, including Windows-based PCs, Linux machines, and macOS systems. For hardware integration, we have confirmed that the framework works seamlessly with microcontrollers such as Arduino or Teensy, requiring only minor modifications to the main script to enable sending and receiving of GPIO signals through those boards. In fact, we are already using the same system in an in-house project on a Linux-based PC where an Arduino is connected to the computer to provide GPIO functionality. Furthermore, the system is not limited to Raspberry Pi or Arduino boards; it can be interfaced with any GPIO-capable devices, including those from Adafruit and other microcontroller platforms, depending on what is readily available in individual labs. Since many neuroscience and engineering laboratories already possess such hardware, we believe this design ensures broad accessibility and ease of integration across diverse experimental setups.

(2) Hardware Constraints: The reliance on Raspberry Pi and Nvidia Jetson (is expensive) for real-time processing could introduce latency issues (~63 ms for CLNF and ~67 ms for CLMF). This latency might limit precision for faster or more complex behaviors, which authors should discuss in the discussion section.

In our system, we measured latencies of approximately ~63 ms for CLNF and ~67 ms for CLMF. While such latencies indeed limit applications requiring millisecond precision, such as fast whisker movements, saccades, or fine-reaching kinematics, we emphasize that many relevant behaviors, including postural adjustments, limb movements, locomotion, and sustained cortical state changes, occur on timescales that are well within the capture range of our system. Thus, our platform is appropriate for a range of mesoscale behavioral studies that probably needs to be discussed more. It is also important to note that these latencies are not solely dictated by hardware constraints. A significant component arises from the inherent biological dynamics of the calcium indicator (GCaMP6s) and calcium signaling itself, which introduce slower temporal kinetics independent of processing delays. Newer variants, such as GCaMP8f, offer faster response times and could further reduce effective biological latency in future implementations.

With respect to hardware, we acknowledge that Raspberry Pi provides a low-cost solution but contributes to modest computational delays, while Nvidia Jetson offers faster inference at higher cost. Our choice reflects a balance between accessibility, cost-effectiveness, and performance, making the system deployable in many laboratories. Importantly, the modular and open-source design means the pipeline can readily be adapted to higher-performance GPUs or integrated with electrophysiological recordings, which provide higher temporal resolution. Finally, we agree with the reviewer that the issue of latency highlights deeper and interesting questions regarding the temporal requirements of behavior classification. Specifically, how much data (in time) is required to reliably identify a behavior, and what is the minimum feedback delay necessary to alter neural or behavioral trajectories? These are critical questions for the design of future closed-loop systems and ones that our work helps frame.

We have added a slightly modified version of our response above in the discussion section under “Experimental applications and implications”.

(3) Neurofeedback Specificity: The task focuses on mesoscale imaging and ignores finer spatiotemporal details. Sub-second events might be significant in more nuanced behaviors. Can this be discussed in the discussion section?

This is a great point  and we have added the following to the discussion section. “In the case of CLNF we have focused on regional cortical GCAMP signals that are relatively slow in kinetics. While such changes are well suited for transcranial mesoscale imaging assessment, it is possible that cellular 2-photon imaging (Yu et al. 2021) or preparations that employ cleared crystal skulls (Kim et al. 2016) could resolve more localized and higher frequency kinetic signatures.”

(4) The activity over 6s is being averaged to determine if the threshold is being crossed before the reward is delivered. This is a rather long duration of time during which the mice may be exhibiting stereotyped behaviors that may result in the changes in DFF that are being observed. It would be interesting for the authors to compare (if data is available) the behavior of the mice in trials where they successfully crossed the threshold for reward delivery and in those trials where the threshold was not breached. How is this different from spontaneous behavior and behaviors exhibited when they are performing the test with CLNF? 

We would like to emphasize that we are not directly averaging activity over 6 s to compare against the reward threshold. Instead, the preceding 6 s of activity is used solely to compute a dynamic baseline for ΔF/F₀ ( ΔF/F₀ = (F –F₀ )/F₀). Here, F₀is calculated as the mean fluorescence intensity over the prior 6 s window and is updated continuously throughout the session. This baseline is then subtracted from the instantaneous fluorescence signal to detect relative changes in activity. The reward threshold is therefore evaluated against these baseline-corrected ΔF/F₀ values at the current time point, not against an average over 6 s. This moving-window baseline correction is a standard approach in calcium imaging analyses, as it helps control for slow drifts in signal intensity, bleaching effects, or ongoing fluctuations unrelated to the behavior of interest. Thus, the 6-s window is not introducing a temporal lag in reward assignment but is instead providing a reference to detect rapid increases in cortical activity.  We have added the term dynamic baseline to the Methods to clarify.

Recommendations for the authors

Reviewer #1 (Recommendations for the authors):

Additional suggestions for improved or additional experiments, data or analyses.

For: "Looking closely at their reward rate on day 5 (day of rule change), they had a higher reward rate in the second half of the session as compared to the first half, indicating they were adapting to the rule change within one session." It would be helpful to see this data, and would be good to see within-session learning on the rule change day

Thank you for pointing this out. We had missed referencing the figure in the text, and have now added a citation to Supplementary Figure 4A, which shows the cumulative rewards for each day of training. As seen in the plot for day 5, the cumulative rewards are comparable to those on day 1, with most rewards occurring during the second half of the session.

For: "These results suggest that motor learning led to less cortical activation across multiple regions, which may reflect more efficient processing of movement-related activity," it could also be the case that the behaviour became more stereotyped over learning, which would lead to more concentrated, correlated activity. To test this, it would be good to look at the limb variability across sessions. Similarly, if it is movement-related, there should be good decoding of limb kinematics.

Indeed, we observed that behavior became more stereotyped over the course of learning, as shown in Supplementary Figure 4C, 4D. One plausible explanation for the reduction in cortical activation across multiple regions is that behavior itself became more stereotyped, a possibility we have explored in the manuscript. Specifically, forelimb movements during the trial became increasingly correlated as mice improved on the task, particularly in the groups that received auditory feedback (Rule-change and No-rule-change groups; Figure 8). As movements became more correlated, overall body movements during trials decreased and aligned more closely with the task rule (Figure 9D). This suggests that reduced cortical activity may in part reflect changes in behavior. Importantly, however, in the Rule-change group, we observed that on the day of the rule switch (day 5), when the target shifted from the left to the right forelimb, cortical activity increased bilaterally (Figure 9A–C). This finding highlights our central point: groups that received feedback (Rule-change and No-rule-change) were able to identify the task rule more effectively, and both their behavior and cortical activity became more specifically aligned with the rule compared to the No-feedback group. We agree with the reviewers that additional analyses along these lines would be valuable future directions. To facilitate this, we have included the movement data for readers who may wish to pursue further analyses, details can be found under “Data and code availability” in Methods section. However, given the limited sample sizes in our dataset and the need to keep the manuscript focused on the central message, we felt that including these additional analyses here would risk obscuring the main findings.

For: "We believe the decrease in ΔF/F0peak is unlikely to be driven by changes in movement, as movement amplitudes did not decrease significantly during these periods (Figure 7D CLMF Rule-change)." I would formally compare the two conditions. This is an important control. Also, another way to see if the change in deltaF is related to movement would be to see if you can predict movement from the deltaF.

Figure 7D in the previous version is Figure 9D in the current revision of the manuscript. We've assessed this for the examples shown based on graphing the movement data, unfortunately there is not enough of that data to do a group analysis of movement magnitude. We would suggest that this would be an excellent future direction that would take advantage of the flexible open source nature of our tool.

Recommendations for improving the writing and presentation.

In the abstract there is no mention of the rationale for the project, or the resulting significance. I would modify this to increase readership by the behavioral neuroscience community. Similarly, the introduction also doesn't highlight the value of this resource for the field. Again, I think the pyControl paper does a good job of this. For readability, I would add more subheadings earlier in the results, to separate the different technical aspects of the system.

We have revised the introduction to include the rationale for the project, its potential implications, and its relevance for translational research. We have also framed the work within the broader context of the behavioral and systems neuroscience community. We greatly appreciate this suggestion, as we believe it enhances the clarity and accessibility of the manuscript for the community.

For: "While brain activity can be controlled through feedback, other variables such as movements have been less studied, in part because their analysis in real time is more challenging." I would highlight research that has studied the control of behavior through feedback, such as the Mathis paper where mice learn to pull a joystick to a virtual box, and adapt this motion to a force perturbation.

We have added a citation to the Mathis paper and describe this as an additional form of feedback. The text is quoted below:

“Opportunities also exist in extending real time pose classification (Forys et al. 2020; Kane et al. 2020) and movement perturbation (Mathis et al. 2017) to shape aspects of an animal’s motor repertoire.”

Some of the results content would be better suited for the methods, one example: "A previous version of the CLNF system was found to have non-linear audio generation above 10 kHz, partly due to problems in the audio generation library and partly due to the consumer-grade speaker hardware we were employing. This was fixed by switching to the Audiostream (https://github.com/kivy/audiostream) library for audio generation and testing the speakers to make sure they could output the commanded frequencies"

This is now moved to the Methods section.

For: "There are reports of cortical plasticity during motor learning tasks, both at cellular and mesoscopic scales (17-19), supporting the idea that neural efficiency could improve with learning," not sure I agree with this, the studies on cortical plasticity are usually to show a neural basis for the learning observed, efficiency is separate from this.

We have modified this statement to remove the concept of efficiency "There are reports of cortical plasticity during motor learning tasks, both at cellular and mesoscopic scales (17-19).”

The paragraph that opens "Distinct task- and reward-related cortical dynamics" that describes the experiment should appear in the previous section, as the data is introduced there.

We have moved the mentioned paragraphs in the previous section where we presented the data and other experiment details. This makes the text more readable and contextual.

I would present the different ROI rules with better descriptors and visualization to improve the readability.

We have added Supplementary Figure 7, which provides visualizations of the ROIs across all task rules used in the CLNF experiments.

Minor corrections to the text and figures.

Figure 1 is a little crowded, combining the CLNF and CLMF experiments, I would turn this into a 2 panel figure, one for each, similar to how you did figure 2.

We have revised Figure 1 to include two panels, one for CLNF and one for CLMF. The colored components indicate elements specific to each setup, while the uncolored components represent elements shared between CLNF and CLMF. Relevant text in the manuscript is updated to refer to these figures.

For Figure 2, the organization of the CLMF section is not intuitive for the reader. I would reorder it so it has a similar flow as the CLNF experiment.

We have revised the figure by updating the layout of panel B (CLMF) to align with panel A (CLNF), thereby creating a more intuitive and consistent flow between the panels. We appreciate this helpful suggestion, which we believe has substantially improved the clarity of the figure. The corresponding text in the manuscript has also been updated to reflect these changes.

For Figure 3, highlight that C and E are examples. They also seem a little out of place, so they could even be removed.

We have now explicitly labeled Figures 3C and 3E as representative examples (figure legend and on figure itself). We believe including these panels provides helpful context for readers: Figure 3C illustrates how the ROIs align on the dorsal cortical brain map with segmented cortical regions, while Figure 3E shows example paw trajectories in three dimensions, allowing visualization of the movement patterns observed during the trials.

In the plots, I would add sample sizes, for instance, in CLNF learning curve in Figure 4A, how many animals are in each group? 

We have labeled Figure 4 with number of animals used in CLNF (No-rule-change, N=23; Rule-change, N=17), and CLMF (Rule-change, N=8; No-rule-change, N=4; No-feedback, N=4).

Also, Figure 7 for example, which figures are single-sessions, versus across animals? For Figure 7c, what time bin is the data taken from?

We have clarified this now and mentioned it in all the figures. Figure 7 in the previous version is Figure 9 in the current updated manuscript. Figure 9A is from individual sessions on different days from the same mouse. Figure 9B is the group average reward centered ΔF/F₀ activity in different cortical regions (Rule-change, N=8; No-rule-change, N=4; No-feedback, N=4). Figure 9C shows average ΔF/F₀ peak values obtained within -1sec to +1sec centered around the reward point (N=8).

It says "punish" in Figure 3, but there is no punishment?

Yes, the task did not involve punishment. Each trial resulted in either a success, which is followed by a reward, or a failure, which is followed by a buzzer sound. To better reflect these outcomes, we have updated Figure 3 and replaced the labels “Reward” with “Success” and “Punish” with “Failure.”

The regression on 5c doesn't look quite right, also this panel is not mentioned in the text.

The figure referred to by the reviewer as Figure 5 is now presented as Figure 6 in the revised manuscript. Regarding the reviewer’s observation about the regression line in the left panel of Figure 5C, the apparent misalignment arises because the majority of the data points are densely clustered at the center of the scatter plot, where they overlap substantially. The regression line accurately reflects this concentration of overlapping data. To improve clarity, we have updated the figure and ensured that it is now appropriately referenced in the Results section.

Reviewer #2 (Recommendations for the authors):

(1) There would be many interesting observations and links between the peripheral and cortical studies if there was a body video available during the cortical study. Is there any such data available?

We agree that a detailed analysis of behavior during the CLNF task would be necessary to explore any behavior correlates with success in the task. Unfortunately, we do not have a sufficient video of the whole body to perform such an analysis.

(2) The text (p. 24) states: [intracortical GCAMP transients measured over days became more stereotyped in kinetics and were more correlated (to each other) as the task performance increased over the sessions (Figure 7E).] But I cannot find this quantification in the figures or text?

Figure 7 in the previous version of the manuscript now appears as Figure 9. In this figure, we present cortical activity across selected regions during trials, and in Figure 9E we highlight that this activity becomes more correlated. Since we did not formally quantify variability, we have removed the previous claim that the activity became stereotyped and revised the text in the updated manuscript accordingly.

Typos:

10-serest c (page 13)

Inverted color codes in figure 4E vs F

Reviewer #3 (Recommendations for the authors):

We have mostly attempted to limit the feedback to suggestions and posed a few questions that might be interesting to explore given the dataset the authors have collected.

Comments:

In close loop systems the latency is primary concern, and authors have successfully tested the latency of the system (Delay): from detection of an event to the reaction time was less than 67ms.

We have commented on the issues and limitations caused by latency, and potential future directions to overcome these challenges in responses to some of the previous comments.

Additional major comments:

"In general, all ROIs assessed that encompassed sensory, pre-motor, and motor areas were capable of supporting increased reward rates over time (Figure 4A, Animation 1)." Fig 4A is merely showing change in task performance over time and does not have information regarding the changes observed specific to CLNF for each ROI.

We acknowledge that the sample size for individual ROI rules was not sufficient for meaningful comparisons. To address this limitation, we pooled the data across all the rules tested. The manuscript includes a detailed list of the rules along with their corresponding sample sizes for transparency.

A ΔF/F₀ threshold value was calculated from a baseline session on day 0 that would have allowed 25% performance. Starting from this basal performance of around 25% on day 1, mice (CLNF No-rule-change, n=28 and CLNF Rule-change, n=13). It is unclear what the replicates here are. Trials or mice? The corresponding Figure legend has a much smaller n value.

Thank you for pointing this out. We realized that we had not indicated the sample replicates in the figure, and the use of n instead of N for the number of animals may have been misleading. We have now corrected the notation and clarified this information in the figure to resolve the discrepancy.

What were the replicates for each ROI pairs evaluated?

Each ROI rule and number of mice and trials are listed in Table 5 and Table 6.

Our analysis revealed that certain ROI rules (see description in methods) lead to a greater increase in success rate over time than others (Supplementary Figure 3D). The Supplementary figures 3C and 3D are blurry and could use higher resolution images. 

We have increased the font size of the text that was previously difficult to read and re-exported the figure at a higher resolution (300 DPI). We believe these changes will resolve the issue.

Also, It will help the reader is a visual representation of the ROI pairs are provided, instead of the text view. One interesting question is whether there are anatomical biases to fast vs slow learning pairs (Directionality - anterior/posterior, distance between the selected ROIs etc). This could be interesting to tease apart.

We have added Supplementary Figure 7, which provides visualizations of the ROIs across all task rules used in the CLNF experiments. While a detailed investigation of the anatomical basis of fast versus slow learning cortical ROIs is beyond the scope of the present study, we agree that this represents an exciting future direction for further research.

How distant should the ROIs be to achieve increased task performance?

We appreciate this insightful question. We did not specifically test this scenario. In our study, we selected 0.3 × 0.3 mm ROIs centered on the standard AIBS mouse brain atlas (CCF). At this resolution, ROIs do not overlap, regardless of their placement in a two-ROI experiment. Furthermore, because our threshold calculations are based on baseline recordings, we expect the system would function for any combination of ROI placements. Nonetheless, exploring this systematically would be an interesting avenue for future experiments.

Figures:

I would leave out some of the methodological details such as the protocol for water restriction (Fig. 3) out of the legend. This will help with readability.

We have removed some of the methodological details, including those mentioned above, from the legend of Figure 3 in the updated manuscript.

Fig 1 and Fig 2: In my opinion, It would be easier for the reader if the current Fig. 2, which provides a high level description of CLNF and CLBF is presented as Fig. 1. The current Fig. 1, goes into a lot of methodological implementation details, and also includes a lot of programming jargon that is being introduced early in the paper that is hard to digest early on in the paper's narrative.

Thank you for the suggestion. In the new manuscript, Figure 1 and Figure 2 have been swapped.

Higher-resolution images/ plots are needed in many instances. Unsure if this is the pdf compression done by the manuscript portal that is causing this.

All figures were prepared in vector graphics format using the open-source software Inkscape. For this manuscript, we exported the images at 300 DPI, which is generally sufficient for publication-quality documents. The submission portal may apply additional processing, which could have resulted in a reduction in image quality. We will carefully review the final submission files and ensure that all figures are clear and of high quality.

The authors repeatedly show ROI specific analysis M1_L, F1_R etc. It will be helpful to provide a key, even if redundant in all figures to help the reader.

We have now included keys to all such abbreviations in all the figures.

There are also instances of editorialization and interpretation e.g., "Surprisingly, the "Rule-change" mice were able to discover the change in rule and started performing above 70% within a day of the rule change, on day 6" that would be more appropriate in the main body of the paper.

Thank you for pointing this out in the figure legend, and we have removed it now since we already discussed this in the Results.

Minor comments

(1) The description of Figure 1 is hard to follow and can be described better based on how the information is processed and executed in the system from source to processing and back. Using separated colors (instead of shaded of grey) for the neuro feedback and movement feedback would help as well. Common components could have a different color. The specification like the description of the config file should come later.

Figure 1 in the previous version is Figure 2 in the updated version. We have taken suggestions from other reviewers and made the figure easier to understand and split it into two panels with color coding Green for CLNF, Pink for CLMF specific parts while common shared parts are left without any color.

(2) Page 20 last paragraph:

Authors are neglecting that the rule change is done one day prior and the results that you see in the second half on the 6th day are not just because of the first half of the 6th day instead combined training on the 5th day (rule change) and then the first half of the 6th day. Rephrasing this observation is essential.

We have revised the text for clarity to indicate that the performance increase observed on day 6 is not necessarily attributable to training on that day. In fact, we noted and mentioned that mice began to perform the task better during the second half of the session on day 5 itself.

(3)  The method section description of the CLMF setup (Page no 39 first paragraph) is more detailed, a diagram of this setup would make it easy to follow and a better read.

We have made changes to the CLMF setup (Figure 1B) and CLMF schematic (Figure 2B) to make it easier to understand parts of the setup and flow of control.

Author response:

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

Public Reviews:  

Reviewer #1 (Public review):  

Summary:  

The image analysis pipeline is tested in analysing microscopy imaging data of gastruloids of varying sizes, for which an optimised protocol for in toto image acquisition is established based on whole mount sample preparation using an optimal refractive index matched mounting media, opposing dual side imaging with two-photon microscopy for enhanced laser penetration, dual view registration, and weighted fusion for improved in toto sample data representation. For enhanced imaging speed in a two-photon microscope, parallel imaging was used, and the authors performed spectral unmixing analysis to avoid issues of signal cross-talk.  

In the image analysis pipeline, different pre-treatments are done depending on the analysis to be performed (for nuclear segmentation - contrast enhancement and normalisation; for quantitative analysis of gene expression - corrections for optical artifacts inducing signal intensity variations). Stardist3D was used for the nuclear segmentation. The study analyses into properties of gastruloid nuclear density, patterns of cell division, morphology, deformation, and gene expression.  

Strengths:  

The methods developed are sound, well described, and well-validated, using a sample challenging for microscopy, gastruloids. Many of the established methods are very useful (e.g. registration, corrections, signal normalisation, lazy loading bioimage visualisation, spectral decomposition analysis), facilitate the development of quantitative research, and would be of interest to the wider scientific community.

We thank the reviewer for this positive feedback.

Weaknesses:  

A recommendation should be added on when or under which conditions to use this pipeline. 

We thank the reviewer for this valuable feedback, we added the text in the revised version, ines 418 to 474. “In general, the pipeline is applicable to any tissue, but it is particularly useful for large and dense 3D samples—such as organoids, embryos, explants, spheroids, or tumors—that are typically composed of multiple cell layers and have a thickness greater than 50 µm”.

“The processing and analysis pipeline are compatible with any type of 3D imaging data (e.g. confocal, 2 photon, light-sheet, live or fixed)”.

“Spectral unmixing to remove signal cross-talk of multiple fluorescent targets is typically more relevant in two-photon imaging due to the broader excitation spectra of fluorophores compared to single-photon imaging. In confocal or light-sheet microscopy, alternating excitation wavelengths often circumvents the need for unmixing. Spectral decomposition performs even better with true spectral detectors; however, these are usually not non-descanned detectors, which are more appropriate for deep tissue imaging. Our approach demonstrates that simultaneous cross-talk-free four-color two-photon imaging can be achieved in dense 3D specimen with four non-descanned detectors and co-excitation by just two laser lines. Depending on the dispersion in optically dense samples, depth-dependent apparent emission spectra need to be considered”.

“Nuclei segmentation using our trained StarDist3D model is applicable to any system under two conditions: (1) the nuclei exhibit a star-convex shape, as required by the StarDist architecture, and (2) the image resolution is sufficient in XYZ to allow resampling. The exact sampling required is object- and system-dependent, but the goal is to achieve nearly isotropic objects with diameters of approximately 15 pixels while maintaining image quality. In practice, images containing objects that are natively close to or larger than 15 pixels in diameter should segment well after resampling. Conversely, images with objects that are significantly smaller along one or more dimensions will require careful inspection of the segmentation results”.

“Normalization is broadly applicable to multicolor data when at least one channel is expected to be ubiquitously expressed within its domain. Wavelength-dependent correction requires experimental calibration using either an ubiquitous signal at each wavelength. Importantly, this calibration only needs to be performed once for a given set of experimental conditions (e.g., fluorophores, tissue type, mounting medium)”.

“Multi-scale analysis of gene expression and morphometrics is applicable to any 3D multicolor image. This includes both the 3D visualization tools (Napari plugins) and the various analytical plots (e.g., correlation plots, radial analysis). Multi-scale analysis can be performed even with imperfect segmentation, as long as segmentation errors tend to cancel out when averaged locally at the relevant spatial scale. However, systematic errors—such as segmentation uncertainty along the Z-axis due to strong anisotropy—may accumulate and introduce bias in downstream analyses. Caution is advised when analyzing hollow structures (e.g., curved epithelial monolayers with large cavities), as the pipeline was developed primarily for 3D bulk tissues, and appropriate masking of cavities would be needed”.

Reviewer #2 (Public review):  

Summary:  

This study presents an integrated experimental and computational pipeline for high-resolution, quantitative imaging and analysis of gastruloids. The experimental module employs dual-view two-photon spectral imaging combined with optimized clearing and mounting techniques to image whole-mount immunostained gastruloids. This approach enables the acquisition of comprehensive 3D images that capture both tissue-scale and single-cell level information.  

The computational module encompasses both pre-processing of acquired images and downstream analysis, providing quantitative insights into the structural and molecular characteristics of gastruloids. The pre-processing pipeline, tailored for dual-view two-photon microscopy, includes spectral unmixing of fluorescence signals using depth-dependent spectral profiles, as well as image fusion via rigid 3D transformation based on content-based block-matching algorithms. Nuclei segmentation was performed using a custom-trained StarDist3D model, validated against 2D manual annotations, and achieving an F1 score of 85+/-3% at a 50% intersection-over-union (IoU) threshold. Another custom-trained StarDist3D model enabled accurate detection of proliferating cells and the generation of 3D spatial maps of nuclear density and proliferation probability. Moreover, the pipeline facilitates detailed morphometric analysis of cell density and nuclear deformation, revealing pronounced spatial heterogeneities during early gastruloid morphogenesis.  

All computational tools developed in this study are released as open-source, Python-based software.  

Strengths:  

The authors applied two-photon microscopy to whole-mount deep imaging of gastruloids, achieving in toto visualization at single-cell resolution. By combining spectral imaging with an unmixing algorithm, they successfully separated four fluorescent signals, enabling spatial analysis of gene expression patterns.  

The entire computational workflow, from image pre-processing to segmentation with a custom-trained StarDist3D model and subsequent quantitative analysis, is made available as open-source software. In addition, user-friendly interfaces are provided through the open-source, community-driven Napari platform, facilitating interactive exploration and analysis.

We thank the reviewer for this positive feedback.

Weaknesses:  

The computational module appears promising. However, the analysis pipeline has not been validated on datasets beyond those generated by the authors, making it difficult to assess its general applicability.

We agree that applying our analysis pipeline to published datasets—particularly those acquired with different imaging systems—would be valuable. However, only a few high-resolution datasets of large organoid samples are publicly available, and most of these either lack multiple fluorescence channels or represent 3D hollow structures. Our computational pipeline consists of several independent modules: spectral filtering, dual-view registration, local contrast enhancement, 3D nuclei segmentation, image normalization based on a ubiquitous marker, and multiscale analysis of gene expression and morphometrics. We added the following sentences to the Discussion, lines 418 to 474, and completed the discussion on applicability with a table showing the purpose, requirements, applicability and limitations of each step of the processing and analysis pipeline.

“Spectral filtering has already been applied in other systems (e.g. [7] and [8]), but is here extended to account for imaging depth-dependent apparent emission spectra of the different fluorophores. In our pipeline, we provide code to run spectral filtering on multichannel images, integrated in Python. In order to apply the spectral filtering algorithm utilized here, spectral patterns of each fluorophore need to be calibrated as a function of imaging depth, which depend on the specific emission windows and detector settings of the microscope”.

“Image normalization using a wavelength-dependent correction also requires calibration on a given imaging setup to measure the difference in signal decay among the different fluorophores species. To our knowledge, the calibration procedures for spectral-filtering and our image-normalization approach have not been performed previously in 3D samples, which is why validation on published datasets is not readily possible. Nevertheless, they are described in detail in the Methods section, and the code used—from the calibration measurements to the corrected images—is available open-source at the Zenodo link in the manuscript”.

Dual-view registration, local contrast enhancement, and multiscale analysis of gene expression and morphometrics are not limited to organoid data or our specific imaging modalities. To evaluate our 3D nuclei segmentation model, we tested it on diverse systems, including gastruloids stained with the nuclear marker Draq5 from Moos et al. [1]; breast cancer spheroids; primary ductal adenocarcinoma organoids; human colon organoids and HCT116 monolayers from Ong et al. [2]; and zebrafish tissues imaged by confocal microscopy from Li et al [3]. These datasets were acquired using either light-sheet or confocal microscopy, with varying imaging parameters (e.g., objective lens, pixel size, staining method). The results are added in the manuscript, Fig. S9b.

Besides, the nuclei segmentation component lacks benchmarking against existing methods.  

We agree with the reviewer that a benchmark against existing segmentation methods would be very useful. We tried different pre-trained models:

CellPose, which we tested in a previous paper ([4]) and which showed poor performances compared to our trained StarDist3D model.

DeepStar3D ([2]) is only available in the software 3DCellScope. We could not benchmark the model on our data, because the free and accessible version of the software is limited to small datasets. An image of a single whole-mount gastruloid with one channel, having dimensions (347,467,477) was too large to be processed, see screenshot below. The segmentation model could not be extracted from the source code and tested externally because the trained DeepStar3D weights are encrypted.

Author response image 1.

Screenshot of the 3DCellScore software. We could not perform 3D nuclei segmentation of a whole-mount gastruloids because the image size was too large to be processed.

AnyStar ([5]), which is a model trained from the StarDist3D architecture, was not performing well on our data because of the heterogeneous stainings. Basic pre-processing such as median and gaussian filtering did not improve the results and led to wrong segmentation of touching nuclei. AnyStar was demonstrated to segment well colon organoids in Ong et al, 2025 ([2]), but the nuclei were more homogeneously stained. Our Hoechst staining displays bright chromatin spots that are incorrectly labeled as individual nuclei.

Cellos ([6]), another model trained from StarDist3D, was also not performing well. The objects used for training and to validate the results are sparse and not touching, so the predicted segmentation has a lot of false negatives even when lowering the probability threshold to detect more objects. Additionally, the network was trained with an anisotropy of (9,1,1), based on images with low z resolution, so it performed poorly on almost isotropic images. Adapting our images to the network’s anisotropy results in an imprecise segmentation that can not be used to measure 3D nuclei deformations.

We tried both Cellos and AnyStar predictions on a gastruloid image from Fig. S2 of our main manuscript.  The results are added in the manuscript, Fig. S9b. Fig3 displays the results qualitatively compared to our trained model Stardist-tapenade.

