Does this mean that witnesses who speak different languages could remember the same accident differently in court? How this could affect the judgment?

I wouldn't be able to point north right now, it's crazy that a kid can do this just because of the language she speaks

As someone who speaks Portuguese and English, I wonder if my way of thinking changes depending on which language I'm using. I do, however, believe that I communicate with a whole different personality, but not a differet way of thinking.

it's surprising that the way we describe an accident could affect what we remember about it.

How can we know if language changes our thinking or just reflects how we already think?

I can't imagine using north and south every time I need to explain where something is. I'm so used to using left and right that this example made me realize how much language influences even simple things in our daily lives.

I think this theory makes a lot of sense because we usually assume that everyone sees the world in the same way we do. But maybe our language influences our perspective.

This made me think, if language shapes how well we remember who caused an accident, can a person's native language unintentionally bias court proceedings or police relative things?

just as Lera Boroditsky said, I thought It was amazing how a language can force a native speaker to develop an hability, not just an internal compass, just to communicate daily

So, what would be the results of teaching a children two languages, like, one more focused in rational and another in emotions/expressions, like chinese and portuguese? Like, would it be some kind of "Mind maxxing"?

I like this idea! Learning a new language can also help us see the world differently.

In Portuguese we do something similar.

This account for language variations/dialects or just different languages?

Letter "H"

eLife Assessment

Mechanical transduction channels of sensory hair cells possess lipid scramblase activity. Membrane lipid disruption resulting from mechanical transduction is thought to be restored by flippase activities. This fundamental study provides compelling evidence that ATP8B1, a P4-ATP flippase and its subunit TMEM30B, are key in mediating this restorative function in outer hair cells of the mammalian cochlea.

Reviewer #1 (Public review):

Sensory hair cells of the inner ear convert mechanical sound vibrations into electrical signals through mechano-electrical transduction (MET). While the protein components of the MET machinery have been studied extensively, much less is known about how the surrounding membrane lipid environment contributes to hair cell function. The recent discovery that TMC1 and TMC2 also function as lipid scramblases has brought renewed attention to the importance of membrane lipid asymmetry and the mechanisms that maintain it in sensory hair cells.

In this study, the authors identify the P4-ATPase ATP8B1 and its partner TMEM30B as key regulators of membrane lipid asymmetry in outer hair cells. Using complementary genetic models, HA-tagged knock-in mice, localization analyses, and functional experiments, they show that ATP8B1-TMEM30B is enriched in stereocilia and the apical membrane of outer hair cells and is required to maintain phosphatidylserine asymmetry, support hair cell survival, and preserve normal hearing. The parallels between the ATP8B1/TMEM30B loss-of-function phenotypes and TMC1 deafness-associated mutants with constitutive scrambling support a model in which ATP8B1-TMEM30B flippase activity maintains membrane lipid asymmetry and homeostasis, whereas constitutive TMC1-mediated phospholipid scrambling disrupts this balance and contributes to membrane instability.

The authors have addressed the points raised during the initial review thoroughly. The revised manuscript includes clearer methodological details, additional physiological characterization, improved presentation and quantification of several datasets, and a more balanced interpretation of the localization and mechanistic findings. These changes improve both the clarity and rigor of the study while leaving its main conclusions unchanged.

As with any study that opens a new area of investigation, important mechanistic questions remain. In particular, it will be interesting to determine how disruption of membrane lipid asymmetry ultimately impairs MET function and triggers hair cell degeneration, how flippase and scramblase activities are coordinated in vivo, and how these pathways are integrated with the broader molecular machinery underlying mechanotransduction. These questions highlight the exciting directions that this study opens for the field.

Overall, this work provides evidence that ATP8B1-TMEM30B is a critical regulator of stereocilia membrane lipid asymmetry and represents an important contribution to our understanding of membrane homeostasis in auditory hair cells. I have no further major concerns and support publication.

Comments on second revision:

I appreciate the authors' efforts to address the issue and perform the additional experiment, and I agree that removing these data is reasonable and does not affect the main conclusions of the manuscript.

Reviewer #2 (Public review):

Summary:

Prior work identified TMEM30B (knockout mice) as well as ATP8B1 (human genetics and mouse model), ATP8A2 (knockout mice), and ATP811A (human genetics) as relevant for hearing. The authors also reasoned that given the recent discovery of TMC1 and TMC2's dual function as mechanotransduction channels of the inner ear and as lipid scramblases, a counterpart flippase should be in the sensory hair-cell stereocilia bundle where mechanotransduction happens. They use CRISPR/CAS to modify the endogenous mouse genes and add an HA tag at the N-terminus of the ATP8B1, ATP8A1, ATP8A2, and ATP11A proteins. Their experiments with these mice unambiguously localized ATP8B1 at the base of outer hair cell stereocilia bundles. Knockout of ATP8B1 results in loss of outer hair cells, deficient auditory function (ABR), and degeneration of outer hair cell stereocilia bundles. Similarly, hair cells from genetically modified mice with endogenous HA-tagged TMEM30B proteins show localization of this protein to outer hair cell stereocilia bundles. TMEM30B knock out mice phenocopy the ATP8B1 knock out model. Interestingly, the authors show that annexing V staining precedes hair cell loss in ATP8B1 and TMEM30B knockout mice.

Strengths:

(1) Use of knock-in HA-tagged proteins to unambiguously localize ATP8B1 and TMEM30B

(2) Systematic characterization of auditory function (ABR), hair cell loss, and hair-cell stereocilia bundle morphology.

(3) Advances our understanding of the role played by lipid homeostasis in auditory function.

(4) Reports on mouse models that will be helpful to further understand the mechanistic role played by ATP8B1 and TMEM30B in normal hearing and hereditary deafness.

Comments on second revision:

It is interesting that in the images selected as representative of the new experiments the effect seems to be opposite to what was reported before - more ATP8B1-HA in the bundle with transduction blockage. However, this does not seem to be supported by the quantification, and further exploration at different ages, blocker concentrations, effective transduction blockage, etc. might be needed to really have a solid result. Thus, I agree that leaving out these results, and the previous sections linking mechanotransduction to localization of ATP8B1, is the best option.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Sensory hair cells of the inner ear convert mechanical sound vibrations into electrical signals through mechano-electrical transduction (MET). While the protein components of the MET machinery have been studied extensively, much less is known about how the surrounding membrane lipid environment contributes to hair cell function. The recent discovery that TMC1 and TMC2 also function as lipid scramblases has brought renewed attention to the importance of membrane lipid asymmetry and the mechanisms that maintain it in sensory hair cells.

In this study, the authors identify the P4-ATPase ATP8B1 and its partner TMEM30B as key regulators of membrane lipid asymmetry in outer hair cells. Using complementary genetic models, HA-tagged knock-in mice, localization analyses, and functional experiments, they show that ATP8B1-TMEM30B is enriched in stereocilia and the apical membrane of outer hair cells and is required to maintain phosphatidylserine asymmetry, support hair cell survival, and preserve normal hearing. The parallels between the ATP8B1/TMEM30B loss-of-function phenotypes and TMC1 deafness-associated mutants with constitutive scrambling support a model in which ATP8B1-TMEM30B flippase activity maintains membrane lipid asymmetry and homeostasis, whereas constitutive TMC1-mediated phospholipid scrambling disrupts this balance and contributes to membrane instability.

The authors have addressed the points raised during the initial review thoroughly. The revised manuscript includes clearer methodological details, additional physiological characterization, improved presentation and quantification of several datasets, and a more balanced interpretation of the localization and mechanistic findings. These changes improve both the clarity and rigor of the study while leaving its main conclusions unchanged.

As with any study that opens a new area of investigation, important mechanistic questions remain. In particular, it will be interesting to determine how disruption of membrane lipid asymmetry ultimately impairs MET function and triggers hair cell degeneration, how flippase and scramblase activities are coordinated in vivo, and how these pathways are integrated with the broader molecular machinery underlying mechanotransduction. These questions highlight the exciting directions that this study opens for the field.

Overall, this work provides evidence that ATP8B1-TMEM30B is a critical regulator of stereocilia membrane lipid asymmetry and represents an important contribution to our understanding of membrane homeostasis in auditory hair cells. I have no further major concerns and support publication.

Reviewer #2 (Public review):

Summary:

Prior work identified TMEM30B (knockout mice) as well as ATP8B1 (human genetics and mouse model), ATP8A2 (knockout mice), and ATP811A (human genetics) as relevant for hearing. The authors also reasoned that given the recent discovery of TMC1 and TMC2's dual function as mechanotransduction channels of the inner ear and as lipid scramblases, a counterpart flippase should be in the sensory hair-cell stereocilia bundle where mechanotransduction happens. They use CRISPR/CAS to modify the endogenous mouse genes and add an HA tag at the N-terminus of the ATP8B1, ATP8A1, ATP8A2, and ATP11A proteins. Their experiments with these mice unambiguously localized ATP8B1 at the base of outer hair cell stereocilia bundles. Knockout of ATP8B1 results in loss of outer hair cells, deficient auditory function (ABR), and degeneration of outer hair cell stereocilia bundles. Similarly, hair cells from genetically modified mice with endogenous HA-tagged TMEM30B proteins show localization of this protein to outer hair cell stereocilia bundles. TMEM30B knock out mice phenocopy the ATP8B1 knock out model. Interestingly, the authors show that annexing V staining precedes hair cell loss in ATP8B1 and TMEM30B knockout mice and that proper localization of these proteins is lost in mice that lack CIB2, a protein essential for hair cell mechanotransduction.

Strengths:

(1) Use of knock-in HA-tagged proteins to unambiguously localize ATP8B1 and TMEM30B

(2) Systematic characterization of auditory function (ABR), hair cell loss, and hair-cell stereocilia bundle morphology.

(3) Advances our understanding of the role played by lipid homeostasis in auditory function.

(4) Reports on mouse models that will be helpful to further understand the mechanistic role played by ATP8B1 and TMEM30B in normal hearing and hereditary deafness.

Weaknesses:

(1) Are the HA tags causing any functional issues? Function and localization of tagged proteins can sometimes be compromised. This is checked for TMEM30B and ATP8B1, but not for ATP8A1, ATP8A2, and ATP11A.

(2) Following on the point above, is it possible that ATP8B1-HA is well localized, but localization for the other three flippases (ATP8A1-HA, ATP8A2-HA, and ATP11A-HA) is compromised by the tag? Is this potential miss-localization causing any functional phenotypes? I find surprising that there are flippases only in outer hair cells and only formed by ATP8B1. A possible explanation is that the tag is interfering with trafficking. If so, there should be a phenotype (ABRs), although this might be masked by redundancy among these flippases or caused by systemic issues (admittedly difficult to sort out).

We would like to apologize for the oversight on our end that caused the delay and repeat consultation with you, and would like to thank you for your patience.

As a reminder, after our manuscript underwent the full review, we discovered an issue with the final figure of the paper. This experiment is ancillary to the main story, and its removal does not alter the paper’s central findings or conclusions. This Figure 7 asked whether genetic loss of mechanotransduction (MET) alters ATP8B1/TMEM30B distribution in hair cells. After we discovered a problem with the MET-negative mouse model, we agreed with the reviewers to instead test whether pharmacological MET block has the same effect. We found that a 30-minute incubation with benzamil (MET blocker) did not alter ATP8B1 distribution (see uploaded PDF named “ATP8B1-HA_Benzamil”).

Because this experiment was limited in scope and is difficult to compare directly with genetic deletion of MET, we think it is best to proceed with the manuscript version that removes this line of inquiry.

We have made the following changes (compared to the most recent submission):

- Removed Figure 7

Por lo tanto, trabajar siempre desde una carpeta, y partir el trabajo abriendo la carpeta en Positron

Agregaría un link al render de la plantilla

Esto lo pondría como un bonus track, dejando claro que no es necesario ni exigible. La bilbiografía se puede hacer manual, pero si alguien ya trabaja con software de gestión re referencias (Zotero, Mendeley, etc) puede exportar su archivo .bib acá y referenciar automatizadamente.

problema con la numeración

en una sola carpeta

contiene texto y "trozos" (chinks" de código de análisis

(en Positron: Preview)

Agregaría como el bib y el csl van definidos en yaml.

Cannot see separate parts because it was distributed uniformly

eLife Assessment

This study presents an important conceptual advance linking viral lifestyle (temperate versus lytic) to patterns of central carbon metabolism gene content across coral reef viromes, proposing that these associations may reinforce feedback loops influencing reef microbialization state. The revised manuscript better aligns its claims with the underlying data by separating observed metabolic gene associations from the hypothesized downstream effects on infection, host metabolism, and reef state, but the evidence for the central mechanistic claims remains incomplete, as no new analyses were added to establish that the identified metabolic genes are mechanistically linked to temperate viral genomes, to rule out compositional effects, or to validate key gene annotations. This work will be of interest to viral ecologists and to researchers studying coral reef microbial dynamics, providing a useful foundation for future studies testing these proposed relationships directly.

Reviewer #2 (Public review):

Summary:

The manuscript by Kelman and coauthors investigates how viral communities differ in the genes they encode in healthy and degraded coral reef ecosystems. Across 19 viral metagenomes from Central Pacific reefs, the authors assess the frequency of integration/excision genes as a proxy for viral community temperateness and ask whether genes associated with central carbon metabolism covary with signatures of temperateness. The main finding is that viral communities with more temperate-related genes encode more genes from the Entner-Doudoroff pathway and other reactions interpreted as anaplerotic, whereas more lytic-associated viral communities show greater representation of some pentose phosphate pathway, TCA, and redox-associated genes interpreted as cataplerotic. The authors propose a model based on these patterns in which viruses may reinforce feedback loops that influence reef microbialization state.

In the revised manuscript, the authors have refined the separation between the observations and hypothesized effects on infection, host metabolism, and reef state, which align the claims much closer to what the data support. No new analyses were added to buttress whether the metabolic genes are linked to temperate viral genomes, to address compositional effects, or to validate the key annotations, so the evidence for the central mechanistic claims is largely unchanged.

Overall, the study addresses an interesting and potentially important concept - that viral auxiliary metabolic genes are important components of microbial communities and can affect ecosystem functioning. Linking viral metabolism to coral reef microbialization is a creative conceptual advance. The manuscript is clearly written, and the contrasting metabolic gene profiles of these viromes is an interesting pattern that could motivate future work on how viral metabolic potential varies across reef states.

Strengths:

(1) The study connects viral lifestyle, central carbon metabolism, bacterial overgrowth, and reef degradation in a framework that could be useful for future studies of coral reef ecosystems and viral ecology. This is an interesting synthesis that links viral auxiliary metabolism to broader questions about microbialization and reef state.

(2) The manuscript is generally clearly organized around a testable prediction: viral metabolic gene content should vary along a lytic-to-temperate viral community gradient. The reported enrichment of anaplerotic genes in viromes with a larger fraction of temperate viruses is an intriguing result.

(3) The authors highlight several metabolic genes that may not have been previously reported in viral datasets or genomes. With further validation, these observations could expand the known repertoire of viral metabolic potential.

(4) The modelling helps clarify the feedbacks the authors propose may connect viral lifestyle, bacterial metabolism, and coral reef degradation. It provides a foundation for generating hypotheses about how viral metabolic genes could influence reef microbial dynamics.

(5) The revised manuscript is clearer about scope. The methods section now describes the read-based framework and its limitations, and the model is presented as a tool for generating hypotheses rather than as evidence.

Weaknesses:

(1) The main limitation remains that the evidence for several key claims remains indirect. The core analysis is based on correlations between metabolic gene frequencies and integration/excision-related genes. This does not demonstrate that the metabolic genes occur in temperate viral genomes, are physically linked to lysogeny genes, are expressed during infection, or alter host metabolism. The authors did not to attempt contig-level linkage. Thus, the data support an association between VLP-associated metabolic annotations and a community-level temperateness proxy, but not a direct link between temperate phages and these metabolic functions. The manuscript does not discuss alternative explanations for these correlations. More broadly, community-level gene frequencies should not be equated with genome-level or infection-level metabolic programs. A virome may contain more anaplerotic genes overall, but this does not demonstrate that individual viruses reprogram their hosts in an anaplerotic manner or that infection produces a net anaplerotic effect. Individual viruses may encode both anaplerotic and cataplerotic genes, and a smaller number of cataplerotic genes could have stronger metabolic consequences depending on expression, enzyme efficiency, pathway position, and host context.

(2) The revised framing is more careful, but some language still goes beyond the data. The ecological interpretation assumes that viral infection is strong enough to influence reef-scale bacterial population dynamics. However, the study does not directly measure infection frequency, lysis rates, viral production, burst size, lysogeny frequency, prophage induction, gene expression, or bacterial mortality. If viral mortality or lysogenic conversion were rare in these systems, the observed gene-frequency patterns could have limited ecosystem-level consequence. The discussion includes statements such as healthy reefs being "guarded by lytic viruses" and nutrient interventions could promote "re-viralization" for reef restoration. These are reasonable hypotheses, but they depend on infection rates, gene expression, and metabolic effects that were not measured nor discussed.

(3) Because gene frequencies are expressed as proportions of annotated genes, the large decline in genes assigned to phages (from about half of annotated genes in lytic viromes to about 5% in temperate viromes) can force most other gene categories upward with temperateness. The authors now acknowledge this compositional effect but do not test whether the main associations hold once it is accounted for. The many correlations examined are also not corrected for multiple comparisons. As a result, individual gene-level associations, particularly the temperate-associated ones, should be treated as tentative.

(4) The anaplerotic/cataplerotic classification still relies on sequence similarity annotations, so may be vulnerable to misannotation, or functional misinterpretation (notable examples of definitively annotated, but functionally ambiguous genes such as phoH and cobS have been well documented in viruses). The authors did not to include any further domain-based or phylogenetic checks for the genes important the main conclusions.

Overall, the manuscript presents a valuable hypothesis and highlights new ecological patterns in coral reef viral metagenomes. The revision substantially improves the discussion of the claims, but the evidence linking temperate viruses to specific metabolic functions and reef-scale outcomes remains incomplete. The work would be strengthened by analyses that directly link metabolic genes to viral genomes or lysogeny markers, address compositional effects, validate key annotations, and more clearly distinguish observed gene-frequency associations from hypothesized effects on infection, host metabolism, and reef state.

Author response:

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

eLife Assessment:

The worldwide decline in the health of coral reefs is well documented, and overgrowth by microbial consortia can be a contributing factor. Kelman and colleagues used metagenomic analysis to interrogate potential changes in phage-associated genes predicted to be involved in central carbon metabolism. The study addresses the hypothesis that metabolic genes associated with carbon metabolism that are encoded by viruses reflect the health of the corals. The study contributes a valuable perspective on the potential role of phages in coral health, although limitations of the data and analyses offer an exploratory examination rather than a definitive result. Overall, the evidence supporting the major findings is incomplete, in part because the conceptual model relies on qualitative assumptions rather than empirical data.

We want to first thank both reviewers and the editor for their comments. They were incredibly constructive and thoughtful, and provided a roadmap to a much stronger paper for us to follow. Guided by the comments, we have sought not only to address the individual points raised below, but also to expand upon them where doing so improved the clarity and accessibility of the work. The paper is now stronger, more focused, more conservative, and more robust because of the guidance provided by the reviewers. Thank you.

In addition to more point-by-point issues, the manuscript has been strengthened in three main ways:

(1) Clarified the distinction between observations, inferences, and broader ecological implications, ensuring that empirical results, conceptual synthesis, and model predictions are clearly separated throughout the manuscript.

(2) Reframed and expanded the presentation of the conceptual model, clarifying its purpose as a qualitative framework for integrating our observations with established reef ecology and for generating experimentally testable hypotheses, rather than as an additional source of empirical evidence.

(3) Clarified the analytical framework and statistical interpretation, including expanding the Methods to better explain the inferential pipeline, the interpretation of community-level metabolic associations, and the use of bootstrapped confidence intervals to quantify uncertainty around ecological effect sizes.

Although the reviewers approached the manuscript from different perspectives, we found their recommendations to be remarkably complementary. Reviewer 1 consistently encouraged us to improve the clarity, transparency, and accessibility of the manuscript, while Reviewer 2 challenged us to more carefully align the strength of our conclusions with the strength of the available evidence. Rather than addressing these concerns independently, we used them as the basis for a broader restructuring that simultaneously improved the manuscript's organization, transparency, clarity, and evidentiary discipline. We believe the result is a substantially stronger paper.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Microbialization (bacterial overgrowth) is a recognized component of degraded, eutrophied coral reefs where there is a shift from coral to algal dominance on the benthos. In addition, previous work has demonstrated that virus communities shift from a lytic strategy dominated (kill-the-winner) to a temperate (lysogenic) strategy dominated with reef microbialization. Kelman et al. sought to leverage previously published virus metagenomes produced from the water column of healthy and degraded coral reefs to assess virus community metabolic shifts. The authors also produce a conceptual model to demonstrate the potential impact of the observed metabolism shifts on reef fates.

Strengths:

The main strength of the manuscript is the findings from their metagenomic analyses and results. The virus metagenomes were produced using established approaches in the field and yield sufficient data per sample for their analyses. Interesting results regarding the shift in the types of genes from anaplerotic to cataplerotic provide the foundation for testable hypotheses to determine the magnitude of impact virus strategies have on reef health. The introduction is also well written and sets up the scene very well.

Weaknesses:

(1) The methods text currently omits important information related to the sampling design. It is not clear how many metagenomes are from healthy and degraded communities. This impacts the interpretability and robustness of the statistical results. Furthermore, it is unclear if analyses are based on assembled contigs or read-based alignments. Improving the clarity and organization of the Methods is essential for reproducibility.

(2) Regarding the bioinformatics approach, normalization using the "per cent known" approach within samples may not fully account for discovery bias related to sequencing depth. While Supplementary Table 1 shows variability in read counts, the lack of community-level metadata makes it difficult to determine if sequencing depth covaries with community type (healthy vs. degraded). The study would benefit from a rarefaction analysis or subsampling to ensure that gene frequency trends and Spearman correlations are biological signals rather than artifacts of sequencing effort.

(3) The qualitative model in Figure 5 is positioned as evidence for the role of viruses in reef health, but it does not provide independent support for the authors' hypotheses. Since the model is parameterized using "arbitrary units" to reflect the authors' assumptions rather than being derived from the empirical metagenomic data, it serves as a helpful illustration of a hypothesis but not as a validation of the findings.