Author response image 2.

Qualitative comparison of two published segmentation models versus our model. We show one slice from the XY plane for simplicity. Segmentations are displayed with their contours only. (Top left) Gastruloid stained with Hoechst, image extracted from Fig S2 of our manuscript. (Top right) Same image overlayed with the prediction from the Cellos model, showing many false negatives. (Bottom left) Same image overlayed with the prediction from our Stardist-tapenade model. (Bottom right) Same image overlayed with the prediction from the AnyStar model, false positives are indicated with a red arrow.

CellPose-SAM, which is a recent model developed building on the CellPose framework. The pre-trained model performs well on gastruloids imaged using our pipeline, and performs better than StarDist3D at segmenting elongated objects such as deformed nuclei. The performances are qualitatively compared on Fig. S9a and S10.  We also demonstrate how using local contrast enhancement improves the results of CellPose-SAM (Fig. S10a), showing the versatility of the Tapenade pre-processing module. Tissue-scale, packing-related metrics from Cellpose–SAM labels qualitatively match those from stardist-tapenade as shown Fig.10c and d.

Appraisal:  

The authors set out to establish a quantitative imaging and analysis pipeline for gastruloids using dual-view two-photon microscopy, spectral unmixing, and a custom computational framework for 3D segmentation and gene expression analysis. This aim is largely achieved. The integration of experimental and computational modules enables high-resolution in toto imaging and robust quantitative analysis at the single-cell level. The data presented support the authors' conclusions regarding the ability to capture spatial patterns of gene expression and cellular morphology across developmental stages.  

Impact and utility:  

This work presents a compelling and broadly applicable methodological advance. The approach is particularly impactful for the developmental biology community, as it allows researchers to extract quantitative information from high-resolution images to better understand morphogenetic processes. The data are publicly available on Zenodo, and the software is released on GitHub, making them highly valuable resources for the community.  

We thank the reviewer for these positive feedbacks.

Reviewer #3 (Public review):

Summary  

The paper presents an imaging and analysis pipeline for whole-mount gastruloid imaging with two-photon microscopy. The presented pipeline includes spectral unmixing, registration, segmentation, and a wavelength-dependent intensity normalization step, followed by quantitative analysis of spatial gene expression patterns and nuclear morphometry on a tissue level. The utility of the approach is demonstrated by several experimental findings, such as establishing spatial correlations between local nuclear deformation and tissue density changes, as well as the radial distribution pattern of mesoderm markers. The pipeline is distributed as a Python package, notebooks, and multiple napari plugins.  

Strengths  

The paper is well-written with detailed methodological descriptions, which I think would make it a valuable reference for researchers performing similar volumetric tissue imaging experiments (gastruloids/organoids). The pipeline itself addresses many practical challenges, including resolution loss within tissue, registration of large volumes, nuclear segmentation, and intensity normalization. Especially the intensity decay measurements and wavelength-dependent intensity normalization approach using nuclear (Hoechst) signal as reference are very interesting and should be applicable to other imaging contexts. The morphometric analysis is equally well done, with the correlation between nuclear shape deformation and tissue density changes being an interesting finding. The paper is quite thorough in its technical description of the methods (which are a lot), and their experimental validation is appropriate. Finally, the provided code and napari plugins seem to be well done (I installed a selected list of the plugins and they ran without issues) and should be very helpful for the community.

We thank the reviewer for his positive feedback and appreciation of our work.

Weaknesses  

I don't see any major weaknesses, and I would only have two issues that I think should be addressed in a revision:  

(1) The demonstration notebooks lack accompanying sample datasets, preventing users from running them immediately and limiting the pipeline's accessibility. I would suggest to include (selective) demo data set that can be used to run the notebooks (e.g. for spectral unmixing) and or provide easily accessible demo input sample data for the napari plugins (I saw that there is some sample data for the processing plugin, so this maybe could already be used for the notebooks?).  

We thank the reviewer for this relevant suggestion. The 7 notebooks were updated to automatically download sample tests. The different parts of the pipeline can now be run immediately:

https://github.com/GuignardLab/tapenade/tree/chekcs_on_notebooks/src/tapenade/notebooks

(2) The results for the morphometric analysis (Figure 4) seem to be only shown in lateral (xy) views without the corresponding axial (z) views. I would suggest adding this to the figure and showing the density/strain/angle distributions for those axial views as well.

A morphometric analysis based on the axial views was added as Fig. S6a of the manuscript, complementary to the XY views.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):  

In lines 64 and 65, it is mentioned that confocal and light-sheet microscopy remain limited to samples under 100μm in diameter. I would recommend revising this sentence. In the paper of Moos and colleagues (also cited in this manuscript; PMID: 38509326), gastruloid samples larger than 100μm are imaged in toto with an open-top dual-view and dual-illumination light-sheet microscope, and live cell behaviour is analysed. Another example, if considering also multi-angle systems, is the impressive work of McDole and colleagues (PMID: 30318151), in which one of the authors of this manuscript is a corresponding author. There, multi-angle light sheet microscopy is used for in toto imaging and reconstruction of post-implantation mouse development (samples much larger than 100μm). Some multi-sample imaging strategies have been developed for this type of imaging system, though not to the sample number extent allowed by the Viventis LS2 system or the Bruker TruLive3D imager, which have higher image quality limitations.

We thank the reviewer for this remark. As reported in their paper, Moos et al. used dual-view light-sheet microscopy to image gastruloids, which are particularly dense and challenging tissues, with whole-mount samples of approximately 250 µm in diameter. Nevertheless, their image quality metric (DCT) shows a rapid twofold decrease within 50 µm depth (Extended Fig 5.h), whereas with two-photon microscopy, our image quality metric (FRC-QE) decreases by a factor of two over 150 µm in non-cleared samples (PBS) (see Fig. 2 c). While these two measurements (FRC-QE versus DCT) are not directly comparable, the observed difference reflects the superior depth performance of two-photon microscopy, owing in part to the use of non-descanned detectors. In our case, imaging was performed with Hoechst, a blue fluorophore suboptimal for deep imaging, whereas in the Moos dataset (Draq5, far-red), the configuration was more favorable for imaging in depth  which further supports our conclusion.

In McDole et al, tissues reaching 250µm were imaged from 4 views, but do not reach cellular-scale resolution in deeper layers compatible with cell segmentation to our knowledge.

We corrected the sentence ‘However, light-sheet and confocal imaging approaches remain limited to relatively small organoids typically under 100 micrometers in diameter ‘ by the following (line 64) :

“While advances in light-sheet microscopy have extended imaging depth in organoids, maintaining high image quality throughout thick samples remains challenging. In practice, quantitative analyses are still largely restricted to organoids under roughly 100 µm in diameter”.

It is worth mentioning that two-photon microscopes are much more widely available than light sheet microscopes, and light sheet systems with 2-photon excitation are even less accessible, which makes the described workflow of Gros and colleagues have a wide community interest.  

We thank the reviewer for this remark, and added this suggestion line 74:

“Finally, two-photon microscopes are typically more accessible than light-sheet systems and allow for straightforward sample mounting, as they rely on procedures comparable to standard confocal imaging”.

Reviewer #2 (Recommendations for the authors):  

Suggestions:  

A comparison with established pre-trained models for 3D organoid image segmentation (e.g., Cellos[1], AnyStar[2], and DeepStar3D[3], all based on StarDist3D) would help highlight the advantages of the authors' custom StarDist3D model, which has been specifically optimized for two-photon microscopy images.  

(1)  Cellos: https://doi.org/10.1038/s41467-023-44162-6

(2)  AnyStar: https://doi.org/10.1109/WACV57701.2024.00742

(3)  DeepStar3D: https://doi.org/10.1038/s41592-025-02685-4

We agree with the reviewer that a benchmark against existing segmentation methods is very useful. This is addressed in the revised version, as detailed above (Figure 3).

Recommendations:  

Please clarify the following point. In line 195, the authors state, "This allowed us to detect all mitotic nuclei in whole-mount samples for any stage and size." Does this mean that the custom-trained StarDist3D model can detect 100% of mitotic nuclei? It was not clear from the manuscript, figures, or videos how this was validated. Given the reported performance scores of the StarDist3D model for detecting all nuclei, claiming 100% detection of mitotic nuclei seems surprisingly high.

We thank the reviewer for this comment. As it was detailed in the methods section, the detection score reaches 82%, and only the complete pipeline (detection+minimal manual curation) allows us to detect all mitotic nuclei. To make it clearer, the following precisions were added in the Results section:

”To detect division events, we stained gastruloids with phosphohistone H3 (ph3) and trained a separate custom Stardist3D model using 3D annotations of nuclei expressing ph3 (see Methods III H). This model together allowed us to detect nearly all mitotic nuclei in whole-mount samples for any stage and size (Fig.3f and Suppl.Movie 4), and we used minimal manual curation to correct remaining errors.”

Minor corrections:  

It appears that Figures 4-6 are missing from the submitted version, but they can be found in the manuscript available on bioRxiv.

We thank the reviewer for this remark, this was corrected immediately to add Figures 4 to 6.

In line 185, is the intended phrase "by comparing the 2D predictions and the 2D sliced annotated segments..."? 

To gain some clarity, we replaced the initial sentence:

“The f1 score obtained by comparing the 3D prediction and the 3D ground-truth is well approximated by the f1 score obtained by comparing the 2D annotations and the 2D sliced annotated segments, with at most a 5% difference between the two scores.” by

“The f1 score obtained in 3D (3D prediction compared with the 3D ground-truth) is well approximated by the f1 score obtained in 2D (2D predictions compared with the 2D sliced annotated segments). The difference between the 2 scores was at most 5%.”

Reviewer #3 (Recommendations for the authors):

(1) How is the "local neighborhood volume" defined, and how was it computed?

The reviewer is referring to this paragraph (the term is underscored) :

“To probe quantities related to the tissue structure at multiple scales, we smooth their signal with a Gaussian kernel of width σ, with σ defined as the spatial scale of interest. From the segmented nuclei instances, we compute 3D fields of cell density (number of cells per unit volume), nuclear volume fraction (ratio of nuclear volume to local neighborhood volume), and nuclear volume at multiple scales.”

To improve clarity, the phrasing has been revised: the term local neighborhood volume has been replaced by local averaging volume, and a reference to the Methods section has been added.

From the segmented nuclei instances, we compute 3D fields of cell density (number of cells per unit volume), nuclear volume fraction (ratio of space occupied by nuclear volume within the local averaging volume, as defined in the Methods III I), and nuclear volume at multiple scales.

(2) In the definition of inertia tensor (18), isn't the inner part normally defined in the reversed way (delta_i,j - ...)?

We thank the reviewer for noticing this error, which we fixed in the manuscript.

(3) For intensity normalization, the paper uses the Hoechst signal density as a proxy for a ubiquitous nuclei signal. I would assume that this is problematic, for eg, dividing cells (which would overestimate it). Would using the average Hoechst signal per nucleus mask (as segmentation is available) be a better proxy?

We agree that this idea is appealing if one assumes a clear relationship between nuclear volume and Hoechst intensity. However, since cell and nuclear volumes vary substantially with differentiation state (see Fig. 4), such a normalization approach would introduce additional biases at large spatial scales. We believe that the most robust improvement would instead consist in masking dividing cells during the normalization procedure, as these events could be detected and excluded from the computation.

Nonetheless, we believe the method proposed by the reviewer could prove relevant for other types of data, so we will implement this recommendation in the code available in the Tapenade package.

(4) Figures 4-6 were part of the Supplementary Material, but should be included in the main text?

We thank the reviewer for this remark, this was corrected immediately to add Figures 4-6.

We also noticed a missing reference to Fig. S3 in the main text, so we added lines 302 to 307 to comment on the wavelength-dependency of the normalization method. We improved the description of Fig.6, which lacked clarity (line 316 to 321, line 327).

(1) Moos, F., Suppinger, S., de Medeiros, G., Oost, K.C., Boni, A., Rémy, C., Weevers, S.L., Tsiairis, C., Strnad, P. and Liberali, P., 2024. Open-top multisample dual-view light-sheet microscope for live imaging of large multicellular systems. Nature Methods, 21(5), pp.798-803.

(2) Ong, H. T.; Karatas, E.; Poquillon, T.; Grenci, G.; Furlan, A.; Dilasser, F.; Mohamad Raffi, S. B.; Blanc, D.; Drimaracci, E.; Mikec, D.; Galisot, G.; Johnson, B. A.; Liu, A. Z.; Thiel, C.; Ullrich, O.; OrgaRES Consortium; Racine, V.; Beghin, A. (2025). Digitalized organoids: integrated pipeline for high-speed 3D analysis of organoid structures using multilevel segmentation and cellular topology.  Nature Methods, 22(6), pp.1343-1354

(3) Li, L., Wu, L., Chen, A., Delp, E.J. and Umulis, D.M., 2023. 3D nuclei segmentation for multi-cellular quantification of zebrafish embryos using NISNet3D. Electronic Imaging, 35, pp.1-9.

(4) Vanaret, J., Dupuis, V., Lenne, P. F., Richard, F., Tlili, S., & Roudot, P. (2023). A detector-independent quality score for cell segmentation without ground truth in 3D live fluorescence microscopy. IEEE Journal of Selected Topics in Quantum Electronics, 29(4:Biophotonics), 1-12.

(5) Dey, N., Abulnaga, M., Billot, B., Turk, E. A., Grant, E., Dalca, A. V., & Golland, P. (2024). AnyStar: Domain randomized universal star-convex 3D instance segmentation. In Proceedings of the IEEE/CVF Winter Conference on Applications of Computer Vision (pp. 7593-7603).

(6) Mukashyaka, P., Kumar, P., Mellert, D. J., Nicholas, S., Noorbakhsh, J., Brugiolo, M., ... & Chuang, J. H. (2023). High-throughput deconvolution of 3D organoid dynamics at cellular resolution for cancer pharmacology with Cellos. Nature Communications, 14(1), 8406.

(7) Rakhymzhan, A., Leben, R., Zimmermann, H., Günther, R., Mex, P., Reismann, D., ... & Niesner, R. A. (2017). Synergistic strategy for multicolor two-photon microscopy: application to the analysis of germinal center reactions in vivo. Scientific reports, 7(1), 7101.

(8) Dunsing, V., Petrich, A., & Chiantia, S. (2021). Multicolor fluorescence fluctuation spectroscopy in living cells via spectral detection. Elife, 10, e69687.

protected

Configuration: System Settings / Keyboard / Keyboard Shortcuts / Keyboard / Move focus to next window

Speed Test Summary: Windows XP vs Vista vs 7 vs 8.1 vs 10 vs 11

Test Setup [00:00:00]

• Hardware: Older hardware used to ensure compatibility with older OS versions (XP/Vista) and to stress-test newer ones.
• OS Versions: All running Pro versions with the latest available updates; Windows XP is the 64-bit version.

Performance Tests

• Startup Speed [00:00:48]:
  • Winner: Windows 8.1 (fast boot advantage).
  • Surprise: Windows 10 and XP started at nearly the same time.
  • Loser: Windows 11 (struggled to load taskbar).
• Storage Footprint [00:02:13]:
  • Winner: Windows XP (least space used).
  • Heaviest: Windows 7 took up the most storage.
• RAM Management (Idle) [00:02:40]:
  • Winner: Windows XP (lowest usage).
  • Loser: Windows 11 (3.5–3.7 GB idle usage vs 2.3 GB for Windows 10).
• Web Browser Stress Test (Tab limit before 5GB usage) [00:03:29]:
  • Winners: Windows 7 and 8.1 (reached over 200 tabs).
  • Loser: Windows 11 (failed to reach 50 tabs due to high base usage).
  • Note: Windows XP crashed at 50 tabs due to virtual memory limits.
• Battery Life [00:04:49]:
  • Winner: Windows XP (pleasant surprise).
  • Runner-ups: Windows 10 (2nd), Windows 8.1 (3rd).
  • Loser: Windows 11 died first.
• Video Editing Rendering [00:06:08]:
  • Winner: Windows 10.
  • Runner-up: Windows 8.1.
  • Loser: Windows 11 (slowest).
• Application Launching (Explorer, Paint, Calc) [00:06:48]:
  • Trend: Older OS versions (8.1 and below) opened "classic" apps significantly faster.
  • Loser: Windows 11 showed significant delays, likely due to modern app rebuilds and mixed UI elements.
• File Transfer (USB to Disk) [00:08:41]:
  • Winner: Windows 10 (barely beat 11).
  • Trend: Newer OS versions generally faster than older ones here.
• Malware Scans [00:09:02]:
  • Winner: Windows 7 (fastest scan).
  • Loser: Windows 11 (took almost a minute longer than Win 10).

Benchmarks (Synthetic) [00:10:04]

• CPU-Z: Older OSs generally better in single-threaded; Windows 7 best in multi-threaded.
• Geekbench: Windows 10 best multi-core; Windows 11 best single-core.
• CrystalDiskMark: XP best read speeds; Windows 7/Vista performed poorly on reads.

Conclusion & Ranking [00:12:37]

Based on the "polish," "speed," and "stability" on older hardware as tested in the video:

1. Windows 8.1 (Praised as the most polished, fast, and stable).
2. Windows 10 (Performed consistently well, winning video editing and file transfers).
3. Windows 7 (Strong showing in RAM management and security scanning).
4. Windows XP (Excellent battery life and low resource usage, but limited by age/compatibility).
5. Windows Vista (Average performance, often lagging behind 7).
6. Windows 11 (Ranked last; described as "one of the slowest," with massive memory consumption).

Metaphor: Her eyelids will close like windows.

Description of the effects of the portion: She'll look dead: cold, no pulse, pale, stiff.

Symbolism: Darkness represents his depression. He's hiding from light/life.

I can see various characterizations, themes and stylistic devices, which I will discuss below

https://web.archive.org/web/20260105192105/https://www.office.com/

#2026/01/05 the day that Office was renamed to 'Microsoft 365 Copilot app' Meanwhile a billion PC owners are holding out on even Windows 11. [[Windows 10 is out of support, but 1 billion PCs still haven’t upgraded]] And MS CEO asks all to pretty please don't talk about slop or Microslop.... [[Microsoft CEO Begs Users to Stop Calling It Slop]]

Dell COO in q3 earnings call said 500 million PCs that could have not been upgraded to Windows 11, and 500 million PCs that couldn't are also still in operation on Windows 10. 1billion PCs thusfar not moving to Win11.

1 billion PCs still running Windows 10. Here seen as sign of resistance to Win 11 and AI slop

Selection

Harassment has intensified because technology allows anonymity, instant spread, and 24/7 access, so the government promotes education and safer reporting systems to combat this.

These guys ruined their Windows app by downgrading it to a laggy PWA, and it doesn't even let you customize notification channels anymore

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, Chengjian Zhao et al. focused on the interactions between vascular, biliary, and neural networks in the liver microenvironment, addressing the critical bottleneck that the lack of high-resolution 3D visualization has hindered understanding of these interactions in liver disease.

Strengths:

This study developed a high-resolution multiplex 3D imaging method that integrates multicolor metallic compound nanoparticle (MCNP) perfusion with optimized CUBIC tissue clearing. This method enables the simultaneous 3D visualization of spatial networks of the portal vein, hepatic artery, bile ducts, and central vein in the mouse liver. The authors reported a perivascular structure termed the Periportal Lamellar Complex (PLC), which is identified along the portal vein axis. This study clarifies that the PLC comprises CD34⁺Sca-1⁺ dual-positive endothelial cells with a distinct gene expression profile, and reveals its colocalization with terminal bile duct branches and sympathetic nerve fibers under physiological conditions.<br />

Weaknesses:

This manuscript is well-written, organized, and informative. However, there are some points that need to be clarified.

(1) After MCNP-dye injection, does it remain in the blood vessels, adsorb onto the cell surface, or permeate into the cells? Does the MCNP-dye have cell selectivity?

The experimental results showed that after injection, the MCNP series nanoparticles predominantly remained within the lumens of blood vessels and bile ducts, with their tissue distribution determined by physical perfusion. No diffusion of the dye signal into the surrounding parenchymal tissue was observed, nor was there any evidence of adsorption onto the cell surface or entry into cells. The newly added Supplementary Figure S2A–H further confirmed this feature, demonstrating that the dye signals were strictly confined to the luminal space, clearly delineating the continuous course of blood vessels and the branching morphology of bile ducts. These findings strongly support the conclusion that “MCNP dyes are distributed exclusively within the luminal compartments.”

Therefore, the MCNP dyes primarily serve as intraluminal tracers within the tissue rather than as labels for specific cell types.

(2) All MCNP-dyes were injected after the mice were sacrificed, and the mice's livers were fixed with PFA. After the blood flow had ceased, how did the authors ensure that the MCNP-dyes were fully and uniformly perfused into the microcirculation of the liver?

Thank you for the reviewer’s valuable comments. Indeed, since all MCNP dyes were perfused after the mice were euthanized and blood circulation had ceased, we cannot fully ensure a homogeneous distribution of the dye within the hepatic microcirculation. The vascular labeling technique based on metallic nanoparticle dyes used in this study offers clear imaging, stable fluorescence intensity, and multiplexing advantages; however, it also has certain limitations. The main issue is that the dye distribution within the hepatic parenchyma can be affected by factors such as lobular overlap, local tissue compression, and variations in vascular pathways, resulting in regional inhomogeneity of dye perfusion. This is particularly evident in areas where multiple lobes converge or where anatomical structures are complex, leading to local dye accumulation or over-perfusion.

In our experiments, we attempted to minimize local blockage or over-perfusion by performing PBS pre-flushing and low-pressure, constant-speed perfusion. Nevertheless, localized dye accumulation or uneven distribution may still occur in lobe junctions or structurally complex regions. Such variation represents one of the methodological limitations. Overall, the dye signals in most samples remained confined to the vascular and biliary lumens, and the distribution pattern was highly reproducible.

We have addressed this issue in the Discussion section but would like to emphasize here that, although this system has clear advantages, it remains sensitive to anatomical variability in the liver—such as lobular overlap and vascular heterogeneity. At vascular junctions, local perfusion inhomogeneity or dye accumulation may occur; therefore, injection strategies and perfusion parameters should be adjusted according to liver size and vascular condition to improve reproducibility and imaging quality. It should also be noted that the results obtained using this method primarily aim to visualize the overall and fine anatomical structures of the hepatic vascular system rather than to quantitatively reflect hemodynamic processes. In the future, we plan to combine in vivo perfusion or dynamic fluid modeling to further validate the diffusion characteristics of the dyes within the hepatic microcirculation.

(3) It is advisable to present additional 3D perspective views in the article, as the current images exhibit very weak 3D effects. Furthermore, it would be better to supplement with some videos to demonstrate the 3D effects of the stained blood vessels.

Thank you for the reviewer’s valuable comments. In response to the suggestion, we have added perspective-rendered images generated from the 3D staining datasets to provide a more intuitive visualization of the spatial morphology of the hepatic vasculature. These images have been included in Figure S2A–J. In addition, we have prepared supplementary videos (available upon request) that dynamically display the three-dimensional distribution of the stained vessels, further enhancing the spatial perception and visualization of the results.

(4) In Figure 1-I, the authors used MCNP-Black to stain the central veins; however, in addition to black, there are also yellow and red stains in the image. The authors need to explain what these stains are in the legend.

Thank you for the reviewer’s constructive comment. In Figure 1I, MCNP-Black labels the central vein (black), MCNP-Yellow labels the portal vein (yellow), MCNP-Pink labels the hepatic artery (pink), and MCNP-Green labels the bile duct (green). We have revised the Figure 1 legend to include detailed descriptions of the color signals and their corresponding structures to avoid any potential confusion.

(5) There is a typo in the title of Figure 4F; it should be "stem cell".

Thank you for the reviewer’s careful correction. We have corrected the spelling error in the title of Figure 4F to “stem cell” and updated it in the revised manuscript.

(6) Nuclear staining is necessary in immunofluorescence staining, especially for Figure 5e. This will help readers distinguish whether the green color in the image corresponds to cells or dye deposits.

We thank the reviewer for the valuable suggestion. We understand that nuclear staining can help determine the origin of fluorescence signals. However, in our three-dimensional imaging system, the deep signal acquisition range after tissue clearing often causes nuclear dyes such as DAPI to generate highly dense and widespread fluorescence, especially in regions rich in vascular structures, which can obscure the fine vascular and perivascular details of interest. Therefore, this study primarily focuses on high-resolution visualization of the spatial architecture of the vascular and biliary systems. We have added an explanation regarding this point in Figures S2I–J.

Reviewer #2 (Public review):

Summary:

The present manuscript of Xu et al. reports a novel clearing and imaging method focusing on the liver. The authors simultaneously visualized the portal vein, hepatic artery, central vein, and bile duct systems by injecting metal compound nanoparticles (MCNPs) with different colors into the portal vein, heart left ventricle, inferior vena cava, and the extrahepatic bile duct, respectively. The method involves: trans-cardiac perfusion with 4% PFA, the injection of MCNPs with different colors, clearing with the modified CUBIC method, cutting 200 micrometer thick slices by vibratome, and then microscopic imaging. The authors also perform various immunostaining (DAB or TSA signal amplification methods) on the tissue slices from MCNP-perfused tissue blocks. With the application of this methodical approach, the authors report dense and very fine vascular branches along the portal vein. The authors name them as 'periportal lamellar complex (PLC)' and report that PLC fine branches are directly connected to the sinusoids. The authors also claim that these structures co-localize with terminal bile duct branches and sympathetic nerve fibers, and contain endothelial cells with a distinct gene expression profile. Finally, the authors claim that PLC-s proliferate in liver fibrosis (CCl4 model) and act as a scaffold for proliferating bile ducts in ductular reaction and for ectopic parenchymal sympathetic nerve sprouting.

Strengths:

The simultaneous visualization of different hepatic vascular compartments and their combination with immunostaining is a potentially interesting novel methodological approach.

Weaknesses:

This reviewer has several concerns about the validity of the microscopic/morphological findings as well as the transcriptomics results. In this reviewer's opinion, the introduction contains overstatements regarding the potential of the method, there are severe caveats in the method descriptions, and several parts of the Results are not fully supported by the documentation. Thus, the conclusions of the paper may be critically viewed in their present form and may need reconsideration by the authors.

We sincerely thank the reviewer for the thorough evaluation and constructive comments on our study. We fully understand and appreciate the reviewer’s concerns regarding the methodological validity and interpretation of the results. In response, we have made comprehensive revisions and additions to the manuscript as follows:

First, we have carefully revised the Introduction and Discussion sections to provide a more balanced description of the methodological potential, removing statements that might be considered overstated, and clarifying the applicable scope and limitations of our approach (see the revised Introduction and Discussion).

Second, we have substantially expanded the Methods section with detailed information on model construction, imaging parameters, data processing workflow, and technical aspects of the single-cell transcriptomic reanalysis, to enhance the transparency and reproducibility of the study.

Third, we have added additional references and explanatory notes in the Results section to better support the main conclusions (see Section 6 of the Results).

Finally, we have rechecked and validated all experimental data, and conducted a verification analysis using an independent single-cell RNA-seq dataset (Figure S6). The results confirm that the morphological observations and transcriptomic findings are consistent and reproducible across independent experiments.

We believe these revisions have greatly strengthened the reliability of our conclusions and the overall scientific rigor of the manuscript. Once again, we sincerely appreciate the reviewer’s valuable comments, which have been very helpful in improving the logic and clarity of our work.

Reviewer #3 (Public review):

Summary:

In the reviewed manuscript, researchers aimed to overcome the obstacles of high-resolution imaging of intact liver tissue. They report successful modification of the existing CUBIC protocol into Liver-CUBIC, a high-resolution multiplex 3D imaging method that integrates multicolor metallic compound nanoparticle (MCNP) perfusion with optimized liver tissue clearing, significantly reducing clearing time and enabling simultaneous 3D visualization of the portal vein, hepatic artery, bile ducts, and central vein spatial networks in the mouse liver. Using this novel platform, the researchers describe a previously unrecognized perivascular structure they termed Periportal Lamellar Complex (PLC), regularly distributed along the portal vein axis. The PLC originates from the portal vein and is characterized by a unique population of CD34⁺Sca-1⁺ dual-positive endothelial cells. Using available scRNAseq data, the authors assessed the CD34⁺Sca-1⁺ cells' expression profile, highlighting the mRNA presence of genes linked to neurodevelopment, biliary function, and hematopoietic niche potential. Different aspects of this analysis were then addressed by protein staining of selected marker proteins in the mouse liver tissue. Next, the authors addressed how the PLC and biliary system react to CCL4-induced liver fibrosis, implying PLC dynamically extends, acting as a scaffold that guides the migration and expansion of terminal bile ducts and sympathetic nerve fibers into the hepatic parenchyma upon injury.

The work clearly demonstrates the usefulness of the Liver-CUBIC technique and the improvement of both resolution and complexity of the information, gained by simultaneous visualization of multiple vascular and biliary systems of the liver at the same time. The identification of PLC and the interpretation of its function represent an intriguing set of observations that will surely attract the attention of liver biologists as well as hepatologists; however, some claims need more thorough assessment by functional experimental approaches to decipher the functional molecules and the sequence of events before establishing the PLC as the key hub governing the activity of biliary, arterial, and neuronal liver systems. Similarly, the level of detail of the methods section does not appear to be sufficient to exactly recapitulate the performed experiments, which is of concern, given that the new technique is a cornerstone of the manuscript.