(4) Results and discussion require revisions to improve readability and connectivity across sections. Ensuring a clear distinction between empirical data and model-based speculation would help the audience better appreciate the science.

We thank the reviewer for their thoughtful and constructive review. Their comments were particularly helpful in identifying opportunities to improve the clarity, organization, and reproducibility of the manuscript. In response, we substantially expanded and reorganized the Methods, streamlined the Results and their connection to the Discussion, and clarified the role of the conceptual model as a framework for integrating our observations and generating testable hypotheses rather than as independent empirical evidence. We respond to the specific comments below.

Reviewer #2 (Public review):

Summary:

The manuscript by Kelman and coauthors investigates how viral communities differ in the genes they encode in healthy and degraded coral reef ecosystems. Across 19 viral metagenomes from Central Pacific reefs, the authors assess the frequency of integration/excision genes as a proxy for viral community temperateness and ask whether genes associated with central carbon metabolism covary with signatures of temperateness. The main finding is that viral communities with more temperate-related genes encode more genes from the Entner-Doudoroff pathway and other reactions interpreted as anaplerotic, whereas more lytic-associated viral communities show greater representation of some pentose phosphate pathway, TCA, and redox-associated genes interpreted as cataplerotic. The authors propose a model based on these patterns in which lytic viral metabolism helps suppress bacterial overgrowth on healthy reefs, while temperate viral metabolism may promote microbialization on degraded reefs. The study addresses an interesting and potentially important concept - that viral auxiliary metabolic genes are important components of microbial communities and can affect ecosystem functioning. Linking viral metabolism to coral reef microbialization is a creative conceptual advance. The manuscript is clearly written, and the reported enrichment of anaplerotic genes in temperate-associated viromes is an interesting pattern that could motivate future work on how viral metabolic potential varies across reef states.

Strengths:

(1) The study connects viral lifestyle, central carbon metabolism, bacterial overgrowth, and reef degradation in a framework that could be useful for future studies of coral reef ecosystems and viral ecology. This is an interesting synthesis that links viral auxiliary metabolism to broader questions about microbialization and reef state.

(2) The manuscript is generally clearly organized around a testable prediction: viral metabolic gene content should vary along a lytic-to-temperate viral community gradient. The reported enrichment of anaplerotic genes in viromes with a larger fraction of temperate viruses is a compelling result.

(3) The authors highlight several virus-encoded metabolic genes that may not have been previously reported in viral datasets or genomes. If supported by further validation, these observations could expand the known repertoire of viral metabolic potential.

(4) The modeling helps clarify the feedbacks the authors propose may connect viral lifestyle, bacterial metabolism, and coral reef degradation. It provides a foundation for generating hypotheses about how viral metabolic genes could influence reef microbial dynamics.

Weaknesses:

(1) The main limitation is that the evidence for several key claims remains indirect. The core analysis is based on correlations between metabolic gene frequencies and integration/excision-related genes. This does not demonstrate that the metabolic genes occur in temperate viral genomes, are physically linked to lysogeny genes, are expressed during infection, or alter host metabolism. Thus, the data support an association between VLP-associated metabolic annotations and a community-level temperateness proxy, but not a direct link between temperate phages and these metabolic functions.

(2) It is important not to equate community-level gene frequencies with genome-level or infection-level metabolic programs. A virome may contain more anaplerotic genes overall, but that does not demonstrate that individual viruses reprogram their hosts in an anaplerotic manner nor that infection produces a net anaplerotic effect. Individual viruses may encode both anaplerotic and cataplerotic genes, and a smaller number of cataplerotic genes could have stronger metabolic consequences depending on expression, enzyme efficiency, pathway position, and host context. This is an important limitation that should be acknowledged and, if possible, addressed with contig- or genome-level analyses.

(3) The ecological interpretation assumes that viral infection is strong enough to influence reef-scale bacterial population dynamics. However, the study does not directly measure infection frequency, lysis rates, viral production, burst size, lysogeny frequency, prophage induction, gene expression, or bacterial mortality. If viral mortality or lysogenic conversion were rare in these systems, the observed gene-frequency patterns could have limited ecosystem-level consequences. This makes claims about viral metabolism suppressing bacterial overgrowth, accelerating microbialization, or acting as a conservation lever more speculative than suggested.

(4) There are statistical limitations related to the use of relative gene frequencies. Because genes are normalized as percentages of known genes, the data are compositional. Apparent increases in some categories may partly reflect decreases in others. Bootstrapped Spearman correlations are useful for assessing the robustness of these associations, but they do not address compositionality or multiple testing.

(5) The anaplerotic/cataplerotic classification is central to the manuscript's conclusions and would benefit from more support. The framework is useful, but it depends on both annotation confidence and biochemical context. Sequence-similarity annotations alone may be vulnerable to misannotation, especially for central metabolic enzymes that share conserved domains across functionally distinct proteins. Stronger evidence that key genes contain key functional domains and/or are phylogenetically related to characterized enzymes would help support the proposed functions. In addition, many central carbon enzymes are reversible or context-dependent, so a clearer rationale for each classification would strengthen the interpretation.

Overall, the manuscript presents a valuable hypothesis and highlights new ecological patterns in coral reef viral metagenomes, but falls short of the evidence needed for the strongest claims. The work would be strengthened by analyses that directly link metabolic genes to viral genomes or lysogeny markers, address compositional effects, validate key annotations, and more clearly distinguish observed gene-frequency associations from hypothesized effects on infection, host metabolism, and reef state.

We thank the reviewer for their careful and constructive assessment. Their comments were particularly valuable in sharpening the evidentiary boundaries of the study. In response, we revised the manuscript throughout to distinguish more clearly between the community-level gene-frequency associations we observe and genome-level linkage, infection-level metabolic effects, and ecosystem-level consequences that remain hypotheses for future testing. We also revised the statistical presentation and discussion of methodological limitations to better reflect the strength and scope of the available evidence. We respond to the specific comments below.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Significance

General comments

Well written and highlights the findings of the study. However, the final sentence needs rewording to be clearer regarding the claims being made (see below).

Specific comments:

Lines 86-88 - I suggest revising the final sentence to better match the strength of the data presented. As currently written, the sentence makes broad causal claims that are not directly supported by the results.

For example, the phrase "viral metabolism can either reinforce reef resilience or exacerbate collapse" implies a level of mechanistic certainty that the current data do not demonstrate. The results show shifts in viral community metabolism, measured through gene abundances, that are likely associated with changes in the environment, host assemblages, and virus community diversity. These shifts may potentiate the DDAM feedback loop, but additional data and experimental work would be needed to determine whether viruses actively maintain resilience or contribute to collapse.

Similarly, the phrase "making it a hidden driver of ecosystem fate" feels too strong for the results presented. A more appropriate framing would be to present viral community metabolism as a promising and important avenue for future research into reef trajectories and ecosystem change.

Finally, the phrase "a potential target for conservation strategies" is somewhat unclear. It is not obvious whether viral metabolism is being framed as something conservation efforts should directly manipulate, or as an indicator/marker of reef condition and recovery. Clarifying this would strengthen the significance statement.

We thank the reviewer for this thoughtful and constructive suggestion. We agreed that the Significance statement occasionally conveyed greater mechanistic certainty than was supported by the observational nature of the data. Guided by these comments, we revised the section throughout to more clearly distinguish between our empirical observations, the ecological interpretations they support, and the broader hypotheses and implications they motivate. In particular, we softened causal language regarding the role of viral metabolism in reef resilience and decline, reframed the discussion of conservation to emphasize future opportunities rather than immediate application, and clarified that the manuscript provides a conceptual ecological framework for future investigation rather than direct evidence of ecosystem-scale mechanisms. We believe these revisions now more accurately reflect both the strengths and the limitations of the study while preserving its central ecological significance (lines 78-93).

(2) Abstract

Specific comments

Lines 97-102 - Add commas to improve readability:

Original: We found that viral metabolism shifted broadly from being dominated by metabolism that builds up pools of central intermediates on degraded reefs dominated by temperate viral infection ('anaplerotic' reactions) to metabolism that consumes these pools to prioritize production of metabolic precursors for virion construction on healthy reefs dominated by lytic infection ('cataplerotic' reactions).

Revised: We found that viral metabolism shifted broadly from being dominated by metabolism that builds up pools of central intermediates on degraded reefs, dominated by temperate viral infection ('anaplerotic' reactions), to metabolism that consumes these pools to prioritize production of metabolic precursors for virion construction on healthy reefs, dominated by lytic infection ('cataplerotic' reactions).

Thank you. We agreed that this sentence needed revision for clarity. In addition to improving its readability, we revised it to describe the observed pattern explicitly at the level of viral-community metabolic gene content rather than implying a demonstrated shift in metabolism itself (lines 102-107).

(3) Introduction

General comments

Very well written introduction that sets up an exciting scene!

Specific comments

Lines 134-136 - Minor revision to improve readability:

Original: "Viral predation could, in principle, preclude microbialization by killing proliferating microbes, as lytic infection and lysis rates are predicted by established predator-prey models to rise with host densities and growth rates"

Revised: "Viral predation could, in principle, preclude microbialization by killing proliferating microbes, as lytic infection and lysis rates are predicted to rise with host densities and growth rates by established predator-prey models."

Thank you. We are glad the Introduction was engaging. We have adopted this edit (lines 140-142).

(4) Methods

General comments

The methods text needs to be revised to increase readability and transparency. I would love to really appreciate the work done and the results produced, but some aspects are unclear, which leaves me with a cloudy understanding of how the data was processed and the results were generated. I am also concerned that the qualitative model makes many assumptions regarding ecological interactions between the components. It might be good to clearly state these assumptions and their impact on the outcome in a table or explicitly within the text.

We thank the reviewer for these thoughtful comments. We agreed that the original Methods section did not always provide sufficient detail to allow readers to fully understand the analytical framework or the inferential pathway from the underlying sequence data to the ecological conclusions presented. Rather than addressing these comments individually in isolation, we substantially reorganized and expanded the Methods to improve transparency, readability, and reproducibility throughout. In particular, we clarified the study design and sampling framework, explicitly distinguished between the previously generated viral metagenomic datasets and the new analyses performed in this study, and expanded our description of the bioinformatic and statistical workflows. We also more clearly explain our decision to retain the community-level, read-based analytical framework of the previous studies while extending those analyses using the MG-RAST annotation platform. By avoiding a fundamentally different analytical approach, we maintain conceptual continuity and direct comparability. Finally, we clarified the assumptions underlying the conceptual model and its intended role as a qualitative framework for hypothesis generation rather than empirical validation. Collectively, these revisions provide a clearer, more transparent, and more reproducible account of the analytical framework used throughout the study (lines 206-390; this spans the entire Methods section).

Specific comments (reordered for clarity where needed)

Line 189-190 - Sentence needs rewording. Currently, it reads a bit awkwardly, and it should be clearer that these metagenomes were previously produced and sourced from a different manuscript. It reads as if data were generated from new samples and processed as previously described, rather than a reanalysis of a dataset.

Line 189-212 - Information related to the sample design (e.g., how many metagenomes from how many reefs/reef health states) is missing and should be added in this section to provide more context for the reader.

We thank the reviewer for this helpful suggestion. We have substantially revised the opening of the Methods to clarify that this study is an analysis of previously generated virus-like particle (VLP) metagenomes, most of which had been used in prior publications, from Pacific coral reefs rather than newly generated samples. We also expanded the description of the sampling design, including the number of metagenomes analyzed and their relationship to previous studies, and explain that we retained a bioinformatic framework closely aligned with those earlier analyses to maintain methodological continuity and enable direct comparison with the published work. We agree that these additions improve the clarity, transparency, and reproducibility of the study (Intro lines 173-176, Methods lines 206-211, Supplementary Table 1).

Line 208-210 - This sentence produced concern upon reading it. If contamination is a worry and would have a direct impact on the results (especially given that results seem to be based on read alignments to a reference database), I suggest a bacterial read removal step with Kraken or alignment to a bacterial reference be performed prior to functional annotation. Given that there were multiple steps in the VLP DNA processing/extraction, there is unlikely to be a large amount of bacterial sequence reads; however, it would be good to confirm.

Lines 213-218 - It is unclear if the reads were assembled into a contig prior to annotation. In addition, in the Supplementary Table 1, please clarify if "sequences" is equal to reads or assembled contigs. 

We thank the reviewer for these helpful comments. We have clarified that the analyses are based on read-level annotations rather than assembled contigs, consistent with the original virome studies and with our aim of maintaining methodological continuity with those published analyses. We also expanded the Methods to describe the multiple safeguards used to minimize cellular contamination, including 0.45-µm filtration and chloroform treatment, cesium chloride purification, DNase treatment, microscopy confirming the absence of cells, and PCR confirmation of the absence of detectable 16S rDNA amplification. While no purification protocol can completely exclude the possibility of trace contamination, these independent purification and validation steps substantially reduce this possibility. We have therefore retained the existing read-level analytical framework while making both its basis and its limitations clearer in the revised manuscript (lines 205-252).

Line 219-224 - I am concerned that allowing alignment lengths as short at 15 bp will lead to false positives. Considering the minimum read length is 100 bp, a 50 bp alignment length is a more reasonable cutoff.

We thank the reviewer for drawing our attention to this point. In reviewing the MG-RAST parameters, we identified that the original manuscript incorrectly described the minimum alignment-length setting as 15 bp. The MG-RAST parameter used in our analysis is a minimum alignment length of 15 amino acids, and we have corrected the Methods accordingly. We have also clarified that these are the default MG-RAST annotation settings and that, because they are permissive, the resulting read-level annotations are used here for relative comparisons of broad functional representation among identically processed viromes rather than to establish the function of any individual read (lines 243-252).

Lines 231-232 - The described normalization approach does not account for sequencing depth per sample since, based on how I interpret the text, you are calculating the relative abundance of genes within a sample. This does not control for the potential increase in the number of detected genes within a sample driven by higher sequencing depth. To confirm that sequencing depth does not influence results, I suggest performing a rarefaction analysis or having a subsampling step to test for the sensitivity of read depth on results.

We thank the reviewer for this thoughtful comment. Our objective was to compare the relative frequencies of annotated functional categories within viral communities rather than estimate absolute gene abundance or gene richness. We therefore normalized gene frequencies within each virome as the proportion of annotated ("known") genes, allowing direct comparison of relative community composition among metagenomes with differing sequencing depths. This normalization strategy is also consistent with our previous community-level analyses of these viromes. To make this analytical framework clearer, we have substantially expanded the Methods to explain the rationale for this normalization approach, how higher-order functional categories were constructed, and how gene frequencies were compared across samples (lines 296-316).

We also clarify a related consequence of this normalization. Because gene frequencies are expressed as proportions of a common total of annotated genes, the data are compositional, and an increase in the relative frequency of one category is necessarily accompanied by decreases in others. We have now added an explicit statement of this limitation to the Methods and clarify that the values reported here represent relative community composition rather than absolute gene abundance (lines 253–257).

Line 240 - Define "EC" -> "... Enzyme Commission (EC) numbers...". All abbreviations should be clearly defined prior to use throughout the manuscript.

Line 262 - Minor: Define the acronym "CIs" here - "Confidence intervals (CIs)..."

We thank the reviewer for identifying these omissions. We now define Enzyme Commission (EC) upon first use in the manuscript in the Methods and Results sections (lines 261 and 423). Similarly, we now define confidence intervals (CIs) when introduced in the Methods and Figure 1 legend (lines 283–286 and 777–778).

Lines 264-265 - This sentence is repeated later in the manuscript, and it's not clear what is meant as is. I would revise to make it more clear it is meant to signal that the CIs will be within brackets within the text. Or, it may be best to just have CIs like so:

Example from line 372:

Original = "(Figure 1; ρs = -0.81; [-0.95, -0.58])"

Suggested revision throughout the manuscript = "(Figure 1; ρs = -0.81; CIs: -0.95, -0.58)"

We thank the reviewer for this helpful suggestion. To improve clarity, we now explicitly state in the Methods that 95% confidence intervals are reported in square brackets following each Spearman's rho estimate (lines 285-286), and we have changed Figure 1 to be consistent with that (lines 777-778). We retained this notation because it provides a compact and consistent presentation of the effect size and its associated uncertainty.

Lines 270-273 - Unclear what is being measured, diversity of genes within samples? Or is taxonomic diversity present within samples?

Thank you for pointing this out. We have now clarified that diversity is the Shannon index (H’) using the relative frequencies of annotated functional genes in each sample (lines 290-293).

Line 276-279 - Add "to" in "...was defined aid our..."

We thank the reviewer for identifying this issue. This sentence has been revised as part of our broader effort to improve the clarity of the manuscript (lines 319-322).

(5) Results

General comments

I believe this section would benefit from a bit of reorganization to help the flow of the manuscript. Certain sections, like the "Functional homologues as viral lifestyle markers", are not descriptive enough, and it is unclear how "the divergent correlations in these genes across a viral temperateness spectrum may reflect viral life strategies" is justified. Also, several results are not discussed in the discussion.

We thank the reviewer for this helpful observation. We agree that the Results would benefit from clearer organization and stronger links between individual observations and their broader interpretation. In response, we substantially reorganized the Results to improve their logical progression. We moved explanatory material describing the analytical framework to the Methods and reorganized the remaining Results from broad community-level patterns to increasingly focused analyses of central carbon metabolism. We also revised the Discussion to ensure that the principal observations presented in the Results are revisited and interpreted within the broader ecological framework developed in the manuscript. More broadly, the revised framing now consistently presents individual observations as community-level associations and their ecological implications as hypotheses rather than definitive functional interpretations (Introduction lines 190-195, Methods lines 296-316, 317-327 and 328-330; Results lines 392-518; Discussion, lines 525-529).

We agree that the original “Functional homologues as viral lifestyle markers” section overinterpreted these community-level associations. Because the confidence intervals for the two fructose-bisphosphate aldolase homologues both span zero, we have removed this subsection rather than present these patterns as evidence for viral lifestyle markers. The individual estimates remain reported in Table 1 for completeness.

Specific comments

Lines 346-369 - Overall, this "Hallmarks of viral temperateness" text seems more appropriate for the methods section and/or a figure/table caption rather than a results section. It is unclear to me whether there are any results being presented here; instead, it reads more like a description of how to interpret upcoming results. The text should be revised to make the results more clearly presented or moved to a more appropriate section of the manuscript.

We agree, and have moved the explanatory material into the Methods/Analytical Framework and rewritten the opening of the Results so that this section now presents observations rather than instructions for interpreting subsequent analyses (Methods, lines 296-316; Results, lines 392-403).

Line 353-355 - This sentence needs revision. It feels like two similarly themed, but mismatched, sentence fragments. The first part sets up for a methods statement, but the second part defines a metric?

Sentence: "As a measure of how consistently or monotonously gene frequency and sample temperateness covary, Spearman Rho (ρs) values reflect the strength and sign of their correlation."

Maybe it is just how I am reading it, but I feel it should be revised to (or something similar):

"As a measure of how consistently or monotonously gene frequency and sample temperateness covary, a Spearman's Rank Correlation analysis was performed, generating Spearman Rho (ρs) values reflecting the strength and sign of their correlation."

We thank the reviewer for this helpful observation. We agree that the opening of the Results conflated methodological explanation with the presentation of results, resulting in awkward phrasing and reduced clarity. Rather than simply revising the sentence, we substantially reorganized this portion of the manuscript. The analytical framework, including the rationale for the temperateness proxy, the interpretation of Spearman's ρ, and the relationship between Figures 1–5, has now been moved to a dedicated Analytical framework subsection of the Methods. This allows the Results to focus directly on the empirical observations while presenting the methodological context in its more appropriate location. We believe this restructuring substantially improves the clarity and flow of the manuscript (lines 272-316 and 392-403).

Line 357 - Missing a closing parenthesis on "(ps < 0."

Line 357-358 - In this sentence, it says the 95% confidence intervals are listed in square brackets (I am assuming in Figure 1). But Figure 1 has confidence intervals in parentheses, and this is stated within the figure caption as well. Needs to be made consistent across components of the manuscript. Revisiting this comment as I read the next section of the results, I understand now what was meant regarding the brackets. This should be clarified here (and previously).

Corrected. The missing parenthesis was added during the revision and restructuring of this section, and the presentation of confidence intervals has been standardized throughout the manuscript using square brackets for consistency and clarity (lines 285-286, 394-397, and the Figure 1 legend, line 777-778).

Lines 465-500 - The text here presents model results as valid biological outcomes. There is also a bit of discussion text in this section. Given this is a qualitative model with many strong assumptions, it's best to illustrate hypotheses rather than being framed as evidence.

We thank the reviewer for this important observation. We agree that the original presentation did not always sufficiently distinguish between the empirical observations presented in this study and the qualitative hypotheses generated by the conceptual model. We therefore substantially revised both the Results and the Discussion to more clearly separate these two levels of inference. Throughout the manuscript, the conceptual model is now consistently presented as a qualitative framework for integrating our observations with established reef ecology and for generating experimentally testable hypotheses, rather than as independent empirical evidence. Correspondingly, we adopted more conservative language throughout this section to ensure that model outputs are interpreted as conceptual scenarios illustrating possible ecological consequences of the observed community-level metabolic associations, rather than as demonstrated biological outcomes. We believe these revisions more accurately reflect both the purpose of the model and the observational nature of the underlying data (Methods, lines 317-330; Results, lines 483-518; Discussion, eg line 527).

(6) Discussion

General comments

There are a lot of results explicitly mentioned in the Results section left out of the discussion. Revisions can be made to increase the connectivity between sections and streamline the story of the manuscript to help the reader appreciate the findings and implications.

We thank the reviewer for this suggestion. In revising the manuscript, we substantially reorganized the Discussion to focus on the principal findings and their broader ecological implications. The revised Discussion now revisits the major observations underlying our conclusions while distinguishing more clearly between empirical observations, ecological inferences, and conceptual hypotheses. We elected not to discuss every individual observation in detail, instead focusing the Discussion on those findings most central to the manuscript's overarching conclusions.