Nevertheless, the work does bring a clear new insight into the liver structure and functional units and greatly improves the methodological toolbox to study it even further, and thus fully deserves the attention of readers.

Strengths:

The authors clearly demonstrate an improved technique tailored to the visualization of the liver vasulo-biliary architecture in unprecedented resolution.

This work proposes a new biological framework between the portal vein, hepatic arteries, biliary tree, and intrahepatic innervation, centered at previously underappreciated protrusions of the portal veins - the Periportal Lamellar Complexes (PLCs).

Weaknesses:

Possible overinterpretation of the CD34+Sca1+ findings was built on re-analysis of one scRNAseq dataset.

Lack of detail in the materials and methods section greatly limits the usefulness of the new technique to other researchers.

We thank the reviewer for this important comment. We agree that when conclusions are mainly based on a single dataset, overinterpretation should be avoided. In response to this concern, we have carefully re-evaluated and clearly limited the scope of our interpretation of the scRNA-seq analysis. In addition, we performed a validation analysis using an independent single-cell RNA-seq dataset (see new Figure S6), which consistently confirmed the presence and characteristic transcriptional profile of the periportal CD34⁺Sca1⁺ endothelial cell population. These supplementary analyses strengthen the robustness of our findings and address the reviewer’s concern regarding potential overinterpretation.

In the revised manuscript, we have also greatly expanded the Materials and Methods section by providing detailed information on sample preparation, imaging parameters, data processing workflow, and single-cell reanalysis procedures. These revisions substantially improve the transparency and reproducibility of our methodology, thereby enhancing the usability and reference value of this technique for other researchers.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Introduction

(1) In general, the Introduction is very lengthy and repetitive. It needs extensive shortening to a maximum of 2 A4 pages.

We thank the reviewer for the valuable suggestions. We have thoroughly condensed and restructured the Introduction, removing redundant content and merging related paragraphs to make the theme more focused and the logic clearer. The revised Introduction has been shortened to within two A4 pages, emphasizing the scientific question, innovation, and technical approach of the study.

(2) Please correct this erroneous sentence:

'...the liver has evolved the most complex and densely n organized vascular network in the body, consisting primarily of the portal vein system, central vein system, hepatic artery system, biliary system, and intrahepatic autonomic nerve network [6, 7].'

We thank the reviewer for pointing out this spelling error. The revised sentence is as follows:

“…the liver has evolved the most complex and densely organized ductal-vascular network in the body, consisting primarily of the portal vein system, central vein system, hepatic artery system, biliary system, and intrahepatic autonomic nerve network [6, 7].”

(3) '...we achieved a 63.89% improvement in clearing efficiency and a 20.12% increase in tissue transparency'

Please clarify what you exactly mean by 'clearing efficiency' and 'increased tissue transparency'.

We thank the reviewer for the valuable comments and have clarified the relevant terminology in the revised manuscript.

“Clearing efficiency” refers to the improvement in the time required for the liver tissue to become completely transparent when treated with the optimized Liver-CUBIC protocol (40% urea + H₂O₂), compared with the conventional CUBIC method. In this study, the clearing time was reduced from 9 days to 3.25 days, representing a 63.89% increase in time efficiency.

“Tissue transparency” refers to the ability of the cleared tissue to transmit visible light. We quantified the optical transparency by measuring light transmittance across the 400–900 nm wavelength range using a microplate reader. The results showed that the average transmittance increased by 20.12%, indicating that Liver-CUBIC treatment markedly enhanced the optical clarity of the liver tissue.

(4) I am concerned about claiming this imaging method as real '3D imaging'. Namely, while the authors clear full lobes, they actually cut the cleared lobes into 200-micrometer-thick slices and perform further microscopy imaging on these slices. Considering that they focus on ductular structures of the liver (such as vasculature, bile duct system, and innervations), 200 micrometer allows a very limited 3D overview, particularly in comparison with the whole-mount immuno-imaging methods combined with light sheet microscopy (such as Adori 2021, Liu 2021, etc). In this context, I feel several parts of the Introduction to be an overstatement: besides of emphasizing the advantages of the technique (such as simultaneous visualization of different hepatic vascular compartments and the bile duct system by MCNPs, the combination with immunostainings), the authors must honestly discuss the limitations (such as limited tissue overview, potential dye perfusion problems - uneven distribution of the dye etc).

We appreciate the reviewer’s insightful comments. It is true that most of the imaging depth in this study was limited to approximately 200 μm, and thus it could not achieve whole-liver three-dimensional imaging comparable to light-sheet microscopy. However, the primary focus of our study was to resolve the microscopic intrahepatic architecture, particularly the spatial relationships among blood vessels, bile ducts, and nerve fibers. Through high-resolution imaging of thick tissue sections, combined with MCNP-based multichannel labeling and immunofluorescence co-staining, we were able to accurately delineate the three-dimensional distribution of these microstructures within localized regions.

In addition to thick-section imaging, we also obtained whole-lobe dye perfusion data (as shown in Figure S1F), which comprehensively depict the three-dimensional branching patterns and distribution of the vascular systems within the liver lobe. These images were acquired from intact liver lobes perfused with MCNP dyes, revealing a continuous vascular network extending from major trunks to peripheral branches, thereby demonstrating that our approach is also capable of achieving organ-level visualization.

We have added this image and a corresponding description in the revised manuscript to more comprehensively present the coverage of our imaging system, and we have incorporated this clarification into the Discussion section.

Method

(5) More information may be needed about MCNPs:

a) As reported, there are nanoparticles with different colors in brightfield microscopy, but the particles are also excitable in fluorescence microscopy. Would you please provide a summary about excitation/emission wavelengths of the different MCNPs? This is crucial to understand to what extent the method is compatible with fluorescence immunohistochemistry.

We thank the reviewer for the careful attention and professional suggestion. We fully agree that this issue is critical for evaluating the compatibility of our method with fluorescent immunohistochemistry. Different types of metal compound nanoparticles (MCNPs) have clearly distinguishable spectral properties:

- MCNP-Green and MCNP-Yellow: AF488-matched spectra, with excitation/emission wavelengths of 495/519 nm.

- MCNP-Pink: Designed for far-red spectra, with excitation/emission wavelengths of 561/640 nm.

- MCNP-Black: Non-fluorescent, appearing black under bright-field microscopy only.

The above information has been added to the Materials and Methods section.

b) Also, is there more systematic information available concerning the advantage of these particles compared to 'traditional' fluorescence dyes, such as Alexa fluor or Cy-dyes, in fluorescence microscopy and concerning their compatibility with various tissue clearing methods (e.g., with the frequently used organic-solvent-based methods)?

We thank the reviewer for the detailed question. Compared with conventional organic fluorescent dyes, MCNP offers the following advantages:

- Enhanced photostability: Its inorganic core-shell structure resists fading even after hydrogen peroxide bleaching.

- High signal stability: Fluorescence is maintained during aqueous-based clearing (e.g., CUBIC) and multiple rounds of staining without quenching.

We appreciate the reviewer’s suggestion. In our Liver-CUBIC system, MCNP nanoparticles exhibited excellent multi-channel labeling stability and fluorescence signal retention. Regarding compatibility with other clearing methods (e.g., SCAFE, SeeDB, CUBIC), since these methods have limited effectiveness for whole-liver clearing (see Figure 2 of Tainaka, et al. 2014) and cannot meet the requirements for high-resolution microstructural imaging in this study, we consider further testing of their compatibility unnecessary.

In summary, MCNP dye demonstrates superior signal stability and spectral separation compared with conventional organic fluorescent dyes in multi-channel, long-term, high-transparency three-dimensional tissue imaging.

c) When you perfuse these particles, to which structures do they bind inside the ducts (vessels, bile ducts)? Is the 48h post-fixation enough to keep them inside the tubes/bind them to the vessel walls? Is there any 'wash-out' during the complex cutting/staining procedure? E.g., in Figure 2D: the 'classical' hepatic artery in the portal triad is not visible - but the MCNP apparently penetrated to the adjacent sinusoids at the edge of the lobulus. Also, in Figure 3B, there is a significant mismatch between the MNCP-green (bile duct) signal and the CD19 (epithelium marker) immunostaining. Please discuss these.

The experimental results showed that following injection, MCNP nanoparticles primarily remained within the vascular and biliary lumens, and their tissue distribution depended on physical perfusion. No dye signal was observed to diffuse into the surrounding parenchyma, nor did the particles adhere to cell surfaces or enter cells. The newly added Supplementary Figures S2A–H further confirm this feature: the dye signal is strictly confined within the lumens, clearly delineating continuous vascular paths and biliary branching patterns, strongly supporting the conclusion that “MCNP dye is distributed only within luminal spaces.”

Thus, MCNP dye mainly serves as an intraluminal tracer rather than a label for specific cell types.

We provide the following explanations and analyses regarding MCNP distribution in the hepatic vascular and biliary systems and its post-fixation stability:

- Potential signal displacement during sectioning/immunostaining: During slicing and immunostaining, a small number of particles may be washed away due to mechanical cutting or washing steps; however, the overall three-dimensional structure retains high spatial fidelity.

- Observation in Figure 2D: MCNP was seen entering the sinusoidal spaces at the lobule periphery, but hepatic arteries were not visible, likely due to limitations in section thickness. Although arteries were not apparent in this slice, arterial distribution around the portal vein is visible in Figure 2C. It should be noted that Figures 2C, D, and E do not represent whole-liver imaging, so not all regions necessarily contain visible hepatic arteries. For easier identification, the main hepatic artery trunk is highlighted in cyan in Figure 2E.

- Incomplete biliary signal in Figure 3B: This may be because CK19 labeling only covers biliary epithelial cells, whereas MCNP-green distributes throughout the biliary lumen. In Figure 3B, the terminal MCNP-green signal exhibits irregular polygonal structures, which we interpret as the canalicular regions.

(6) Which fixative was used for 48h of postfixation (step 6) after MCNP injections?

After MCNP injection, mouse livers were post-fixed in 4% paraformaldehyde (PFA) for 48 hours. This fixation condition effectively “locks” the MCNP particles within the vascular and biliary lumens, maintaining their spatial positions, while also being compatible with subsequent sectioning and multi-channel immunostaining analyses.

The above information has been added to the Materials and Methods section

(7) What is the 'desired thickness' in step 7? In the case of immunostained tissue, a 200-micrometer slice thickness is mentioned. However, based on the Methods, it is not completely clear what the actual thickness of the tissue was that was examined ultimately in the microscopes, and whether or not the clearing preceded the cutting or vice versa.

We appreciate the reviewer’s question. The “desired thickness” referred to in step 7 of the manuscript corresponds to the thickness of tissue sections used for immunostaining and high-resolution microscopic imaging, which is typically around 200 µm. We selected 200 µm because this thickness is sufficient to observe the PLC structure in its entirety, allows efficient staining, and preserves tissue architecture well. Other researchers may choose different section thicknesses according to their experimental needs.

In this study, the processing order for immunostained tissue samples was sectioning followed by clearing, as detailed below:

Section Thickness

To ensure antibody penetration and preservation of three-dimensional structure, tissue sections were typically cut to ~200 µm. Thicker sections can be used if more complete three-dimensional structures are required, but adjustments may be needed based on antibody penetration and fluorescence detection conditions.

Clearing Sequence

After sectioning, slices were processed using the Liver-CUBIC aqueous-based clearing system.

(8) More information is needed concerning the 'deep-focus microscopy' (Keyence), the applied confocal system, and the THUNDER 'high resolution imaging system': basic technical information, resolutions, objectives (N.A., working distance), lasers/illumination, filters, etc.

In this study, all liver lobes (left, right, caudate, and quadrate lobes) were subjected to Liver-CUBIC aqueous-based clearing to ensure uniform visualization of MCNP fluorescence and immunolabeling throughout the three-dimensional imaging of the entire liver.

The above information has been added to the Materials and Methods section.

Imaging Systems and Settings

VHX-6000 Extended Depth-of-Field Microscope: Objective: VH-Z100R, 100×–1000×; resolution: 1 µm (typical); illumination: coaxial reflected; transmitted illumination on platform: ON.

Zeiss Confocal Microscope (980): Objectives: 20× or 40×; image size: 1024 × 1024. Fluorescence detection was set up in three channels:

- Channel 1: 639 nm laser, excitation 650 nm, emission 673 nm, detection range 673–758 nm, corresponding to Cy5-T1 (red).

- Channel 2: 561 nm laser, excitation 548 nm, emission 561 nm, detection range 547–637 nm, corresponding to Cy3-T2 (orange).

- Channel 3: 488 nm laser, excitation 493 nm, emission 517 nm, detection range 490–529 nm, corresponding to AF488-T3 (green).

Leica THUNDER Imager 3D Tissue: Fluorescence detection in two channels:

- Channel 1: FITC channel (excitation 488 nm, emission ~520 nm).

- Channel 2: Orange-red channel (excitation/emission 561/640 nm).<br /> Equipped with matching filter sets to ensure signal separation.

The above information has been added to the Materials and Methods section.

(9) Liver-CUBIC, step 2: which lobe(s) did you clear (...whole liver lobes...).

In this study, all liver lobes (left, right, caudate, and quadrate lobes) were subjected to Liver-CUBIC aqueous-based clearing to ensure uniform visualization of MCNP fluorescence and immunolabeling throughout the three-dimensional imaging of the entire liver.

The above information has been added to the Materials and Methods section.

(10) For the DAB and TSA IHC stainings, did you use free-floating slices, or did you mount the vibratome sections and do the staining on mounted sections?

In this study, fixed livers were first sectioned into thick slices (~200 µm) using a vibratome. Subsequently, DAB and TSA immunohistochemical (IHC) staining were performed on free-floating sections. During the entire staining process, the slices were kept floating in the solutions, ensuring thorough antibody penetration in the thick sections while preserving the three-dimensional tissue architecture, thereby facilitating multiple rounds of staining and three-dimensional imaging.

(11) Regarding the 'transmission quantification': this was measured on 1 mm thick slices. While it is interesting to make a comparison between different clearing methods in general, one must note that it is relatively easy to clear 1mm thick tissue slices with almost any kind of clearing technique and in any tissues. The 'real' differences come with thicker blocks, such as >5mm in the thinnest dimension. Do you have such experiences (e.g., comparison in whole 'left lateral liver lobes')?

In this study, we performed three-dimensional visualization of entire liver lobes to depict the distribution of MCNPs and the overall spatial architecture of the vascular and biliary systems (Figure S1F). However, due to the limitations of the plate reader and fluorescence imaging systems in terms of spatial resolution and light penetration depth, quantitative analyses were conducted only on tissue sections approximately 1 mm thick.

Regarding the comparative quantification of different clearing methods, as the reviewer noted, nearly all aqueous- or organic solvent–based clearing techniques can achieve relatively uniform transparency in 1 mm-thick tissue sections, so differences at this thickness are limited. We have not yet conducted systematic comparisons on whole-lobe sections thicker than 5 mm and therefore cannot provide “true” difference data for thicker tissues.

(12) There is no method description for the ELMI studies in the Methods.

Transmission Electron Microscopy (TEM) Analysis of MCNPs

Before imaging, the MCNP dye solution was centrifuged at 14,000 × g for 10 minutes at 4 °C to remove aggregates and impurities. The supernatant was collected, diluted 50-fold, and 3–4 μL of the sample was applied onto freshly glow-discharged Quantifoil R1.2/1.3 copper grids (Electron Microscopy Sciences, 300 mesh). The sample was allowed to sit for 30 seconds to enable particle adsorption, after which excess liquid was gently wicked away with filter paper and the grid was air-dried at room temperature. The sample was then negatively stained with 1% uranyl acetate for 30 seconds and air-dried again before imaging.

Negative-stain TEM images were acquired using a JEOL JEM-1400 transmission electron microscope operating at 120 kV and equipped with a CCD camera. Data acquisition followed standard imaging conditions.

The above information has been added to the Materials and Methods section.

(13) Please, provide a method description for the applied CCl4 cirrhosis model. This is completely missing.

(1) Under a fume hood, carbon tetrachloride (CCl₄) was dissolved in corn oil at a 1:3 volume ratio to prepare a working solution, which was filtered through a 0.2 μm filter into a 30 mL glass vial. In our laboratory, to mimic chronic injury, mice in the experimental group were intraperitoneally injected at a dose of 1 mL/kg body weight per administration.

(2) Mice were carefully removed from the cage and placed on a scale to record body weight for calculation of the injection volume.

(3) The needle cap was carefully removed, and the required volume of the pre-prepared CCl₄ solution was drawn into the syringe. The syringe was gently flicked to remove any air bubbles.

(4) Mice were placed on a textured surface (e.g., wire cage) and restrained. When the mouse was properly positioned, ideally with the head lowered about 30°, the left lower or right lower abdominal quadrant was identified.

(5) Holding the syringe at a 45° angle, with the bevel facing up, the needle was inserted approximately 4–5 mm into the abdominal wall, and the calculated volume of CCl₄ was injected.

(6) Mice were returned to their cage and observed for any signs of discomfort.

(7) Needles and syringes were disposed of in a sharps container without recapping. A new syringe or needle was used for each mouse.

(8) To establish a progressive liver fibrosis model, injections were administered twice per week (e.g., Monday and Thursday) for 3 or 6 consecutive weeks (n=3 per group). Control mice were injected with an equal volume of corn oil for 3 or 6 weeks (n=3 per group).

(9) Forty-eight hours after the last injection, mice were euthanized by cervical dislocation, and livers were rapidly harvested. Portions of the liver were processed for paraffin embedding and histological sectioning, while the remaining tissue was either immediately frozen or used for subsequent molecular biology analyses.

The above information has been added to the Materials and Methods section.

(14) Please provide a method description for the quantifications reported in Figures 5D, 5F, and 6E.

ImageJ software was used to analyze 3D stained images (Figs. 5F, 6E), and the ultra-depth-of-field 3D analysis module was used to analyze 3D DAB images (Fig. 5D). The specific steps are as follows:

Figure 5D: DAB-stained 3D images from the control group and the CCl₄ 6-week (CCl₄-6W) group were analyzed. For each group, 20 terminal bile duct branch nodes were randomly selected, and the actual path distance along the branch to the nearest portal vein surface was measured. All measurements were plotted as scatter plots to reflect the spatial extension of bile ducts relative to the portal vein under different conditions.

Figure 5F: TSA 3D multiplex-stained images from the control group, CCl₄ 3-week (CCl₄-3W), and CCl₄ 6-week (CCl₄-6W) groups were analyzed. For each group, 5 terminal bile duct branch nodes were randomly selected, and the actual path distance along the branch to the nearest portal vein surface was measured. Measurements were plotted as scatter plots to illustrate bile duct spatial extension.

Figure 6E: TSA 3D multiplex-stained images from the control, CCl₄-3W, and CCl₄-6W groups were analyzed. For each group, 5 terminal nerve branch nodes were randomly selected, and the actual path distance along the branch to the nearest portal vein surface was measured. Scatter plots were generated to depict the spatial distribution of nerves under different treatment conditions.

(15) Please provide a method description for the human liver samples you used in Figure S6. Patient data, fixation, etc...

The human liver tissue samples shown in Figure S6 were obtained from adjacent non-tumor liver tissues resected during surgical operations at West China Hospital, Sichuan University. All samples used were anonymized archived tissues, which were applied for scientific research in accordance with institutional ethical guidelines and did not involve any identifiable patient information. After being fixed in 10% neutral formalin for 24 hours, the tissues were routinely processed for paraffin embedding (FFPE), and sectioned into 4 μm-thick slices for immunostaining and fluorescence imaging.

Results

(16) While it is stated in the Methods that certain color MCNPs were used for labelling different structures (i.e., yellow: hepatic artery; green: bile duct; portal vein: pink; central veins: black), in some figures, apparently different color MCNPs are used for the respective structures. E.g., in Figure 1J, the artery is pink and the portal vein is green. Please clarify this.

The color assignment of MCNP dyes is not fixed across different experiments or schematic illustrations. MCNP dyes of different colors are fundamentally identical in their physical and chemical properties and do not exhibit specific binding or affinity for particular vascular structures. We select different colors based on experimental design and imaging presentation needs to facilitate distinction and visualization, thereby enhancing recognition in 3D reconstruction and image display. Therefore, the color labeling in Figure 1F is primarily intended to illustrate the distribution of different vascular systems, rather than indicating a fixed correspondence to a specific dye or injection color.

(17) In Figure 1J, the hepatic artery is extremely shrunk, while the portal vein is extremely dilated - compared to the physiological situation. Does it relate to the perfusion conditions?

We appreciate the reviewer’s attention. In fact, under normal physiological conditions, the hepatic arteries labeled by CD31 are naturally narrow. Therefore, the relatively thin hepatic arteries and thicker portal veins shown in Figure 1J are normal and unrelated to the perfusion conditions. See figure 1E of Adori et al., 2021.

(18) Re: MCNP-black labelled 'oval fenestrae': the Results state 50-100 nm, while they are apparently 5-10-micron diameter in Figure 1I. Accordingly, the comparison with the ELMI studies in the subsequent paragraph is inappropriate.

We thank the reviewer for the correction. The previous statement was a typographical error. In fact, the diameter of the “elliptical windows” marked by MCNP-black is 5–10 μm, so the diameter of 5–10 μm shown in Figure 1I is correct.

(19) Please, correct this erroneous sentence: 'Pink marked the hepatic arterial system by injection extrahepatic duct (Figure 2B).'

Original sentence: “The hepatic arterial system was labeled in pink by injection through the extrahepatic duct (Figure 2B).”

Revised sentence: “The hepatic arterial system was labeled in pink by injection through the left ventricle (Figure 2B).”

(20) How do you define the 'primary portal vein tract'?

We thank the reviewer for the question. The term “primary portal vein tract” refers to the first-order branches of the portal vein that enter the liver from the hepatic hilum. These are the major branches arising directly from the main portal vein trunk and are responsible for supplying blood to the respective hepatic lobes. This definition corresponds to the concept of the first-order portal vein in hepatic anatomy.

(21) I am concerned that the 'periportal lamellar complex (PLC)' that the Authors describe really exists as a distinct anatomical or functional unit. I also see these in 3D scans - in my opinion, these are fine, lower-order portal vein branches that connect the portal veins to the adjacent sinusoid. The strong MCNP-labelling of these structures may be caused by the 'sticking' of the perfused MCNP solutions in these 'pockets' during the perfusion process. What do these structures look like with SMA or CD31 immunostaining? Also, one may consider that the anatomical evaluation of these structures may have limitations in tissue slices. Have you ever checked MCNP-perfused, cleared full live lobes in light sheet microscope scans? I think this would be very useful to have a comprehensive morphological overview. Unfortunately, based on the presented documentation, I am also not convinced that PLCs are 'co-localize' with fine terminal bile duct branches (Figure 3E, S3C), or with TH+ 'neuronal bead chain networks' (Fig 6C). More detailed and more convincing documentation is needed here.

We thank the reviewer for the detailed comments. Regarding the existence and function of the periportal lamellar complex (PLC), our observations are based on MCNP-Pink labeling of the portal vein, through which we were able to identify the PLC structure surrounding the portal branches. It should be noted that the PLC represents a very small anatomical structure. Although we have not yet performed light-sheet microscopy scanning, we anticipate that such imaging would primarily visualize larger portal vein branches. Nevertheless, this does not affect our overall conclusions.

We also appreciate the reviewer’s suggestion that the observed structures might result from MCNP adherence during perfusion. To verify the structural characteristics of the PLC, we performed immunostaining for SMA and CD31, which revealed a specific arrangement pattern of smooth muscle and endothelial markers rather than simple perfusion-induced deposition (Figures 4F and S6B).

Regarding the apparent colocalization of the PLC with terminal bile duct branches (Figures 3E and S3C) and TH⁺ neuronal bead-like networks (Figure 6C), we acknowledge that current literature evidence remains limited. Therefore, we have carefully described these observations as possible spatial associations rather than definitive conclusions. Future studies integrating high-resolution three-dimensional imaging with functional analyses will help to further clarify the anatomical and physiological significance of the PLC.

(22) 'Extended depth-of-field three-dimensional bright-field imaging revealed a strict 1:1 anatomical association between the primary portal vein trunk (diameter 280 {plus minus} 32 μm) and the first-order bile duct (diameter 69 {plus minus} 8 μm) (Figures 3A and S3A)'.

How do you define '1:1 anatomical association'? How do you define and identify the 'order' (primary, secondary) of vessel and bile duct branches in 200-micrometer slices?

We thank the reviewer for the question. In this study, the term “1:1 anatomical correlation” refers to the stable paired spatial relationship between the main portal vein trunk and its corresponding primary bile duct within the same portal territory. In other words, each main portal vein branch is accompanied by a primary bile duct of matching branching order and trajectory, together forming a “vascular–biliary bundle.”

The definitions of “primary” and “secondary” branches were based on extended-depth 3D bright-field reconstructions, considering both branching hierarchy and vessel/duct diameters: primary branches arise directly from the main trunk at the hepatic hilum and exhibit the largest diameters (averaging 280 ± 32 μm for the portal vein and 69 ± 8 μm for the bile duct), whereas secondary branches extend from the primary branches toward the lobular interior with smaller calibers.

(23) In my opinion, the applied methodical approach in the single cell transcriptomics part (data mining in the existing liver single cell database and performing Venn diagram intersection analysis in hepatic endothelial subpopulations) is largely inappropriate and thus, all the statements here are purely speculative. In my opinion, to identify the molecular characteristics of such small and spatially highly organized structures like those fine radial portal branches, the only way is to perform high-resolution spatial transcriptomic.

We thank the reviewer for the comment. We fully acknowledge the importance of high-resolution spatial transcriptomics in identifying the fine structural characteristics of portal vein branches. Due to current funding and technical limitations, we were unable to perform such high-resolution spatial transcriptomic analyses. However, we validated the molecular features of the PLC using another publicly available liver single-cell RNA-sequencing dataset, which provided preliminary supporting evidence (Figures S6B and S6C). In the manuscript, we have carefully stated that this analysis is exploratory in nature and have avoided overinterpretation. In future studies, high-resolution spatial omics approaches will be invaluable for more precisely delineating the molecular characteristics of these fine structures.

(24) 'How the autonomic nervous system regulates liver function in mice despite the apparent absence of substantive nerve fiber invasion into the parenchyma remains unclear.'

Please consider the role of gap junctions between hepatocytes (e.g., Miyashita, 1991; Seseke, 1992).

In this study, we analyzed the spatial distribution of hepatic nerves in mice using immunofluorescence staining and found that nerve fibers were almost exclusively confined to the portal vein region (Figure S6A). Notably, this distribution pattern differs markedly from that in humans. Previous studies have shown that, in human livers, nerves are not only located around the portal veins but also present along the central veins, interlobular septa, and within the parenchymal connective tissue (Miller et al., 2021; Yi, la Fleur, Fliers & Kalsbeek, 2010).

Further research has provided a physiological explanation for this interspecies difference: even among species with distinct sympathetic innervation patterns in the parenchyma—i.e., with or without direct sympathetic input—the sympathetic efferent regulatory functions may remain comparable (Beckh, Fuchs, Ballé & Jungermann, 1990). This is because signals released from aminergic and peptidergic nerve terminals can be transmitted to hepatocytes through gap junctions as electrical signals (Hertzberg & Gilula, 1979; Jensen, Alpini & Glaser, 2013; Seseke, Gardemann & Jungermann, 1992; Taher, Farr & Adeli, 2017).

However, the scarcity of nerve fibers within the mouse hepatic parenchyma suggests that the mechanisms by which the autonomic nervous system regulates liver function in mice may differ from those in humans. This observation prompted us to further investigate the potential role of PLC endothelial cells in this process.

(25) Please, correct typos throughout the text.

We thank the reviewer for this comment. We have carefully proofread the entire manuscript and corrected all typographical errors and minor language issues throughout the text.

Reviewer #3 (Recommendations for the authors):

(1) A strong recommendation - the authors ought to challenge their scRNAsq- re-analysis with another scRNAseq dataset, namely a recently published atlas of adult liver endothelial, but also mesenchymal, immune, and parenchymal cell populations https://pubmed.ncbi.nlm.nih.gov/40954217/, performed with Smart-seq2 approach, which is perfectly suitable as it brings higher resolution data, and extensive cluster identity validation with stainings. Pietilä et al. indicate a clear distinction of portal vein endothelial cells into two populations that express Adgrg6, Jag1 (e2c), from Vegfc double-positive populations (e5c and e2c). Moreover, the dataset also includes the arterial endothelial cells that were shown to be part of the PLC, but were not followed up with the scRNAseq analysis. This distinction could help the authors to further validate their results, better controlling for cross-contaminations that may occur during scRNAseq preparation.

We thank the reviewer for the valuable suggestion. As noted, we have further validated the molecular characteristics of the PLC using a recently published atlas of adult liver endothelial cells (Pietilä et al., 2023, PMID: 40954217). This dataset, generated using the Smart-seq2 technique, provides high-resolution transcriptomic profiles. By analyzing this dataset, we identified a CD34⁺LY6A⁺ portal vein endothelial cell population within the e2 cluster, which is localized around the portal vein. We then examined pathways and gene expression patterns related to hematopoiesis, bile duct formation, and neural signaling within these cells. The results revealed gene enrichment patterns consistent with those observed in our primary dataset, further supporting the robustness of our analysis of the PLC’s molecular characteristics.