(7) Figures

Figure 1 - A previous comment was made regarding the mismatch between the CIs in brackets and the figure containing them in parentheses (not a fatal error, just a quick fix in the text). An additional recommendation for this figure is to make it clearer which gene correlations are significant. In the main text and within the figure caption, it states that:

"Genes where the 95 % confidence intervals exclude zero are significant at the p < 0.05 level."

Within the figure, there are a few genes that don't seem to be significant given this guideline (Cell division & cycle, Stress response, Protein metabolism). I suggest some sort of visual aid that would allow the reader to determine which are significant and which are not. Adding an asterisk to all significant correlations (or removal of non-significant) could help interpretability for the reader.

The authors may also want to consider some visual way to signal temperature-associated vs lytic-associated genes in the figure. One way may be to organize the panels into lytic- and temperate-associated groups.

Thank you for these suggestions. Confidence intervals are now presented consistently in square brackets throughout the manuscript. We substantially revised the statistical presentation throughout the manuscript (lines 285-286, 397, 777-778). Rather than emphasizing null hypothesis significance testing, we now consistently present bootstrapped median Spearman’s ρ estimates together with 95% confidence intervals to quantify uncertainty around each estimate (lines 287-289). We believe this presentation more clearly communicates the magnitude, direction, and uncertainty of the observed community-level associations. Because these confidence intervals are not adjusted for multiplicity, we elected not to add asterisks to Figure 1 or to use confidence-interval exclusion of zero as the primary basis for our conclusions. The Figure 1 legend instead states that the confidence intervals quantify uncertainty and do not represent multiple-testing-adjusted significance (lines 785-786). Asterisks retained in Table 1 and Figure 2 are provided only as visual guides and are not interpreted as formal discoveries (lines 765-766, 797-799). Instead, our interpretation emphasizes the magnitude, uncertainty, direction, and coherence of associations across predefined pathways and functional categories.

In terms of figure layout, we retained mean gene frequency ordering of the functional categories to facilitate navigation of the figure. Because Figure 1 serves primarily as a reference across a broad range of SEED Level 1 functional categories, we felt that mean gene frequency ordering provides the clearest and most accessible presentation to help contextualize our results. We now clarify the meaning of positive and negative correlations in the figure legends for Figures 1 and 2: “Positive Spearman’s ρ values indicate temperate-associated gene categories, whereas negative ρ values indicate lytic-associated gene categories” (lines 778-780, 792-794).

(8) Data availability

I tried to access data on MG-RAST servers and was unable to find them due to a server error.

We thank the reviewer for bringing this to our attention. We have also occasionally encountered intermittent server availability on MG-RAST. To ensure continued accessibility of the underlying data, the FASTA files for all metagenomes, together with the project code, annotations, and simulation files, are also available through our GitHub repository (https://github.com/hopefulmonstersucla/viral-metabolism; lines 583-590). We continue to provide the MG-RAST accession numbers as the primary archival record of the datasets, while the GitHub repository provides an alternative access route should MG-RAST be temporarily unavailable.

To end, we again thank the reviewer for their thoughtful and constructive review. Throughout the revision, their comments consistently encouraged us to improve the clarity, organization, and accessibility of the manuscript. We believe the resulting paper is substantially clearer, more transparent, and more accessible to readers, and we are grateful for the roadmap the reviewer provided.

Reviewer #2 (Recommendations for the authors):

(1) My largest concern is that the language in the manuscript moves from gene frequency correlations to claims about viral metabolism driving reef decline, supporting bacterial proliferation, and offering a conservation lever. The abstract says the findings position viral metabolism as both a driver of reef decline and a conservation lever, with "re-viralization" as a restoration strategy. I do not think the current data support that level of inference. I believe the authors should consistently and clearly distinguish between conclusions that the data support (Viral communities are associated with different metabolic gene profiles. Those genes may indicate different metabolic potentials.) and those that are speculative, not demonstrated outcomes (Those potentials may influence host metabolism during infection. Those infection-level processes may alter reef-scale microbialization.) in their writing.

We thank the reviewer for identifying what we also came to view as the central issue in revising the original manuscript. We agree that the original framing did not always clearly distinguish between our empirical observations, the ecological inferences they support, and the broader hypotheses that they motivate. Addressing this concern became a major focus of the revision. Throughout the manuscript, we now consistently distinguish between community-level observations, conceptual interpretation, and broader ecological implications. We substantially revised the Significance statement, Abstract, Introduction, Results, Discussion, and conceptual model to ensure that the strength of our conclusions reflects the strength of the underlying evidence. In particular, we now present the observed metabolic associations as community-level patterns, while framing their potential consequences for infection, host metabolism, microbialization, and reef resilience as hypotheses generated by our conceptual framework rather than demonstrated outcomes. We believe this distinction now more accurately reflects both the scope of the data and the purpose of the study.

(2) A broader issue is the presentation and interpretation of the many correlation analyses. Figures 1 and 2 contain a large number (20+) of small panels, and it is difficult to assess which relationships are most important, what the direction of each relationship is, and which results are well supported. Because the manuscript's conclusions rely on recognizing broader patterns across many categories and genes, I think these figures should do more to guide interpretation. Some combination of color and symbol could improve readability. For example, using different colors for positive vs negative correlations and a separate indicator for whether confidence intervals exclude zero or whether results remain significant after multiple-testing correction. A compact summary panel or heatmap may also help readers synthesize the overall pattern more efficiently. Relatedly, the manuscript appears to evaluate a large number of separate correlations, but I do not see a correction for multiple testing. Interpreting each correlation based on whether its 95% bootstrap confidence interval excludes zero does not address false discovery across the full set of comparisons. I recommend that the authors report the number of tests performed and apply an appropriate false discovery rate correction, such as Benjamini-Hochberg. This would make it much easier to distinguish the most robust results from more tentative patterns.

We thank the reviewer for this thoughtful suggestion. We agreed that the original presentation required clearer guidance to help readers interpret the broader patterns across the many community-level correlations. In response, we substantially revised both the analytical framework and the figure framing. The manuscript now explicitly explains the interpretation of positive and negative Spearman’s ρ values within the Methods, and the legends for Figures 1 and 2 now clarify that positive correlations indicate temperate-associated gene categories whereas negative correlations indicate lytic-associated gene categories (lines 778-780, 792-794). Figure 1 retains all functional categories and presents their bootstrapped ρ estimates and 95% confidence intervals without asterisks. Its legend states that the confidence intervals quantify uncertainty and do not represent multiple-testing-adjusted significance (lines 785-786). Table 1 and Figure 2 retain asterisks only as visual guides to intervals that exclude zero, and their legends explicitly state that these do not represent multiple-testing-adjusted significance (lines 765-766, 797-799).

With respect to multiple testing, our objective was not to identify a small subset of individually significant genes through formal hypothesis testing, but rather to characterize broad community-level metabolic patterns across predefined functional categories and pathways. Accordingly, we emphasize bootstrapped effect sizes together with their associated confidence intervals to quantify uncertainty around each estimate, rather than relying primarily on null hypothesis significance testing. We therefore retained this estimation-focused analytical framework throughout the manuscript (eg lines 287-289). Finally, because Figures 3 and 4 already synthesize the pathway- and functional-level patterns emerging from the individual correlations shown in Figures 1 and 2, we elected not to add an additional summary heatmap, as we felt this would largely duplicate information already presented.

We also thank the reviewer for raising compositionality, which we agree we had not engaged with adequately in the original manuscript. Because gene frequencies are expressed as proportions of a common total of annotated genes, the data are compositional, and an increase in the relative frequency of one category is necessarily accompanied by decreases in others. We have now added an explicit statement of this limitation to the Methods and clarify that the values reported here represent relative community composition rather than absolute gene abundance (lines 253–257).

(3) The manuscript would be strengthened by additional scrutiny of the gene annotations and the viral origin of the metabolic genes. The conclusions depend on the interpretation that specific central carbon metabolism genes are encoded by viral communities and vary with viral lifestyle. However, the current analysis appears to rely primarily on read-level annotation against SEED/MG-RAST categories. This is useful for broad screening, but I do not think it is sufficient on its own to support the stronger claims about viral metabolic strategy. I recommend that the authors add additional validation steps for the key metabolic genes that drive the manuscript's conclusions. For example, metagenomic assembly could be used to determine whether central carbon metabolism genes occur on contigs with viral hallmark genes, especially integrases, excisionases, structural genes, or other viral replication genes. This would help establish whether the metabolic genes are physically linked to viral genomes (likely, but good to independently test) and whether they are associated specifically with temperate viral genome fragments (currently unclear). If assemblies are limited by read depth or read length, the authors should report this clearly and present the analysis as a limitation. I also recommend additional functional validation of the key enzyme annotations. For the genes that support the main anaplerotic/cataplerotic conclusions, the authors could use protein-domain-based annotation, reciprocal best-hit approaches, HMM searches, or phylogenetic analyses to confirm that these reads or contigs encode the proposed enzyme functions. These additional analyses do not need to validate every annotated gene in the dataset, but they should focus on the subset of genes that carry the main conclusions and those that are the most novel. This would make the manuscript's central claims much more convincing and would help distinguish robust viral metabolic signals from more tentative read-level functional assignments.

We thank the reviewer for this thoughtful suggestion. We agree that contig-level analyses, protein-domain validation, and phylogenetic confirmation would provide valuable complementary evidence regarding the genomic context and evolutionary history of individual metabolic genes. However, these analyses address a different question from the one considered here. Our objective was to characterize community-level associations between viral metabolic gene frequencies and a previously established proxy for viral community temperateness using the same read-based analytical framework as the earlier studies on which this work builds. To make this scope clearer, we substantially expanded the Methods to explain our rationale for retaining this analytical framework and revised the manuscript throughout to ensure that our conclusions are explicitly limited to community-level metabolic associations rather than genome-level linkage or infection-level function (eg 206-208, 296-316). We now consistently present these observations as generating hypotheses regarding viral metabolic strategies that future genome-resolved studies can test directly (eg lines 185-195, 317-330, 525-529). We believe these revisions more accurately align the strength and scale of our conclusions with the evidence presented.

(4) The anaplerotic/cataplerotic classification in Table 1 is a core part of the manuscript, but the rationale for several gene assignments is not sufficiently clear. I appreciate that the authors define these terms more broadly than their conventional TCA-cycle usage. However, many of the enzymes listed in Table 1 are reversible or participate in multiple pathways, so their classification depends on assumed flux direction and physiological context rather than gene presence alone. I recommend that the authors add a supplementary table explaining the rationale for each anaplerotic/cataplerotic assignment, including the assumed reaction direction and the relevant substrate and product pools.

We thank the reviewer for this thoughtful suggestion. We agree that anaplerotic and cataplerotic classifications depend on biochemical context and do not imply that every enzyme involved is intrinsically irreversible. These terms are also commonly applied within the TCA cycle to reversible reactions when their predominant net flux, under a given physiological context, replenishes central metabolite pools (anaplerotic) or draws from those pools toward energy production or specialized biosynthetic precursors (cataplerotic). We use the terms in this broader functional sense rather than restricting them to TCA-cycle reactions alone (lines 102-107, 262-271). Accordingly, the assignments in Table 1 reflect the expected predominant role of each reaction within the pathway context represented in Figure 3 (see line 271), rather than a demonstrated in vivo flux direction during infection. Figure 3 explicitly distinguishes reversible reactions with double-headed arrows from irreversible reactions with single-headed arrows, while Table 1 presents each classification alongside its pathway, gene identity, and enzyme annotation. We therefore felt that an additional supplementary table would largely duplicate information already presented across the Methods, Table 1, and Figure 3.

(5) Minor comment: I suggest revising phrases such as "the conceptual model reveals" to something like "the numerical model suggests" (e.g. line 179).

We thank the reviewer for this helpful suggestion. Throughout the revised manuscript, we adopted more cautious language when describing the conceptual model and its outputs. We now consistently use language such as suggests, illustrates, explores, and predicts rather than wording that could imply direct empirical demonstration. These changes permeate the entire revised manuscript. These revisions are consistent with our broader effort to present the model as a qualitative conceptual framework for integrating our observations with established reef ecology and for generating experimentally testable hypotheses, rather than as an independent source of empirical evidence (lines 111-118, 185-195, 317-330, 483-518, and 569-582).

To end, we again thank the reviewer for their thoughtful and insightful review. Their comments consistently challenged us to better align the strength of our conclusions with the strength of the available evidence. As a result, we substantially strengthened the manuscript by more clearly distinguishing between empirical observations, ecological inferences, and conceptual hypotheses. We believe these revisions have made the manuscript more rigorous, more transparent, and ultimately a stronger contribution, and we are grateful for the careful consideration the reviewer gave to our work.

eLife Assessment

This valuable study presents a mechanistic model of predictive coding by medial entorhinal cortex grid cells, implemented with biologically detailed conductance-based neurons. The evidence supporting the emergence of this coding scheme from specific membrane currents and the anatomical connectivity among inhibitory neurons is convincing. This work will be of interest to neuroscientists working on spatial navigation, circuit dynamics, and neuronal coding.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors aim to elucidate the mechanisms by which grid cells in the medial entorhinal cortex generate predictive representations of spatial location. To address this, they built a computational model integrating intrinsic neuronal dynamics with structured network connectivity. Specifically, they combine a conductance-based single-cell model incorporating biologically realistic HCN channels with a continuous attractor network that reflects known properties of grid cell circuitry. Their simulations show that HCN conductance can shift grid fields forward by approximately 5% of their diameter, consistent with experimental observations in layer II grid cells. Additionally, by introducing asymmetry in the connectivity of interneurons, the model produces larger forward shifts, which parallels properties observed in layer III grid cells. Together, these two mechanisms provide a unified framework for explaining layer-specific predictive coding in the entorhinal cortex.

Strengths:

A major strength of the study lies in its conceptual contribution. The authors propose two distinct mechanisms to generate forward-shifted grid fields for predictive coding. One mechanism is intrinsic and depends on the time constants associated with HCN channels. The other is network-based and results from asymmetries in interneuron connectivity. These two mechanisms correspond to different observed properties of grid cells in layer II and layer III, respectively. The modeling is based on previously validated frameworks of continuous attractor network models (e.g., Burak & Fiete; Kang & DeWeese), but it incorporates several novel features, including the incorporation of biophysically realistic HCN channels, a network architecture that excludes stellate-stellate connections and relies on interneurons, and asymmetric interneuron connectivity.

Weaknesses:

One of the proposed mechanisms for predictive coding, namely asymmetric interneuron connectivity, is a novel idea. However, this type of connectivity has not yet been demonstrated experimentally in the medial entorhinal cortex. Therefore, the biological plausibility of this mechanism remains uncertain and will need to be evaluated in future empirical studies. The revised manuscript now clearly acknowledges this limitation and discusses how this prediction could be tested experimentally, for example through paired recordings or connectomic reconstruction of interneuron-stellate cell connectivity.

Comments on revised version.

The authors have adequately addressed my previous comments, and the revised manuscript has been substantially improved. I have no further major comments.

Reviewer #2 (Public review):

Summary:

This study proposes that predictive spatial representations in medial entorhinal cortex (MEC) grid cells arise through two distinct biophysical mechanisms: (1) HCN conductance-dependent temporal dynamics, which generate modest forward shifts (~5% of grid field diameter) in Layer II cells, and (2) network asymmetry, enabling larger predictive shifts (~25% of grid field diameter) in Layer III cells. The model further predicts a dorsoventral gradient in predictive coding magnitude, correlating with observed HCN conductance variations. These results provide a mechanistic framework for understanding how intrinsic cellular properties and circuit architecture collectively enable prospective spatial coding in the MEC. This is an important and novel study with a new model.

Strengths:

These findings reveal how cellular properties and circuit design enable prospective spatial coding. This novel, impactful study will interest the field upon publication.

Weaknesses:

Some of the model is too mathematical and not fit with the biological observation.

Comments on revised version.

I have no other concern about the papers.

Reviewer #3 (Public review):

Summary:

The manuscript by Shaikh and Assisi addresses a timely and important question related to the neural circuit mechanisms underlying spatial representations during navigation. Concretely, they present a valuable model of the medial entorhinal cortex (MEC) with biophysically detailed conductance-based stellate cells that can perform path integration and reveals two potential mechanisms underlying two forms of predictive coding by grid cells in the MEC. One mechanism uses HCN channels to explain predictive coding in MEC layer II grid cells equivalent to ~5% of the diameter of a grid field, and the other uses asymmetric connections between interneurons and stellate cells, resulting in a ~25% predictive bias of layer III grid cells. The methods and model are convincing, and the model is expected to be valuable for computational neuroscientists studying neural mechanism of spatial navigation.

Strengths:

One strength of the model is its use of conductance-based neuron models of stellate cells and interneurons, adding important biophysical constraints and details to existing continuous attractor network models of grid cells. The model fills a gap in the literature by providing mechanisms for predictive coding constrained by biophysical properties of stellate cells and simplified network topology. The model generates testable hypotheses and advances our mechanistic understanding of the grid cell network.

Weaknesses:

A few weaknesses of the study remain:

(1) MEC interneurons display a very similar spatial periodicity in their firing as stellate cells. This seems inconsistent with experimental data (Buetfering et al., 2014).

(2) In the model, stellate cells are responsive to movement direction. Although this is consistent with most existing attractor network models, grid cells respond much stronger to head direction than to movement direction (Raudies et al., 2015). Likewise, grid cell sweeps follow an internal movement direction signal and not head direction (Vollan et al., 2026).

References:

Buetfering C, Allen K, Monyer H (2014) Parvalbumin interneurons provide grid cell-driven recurrent inhibition in the medial entorhinal cortex. Nat Neurosci 17:710-718.

Raudies F, Brandon MP, Chapman GW, Hasselmo ME (2015) Head direction is coded more strongly than movement direction in a population of entorhinal neurons. Brain Res 1621:355-367.

Vollan AZ, Schellenberger MF, Gardner RJ, Moser M-B, Moser EI (2026) Adaptive modulation of theta sweeps in the brain's navigation circuit. Science 393:eaef4184.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors aim to elucidate the mechanisms by which grid cells in the medial entorhinal cortex generate predictive representations of spatial location. To address this, they built a computational model integrating intrinsic neuronal dynamics with structured network connectivity. Specifically, they combine a conductance-based single-cell model incorporating biologically realistic HCN channels with a continuous attractor network that reflects known properties of grid cell circuitry. Their simulations show that HCN conductance can shift grid fields forward by approximately 5% of their diameter, consistent with experimental observations in layer II grid cells. Additionally, by introducing asymmetry in the connectivity of interneurons, the model produces larger forward shifts, which parallel properties observed in layer III grid cells. Together, these two mechanisms provide a unified framework for explaining layer-specific predictive coding in the entorhinal cortex.

Strengths:

A major strength of the study lies in its conceptual contribution. The authors propose two distinct mechanisms to generate forward-shifted grid fields for predictive coding. One mechanism is intrinsic and depends on the time constants associated with HCN channels. The other is network-based and results from asymmetries in interneuron connectivity. These two mechanisms correspond to different observed properties of grid cells in layer II and layer III, respectively. The modeling is based on previously validated frameworks of continuous attractor network models (e.g., Burak & Fiete; Kang & DeWeese), but it incorporates several novel features, including the incorporation of biophysically realistic HCN channels, a network architecture that excludes stellate-stellate connections and relies on interneurons, and asymmetric interneuron connectivity.

Weaknesses:

One of the proposed mechanisms for predictive coding, namely asymmetric interneuron connectivity, is a novel idea. However, this type of connectivity has not yet been demonstrated experimentally in the medial entorhinal cortex. Therefore, the biological plausibility of this mechanism remains uncertain and will need to be evaluated in future empirical studies.

We agree that asymmetric interneuron-to-stellate connectivity has not yet been directly demonstrated, and we have revised the Discussion (page 15, lines 436–449) to state this limitation explicitly. As we note there, and as in most continuous attractor network models of grid cells, several elements of our network's connectivity, including the offset excitatory projections from stellate cells to interneurons that set the direction of attractor propagation, and the asymmetric interneuron-to-stellate connectivity that generates the layer III-like predictive bias, are constraints that are not derived from a fully specified, data-driven wiring diagram of the MEC. There are marked differences between the predictive coding of layer II and layer III grid cells, with the predictive bias in layer III roughly five-fold larger than in layer II. Our model predicts that these differences arise from an asymmetric directional skew in the synaptic weights between interneurons and stellate cells, present in layer III and absent, or much weaker, in layer II. Such a difference in synaptic weight or connection probability should become evident in paired recordings or connectomic reconstruction of interneuron-stellate synapses. This asymmetry has not yet been demonstrated directly, though recent anatomical work showing that stellate cell-interneuron synapses are organized at the spatial scale of individual grid-cell clusters [1] is at least consistent with the kind of spatially patterned connectivity our model requires (schematic figure 8 in Huang et. al. [1]).

Manuscript change: Discussion (page 15, lines 436–449): added a new paragraph explicitly framing the asymmetric interneuron-stellate connectivity as an untested, falsifiable prediction, citing supporting anatomical evidence (Huang et al., 2024).

Reviewer #2 (Public review):

Summary:

This study proposes that predictive spatial representations in medial entorhinal cortex (MEC) grid cells arise through two distinct biophysical mechanisms: (1) HCN conductance-dependent temporal dynamics, which generate modest forward shifts (~5% of grid field diameter) in Layer II cells, and (2) network asymmetry, enabling larger predictive shifts (~25% of grid field diameter) in Layer III cells. The model further predicts a dorsoventral gradient in predictive coding magnitude, correlating with observed HCN conductance variations. These results provide a mechanistic framework for understanding how intrinsic cellular properties and circuit architecture collectively enable prospective spatial coding in the MEC. This is an important study.

Strengths:

These findings reveal how cellular properties and circuit design enable prospective spatial coding. This novel, impactful study will be of interest to the field.

Weaknesses:

Some of the models are too mathematical and do not fit with the biological observation.

We understand the concern that the manuscript may read as too mathematical. We have used a conductance-based formalism to describe the neurons, and much of this mathematical complexity is itself inherited from earlier models that were built directly from detailed voltage- and current-clamp experiments. The stellate cell model we use is a simplified version, due to Acker et al. (2003) [2], of the more detailed biophysical model of Fransén et al. (2004) [3]. We have added this lineage to the Methods section (“Neuron and Synaptic Models,” page 15, lines 466–467), where the stellate cell model is first introduced.