(2) Improving the methods section is highly recommended, this includes more detailed information for material and protocols used - catalog numbers; protocol details of the usage - rocking platforms, timing, and tubes used for incubations; GitHub or similar page with code used for the scRNA seq re-analysis.

We thank the reviewer for the valuable suggestion. We have added more detailed information regarding the materials and experimental procedures in the Methods section, including catalog numbers, incubation conditions (such as the type of shaker, incubation time, and tube specifications), and other relevant parameters.

(3) In Figure 2A, the authors claim the size of the nanoparticle is 100nm, while based on the image, the size is ~150-180nm. A more thorough quantification of the particle size would help users estimate the usability of their method for further applications.

We thank the reviewer for the comment. In the TEM image shown in Figure 2A, the nanoparticles indeed appear to be approximately 150–200 nm in size. We have re-verified the particle dimensions and will update the corresponding description in the Methods section to allow readers to more accurately assess the applicability of this approach.

(4) In Figure 3E, it is not clear what is labeled by the pink signal. Please consider labeling the structures in the figure.

We thank the reviewer for the valuable comment. The pink signal in Figure 3E was originally intended to label the hepatic artery. However, a slight spatial misalignment occurred during the labeling process, making its position appear closer to the central vein rather than the portal vein in the image. To avoid misunderstanding, we will add clear annotations to the image and clarify this deviation in the figure legend in the revised version. It should also be noted that this figure primarily aims to illustrate the spatial relationship between the bile duct and the portal vein, and this minor deviation does not affect the reliability of our experimental conclusions.

(5) The following statement is not backed by quantification as it ought to be „Dual-channel three-dimensional confocal imaging combined with CK19 immunostaining revealed that the sites of dye leakage did not coincide with the CK19-positive terminal bile duct epithelium, but instead were predominantly localized within regions adjacent to the PLC structures".

We thank the reviewer for the valuable comment. We have added the corresponding quantitative analysis to support this conclusion. Quantitative assessment of the extended-depth imaging data revealed that dye leakage predominantly occurred in regions adjacent to the PLC structure, rather than in the perivenous sinusoidal areas. The corresponding results have been presented in the revised Figure 3G.

(6) Similarly, Figure 4F is central to the Sca1CD34 cell type identification but lacks any quantification, providing it would strengthen the key statement of the article. A possible way to approach this is also by FACS sorting the double-positive cells and bluk/qRT validation.

We thank the reviewer for raising this point. We agree that quantitative validation of the Sca1⁺CD34⁺ population by FACS sorting could further support our conclusions. However, the primary focus of this study is on the spatial localization and transcriptional features of PLC endothelial cells. The identification of the Sca1⁺CD34⁺ subset is robustly supported by multiple complementary approaches, including three-dimensional imaging, co-staining with pan-endothelial markers, and projection mapping analyses. Collectively, these lines of evidence provide a solid basis for characterizing this unique endothelial population.

(7) The images in Figure S4D are not comparable, as the Sca1-stained image shows a longitudinal section of the PV, but the other stainings are cross-sections of PVs.

We thank the reviewer for the careful comment. We agree that the original Sca1-stained image, being a longitudinal section of the portal vein, was not optimal for direct comparison with other cross-sectional images. We have replaced it with a cross-sectional image of the portal vein to ensure comparability across all images. The updated image has been included in the revised Supplementary Figure S4D.

(8) I might be wrong, but Figure 4J is entirely missing, and only a cartoon is provided. Either remove the results part or provide the data.

We appreciate the reviewer’s careful observation. Figure 4J was intentionally designed as a schematic illustration to summarize the structural relationships and spatial organization of the portal vein, hepatic artery, and PLC identified in the previous panels (Figures 4A–4I). It does not represent newly acquired experimental data, but rather serves to provide a conceptual overview of the findings.

To avoid misunderstanding, we have clarified this point in the figure legend and the main text, stating that Figure 4J is a schematic summary rather than an experimental image. Therefore, we respectfully prefer to retain the schematic figure to aid readers’ interpretation of the preceding results.

(9) The methods section lacks information about the CCL4concentration, and it is thus hard to estimate the dosage of CCL4 received (ml/kg). This is important for the interpretation of the severity of the fibrosis and presence of cirrhosis, as different doses may or may not lead to cirrhosis within the short regimen performed by the authors [PMID: 16015684 DOI: 10.3748/wjg.v11.i27.4167]. Validation of the fibrosis/cirrhosis severity is, in this case, crucial for the correct interpretation of the results. If the level of cirrhosis is not confirmed, only progressive fibrosis should be mentioned in the manuscript, as these two terms cannot be used interchangeably.

Thank you for the reviewer’s comment. We indeed omitted the information on the concentration of carbon tetrachloride (CCl₄) in the Methods section. In our experiments, mice received intraperitoneal injections of CCl₄ at a dose of 1 mL/kg body weight, twice per week, for a total of six weeks. We have revised the manuscript accordingly, using the term “progressive fibrosis” to avoid confusion between fibrosis and cirrhosis.

(10) The following statement is not backed by any correlation analysis: "Particularly during liver fibrosis progression, the PLC exhibits dynamic structural extension correlating with fibrosis severity,.. ".

We thank the reviewer for the comment. The original statement that the “PLC correlates with fibrosis severity” lacked support from quantitative analysis. To ensure a precise description, we have revised the sentence as follows: “During liver fibrosis progression, the PLC exhibits dynamic structural extension.”

(11) Similarly, the following statement is not followed by data that would address the impact of innervation on liver function: "How the autonomic nervous system regulates liver function in mice despite the apparent absence of substantive nerve fiber invasion into the parenchyma remains unclear.".

This section has been revised. In this study, we analyzed the spatial distribution of nerves in the mouse liver using immunofluorescence staining. The results showed that nerve fibers were almost entirely confined to the portal vein region (Figure S6A). Notably, this distribution pattern differs significantly from that in humans. Previous studies have demonstrated that in the human liver, nerves are not only distributed around the portal vein but also present in the central vein, interlobular septa, and connective tissue of the hepatic parenchyma (Miller et al., 2021; Yi, la Fleur, Fliers & Kalsbeek, 2010).

Previous studies have further explained the physiological basis for this difference: even among species with differences in parenchymal sympathetic innervation (i.e., species with or without direct sympathetic input), their sympathetic efferent regulatory functions may still be similar (Beckh, Fuchs, Ballé & Jungermann, 1990). This is because signals released by adrenergic and peptidergic nerve terminals can be transmitted to hepatocytes as electrical signals through intercellular gap junctions (Hertzberg & Gilula, 1979; Jensen, Alpini & Glaser, 2013; Seseke, Gardemann & Jungermann, 1992; Taher, Farr & Adeli, 2017). However, the scarcity of nerve fibers in the mouse hepatic parenchyma suggests that the mechanism by which the autonomic nervous system regulates liver function in mice may differ from that in humans. This finding also prompts us to further explore the potential role of PLC endothelial cells in this process.

(12) Could the authors discuss their interpretation of the results in light of the fact that the innervation is lower in cirrhotic patients? https://pmc.ncbi.nlm.nih.gov/articles/PMC2871629/. Also, while ADGRG6 (Gpr126) may play important roles in liver Schwann cells, it is likely not through affecting myelination of the nerves, as the liver nerves are not myelinated https://pubmed.ncbi.nlm.nih.gov/2407769/ and https://www.pnas.org/doi/10.1073/pnas.93.23.13280.

We have revised the text to state that although most hepatic nerves are unmyelinated, GPR126 (ADGRG6) may regulate hepatic nerve distribution via non-myelination-dependent mechanisms. Studies have shown that GPR126 exerts both Schwann cell–dependent and –independent functions during peripheral nerve repair, influencing axon guidance, mechanosensation, and ECM remodeling (Mogha et al., 2016; Monk et al., 2011; Paavola et al., 2014).

(13) The manuscript would benefit from text curation that would:

a) Unify the language describing the PLC, so it is clear that (if) it represents protrusions of the portal veins.

We have standardized the description of the PLC throughout the manuscript, clearly specifying its anatomical relationship with the portal vein. Wherever appropriate, we indicate that the PLC represents protrusions associated with the portal vein, avoiding ambiguous or inconsistent statements.

b) Increase the accuracy of the statements.

Examples: "bile ducts, and the central vein in adult mouse livers."

We have refined all statements for accuracy.

c) Reduce the space given to discussion and results in the introduction, moving them to the respective parts. The same applies to the results section, where discussion occurs at more places than in the Discussion part itself.

We have edited the Introduction, removing detailed results and functional explanations, and retaining only a concise overview.

Examples: "The formation of PLC structures in the adventitial layer may participate in local blood flow regulation, maintenance of microenvironmental homeostasis, and vascular-stem cell interactions."

"This finding suggests that PLC endothelial cells not only regulate the periportal microcirculatory blood flow, but also establish a specialized microenvironment that supports periportal hematopoietic regulation, contributing to stem cell recruitment, vascular homeostasis, and tissue repair. "

"Together, these findings suggest the PLC endothelium may act as a key regulator of bile duct branching and fibrotic microenvironment remodeling in liver cirrhosis. " This one in particular would require further validation with protein stainings and similar, directly in your model.

d) Provide a clear reference for the used scRNA seq so it's clear that the data were re-analyzed.

Example: "single-cell transcriptomic analysis revealed significant upregulation of bile duct-related genes in the CD34⁺Sca-1⁺ endothelium of PLC in cirrhotic liver, with notably high expression of Lgals1 (Galectin-1) and HGF(Figure 5G) "

When describing the transcriptional analysis of PLC endothelial cells, we explicitly cited the original scRNA-seq dataset (Su et al., 2021), clarifying that these data were reanalyzed rather than newly generated.

e) Introducing references for claims that, in places, are crucial for further interpretation of experiments.

Examples: "It not only guides bile duct branching during development but also"; the authors show no data from liver development.

Thank you for pointing this out. We have revised the relevant statement to ensure that the claim is accurate and well-supported.

f) Results sentence "Instead, bile duct epithelial cells at the terminal ducts extended partially along the canalicular network without directly participating in the formation of the bile duct lumen." Lacks a callout to the respective Figure.

We would like to thank the reviewers for pointing out this issue. In the revised manuscript, the relevant image (Figure 3D) has been clearly annotated with white arrows to indicate the phenomenon of terminal cholangiocytes extending along the bile canaliculi network. Additionally, the schematic diagram on the right side clearly shows the bile canaliculi, cholangiocytes, and bile flow direction using arrows and color coding, thus intuitively corresponding to the textual description.

(14) Formal text suggestions: The manuscript text contains a lot of missed or excessive spaces and several typos that ought to be fixed. A few examples follow:

a) "densely n organized vascular network "

b) "analysis, while offering high spatial "

c) "specific differences, In the human liver, "

d) Figure 4F has a typo in the description.

e) "generation of high signal-to-noise ratio, multi-target " SNR abbreviation was introduced earlier.

f) Canals of Hering, CoH abbreviation comes much later than the first mention of the Canals of Hering.

We thank the reviewer for the helpful comment regarding textual consistency. We have carefully reviewed and revised the entire manuscript to improve the accuracy, clarity, and consistency of the text.

Reviewer #1 (Public review):

Summary:

This study investigates how the brain processes facial expressions across development by analyzing intracranial EEG (iEEG) data from children (ages 5-10) and post-childhood individuals (ages 13-55). The researchers used a short film containing emotional facial expressions and applied AI-based models to decode brain responses to facial emotions. They found that in children, facial emotion information is represented primarily in the posterior superior temporal cortex (pSTC)-a sensory processing area-but not in the dorsolateral prefrontal cortex (DLPFC), which is involved in higher-level social cognition. In contrast, post-childhood individuals showed emotion encoding in both regions. Importantly, the complexity of emotions encoded in the pSTC increased with age, particularly for socially nuanced emotions like embarrassment, guilt, and pride.The authors claim that these findings suggest that emotion recognition matures through increasing involvement of the prefrontal cortex, supporting a developmental trajectory where top-down modulation enhances understanding of complex emotions as children grow older.

Strengths:

(1) The inclusion of pediatric iEEG makes this study uniquely positioned to offer high-resolution temporal and spatial insights into neural development compared to non-invasive approaches, e.g., fMRI, scalp EEG, etc.

(2) Using a naturalistic film paradigm enhances ecological validity compared to static image tasks often used in emotion studies.

(3) The idea of using state-of-the-art AI models to extract facial emotion features allows for high-dimensional and dynamic emotion labeling in real time.

Weaknesses:

(1) The study has notable limitations that constrain the generalizability and depth of its conclusions. The sample size was very small, with only nine children included and just two having sufficient electrode coverage in the posterior superior temporal cortex (pSTC), which weakens the reliability and statistical power of the findings, especially for analyses involving age. Authors pointed out that a similar sample size has been used in previous iEEG studies, but the cited works focus on adults and do not look at the developmental perspectives. Similar work looking at developmental changes in iEEG signals usually includes many more subjects (e.g., n = 101 children from Cross ZR et al., Nature Human Behavior, 2025) to account for inter-subject variabilities.

(2) Electrode coverage was also uneven across brain regions, with not all participants having electrodes in both the dorsolateral prefrontal cortex (DLPFC) and pSTC, making the conclusion regarding the different developmental changes between DLPFC and pSTC hard to interpret (related to point 3 below). It is understood that it is rare to have such iEEG data collected in this age group, and the electrode location is only determined by clinical needs. However, the scientific rigor should not be compromised by the limited data access. It's the authors' decision whether such an approach is valid and appropriate to address the scientific questions, here the developmental changes in the brain, given all the advantages and constraints of the data modality.

(3) The developmental differences observed were based on cross-sectional comparisons rather than longitudinal data, reducing the ability to draw causal conclusions about developmental trajectories. Also, see comments in point 2.

(4) Moreover, the analysis focused narrowly on DLPFC, neglecting other relevant prefrontal areas such as the orbitofrontal cortex (OFC) and anterior cingulate cortex (ACC), which play key roles in emotion and social processing. Agree that this might be beyond the scope of this paper, but a discussion section might be insightful.

(5) Although the use of a naturalistic film stimulus enhances ecological validity, it comes at the cost of experimental control, with no behavioral confirmation of the emotions perceived by participants and uncertain model validity for complex emotional expressions in children. A non-facial music block that could have served as a control was available but not analyzed. The validation of AI model's emotional output needs to be tested. It is understood that we cannot collect these behavioral data retrospectively within the recorded subjects. Maybe potential post-hoc experiments and analyses could be done, e.g., collect behavioral, emotional perception data from age-matched healthy subjects.

(6) Generalizability is further limited by the fact that all participants were neurosurgical patients, potentially with neurological conditions such as epilepsy that may influence brain responses. At least some behavioral measures between the patient population and the healthy groups should be done to ensure the perception of emotions is similar.

(7) Additionally, the high temporal resolution of intracranial EEG was not fully utilized, as data were downsampled and averaged in 500-ms windows. It seems like the authors are trying to compromise the iEEG data analyses to match up with the AI's output resolution, which is 2Hz. It is not clear then why not directly use fMRI, which is non-invasive and seems to meet the needs here already. The advantages of using iEEG in this study are missing here.

(8) Finally, the absence of behavioral measures or eye-tracking data makes it difficult to directly link neural activity to emotional understanding or determine which facial features participants attended to. Related to point 5 as well.

Comments on revisions:

A behavioral measurement will help address a lot of these questions. If the data continues collecting, additional subjects with iEEG recording and also behavioral measurements would be valuable.

Author response:

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

eLife Assessment

This study examines a valuable question regarding the developmental trajectory of neural mechanisms supporting facial expression processing. Leveraging a rare intracranial EEG (iEEG) dataset including both children and adults, the authors reported that facial expression recognition mainly engaged the posterior superior temporal cortex (pSTC) among children, while both pSTC and the prefrontal cortex were engaged among adults. However, the sample size is relatively small, with analyses appearing incomplete to fully support the primary claims. 

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study investigates how the brain processes facial expressions across development by analyzing intracranial EEG (iEEG) data from children (ages 5-10) and post-childhood individuals (ages 13-55). The researchers used a short film containing emotional facial expressions and applied AI-based models to decode brain responses to facial emotions. They found that in children, facial emotion information is represented primarily in the posterior superior temporal cortex (pSTC) - a sensory processing area - but not in the dorsolateral prefrontal cortex (DLPFC), which is involved in higher-level social cognition. In contrast, post-childhood individuals showed emotion encoding in both regions. Importantly, the complexity of emotions encoded in the pSTC increased with age, particularly for socially nuanced emotions like embarrassment, guilt, and pride. The authors claim that these findings suggest that emotion recognition matures through increasing involvement of the prefrontal cortex, supporting a developmental trajectory where top-down modulation enhances understanding of complex emotions as children grow older.

Strengths:

(1) The inclusion of pediatric iEEG makes this study uniquely positioned to offer high-resolution temporal and spatial insights into neural development compared to non-invasive approaches, e.g., fMRI, scalp EEG, etc.

(2) Using a naturalistic film paradigm enhances ecological validity compared to static image tasks often used in emotion studies.

(3) The idea of using state-of-the-art AI models to extract facial emotion features allows for high-dimensional and dynamic emotion labeling in real time

Weaknesses:

(1) The study has notable limitations that constrain the generalizability and depth of its conclusions. The sample size was very small, with only nine children included and just two having sufficient electrode coverage in the posterior superior temporal cortex (pSTC), which weakens the reliability and statistical power of the findings, especially for analyses involving age

We appreciated the reviewer’s point regarding the constrained sample size.

As an invasive method, iEEG recordings can only be obtained from patients undergoing electrode implantation for clinical purposes. Thus, iEEG data from young children are extremely rare,  and rapidly increasing the sample size within a few years is not feasible. However, we are confident in the reliability of our main conclusions. Specifically, 8 children (53 recording contacts in total) and 13 control participants (99 recording contacts in total) with electrode coverage in the DLPFC are included in our DLPFC analysis. This sample size is comparable to other iEEG studies with similar experiment designs [1-3]. 

For pSTC, we returned to the data set and found another two children who had pSTC coverage. After involving these children’s data, the group-level analysis using permutation test showed that children’s pSTC significantly encode facial emotion in naturalistic contexts (Figure 3B). Notably, the two new children’s (S33 and S49) responses were highly consistent with our previous observations. Moreover, the averaged prediction accuracy in children’s pSTC (r_speech=0.1565) was highly comparable to that in post-childhood group (r_speech=0.1515).

(1) Zheng, J. et al. Multiplexing of Theta and Alpha Rhythms in the Amygdala-Hippocampal Circuit Supports Pafern Separation of Emotional Information. Neuron 102, 887-898.e5 (2019).

(2) Diamond, J. M. et al. Focal seizures induce spatiotemporally organized spiking activity in the human cortex. Nat. Commun. 15, 7075 (2024).

(3) Schrouff, J. et al. Fast temporal dynamics and causal relevance of face processing in the human temporal cortex. Nat. Commun. 11, 656 (2020).

(2) Electrode coverage was also uneven across brain regions, with not all participants having electrodes in both the dorsolateral prefrontal cortex (DLPFC) and pSTC, and most coverage limited to the left hemisphere-hindering within-subject comparisons and limiting insights into lateralization.

The electrode coverage in each patient is determined entirely by the clinical needs. Only a few patients have electrodes in both DLPFC and pSTC because these two regions are far apart, so it’s rare for a single patient’s suspected seizure network to span such a large territory. However, it does not affect our results, as most iEEG studies combine data from multiple patients to achieve sufficient electrode coverage in each target brain area. As our data are mainly from left hemisphere (due to the clinical needs), this study was not designed to examine whether there is a difference between hemispheres in emotion encoding. Nevertheless, lateralization remains an interesting question that should be addressed in future research, and we have noted this limitation in the Discussion (Page 8, in the last paragraph of the Discussion).

(3) The developmental differences observed were based on cross-sectional comparisons rather than longitudinal data, reducing the ability to draw causal conclusions about developmental trajectories.  

In the context of pediatric intracranial EEG, longitudinal data collection is not feasible due to the invasive nature of electrode implantation. We have added this point to the Discussion to acknowledge that while our results reveal robust age-related differences in the cortical encoding of facial emotions, longitudinal studies using non-invasive methods will be essential to directly track developmental trajectories (Page 8, in the last paragraph of Discussion). In addition, we revised our manuscript to avoid emphasis causal conclusions about developmental trajectories in the current study (For example, we use “imply” instead of “suggest” in the fifth paragraph of Discussion).

(4) Moreover, the analysis focused narrowly on DLPFC, neglecting other relevant prefrontal areas such as the orbitofrontal cortex (OFC) and anterior cingulate cortex (ACC), which play key roles in emotion and social processing.

We agree that both OFC and ACC are critically involved in emotion and social processing. However, we have no recordings from these areas because ECoG rarely covers the ACC or OFC due to technical constraints. We have noted this limitation in the Discussion(Page 8, in the last paragraph of Discussion). Future follow-up studies using sEEG or non-invasive imaging methods could be used to examine developmental patterns in these regions.

(5) Although the use of a naturalistic film stimulus enhances ecological validity, it comes at the cost of experimental control, with no behavioral confirmation of the emotions perceived by participants and uncertain model validity for complex emotional expressions in children. A nonfacial music block that could have served as a control was available but not analyzed. 

The facial emotion features used in our encoding models were extracted by Hume AI models, which were trained on human intensity ratings of large-scale, experimentally controlled emotional expression data[1-2]. Thus, the outputs of Hume AI model reflect what typical facial expressions convey, that is, the presented facial emotion. Our goal of the present study was to examine how facial emotions presented in the videos are encoded in the human brain at different developmental stages. We agree that children’s interpretation of complex emotions may differ from that of adults, resulting in different perceived emotion (i.e., the emotion that the observer subjectively interprets). Behavioral ratings are necessary to study the encoding of subjectively perceived emotion, which is a very interesting direction but beyond the scope of the present work. We have added a paragraph in the Discussion (see Page 8) to explicitly note that our study focused on the encoding of presented emotion.

We appreciated the reviewer’s point regarding the value of non-facial music blocks. However,  although there are segments in music condition that have no faces presented, these cannot be used as a control condition to test whether the encoding model’s prediction accuracy in pSTC or DLPFC drops to chance when no facial emotion is present. This is because, in the absence of faces, no extracted emotion features are available to be used for the construction of encoding model (see Author response image 1 below).  Thus, we chose to use a different control analysis for the present work. For children’s pSTC, we shuffled facial emotion feature in time to generate a null distribution, which was then used to test the statistical significance of the encoding models (see Methods/Encoding model fitting for details).

(1) Brooks, J. A. et al. Deep learning reveals what facial expressions mean to people in different cultures. iScience 27, 109175 (2024).

(2) Brooks, J. A. et al. Deep learning reveals what vocal bursts express in different cultures. Nat. Hum. Behav. 7, 240–250 (2023).

Author response image 1.

Time courses of Hume AI extracted facial expression features for the first block of music condition. Only top 5 facial expressions were shown here to due to space limitation.

(6) Generalizability is further limited by the fact that all participants were neurosurgical patients, potentially with neurological conditions such as epilepsy that may influence brain responses. 

We appreciated the reviewer’s point. However, iEEG data can only be obtained from clinical populations (usually epilepsy patients) who have electrodes implantation.  Given current knowledge about focal epilepsy and its potential effects on brain activity, researchers believe that epilepsy-affected brains can serve as a reasonable proxy for normal human brains when confounding influences are minimized through rigorous procedures[1]. In our study, we took several steps to ensure data quality: (1) all data segments containing epileptiform discharges were identified and removed at the very beginning of preprocessing, (2) patients were asked to participate the experiment several hours outside the window of seizures. Please see Method for data quality check description (Page 9/ Experimental procedures and iEEG data processing). 

(1) Parvizi J, Kastner S. 2018. Promises and limitations of human intracranial electroencephalography. Nat Neurosci 21:474–483. doi:10.1038/s41593-018-0108-2

(7) Additionally, the high temporal resolution of intracranial EEG was not fully utilized, as data were down-sampled and averaged in 500-ms windows.  

We agree that one of the major advantages of iEEG is its millisecond-level temporal resolution. In our case, the main reason for down-sampling was that the time series of facial emotion features extracted from the videos had a temporal resolution of 2 Hz, which were used for the modelling neural responses. In naturalistic contexts, facial emotion features do not change on a millisecond timescale, so a 500 ms window is sufficient to capture the relevant dynamics. Another advantage of iEEG is its tolerance to motion, which is excessive in young children (e.g., 5-year-olds). This makes our dataset uniquely valuable, suggesting robust representation in the pSTC but not in the DLPFC in young children. Moreover, since our method framework (Figure 1) does not rely on high temporal resolution method, so it can be transferred to non-invasive modalities such as fMRI, enabling future studies to test these developmental patterns in larger populations.

(8) Finally, the absence of behavioral measures or eye-tracking data makes it difficult to directly link neural activity to emotional understanding or determine which facial features participants afended to.  

We appreciated this point. Part of our rationale is presented in our response to (5) for the absence of behavioral measures. Following the same rationale, identifying which facial features participants attended to is not necessary for testing our main hypotheses because our analyses examined responses to the overall emotional content of the faces. However, we agree and recommend future studies use eye-tracking and corresponding behavioral measures in studies of subjective emotional understanding. 

Reviewer #2 (Public review):

Summary:

In this paper, Fan et al. aim to characterize how neural representations of facial emotions evolve from childhood to adulthood. Using intracranial EEG recordings from participants aged 5 to 55, the authors assess the encoding of emotional content in high-level cortical regions. They report that while both the posterior superior temporal cortex (pSTC) and dorsolateral prefrontal cortex (DLPFC) are involved in representing facial emotions in older individuals, only the pSTC shows significant encoding in children. Moreover, the encoding of complex emotions in the pSTC appears to strengthen with age. These findings lead the authors to suggest that young children rely more on low-level sensory areas and propose a developmental shiZ from reliance on lower-level sensory areas in early childhood to increased top-down modulation by the prefrontal cortex as individuals mature.

Strengths: 

(1) Rare and valuable dataset: The use of intracranial EEG recordings in a developmental sample is highly unusual and provides a unique opportunity to investigate neural dynamics with both high spatial and temporal resolution. 

(2) Developmentally relevant design: The broad age range and cross-sectional design are well-suited to explore age-related changes in neural representations. 

(3) Ecological validity: The use of naturalistic stimuli (movie clips) increases the ecological relevance of the findings. 

(4) Feature-based analysis: The authors employ AIbased tools to extract emotion-related features from naturalistic stimuli, which enables a data-driven approach to decoding neural representations of emotional content. This method allows for a more fine-grained analysis of emotion processing beyond traditional categorical labels. 

Weaknesses: 

(1) The emotional stimuli included facial expressions embedded in speech or music, making it difficult to isolate neural responses to facial emotion per se from those related to speech content or music-induced emotion. 

We thank the reviewer for their raising this important point. We agree that in naturalistic settings, face often co-occur with speech, and that these sources of emotion can overlap. However, background music induced emotions have distinct temporal dynamics which are separable from facial emotion (See the Author response image 2 (A) and (B) below). In addition, face can convey a wide range of emotions (48 categories in Hume AI model), whereas music conveys far fewer (13 categories reported by a recent study [1]). Thus, when using facial emotion feature time series as regressors (with 48 emotion categories and rapid temporal dynamics), the model performance will reflect neural encoding of facial emotion in the music condition, rather than the slower and lower-dimensional emotion from music. 

For the speech condition, we acknowledge that it is difficult to fully isolate neural responses to facial emotion from those to speech when the emotional content from faces and speech highly overlaps. However, in our study, (1) the time courses of emotion features from face and voice are still different (Author response image 2 (C) and (D)), (2) our main finding that DLPFC encodes facial expression information in postchildhood individuals but not in young children was found in both speech and music condition (Figure 2B and 2C). In music condition, neural responses to facial emotion are not affected by speech. Thus, we have included the DLPFC results from the music condition in the revised manuscript (Figure 2C), and we acknowledge that this issue should be carefully considered in future studies using videos with speech, as we have indicated in the future directions in the last paragraph of Discussion.

(1) Cowen, A. S., Fang, X., Sauter, D. & Keltner, D. What music makes us feel: At least 13 dimensions organize subjective experiences associated with music across different cultures. Proc Natl Acad Sci USA 117, 1924–1934 (2020).

Author response image 2.

Time courses of the amusement. (A) and (B) Amusement conveyed by face or music in a 30-s music block. Facial emotion features are extracted by Hume AI. For emotion from music, we approximated the amusement time course using a weighted combination of low-level acoustic features (RMS energy, spectral centroid, MFCCs), which capture intensity, brightness, and timbre cues linked to amusement. Notice that music continues when there are no faces presented. (C) and (D) Amusement conveyed by face or voice in a 30-s speech block. From 0 to 5 seconds, a girl is introducing her friend to a stranger. The camera focuses on the friend, who appears nervous, while the girl’s voice sounds cheerful. This mismatch explains why the shapes of the two time series differ at the beginning. Such situations occur frequently in naturalistic movies

(2) While the authors leveraged Hume AI to extract facial expression features from the video stimuli, they did not provide any validation of the tool's accuracy or reliability in the context of their dataset. It remains unclear how well the AI-derived emotion ratings align with human perception, particularly given the complexity and variability of naturalistic stimuli. Without such validation, it is difficult to assess the interpretability and robustness of the decoding results based on these features.  