The exact synaptic connectivity of the MEC network has also not been completely established. Guided by the anatomical work of Gu et al. (2018) [4], we speculate a local connectivity pattern consistent with that used in other continuous attractor network models of grid cells. As shown by Couey et al. (2013) [5], stellate cells are not connected to each other directly, but interact only through inhibitory interneurons, a motif we adopt in the model. The network motif and connectivity reported by Huang et al. (2024) [1] provide further support for the type of connectivity pattern used in our model. This anatomical grounding is already described in the Results section (“Biophysically detailed conductance-based grid cell attractor model,” page 3, lines 110–117).

As stated in our response to Reviewer 1's comments, the exact connectivity of the network is not completely established. However, based on these anatomical observations, we make a testable prediction regarding the skew of the interneuron-stellate synaptic weight distribution. This skew should be present in layer III, where the predictive bias is large, and weak or absent in layer II. This prediction is already presented in the Discussion (page 15, lines 436–449), in the paragraph before the summary.

Manuscript change: Methods and Materials, “Neuron and Synaptic Models” (page 15, lines 466–467): added a clause tracing the conductance-based stellate cell model to Fransén et al. (2004), as simplified by Acker et al. (2003). The related connectivity grounding (Gu et al., 2018; Couey et al., 2013; Huang et al., 2024) is already covered by Discussion (page 15, lines 436–449), and the testable, skew-based connectivity prediction is already covered by item 18; these points are not repeated in the Discussion. “Biophysically detailed conductance-based grid cell attractor model” (page 3, lines 110–117): added two sentences grounding the network topology (stellate-interneuron-only connectivity, exclusion of pyramidal cells) in anatomical data, and the testable, skew-based prediction was already present in the Discussion paragraph preceding the summary (page 15, lines 436–449): added a new paragraph explicitly framing the asymmetric interneuron-stellate connectivity as an untested, falsifiable prediction, citing supporting anatomical evidence (Huang et al., 2024).

Reviewer #3 (Public review):

Summary:

The manuscript by Shaikh and Assisi addresses a timely and important question related to the neural circuit mechanisms underlying spatial representations during navigation. Concretely, they present a model of the medial entorhinal cortex (MEC) with biophysically detailed conductance-based stellate cells that can perform path integration and reveal two potential mechanisms underlying two forms of predictive coding by grid cells in the MEC. One mechanism uses HCN channels to explain predictive coding in MEC layer II grid cells equivalent to ~5% of the diameter of a grid field, and the other uses asymmetric connections between interneurons and stellate cells, resulting in a ~25% predictive bias of layer III grid cells. The methods and model are technically sound, and the model is expected to be useful for computational neuroscientists studying the neural mechanisms of spatial navigation.

Strengths:

One strength of the model is its use of conductance-based neuron models of stellate cells and interneurons, adding important biophysical constraints and details to existing continuous attractor network models of grid cells. The model fills a gap in the literature by providing mechanisms for predictive coding constrained by biophysical properties of stellate cells and simplified network topology.

Weaknesses:

A weakness of the model is that the neural network is relatively small (five sheets with 71 × 71 neurons each), and the 2-D toroidal topology is further simplified to a 1-D ring attractor consisting of three rings with 192 neurons each.

The neurons were connected using periodic boundary conditions to minimize edge effects, and the connectivity was radially symmetric to limit the influence of topographic irregularities on the collective dynamics of grid cells. Therefore, we believe that increasing the network size would not have significantly altered the simulation outcomes.

We were constrained by the number of biophysically realistic neurons that could be simulated within a reasonable time frame—approximately 25,000 for the 2-D attractor network and 576 for the ring network. There were two main reasons for this limitation. (i) The simulations had to run over time scales ranging from several seconds to minutes to ensure that the trajectory repeatedly passed through the same local neighbourhood and that the spike density was sufficient to delineate the grid fields. This process was especially time-consuming for the 2-D environment, though we managed to achieve it in a smaller network representing a 1-D environment. Additionally, the trajectories needed to extend over time to allow us to estimate any drift between the simulated animal’s actual position and its inferred position from neuronal activity. (ii) The simulations required extensive multi-parameter sweeps within the bounds of experimentally observed values, further increasing the total simulation time. Given these computational constraints, we had to limit our model to smaller neuron populations. While using simpler neuron models could have allowed larger networks, we considered it essential to retain a degree of biophysical realism. This level of detail enabled us to explore how specific conductances influenced the overall dynamics of the network. We have also added a sentence to the Methods section (“2D model,” page 16, lines 488–494) stating these computational constraints explicitly and noting that periodic boundary conditions and radially symmetric connectivity were used throughout to minimize edge and finite-size effects.

Manuscript change: Methods and Materials, “2D model” (page 16, lines 488–494): added a sentence explaining the computational constraints that determined network size and the use of periodic, radially symmetric connectivity to limit edge effects.

The model incorporates biophysical detail at the single-neuron level, but not at the network level. For example, it includes only stellate cells and a generic interneuron type and does not implement data-driven connectivity patterns. The restricted network size and the limited experimental knowledge about connectivity among stellate cells, principal cells, and different interneuron types in the MEC could be addressed in more detail.

Because the network connectivity of the medial entorhinal cortex (MEC) is not yet fully understood, our model incorporates prior findings showing that stellate cells interact only through inhibitory interneurons [5–8]. In layer II, stellate cells that function as grid cells also show a topographic organization. They form clusters located between patches of pyramidal neurons. Each grid cell module consists of stellate cells that are physically contiguous, although cells from neighboring modules intermingle at their borders. Within a module, stellate cells tend to form a noisy two-dimensional lattice organized according to the phases of their grid fields [4]. In addition, axonal projections in layer II of the MEC create spatially organized connections between stellate cells and parvalbumin interneurons. Nearby neurons often, but not always, share direct connections, whereas neurons that are farther apart are linked primarily through multisynaptic pathways [5]. Together, these observations suggest that stellate cells interact via inhibitory intermediaries and are locally arranged in a network topology that closely resembles standard Continuous Attractor Network (CAN) models. We have added two sentences to the Results section (“Biophysically detailed conductance-based grid cell attractor model,” page 3, lines 110–117) making this anatomical justification explicit, and stating that layer II pyramidal cells, which form a separate microcircuit, are correspondingly excluded from the model.

Manuscript change: Results, “Biophysically detailed conductance-based grid cell attractor model” (page 3, lines 110–117): added two sentences grounding the network topology (stellate-interneuron-only connectivity, exclusion of pyramidal cells) in anatomical data.;See Discussion (page 15, lines 436–449): added a new paragraph explicitly framing the asymmetric interneuron-stellate connectivity as an untested, falsifiable prediction, citing supporting anatomical evidence (Huang et al., 2024).

Moreover, the manuscript lacks a thorough discussion of assumptions common to most continuous attractor network (CAN) models of grid cells, such as the use of "hand-crafted" connections between direction-sensitive conjunctive grid cells and network cells to drive attractor shifts. Including such a discussion would strengthen the manuscript. This is especially relevant given the authors' explicit claim that they have revealed two mechanisms underlying the emergence of a predictive code in the MEC. In this reviewer's view, the work demonstrates a potential mechanism, but one that requires experimental verification. The significance of the model would thus be increased by providing more experimentally testable predictions of the model.

The exact connectivity of stellate cells and interneurons is yet unknown. But several lines of evidence point to an attractor-like connection topology. We have now included a more detailed discussion of the connectivity used in CAN models.

Manuscript change: Discussion (page 15, lines 436–449): added a new paragraph explicitly framing the asymmetric interneuron-stellate connectivity as an untested, falsifiable prediction, citing supporting anatomical evidence (Huang et al., 2024).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) In the abstract, the authors write:

"Our model revealed two mechanisms underlying the emergence of a predictive code in the MEC. The first relied on a time scale associated with the HCN conductance. The other depended on the degree of asymmetry in the topology of the MEC network."

Given the central importance of these two mechanisms, the description here may be overly brief. Even in an abstract, a slightly more detailed explanation of each mechanism would enhance clarity and accessibility.

We have modified the abstract (page 1, lines 7–21) which now includes a brief explanation of how the timing of stellate cell spikes are advanced

Manuscript change: Abstract (page 1, lines 7–21): modified the abstract to include a detailed description of the mechanism.

(2) In both experimental (e.g., Hafting et al., 2008; Chaudhuri-Vayalambrone et al., 2023; Ouchi & Fujisawa, 2024) and theoretical studies (e.g., Kang & DeWeese, 2019), predictive coding in grid cells has been closely associated with the phase profile of theta oscillations, including phenomena such as phase precession and phase locking. The authors' model successfully reproduces theta-range membrane potential oscillations, consistent with physiological observations. Given this, it would be valuable to know whether the model allows for an integrated analysis of the relationship between predictive coding and spike timing relative to theta phase. If such a simulation could be included in the present study, it would likely strengthen the contribution of the manuscript. However, if this is beyond the scope of the current work, a brief discussion of the potential relevance of theta-phase dynamics to predictive coding, and how this might be addressed in future studies, would still help broaden the perspective and impact of the paper.

The predictive grid cells [9,10] are phase-locked to theta oscillations. In line with this observation, our model demonstrates that for sufficiently high theta amplitude stellate cells can be entrained to the input oscillations. We have added a paragraph to the Discussion (page 12, lines 365–370) describing this entrainment finding in the text. However, we have not included the analysis figure (see Author response image 1) itself in the manuscript.

Manuscript change: Discussion (page 12, lines 365–370): added a new paragraph noting that the model reproduces theta-entrainment of stellate cell spiking consistent with phase-locked predictive grid cells, without including the underlying analysis figure in the manuscript.

Author response image 1.

(3) The Discussion section currently ends somewhat abruptly. Adding a concluding paragraph that summarizes the key findings and their broader implications would help reinforce the significance of the work for readers.

We have now modified the discussion section (page 15, lines 450–463) to summarize key findings and the broader implications of the study.

Manuscript change: Discussion (page 15, lines 450–463): a concluding paragraph has been added at the end of the Discussion section.

(4) "These properties are due to the presence of a hyperpolarization-activated depolarizing current (Ih) and a persistent sodium current (INaP) in addition to leak and spiking currents (IL, IK, INa). An interplay between Ih and INaP is needed to generate the membrane potential oscillations observed here. In addition, these oscillations fall squarely within the range of theta oscillations (4-12 Hz)." (Page 3, Line 97)

Please provide supporting evidence for these claims, such as simulation results or relevant literature references.

We have added references supporting our claims.

Manuscript change: Results, “Biophysically detailed conductance-based grid cell attractor model” (page 3, lines 97–100): added reference to "An interplay between I_h and I_NaP is needed to generate the membrane potential oscillations observed here. In addition, these oscillations fall squarely within the range of theta oscillations (4–12 Hz)."

(5) "How does HCN give rise to a predictive bias? The HCN channel depolarizes the cell and is activated by inhibitory input from interneurons in the model network. Since HCN increases the cell's excitability, it speeds up the onset of spiking, translating grid fields that are farther away to locations closer to the animal." (Page 7, Line 285).

Is this explanation derived directly from simulation data? If so, please indicate the relevant figures or results that support this interpretation.

Reference to support the effect of HCN on the cell’s excitability has been added (page 10, lines 296–299). A paragraph in the manuscript explains how this change in excitability can cause the grid field to be translated closer to the animal (page 10, lines 300-305).

Manuscript change: Results, “Cellular and network-based mechanisms for predictive and retrospective coding” (page 10, lines 296–299): added reference to "How does HCN give rise to a predictive bias? The HCN channel depolarizes the cell and is activated by inhibitory input from interneurons in the model Network. Since HCN increases the cell's excitability, it speeds up the onset of spiking, translating grid fields that are farther away to locations closer to the animal."

(6) Some elements in the main figures are not clearly explained or referenced in the main text. For example, Figures 1E and F, and Figure 3B appear to lack corresponding descriptions or interpretation. Please ensure that all figure panels are explicitly discussed in the results.

Missing explanations for Figure 1E and F have been added to the result section. Figure 3b is mentioned in the article (Page 8, line 235)

Manuscript change: Results, “Biophysically detailed conductance-based grid cell attractor model” (page 4, lines 153–154): added missing references to Figure 1e and Figure 1f in the manuscript.

(7) Typos

(a) Page 4, Line 140: "as shown in Figure 1A". It seems "Figure 1D" is intended.

(b) Figure 2A (color legend): "m.p. eamp (mV)" should be "m.p. ramp (mV)".

These typos have been fixed.

Manuscript change: fixed the Figure 1 panel-letter typo (Results, “Biophysically detailed conductance-based grid cell attractor model,” page 4, lines 146–147): fixed figure reference from Figure 1A (bottom) to Figure 1d (bottom) and the Figure 3 colour-legend typo (Figure 3a, page 9): fixed colour label typo from "m.p. eamp (mV)" to "m.p. ramp (mV)". and standardized all figure panel references to lowercase throughout the manuscript: Figure panel references were changed to lowercase throughout the manuscript.

Reviewer #2 (Recommendations for the authors):

(1) The model is based on five interconnected neuronal sheets organized in a toroidal topology, with four layers of stellate cells (71×71 neurons each) and one inhibitory interneuron layer. Key architectural features included: Stellate cells interacted exclusively via feedforward inhibition through interneurons, consistent with experimental observations (Couey et al., 2013). Interneurons projected symmetrically to other interneurons within their sheet, and each interneuron inhibited a concentric ring of stellate cells. This spatially structured inhibition, combined with toroidal boundary conditions, generated stable hexagonal activity patterns in both stellate and interneuron populations. In this model, it will be very likely that the interneurons also exhibited perspective coding, but this is not consistent with the physiology data. Can the authors comment on this?

As stated in materials and methods, we used the interneuron activity as the “true” position of the animal. This was done because the errors accumulated during path integration were far greater than the predictive bias shown by the grid network. Therefore, it would not have been possible to discern the predictive bias from the path integration error. The interneuron field does show a skew in the opposite direction to the direction of travel. However, unlike stellate cells, this is not translation of the grid field, See Author response image 2. This is due to asymmetry in the firing rates of interneurons along its field. We have added a sentence to the Methods section (“Predictive and retrospective coding,” page 17, lines 521–525) making this distinction, between a firing-rate asymmetry and an actual translation of positional tuning, explicit.

Manuscript change: Methods and Materials, “Predictive and retrospective coding” (page 17, lines 521–525): added a sentence clarifying that interneuron firing-rate asymmetry does not reflect a translation of positional tuning, justifying its use as the position reference.

Author response image 2.

(2) In the original study (Ouchi et al., 2024), it reported predictive grid cells; it has been shown that theta-rhythmic population activity in the MEC supports dynamic spatial representation, with phase-organized firing patterns enabling continuous trajectory prediction. The current model did not examine this in much detail. Could the authors discuss this or test this in their model?

Our simulations have shown that the impact of theta oscillations on the temporal organisation of grid fields is more intricate than we initially anticipated, and further work is underway to elucidate these mechanisms. However, in line with experimental observations [9], our model demonstrates that stellate cells can be entrained to the input oscillations by increasing the amplitude of theta. See Author response image 1. As above, we have added a Discussion paragraph describing this entrainment result in the text, without including the corresponding figure in the manuscript.

Manuscript change: Discussion (page 12, lines 365–370): added a new paragraph noting that the model reproduces theta-entrainment of stellate cell spiking consistent with phase-locked predictive grid cells, without including the underlying analysis figure in the manuscript.

(3) In the data, the shift of the predictive grid is in a range of distribution from 22.5 {plus minus} 10.2 cm; the model did not clearly show the shift distance of the grid in the current model. It would be helpful to examine why the grid cells with different spacing could show a range of their shift in the current model.

The expansion of grid spacing is accompanied by a lengthening of HCN conductance time scales. As demonstrated in Figure 5e, the extent of predictive coding can be enhanced by increasing these intrinsic temporal constants. We have added a sentence to the Results section (“Cellular and network-based mechanisms for predictive and retrospective coding”, page 10, lines 315–320) relating this range of model-predicted shift distances explicitly to experiments.

Manuscript change: Results, “Cellular and network-based mechanisms for predictive and retrospective coding” (page 10, lines 315–320): added a sentence relating the range of model-predicted shift distances across grid scales to the experimentally reported range.

(4) In the non-linearity and ensure accurate path integration, the author mapped each value of speed𝑠 measured in (𝑟𝑎𝑑∕𝑠) to its corresponding depolarising drive 𝐼 = 𝑓(𝑠) (Figure 2a). It is necessary to discuss the biological meaning of the depolarizing drive. Is the value reasonable in the biological range?

The depolarizing drive I = f(s) is used to represent the population speed signal that is delivered to stellate cells as a somatic current, and across the simulated range of speeds its magnitude remains within the sub-nanoampere range used for current-clamp characterization of stellate cell and interneuron excitability in the original single-cell studies from which our conductance parameters were taken [2,3,11,12] We have added a sentence to the Results section (“Grid cell network can accurately path integrate 1D trajectories,” page 6, lines 184–188) stating this explicitly, so that the biological plausibility of the depolarizing drive is clear to the reader.

Manuscript change: Results, “Grid cell network can accurately path integrate 1D trajectories” (page 6, lines 184–188): added a sentence clarifying that the depolarizing drive I=f(s) remains within the sub-nanoampere range used experimentally to characterize stellate cell and interneuron excitability.

(5) In the study after HCN knockout, the spacing change of grid cells exhibited a linear drift to higher spacing (Giocomo et al., 2011a). This also shows grid cells with discrete modules (Stensola et al., 2012, Nature). Regarding this, how does the current model represent the discretized modules and their predictive coding?

In our model, all stellate cells share the same grid scale and can therefore be treated as belonging to a single module. Experimentally, however, grid scale varies along the dorsoventral axis of the MEC, in parallel with systematic changes in inhibitory connectivity and HCN channel conductance [13–15]. In the model, we can reproduce different grid spacings (as seen across modules) by increasing the range of lateral inhibition, and the grid expansion observed after HCN knockout would similarly apply to modules with different grid scales. Our current implementation does not include a mechanism for generating discrete modules, which would require a network with a graded change in lateral inhibition across its spatial extent. In networks with such graded organization, several mechanisms have been proposed for how modules emerge [16,17] and these would likely apply to our model as well. We have added a paragraph to the Discussion (page 15, lines 428–435) stating this limitation and the proposed extension explicitly, with supporting citations.

Manuscript change: Discussion (page 15, lines 428–435): added a new paragraph on the model's single-module limitation and possible extensions to discrete, dorsoventrally organized modules.

(6) The grid cells have been shown in both the Stella cells and the pyramidal cell group? Will the current model bias their conclusion toward different cell groups? Or can it not represent these cell groups? It could be necessary to discuss this.

Within Layer II of the MEC, stellate cells and pyramidal cells form separate, largely non-overlapping microcircuits. Pyramidal cells are commonly connected via 5− HT3a positive interneurons, while stellate cells are primarily connected via fast-spiking parvalbumin (PV⁺) cells and slower-spiking somatostatin-positive cells [5–7]. Further, stellate cells show a topographic organization with stellate cell clusters being separated by pyramidal neurons [1].

Given these observations we chose a model stellate cell and fast-spiking interneuron.

Based on our work it would be hard to say what, if any, the effect of pyramidal neurons would be to the stellate grid cell network. We have added a sentence to the Results section

(“Biophysically detailed conductance-based grid cell attractor model,” page 3, lines 110–117) stating explicitly that the model does not include pyramidal cells and that our conclusions are specific to the stellate-cell grid-cell population.

Manuscript change: Results, “Biophysically detailed conductance-based grid cell attractor model” (page 3, lines 110–117): added two sentences grounding the network topology (stellate-interneuron-only connectivity, exclusion of pyramidal cells) in anatomical data, which states the exclusion of pyramidal cells explicitly.

(7) In Kropff et al., 2015 Nature, speed cells have been shown also represent predictive shift in their coding, the author achieved accurate path integration with a linear relationship between the speed of the animal and the movement of attractor is necessary and for this by introducing an invertible mapping between speed and the amplitude of the depolarizing input used to drive the stellate cells. The current model did not address the possible contribution of speed coding to the retrospective coding in grid cells. Will the authors discuss this?

This is an interesting point. Kropff et al. (2015) [18] showed that a subset of speed-tuned cells in the MEC represent running speed with a temporal offset, effectively encoding a predictive or retrospective estimate of speed itself. Our model currently represents the population speed signal as a single, instantaneous depolarizing drive I = f(s) and does not incorporate this heterogeneity. We have added a passage to the Discussion (page 14, lines 393–402) noting that if even a fraction of the depolarizing drive to stellate cells were itself temporally offset in the way Kropff et al. describe, this could shift the magnitude, or potentially the sign, of the retrospective bias that we attribute to network asymmetry, providing an additional, speed-coding-dependent route to retrospective coding that could act alongside the intrinsic and network mechanisms we describe. Disentangling the relative contributions of speed-signal timing and network asymmetry to retrospective coding is a promising direction for future modeling work.

Manuscript change: Discussion (page 14, lines 393–402): added a discussion of how heterogeneity in speed-cell timing (Kropff et al., 2015) could interact with network-asymmetry-based retrospective coding.

References

(1) Huang, L.-W., Garden, D. L., McClure, C. & Nolan, M. F. Synaptic interactions between stellate cells and parvalbumin interneurons in layer 2 of the medial entorhinal cortex are organized at the scale of grid cell clusters. eLife 12, RP92854 (2024).

(2) Acker, C. D., Kopell, N. & White, J. A. Synchronization of Strongly Coupled Excitatory Neurons: Relating Network Behavior to Biophysics. J. Comput. Neurosci. 15, 71–90 (2003).

(3) Fransén, E., Alonso, A. A., Dickson, C. T., Magistretti, J. & Hasselmo, M. E. Ionic mechanisms in the generation of subthreshold oscillations and action potential clustering in entorhinal layer II stellate neurons. Hippocampus 14, 368–384 (2004).

(4) Gu, Y. et al. A Map-like Micro-Organization of Grid Cells in the Medial Entorhinal Cortex. Cell 175, 736-750.e30 (2018).

(5) Couey, J. J. et al. Recurrent inhibitory circuitry as a mechanism for grid formation. Nature neuroscience 16, 318–324 (2013).