Hume AI models were trained and validated by human intensity ratings of large-scale, experimentally controlled emotional expression data [1-2]. The training process used both manual annotations from human raters and deep neural networks. Over 3000 human raters categorized facial expressions into emotion categories and rated on a 1-100 intensity scale. Thus, the outputs of Hume AI model reflect what typical facial expressions convey (based on how people actually interpret them), that is, the presented facial emotion. Our goal of the present study was to examine how facial emotions presented in the videos are encoded in the human brain at different developmental stages. We agree that the interpretation of facial emotions may be different in individual participants, resulting in different perceived emotion (i.e., the emotion that the observer subjectively interprets). Behavioral ratings are necessary to study the encoding of subjectively perceived emotion, which is a very interesting direction but beyond the scope of the present work. We have added text in the Discussion to explicitly note that our study focused on the encoding of presented emotion (second paragraph in Page 8).

(1) Brooks, J. A. et al. Deep learning reveals what facial expressions mean to people in different cultures. iScience 27, 109175 (2024).

(2) Brooks, J. A. et al. Deep learning reveals what vocal bursts express in different cultures. Nat. Hum. Behav. 7, 240–250 (2023).

(3) Only two children had relevant pSTC coverage, severely limiting the reliability and generalizability of results.  

We appreciated this point and agreed with both reviewers who raised it as a significant concern. As described in response to reviewer 1 (comment 1), we have added data from another two children who have pSTC coverage. Group-level analysis using permutation test showed that children’s pSTC significantly encode facial emotion in naturalistic contexts (Figure 3B). Because iEEG data from young children are extremely rare, rapidly increasing the sample size within a few years is not feasible. However, we are confident in the reliability of our conclusion that children’s pSTC can encode facial emotion. First,  the two new children’s responses (S33 and S49) from pSTC were highly consistent with our previous observations (see individual data in Figure 3B). Second, the averaged prediction accuracy in children’s pSTC (r_speech=0.1565) was highly comparable to that in post-childhood group (r_speech=0.1515).

(4) The rationale for focusing exclusively on high-frequency activity for decoding emotion representations is not provided, nor are results from other frequency bands explored.   

We focused on high-frequency broadband (HFB) activity because it is widely considered to reflect the responses of local neuronal populations near the recording electrode, whereas low-frequency oscillations in the theta, alpha, and beta ranges are thought to serve as carrier frequencies for long-range communication across distributed networks[1-2]. Since our study aimed to examine the representation of facial emotion in localized cortical regions (DLPFC and pSTC), HFB activity provides the most direct measure of the relevant neural responses. We have added this rationale to the manuscript (Page 3).

(1) Parvizi, J. & Kastner, S. Promises and limitations of human intracranial electroencephalography. Nat. Neurosci. 21, 474–483 (2018).

(2) Buzsaki, G. Rhythms of the Brain. (Oxford University Press, Oxford, 200ti).

(5) The hypothesis of developmental emergence of top-down prefrontal modulation is not directly tested. No connectivity or co-activation analyses are reported, and the number of participants with simultaneous coverage of pSTC and DLPFC is not specified.  

Directional connectivity analysis results were not shown because only one child has simultaneous coverage of pSTC and DLPFC. However, the  Granger Causality results from post-childhood group (N=7) clearly showed that the influence in the alpha/beta band from DLPFC to pSTC (top-down) is gradually increased above the onset of face presentation (Author response image 3, below left, plotted in red). By comparison, the influence in the alpha/beta band from pSTC to DLPFC (bottom-up) is gradually decreased after the onset of face presentation (Author response image 3, below left, blue curve). The influence in alpha/beta band from DLPFC to pSTC was significantly increased at 750 and 1250 ms after the face presentation (face vs nonface, paired t-test, Bonferroni  corrected P=0.005, 0.006), suggesting an enhanced top-down modulation in the post-childhood group during watching emotional faces. Interestingly, this top-down influence appears very different in the 8-year-old child at 1250 ms after the face presentation (Author response image 3, below left, black curve).

As we cannot draw direct conclusions from the single-subject sample presented here, the top-down hypothesis is introduced only as a possible explanation for our current results. We have removed potentially misleading statements, and we plan to test this hypothesis directly using MEG in the future.

Author response image 3.

Difference of Granger causality indices (face – nonface) in alpha/beta and gamma band for both directions. We identified a series of face onset in the movie that paticipant watched. Each trial was defined as -0.1 to 1.5 s relative to the onset. For the non-face control trials, we used houses, animals and scenes. Granger causality was calculated for 0-0.5 s, 0.5-1 s and 1-1.5 s time window. For the post-childhood group, GC indices were averaged across participants. Error bar is sem.

(6) The "post-childhood" group spans ages 13-55, conflating adolescence, young adulthood, and middle age. Developmental conclusions would benefit from finer age stratification.  

We appreciate this insightful comment. Our current sample size does not allow such stratification. But we plan to address this important issue in future MEG studies with larger cohorts.

(7) The so-called "complex emotions" (e.g., embarrassment, pride, guilt, interest) used in the study often require contextual information, such as speech or narrative cues, for accurate interpretation, and are not typically discernible from facial expressions alone. As such, the observed age-related increase in neural encoding of these emotions may reflect not solely the maturation of facial emotion perception, but rather the development of integrative processing that combines facial, linguistic, and contextual cues. This raises the possibility that the reported effects are driven in part by language comprehension or broader social-cognitive integration, rather than by changes in facial expression processing per se.  

We agree with this interpretation. Indeed, our results already show that speech influences the encoding of facial emotion in the DLPFC differently in the childhood and post-childhood groups (Figure 2D), suggesting that children’s ability to integrate multiple cues is still developing. Future studies are needed to systematically examine how linguistic cues and prior experiences contribute to the understanding of complex emotions from faces, which we have added to our future directions section (last paragraph in Discussion, Page 8-9 ).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

In the introduction: "These neuroimaging data imply that social and emotional experiences shape the prefrontal cortex's involvement in processing the emotional meaning of faces throughout development, probably through top-down modulation of early sensory areas." Aren't these supposed to be iEEG data instead of neuroimaging? 

Corrected.

Reviewer #2 (Recommendations for the authors):

This manuscript would benefit from several improvements to strengthen the validity and interpretability of the findings:

(1) Increase the sample size, especially for children with pSTC coverage. 

We added data from another two children who have pSTC coverage. Please see our response to reviewer 2’s comment 3 and reviewer 1’s comment 1.

(2) Include directional connectivity analyses to test the proposed top-down modulation from DLPFC to pSTC. 

Thanks for the suggestion. Please see our response to reviewer 2’s comment 5.

(3) Use controlled stimuli in an additional experiment to separate the effects of facial expression, speech, and music. 

This is an excellent point. However, iEEG data collection from children is an exceptionally rare opportunity and typically requires many years, so we are unable to add a controlled-stimulus experiment to the current study. We plan to consider using controlled stimuli to study the processing of complex emotion using non-invasive method in the future. In addition, please see our response to reviewer 2’s comment 1 for a description of how neural responses to facial expression and music are separated in our study.

Author response:

The following is the authors’ response to the original reviews

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

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

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

(3) Experimental work supports the computational predictions.     

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

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

Weaknesses:

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Reviewer #2 (Public review):

Summary:

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

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

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

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

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

Strengths:

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

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

Weaknesses:

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Recommendations for the authors: 

Reviewer #1 (Recommendations for the authors):

Additional comments:

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

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

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

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

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

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

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

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

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

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

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

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

Please see above responses and new analysis.

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

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

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

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

Fixed.

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

Single splice junction pre-training.

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

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

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

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

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

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

(12) Typos, grammar:

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

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

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

Fixed

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

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

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

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

Reviewer #2 (Recommendations for the authors):

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

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

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

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

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

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

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

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

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

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

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

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

Reviewer 1 

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

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

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

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

Right - we removed that sentence.. 

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

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

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

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

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

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

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

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

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

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

Fixed.

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

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

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

We updated the text to read: 

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

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

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

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

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

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

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

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

Added.

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

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

(20) Minor typographical comments:

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

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

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

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

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

Definition now included (see above).

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

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

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

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

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

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

We updated the text to read:

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

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

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

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

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

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

Fixed, thank you for noticing this.

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

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

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

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

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

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

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

We removed Figure 1b cartoon.

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

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

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

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

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

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

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

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

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

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

Fixed.

-   L221, "the DNABERT" => "DNABERT".

Fixed.

-   L232, missing percent sign.

-    

Fixed.

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

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

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

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

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

Fixed.

-   p252, "polypyrimidine" (no capitalization).

Fixed.

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

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

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

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

-   Figure 4 legend typo: "two three".

Fixed.

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

Fixed.

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

Fixed.

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

Fixed.

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

Fixed.

-   L580-581, citations missing.

Fixed.

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

Fixed.

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

Fixed.

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

Fixed.

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

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

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

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

Reviewer #1 (Public review):

Summary:

This study presents convincing findings that oligodendrocytes play a regulatory role in spontaneous neural activity synchronization during early postnatal development, with implications for adult brain function. Utilizing targeted genetic approaches, the authors demonstrate how oligodendrocyte depletion impacts Purkinje cell activity and behaviors dependent on cerebellar function. Delayed myelination during critical developmental windows is linked to persistent alterations in neural circuit function, underscoring the lasting impact of oligodendrocyte activity.

Strengths:

(1) The research leverages the anatomically distinct olivocerebellar circuit, a well-characterized system with known developmental timelines and inputs, strengthening the link between oligodendrocyte function and neural synchronization.

(2) Functional assessments, supported by behavioral tests, validate the findings of in vivo calcium imaging, enhancing the study's credibility.

(3) Extending the study to assess long-term effects of early life myelination disruptions adds depth to the implications for both circuit function and behavior.

Weaknesses:

(1) The study would benefit from a closer analysis of myelination during the periods when synchrony is recorded. Direct correlations between myelination and synchronized activity would substantiate the mechanistic link and clarify if observed behavioral deficits stem from altered myelination timing.

(2) Although the study focuses on Purkinje cells in the cerebellum, neural synchrony typically involves cross-regional interactions. Expanding the discussion on how localized Purkinje synchrony affects broader behaviors-such as anxiety, motor function, and sociality - would enhance the findings' functional significance.

(3) The authors discuss the possibility of oligodendrocyte-mediated synapse elimination as a possible mechanism behind their findings, drawing from relevant recent literature on oligodendrocyte precursor cells. However, there are no data presented supporting these assumptions. The authors should explain why they think the mechanism behind their observation extends beyond the contribution of myelination or remove this point from the discussion entirely.

Comment for resubmission: Although the argument on synaptic elimination has been removed, it has been replaced with similarly unclear speculation about roles for oligodendrocytes outside of conventional myelination or metabolic support, again without clear evidence. The authors measured MBP area but have not performed detailed analysis of oligodendrocyte biology to support the claims made in the discussion. Please consider removing this section or rephrasing it to align with the data presented.

(4) It would be valuable to investigate secondary effects of oligodendrocyte depletion on other glial cells, particularly astrocytes or microglia, which could influence long-term behavioral outcomes. Identifying whether the lasting effects stem from developmental oligodendrocyte function alone or also involve myelination could deepen the study's insights.

(5) The authors should explore the use of different methods to disturb myelin production for a longer time, in order to further determine if the observed effects are transient or if they could have longer-lasting effects.

(6) Throughout the paper, there are concerns about statistical analyses, particularly on the use of the Mann-Whitney test or using fields of view as biological replicates.

Author response:

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

Public Reviews:

Reviewer #1 (Public review): 

Summary: 

This study presents convincing findings that oligodendrocytes play a regulatory role in spontaneous neural activity synchronisation during early postnatal development, with implications for adult brain function. Utilising targeted genetic approaches, the authors demonstrate how oligodendrocyte depletion impacts Purkinje cell activity and behaviours dependent on cerebellar function. Delayed myelination during critical developmental windows is linked to persistent alterations in neural circuit function, underscoring the lasting impact of oligodendrocyte activity. 

Strengths: 

(1) The research leverages the anatomically distinct olivocerebellar circuit, a well-characterized system with known developmental timelines and inputs, strengthening the link between oligodendrocyte function and neural synchronization. 

(2) Functional assessments, supported by behavioral tests, validate the findings of in vivo calcium imaging, enhancing the study's credibility. 

(3) Extending the study to assess the long-term effects of early-life myelination disruptions adds depth to the implications for both circuit function and behavior.

We appreciate these positive evaluation.

Weaknesses: 

(1) The study would benefit from a closer analysis of myelination during the periods when synchrony is recorded. Direct correlations between myelination and synchronized activity would substantiate the mechanistic link and clarify if observed behavioral deficits stem from altered myelination timing. 

We appreciate the reviewer’s thoughtful suggestion and have expanded the manuscript to clarify how oligodendrocyte maturation relates to the development of Purkinje-cell synchrony. The developmental trajectory of Purkinje-cell synchrony has already been comprehensively characterized by Good et al. (2017, Cell Reports 21: 2066–2073): synchrony drops from a high level at P3–P5 to adult-like values by P8. We found that the myelination in the cerebellum starts to appear from P5-P7 (Figure S1A, B), indicating that the timing of Purkinje cell desynchronization coincides with the initial appearance of oligodendrocytes and myelin in the cerebellum. To determine whether myelin growth could nevertheless modulate this process, we quantified ASPA-positive oligodendrocyte density and MBP-positive bundle thickness and area at P10, P14, P21 and adulthood (Fig. 1J, K, Fig. S1E). Both metrics increase monotonically and clearly lag behind the rapid drop in synchrony, indicating that myelination could be not the primary trigger for the desynchronization. When oligodendrocytes were ablated during the second postnatal week, the synchrony was reduced (new Fig. 2). Thus, once myelination is underway, oligodendrocytes become critical for maintaining the synchrony, acting not as the initiators but as the stabilizers and refiners of the mature network state.

We have added the new subsection in discussion (lines 451–467) now in which we propose a two-phase model. Phase I (P3–P8): High early synchrony is generated by non-myelin mechanisms (e.g. transient gap junctions, shared climbing-fiber input). Phase II (P8-). As oligodendrocytes proliferate and ensheath axons, they fine-tune conduction velocity and stabilize the mature, low-synchrony network state.

We believe these additions fully address the reviewer’s concerns.

(2) Although the study focuses on Purkinje cells in the cerebellum, neural synchrony typically involves cross-regional interactions. Expanding the discussion on how localized Purkinje synchrony affects broader behaviors - such as anxiety, motor function, and sociality - would enhance the findings' functional significance.

We appreciate the reviewer’s helpful suggestion and have expanded the Discussion (lines 543–564) to clarify how localized Purkinje-cell synchrony can influence broader behavioral domains. In the revised text we note that changes in PC synchrony propagate  into thalamic, prefrontal, limbic, and parietal targets, thereby impacting distributed networks involved in motor coordination, affect, and social interaction. Our optogenetic rescue experiments further support this framework, as transient resynchronization of PCs normalized sociability and motor coordination while leaving anxiety-like behavior impaired. This dissociation highlights that different behavioral domains rely to varying degrees on precise cerebellar synchrony and underscores how even localized perturbations in Purkinje timing can acquire system-level significance.

(3) The authors discuss the possibility of oligodendrocyte-mediated synapse elimination as a possible mechanism behind their findings, drawing from relevant recent literature on oligodendrocyte precursor cells. However, there are no data presented supporting this assumption. The authors should explain why they think the mechanism behind their observation extends beyond the contribution of myelination or remove this point from the discussion entirely.

We thank the reviewer for pointing out that our original discussion of oligodendrocyte-mediated synapse elimination was not directly supported by data in the present manuscript. Because we are actively analyzing this question in a separate, follow-up study, we have deleted the speculative passage to keep the current paper focused on the demonstrated, myelination-dependent effects. We believe this change sharpens the mechanistic narrative and fully addresses the reviewer’s concern.

(4) It would be valuable to investigate the secondary effects of oligodendrocyte depletion on other glial cells, particularly astrocytes or microglia, which could influence long-term behavioral outcomes. Identifying whether the lasting effects stem from developmental oligodendrocyte function alone or also involve myelination could deepen the study's insights. 

We thank the reviewer for raising this point and have performed the requested analyses. Using IBA1 immunostaining for microglia and S100b for Bergmann glia, we quantified cell density and these marker signal intensity at P14 and P21. Neither microglial or Bergmann-glial differed between control and oligodendrocyte-ablated mice at either time‐point (new Figure S2). These results indicate that the behavioral phenotypes we report are unlikely to arise from secondary activation or loss of other glial populations.

We now added results (lines 275–286) and also discuss myelination and other oligodendrocyte function (lines 443–450). It remains difficult to disentangle conduction-related effects from myelination-independent trophic roles of oligodendrocytes. We therefore note explicitly that future work employing stage-specific genetic tools or acute metabolic manipulations will be required to parse these contributions more definitively.

(5) The authors should explore the use of different methods to disturb myelin production for a longer time, in order to further determine if the observed effects are transient or if they could have longer-lasting effects.

We agree that distinguishing transient from enduring effects is critical. Importantly, our original submission already included data demonstrating a persistent deficit of PC population synchrony (Fig. 4, previous Fig. 3): (i) at P14—the early age after oligodendrocyte ablation—population synchrony is reduced, and (ii) the same deficit is still present in adults (P60–P70) despite full recovery of ASPA-positive cell density and MBP-area and -thickness (Fig. 2H-K, Fig. S1E, and Fig. 4). We also performed the ablation of oligodendrocytes after the third postnatal week. Despite a similar acute drop in ASPA-positive cells, neither population synchrony nor anxiety-, motor-, or social behaviors differed from littermate controls. Thus, extending myelin disruption beyond the developmental window does not exacerbate or prolong the phenotype, whereas a short perturbation within that window leaves a permanent timing defect. These findings strengthen our conclusion that it is the developmental oligodendrocyte/myelination program itself—rather than ongoing adult myelin production—that is essential for establishing stable network synchrony. We now highlight this point explicitly in the revised Discussion (lines 507–522).

(6) Throughout the paper, there are concerns about statistical analyses, particularly on the use of the Mann-Whitney test or using fields of view as biological replicates.

We appreciate the reviewer’s guidance on appropriate statistical treatment. To address these concerns we have re-analyzed all datasets that contained multiple measurements per animal (e.g., fields of view, lobules, or trials) using nested statistics with animal as the higher-order unit. Specifically, we applied a two-level nested ANOVA when more than two groups were compared and a nested t-test when two conditions were present. The re-analysis confirmed all original conclusions. Because the nested models yielded comparable effect sizes to the Mann–Whitney tests, we have retained the mean ± SEM for ease of comparison with prior literature but now also report all values for each mouse in Table 1. In cases where a single measurement per mouse was compared between two groups, we used the Mann–Whitney test and present the results in the graphs as median values.

Major

(1) The authors present compelling evidence that early loss of myelination disrupts synchronous firing prematurely. However, synchronous neuronal firing does not equate to circuit synchronization. It is improbable that myelination directly generates synchronous firing in Purkinje cells (PCs). For instance, Foran et al. (1992) identified that cerebellar myelination begins around postnatal day 6 (P6), while Good et al. (2017) recorded a developmental decline in PC activity correlation from P5-P11. To clarify myelin's role, we recommend detailed myelin imaging through light microscopy (MBP staining at higher magnification) to assess the extent of myelin removal accurately. Myelin sheaths, as shown by Snaidero et al. (2020), can persist after oligodendrocyte (OL) death, particularly following DTA induction (Pohl et al. 2011). Quantification of MBP+ area, rather than mean MBP intensity, is necessary to accurately measure myelin coverage.

We appreciate the reviewer’s concern that residual sheaths might remain after oligodendrocyte ablation and have therefore re-examined myelin at higher spatial resolution. Then, two independent metrics were extracted: MBP⁺ area fraction in the white matter and MBP⁺ bundle thickness (new Figure 1J, K, and Fig. S1E). We confirm a robust, transient loss of myelin at P10 and P14 as shown by the reduction of MBP⁺ area and MBP⁺ bundle thickness. Both parameters recovered to control values by P21 and adulthood, indicating effective remyelination. These data demonstrate that, in our paradigm, oligodendrocyte ablation is accompanied by substantial sheath loss rather than the persistent myelin reported after acute toxin exposure. We have added them in Result (lines 266–271).

The results reinforce the view that myelin removal and/or loss of trophic support during a narrow developmental window drive the long-term hyposynchrony and behavioral phenotypes we report. We have added the new subsection in discussion (lines 443–450) now in which we propose a two-phase model. Phase I (P3–P8): High early synchrony is generated by non-myelin mechanisms (e.g. transient gap junctions, shared climbing-fiber input). Phase II (P8-). As oligodendrocytes proliferate and ensheath axons, they fine-tune conduction velocity and stabilize the mature, low-synchrony network state. We believe these additions fully address the reviewer’s concerns.

(2) Surprisingly, the authors speculate about oligodendrocyte-mediated synaptic pruning without supportive data, shifting the focus away from the potential impact of myelination. Even if OLs perform synaptic pruning, OL depletion would likely maintain synchrony, yet the opposite was observed. Further characterisation of the model and the potential source of the effect is needed. 

We thank the reviewer for pointing out that our original discussion of oligodendrocyte-mediated synapse elimination was not directly supported by data in the present manuscript. Because we are actively analyzing this question in a separate, follow-up study, we have deleted the speculative passage to keep the current paper focused on the demonstrated, myelination-dependent effects. We believe this change sharpens the mechanistic narrative and fully addresses the reviewer’s concern.

(3) Improved characterization of the DTA model would add clarity. Although almost all infected cells are reported as OLs, quantification of infected OL-lineage cells (e.g., via Olig2 staining) would verify this. It remains possible that observed activity changes are driven by OL-independent demyelination effects. We suggest cross-staining with Iba1 and GFAP to rule out inflammation or gliosis. 

We thank the reviewer for this important suggestion and have expanded our histological characterization accordingly. First, to verify that DTA expression is confined to mature oligodendrocytes, we co-stained cerebellar sections collected 7 days after AAV-hMAG-mCherry injection with Olig2 (pan-OL lineage) and ASPA (mature OL marker) as shown in Figure S1C-D. Quantitative analysis revealed that 100 % of mCherry⁺ cells were Olig2⁺/ASPA⁺, whereas mCherry signal was virtually absent in Olig2⁺/ASPA⁻ immature oligodendrocytes. These data confirm that our DTA manipulation targets mature myelinating OLs rather than earlier lineage stages. We have added them in Result (lines 260–262).

Second, to examine indirect effects mediated by other glia, we performed cross-staining with IBA1 (microglia) and S100β (Bergmann). Cell density and fluorescence intensity for each marker were indistinguishable between control and DTA groups at P14 and P21 (Figure S2A-H). Thus, neither inflammation nor astro-/microgliosis accompanies OL ablation. We have added them in Result (lines 275–286).

Collectively, these results demonstrate that the observed desynchronization and behavioral phenotypes arise from specific loss of mature oligodendrocytes and their myelin, rather than from off-target viral expression or secondary glial responses.

(4) The use of an independent model of myelin loss, such as the inducible Myrf knockout mouse with a MAG promoter, to assess if oligodendrocyte loss causes temporary or sustained impacts, employing an extended knockout model like Myrf cKO with MAG-Cre viral methods would be advantageous.

We agree that distinguishing transient from enduring effects is critical. Importantly, our original submission already included data demonstrating a persistent deficit of PC population synchrony (Fig. 4, previous Fig. 3): (i) at P13-15—the early age after oligodendrocyte ablation—population synchrony is reduced, and (ii) the same deficit is still present in adults (P60–P70) despite full recovery of ASPA-positive cell density and MBP-area and -thickness (Fig. 2H-K, Fig. S1E, and Fig. 4). We also performed the ablation of oligodendrocytes after the third postnatal week. Despite a similar acute drop in ASPA-positive cells, neither population synchrony nor anxiety-, motor-, or social behaviors differed from littermate controls. Thus, extending myelin disruption beyond the developmental window does not exacerbate or prolong the phenotype, whereas a short perturbation within that window leaves a permanent timing defect. These findings strengthen our conclusion that it is the developmental oligodendrocyte/myelination program itself—rather than ongoing adult myelin production—that is essential for establishing stable network synchrony. We now highlight this point explicitly in the revised Discussion (lines 507–522).

(5) For statistical robustness, the use of non-parametric tests (Mann-Whitney) necessitates reporting the median instead of the mean as the authors do. Furthermore, as repeated measurements within the same animal are not independent, the authors should ideally use nested ANOVA (or nested t-test comparing two conditions) to validate their findings (Aarts et al., Nat. Neuroscience 2014). Alternatively use one-way ANOVA with each animal as a biological replicate, although this means that the distribution in the data sets per animal is lost.

We appreciate the reviewer’s guidance on appropriate statistical treatment. To address these concerns we have re-analyzed all datasets that contained multiple measurements per animal (e.g., fields of view, lobules, or trials) using nested statistics with animal as the higher-order unit. Specifically, we applied a two-level nested ANOVA when more than two groups were compared and a nested t-test when two conditions were present. The re-analysis confirmed all original conclusions. Because the nested models yielded comparable effect sizes to the Mann–Whitney tests, we have retained the mean ± SEM for ease of comparison with prior literature but now also report all values for each mouse in Table 1. In cases where a single measurement per mouse was compared between two groups, we used the Mann–Whitney test and present the results in the graphs as median values.

Minor Points 

(1) In all figures, please specify the ages at which each procedure was conducted, as demonstrated in Figure 2A.

All main and supplementary figures now specify the exact postnatal age.

(2) Clarify the selection criteria for regions of interest (ROI) in calcium imaging, and provide representative ROIs.

We appreciate the reviewer’s guidance. We have clarified that our ROI detection followed the protocol reported by our previous paper (Tanigawa et al., 2024, Communications Biology) (lines 177-178) and representative Purkinje cell ROIs are now shown in Fig. 2B.

(3) Include data on the proportion of climbing fiber or inferior olive neurons expressing Kir and the total number of neurons transfected, which would help contextualize the observed effects on PC synchronization and its broader implications for cerebellar circuit function.

We appreciate the reviewer’s guidance. New Fig. 7C summarizes the efficiency of AAV-GFP and AAV-Kir2.1-GFP injections into the inferior olive. Across 4 mice PCs with GFP-labeled CFs was detected in 19.3 ± 11.9 (mean ± S.D.) % for control and 26.2 ± 11.8 (mean ± S.D.) % for Kir2.1 of PCs. These numbers are reported in the Results (lines 373–375).

(4) Higher magnification images in Figures 1 and S3 would improve visual clarity. 

We have addressed the request for higher-magnification images in two ways. First, all panels in Figure S3 were placed on a larger canvas. Second, in Figure 1 we adjusted panel sizes to emphasize fine structure: panel 1C already represents an enlargement of the RFP positive cells shown in 1B, and panel 1H and 1J now occupies a wider span so that every ASPA-positive cell body can be distinguished. Should the reviewer still require an even closer view, we have additional ready for upload.

(5) Consider language editing to enhance overall clarity and readability.

The entire manuscript was edited to improve flow, consistency, and readability.

(6) Refine the discussion to align with the presented data.

We have refined the discussion.

Thank you once again for your constructive suggestions and comments. We believe these changes have improved the clarity and readability of our manuscript.

Reviewer #2 (Public review):

We appreciate Reviewer #2’s positive evaluation of our work and thank him/her for the constructive suggestions and comments. We followed these suggestions and comments and have conducted additional experiments. We have rewritten the manuscript and revised the figures according to the points Reviewer #1 mentioned. Our point-by-point responses to the comments are as follows.

Summary:

In this manuscript, the authors use genetic tools to ablate oligodendrocytes in the cerebellum during postnatal development. They show that the oligodendrocyte numbers return to normal post-weaning. Yet, the loss of oligodendrocytes during development seems to result in decreased synchrony of calcium transients in Purkinje neurons across the cerebellum. Further, there were deficits in social behaviors and motor coordination. Finally, they suppress activity in a subset of climbing fibers to show that it results in similar phenotypes in the calcium signaling and behavioral assays. They conclude that the behavioral deficits in the oligodendrocyte ablation experiments must result from loss of synchrony. 

Strengths:

Use of genetic tools to induce perturbations in a spatiotemporally specific manner.

We appreciate these positive evaluation.

Weaknesses: 

The main weakness in this manuscript is the lack of a cohesive causal connection between the experimental manipulation performed and the phenotypes observed. Though they have taken great care to induce oligodendrocyte loss specifically in the cerebellum and at specific time windows, the subsequent experiments do not address specific questions regarding the effect of this manipulation.

Calcium transients in Purkinje neurons are caused to a large extent by climbing fibers, but there is evidence for simple spikes to also underlie the dF/F signatures (Ramirez and Stell, Cell Reports, 2016).

We thank the reviewer for drawing attention to the work of Ramirez & Stell (2016), which showed that simple-spike bursts can elicit Ca²⁺ rises, but only in the soma and proximal dendrites of adult Purkinje cells. In our study, Regions of Interest were restricted to the dendritic arbor, where SS-evoked signals are essentially undetectable (Ramirez & Stell, 2016), whereas climbing-fiber complex spikes generate large, all-or-none transients (Good et al., 2017). Accordingly, even if a rare SS-driven event reached threshold it would likely fall outside our ROIs.