(6) Nilssen, E. S., Doan, T. P., Ohara, S. & Witter, M. P. A reappraisal of the lateral and medial entorhinal subdivisions mediating parallel cortical pathways. Hippocampus in press, 1–17 (2019).

(7) Witter, M. P., Doan, T. P., Jacobsen, B., Nilssen, E. S. & Ohara, S. Architecture of the entorhinal cortex: a review of entorhinal anatomy in rodents with some comparative notes. Frontiers in systems neuroscience 11, 1–12 (2017).

(8) Nilssen, X. E. S. et al. Inhibitory Connectivity Dominates the Fan Cell Network in Layer II of Lateral Entorhinal Cortex. The Journal of neuroscience: the official journal of the Society for Neuroscience 38, 9712–9727 (2018).

(9) Ouchi, A. & Fujisawa, S. Predictive grid coding in the medial entorhinal cortex. Science 385, 776–784 (2024).

(10) Ouchi, A. Predictive grid cells: Future spatial representations in the hippocampal-entorhinal circuit. Neurosci. Res. 227, 105053 (2026).

(11) Dickson, C. T. et al. Properties and role of I(h) in the pacing of subthreshold oscillations in entorhinal cortex layer II neurons. Journal of neurophysiology 83, 2562–2579 (2000).

(12) Alonso, A. & Klink, R. Differential electroresponsiveness of stellate and pyramidal-like cells of medial entorhinal cortex layer II. J. Neurophysiol. 70, 128–143 (1993).

(13) Garden, D. L. F., Dodson, P. D., O’Donnell, C., White, M. D. & Nolan, M. F. Tuning of Synaptic Integration in the Medial Entorhinal Cortex to the Organization of Grid Cell Firing Fields. Neuron 60, 875–889 (2008).

(14) Giocomo, L. M. et al. Grid Cells Use HCN1 Channels for Spatial Scaling. Cell 147, 1159–1170 (2011).

(15) Yoshida, M., Giocomo, L. M., Boardman, I. & Hasselmo, M. E. Frequency of subthreshold oscillations at different membrane potential voltages in neurons at different anatomical positions on the dorsoventral axis in the rat medial entorhinal cortex. The Journal of neuroscience: the official journal of the Society for Neuroscience 31, 12683–12694 (2011).

(16) Kang, L. & Balasubramanian, V. A geometric attractor mechanism for self-organization of entorhinal grid modules. eLife 8, e46687 (2019).

(17) Khona, M., Chandra, S. & Fiete, I. Global modules robustly emerge from local interactions and smooth gradients. Nature 640, 155–164 (2025).

(18) Kropff, E., Carmichael, J. E., Moser, M.-B. & Moser, E. I. Speed cells in the medial entorhinal cortex. Nature 523, 419–424 (2015).

true

eLife Assessment

This important study examines excitation/inhibition (E/I) balance in the CA3-CA1 circuit of the hippocampus, yielding results that suggest a way in which CA1 neurons can perform mismatch detection. A combination of experimental and computational modeling results are presented and supported by solid evidence. The results are likely to be of interest to experimental and computational researchers who study the hippocampal circuit.

Reviewer #3 (Public review):

Summary:

This work shows experimentally and computationally that single CA1 neurons can perform mismatch detection on patterned CA3 inputs and that STP and EI balance underlie this detection.

Strengths:

It has been known that STP can enhance the EPSP when the corresponding presynaptic input exhibits abrupt changes in firing rate. This work provides experimental evidence and further computational support for the hypothesis that the basic computation through STP is useful for detecting abrupt changes in the spatial pattern of synaptic inputs at the Schaffer collaterals. Their results indicate the novel view that mismatch detection is most efficient when gamma-frequency bursting inputs exhibit mismatches between theta cycles. These results are robust against variations in external and internal conditions.

Weaknesses:

While this study shows an intriguing example of combined experimental and computational studies, the results of the experiments and those of the computational model display non-negligible deviations in some conditions. However, discrepancies are expected in modeling studies due to the simplifications in the model setting and guide the directions of future research.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study uses optogenetics to activate CA3 while recordings from CA1 neurons and characterizing the excitation/inhibition (E/I) balance. They observe use-dependent alterations in the E/I balance as a result of STP and they develop a model to describe these observations. This is a very ambitious paper that deals with many issues using both experimental and modeling approaches.

Strengths:

This paper examines important principles regarding the manner in which synaptic circuitry and use-dependent synaptic plasticity can transform inputs and perform computations.

Weaknesses:

(1) I am pleased that the authors revised their section on external calcium. They now approach this issue by calculating the effect of low external calcium on plasticity. These calculations are based on studies of numerous types of synapses, which are unlikely to be directly comparable to hippocampal synapses.

We have clarified how we use published studies and our own model to estimate the effect of lower (more physiological) levels of external calcium. Among these we do have data from hippocampus. From the text:

“Specifically, in hippocampal CA3->CA1 glutamatergic synapses at 1.5 mM extCa the paired-pulse ratio is 15% larger than at 2mM (Blatow et al. 2003). In primary hippocampal neuronal culture, inhibitory synapses also undergo a 50% increase in paired-pulse ratio at 0.5 mM compared to 2 mM extCa (Kravchenko et al. 2006).”

They focus on PPR rather than the overall response during more sustained activation that is likely to produce more complex responses. Obviously, it would have been preferable to simply measure the responses in the appropriate external calcium.

The reviewer correctly says that we focus on the PPR when referring to previous work which looks at how external calcium affects short-term plasticity. This was because this was the common denominator of such studies, in particular those of Blatow et al. 2003, whose work was on hippocampal CA3-CA1 synapses. Blatow et al. did have one figure panel with a 5-pulse burst but this was at 2mM and 3mM calcium, so it did not pertain to the more physiological 1.5mM case that we would need to infer what happens for bursts at physiological calcium.

We agree that direct measurements with reduced calcium in our own preparation would have been ideal, but it was not feasible to redo the technically demanding experiments.

(2) The illumination intensity and the effect on fiber stimulation is a limitation that will alter apparent plasticity.

We agree that these are among the factors that affect apparent plasticity. As we state in the text, we chose settings that have previously been reported to minimize desensitization, Regarding illumination intensity, we refer to a careful calibration study by Mattis et al 2012. Based on this, we used the highest optical power available in our setup with brief pulses of 2ms or 5 ms. From the text:

“Each presentation of a pattern was either for 2 ms (Poisson spike train experiments, Figure 6 and frequency sweeps, Figure 1-3) or 5 ms (Mismatch experiments, Figure 7 and frequency sweeps, Figure 1-3). We chose short light pulses for two reasons. First, to decrease jitter in the light-triggered CA3 neuron spike timings. Second, if one is below saturating light intensities, short pulses at higher power give more consistent spiking over multi-pulse trains (Mattis et al. 2012), Figure 2A, using a 2ms pulse width). …For all experiments, unless mentioned, the intensity of light was kept at 100%.”

Additionally, we monitored fiber activation through field potential recordings in the CA3, and estimated the extent of its reduction over the course of a burst or train of inputs. From the text:

“To estimate this reduction, we measured the field EPSP in the CA3 during the optical stimulation, and fitted an exponential decay function to the peaks (Figure 7-figure supplement 2). We find that the largest decay was ~30% of the initial fEPSP. The fEPSP decayed over a wide range of time-courses, with median around 800ms. We estimate that the recovery time from ChR2 desensitization was around 150ms, again highly different between slices (Figure 7-figure supplement 2). Thus the mismatch detection was largely robust to ChR2 desensitization effects over the pulse train.”

Reviewer #3 (Public review):

Summary:

This work shows experimentally and computationally that single CA1 neurons can perform mismatch detection on patterned CA3 inputs and that STP and EI balance underlie this detection.

Strengths:

It has been known that STP can enhance the EPSP when the corresponding presynaptic input exhibits abrupt changes in firing rate. This work provides experimental evidence and further computational support for the hypothesis that the basic computation through STP is useful for detecting abrupt changes in the spatial pattern of synaptic inputs at the Schaffer collaterals. Further, their results indicate the novel view that mismatch detection is most efficient when gamma-frequency bursting inputs exhibit mismatches between theta cycles. The authors included novel results in the revised manuscript to show that the effective frequency range of gamma oscillation is broad, including both slow and fast gamma bands.

In the initial submission, the dependence of mismatch detection performance on model parameters and experimental settings, such as pattern overlaps and other network parameters, was not sufficiently explored. In the revised manuscript, the authors extensively studied these points and summarized the novel results in Fig. 9. Furthermore, the authors clarified that jitters in input spikes can improve detection performance in some cases. These results show the robustness of their results against variations in external and internal conditions.

Weaknesses:

While this study shows an intriguing example of combined experimental and computational studies, the results of experiments and those of the computational model display relatively large deviations in some conditions. The cause of this discrepancy needs further clarification.

The reviewer correctly points out that our model deviates from the experiments in some conditions. We have added a new paragraph in the discussion section to address the main points of difference:

“As expected for a reduced model, our predictions differed quantitatively from experiments in a few respects. The strongest of these is the difference in mismatch selectivity at 50 Hz in Figure 7Fi vs 7Fiii. We speculate that this is due to one of the major simplifications in our model, the use of a single class of inhibitory interneurons. An additional point of difference is the decay time-course of EPSP vs ISI from Figure 6F. Here again we implicate the simplification with respect to interneurons. An additional likely cause is our limited use of the diversity of STP profiles in the model compared to experiment. Specifically, we used STP profiles from Figure 4-figure Supplement 1, but the population is quite diverse (Figure 4-figure supplements 1 to 4). Finally, despite our efforts to model the CA3 cell population with ChR2 desensitization constrained by experiment, we have clearly simplified the recurrence and optical illumination profiles of the CA3. Thus, at the spiking level, our stimulus patterns can only approximate physiological activity.”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Both external calcium and light activation are important limitations. Although I might take a different approach if it were my own paper, at this point I favor allowing the paper to proceed as long as they clearly point out these limitations.

We have pointed out these limitations. From the text:

“Our bath solution had 2mM Ca2+, which is above the physiological 1.2 to 1.5 mM range and hence is likely to exhibit ~20% lower STP both for inhibitory and excitatory synapses (Kravchenko et al. 2006; Blatow et al. 2003).”

Also, from the discussion:

“Finally, despite our efforts to model the CA3 cell population with ChR2 desensitization constrained by experiment, we have clearly simplified the recurrence and optical illumination profiles of the CA3. Thus, at the spiking level, our stimulus patterns can only approximate experiments.”

Reviewer #3 (Recommendations for the authors):

This reviewer has no further comments except a minor comment. The authors use the word "squares" to specify the stimulus patterns tested. On reading the revised manuscript, I could not quickly find what the " square" means. The shape of the stimuli will not be particularly important in this study. The authors may use a different word.

We thank the reviewer for pointing out this inconsistency. At the outset we explain why we use the term ‘square’ and we have gone through the text and where necessary we have replaced the term ‘spot’ with ‘square’ or ‘illumination square’ to resolve ambiguity. At the point where we define the illumination patterns, we have added this line:

“Due to the grid pattern of illumination and the rectangular profile of the illumination spots, we refer to them as ‘squares’ in subsequent analysis, though the exact shape is unlikely to affect the activation of CA3 neurons.”

AHHHHHHHH

Triage: thngs that are super ready fo rscaling, things that have potential, things that need evidence (pilots).

Japanese coercion to provoke the signing of the Treaty

Japanese would use coercive force to influence the Korean legation

Korean independence would merely see another foreign intervention

Japan saw elite cooperation as essential for their protectorate

Korean refusal would place them in a dangerous position (potential Japanese military intervention)

Partnership in imperialism rather than rivalry

Foreign powers would need to be appeased in order to prevent a rerun of the triple intervention

Japan was already moving toward a protectorate before its official signing

Japanese advisors would widen Japanese influence in Korea

Military control allowed for the deposition of government

Japan was growing its control by assuming power due to Korean ineffectiveness

Promotion of economic development would go hand and hand with an increase in Japanese economic interests in Korea

Communication control

Railway system as key for the administration of the country

Japanese supervision of Korean finance

Japan would need to defend Korea and its independence (and also help support the defense of the Japanese empire)

Korea was crucial for Japanese defense and therefore no other country could take control of it

Obtain military control for internal and external defense as well as for Japanese defense

Expansion of economic interests and economic control

Reform to help protect Japanese economic interests and internal control.

Massive Japanese military presence for internal control and external defense, sweeping internal reforms to place Korean administration into Japanese hands (and for the civilizing mission), and an expansion of Japanese economic presence to exploit Korea's economic opportunities and to justify Japanese intervention

Japan would need greater intervention to secure its position in Korea

While the treaty allowed for Japanese military deployments, it did not advance other Japanese interests beyond military

Opportunity of Japanese victory

Japanese victories, led to growing Korean support for Japan

Japan would now take the dominant place in defending Korean "independence"

Korean leaders attempted to assure its independence but it was simply too weak to do so

Yamamoto saw the preemptive sending of soldiers as too risky as it would alienate foreign opinion and lead to greater hostility with the Russians

Either seize control through military means to establish a protectorate over Korea

The threat of the Russians thus placed Korea under far more importance, and far more danger of Japanese authoritarianism

Japan would have to maintain control of Korea to prevent any loss of control in such a dangerous moment

Similar reasoning to the Germans and Austro-Hungarians in 1914

Japanese protection in exchange for a Japanese sphere of influence

Korea as a keystone for Japanese defense and a jumping off point to supplant Russia in Manchuria

Korea as a key piece of national defense

Recognition of both sides interests in Northeast Asia to prevent conflict and allow Japan to maintain her dominance in Korea (in exchange for Russian dominance in Manchuria)

Neutralization would merely be a buy for time

Neutralization would merely deprive Japan of its dominant position in Korea while Russia consolidated its position in Manchuria

Recognized sphere of influences

Japan could not allow Russia control of any part of Korea if it were too also have Manchuria

Russia influence in Manchuria could be a trading chip for allowing Japanese interest in Korea

Japan by gaining a protectorate could influence the Korean reform effort and allow the freedom of action to defend Korea from a third power

Protectorate served to advance European control while maintaining the civilizing mission

Japan saw the need for Korean reform, reform only Japan could provide

"Civilizing" justification due to the backward nature of the Korean government

China crisis led to a new threat as Russia and Japan began to conflict over Korea

Korea not became a key linchpin of Japanese defense against Russian expansionism

Japan could no longer count on a partition of China

Japanese interests in South China represented a direct threat to US and UK economic interests, who advocating for the Open Door, wanted to prevent the growth of Japanese interests in the South

Boxer Rebellion could be an opportunity, with the weakness of the Qing, to expand Japanese territorial gains in South China

Korean future through the lens of Chinese territorial breakdown

"Scramble for China" initiated by German seizure of Kiaochow Bay

eLife Assessment

This valuable study identifies knowledge of letter shape as a distinct component of letter knowledge that can be acquired before formal reading instruction and without the knowledge of letter sound. The evidence is solid for the presence of early letter-shape familiarity and its unique association with search performance, supported by a large developmental sample and converging analyses. The findings will be of interest to researchers studying literacy and visual learning.

Reviewer #1 (Public review):

Summary:

This study examines whether children at the beginning of formal reading instruction possess visual knowledge of letter shapes that can be distinguished from their ability to name letters. In a large sample of children learning Kannada, many children reliably distinguished upright from inverted letters despite limited letter-naming performance. Children also searched more efficiently for upright than inverted letters, and this search advantage was uniquely associated with letter-shape familiarity after controlling for letter-naming performance and other measured factors. These findings suggest that familiarity with the visual structure of letters can emerge before extensive formal instruction in letter-name or letter-sound associations.

Strengths:

The study addresses a relatively understudied component of emergent literacy by distinguishing visual familiarity with letter shapes from explicit letter naming. This question is theoretically important, particularly in light of functional subdivisions within the visual word form area, with posterior regions associated with letter and orthographic shape and anterior regions with linguistic features of orthography (Caffarra et al., 2021; Lerma-Usabiaga et al., 2018). The large sample of children at an early stage of reading instruction provides an informative opportunity to examine these abilities before they become highly correlated through extensive reading experience. The revised manuscript has also been strengthened by convergent results across multiple analytical approaches.

Weaknesses:

The comparison between letter-shape familiarity and letter-name knowledge is influenced by differences between the receptive familiarity task and the production-based naming task, although the authors now appropriately acknowledge this limitation. More importantly, the cross-sectional study does not establish whether early letter-shape familiarity contributes to subsequent literacy development; longitudinal evidence will be needed to determine its role in later reading acquisition.

Comments on revised version:

I am satisfied that the authors have addressed most of my previous comments. I have only a few minor comments that require further attention.

(1) Direct comparison of familiarity and recognition effects

The newly added regression and mixed-effects analyses strengthen the finding that familiarity is associated with the upright-search advantage after controlling for recognition and the other measured factors. However, the central comparative claim remains incompletely tested. A significant effect of familiarity alongside a nonsignificant effect of recognition does not establish that the two associations differ significantly. The authors should directly compare the effects of these two abilities. Otherwise, the conclusion should be limited to stating that familiarity explains unique variance after controlling for recognition, rather than that familiarity is more strongly associated with the upright-search advantage.

(2) Interpretation of the VGG-16 analysis

I appreciate the addition of the VGG-16 analysis, which provides an interesting characterization of the visual relationship between recognized and unrecognized letters. However, the interpretation of these results is potentially ambiguous. For example, the positive correlations indicate that children with higher familiarity and recognition scores tended to show greater VGG-derived visual separation between their recognized and unrecognized letter sets. This pattern could suggest that the visual structure or discriminability of the letters contributes to which letters become recognized, rather than simply ruling out generalization from recognized letters. The authors should therefore consider and discuss alternative interpretations of this finding rather than presenting it solely as evidence against the generalization account.

(3) Placement and reporting of the additional analyses

Several analyses added in response to the reviewers are important to the manuscript's main conclusions but remain primarily in the Supplementary Information. Although the GLME and VGG-16 analyses are briefly mentioned in the main Results, they are not reported in sufficient detail for readers to evaluate the central evidence. Given that the GLME directly models the orientation-dependent associations and the VGG-16 analysis addresses an important alternative account of familiarity with unrecognized letters, these analyses should be described in greater detail in the main manuscript. In addition, the analyses concerning familiarity and recognition reported in Section S1 of the Supplementary Information deserve a brief summary in the main Results, as they provide a fuller picture of the relationship between familiarity and recognition-the central topic of the study.

Reviewer #2 (Public review):

Summary:

In this study, the authors propose that there are two types of letter knowledge: knowledge about letter sound and knowledge about letter shape. Based on previous studies on implicit statistical learning in adults and babies, the authors hypothesized that passive exposure to letters in the environment allows early readers to acquire knowledge of letter shapes even before knowledge of letter-sound association. Children performed a set of experiments that measures letter shape familiarity, letter-sound association performance, visual processing of letters, and a reading-related cognitive skill. The results show that even the children who have little to no knowledge of letter names are familiar with letter shapes, and that this letter shape familiarity is predictive of performance in visual processing of letters.

Strengths:

The authors' hypothesis is based on widely accepted findings in vision science that repeated exposure to certain stimuli promotes implicit learning of, for example, statistical properties of the stimuli. They used simple and well-established tasks in large-scale experiments with a special population (i.e., children). The data analysis is quite comprehensive, accounting for any alternative explanations when needed. The data supports at least a part of their hypothesis that the knowledge of letter shapes is distinct from, and precedes, the knowledge of letter-sound association, and is associated with performance in visual processing of the letters. This study shed light on a rather overlooked aspect of letter knowledge, i.e., letter shapes, challenging the idea that letters are learned only through formal instruction and calling for future research on the role of passive exposure to letters in reading acquisition.

Weaknesses:

Although the authors have successfully identified the knowledge of letter shapes as another type of letter knowledge other than the knowledge of letter-sound association, the question of whether it drives the subsequent reading acquisition remains largely unanswered. The authors collected a RAN score, which is known to robustly predict future reading fluency, but it did not show a significant partial correlation with familiarity accuracy (i.e., familiarity accuracy is not necessary to predict RAN score). Future work may address whether the knowledge of letter shape leads to better reading fluency that is not captured by RAN scores.

Comments on revised version:

The authors have adequately addressed my comments. I don't have any further comments.

Reviewer #3 (Public review):

Summary:

This study investigates whether early print knowledge in children with minimal formal literacy instruction consists of separable components: letter shape familiarity and letter recognition. Using a series of behavioral experiments, the authors show that children can develop familiarity with letter shapes even when explicit letter naming knowledge is limited. They further demonstrate that letter shape familiarity is uniquely associated with the visual processing advantage for upright letters, whereas letter recognition is uniquely associated with RAN performance. In addition, the authors examine whether letter recognition mediates the relationship between letter shape familiarity and RAN, suggesting that letter recognition may serve as a pathway linking early visual familiarity with reading-related skills.

Strength:

This study addresses an important research gap by examining whether children develop letter familiarity prior to formal literacy instruction and by distinguishing letter shape familiarity from explicit letter recognition as separate components of early print knowledge. This conceptual distinction provides new insights into the development of emergent literacy and highlights a potentially overlooked component of early reading acquisition. The carefully designed behavioral tasks and comprehensive analyses further strengthen the study by allowing the authors to examine the unique contributions of these two components to visual processing and RAN.

Weakness:

Although the theoretical motivation of the study is compelling, I can't buy the conclusions from the analysis and results the author provided in the manuscript. The key problem that I am confused from the analysis is that whether the present study represents a double-dissociation design or a correlational study. If the authors divided the subjects into different groups by treating letter familiarity and letter recognition as two separate independent variables, then why correlation and mediation models for these variables were further conducted later on.

There are also several other analytical and interpretational issues require further clarification. First, some aspects of the statistical modelling need stronger theoretical justification. In particular, the rationale for selecting control variables in the partial correlation analyses is not always clear. Letter familiarity and letter recognition are conceptualized as components of letter knowledge, whereas visual search advantage and RAN appear to be outcome measures that may be influenced by these components. Therefore, controlling for RAN when examining the association between letter knowledge components and visual search advantage, and conversely controlling for visual search advantage when examining predictors of RAN, may complicate the interpretation of the unique contributions of familiarity and recognition. A clearer theoretical justification for these modelling choices would strengthen the conclusions.