In addition, we directly imaged CF population activity by expressing GCaMP7f in inferior-olive neurons. Correlation analysis of CF boutons revealed that DTA ablation lowers CF–CF synchrony at P14 (new Fig. 3A–D). Because CF synchrony is a principal driver of Purkinje-cell co-activation, this reduction provides a mechanistic link between oligodendrocyte loss and the hyposynchrony we observe among Purkinje cells. Consistent with this interpretation, electrophysiological recordings showed that parallel-fiber EPSCs and inhibitory synaptic inputs onto Purkinje cells were unchanged by DTA treatment (Fig. 3E-H) , which makes it less likely that the reduced synchrony simply reflects changes in other excitatory or inhibitory synaptic drive.

That said, SS-dependent somatic Ca²⁺ signals could still influence downstream plasticity and long-term cerebellar function. In future work we therefore plan to combine somatic imaging with stage-specific oligodendrocyte manipulations to test whether SS-evoked Ca²⁺ dynamics are themselves modulated by oligodendrocyte support. We have added these descriptions in the Results (lines 288–294) and Discussion (lines 423–434).

Also, it is erroneous to categorize these calcium signals as signatures of "spontaneous activity" of Purkinje neurons as they can have dual origins.

Thank you for pointing out the potential ambiguity. In the revised manuscript we have clarified how we use the term “spontaneous activity” in the context of our measurements (lines 289-290). Our calcium imaging was restricted to the dendritic arbor of Purkinje cells, where calcium transients are dominated by climbing-fiber (CF) inputs (Ramirez & Stell, 2016; Good et al., 2017). Thus, the synchrony values reported here primarily reflect CF-driven complex spikes rather than mixed signals of dual origin. We have revised the Results section accordingly (lines 289–293) to make this measurement-specific limitation explicit.

Further, the effect of developmental oligodendrocyte ablation on the cerebellum has been previously reported by Mathis et al., Development, 2003. They report very severe effects such as the loss of molecular layer interneurons, stunted Purkinje neuron dendritic arbors, abnormal foliations, etc. In this context, it is hardly surprising that one would observe a reduction of synchrony in Purkinje neurons (perhaps due to loss of synaptic contacts, not only from CFs but also from granule cells).

We appreciate the reviewer’s comparison to Mathis et al. (2003). Mathis et al. used MBP–HSV-TK transgenic mice in which systemic FIAU treatment eliminates oligodendrocytes. When ablation began at P1, they observed severe dysmorphology—loss of molecular-layer interneurons, Purkinje-cell (PC) dendritic stunting, and abnormal foliation. Crucially, however, the same study reports that starting the ablation later (FIAU from P6-P20) left cerebellar cyto-architecture entirely normal.

Our AAV MAG-DTA paradigm resembles this later window. Our temporally restricted DTA protocol produces the same ‘late-onset’ profile—robust yet reversible hypomyelination with no loss of Purkinje cells, interneurons, dendritic length, or synaptic input (new Fig. S1–S2, Fig. 3E-H). The enduring hyposynchrony we report therefore cannot be attributed to the dramatic anatomical defects seen after prenatal ablation, but instead reveals a specific requirement for early-postnatal myelin in stabilizing PC synchrony, especially affecting CF-CF synchrony.

This clarification shows that we have carefully considered the Mathis model and that our findings not only replicate, but also extend the earlier work. We have added these description in Result (lines 273-286)

The last experiment with the expression of Kir2.1 in the inferior olive is hardly convincing.

We appreciate the reviewer’s concern and have reinforced the causal link between Purkinje-cell synchrony and behavior. To test whether restoring PC synchrony is sufficient to rescue behavior, we introduced a red-shifted opsin (AAV-L7-rsChrimine) into PCs of DTA mice raised to adulthood. During testing we delivered 590-nm light pulses (10 ms, 1 Hz) to the vermis, driving brief, population-wide spiking (new Fig. 8). This periodic re-synchronization left anxiety measures unchanged (open-field center time remained low) but rescued both motor coordination (rotarod latency normalized to control levels) and sociability (time spent with a novel mouse restored). The dissociation implies that distinct behavioral domains differ in their sensitivity to PC timing precision and confirms that reduced synchrony—not cell loss or gross circuit damage (Fig. S1F, S2)—is the primary driver of the motor and social deficits. Together, the optogenetic rescue establishes a bidirectional, mechanistic link between PC synchrony and behavior, addressing the reviewer’s reservations about the original experiment. We have added these descriptions in Result (lines 394-415)

In summary, while the authors used a specific tool to probe the role of developmental oligodendrocytes in cerebellar physiology and function, they failed to answer specific questions regarding this role, which they could have done with more fine-grained experimental analysis.

Thank you once again for your constructive suggestions and comments. We believe these changes have improved the clarity and readability of our manuscript.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Show that ODC loss is specific to the cerebellum.

We thank the reviewer for requesting additional evidence. To verify that oligodendrocyte ablation was confined to the cerebellum, we injected an AAV carrying mCherry under the human MAG promoter (AAV-hMAG-mCherry) into the cerebellum, and screened the whole brain one week later. As shown in the new Figure 1E–G, mCherry positive cells were present throughout the injected cerebellar cortex (Fig. 1E), but no fluorescent cells were detected in extracerebellar regions—including cerebral cortex, medulla, pons, midbrain. These data demonstrate that our viral approach are specific to the cerebellum, ruling out off-target demyelination elsewhere in the CNS as a contributor to the behavioral and synchrony phenotypes. We have added these descriptions in Result (lines 262-264)

(2) Characterize the gross morphology of the cerebellum at different developmental stages. Are major cell types all present? Major pathways preserved? 

We thank the reviewer for requesting additional evidence. To ensure that the developmental loss of oligodendrocytes did not globally disturb cerebellar architecture, we performed a comprehensive histological and electrophysiological survey during development. New data are presented (new Fig. S1–S2, Fig. 3E-H).

(1) Overall morphology. Low-magnification parvalbumin counterstaining revealed similar cerebellar area in DTA versus control mice at every age (Fig. S1F, G).

(2) Major neuronal classes. Quantification of parvalbumin-positive Purkinje cells and interneurons showed no differences in density between control and DTA (Fig. S2E, H, M, N, P). Purkinje dendritic arbors were not different between control and DTA (Fig. S2G, O).

(3) Excitatory and inhibitory synapse inputs. Miniature IPSCs and Parallel-fiber-EPSCs onto Purkinje cells were quantified; neither was differed between groups (Fig. 3E-G).

(4) Glial populations. IBA1-positive microglia and S100β-positive astrocytes exhibited normal density and marker intensity (Fig. S2).

Taken together, these analyses show that all major cell types are present at normal density, synaptic inputs from excitatory and inhibitory neurons are preserved, and gross cerebellar morphology is intact after DTA-mediated oligodendrocyte ablation.

(3) Recording of PNs to see whether the lack of synchrony is due to CFs or simple spikes.

We thank the reviewer for drawing attention to the work of Ramirez & Stell (2016), which showed that simple-spike bursts can elicit Ca²⁺ rises, but only in the soma and proximal dendrites of adult Purkinje cells. In our study, Regions of Interest were restricted to the dendritic arbor, where SS-evoked signals are essentially undetectable (Ramirez & Stell, 2016), whereas climbing-fiber complex spikes generate large, all-or-none transients (Good et al., 2017). Accordingly, even if a rare SS-driven event reached threshold it would likely fall outside our ROIs.

In addition, we directly imaged CF population activity by expressing GCaMP7f in inferior-olive neurons. Correlation analysis of CF boutons revealed that DTA ablation lowers CF–CF synchrony at P14 (new Fig. 3A–D). Because CF synchrony is a principal driver of Purkinje-cell co-activation, this reduction provides a mechanistic link between oligodendrocyte loss and the hyposynchrony we observe among Purkinje cells. Consistent with this interpretation, electrophysiological recordings showed that parallel-fiber EPSCs and inhibitory synaptic inputs onto Purkinje cells were unchanged by DTA treatment (Fig. 3E-H) , which makes it less likely that the reduced synchrony simply reflects changes in other excitatory or inhibitory synaptic drive.

That said, SS-dependent somatic Ca²⁺ signals could still influence downstream plasticity and long-term cerebellar function. In future work we therefore plan to combine somatic imaging with stage-specific oligodendrocyte manipulations to test whether SS-evoked Ca²⁺ dynamics are themselves modulated by oligodendrocyte support. We have added these descriptions in the Results (lines 301–312) and Discussion (lines 423–434).

(4) Is CF synapse elimination altered? Test using evoked EPSCs or staining methods.

We agree that directly testing whether oligodendrocyte loss disturbs climbing-fiber synapse elimination would provide a full mechanistic picture. We are already quantifying climbing fiber terminal number with vGluT2 immunostaining and recording evoked CF-EPSCs in the same DTA model; these data, together with an analysis of how population synchrony is involved in synapse elimination, will form the basis of a separate manuscript now in preparation. To keep the present paper focused on the phenomena we have rigorously documented—transient oligodendrocyte loss and the resulting long-lasting hyposynchrony and abnormal behaviors—we have removed the speculative sentence on oligodendrocyte-mediated synapse elimination. We believe this revision meets the reviewer’s request without over-extending the current dataset.

Thank you once again for your constructive suggestions and comments. We believe these changes have improved the clarity and readability of our manuscript.

The likelihood of it increases with social distance (no community) and with places where the underlying logic is different (vgl [[Waarheid en kennis kent historische periodes 20250914161603]] Foucault's periods of epistemic assumptions), at a smaller scale), clashes of differently positions 'Overton' type of windows of accepted discourse, and Rorty being forced wording the new in the language of the old. It's a language came underneath.

eLife Assessment

This valuable study investigates the relationship between pupil dilation and information gain during associative learning, using two different tasks. A key strength of this study is its exploration of pupil dilation beyond the immediate response period, extending analysis to later time windows after feedback, and it provides convincing evidence that pupillary response to information gain may be context-dependent during associative learning. The interpretation remains limited by task heterogeneity and unresolved contextual factors influencing pupil dynamics, but a range of interesting ideas are discussed.

Reviewer #1 (Public review):

Summary:

This study examines whether changes in pupil size index prediction-error-related updating during associative learning, formalised as information gain via Kullback-Leibler (KL) divergence. Across two independent tasks, pupil responses scaled with KL divergence shortly after feedback, with the timing and direction of the response varying by task. Overall, the work supports the view that pupil size reflects information-theoretic processes in a context-dependent manner.

Strengths:

This study provides a novel and convincing contribution by linking pupil dilation to information-theoretic measures, such as KL divergence, supporting Zénon's hypothesis that pupil responses reflect information gain during learning. The robust methodology, including two independent datasets with distinct task structures, enhances the reliability and generalisability of the findings. By carefully analysing early and late time windows, the authors capture the timing and direction of prediction-error-related responses, offering new insights into the temporal dynamics of model updating. The use of an ideal-learner framework to quantify prediction errors, surprise, and uncertainty provides a principled account of the computational processes underlying pupil responses. The work also highlights the critical role of task context in shaping the direction and magnitude of these effects, revealing the adaptability of predictive processing mechanisms. Importantly, the conclusions are supported by rigorous control analyses and preprocessing sanity checks, as well as convergent results from frequentist and Bayesian linear mixed-effects modelling approaches.

Weaknesses:

Some aspects of directionality remain context-dependent, and on current evidence cannot be attributed specifically to whether average uncertainty increases or decreases across trials. Differences between the two tasks (e.g., sensory modality and learning regime) limit direct comparisons of effect direction and make mechanistic attribution cautious. In addition, subjective factors such as confidence were not measured and could influence both prediction-error signals and pupil responses. Importantly, the authors explicitly acknowledge these limitations, and the manuscript clearly frames them as areas for future work rather than settled conclusions.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study examines whether changes in pupil size index prediction-error-related updating during associative learning, formalised as information gain via Kullback-Leibler (KL) divergence. Across two independent tasks, pupil responses scaled with KL divergence shortly after feedback, with the timing and direction of the response varying by task. Overall, the work supports the view that pupil size reflects information-theoretic processes in a context-dependent manner.

Strengths:

This study provides a novel and convincing contribution by linking pupil dilation to informationtheoretic measures, such as KL divergence, supporting Zénon's hypothesis that pupil responses reflect information gain during learning. The robust methodology, including two independent datasets with distinct task structures, enhances the reliability and generalisability of the findings. By carefully analysing early and late time windows, the authors capture the timing and direction of prediction-error-related responses, oPering new insights into the temporal dynamics of model updating. The use of an ideal-learner framework to quantify prediction errors, surprise, and uncertainty provides a principled account of the computational processes underlying pupil responses. The work also highlights the critical role of task context in shaping the direction and magnitude of these ePects, revealing the adaptability of predictive processing mechanisms. Importantly, the conclusions are supported by rigorous control analyses and preprocessing sanity checks, as well as convergent results from frequentist and Bayesian linear mixed-ePects modelling approaches.

Weaknesses:

Some aspects of directionality remain context-dependent, and on current evidence cannot be attributed specifically to whether average uncertainty increases or decreases across trials. DiPerences between the two tasks (e.g., sensory modality and learning regime) limit direct comparisons of ePect direction and make mechanistic attribution cautious. In addition, subjective factors such as confidence were not measured and could influence both predictionerror signals and pupil responses. Importantly, the authors explicitly acknowledge these limitations, and the manuscript clearly frames them as areas for future work rather than settled conclusions.

Reviewer #2 (Public review):

Summary:

The authors investigate whether pupil dilation reflects information gain during associative learning, formalised as Kullback-Leibler divergence within an ideal observer framework. They examine pupil responses in a late time window after feedback and compare these to informationtheoretic estimates (information gain, surprise, and entropy) derived from two diPerent tasks with contrasting uncertainty dynamics.

Strength:

The exploration of task evoked pupil dynamics beyond the immediate response/feedback period and then associating them with model estimates was interesting and inspiring. This oPered a new perspective on the relationship between pupil dilation and information processing.

Weakness:

However, the interpretability of the findings remains constrained by the fundamental diPerences between the two tasks (stimulus modality, feedback type, and learning structure), which confound the claimed context-dependent ePects. The later time-window pupil ePects, although intriguing, are small in magnitude and may reflect residual noise or task-specific arousal fluctuations rather than distinct information-processing signals. Thus, while the study oPers valuable methodological insight and contributes to ongoing debates about the role of the pupil in cognitive inference, its conclusions about the functional significance of late pupil responses should be treated with caution.

Reviewer #3 (Public review):

Summary:

Thank you for inviting me to review this manuscript entitled "Pupil dilation oPers a time-window on prediction error" by Colizoli and colleagues. The study examines prediction errors, information gain (Kullback-Leibler [KL] divergence), and uncertainty (entropy) from an information-theory perspective using two experimental tasks and pupillometry. The authors aim to test a theoretical proposal by Zénon (2019) that the pupil response reflects information gain (KL divergence). The conclusion of this work is that (post-feedback) pupil dilation in response to information gain is context dependent.

Strengths:

Use of an established Bayesian model to compute KL divergence and entropy.

Pupillometry data preprocessing and multiple robustness checks.

Weaknesses:

Operationalization of prediction errors based on frequency, accuracy, and their interaction:

The authors rely on a more model-agnostic definition of the prediction error in terms of stimulus frequency ("unsigned prediction error"), accuracy, and their interaction ("signed prediction error"). While I see the point, I would argue that this approach provides a simple approximation of the prediction error, but that a model-based approach would be more appropriate.

Model validation:

My impression is that the ideal learner model should work well in this case. However, the authors don't directly compare model behavior to participant behavior ("posterior predictive checks") to validate the model. Therefore, it is currently unclear if the model-derived terms like KL divergence and entropy provide reasonable estimates for the participant data.

Lack of a clear conclusion:

The authors conclude that this study shows for the first time that (post-feedback) pupil dilation in response to information gain is context dependent. However, the study does not oPer a unifying explanation for such context dependence. The discussion is quite detailed with respect to taskspecific ePects, but fails to provide an overarching perspective on the context-dependent nature of pupil signatures of information gain. This seems to be partly due to the strong diPerences between the experimental tasks.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I highly appreciate the care and detail in the authors' response and thank them for the ePort invested in revising the manuscript. They addressed the core concerns to a high standard, and the manuscript has substantially improved in methodological rigour (through additional controls/sanity checks and complementary mixed-ePects analyses) and in clarity of interpretation (by explicitly acknowledging context-dependence and tempering stronger claims). The present version reads clearly and is much strengthened overall. I only have a few minor points below:

Minor suggestions:

Abstract:

In the abstract KL is introduced as abbreviation, but at first occurence it should be written out as "Kullback-Leibler (KL)" for readers not familiar with it.

We thank the reviewer for catching this error. It has been correct in the version of record.

Methods:

I appreciate the additional bayesian LME analysis. I only had a few things that I thought were missing from knowing the parameters: 1) what was the target acceptance rate (default of .95?), 2) which family was used to model the response distribution: (default) "gaussian" or robust "student-t"? Depending on the data a student-t would be preferred, but since the author's checked the fit & the results corroborate the correlation analysis, using the default would also be fine! Just add the information for completeness.

Thank you for bringing this to our attention. We have now noted that default parameters were used in all cases unless otherwise mentioned. 

Thank you once again for your time and consideration.

Reviewer #2 (Recommendations for the authors):

Thanks to the authors' ePort on revision. I am happy with this new version of manuscript.

Thank you once again for your time and consideration.

Reviewer #3 (Recommendations for the authors):

(1) Regarding comments #3 and #6 (first round) on model validation and posterior predictive checks, the authors replied that since their model is not a "generative" one, they can't perform posterior predictive checks. Crucially, in eq. 2, the authors present the p{tilde}^j_k variable denoting the learned probability of event k on trial j. I don't see why this can't be exploited for simulations. In my opinion, one could (and should) generate predictions based on this variable. The simplest implementation would translate the probability into a categorical choice (w/o fitting any free parameter). Based on this, they could assess whether the model and data are comparable.

We thank the reviewer for this clarification. The reviewer suggests using the probability distributions at each trial to predict which event should be chosen on each trial. More specifically, the event(s) with the highest probability on trial j could be used to generate a prediction for the choice of the participant on trial j. We agree that this would indeed be an interesting analysis. However, the response options of each task are limited to two-alternatives. In the cue-target task, four events are modeled (representing all possible cue-target conditions) while the participants’ response options are only “left” and “right”. Similarly, in the letter-color task, 36 events are modeled while the participants’ response options are “match” and “no-match”. In other words, we do not know which event (either four or 36, for the two tasks) the participant would have indicated on each trial. As an approximation to this fine-grained analysis, we investigated the relationship between the information-theoretic variables separately for error and correct trials. Our rationale was that we would have more insight into how the model fits depended on the participants’ actual behavior as compared with the ideal learner model.

(2) I recommend providing a plot of the linear mixed model analysis of the pupil data. Currently, results are only presented in the text and tables, but a figure would be much more useful.

We thank the reviewer for the suggestion to add a plot of the linear mixed model results. We appreciate the value of visualizing model estimates; however, we feel that the current presentation in the text and tables clearly conveys the relevant findings. For this reason, and to avoid further lengthening the manuscript, we prefer to retain the current format.

(3) I would consider only presenting the linear mixed ePects for the pupil data in the main results, and the correlation results in the supplement. It is currently quite long.

We thank the reviewer for this recommendation. We agree that the results section is detailed; however, we consider the correlation analyses to be integral to the interpretation of the pupil data and therefore prefer to keep them in the main text rather than move them to the supplement.

The following is the authors’ response to the original reviews

eLife Assessment

This important study seeks to examine the relationship between pupil size and information gain, showing opposite effects dependent upon whether the average uncertainty increases or decreases across trials. Given the broad implications for learning and perception, the findings will be of broad interest to researchers in cognitive neuroscience, decision-making, and computational modelling. Nevertheless, the evidence in support of the particular conclusion is at present incomplete - the conclusions would be strengthened if the authors could both clarify the differences between model-updating and prediction error in their account and clarify the patterns in the data.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study investigates whether pupil dilation reflects prediction error signals during associative learning, defined formally by Kullback-Leibler (KL) divergence, an information-theoretic measure of information gain. Two independent tasks with different entropy dynamics (decreasing and increasing uncertainty) were analyzed: the cue-target 2AFC task and the lettercolor 2AFC task. Results revealed that pupil responses scaled with KL divergence shortly after feedback onset, but the direction of this relationship depended on whether uncertainty (entropy) increased or decreased across trials. Furthermore, signed prediction errors (interaction between frequency and accuracy) emerged at different time windows across tasks, suggesting taskspecific temporal components of model updating. Overall, the findings highlight that pupil dilation reflects information-theoretic processes in a complex, context-dependent manner.

Strengths:

This study provides a novel and convincing contribution by linking pupil dilation to informationtheoretic measures, such as KL divergence, supporting Zénon's hypothesis that pupil responses reflect information gained during learning. The robust methodology, including two independent datasets with distinct entropy dynamics, enhances the reliability and generalisability of the findings. By carefully analysing early and late time windows, the authors capture the temporal dynamics of prediction error signals, offering new insights into the timing of model updates. The use of an ideal learner model to quantify prediction errors, surprise, and entropy provides a principled framework for understanding the computational processes underlying pupil responses. Furthermore, the study highlights the critical role of task context - specifically increasing versus decreasing entropy - in shaping the directionality and magnitude of these effects, revealing the adaptability of predictive processing mechanisms.

Weaknesses:

While this study offers important insights, several limitations remain. The two tasks differ significantly in design (e.g., sensory modality and learning type), complicating direct comparisons and limiting the interpretation of differences in pupil dynamics. Importantly, the apparent context-dependent reversal between pupil constriction and dilation in response to feedback raises concerns about how these opposing effects might confound the observed correlations with KL divergence. 

We agree with the reviewer’s concerns and acknowledge that the speculation concerning the directional effect of entropy across trials can not be fully substantiated by the current study. As the reviewer points out, the directional relationship between pupil dilation and information gain must be due to other factors, for instance, the sensory modality, learning type, or the reversal between pupil constriction and dilation across the two tasks. Also, we would like to note that ongoing experiments in our lab already contradict our original speculation. In line with the reviewer’s point, we noted these differences in the section on “Limitations and future research” in the Discussion. To better align the manuscript with the above mentioned points, we have made several changes in the Abstract, Introduction and Discussion summarized below: 

We have removed the following text from the Abstract and Introduction: “…, specifically related to increasing or decreasing average uncertainty (entropy) across trials.”

We have edited the following text in the Introduction (changes in italics) (p. 5):

“We analyzed two independent datasets featuring distinct associative learning paradigms, one characterized by increasing entropy and the other by decreasing entropy as the tasks progressed. By examining these different tasks, we aimed to identify commonalities (if any) in the results across varying contexts. Additionally, the contrasting directions of entropy in the two tasks enabled us to disentangle the correlation between stimulus-pair frequency and information gain in the postfeedback pupil response.

We have removed the following text from the Discussion:

“…and information gain in fact seems to be driven by increased uncertainty.”

“We speculate that this difference in the direction of scaling between information gain and the pupil response may depend on whether entropy was increasing or decreasing across trials.” 

“…which could explain the opposite direction of the relationship between pupil dilation and information gain”

“… and seems to relate to the direction of the entropy as learning progresses (i.e., either increasing or decreasing average uncertainty).” 

We have edited the following texts in the Discussion (changes in italics):

“For the first time, we show that the direction of the relationship between postfeedback pupil dilation and information gain (defined as KL divergence) was context dependent.” (p. 29):

Finally, we have added the following correction to the Discussion (p. 30):

“Although it is tempting to speculate that the direction of the relationship between pupil dilation and information gain may be due to either increasing or decreasing entropy as the task progressed, we must refrain from this conclusion. We note that the two tasks differ substantially in terms of design with other confounding variables and therefore cannot be directly compared to one another. We expand on these limitations in the section below (see Limitations and future research).”

Finally, subjective factors such as participants' confidence and internal belief states were not measured, despite their potential influence on prediction errors and pupil responses.

Thank you for the thoughtful comment. We agree with the reviewer that subjective factors, such as participants' confidence, can be important in understanding prediction errors and pupil responses. As per the reviewer’s point, we have included the following limitation in the Discussion (p. 33): 

“Finally, while we acknowledge the potential relevance of subjective factors, such as the participants’ overt confidence reports, in understanding prediction errors and pupil responses, the current study focused on the more objective, model-driven measure of information-theoretic variables. This approach aligns with our use of the ideal learner model, which estimates information-theoretic variables while being agnostic about the observer's subjective experience itself. Future research is needed to explore the relationship between information-gain signals in pupil dilation and the observer’s reported experience of or awareness about confidence in their decisions.” 

Reviewer #2 (Public review):

Summary:

The authors proposed that variability in post-feedback pupillary responses during the associative learning tasks can be explained by information gain, which is measured as KL divergence. They analysed pupil responses in a later time window (2.5s-3s after feedback onset) and correlated them with information-theory-based estimates from an ideal learner model (i.e., information gain-KL divergence, surprise-subjective probability, and entropy-average uncertainty) in two different associative decision-making tasks.

Strength:

The exploration of task-evoked pupil dynamics beyond the immediate response/feedback period and then associating them with model estimates was interesting and inspiring. This offered a new perspective on the relationship between pupil dilation and information processing.

Weakness:

However, disentangling these later effects from noise needs caution. Noise in pupillometry can arise from variations in stimuli and task engagement, as well as artefacts from earlier pupil dynamics. The increasing variance in the time series of pupillary responses (e.g., as shown in Figure 2D) highlights this concern.

It's also unclear what this complicated association between information gain and pupil dynamics actually means. The complexity of the two different tasks reported made the interpretation more difficult in the present manuscript.

We share the reviewer’s concerns. To make this point come across more clearly, we have added the following text to the Introduction (p. 5):

“The current study was motivated by Zenon’s hypothesis concerning the relationship between pupil dilation and information gain, particularly in light of the varying sources of signal and noise introduced by task context and pupil dynamics. By demonstrating how task context can influence which signals are reflected in pupil dilation, and highlighting the importance of considering their temporal dynamics, we aim to promote a more nuanced and model-driven approach to cognitive research using pupillometry.”

Reviewer #3 (Public review):

Summary:

This study examines prediction errors, information gain (Kullback-Leibler [KL] divergence), and uncertainty (entropy) from an information-theory perspective using two experimental tasks and pupillometry. The authors aim to test a theoretical proposal by Zénon (2019) that the pupil response reflects information gain (KL divergence). In particular, the study defines the prediction error in terms of KL divergence and speculates that changes in pupil size associated with KL divergence depend on entropy. Moreover, the authors examine the temporal characteristics of pupil correlates of prediction errors, which differed considerably across previous studies that employed different experimental paradigms. In my opinion, the study does not achieve these aims due to several methodological and theoretical issues.

Strengths:

(1)  Use of an established Bayesian model to compute KL divergence and entropy.

(2)  Pupillometry data preprocessing, including deconvolution.

Weaknesses:

(1) Definition of the prediction error in terms of KL divergence:

I'm concerned about the authors' theoretical assumption that the prediction error is defined in terms of KL divergence. The authors primarily refer to a review article by Zénon (2019): "Eye pupil signals information gain". It is my understanding that Zénon argues that KL divergence quantifies the update of a belief, not the prediction error: "In short, updates of the brain's internal model, quantified formally as the Kullback-Leibler (KL) divergence between prior and posterior beliefs, would be the common denominator to all these instances of pupillary dilation to cognition." (Zénon, 2019).

From my perspective, the update differs from the prediction error. Prediction error refers to the difference between outcome and expectation, while update refers to the difference between the prior and the posterior. The prediction error can drive the update, but the update is typically smaller, for example, because the prediction error is weighted by the learning rate to compute the update. My interpretation of Zénon (2019) is that they explicitly argue that KL divergence defines the update in terms of the described difference between prior and posterior, not the prediction error.

The authors also cite a few other papers, including Friston (2010), where I also could not find a definition of the prediction error in terms of KL divergence. For example [KL divergence:] "A non-commutative measure of the non-negative difference between two probability distributions." Similarly, Friston (2010) states: Bayesian Surprise - "A measure of salience based on the Kullback-Leibler divergence between the recognition density (which encodes posterior beliefs) and the prior density. It measures the information that can be recognized in the data." Finally, also in O'Reilly (2013), KL divergence is used to define the update of the internal model, not the prediction error.

The authors seem to mix up this common definition of the model update in terms of KL divergence and their definition of prediction error along the same lines. For example, on page 4: "KL divergence is a measure of the difference between two probability distributions. In the context of predictive processing, KL divergence can be used to quantify the mismatch between the probability distributions corresponding to the brain's expectations about incoming sensory input and the actual sensory input received, in other words, the prediction error (Friston, 2010; Spratling, 2017)."

Similarly (page 23): "In the current study, we investigated whether the pupil's response to decision outcome (i.e., feedback) in the context of associative learning reflects a prediction error as defined by KL divergence."

This is problematic because the results might actually have limited implications for the authors' main perspective (i.e., that the pupil encodes prediction errors) and could be better interpreted in terms of model updating. In my opinion, there are two potential ways to deal with this issue:

(a) Cite work that unambiguously supports the perspective that it is reasonable to define the prediction error in terms of KL divergence and that this has a link to pupillometry. In this case, it would be necessary to clearly explain the definition of the prediction error in terms of KL divergence and dissociate it from the definition in terms of model updating.

(b) If there is no prior work supporting the authors' current perspective on the prediction error, it might be necessary to revise the entire paper substantially and focus on the definition in terms of model updating.

We thank the reviewer for pointy out these inconsistencies in the manuscript and appreciate their suggestions for improvement. We take approach (a) recommended by the reviewer, and provide our reasoning as to why prediction error signals in pupil dilation are expected to correlate with information gain (defined as the KL divergence between posterior and prior belief distributions). This can be found in a new section in the introduction, copied here for convenience (p. 3-4):

“We reasoned that the link between prediction error signals and information gain in pupil dilation is through precision-weighting. Precision refers to the amount of uncertainty (inverse variance) of both the prior belief and sensory input in the prediction error signals [6,64–67]. More precise prediction errors receive more weighting, and therefore, have greater influence on model updating processes. The precisionweighting of prediction error signals may provide a mechanism for distinguishing between known and unknown sources of uncertainty, related to the inherent stochastic nature of a signal versus insufficient information of the part of the observer, respectively [65,67,68]. In Bayesian frameworks, information gain is fundamentally linked to prediction error, modulated by precision [65,66,69–75]. In non-hierarchical Bayesian models, information gain can be derived as a function of prediction errors and the precision of the prior and likelihood distributions, a relationship that can be approximately linear [70]. In hierarchical Bayesian inference, the update in beliefs (posterior mean changes) at each level is proportional to the precision-weighted prediction error; this update encodes the information gained from new observations [65,66,69,71,72]. Neuromodulatory arousal systems are well-situated to act as precision-weighting mechanisms in line with predictive processing frameworks [76,77]. Empirical evidence suggests that neuromodulatory systems broadcast precisionweighted prediction errors to cortical regions [11,59,66,78]. Therefore, the hypothesis that feedback-locked pupil dilation reflects a prediction error signal is similarly in line with Zenon’s main claim that pupil dilation generally reflects information gain, through precision-weighting of the prediction error. We expected a prediction error signal in pupil dilation to be proportional to the information gain.”

We have referenced previous work that has linked prediction error and information gain directly (p. 4): “The KL divergence between posterior and prior belief distributions has been previously considered to be a proxy of (precision-weighted) prediction errors [68,72].”

We have taken the following steps to remedy this error of equating “prediction error” directly with the information gain.

First, we have replaced “KL divergence” with “information gain” whenever possible throughout the manuscript for greater clarity. 

Second, we have edited the section in the introduction defining information gain substantially (p. 4): 

“Information gain can be operationalized within information theory as the KullbackLeibler (KL) divergence between the posterior and prior belief distributions of a Bayesian observer, representing a formalized quantity that is used to update internal models [29,79,80]. Itti and Baldi (2005)81 termed the KL divergence between posterior and prior belief distributions as “Bayesian surprise” and showed a link to the allocation of attention. The KL divergence between posterior and prior belief distributions has been previously considered to be a proxy of (precision-weighted) prediction errors[68,72]. According to Zénon’s hypothesis, if pupil dilation reflects information gain during the observation of an outcome event, such as feedback on decision accuracy, then pupil size will be expected to increase in proportion to how much novel sensory evidence is used to update current beliefs [29,63]. ” 

Finally, we have made several minor textual edits to the Abstract and main text wherever possible to further clarify the proposed relationship between prediction errors and information gain.

(2) Operationalization of prediction errors based on frequency, accuracy, and their interaction:

The authors also rely on a more model-agnostic definition of the prediction error in terms of stimulus frequency ("unsigned prediction error"), accuracy, and their interaction ("signed prediction error"). While I see the point here, I would argue that this approach offers a simple approximation to the prediction error, but it is possible that factors like difficulty and effort can influence the pupil signal at the same time, which the current approach does not take into account. I recommend computing prediction errors (defined in terms of the difference between outcome and expectation) based on a simple reinforcement-learning model and analyzing the data using a pupillometry regression model in which nuisance regressors are controlled, and results are corrected for multiple comparisons.

We agree with the reviewer’s suggestion that alternatively modeling the data in a reinforcement learning paradigm would be fruitful. We adopted the ideal learner model as we were primarily focused on Information Theory, stemming from our aim to test Zenon’s hypothesis that information gain drives pupil dilation. However, we agree with the reviewer that it is worthwhile to pursue different modeling approaches in future work. We have now included a complementary linear mixed model analysis in which we controlled for the effects of the information-theoretic variables on one another, while also including the nuisance regressors of pre-feedback baseline pupil dilation and reaction times (explained in more detail below in our response to your point #4). Results including correction for multiple comparisons was reported for all pupil time course data as detailed in Methods section 2.5. 

(3) The link between model-based (KL divergence) and model-agnostic (frequency- and accuracy-based) prediction errors:

I was expecting a validation analysis showing that KL divergence and model-agnostic prediction errors are correlated (in the behavioral data). This would be useful to validate the theoretical assumptions empirically.

The model limitations and the operalization of prediction error in terms of post-feedback processing do not seem to allow for a comparison of information gain and model-agnostic prediction errors in the behavioral data for the following reasons. First, the simple ideal learner model used here is not a generative model, and therefore, cannot replicate or simulate the participants responses (see also our response to your point #6 “model validation” below). Second, the behavioral dependent variables obtained are accuracy and reaction times, which both occur before feedback presentation. While accuracy and reaction times can serve as a marker of the participant’s (statistical) confidence/uncertainty following the decision interval, these behavioral measures cannot provide access to post-feedback information processing. The pupil dilation is of interest to us because the peripheral arousal system is able to provide a marker of post-feedback processing. Through the analysis presented in Figure 3, we indeed aimed to make the comparison of the model-based information gain to the model-agnostic prediction errors via the proxy variable of post-feedback pupil dilation instead of behavioral variables. To bridge the gap between the “behaviorally agnostic” model parameters and the actual performance of the participants, we examined the relationship between the model-based information gain and the post-feedback pupil dilation separately for error and correct trials as shown in Figure 3D-F & Figure 3J-L. We hope this addresses the reviewers concern and apologize in case we did not understand the reviewers suggestion here.

(4) Model-based analyses of pupil data:

I'm concerned about the authors' model-based analyses of the pupil data. The current approach is to simply compute a correlation for each model term separately (i.e., KL divergence, surprise, entropy). While the authors do show low correlations between these terms, single correlational analyses do not allow them to control for additional variables like outcome valence, prediction error (defined in terms of the difference between outcome and expectation), and additional nuisance variables like reaction time, as well as x and y coordinates of gaze.

Moreover, including entropy and KL divergence in the same regression model could, at least within each task, provide some insights into whether the pupil response to KL divergence depends on entropy. This could be achieved by including an interaction term between KL divergence and entropy in the model.

In line with the reviewer’s suggestions, we have included a complementary linear mixed model analysis in which we controlled for the effects of the information-theoretic variables on one another, while also including the nuisance regressors of pre-feedback baseline pupil dilation and reaction times. We compared the performance of two models on the post-feedback pupil dilation in each time window of interest: Modle 1 had no interaction between information gain and entropy and Model 2 included an interaction term as suggested. We did not include the x- and y- coordinates of gaze in the mixed linear model analysis, as there are multiple values of these coordinates per trial. Furthermore, regressing out the x and y- coordinates of gaze can potentially remove signal of interest in the pupil dilation data in addition to the gaze-related confounds and we did not measure absolute pupil size (Mathôt, Melmi & Castet, 2015; Hayes & Petrov, 2015). We present more sanity checks on the pre-processing pipeline as recommended by Reviewer 1.  

This new analysis resulted in several additions to the Methods (see Section 2.5) and Results. In sum, we found that including an interaction term for information gain and entropy did not lead to better model fits, but sometimes lead to significantly worse fits. Overall, the results of the linear mixed model corroborated the “simple” correlation analysis across the pupil time course while accounting for the relationship to the pre-feedback baseline pupil and preceeding reaction time differences. There was only one difference to note between the correlation and linear mixed modeling analyses: for the error trials in the cue-target 2AFC task, including entropy in the model accounted for the variance previously explained by surprise.

(5) Major differences between experimental tasks:

More generally, I'm not convinced that the authors' conclusion that the pupil response to KL divergence depends on entropy is sufficiently supported by the current design. The two tasks differ on different levels (stimuli, contingencies, when learning takes place), not just in terms of entropy. In my opinion, it would be necessary to rely on a common task with two conditions that differ primarily in terms of entropy while controlling for other potentially confounding factors. I'm afraid that seemingly minor task details can dramatically change pupil responses. The positive/negative difference in the correlation with KL divergence that the authors interpret to be driven by entropy may depend on another potentially confounding factor currently not controlled.

We agree with the reviewer’s concerns and acknowledge that the speculation concerning the directional effect of entropy across trials can not be fully substantiated by the currect study. We note that Review #1 had a similar concern. Our response to Reviewer #1 addresses this concern of Reviewer #3 as well. To better align the manuscript with the above mentioned points, we have made several changes that are detailed in our response to Reviewer #1’s public review (above). 

(6) Model validation:

My impression is that the ideal learner model should work well in this case. However, the authors don't directly compare model behavior to participant behavior ("posterior predictive checks") to validate the model. Therefore, it is currently unclear if the model-derived terms like KL divergence and entropy provide reasonable estimates for the participant data.

Based on our understanding, posterior predictive checks are used to assess the goodness of fit between generated (or simulated) data and observed data. Given that the “simple” ideal learner model employed in the current study is not a generative model, a posterior predictive check would not apply here (Gelman, Carlin, Stern, Dunson, Vehtari, & Rubin (2013). The ideal learner model is unable to simulate or replicate the participants’ responses and behaviors such as accuracy and reaction times; it simply computes the probability of seeing each stimulus type at each trial based on the prior distribution and the exact trial order of the stimuli presented to each participant. The model’s probabilities are computed directly from a Dirichlet distribution of values that represent the number of occurences of each stimulus-pair type for each task. The information-theoretic variables are then directly computed from these probabilities using standard formulas. The exact formulas used in the ideal learner model can be found in section 2.4.

We have now included a complementary linear mixed model analysis which also provides insight into the amount of explained variance of these information-theoretic predictors on the post-feedback pupil response, while also including the pre-feedback baseline pupil and reaction time differences (see section 3.3, Tables 3 & 4). The R² values ranged from 0.16 – 0.50 across all conditions tested.

(7) Discussion:

The authors interpret the directional effect of the pupil response w.r.t. KL divergence in terms of differences in entropy. However, I did not find a normative/computational explanation supporting this interpretation. Why should the pupil (or the central arousal system) respond differently to KL divergence depending on differences in entropy?

The current suggestion (page 24) that might go in this direction is that pupil responses are driven by uncertainty (entropy) rather than learning (quoting O'Reilly et al. (2013)). However, this might be inconsistent with the authors' overarching perspective based on Zénon (2019) stating that pupil responses reflect updating, which seems to imply learning, in my opinion. To go beyond the suggestion that the relationship between KL divergence and pupil size "needs more context" than previously assumed, I would recommend a deeper discussion of the computational underpinnings of the result.

Since we have removed the original speculative conclusion from the manuscript, we will refrain from discussing the computational underpinnings of a potential mechanism. To note as mentioned above, we have preliminary data from our own lab that contradicts our original hypothesis about the relationship between entropy and information gain on the post-feedback pupil response. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Apart from the points raised in the public review above, I'd like to use the opportunity here to provide a more detailed review of potential issues, questions, and queries I have:

(1) Constriction vs. Dilation Effects:

The study observes a context-dependent relationship between KL divergence and pupil responses, where pupil dilation and constriction appear to exhibit opposing effects. However, this phenomenon raises a critical concern: Could the initial pupil constriction to visual stimuli (e.g., in the cue-target task) confound correlations with KL divergence? This potential confound warrants further clarification or control analyses to ensure that the observed effects genuinely reflect prediction error signals and are not merely a result of low-level stimulus-driven responses.

We agree with the reviewers concern and have added the following information to the limitations section in the Discussion (changes in italics below; p. 32-33).

“First, the two associative learning paradigms differed in many ways and were not directly comparable. For instance, the shape of the mean pupil response function differed across the two tasks in accordance with a visual or auditory feedback stimulus (compare Supplementary Figure 3A with Supplementary Figure 3D), and it is unclear whether these overall response differences contributed to any differences obtained between task conditions within each task. We are unable to rule out whether so-called “low level” effects such as the initial constriction to visual stimuli in the cue-target 2AFC task as compared with the dilation in response auditory stimuli in letter-color 2AFC task could confound correlations with information gain. Future work should strive to disentangle how the specific aspects of the associative learning paradigms relate to prediction errors in pupil dilation by systematically manipulating design elements within each task.”

Here, I also was curious about Supplementary Figure 1, showing 'no difference' between the two tones (indicating 'error' or 'correct'). Was this the case for FDR-corrected or uncorrected cluster statistics? Especially since the main results also showed sig. differences only for uncorrected cluster statistics (Figure 2), but were n.s. for FDR corrected. I.e. can we be sure to rule out a confound of the tones here after all?

As per the reviewer’s suggestion, we verified that there were also no significant clusters after feedback onset before applying the correction for multiple comparisons. We have added this information to Supplemenatary section 1.2 as follows: 

“Results showed that the auditory tone dilated pupils on average (Supplementary Figure 1C). Crucially, however, the two tones did not differ from one another in either of the time windows of interest (Supplementary Figure 1D; no significant time points after feedback onset were obtained either before or after correcting for multiple comparisons using cluster-based permutation methods; see Section 2.5.” 

Supplementary Figure 1 is showing effects cluster-corrected for multiple comparisons using cluster-based permutation tests from the MNE software package in Python (see Methods section 2.5). We have clarified that the cluster-correction was based on permutation testing in the figure legend. 

(2) Participant-Specific Priors:

The ideal learner models do not account for individualised priors, assuming homogeneous learning behaviour across participants. Could incorporating participant-specific priors better reflect variability in how individuals update their beliefs during associative learning?

We have clarified in the Methods (see section 2.4) that the ideal learner models did account for participant-specific stimuli including participant-specific priors in the letter-color 2AFC task. We have added the following texts: 

“We also note that while the ideal learner model for the cue-target 2AFC task used a uniform (flat) prior distribution for all participants, the model parameters were based on the participant-specific cue-target counterbalancing conditions and randomized trial order.” (p. 13)

“The prior distributions used for the letter-color 2AFC task were estimated from the randomized letter-color pairs and randomized trial order presentation in the preceding odd-ball task; this resulted in participant-specific prior distributions for the ideal learner model of the letter-color 2AFC task. The model parameters were likewise estimated from the (participant-specific) randomized trial order presented in the letter-color 2AFC task.” (p. 13)

(3) Trial-by-Trial Variability:

The analysis does not account for random effects or inter-trial variability using mixed-effects models. Including such models could provide a more robust statistical framework and ensure the observed relationships are not influenced by unaccounted participant- or trial-specific factors.

We have included a complementary linear mixed model analysis in which “subject” was modeled as a random effect on the post-feedback pupil response in each time window of interest and for each task. Across all trials, the results of the linear mixed model corroborated the “simple” correlation analysis across the pupil time course while accounting for the relationship to the prefeedback baseline pupil and preceeding reaction time differences (see section 3.3, Tables 3 & 4).

(4) Preprocessing/Analysis choices:

Before anything else, I'd like to highlight the authors' effort in providing public code (and data) in a very readable and detailed format!

We appreciate the compliment - thank you for taking the time to look at the data and code provided.

I found the idea of regressing the effect of Blinks/Saccades on the pupil trace intriguing. However, I miss a complete picture here to understand how well this actually worked, especially since it seems to be performed on already interpolated data. My main points here are:

(4.1) Why is the deconvolution performed on already interpolated data and not on 'raw' data where there are actually peaks of information to fit?

To our understanding, at least one critical reason for interpolating the data before proceeding with the deconvolution analysis is that the raw data contain many missing values (i.e., NaNs) due to the presence of blinks. Interpolating over the missing data first ensures that there are valid numerical elements in the linear algebra equations. We refer the reviewer to the methods detailed in Knapen et al. (2016) for more details on this pre-processing method. 

(4.2) What is the model fit (e.g. R-squared)? If this was a poor fit for the regressors in the first place, can we trust the residuals (i.e. clean pupil trace)? Is it possible to plot the same Pupil trace of Figure 1D with a) the 'raw' pupil time-series, b) after interpolation only (both of course also mean-centered for comparison), on top of the residuals after deconvolution (already presented), so we can be sure that this is not driving the effects in a 'bad' way? I'd just like to make sure that this approach did not lead to artefacts in the residuals rather than removing them.

We thank the reviewer for this suggestion. In the Supplementary Materials, we have included a new figure (Supplementary Figure 2, copied below for convience), which illustrates the same conditions as in Figure 1D and Figure 2D, with 1) the raw data, and 2) the interpolated data before the nuisance regression. Both the raw data and interpolated data have been band-pass filtered as was done in the original pre-processing pipeline and converted to percent signal change. These figures can be compared directly to Figure 1D and Figure 2D, for the two tasks, respectively. 

Of note is that the raw data seem to be dominated by responses to blinks (and/or saccades). Crucially, the pattern of results remains overall unchaged between the interpolated-only and fully pre-processed version of the data for both tasks. 

In the Supplementary Materials (see Supplementary section 2), we have added the descriptives of the model fits from the deconvolution method. Model fits (R²) for the nuisance regression were generally low: cue-target 2AFC task, M = 0.03, SD = 0.02, range = [0.00, 0.07]; letter-color visual 2AFC, M = 0.08, SD = 0.04, range = [0.02, 0.16].

Furthermore, a Pearson correlation analysis between the interpolated and fully pre-processed data within the time windows of interest for both task indicated high correspondence: 

Cue-target 2AFC task

Early time window: M = 0.99, SD = 0.01, range = [0.955, 1.000]

Late time window: M = 0.99, SD = 0.01, range = [0.971, 1.000]

Letter-color visual 2AFC

Early time window: M = 0.95, SD = 0.04, range = [0.803, 0.998]

Late time window: M = 0.97, SD = 0.02, range = [0.908, 0.999]

In hindsight, including the deconvolution (nuisance regression) method may not have changed the pattern of results much. However, the decision to include this deconvolution method was not data-driven; instead, it was based on the literature establishing the importance of removing variance (up to 5 s) of these blinks and saccades from cognitive effects of interest in pupil dilation (Knapen et al., 2016). 

(4.3) Since this should also lead to predicted time series for the nuisance-regressors, can we see a similar effect (of what is reported for the pupil dilation) based on the blink/saccade traces of a) their predicted time series based on the deconvolution, which could indicate a problem with the interpretation of the pupil dilation effects, and b) the 'raw' blink/saccade events from the eye-tracker? I understand that this is a very exhaustive analysis so I would actually just be interested here in an averaged time-course / blink&saccade frequency of the same time-window in Figure 1D to complement the PD analysis as a sanity check.

Also included in the Supplementary Figure 2 is the data averaged as in Figure 1D and Figure 2D for the raw data and nuisance-predictor time courses (please refer to the bottom row of the sub-plots). No pattern was observed in either the raw data or the nuisance predictors as was shown in the residual time courses. 

(4.4) How many samples were removed from the time series due to blinks/saccades in the first place? 150ms for both events in both directions is quite a long bit of time so I wonder how much 'original' information of the pupil was actually left in the time windows of interest that were used for subsequent interpretations.

We thank the reviewer for bringing this issue to our attention. The size of the interpolation window was based on previous literature, indicating a range of 100-200 ms as acceptable (Urai et al., 2017; Knapen et al., 2016; Winn et al., 2018). The ratio of interpolated-to-original data (across the entire trial) varied greatly between participants and between trials: cue-target 2AFC task, M = 0.262, SD = 0.242, range = [0,1]; letter-color 2AFC task, M = 0.194, SD = 0.199, range = [0,1]. 

We have now included a conservative analysis in which only trials with more than half (threshold = 60%) of original data are included in the analyses. Crucially, we still observe the same pattern of effects as when all data are considered across both tasks (compare the second to last row in the Supplementary Figure 2 to Figure 1D and Figure 2D).

(4.5) Was the baseline correction performed on the percentage change unit?

Yes, the baseline correction was performed on the pupil timeseries after converting to percentsignal change. We have added that information to the Methods (section 2.3).

(4.6) What metric was used to define events in the derivative as 'peaks'? I assume some sort of threshold? How was this chosen?

The threshold was chosen in a data-driven manner and was kept consistent across both tasks. The following details have been added to the Methods:

“The size of the interpolation window preceding nuisance events was based on previous literature [13,39,99]. After interpolation based on data-markers and/or missing values, remaining blinks and saccades were estimated by testing the first derivative of the pupil dilation time series against a threshold rate of change. The threshold for identifying peaks in the temporal derivative is data-driven, partially based on past work[10,14,33]. The output of each participant’s pre-processing pipeline was checked visually. Once an appropriate threshold was established at the group level, it remained the same for all participants (minimum peak height of 10 units).” (p. 8 & 11).

(5) Multicollinearity Between Variables:

Lastly, the authors state on page 13: "Furthermore, it is expected that these explanatory variables will be correlated with one another. For this reason, we did not adopt a multiple regression approach to test the relationship between the information-theoretic variables and pupil response in a single model". However, the very purpose of multiple regression is to account for and disentangle the contributions of correlated predictors, no? I might have missed something here.

We apologize for the ambiguity of our explanation in the Methods section. We originally sought to assess the overall relationship between the post-feedback response and information gain (primarily), but also surprise and entropy. Our reasoning was that these variables are often investigated in isolation across different experiments (i.e., only investigating Shannon surprise), and we would like to know what the pattern of results would look like when comparing a single information-theoretic variable to the pupil response (one-by-one). We assumed that including additional explanatory variables (that we expected to show some degree of collinearity with each other) in a regression model would affect variance attributed to them as compared with the one-on-one relationships observed with the pupil response (Morrissey & Ruxton 2018). We also acknowledge the value of a multiple regression approach on our data. Based on the suggestions by the reviewers we have included a complementary linear mixed model analysis in which we controlled for the effects of the information-theoretic variables on one another, while also including the nuisance regressors of pre-feedback baseline pupil dilation and reaction times.  

This new analysis resulted in several additions to the Methods (see Section 2.5) and Results (see Tables 3 and 4). Overall, the results of the linear mixed model corroborated the “simple” correlation analysis across the pupil time course while accounting for the relationship to the prefeedback baseline pupil and preceeding reaction time differences. There was only one difference to note between the correlation and linear mixed modeling analyses: for the error trials in the cue-target 2AFC task, including entropy in the model accounted for the variance previously explained by surprise. 

Reviewer #2 (Recommendations for the authors):

(1) Given the inherent temporal dependencies in pupil dynamics, characterising later pupil responses as independent of earlier ones in a three-way repeated measures ANOVA may not be appropriate. A more suitable approach might involve incorporating the earlier pupil response as a covariate in the model.

We thank the reviewer for bringing this issue to our attention. From our understanding, a repeated-measures ANOVA with factor “time window” would be appropriate in the current context for the following reasons. First, autocorrelation (closely tied to sphericity) is generally not considered a problem when only two timepoints are compared from time series data (Field, 2013; Tabachnick & Fidell, 2019). Second, the repeated-measures component of the ANOVA takes the correlated variance between time points into account in the statistical inference. Finally, as a complementary analysis, we present the results testing the interaction between the frequency and accuracy conditions across the full time courses (see Figures 1D and 2D); in these pupil time courses, any difference between the early and late time windows can be judged by the reader visually and qualitatively. 

(2) Please clarify the correlations between KL divergence, surprise, entropy, and pupil response time series. Specifically, state whether these correlations account for the interrelationships between these information-theoretic measures. Given their strong correlations, partialing out these effects is crucial for accurate interpretation.

As mentioned above, based on the suggestions by the reviewers we have included a complementary linear mixed model analysis in which we controlled for the effects of the information-theoretic variables on one another, while also including the nuisance regressors of pre-feedback baseline pupil dilation and reaction times.  

This new analysis resulted in several additions to the Methods (see Section 2.5) and Results (see Tables 3 and 4). Overall, the results of the linear mixed model corroborated the “simple” correlation analysis across the pupil time course while accounting for the relationship to the prefeedback baseline pupil and preceeding reaction time differences. There was only one difference to note between the correlation and linear mixed modeling analyses: for the error trials in the cue-target 2AFC task, including entropy in the model accounted for the variance previously explained by surprise. 

(3) The effects observed in the late time windows appear weak (e.g., Figure 2E vs. 2F, and the generally low correlation coefficients in Figure 3). Please elaborate on the reliability and potential implications of these findings.

We have now included a complementary linear mixed model analysis which also provides insight into the amount of explained variance of these information-theoretic predictors on the post-feedback pupil response, while also including the pre-feedback baseline pupil and reaction time differences (see section 3.3, Tables 3 & 4). The R² values ranged from 0.16 – 0.50 across all conditions tested. Including the pre-feedback baseline pupil dilation as a predictor in the linear mixed model analysis consistently led to more explained variance in the post-feedback pupil response, as expected.  

(4) In Figure 3 (C-J), please clarify how the trial-by-trial correlations were computed (averaged across trials or subjects). Also, specify how the standard error of the mean (SEM) was calculated (using the number of participants or trials).

The trial-by-trial correlations between the pupil signal and model parameters were computed for each participant, then the coefficients were averaged across participants for statistical inference. We have added several clarifications in the text (see section 2.5 and legends of Figure 3 and Supplementary Figure 4).

We have added “the standard error of the mean across participants” to all figure labels.

(5) For all time axes (e.g., Figure 2D), please label the ticks at 0, 0.5, 1, 1.5, 2, 2.5, and 3 seconds. Clearly indicate the duration of the feedback on the time axes. This is particularly important for interpreting the pupil dilation responses evoked by auditory feedback.

We have labeled the x-ticks every 0.5 seconds in all figures and indicated the duration of the auditory feedback in the letter-color decision task and as well as the stimuli presented in the control tasks in the Supplementary Materials. 

Reviewer #3 (Recommendations for the authors):

(1) Introduction page 3: "In information theory, information gain quantifies the reduction of uncertainty about a random variable given the knowledge of another variable. In other words, information gain measures how much knowing about one variable improves the prediction or understanding of another variable."

(2) In my opinion, the description of information gain can be clarified. Currently, it is not very concrete and quite abstract. I would recommend explaining it in the context of belief updating.

We have removed these unclear statements in the Introduction. We now clearly state the following:

“Information gain can be operationalized within information theory as the KullbackLeibler (KL) divergence between the posterior and prior belief distributions of a Bayesian observer, representing a formalized quantity that is used to update internal models [29,79,80].” (p. 4)

(3) Page 4: The inconsistencies across studies are described in extreme detail. I recommend shortening this part and summarizing the inconsistencies instead of listing all of the findings separately.

As per the reviewer’s recommendation, we have shortened this part of the introduction to summarize the inconsistencies in a more concise manner as follows: 

“Previous studies have shown different temporal response dynamics of prediction error signals in pupil dilation following feedback on decision outcome: While some studies suggest that the prediction error signals arise around the peak (~1 s) of the canonical impulse response function of the pupil [11,30,41,61,62,90], other studies have shown evidence that prediction error signals (also) arise considerably later with respect to feedback on choice outcome [10,25,32,41,62]. A relatively slower prediction error signal following feedback presentation may suggest deeper cognitive processing, increased cognitive load from sustained attention or ongoing uncertainty, or that the brain is integrating multiple sources of information before updating its internal model. Taken together, the literature on prediction error signals in pupil dilation following feedback on decision outcome does not converge to produce a consistent temporal signature.” (p. 5)

We would like to note some additional minor corrections to the preprint:

We have clarified the direction of the effect in Supplementary Figure 3 with the following: 

“Participants who showed a larger mean difference between the 80% as compared with the 20% frequency conditions in accuracy also showed smaller differences (a larger mean difference in magnitude in the negative direction) in pupil responses between frequency conditions (see Supplementary Figure 4).”

The y-axis labels in Supplementary Figure 3 were incorrect and have been corrected as the following: “Pupil responses (80-20%)”.

We corrected typos, formatting and grammatical mistakes when discovered during the revision process. Some minor changes were made to improve clarity. Of course, we include a version of the manuscript with Tracked Changes as instructed for consideration.

This is wrong. Download it from here: https://developer.android.com/studio/run/win-usb

Author response:

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

Public Reviews:

Reviewer #1 (Public Reviews):

Summary:

Argunşah et al. describe and investigate the mechanisms underlying the differential response dynamics of barrel vs septa domains of the whisker-related primary somatosensory cortex (S1). Upon repeated stimulation, the authors report that the response ratio between multi- and single-whisker stimulation increases in layer (L) 4 neurons of the septal domain, while remaining constant in barrel L4 neurons. This difference is attributed to the short-term plasticity properties of interneurons, particularly somatostatin-expressing (SST+) neurons. This claim is supported by the increased density of SST+ neurons found in L4 of the septa compared to barrels, along with a stronger response of (L2/3) SST+ neurons to repeated multi- vs single-whisker stimulation. The role of the synaptic protein Elfn1 is then examined. Elfn1 KO mice exhibited little to no functional domain separation between barrel and septa, with no significant difference in single- versus multi-whisker response ratios across barrel and septal domains. Consistently, a decoder trained on WT data fails to generalize to Elfn1 KO responses. Finally, the authors report a relative enrichment of S2- and M1-projecting cell densities in L4 of the septal domain compared to the barrel domain.