Second, the potential overlap among covariates should be considered more carefully. For example, age and grade are highly related developmental variables, and the simultaneous inclusion of them in the analysis may introduce concerns regarding multicollinearity. Similarly, the mediation analysis would benefit from a more rigorous assessment of indirect effects, such as bootstrap confidence intervals, rather than relying only on the significance of individual pathways.

In addition, although the manuscript presents many valuable additional analyses, the overall presentation of the results could be improved. At times, the logical flow between analyses is difficult to follow. For example, the introduction of the full correlation matrix before the RAN-related regression and mediation analyses interrupts the progression of the main argument. A clearer organization linking each analysis to the specific theoretical question being addressed would help readers better understand how the different findings contribute to the proposed model.

Finally, the manuscript does not sufficiently discuss children who show high recognition but relatively low familiarity. While the authors provide a detailed interpretation of children who are highly familiar with letter shapes but have limited letter recognition, the opposite pattern is also theoretically informative. This pattern may provide important insights into whether letter familiarity and recognition develop sequentially, whether recognition can emerge independently through instruction, or whether differences in task demands contribute to the observed dissociation.

Overall, this study provides an important theoretical contribution by identifying letter shape familiarity as a potentially distinct component of early print knowledge. Addressing the analytical and presentation issues above would further strengthen the evidence supporting the authors' conclusions and enhance the impact of this work on the field of literacy development.

Author response:

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

eLife Assessment

This useful study identifies knowledge of letter shape as a distinct component of letter knowledge and shows that children acquire it even before formal reading instruction and without knowing the corresponding letter sounds. However, the evidence supporting the main conclusions is incomplete at the current stage. With additional analyses examining the relationships among the underlying variables and/or revising interpretations, the work would be of broad interest to researchers studying language and vision.

We have now done our best to include additional analyses and interpretation to address the Reviewers’ concerns, and look forward to a more positive assessment.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study examines letter-shape knowledge in a large cohort of children with minimal formal reading instruction. The authors report that these children can reliably distinguish upright from inverted letters despite limited letter naming abilities. They also show a visual-search advantage for upright over inverted letters, and this advantage correlates with letter-shape familiarity. These findings suggest that specialized letter-shape representations can emerge with very limited letter-sound mapping practice.

Thank you for your positive assessment and concise summary of our work.

Strengths:

This study investigates whether children can develop letter-shape knowledge independently of letter-sound mapping abilities. This question is theoretically important, especially in light of functional subdivisions within the visual word form area (VWFA), with posterior regions associated with letter/orthographic shape and anterior regions with linguistic features of orthography (Caffarra et al., 2021; Lerma-Usabiaga et al., 2018). The study also includes a large sample of children at the very beginning of formal reading instruction, thereby minimizing the influence of explicit instruction on the formation of letter-shape knowledge.

Thank you for acknowledging the importance of this work. We agree with you that this issue is important also because letter familiarity and letter-sound association learning could drive the development of the VWFA. We now acknowledge this in the Introduction (p. 7).

Weakness:

A central concern is that a production task (naming) is used to index letter-name knowledge, whereas letter-shape knowledge is assessed with recognition. Production tasks impose additional demands (motor planning, articulation) and typically yield lower performance than recognition tasks (e.g., letter-sound verification). Thus, comparisons between letter-shape and letter-name knowledge are confounded by task type. The authors' partial-correlation and multiple-regression analyses linking familiarity (but not production) to the upright-search advantage are informative; however, they do not resolve the recognition-versus-production mismatch. Consequently, the current data cannot unambiguously support the claim that letter-shape representations are independent of letter-name knowledge.

Thank you for raising this very important point. We agree with you that letter naming is not the only way to measure letter-sound knowledge, and that naming could involve production demands that are absent in other measures such as recognition. However, there is extensive literature showing that recall and recognition depend on shared mechanisms, and that performance on recall and recognition tasks is often correlated. Thus, it is unlikely that children with low naming accuracy would have high recognition accuracy. Of course, we cannot conclusively rule out the absence of letter name or recognition knowledge, and it would certainly be interesting to include additional tests of letter name knowledge in future studies. However, we do feel that our observations are important and intriguing, and will spur further research in this direction. We now acknowledge this issue in the Discussion (p. 29-30).

Reviewer #2 (Public review):

Summary:

In this study, the authors propose that there are two types of letter knowledge: knowledge about letter sound and knowledge about letter shape. Based on previous studies on implicit statistical learning in adults and babies, the authors hypothesized that passive exposure to letters in the environment allows early readers to acquire knowledge of letter shapes even before knowledge of letter-sound association. Children performed a set of experiments that measures letter shape familiarity, letter-sound association performance, visual processing of letters, and a reading-related cognitive skill. The results show that even the children who have little to no knowledge of letter names are familiar with letter shapes, and that this letter shape familiarity is predictive of performance in visual processing of letters.

Thank you for your positive assessment and concise summary of our work.

Strengths:

The authors' hypothesis is based on widely accepted findings in vision science that repeated exposure to certain stimuli promotes implicit learning of, for example, statistical properties of the stimuli. They used simple and well-established tasks in large-scale experiments with a special population (i.e., children). The data analysis is quite comprehensive, accounting for any alternative explanations when needed. The data support at least a part of their hypothesis that the knowledge of letter shapes is distinct from, and precedes, the knowledge of letter-sound association, and is associated with performance in visual processing of the letters. This study shed light on a rather overlooked aspect of letter knowledge, i.e., letter shapes, challenging the idea that letters are learned only through formal instruction and calling for future research on the role of passive exposure to letters in reading acquisition.

We are happy to note that you found our study interesting.

Weaknesses:

Although the authors have successfully identified the knowledge of letter shapes as another type of letter knowledge other than the knowledge of letter-sound association, the question of whether it drives the subsequent reading acquisition remains largely unanswered, despite it being strongly implied in the Introduction. The authors collected a RAN score, which is known to robustly predict future reading fluency, but it did not show a significant partial correlation with familiarity accuracy (i.e., familiarity accuracy is not necessary to predict RAN score). The authors discussed that the performance in visual processing of letters might capture unique variance in reading fluency unexplained by RAN scores, but currently, this claim seems speculative.

We totally agree with you and we have carefully reviewed our manuscript throughout to clarify that this is a speculation that follows from our findings, but remains to be proved.

Since, even children without formal literacy instruction were highly familiar with letter shapes, it would be reasonable to assume that they had obtained the knowledge through passive exposure. However, the role of passive exposure was not directly tested in the study.

We agree that letter shape knowledge must have come from passive print exposure. Understanding passive exposure in detail will require characterizing it in conjunction with several other important home related variables (parental educational status, parental involvement, literacy artefacts in the home, scripts in the home, adult literacy practices in the home, home tutoring, home-school linkages), and is beyond the scope of the present study. We now acknowledge these issues in the Discussion (p 32: Limitations and Future Directions).

Given the superimposed straight lines in Figure 2, I assume the authors computed Pearson correlation coefficients. Testing the statistical significance of the Pearson correlation coefficient requires the assumption of bivariate normality (and therefore constant variance of a variable across the range of the other). According to Figure 2, this doesn't seem to be met, as the familiarity accuracy is hitting the ceiling. The ceiling effect might not be critical in Figure 2, since it tends to attenuate correlation, not inflate it. But in Figures 3 and 4, the authors' conclusion depends on the non-significant partial correlation. In fact, the authors themselves wrote that the ceiling effect might lead to a non-significant correlation even if there is an actual effect (line 404).

Thank you for your careful reading! We have now clarified how the straight-line fit in Figure 2A was generated (line 261-263, p. 13) and now report the non-parametric Spearman correlation which is also statistically significant.

Regarding Figures 3 and 4, the reviewer raised an important concern about whether ceiling effects might obscure meaningful relationships in the reported partial correlations. Such an issue would arise only if the relevant parameter pairs (e.g., other parameters versus upright search advantage in Figure 3, or versus RAN score in Figure 4) exhibited comparable ceiling effects. To directly address this concern and demonstrate the robustness of our findings, we have undertaken the following additional analyses:

(1) Parameter distributions. We now include the distribution of each parameter (Supplementary Figure S1.2). This analysis shows that only two relevant measures: motor accuracy and familiarity accuracy, exhibit ceiling effects. Although upright and inverted search accuracy do approach the ceiling, our analyses use the accuracy difference, which follows an approximately normal distribution.

(2) Scatter plot visualization. We have added scatter plots for the relevant parameter pairs (Supplementary Figure S2.1 for Figure 3 and Supplementary Figure S3.1 for Figure 4). These plots demonstrate that the data are sufficiently well distributed across the measurement range, indicating that meaningful associations would be detectable if present.

(3) Multiple regression and mixed-effects modelling. Previously, we used multiple linear regression analyses to validate the robustness of the partial correlation results in Figure 3 (now reported in detailed under Supplementary Section S2.2). We have now extended this approach by replicating the linear regression analysis for modelling RAN scores (Supplementary Section S3.2) and by conducting mixed-effects modelling to assess the contribution of different parameters to search reaction time (Supplementary Section 2.3).

Together, these additional analyses provide converging evidence that our results are not driven by ceiling effects or other statistical artifacts, and they reinforce the robustness of the conclusions drawn from Figures 3 and 4.

Reviewer #3 (Public review):

Summary:

This study examined how young children with minimal reading instruction process letters, focusing on their familiarity with letter shapes, knowledge of letter names, and visual discrimination of upright versus inverted letters. Across four experiments, kindergarten and Grade 1 children could identify the correct orientation of letters even without knowing their names.

Thank you for your positive assessment and concise summary of our work.

Strengths:

This study addresses an important research gap by examining whether children develop letter familiarity prior to formal literacy instruction and how this skill relates to reading-related cognitive abilities. By emphasizing letter familiarity alongside letter recognition, the study highlights a potentially overlooked yet important component of emergent literacy development.

We are happy to note that you found our study to be addressing an important research gap.

Weaknesses:

The study's methods and results do not effectively test its stated research goals. Reading ability was not directly measured; instead, the authors inferred its relationship with reading from correlations between letter familiarity and reading-related cognitive measures, which limits the validity of their conclusions. Furthermore, the analytical approach was rather limited, relying primarily on simple and partial correlations without employing more advanced statistical methods that could better capture the underlying relationships.

We respectfully disagree for the following reasons.

(1) We strategically targeted early readers because it is only in early readers that we could hope to disentangle letter familiarity from letter recognition. Once a child is reading fluently, his/her letter familiarity could come from knowing the names of letters, rather than from shape familiarity alone. We could not measure reading ability directly since these children were in the early stages of learning to read, and so we have measured their RAN score instead which is a precursor for fluent reading.

(2) We have claimed that letter familiarity could potentially boost early reading, because we have shown that it already leads to a visual processing advantage. We have acknowledged throughout that our observations are important as such, and imply (but do not prove) a potential role for letter shape familiarity in early reading.

(3) We have now replicated all our analyses using advanced statistical techniques, which are now reported in the Supplementary Material. In general, partial correlation analyses are mathematically equivalent to multiple linear regression and generalized linear modelling, so it is unsurprising that all these analyses yield similar conclusions.

Major Comments:

(1) Limited Novelty and Unclear Theoretical Contribution:

The authors aim to challenge the view that children acquire letter shape knowledge only through formal literacy instruction, but similar questions regarding letter familiarity have already been explored in previous research. The manuscript does not clearly articulate how the present study advances beyond existing findings or why examining letter familiarity specifically before formal instruction provides new theoretical insight. Moreover, if letter familiarity and letter recognition are treated as distinct constructs, the authors should better justify their differentiation and clarify the theoretical significance of focusing on familiarity as an independent component of emergent literacy.

We respectfully disagree with this reading of the current study. We have searched through the literature on this topic once again and most studies have compared frequent versus infrequent letters or strings but have not directly tested letter familiarity as we have done. In other words, there is little in the literature on the distinction between letter familiarity and letter recognition. We have now reworked the Introduction section to highlight this conceptual distinction, drawing attention to components within the term letter knowledge: letter shape familiarity, and letter recognition, (p. 3-5). We would, however, be happy to review and contrast with prior work if you can point us to it.

(2) Overgeneralization to Reading Ability:

Although the study measured several literacy-related cognitive skills and examined correlations with letter familiarity, it did not directly assess children's reading ability, as participants had not yet received formal literacy instruction. Therefore, the conclusion that letter familiarity influences reading skills (e.g., Line 519: "Our results are broadly consistent with previous work that has highlighted print letter knowledge as a strong predictor of future reading skills") is not fully supported and should be clarified or revised.

We agree that the line was ambiguous, which led this confusion. By letter knowledge, we were referring to letter recognition ability (not letter shape familiarity), which is a well-established predictor of reading ability and is also partially correlated with the RAN score in our study (Figure 4B). We have now clarified this ambiguity by changing “letter knowledge”, to “letter naming knowledge” (line 667-669 now, and other places) in the manuscript.

To draw conclusions about the impact on reading ability, a longitudinal study would be more appropriate, assessing the relationship between letter familiarity and reading skills after children have received formal literacy instruction. If a longitudinal study is not feasible, measuring familial risk for dyslexia could provide an alternative approach to infer the potential influence of letter familiarity on later reading development.

While assessing the impact of letter familiarity on later reading ability using a longitudinal design or familial risk is indeed valuable, this is beyond the scope of the current study. We have acknowledged this in the 'Limitations and Future Directions' section (p. 32).

(3) Confusing and Limited Analytical Approach with Potential for More Sophisticated Modelling: The study employs a confusing analytical approach, alternating between simple correlational analyses and group-based comparisons, which may introduce circularity - for example, defining high vs. low familiarity groups partly based on performance differences in upright versus inverted letters and then observing a visual search advantage for upright letters within these groups.

We respectfully disagree that analytical approach related to subgrouping introduces circularity. Subgroups were defined exclusively using Experiments 1 and 2, which measured letter shape familiarity and letter naming based on accuracy. Experiment 3, in contrast, is a visual search task that does not require letter shape or naming knowledge, and its primary outcome measure is search time, not accuracy. Group assignment is therefore independent of the dependent variable in Experiment 3.

Our analyses simply test whether children who differ in letter knowledge also differ in visual search performance. This is not reported before, rather, represent the hypothesis being tested here, making the approach non-circular.

Furthermore, we have analysed our data without dividing participants into groups (Figures 3-4) and obtained similar results.

Moreover, the analyses are relatively simple: although multiple linear regression is mentioned, the results are not fully reported.

We now report the result of multiple linear regression in the supplementary material (Supplementary Section S2.2, and Section S3.2), where we obtained similar results.

These approaches may not fully capture the complex relationships among letter familiarity, recognition, visual search performance, RAN, and other covariates. More sophisticated modeling, such as mixed-effects models to account for repeated measures, structural equation modeling to examine latent constructs, or multivariate approaches jointly modeling familiarity and recognition effects, could provide a clearer understanding of the unique contribution of letter shape familiarity to early literacy outcomes.

We thank the reviewer for this suggestion. We have now conducted mixed-effects modelling to assess the contribution of different parameters to search reaction time. These additional analyses are described in detail in “Supplementary Sections S2.3: Contributions of various factors to letter search advantage: Generalized Linear Mixed-Effects Modelling (GLME)”, and yield results fully consistent with the original partial correlation findings.

In addition, a large number of correlations were conducted without correction for multiple comparisons, which may increase the risk of false positives and raise concerns about the reliability of some significant findings.

We thank the reviewer for this suggestion. We now have reported the correction for multiple comparisons wherever applicable, and all our key findings remain significant.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Introduction: The authors divide print knowledge into two components: letter shape (visual familiarity) and letter name (visual-sound associations). While letter-name knowledge is widely considered important for reading acquisition, it remains unclear whether letter-shape knowledge, independent of letter name, is important for reading development (Q1) and capable of inducing a visual-processing advantage (Q2).

While the question is worthwhile, the motivation needs tightening. The three lines of literature cited - (1) print knowledge in kindergarteners, (2) associations between reading and basic visual skills, and (3) early sensitivity to repetition/statistical regularities - do not, as currently framed, present a strong reason to study letter-shape knowledge per se.

First, evidence from kindergarten print knowledge (Lochy et al., 2016; Maurer et al., 2005) likely includes children with at least some letter-name exposure. Indeed, the neural measures reported there were associated with letter name knowledge measured in their child participants. Likewise, the claim that children from rich home-literacy environments can distinguish words/sentences from scribbles or inverted forms (Levy et al., 2006) does not preclude informal letter-name learning at home and thus does not show that shape familiarity precedes name learning. Please also define "global print features" (L43), explain how they differ from letter-shape features, and clarify why the global features are less relevant.

Thank you for this suggestion. We have now reworked the relevant paragraph of the Introduction to make this clearer.

Second, the work linking reading to basic visual functions is relevant, but the manuscript should connect those findings to letter-shape familiarity specifically-i.e., make explicit why any observed visual advantage should track familiarity with letter forms (controlling for name knowledge).

Third, the repetition/statistical-learning literature cited does not specify representational grain. Such learning may preferentially build whole-word familiarity rather than letter-level representations; many early readers know a small set of high-frequency sight words in their environment (e.g., "McDonald's") without abstracting letter shapes.

Thank you for these suggestions. We have now revised the Introduction (p. 6) to make these points clearer.

(2) Methods and Results:

The Methods and Results sections are difficult to follow. The motivation and procedures for several analyses are not described explicitly or clearly, and some analyses do not address the stated questions. My detailed comments follow.

(a) Experiments 1 & 2:

The analyses of the "top-line" effect (corresponding to /a/) are confusing (L194-200). After computing accuracies for letters with vs. without a top line, why are correlations performed? Correlations highlight similarity, not group differences. To test whether the top line contributes to or influences performance-that is, whether it differentiates the two stimulus groups-paired comparisons or mixed-effects models should be used.

We thank the reviewer for highlighting this. We agree that correlation indicates similarity, and it does not address the specific contribution of the top-line (matraa). We now present a detailed analysis in Supplementary Section 2.4, and also now show that the top line does not have any effect on the upright letter search advantage.

L201: Why do the authors assume some letters are more recognizable than others? Which letters are these? The appropriate test is to compute letter-wise accuracies for the proposed subset and compare them against the remaining letters. Split-half correlations cannot answer this question. As above, correlations between letter sets do not test whether the top line influences recognition accuracy.

Our assumption that some letters are more recognizable than others is grounded in the structure of the school curriculum, in which certain letters are introduced earlier than others. From the 18 letters used in the study, we selected 9 letters introduced early in the curriculum (ಅ, ಆ, ದ, ಗ, ಇ, ಈ, ಖ, ಒ, ರ) and 9 letters introduced later (ದು, ಜ, ಳಿ, ಲ್ಲಿ, ನ, ನಾ, ಣ, ನ್ನು, ವ).

To directly address the reviewer’s concern, we computed recognition accuracy separately for the early- and late-introduced letter sets for each child and compared these measures. Children were significantly more accurate for early-introduced letters than for late-introduced letters (“mean ± SEM accuracy: early taught: 70.1% ± 1.9%; late taught: 38.5% ± 1.9%; p < 0.00005, rank-sum test across 285 children, who did the recognition task”, L250-258, p. 12-13). We have now included this analysis in the Results section.

However, as multiple analyses show that recognition accuracy does not uniquely predict the upright search advantage (Main Text Figure 3B; Supplementary section S2.2, S2.3, S2.4), we did not further pursue analyses examining the differential contributions of early versus late letter recognition accuracy or included early vs late accuracy comparison result in the article.

L218-219: How is the fitted line in Figure 2A determined? Please specify the model.

This was done using standard linear least squares fitting. We have now updated the manuscript with these details (L261-263, p. 13).

L221-234: It is unclear why correlations between familiarity accuracies for unrecognized letters and overall recognition accuracy rule out the alternative explanations the authors propose. Moreover, the fact that some children who can name only a few letters nevertheless achieve high letter-shape recognition does not exclude the possibility that they can generalize shape statistics from those few known letters. Please provide the full argument and supporting evidence (citations) or include analyses that directly test this generalization account.

We thank the reviewer for this comment and agree that the logic was not sufficiently explicit in the manuscript. Our argument has two components.

First, if letter familiarity were merely a byproduct of letter recognition, then any effect of familiarity should be subsumed by recognition. In that case, removing recognition-related variance should eliminate familiarity effects. Contrary to this prediction, across multiple analyses we find that familiarity independently predicts the search advantage, whereas recognition does not, demonstrating that familiarity cannot be reduced to recognition.

Second, to directly test the alternative possibility that children generalize shape statistics from the few letters they recognize, we used a computational similarity analysis. Specifically, we wondered whether letter familiarity for unrecognized letters depended on their similarity to recognized letters. To this end, for each child, we identified the unrecognized letters and calculated their average dissimilarity to recognized letters using a computational model (a neural network pretrained for object categorization, VGG-16), and asked whether the familiarity accuracy varied with the average dissimilarity between the recognized and unrecognized letters. If, familiarity accuracy on unrecognized letters is coming from shape generalization from recognized ones, then the familiarity accuracy will be more, as the dissimilarity decreases, i.e. we will see a negative correlation, but we in fact obtained a weak positive correlation (Section S1.6).

We have included the above text in the Results (L. 299-309, p. 14-15) and in the Supplementary Material (Section S1.6).

(b) Experiment 3:

L280-281: "Thus, the visual processing advantage for upright letters is associated more strongly with visual familiarity for letter shape than with letter recognition." This claim requires an interaction test. For example, quantify the upright advantage as the upright-minus-inverted difference and run a 2×2 analysis (Orientation: upright/inverted × Knowledge type: familiarity/recognition), or an equivalent mixed-effects model, to test main and interaction effects. To their credit, the authors already analyze the difference score and examine unique associations via partial correlations and regression; an explicit interaction/contrast would complete the argument.

We thank the reviewer for this suggestion. We address this directly using a mixed-effects model on raw search reaction times (Supplementary section “S2.3: Contributions of various factors to letter search advantage: Generalized Linear Mixed-Effects Modelling (GLME)”). This analysis shows that familiarity significantly facilitates faster responses in the upright relative to the inverted condition, whereas recognition does not. This supports our claim that the upright advantage is more strongly linked to visual familiarity than to letter recognition.

(c) Effects of grade and language of instruction across experiments:

These sections largely repeat the main analyses on different subsamples/methods and confirm robustness without adding new information. Consider condensing to one sentence, noting consistency across subsamples and moving details to the Supplement. Please also provide a concise summary table of key statistics for readability. Interpretive statements should be moved to the Discussion.

We appreciate the reviewer’s suggestion and understand the concern about redundancy. However, grade and language of instruction are primary variables in this study, as they are directly linked to instructional exposure and the testing context. For this reason, we prefer to keep these analyses in the main text rather than moving them to the Supplement, which is often accessed only by interested readers. Although these analyses confirm robustness across subsamples, we consider this evidence central to our conclusions.

Which factors are associated with rapid automatized naming (RAN) scores?

Please state the motivation for including the RAN analysis and explain how its results inform the central question about letter-shape knowledge and the visual advantage.

We have now added a few lines to address this before discussing the results of the RAN task, under the heading “Which factors are associated with rapid automatized naming (RAN) scores?” (L.550-559, p. 25)

(d) Correlations among all factors across experiments:

The purpose of these correlations is unclear. As presented, they primarily show strong associations between familiarity and recognition (both RT and accuracy), highlighting the close relationship between letter shape and letter name. Reaction time (RT) is also introduced for the first time here; please explain why RTs are not analyzed earlier and how they complement the accuracy-based results.

We focus on accuracy for the letter familiarity and recognition tasks because these measures assess knowledge: whether a child knows the letter, rather than speed of response. In contrast, reaction time (RT) is more informative in visual search tasks, where it reflects the efficiency with which a child can locate the target. Figure 4C is included to illustrate the relationships among all measured parameters, including RT, providing additional context for interested readers. These correlations are not central to our main hypotheses but are reported for completeness.

(5) Discussion:

The Discussion should center on interpreting the core findings - high letter-shape familiarity and the upright-letter advantage in minimally instructed children - by situating them within prior work, outlining plausible formation mechanisms, and identifying contributing factors. Current sections on emergent reading skills (e.g., Understanding emergent literacy; Role of additional factors in reading acquisition) extend beyond what is tested here and should be substantially reduced or reframed. Speculation is acceptable but should not dominate the interpretation; please anchor claims in the present data and prior evidence.

We have reframed the Discussion more closely on our core findings and have reduced the section on the role of additional factors in reading acquisition, as suggested. We believe, the revised version is more firmly grounded in the present results, and we hope it will be more accessible and acceptable to readers and reviewers.

Letter knowledge as a predictor of early reading skills:

The discussion opens by linking letter knowledge to early reading, but this relationship is not tested in the paper. If anything, the null relation with RAN-a well-known precursor of reading-cautions against strong claims. I therefore do not agree with the statement that "Our results are broadly consistent with previous work that has highlighted print letter knowledge as a strong predictor of future reading skills,".

This is a phrasing problem from our side, as we thank you for your careful reading of this point. By ‘letter knowledge,’ we specifically meant letter name knowledge, or letter recognition, not letter shape familiarity. We agree that the original wording was confusing, and we have clarified it accordingly: “Our finding that letter naming in RAN is predicted by letter naming knowledge is broadly consistent with previous work that has highlighted letter naming as a strong predictor of future reading skills….” (L. 668)”.

Minor comment:

L52-54: "For example, children with low RAN scores (an early cognitive skill related to reading, as discussed earlier), showed slower performance in basic visual tasks, such as simple reaction time and same/different decision tasks (Stainthorp et al., 2010)." RT and decision tasks are outcomes or paradigms, not visual mechanisms per se.

We acknowledge the mistake in wording, and now have revised the text to clarify this distinction: (L.69-72) “For example, children with low RAN scores (an early cognitive skill related to reading, as discussed earlier), showed slower performance in basic visual tasks, as measured by simple reaction time and same/different decision tasks (Stainthorp et al., 2010).”

Reviewer #2 (Recommendations for the authors):

(1) The authors wrote that they selected 18 letters with a range of letter frequencies. Would it be possible for the authors to correlate familiarity accuracy for each letter and the frequency of each letter in Kannada? According to the authors' hypothesis of implicit learning through passive exposure, one might expect that readers are more familiar with frequent letters than the infrequent ones. It would be particularly great if the authors could measure the letter frequency in the readers' learning environments (e.g., school, children's book).

We have now included additional analyses of letter frequencies from a children’s book corpus {Citation} in Supplementary Section S1.3. The frequency data come from The Promise Foundation Corpus of Child-Directed Print drawn from 402 books for children between 3 and 10. We find no clear association between letter familiarity and letter frequency, at least for this corpus.

(2) Regarding the question of whether the letter shape familiarity drives the subsequent reading acquisition, can the authors perform a mediation analysis on IV: familiarity accuracy, mediator: recognition accuracy, and DV: RAN scores? The correlations between three variables (i.e., the significant correlation between familiarity accuracy and recognition accuracy, the significant partial correlation between recognition accuracy and RAN scores, and the non-significant partial correlation between familiarity accuracy and RAN scores) jointly suggest a full mediation. However, they do not guarantee a significant indirect effect of familiarity accuracy on RAN scores. The authors might even want to consider other variables, such as age or grade, as a moderator. Please note, though, I'm not suggesting that the authors should make claims about causal directions with the mediation analysis on their observation data.

We thank the reviewer for this insightful suggestion. We performed the mediation analysis as recommended, and the results indicated full mediation: letter shape familiarity predicted recognition accuracy, which in turn predicted RAN scores, while the direct effect of familiarity on RAN was non-significant. We have now included these in the Results (p. 28: Letter-RAN associations: Could letter familiarity affect RAN score through letter recognition?).

(3) Regarding the ceiling effect and the significance testing of correlation coefficients, at the very least, I recommend including scatter plots for key factors in Figures 3 and 4.

We have now added distributions of all relevant parameters (Supplementary Figure S1.2), which indicate that only motor accuracy and familiarity accuracy exhibit ceiling effects. In addition, we have included scatter plots for the key parameter pairs underlying Figures 3 and 4 (Supplementary Figures S2.1, and S3.1). Finally, we report both linear regression and generalized linear mixed-effects (GLME) analyses for Figures 3 and 4 to demonstrate the robustness of our claims (Sections 2 and 3, Supplementary Material).

(4) The letter familiarity task results are shown as either averages across readers or across letters, but not as reader-letter pairs. In the letter familiarity task, each of the 18 letters was repeated four times. Is correctness consistent across four repeats of each letter for each reader? That is, if a dot in Figure 2A says a reader has the familiarity accuracy of 75%, is that number mainly driven by the reader 1) being correct in all four repeats for 75% of 18 letters and incorrect in all four repeats for the remaining 25%, or 2) being correct in three out of four repeats for all 18 letters?

This is an interesting question, thank you for this suggestion. To address this, we computed letter-wise accuracy values (0, 0.25, 0.5, 0.75, or 1, as there were 4 repeats/letter) for each child. We focused this analysis on 41 children whose overall familiarity accuracy did not exceed 90%, as ceiling performance precludes meaningful assessment of variability (Supplementary Section S1.1).

This analysis shows that children with lower overall familiarity accuracy exhibit substantial variability across repetitions of the same letter, indicating inconsistent responding, whereas children with higher overall familiarity accuracy show strong internal consistency, with most letters reaching 100% accuracy across repeats (Supplementary Figure S1.1A). We now report this analysis in the Supplementary Material (supplementary section “S1.1: Internal consistency of familiarity accuracy for each child.”).

(5) Figure 4C: Since the conclusions from Figures 3 and 4 are based on partial correlations, something similar to Figure 4C but with partial correlations might be helpful.

We thank the reviewer for the suggestion. However, we did not have a specific hypothesis motivating a partial correlation for Figure 4C. The correlations presented here are across all parameters measured in our study, and are included primarily for completeness and to allow inquisitive readers to explore potential relationships.

(6) Figures 2D-G are bar plots, but the y-axis starts at 2. I suggest the authors break both the y-axis and the bars to more explicitly prevent readers from misinterpreting the relative differences among the four plots, or alternatively use violin plots.

While we appreciate the point, we consider it a minor issue and believe that the current presentation of Figures 2D–G conveys the data clearly. Therefore, we prefer to keep the plots as they are.

(7) Figures 2 and S1: By eyeballing, there seem to be ~120 data points in Figure 2A, suggesting that some data points are overlapping, probably because there are only 19 levels of recognition accuracy, and familiarity accuracy is hitting the ceiling. Figure S1 suffers even more from the same visualization issue. I think the authors can try using the size or transparency of markers to indicate overlapping data points in Figure S1, but I'm not sure whether it would work for Figure 2 as well.

We have now added transparency to the markers in Figure S1 (now Supplementary S1.5) to better indicate overlapping data points. For Figure 2, however, applying transparency did not improve the visualization, so we have retained the original presentation.

(8) Figure 2 caption: "high/low familiarity (cyan/blue) x high/low recognition (orange/red)" is not an accurate description of the color coding.

Apologies for this confusion. We have now clarified in the revised text (p. 17, L355-359).

Reviewer #3 (Recommendations for the authors):

(1) Line 35: The statement 'a tacit assumption made by most studies is that letter knowledge is taken as the ability to explicitly name or recognize letters' requires supporting references.

We thank the reviewer for this suggestion. We have now included relevant references: L.48-50: “A tacit assumption made by most studies is that letter knowledge is the ability to explicitly name or recognize letters (Muter et al., 2004; Noel Foulin, 2005; Sigmundsson et al., 2020; Stephenson et al., 2008)”.

(2) Line 39: Similarly, the claim 'children only become familiar with letter shapes once they start learning letter names' should be supported by prior literature.

We would like to respectfully note that the reviewer appears to have focused on an incomplete line, which may have caused some confusion. As described in the text, this is an assumption rather than a well-established claim, and it is exactly what we aim to test in our study.

(3) Lines 38-42: The logical connection between the sentences is unclear. If the authors want to emphasize that children from rich home literacy environments HLE can distinguish letters from non-letters before formal literacy instruction, this should be made clearer.

We apologize for any confusion. Here, our intent was simply to highlight that children can become familiar with written forms, even before formal reading instruction. The reference to a rich home literacy environment (HLE) is related to the cited paper and not a claim we are making in our study.

(4) The distinction between Lower and Upper Kindergarten is unclear, as the age ranges are similar, and the LKG group may even have a higher mean age. The criteria for this grouping should be clarified.

The distinction between Lower and Upper Kindergarten (LKG and UKG) is based solely on the class in which the children were enrolled during data collection. In India, schooling typically consists of LKG, UKG, and then first grade. Placement criteria can vary slightly across schools (resulting overlapping age range across LKG and UKG), and we have not examined these school-specific differences.

(5) In Experiment 3, a Wilcoxon signed-rank test was used to compare upright vs. inverted letters. It is unclear whether the data were tested for normality to justify using a non-parametric test rather than a paired t-test. The rationale for choosing a non-parametric test should be provided.

This is a valid concern, as our reasoning was not explicitly stated. We consistently tested all parameters for normality, and whenever one or both parameters failed, we applied a non-parametric test. We have now added the following clarification to the Methods section: “While reporting comparison results, we always tested parameter pairs for normality first, and applied non-parametric alternative to t-tests whenever even one parameter failed normality testing.” (L.791-793)

(6) Lines 324-325 mention a baseline motor task measuring speed and accuracy, but the manuscript does not describe when or how it was administered, what stimuli were used, or whether it was part of the main experiment or separate. This information is necessary to interpret the correlation analysis in Figure 3.

We thank the reviewer for pointing this out. Now we have added details of the motor task in the method section: “At the beginning, to estimate motor speed…”(L:867).

(7) The distributions of task scores for kindergarten and Grade 1 children are not provided. This is particularly important when discussing potential ceiling effects.

We have now included distributions across all children in the Section S1.2, but we did not feel that it was useful to separate them into groups.

(8) Line 548 mentions 'components of emergent literacy evolve over time.' It is unclear whether this refers to the developmental stages of children or the evolution of the theoretical concept.

We agree that the original sentence was ambiguous. We have now rewritten this section such that, this phrase does not exist anymore.

References

Caffarra, S., Karipidis, I. I., Yablonski, M., & Yeatman, J. D. (2021). Anatomy and physiology of word-selective visual cortex: From visual features to lexical processing. Brain Structure and Function, 226(9), 3051–3065. https://doi.org/10.1007/s00429-021-02384-8

Lerma-Usabiaga, G., Carreiras, M., & Paz-Alonso, P. M. (2018). Converging evidence for functional and structural segregation within the left ventral occipitotemporal cortex in reading. Proceedings of the National Academy of Sciences, 115(42), E9981–E9990. https://doi.org/10.1073/pnas.1803003115

Levy, B. A., Gong, Z., Hessels, S., Evans, M. A., & Jared, D. (2006). Understanding print: Early reading development and the contributions of home literacy experiences. Journal of Experimental Child Psychology, 93(1), 63–93. https://doi.org/10.1016/j.jecp.2005.07.003

Lochy, A., Van Reybroeck, M., & Rossion, B. (2016). Left cortical specialization for visual letter strings predicts rudimentary knowledge of letter-sound association in preschoolers. Proceedings of the National Academy of Sciences, 113(30), 8544–8549. https://doi.org/10.1073/pnas.1520366113

Maurer, U., Brem, S., Bucher, K., & Brandeis, D. (2005). Emerging Neurophysiological Specialization for Letter Strings. Journal of Cognitive Neuroscience, 17(10), 1532–1552. https://doi.org/10.1162/089892905774597218

Muter, V., Hulme, C., Snowling, M. J., & Stevenson, J. (2004). Phonemes, Rimes, Vocabulary, and Grammatical Skills as Foundations of Early Reading Development: Evidence From a Longitudinal Study. Developmental Psychology, 40(5), 665–681. https://doi.org/10.1037/0012-1649.40.5.665

Nag, S., John, S., & Agrawal, A. (2024). NSP-SCD: A corpus construction protocol for child-directed print in understudied languages. Behavior Research Methods, 56(4), 2751–2764. https://doi.org/10.3758/s13428-024-02339-x

Noel Foulin, J. (2005). Why is letter-name knowledge such a good predictor of learning to read? Reading and Writing, 18(2), 129–155. https://doi.org/10.1007/s11145-004-5892-2

Sigmundsson, H., Haga, M., Ofteland, G. S., & Solstad, T. (2020). Breaking the reading code: Letter knowledge when children break the reading code the first year in school. New Ideas in Psychology, 57, 100756. https://doi.org/10.1016/j.newideapsych.2019.100756

Stainthorp, R., Stuart, M., Powell, D., Quinlan, P., & Garwood, H. (2010). Visual Processing Deficits in Children With Slow RAN Performance. Scientific Studies of Reading, 14(3), 266–292. https://doi.org/10.1080/10888431003724070

Stephenson, K. A., Parrila, R. K., Georgiou, G. K., & Kirby, J. R. (2008). Effects of Home Literacy, Parents’ Beliefs, and Children’s Task-Focused Behavior on Emergent Literacy and Word Reading Skills. Scientific Studies of Reading, 12(1), 24–50. https://doi.org/10.1080/10888430701746864

Add subcategories: biahazar, pest disease, etc

just_marcha (en singular)

Más menos 10

Reforzaría que esto es simple y constante: Ha: las variables se encuentran asociadas (ej: existen diferencias por sexo en pertenencia al barrio), y Ho: no hay diferencias. La falta de diferencias se expresa en que frecuencias esperadas al azar no son (estadísticamente) distintas de lo que se observa en la tabla inicial. Y entonces, concepto central de Chi2 (y creo el más difícil): frecuencia esperada

le daría otro nombre a este paso (más informativo)

esto no me parece muy informativo

creo que esto lo dejaría más bien al final del primer ejercicio

(observada)

Entre este párrafo y los siguientes, haría un callout con los conceptos dentrales de asociación entre categóricas y una breve definición

o más

eLife Assessment

The article presents important findings of a dissociation between phasic and tonic pain functions in adaptive behavior, combining immersive VR, computational modeling, skin conductance, and EEG data. The methodology used is convincing. Its ecological design and sophisticated computational modeling are major strengths.

Reviewer #1 (Public review):

[Editor's note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed the comments raised in the previous round of review.]

Summary:

This article presents a study consisting of two experiments, which aim to dissociate and quantify the distinct motivational functions of phasic and tonic pain within a naturalistic and immersive VR setting. Specifically, the Authors test two hypotheses: (i) that phasic pain acts as a punishment signal that drives avoidance learning; (ii) that tonic pain reduces motivational vigor, promoting energy conservation and recuperation. In both experiments, participants performed a free-operant foraging task, where they collected virtual pineapples to earn points.

In Experiment 1, phasic pain was delivered as a brief electric shock to the grasping hand when picking up green pineapples. As phasic pain intensity increased, participants were less likely to choose painful fruits. A reinforcement learning model that incorporated reward, pain cost and effort cost was able to successfully capture behavior.

Experiment 2 combined effects of phasic and tonic pain. Tonic pain was induced by a pressure cuff on the non-dominant arm, simulating sustained discomfort. Interestingly, tonic pain did not affect the perceived intensity or avoidance of phasic pain. However, it significantly reduced movement velocity and pineapple collection rate, interpreted as a reduction of motivational vigor. A temporal decision model incorporating vigor cost successfully captured these effects.

Concomitant EEG recordings showed that tonic pain was associated with reduced alpha and beta power in parietal and temporal areas. Phasic pain ratings and decision values distinctively correlated with skin conductance responses.

Overall, these findings indicate that phasic and tonic pain have distinct and dissociable motivational effects.

Strengths:

This is an ambitious study that provides a quantitative dissociation of the roles of phasic and tonic pain in adaptive behavior, by integrating ecological neuroscience, motivational theory, and computational modeling. The use of immersive VR combined with a free-operant foraging task offers a more ecologically valid context to study pain-related behavior compared to traditional paradigms. Furthermore, the study employs a multimodal approach by combining behavioral data, computational frameworks, physiological signals and EEG. In particular, one of the main strengths of the study is the use of sophisticated computational modeling to capture phasic and tonic pain effects. The experiment codes are available on GitHub, increasing reproducibility.

Reviewer #2 (Public review):

Summary:

The study investigated the distinct roles of phasic and tonic pain in adaptive behavior. Phasic pain was proposed to function as a teaching signal, promoting avoidance of further injury, while tonic pain was hypothesized to support recuperative behavior by reducing motivational vigor. This hypothesis was tested using an immersive virtual reality (VR) EEG foraging task, in which participants harvested fruit in a forest environment. Some fruits triggered brief phasic pain to the grasping hand, which in turn reduced the likelihood of choosing those fruits. Concurrently, tonic pressure pain applied to the contralateral upper arm was associated with reduced action velocities. The authors employed a free-operant computational framework to quantify how phasic and tonic pain modulate motivational vigor and decision value. Importantly, model parameters were found to correlate with EEG responses, providing neurophysiological support for the hypothesized functional distinctions.

Comments on revised version.

All my comments have been well addressed.

Reviewer #3 (Public review):

Summary:

This study investigates how phasic and tonic pain modulate behaviour in a free-operant foraging paradigm. The authors apply a computational modeling approach to the behavioural data to quantify the decision value of phasic pain, as well as the degree to which tonic pain reduces motivational vigour. EEG assessments showed, e.g., reduced signal power at alpha and beta frequencies in tonic pain conditions compared to no-tonic-pain conditions, but no association between these neural measures and motivational vigour. The authors conclude that tonic and phasic pain serve different motivational functions, with phasic pain acting as a punishment signal promoting avoidance and tonic pain reducing motivational vigour.

Strengths:

The experimental paradigm is highly innovative. Assessing human behaviour in a naturalistic yet highly controlled setting represents a promising approach to pain research. Notably, assessing pain magnitude implicitly, via its motivational value, offers insights about the overall pain experience that are not usually accessible via common pain ratings.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This article presents a study consisting of two experiments, which aim to dissociate and quantify the distinct motivational functions of phasic and tonic pain within a naturalistic and immersive VR setting. Specifically, the Authors test two hypotheses: (i) that phasic pain acts as a punishment signal that drives avoidance learning; (ii) that tonic pain reduces motivational vigor, promoting energy conservation and recuperation. In both experiments, participants performed a free operant foraging task, where they collected virtual pineapples to earn points.

In Experiment 1, phasic pain was delivered as a brief electric shock to the grasping hand when picking up green pineapples. As phasic pain intensity increased, participants were less likely to choose painful fruits. A reinforcement learning model that incorporated reward, pain cost and effort cost was able to successfully capture behavior.

Experiment 2 combined effects of phasic and tonic pain. Tonic pain was induced by a pressure cuff on the non-dominant arm, simulating sustained discomfort. Interestingly, tonic pain did not affect the perceived intensity or avoidance of phasic pain. However, it significantly reduced movement velocity and pineapple collection rate, interpreted as a reduction of motivational vigor. A temporal decision model incorporating vigor cost successfully captured these effects.

Concomitant EEG recordings showed that tonic pain was associated with reduced alpha and beta power in parietal and temporal areas. Phasic pain ratings and decision values distinctively correlated with skin conductance responses.

Overall, these findings indicate that phasic and tonic pain have distinct and dissociable motivational effects.

Strengths:

This is an ambitious study that provides a quantitative dissociation of the roles of phasic and tonic pain in adaptive behavior, by integrating ecological neuroscience, motivational theory, and computational modeling. The use of immersive VR combined with a free-operant foraging task offers a more ecologically valid context to study pain-related behavior compared to traditional paradigms. Furthermore, the study employs a multimodal approach by combining behavioral data, computational frameworks, physiological signals and EEG. In particular, one of the main strengths of the study is the use of sophisticated computational modeling to capture phasic and tonic pain effects. The experiment codes are available on GitHub, increasing reproducibility.

Weaknesses:

As recognized by the Authors, there is no control condition involving an innocuous salient stimulus to rule out non-specific effects of distraction.

We thank the reviewer for their positive assessment of the study and for highlighting this remaining limitation. We acknowledge that, without an innocuous salient control condition, a nonspecific contribution of distraction cannot be ruled out. The Discussion retains this limitation and considers such a comparison as a direction for future work.