Strengths:

This paper describes and aims to study a circuit underlying differential response between barrel columns and septal domains of the primary somatosensory cortex. This work supports the view that barrel and septal domains contribute differently to processing single versus multi-whisker inputs, suggesting that the barrel cortex multiplexes sensory information coming from the whiskers in different domains.

We thank the reviewer for the very neat summary of our findings that barrel cortex multiplexes converging information in separate domains.

Weaknesses:

While the observed divergence in responses to repeated SWS vs MWS between the barrel and septal domains is intriguing, the presented evidence falls short of demonstrating that short-term plasticity in SST+ neurons critically underpins this difference. The absence of a mechanistic explanation for this observation limits the work’s significance. The measurement of SST neurons’ response is not specific to a particular domain, and the Elfn1 manipulation does not seem to be specific to either stimulus type or a particular domain.

We appreciate the reviewer’s perspective. Although further research is needed to understand the circuit mechanisms underlying the observed phenomenon, we believe our data suggest that altering the short-term dynamics of excitatory inputs onto SST neurons reduces the divergent spiking dynamics in barrels versus septa during repetitive single- and multi-whisker stimulation. Future work could examine how SST neurons, whose somata reside in barrels and septa, respond to different whisker stimuli and the circuits in which they are embedded. At this time, however, the authors believe there is no alternative way to test how the short-term dynamics of excitatory inputs onto SST neurons, as a whole, contribute to the temporal aspects of barrel versus septa spiking.

The study's reach is further constrained by the fact that results were obtained in anesthetized animals, which may not generalize to awake states.

We appreciate the reviewer’s concern regarding the generalizability of our findings from anesthetized animals to awake states. Anesthesia was employed to ensure precise individual whisker stimulation (and multi-whisker in the same animal), which is challenging in awake rodents due to active whisking. While anesthesia may alter higher-order processing, core mechanisms, such as short and long term plasticity in the barrel cortex, are preserved under anesthesia (Martin-Cortecero et al., 2014; Mégevand et al., 2009).

The statistical analysis appears inappropriate, with the use of repeated independent tests, dramatically boosting the false positive error rate.

Thank you for your feedback on our analysis using independent rank-based tests for each time point in wild-type (WT) animals. To address concerns regarding multiple comparisons and temporal dependencies (for Figure 1F and 4D for now but we will add more in our revision), we performed a repeated measures ANOVA for WT animals (13 Barrel, 8 Septa, 20 time points), which revealed a significant main effect of Condition (F(1,19) = 16.33, p < 0.001) and a significant Condition-Time interaction (F(19,361) = 2.37, p = 0.001). Post-hoc tests confirmed significant differences between Barrel and Septa at multiple time points (e.g., p < 0.0025 at times 3, 4, 6, 7, 8, 10, 11, 12, 16, 19 after Bonferroni posthoc correction), supporting a differential multi-whisker vs. single-whisker ratio response in WT animals. In contrast, a repeated measures ANOVA for knock-out (KO) animals (11 Barrel, 7 Septa, 20 time points) showed no significant main effect of Condition (F(1,14) = 0.17, p = 0.684) or Condition-Time interaction (F(19,266) = 0.73, p = 0.791), indicating that the BarrelSepta difference observed in WT animals is absent in KO animals.

Furthermore, the manuscript suffers from imprecision; its conclusions are occasionally vague or overstated. The authors suggest a role for SST+ neurons in the observed divergence in SWS/MWS responses between barrel and septal domains. However, this remains speculative, and some findings appear inconsistent. For instance, the increased response of SST+ neurons to MWS versus SWS is not confined to a specific domain. Why, then, would preferential recruitment of SST+ neurons lead to divergent dynamics between barrel and septal regions? The higher density of SST+ neurons in septal versus barrel L4 is not a sufficient explanation, particularly since the SWS/MWS response divergence is also observed in layers 2/3, where no difference in SST+ neuron density is found.

Moreover, SST+ neuron-mediated inhibition is not necessarily restricted to the layer in which the cell body resides. It remains unclear through which differential microcircuits (barrel vs septum) the enhanced recruitment of SST+ neurons could account for the divergent responses to repeated SWS versus MWS stimulation.

We fully appreciate the reviewer’s comment. We currently do not provide any evidence on the contribution of SST neurons in the barrels versus septa in layer 4 on the response divergence of spiking observed in SWS versus MWS. We only show that these neurons differentially distribute in the two domains in this layer. It is certainly known that there is molecular and circuit-based diversity of SST-positive neurons in different layers of the cortex, so it is plausible that this includes cells located in the two domains of vS1, something which has not been examined so far. Our data on their distribution are one piece of information that SST neurons may have a differential role in inhibiting barrel stellate cells versus septa ones. Morphological reconstructions of SST neurons in L4 of the somatosensory barrel cortex has shown that their dendrites and axons project locally and may confine to individual domains, even though not specifically examined (Fig. 3 of Scala F et al., 2019). The same study also showed that L4 SST cells receive excitatory input from local stellate cells) and is known that they are also directly excited by thalamocortical fibers (Beierlein et al., 2003; Tan et al., 2008), both of which facilitate.

As shown in our supplementary figure, the divergence is also observed in L2/3 where, as the reviewer also points out, where we do not have a differential distribution of SST cells, at least based on a columnar analysis extending from L4. There are multiple scenarios that could explain this “discrepancy” that one would need to examine further in future studies. One straightforward one is that the divergence in spiking in L2/3 domains may be inherited from L4 domains, where L4 SST act on. Another is that even though L2/3 SST neurons are not biased in their distribution their input-output function is, something which one would need to examine by detailed in vitro electrophysiological and perhaps optogenetic approaches in S1. Despite the distinctive differences that have been found between the L4 circuitry in S1 and V1 (Scala F et al., 2019), recent observations indicate that small but regular patches of V1 marked by the absence of muscarinic receptor 2 (M2) have high temporal acuity (Ji et al., 2015), and selectively receive input from SST interneurons (Meier et al., 2025). Regions lacking M2 have distinct input and output connectivity patterns from those that express M2 (Meier et al., 2021; Burkhalter et al., 2023). These findings, together with ours, suggest that SST cells preferentially innervate and regulate specific domains columns- in sensory cortices.

Regardless of the mechanism, the Elfn1 knock-out mouse line almost exclusively affects the incoming excitability onto SST neurons (see also reply to comment below), hence what can be supported by our data is that changing the incoming short-term synaptic plasticity onto these neurons brings the spiking dynamics between barrels and septa closer together.

The Elfn1 KO mouse model seems too unspecific to suggest the role of the short-term plasticity in SST+ neurons in the differential response to repeated SWS vs MWS stimulation across domains. Why would Elfn1-dependent short-term plasticity in SST+ neurons be specific to a pathway, or a stimulation type (SWS vs MWS)? Moreover, the authors report that Elfn1 knockout alters synapses onto VIP+ as well as SST+ neurons (Stachniak et al., 2021; previous version of this paper)-so why attribute the phenotype solely to SST+ circuitry? In fact, the functional distinctions between barrel and septal domains appear largely abolished in the Elfn1 KO.

Previous work by others and us has shown that globally removing Elfn1 selectively removes a synaptic process from the brain without altering brain anatomy or structure. This allows us to study how the temporal dynamics of inhibition shape activity, as opposed to inhibition from particular cell types. We will nevertheless update the text to discuss more global implications for SST interneuron dynamics and include a reference to VIP interneurons that contain Elfn1.

When comparing SWS to MWS, we find that MWS replaces the neighboring excitation which would normally be preferentially removed by short-term plasticity in SST interneurons, thus providing a stable control comparison across animals and genotypes. On average, VIP interneurons failed to show modulation by MWS. We were unable to measure a substantial contribution of VIP cells to this process and also note that the Elfn1 expressing multipolar neurons comprise only ~5% of VIP neurons (Connor and Peters, 1984; Stachniak et al., 2021), a fraction that may be lost when averaging from 138 VIP cells. Moreover, the effect of Elfn1 loss on VIP neurons is quite different and marginal compared to that of SST cells, suggesting that the primary impact of Elfn1 knockout is mediated through SST+ interneuron circuitry. Therefore, even if we cannot rule out that these 5% of VIP neurons contribute to barrel domain segregation, we are of the opinion that their influence would be very limited if any.

Reviewer #2 (Public Reviews):

Summary:

Argunsah and colleagues demonstrate that SST-expressing interneurons are concentrated in the mouse septa and differentially respond to repetitive multi-whisker inputs. Identifying how a specific neuronal phenotype impacts responses is an advance.

Strengths:

(1)  Careful physiological and imaging studies.

(2)  Novel result showing the role of SST+ neurons in shaping responses.

(3)  Good use of a knockout animal to further the main hypothesis.

(4)  Clear analytical techniques.

We thank the reviewer for their appreciation of the study.

Weaknesses:

No major weaknesses were identified by this reviewer. Overall, I appreciated the paper but feel it overlooked a few issues and had some recommendations on how additional clarifications could strengthen the paper. These include:

(1) Significant work from Jerry Chen on how S1 neurons that project to M1 versus S2 respond in a variety of behavioral tasks should be included (e.g. PMID: 26098757). Similarly, work from Barry Connor’s lab on intracortical versus thalamocortical inputs to SST neurons, as well as excitatory inputs onto these neurons (e.g. PMID: 12815025) should be included.

We thank the reviewer for these valuable resources that we overlooked. We will include Chen et al. (2015), Cruikshank et al. (2007) and Gibson et al. (1999) to contextualize S1 projections and SST+ inputs, strengthening the study’s foundation as well as Beierlein et al. (2003) which nicely show both local and thalamocortical facilitation of excitatory inputs onto L4 SST neurons, in contrast to PV cells. The paper also shows the gradual recruitment of SST neurons by thalamocortical inputs to provide feed-forward inhibition onto stellate cells (regular spiking) of the barrel cortex L4 in rat.

(2) Using Layer 2/3 as a proxy to what is happening in layer 4 (~line 234). Given that layer 2/3 cells integrate information from multiple barrels, as well as receiving direct VPm thalamocortical input, and given the time window that is being looked at can receive input from other cortical locations, it is not clear that layer 2/3 is a proxy for what is happening in layer 4.

We agree with the reviewer that what we observe in L2/3 is not necessarily what is taking place in L4 SST-positive cells. The data on L2/3 was included to show that these cells, as a population, can show divergent responses when it comes to SWS vs MWS, which is not seen in L2/3 VIP neurons. Regardless of the mechanisms underlying it, our overall data support that SST-positive neurons can change their activation based on the type of whisker stimulus and when the excitatory input dynamics onto these neurons change due to the removal of Elfn1 the recruitment of barrels vs septa spiking changes at the temporal domain. Having said that, the data shown in Supplementary Figure 3 on the response properties of L2/3 neurons above the septa vs above the barrels (one would say in the respective columns) do show the same divergence as in L4. This suggests that a circuit motif may exist that is common to both layers, involving SST neurons that sit in L4, L5 or even L2/3. This implies that despite the differences in the distribution of SST neurons in septa vs barrels of L4 there is an unidentified input-output spatial connectivity motif that engages in both L2/3 and L4. Please also see our response to a similar point raised by reviewer 1.

(3) Line 267, when discussing distinct temporal response, it is not well defined what this is referring to. Are the neurons no longer showing peaks to whisker stimulation, or are the responses lasting a longer time? It is unclear why PV+ interneurons which may not be impacted by the Elfn1 KO and receive strong thalamocortical inputs, are not constraining activity.

We thank the reviewer for their comment and will clarify the statement.

This convergence of response profiles was further clear in stimulus-aligned stacked images, where the emergent differences between barrels and septa under SWS were largely abolished in the KO (Figure 4B). A distinction between directly stimulated barrels and neighboring barrels persisted in the KO. In addition, the initial response continued to differ between barrel and septa and also septa and neighbor (Figure 4B). This initial stimulus selectivity potentially represents distinct feedforward thalamocortical activity, which includes PV+ interneuron recruitment that is not directly impacted by the Elfn1 KO (Sun et al., 2006; Tan et al., 2008). PV+ cells are strongly excited by thalamocortical inputs, but these exhibit short-term depression, as does their output, contrasting with the sustained facilitation observed in SST+ neurons. These findings suggest that in WT animals, activity spillover from principal barrels is normally constrained by the progressive engagement of SST+ interneurons in septal regions, driven by Elfn1-dependent facilitation at their excitatory synapses. In the absence of Elfn1, this local inhibitory mechanism is disrupted, leading to longer responses in barrels, delayed but stronger responses in septa, and persistently stronger responses in unstimulated neighbors, resulting in a loss of distinction between the responses of barrel and septa domains that normally diverge over time (see Author response image 1 below).

Author response image 1.

(A) Barrel responses are longer following whisker stimulation in KO. (B) Septal responses are slightly delayed but stronger in KO. (C) Unstimulated neighbors show longer persistent responses in KO.

(4) Line 585 “the earliest CSD sink was identified as layer 4…” were post-hoc measurements made to determine where the different shank leads were based on the post-hoc histology?

Post hoc histology was performed on plane-aligned brain sections which would allow us to detect barrels and septa, so as to confirm the insertion domains of each recorded shank. Layer specificity of each electrode therefore could therefore not be confirmed by histology as we did not have coronal sections in which to measure electrode depth.

(5) For the retrograde tracing studies, how were the M1 and S2 injections targeted (stereotaxically or physiologically)? How was it determined that the injections were in the whisker region (or not)?

During the retrograde virus injection, the location of M1 and S2 injections was determined by stereotaxic coordinates (Yamashita et al., 2018). After acquiring the light-sheet images, we were able to post hoc examine the injection site in 3D and confirm that the injections were successful in targeting the regions intended. Although it would have been informative to do so, we did not functionally determine the whisker-related M1 and whisker-related S2 region in this experiment.

(6) Were there any baseline differences in spontaneous activity in the septa versus barrel regions, and did this change in the KO animals?

Thank you for this interesting question. Our previous study found that there was a reduction in baseline activity in L4 barrel cortex of KO animals at postnatal day (P)12, but no differences were found at P21 (Stachniak et al., 2023).

Reviewer #3 (Public Reviews):

Summary:

This study investigates the functional differences between barrel and septal columns in the mouse somatosensory cortex, focusing on how local inhibitory dynamics, particularly involving Elfn1-expressing SST⁺ interneurons, may mediate temporal integration of multiwhisker (MW) stimuli in septa. Using a combination of in vivo multi-unit recordings, calcium imaging, and anatomical tracing, the authors propose that septa integrate MW input in an Elfn1-dependent manner, enabling functional segregation from barrel columns.

Strengths:

The core hypothesis is interesting and potentially impactful. While barrels have been extensively characterized, septa remain less understood, especially in mice, and this study's focus on septal integration of MW stimuli offers valuable insights into this underexplored area. If septa indeed act as selective integrators of distributed sensory input, this would add a novel computational role to cortical microcircuits beyond what is currently attributed to barrels alone. The narrative of this paper is intellectually stimulating.

We thank the reviewer for finding the study intellectually stimulating.

Weaknesses:

The methods used in the current study lack the spatial and cellular resolution needed to conclusively support the central claims. The main physiological findings are based on unsorted multi-unit activity (MUA) recorded via low-channel-count silicon probes. MUA inherently pools signals from multiple neurons across different distances and cell types, making it difficult to assign activity to specific columns (barrel vs. septa) or neuron classes (e.g., SST⁺ vs. excitatory).

The recording radius (~50-100 µm or more) and the narrow width of septa (~50-100 µm or less) make it likely that MUA from "septal" electrodes includes spikes from adjacent barrel neurons.

The authors do not provide spike sorting, unit isolation, or anatomical validation that would strengthen spatial attribution. Calcium imaging is restricted to SST⁺ and VIP⁺ interneurons in superficial layers (L2/3), while the main MUA recordings are from layer 4, creating a mismatch in laminar relevance.

We thank the reviewer for pointing out the possibility of contamination in septal electrodes. Importantly, it may not have been highlighted, although reported in the methods, but we used an extremely high threshold (7.5 std, in methods, line 583) for spike detection in order to overcome the issue raised here, which restricts such spatial contaminations. Since the spike amplitude decays rapidly with distance, at high thresholds, only nearby neurons contribute to our analysis, potentially one or two. We believe that this approach provides a very close approximation of single unit activity (SUA) in our reported data. We will include a sentence earlier in the manuscript to make this explicit and prevent further confusion.

Regarding the point on calcium imaging being performed on L2/3 SST and VIP cells instead of L4. Both reviewer 1 and 2 brought up the same issue and we responded as follows. As shown in our supplementary figure, the divergence is also observed in L2/3 where we do not have a differential distribution of SST cells, at least based on a columnar analysis extending from L4. There are multiple scenarios that could explain this “discrepancy” that one would need to examine further in future studies. One straightforward one is that the divergence in spiking in L2/3 domains may be inherited from L4 domains, where L4 SST act on. Another is that even though L2/3 SST neurons are not biased in their distribution their input-output function is, something which one would need to examine by detailed in vitro electrophysiological and perhaps optogenetic approaches in S1. Despite the distinctive differences that have been found between the L4 circuitry in S1 and V1 (Scala F et al., 2019), recent observations indicate that small but regular patches of V1 marked by the absence of muscarinic receptor 2 (M2) have high temporal acuity (Ji et al., 2015), and selectively receive input from SST interneurons (Meier et al., 2025). Regions lacking M2 have distinct input and output connectivity patterns from those that express M2 (Meier et al., 2021; Burkhalter et al., 2023). These findings, together with ours, suggest that SST cells preferentially innervate and regulate specific domains -columns- in sensory cortices.

Furthermore, while the role of Elfn1 in mediating short-term facilitation is supported by prior studies, no new evidence is presented in this paper to confirm that this synaptic mechanism is indeed disrupted in the knockout mice used here.

We thank Reviewer #3 for noting the absence of new evidence confirming Elfn1’s disruption of short-term facilitation in our knockout mice. We acknowledge that our study relies on previously strong published data demonstrating that Elfn1 mediates short-term synaptic facilitation of excitatory inputs onto SST+ interneurons (Sylwestrak and Ghosh, 2012; Tomioka et al., 2014; Stachniak et al., 2019, 2023). These studies consistently show that Elfn1 knockout abolishes facilitation in SST+ synapses, leading to altered temporal dynamics, which we hypothesize underlies the observed loss of barrel-septa response divergence in our Elfn1 KO mice (Figure 4). Nevertheless, to address the point raised, we will clarify in the revised manuscript (around lines 245-247 and 271-272) that our conclusions are based on these established findings, stating: “Building on prior evidence that Elfn1 knockout disrupts short-term facilitation in SST+ interneurons (Sylwestrak and Ghosh, 2012; Tomioka et al., 2014; Stachniak et al., 2019, 2023), we attribute the abolished barrel-septa divergence in Elfn1 KO mice to altered SST+ synaptic dynamics, though direct synaptic measurements were not performed here.”

Additionally, since Elfn1 is constitutively knocked out from development, the possibility of altered circuit formation-including changes in barrel structure and interneuron distribution, cannot be excluded and is not addressed.

We thank Reviewer #3 for raising the valid concern that constitutive Elfn1 knockout could potentially alter circuit formation, including barrel structure and interneuron distribution. To address this, we will clarify in the revised manuscript (around line ~271 and in the Discussion) that in our previous studies that included both whole-cell patch-clamp in acute brain slices ranging from postnatal day 11 to 22 (P11 - P21) and in vivo recordings from barrel cortex at P12 and P21, we saw no gross abnormalities in barrel structure, with Layer 4 barrels maintaining their characteristic size and organization, consistent with wildtype (WT) mice (Stachniak et al., 2019, 2023). While we cannot fully exclude subtle developmental changes, prior studies indicate that Elfn1 primarily modulates synaptic function rather than cortical cytoarchitecture (Tomioka et al., 2014). Elfn1 KO mice show no gross morphological or connectivity differences and the pattern and abundance of Elfn1 expressing cells (assessed by LacZ knock in) appears normal (Dolan and Mitchell, 2013).

We will add the following to the Discussion: “Although Elfn1 is constitutively knocked out, we find here and in previous studies that barrel structure is preserved (Stachniak et al., 2019, 2023). Further, the distribution of Elfn1 expressing interneurons is not different in KO mice, suggesting minimal developmental disruption (Dolan and Mitchell, 2013).

Nonetheless, we acknowledge that subtle circuit changes cannot be ruled out without the usage of time-depended conditional knockout of the gene.”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

(1) My biggest concern is regarding statistics. Did the authors repeatedly apply independent tests (Mann-Whitney) without any correction for multiple comparisons (Figures 1 and 4)? In that case, the chances of a spurious "significant" result rise dramatically. 

In response to the reviewer’s comment, we now present new statistical results by utilizing ANOVA and blended these results in the manuscript between lines 172 and 192 for WT data and 282 and 298 for Elfn1 KO data. This new statistical approach shows the same differences as we had previously reported, hence consolidating the statements made. 

(2) The findings only hint at a mechanism involving SST+ neurons for how SWS and MWS are processed differently in the barrel vs septal domains. As a direct test of SST+ neuron involvement in the divergence of barrel and septal responses, the authors might consider SST-specific manipulations - for example, inhibitory chemo- or optogenetics during SWS and MWS stimulation.

We thank the reviewer for this comment and agree that a direct manipulation of SST+ neurons via inhibitory chemo- or opto-genetics could provide further supporting evidence for the main claims in our study. We have opted out from performing these experiments for this manuscript as we feel they can be part of a future study.  At the same time, it is conceivable that such manipulations and depending on how they are performed may lead to larger and non-specific effects on cortical activity, since SST neurons will likely be completely shut down. So even though we certainly appreciate and value the strengths of such approaches, our experiments have addressed a more nuanced hypothesis, namely that the synaptic dynamics onto SST+ neurons matter for response divergence of septa versus barrels, which could not have been easily and concretely addressed by manipulating SST+ cell firing activity.  

(3) In general, it is hard to comprehend what microcircuit could lead to the observed divergence in the MWS/SWS ratio in the barrel vs septal domain. There preferential recruitment of SST+ neurons during MWS is not specific to a particular domain, and the higher density of SST+ neurons specifically in L4 septa cannot per se explain the diverging MWS/SWS ratio in L4 septal neurons since similar ratio divergence is observed across domains in L2/3 neurons without increase SST+ neuron density in L2/3. This view would also assume that SST+ inhibition remains contained to its own layer and domain. Is this the case? Is it that different microcircuits between barrels and septa differently shape the response to repeated MWS? This is partially discussed in the paper; can the authors develop on that? What would the proposed mechanism be? Can the short-term plasticity of the thalamic inputs (VPM vs POm) be part of the picture?

We thank the reviewer for raising this important point. We propose that the divergence in MWS/SWS ratios across barrel and septal domains arises from dynamic microcircuit interactions rather than static anatomical features such as SST+ density, which we describe and can provide a hint. In L2/3, where SST+ density is uniform, divergence persists, suggesting that trans-laminar and trans-domain interactions are key. Barrel domains, primarily receiving VPM inputs, exhibit short-term depression onto excitatory cells and engage PV+ and SST+ neurons to stabilize the MWS/SWS ratio, with Elfn1-dependent facilitation of SST+ neurons gradually increasing inhibition during repetitive SWS. Septal domains, in contrast, are targeted by facilitating POm inputs, combined with higher L4 SST+ density and Elfn1-mediated facilitation, producing progressive inhibitory buildup that amplifies the MWS/SWS ratio. SST+ projections in septa may extend trans-laminarly and laterally, influencing L2/3 and neighboring barrels, thereby explaining L2/3 divergence despite uniform SST+ density in L2/3. In this regards, direct laminar-dependent manipulations will be required to confirm whether L2/3 divergence is inherited from L4 dynamics. In Elfn1 KO mice, the loss of facilitation in SST+ neurons likely flattens these dynamics, disrupting functional segregation. Future experiments using VPM/POm-specific optogenetic activation and SST+ silencing will be critical to directly test this model.

We expanded the discussion accordingly.

(4) Can the decoder generalize between SWS and MWS? In this condition, if the decoder accuracy is higher for barrels than septa, it would support the idea that septa are processing the two stimuli differently. 

Our results show that septal decoding accuracy is generally higher than barrel accuracy when generalizing from multi-whisker stimulation (MWS) to single-whisker stimulation (SWS), indicating distinct information processing in septa compared to barrels.

In wild-type (WT) mice, septal accuracy exceeds barrel accuracy across all time windows (150ms, 51-95ms, 1-95ms), with the largest difference in the 51-95ms window (0.9944 vs. 0.9214 at pulse 20, 10Hz stimulation). This septal advantage grows with successive pulses, reflecting robust, separable neural responses, likely driven by the posterior medial nucleus (POm)’s strong MWS integration contrasting with minimal SWS activation. Barrel responses, driven by consistent ventral posteromedial nucleus (VPM) input for both stimuli, are less distinguishable, leading to lower accuracy.

In Elfn1 knockout (KO) mice, which disrupt excitatory drive to somatostatin-positive (SST+) interneurons, barrel accuracy is higher initially in the 1-50ms window (0.8045 vs. 0.7500 at pulse 1), suggesting reduced early septal distinctiveness. However, septal accuracy surpasses barrels in later pulses and time windows (e.g., 0.9714 vs. 0.9227 in 51-95ms at pulse 20), indicating restored septal processing. This supports the role of SST+ interneurons in shaping distinct MWS responses in septa, particularly in late-phase responses (51-95ms), where inhibitory modulation is prominent, as confirmed by calcium imaging showing stronger SST+ activation during MWS.

These findings demonstrate that septa process SWS and MWS differently, with higher decoding accuracy reflecting structured, POm- and SST+-driven response patterns. In Elfn1 KO mice, early deficits in septal processing highlight the importance of SST+ interneurons, with later recovery suggesting compensatory mechanisms. 

We have added Supplementary Figure 4 and included this interpretation between lines 338353. 

We thank the reviewer for suggesting this analysis.

(5) It is not clear to me how the authors achieve SWS. How is it that the pipette tip "placed in contact with the principal whisker" does not detach from the principal whisker or stimulate other whiskers? Please clarify the methods. 

Targeting the specific principal whisker is performed under the stereoscope.  

Specifically, we have added this statement in line 628:

“We trimmed the whiskers where necessary, to avoid them touching each other and to avoid stimulating other whiskers. By putting the pipette tip very close (almost touching) to the principal whisker, the movement of the tip (limited to 1mm) would reliably move the targeted whisker. The specificity of the stimulation of the selected principal whisker was observed under the stereoscope.”

(6) The method for calculating decoder accuracy is not clearly described-how can accuracy exceed 1? The authors should clarify this metric and provide measures of variability (e.g., confidence intervals or standard deviations across runs) to assess the significance of their comparisons. Additionally, using a consistent scale across all plots would improve interoperability. 

We thank the reviewer for raising this point. We have now changed the way accuracies are calculated and adopted a common scale among different plots (see updated Figure 5). We have also changed the methods section accordingly.

(7) Figure 1: The sample size is not specified. It looks like the numbers match the description in the methods, but the sample size should be clearly stated here. 

These are the numbers the reviewer is inquiring about. 

WT: (WT) animals: a 280 × 95 × 20 matrix for the stimulated barrel (14 Barrels, 95ms, 20 pulses), a 180 × 95 × 20 matrix for the septa (9 Septa, 95ms, 20 pulses), and a 360 × 95 × 20 matrix for the neighboring barrel (18 Neighboring barrels, 95ms, 20 pulses). N=4 mice.

KO: 11-barrel columns, 7 septal columns, 11 unstimulated neighbors from N=4 mice.

Panels D-F are missing axes and axis labels (firing rate, p-value). Panel D is mislabeled (left, middle, and right). I can't seem to find the yellow line. 

Thank you for this observation. We made changes in the figures to make them easier to navigate based on the collective feedback from the reviewers.

Why is changing the way to compare the differences in the responses to repeated stimulation between SWS and MWS? 

To assess temporal accumulation of information, we compared responses to repeated single-whisker stimulation (SWS) and multi-whisker stimulation (MWS) using an accumulative decoding approach rather than simple per-pulse firing rates. This method captures domain-specific integration dynamics over successive pulses.

The use of the term "principal whisker" is confusing, as it could refer to the whisker that corresponds to the recorded barrel. 

When we use the term principal whisker, the intention is indeed to refer to the whisker corresponding to the recorded barrel during single whisker stimulation. The term principal whisker is removed from Figure legend 1 and legend S1C where it may have led to  ambiguity.    

Why the statement "after the start of active whisking"? Mice are under anesthesia here; it does not appear to be relevant for the figure. 

“After the start of active whisking” refers to the state of the barrel cortex circuitry at the time of recordings. The particular reference we use comes from the habit of assessing sensory processing also from a developmental point of view. The reviewer is correct that it has nothing to do the with the status of the experiment. Nevertheless, since the reviewer found that it may create confusion, we have now taken it out. 

(8) Figure 3: The y-axis label is missing for panel C. 

This is now fixed. (dF/F).

(9) Figure 4: Axis labels are missing.

Added.

Minor: 

(10) Line 36: "progressive increase in septal spiking activity upon multi-whisker stimulation". There is no increase in septal spiking activity upon MWS; the ratio MWS/SWS increases.