Reviewer #2 (Public review):

Summary:

The study investigated the distinct roles of phasic and tonic pain in adaptive behavior. Phasic pain was proposed to function as a teaching signal, promoting avoidance of further injury, while tonic pain was hypothesized to support recuperative behavior by reducing motivational vigor. This hypothesis was tested using an immersive virtual reality (VR) EEG foraging task, in which participants harvested fruit in a forest environment. Some fruits triggered brief phasic pain to the grasping hand, which in turn reduced the likelihood of choosing those fruits. Concurrently, tonic pressure pain applied to the contralateral upper arm was associated with reduced action velocities. The authors employed a free-operant computational framework to quantify how phasic and tonic pain modulate motivational vigor and decision value. Importantly, model parameters were found to correlate with EEG responses, providing neurophysiological support for the hypothesized functional distinctions.

Comments on revised version.

All my comments have been well addressed.

We thank the reviewer for reviewing the revised manuscript and for confirming that their comments have been addressed.

Reviewer #3 (Public review):

Summary:

This study investigates how phasic and tonic pain modulate behaviour in a free-operant foraging paradigm. The authors apply a computational modeling approach to the behavioural data to quantify the decision value of phasic pain, as well as the degree to which tonic pain reduces motivational vigour. EEG assessments showed, e.g., reduced signal power at alpha and beta frequencies in tonic pain conditions compared to no-tonic-pain conditions, but no association between these neural measures and motivational vigour. The authors conclude that tonic and phasic pain serve different motivational functions, with phasic pain acting as a punishment signal promoting avoidance and tonic pain reducing motivational vigour.

Strengths:

The experimental paradigm is highly innovative. Assessing human behaviour in a naturalistic yet highly controlled setting represents a promising approach to pain research. Notably, assessing pain magnitude implicitly, via its motivational value, offers insights about the overall pain experience that are not usually accessible via common pain ratings.

We thank the reviewer for their assessment of the paradigm and its potential to complement conventional pain ratings. We also appreciate their further recommendations, which we address individually below.

Recommendations for the authors:

Reviewer #3 (Recommendations for the authors):

Overall, the manuscript has improved substantially and is now considerably clearer.

The following comments refer to the numbering of my previous review comments:

(2) If C_m is a unit vector with components h and v, these components are necessarily interdependent and therefore should not be treated or presented as independent variables.

We agree that these components are interdependent. We have corrected and clarified the description of the implemented parameter constraints. In Experiment 1, the fitted movement coefficient vector is normalised jointly with the pain coefficient, such that |C_p|+sqrt(h^2+v^2)=1; describing C_m itself as a unit vector in this experiment was therefore inaccurate. This constraint fixes an otherwise arbitrary common scale: multiplying C_p and C_m by the same positive constant leaves the predicted choices unchanged. We have corrected the definition and distinguished the searched parameters from the derived coefficient C_p in the Experiment 1 model-properties table.

Experiment 2 uses a different parameterisation: C_m is a non-negative unit vector, with h fitted and v=sqrt(1-h^2) derived. The separate vigour coefficient C_v scales the movement cost, and unit length removes the redundant scale between C_m and C_v. The average reward parameter 𝑅̅ is fixed at 1 during fitting to set the overall value scale, with C_p and C_v fitted separately. We have made these constraints explicit in the Experiment 2 model properties table and corrected its list of fitted parameters so that h and v are not presented as separately fitted parameters.

We apologise for the inaccurate description in the previous version of the manuscript and thank the reviewer for helping us identify and correct this issue.

Regarding possible concerns on statistical results involving these interdependent variables: The comparison in panel D of the Experiment 1 behaviour and modelling figure uses a two-sided paired t-test, equivalent to a one-sample test of each participant's difference h-v against zero. It does not require independence between the two components within a participant: the independent units are the participant-level differences. Following the eye-tracking exclusions described below, 20 participants contribute one difference each, giving 20-1=19 degrees of freedom. The within-participant normalisation constraint does not require a further reduction in these degrees of freedom.

We have revised the panel D caption to identify the paired test and the contrast h-v explicitly. After the eye-tracking exclusions, the updated result is t(19)=6.37, p<.001, compared with t(23)=6.72, p<.001 in the reviewed version. The qualitative conclusion remains: the fitted penalty is greater for vertical than horizontal movement.

(5) It is still not full clear to me, what the SCR analysis adds. The central argument appears to be that the relationship between decision values, pain ratings, and SCRs varies across contexts (e.g., target fixation versus painful stimulation), and that SCRs therefore capture distinct aspects of the pain experience. However, this interpretation seems to assume that SCRs measured in different contexts are established markers of separable dimensions of pain experience, which I do not find sufficiently justified.

We have revised the manuscript to distinguish the motivation for the SCR analysis, what the present evidence establishes, and the direction it motivates for further investigation. Our original question remains: what does a pain decision value estimated from choices capture about pain, and how does it relate to subjective ratings? Their correlation does not resolve whether they reflect the same aspects of pain's aversiveness or whether choice-derived values provide additional information. We introduced SCRs as a complementary physiological measurement through which to investigate this question. This rationale is now stated explicitly at the beginning of the revised SCR Results subsection, “Skin conductance responses and the interpretation of pain decision values”.

The two event contexts were chosen because of their roles in the task. Fixation on pain-associated fruit can accompany evaluation of an anticipated cost, whereas shock delivery accompanies receiving the painful stimulus. Comparing physiological associations at these stages offers a way to investigate the relationship between prospective valuation and subsequent pain experience. We agree that event timing alone does not establish either SCR response as a selective marker of a separate dimension of pain. Establishing whether these physiological responses can distinguish aspects captured by ratings and decision values is an empirical objective of this line of research.

The revised analyses do not resolve that distinction. The shock–rating association was the only association consistently supported across both experiments by the primary analysis and both sensitivity specifications. Associations involving decision values provided a less consistent pattern. We have therefore removed the double-dissociation interpretation that was added in the previous version and clarified that separate significance tests do not demonstrate differences between associations; inconclusive findings likewise do not establish equivalence between ratings and decision values. The accompanying timing, eye-tracking and SCR-estimation changes are described under Additional Changes below.

These findings refine the next question without removing the original motivation. The revised Discussion advocates combining subjective reports, choice-based models and physiological measurements to quantify where these measures converge and where they may capture distinct aspects of pain's aversiveness. In our view, future work should directly test differences between their associations and establish the functional interpretation of the physiological responses. We have revised the Results, Methods, figure caption and Discussion to make this progression from rationale, through current evidence, to future investigation explicit.

(8) I think the manuscript should state more explicitly that the assumption that "motivational vigour in a free-operant task can be quantified through an RL framework" is, in fact, a modelling assumption. While this is an interesting and promising approach, the interpretation of the model parameters depends critically on the validity and adequacy of the underlying model.

We agree that the modelling assumption should be explicit. Our aim is to provide a quantitative operationalisation of motivational vigour within a framework relating choices to movement costs and the opportunity cost of time. Movement speed and collection rate describe the behavioural expression of effort and pace, whereas C_v quantifies the weighting of vigour-related movement costs in the choice model. The model gives this quantity a precise mathematical role; interpreting it in motivational terms depends on the validity and adequacy of the framework for the task. We have revised the Discussion to explain this rationale and make that dependence explicit.

The Discussion now states: “We use motivational vigour here for the regulation of effort and pace in goal-directed behaviour, informed by accounts of competing motivations in pain (Fields, 2006). Movement speed and collection rate describe its behavioural expression, while the fitted C_v provides a choice-based operationalisation of vigour-related movement costs. Its motivational interpretation is a modelling assumption that depends on the validity and adequacy of the model; neither approach uniquely identifies motivation.”

We have also examined how well the observed choices constrain this operationalisation. The new fit profiles show that different parameter combinations attain the same minimum prediction error. Within the searched grid, equally optimal fits permit mean tonic-minus-no-tonic C_v contrasts from −4.48 to +31.74, showing that the fitted contrast, including its direction, depends on selection among optima. These are sensitivity bounds, not confidence limits. We retain the first encountered joint minimum as a reproducible reporting convention with a heuristic rationale that C_v estimated from choice trade-off is often bounded below rather than above in this foraging paradigm, and explicitly disclose its limitations in the Results.

This analysis motivates further work on both the estimation of model-based vigour and its relationship to behavioural measures. The revised Discussion proposes richer choice sets to constrain individual C_v estimates more closely, while recognising the additional search, memory and planning demands such tasks may introduce. The objective is to strengthen quantitative tests of how pain regulates effort and pace, and to establish how different operationalisations contribute to that understanding.

Additional changes made to the manuscript

Eye tracking data issue

We identified an acquisition failure in which an asynchronous eye-tracking callback stopped updating, while Unity continued ray casting with stale gaze data marked as valid. Four participants per experiment were excluded from eye-dependent analyses when an identical gaze-direction vector occurred in more than 100 frames (not necessarily consecutive) within any analysed 60-s block, leaving 20 and 27 participants, respectively, before any further analysis-specific quality exclusions. Independent Experiment 2 analyses of ratings, choice probability, whole-block hand speed and collection rate retain 31 participants; the fixation-selected reaching-trajectory analysis uses 27. The main manuscript now declares the eye-tracking exclusions. The new supplementary section, “Eye tracking methods and generation attempt”, details acquisition and quality control, exploratory HAGI gaze generation, and replay limitations. Generated data were not used to reinstate excluded participants.

SCR and EEG clock synchronisation

We added affine clock corrections to improve the alignment of SCR and EEG recordings with task events. The Methods now refer readers to the new supplementary section, “Clock synchronisation”, for the procedures, diagnostic figures and limitations.

SCR estimation and sensitivity analyses

Alongside the clock-synchronisation corrections and eye-tracking exclusions, we revised the SCR analyses to retain eligible block-level coefficients irrespective of their first-level statistical significance. A nonsignificant coefficient remains an uncertain estimate; selecting coefficients according to their significance can distort subsequent association analyses. The primary analysis therefore includes these estimates without significance-based selection. Supplementary inverse-variance models using metafor and brms incorporate differences in coefficient-estimation precision using heteroskedasticity- and autocorrelation-consistent (HAC) sampling variances, while allowing participant variation and additional block-level heterogeneity. These analyses assess whether the conclusions depend on how estimation uncertainty is handled. The specifications and results for both experiments are reported in the new supplementary section, “Skin conductance sensitivity analyses”.

Uncorrelated random effects model

We have clarified in the Methods (“Statistical Analysis”) that, when singular fits occurred within an analysis block, we used a no-correlation structure for the entire block of analysis, including otherwise nonsingular fits, while retaining all subject-level intercepts and random slopes included in the original specification. This applies to SCR models, EEG channel-wise fits and permutation batches. The supplementary “Linear mixed model outputs” section now includes “Maximal and no-correlation fits”, comparing the choice-distance and SCR analyses on identical observations and reporting slopes, confidence intervals, test statistics and singularity classifications for both specifications.

Cluster permutation tests

We added cluster-based permutation tests to the main manuscript alongside the existing electrode-wise Bonferroni correction and updated the channel-wise EEG results following the analysis revisions. The tonic-pain alpha cluster survives cluster correction (p=.006), although none of its individual electrodes survives Bonferroni correction. The beta association does not survive cluster correction. For fitted vigour constants, the alpha association at Pz survives Bonferroni correction (p=.042) but does not reach the cluster-corrected threshold (p=.059). The Results and Discussion now distinguish these outcomes and present the neural associations cautiously, without treating them as uniquely identifying a motivational mechanism.

Event-related and induced responses to phasic pain

In the previous version, the analysis labelled as induced oscillatory responses calculated total event-related power without subtracting the evoked response. We have revised the supplementary section to present both total-power results and induced-power estimates obtained by subtracting each participant’s condition-specific ERP before time–frequency analysis. The induced high–low phasic pain contrast was significant without tonic pain (cluster p = .0001) but not with tonic pain (smallest cluster p = .1925). Direct comparisons between tonic conditions were nonsignificant. We additionally tested the tonic-by-phasic intensity interaction on the baseline-normalised log-power scale; no significant clusters were identified for either total power (smallest cluster-level p = .8382) or induced power (smallest cluster-level p = .1575).

Interpretation is limited by unequal and sometimes sparse high-pain trial counts (3–49; mean 15.48, sample SD 10.06 across 62 participant-by-tonic-condition counts from 31 participants). The free-operant design allowed participants to avoid high-pain outcomes, and ERP estimates based on few trials may retain non-phase-locked activity and noise, limiting the separation of evoked and induced activity. We have added the following paragraph to the main-text Discussion:

“It is worth noting that, while we found no clear behavioural or ERP evidence that tonic pain modulated phasic pain responses, this does not establish that phasic pain processing is independent of tonic pain. Supplementary analyses identified a significant high-low phasic pain contrast in induced power without tonic pain but not with tonic pain; however, direct interaction tests were non-significant for both total event-related and induced power. These findings warrant caution because the free-operant task allowed participants to avoid high-pain outcomes, leaving limited and unequal high-pain trial counts. The subtracted ERP estimate may therefore retain non-phase-locked activity and noise, limiting the separation of evoked and induced activity.”

Type slug cleaning [00:05:27]

Typewriter Type Slug Cleaning Process, Pick Clean Clogged Faces, Restore Shine, Quickly<br /> by [[Duane Jensen]] on YouTube<br /> accessed on 2026-11-10T07:23:36

<br>This is an Annotation for Transparent Inquiry project, published by the Qualitative Data Repository.

Please cite as:

Stohler, Stephan; Ingram, Matthew. 2026. "Data for: 'The Effects of Judges' Institutional Interests on a Free Press'". Qualitative Data Repository. https://doi.org/10.5064/F6QK6YFW

Learn more about ATI here.

<br>AN2<br><br>Citation: Jucha & Żak v. Poland, App. No. 19127/06, Eur. Ct. H.R. (Oct. 23, 2012), https://hudoc.echr.coe.int/eng?i=001-113919.

Analytic note: The original article giving rise to the litigation appeared in the 28 January 2004 and 4 February 2004 issue of TEMI, a local weekly newspaper based in Tarnów, Poland. The first applicant, Dorota Jucha, was a staff journalist there; the second applicant, Tomasz Żak, was its editor-in-chief. The articles at issue formed part of a series of six pieces titled "Marek C. w epizodach" ("Marek C. in Episodes"), all written by Jucha. The Polish version of the article can be found in the ECtHR decision published in Polish, available via the URL provided above.

Source excerpt translation:

Marek C. in episodes

M.C. is certainly a colourful character. This Tarnów councillor, serving his third mandate on the municipal council, tried to become the President of Poland and a member of the Senate. Currently, he is involved in many court cases and is again becoming the subject of scandals.

Everyone remembers well that at the beginning of winter Councillor C. was involved in the eviction of two pregnant women from a flat located at ... Street in Tarnów. Everyone also remembers the explanation of C. who described one of the evicted women as running a shebeen and suggested that she together with her daughter were women of easy virtue. ...

People don't want to speak about C. And if they do, they speak about him as if he were dead – either well or nothing. Otherwise they risk to be taken to court and charged with defamation or breach of his personal rights. The list of persons who have met him in a courtroom is long and new names appear on it all the time. ...

For years the activity of M.C. has been based on balancing on the edge of the law, and even on breaking it. C. is most frequently accused of denigrating people and undermining their authority and of disseminating untruthful information about them. This includes information which suggests corruption links between people whom C. dislikes for reasons exclusively known to him. And that is how the articles and paragraphs of the Criminal Code which are being breached by councillor C. – without much notice on his part – proliferate.

Colleagues on the [municipal] council

People still don't want to speak about C. Are they afraid? Of what? Z.J., formerly for many years chairman of the Tarnów Municipal Council, refused to speak. Similarly, J.R., former mayor, did not want to say anything. (...)

However, A.K., the current chairman of the Municipal Board spoke:

"M.C. is a very touchy person, often he does not weigh his words. Even if a mild opinion is expressed about him, he still considers himself to be offended. At the same time he uses words which in the language of people with at least a minimum of good manners are considered inappropriate. I said already once to Mr C. that his character was not oriented on construction, but on destruction. (...)"

Mayor M.B. does not want to comment on councillor C.'s behaviour. He says that not because he is afraid, but because he thinks that there is nothing to comment on:

"Cooperation with this councillor is entirely out of the question. From his part there is only constant criticism, attack, and most frequently without any order, repetition of the same arguments. Mr C. criticises everything and all the time. ..."

Desk for the councillor

M.C. has ambitions and plans. He wants to become the President of Poland, or mayor of Tarnów, or a member of parliament. And if there are no elections, then he applies for the job of director of the Żabno Cultural Centre. There also without success. Everywhere and on every occasion he promises something. Up to now it would be difficult to find in his CV any positive achievements or just partial fulfilment of his various promises, including the electoral ones.

Sometimes C. attempted to get other "inferior" positions, compared to a chair in the presidential palace. For example, the mayor's plenipotentiary for the establishment of a university in Tarnów. It was being said that an agreement on the taking of this position by C. would be one possible way of calming the political excesses of the councillor. He did not get the position. Unofficially it was being said that similar arguments [were raised] when C. attempted to get another job, namely that of deputy head of the municipal police in Tarnów. This also failed. ... And could it be that his venomous aversion to the media, and in particular to the largest weekly in the region, is the result of its refusing his offer to become the editor in chief of the paper, or is that just a coincidence?

<br>AN4<br><br>Citation: Prager & Oberschlick v. Austria, App. No. 15974/90, 313 Eur. Ct. H.R. (ser. A) (1995).

Analytic note: The article at issue was published on March 15, 1987 in Forum, issue nos. 397/398, a Viennese periodical described in the proceedings both as "a publication dedicated to promoting democratic principles, the rule of law and the interests of indigents" and as "a typical magazine for intellectuals" (ein typisches Blatt der intellektuellen Szene).

Data source: HUDOC URL: https://hudoc.echr.coe.int/eng?i=001-57926</span>

<br>AN7<br><br>Citation: Hari Singh Nagra v. Kapil Sibal (2010) 7 SCC 502

Source excerpt: "The public image of the legal community is at its nadir. Influx of large numbers into the profession, deterioration of moral standards of the legal community questionable integrity of some of those who are in judiciary and the sheer economic cost of starting as a professional and sustaining one self have contributed to these falling standards.

"The judiciary, despite the above, provides a glimmer of hope for the common man. Those who adorn this institution, though tainted, have not yet lost all credibility. We have to all unite together to refurbish the image of the legal fraternity. Before we point fingers at others, let us do some soul-searching.

"For a start, let us concentrate on the junior members of the Bar. Our senior colleagues owe it to the profession to bring up the Junior Bar. This can never be done until junior members of the Bar have access to the chambers of senior lawyers. We must devise what I may call Voluntary Access Scheme: in terms of which the Supreme Court Bar Association should rotate junior members of the bar amongst the chambers of Senior Lawyers who voluntarily want to participate in this scheme. Access should be provided to at least one, if not two, junior members of the bar to each senior on the basis of rotation for 6 months at a time. This will give to the junior members the advantage of having worked with a variety of seniors. Of course, a minimum payment schedule must be part of this scheme.

"We must draw up a Code of Conduct applicable to the members of the Bar which will lay down norms not only in relation to their conduct with each other but also with reference to their conduct qua the Bench. Lawyers must refrain from shouting at each other, speaking in anger, threatening judges, threatening colleagues and the like. It is also necessary that procedures must be devised to ensure adherence to these norms.

"Entry into the profession should be limited to only those who pass an examination which may be conducted by the Bar Council of India. This, of course, requires legislation. Lawyers must get together, apply their mind to this issue and ensure the passing of this legislation.

"It seems that judges have started disciplining lawyers. Judges themselves need disciplining. The judiciary has failed in its efforts to eradicate the phenomenon of corruption. This phenomenon includes receiving monetary benefits for judicial pronouncements rendering blatantly dishonest judgments, kowtowing with political personalities and obviously favouring the Government and thereby losing all sense of objectivity. The legal community instead of publically denigrading judicial system should come forward with proposed legislation to deal with this issue. A committee must be set up by the Supreme Court Bar Association to look into the modalities of bringing about such legislation in the context of the present constitutional frame-work which provides complete protection to the judiciary.

"The issue of legal education must be addressed by the legal fraternity in cooperation with institutions providing legal education in India. Funding should be provided for studies to be conducted in such aspects of the law as required urgent attention.

"There must be greater interaction between the various Bar Associations in the country. Constant interaction will lead to exchange of information which, in turn, will enable all of us to attend urgently to the needs of the members of the legal profession.

"These are thoughts which require both immediate attention and a well thought of strategy. If we pause for a moment and think about what I have said, at least we will have made a start."

Analytic note: The case arose from a written message contributed by a Senior Advocate of the Supreme Court and a candidate for the Supreme Court Bar Association presidency, Kapil Sibal, to a publication created by an association of Supreme Court lawyers for publication in conjunction with its 1994–95 Annual Function. The publication was intended for internal distributed only, and contained contributions from, among others, the sitting Chief Justice of India and several Supreme Court judges. The publication was not sold to the public and not released to the press. But it made its way to the Times of India. It was published when Sibal submitted his candidacy for SCBA presidency.

<br>AN12<br><br>Citation: "Courts Are Established — For the People," Miami Herald, Nov. 2, 1944; "Why People Wonder," Miami Herald, Nov. 7, 1944, both reprinted in Pennekamp v. Florida, 328 U.S. 331, 336 n.4 (1946). The cartoon is taken from Scott D. Makar. 2017. "Free Press in 1940s Florida: Pennekamp v. Florida."" Journal of Supreme Court History 42(3): 295–313.

Source excerpt:

From "Courts Are Established — For the People:" "The seeming ease and pat facility with which the criminally charged have been given technical safeguard have set people to wondering whether their courts are being subverted into refuges for lawbreakers." . . . "[T]he defense got delay when it wanted and prompt decision from the court when it profited it."

From "Why People Wonder:" “Here is an example of why people wonder about the law’s delays and obstructing technicalities operating to the disadvantage of the state — which is the people — in prosecutions.

“After stalling along for months, the defense in the padlock case against the Brook Club appeared before Judge Marshall C. Wiseheart for a decision. The State Attorney was working with the grand jury. The court knocked out the injunction. There was speed, dispatch, immediate attention and action for those charged with violation of the law. So fast that the people didn’t get in a peep.

“That’s one way of gumming up prosecution. Another is to delay action. On March 29, Coy L. Jaggears, bus driver, was sentenced to fifteen days in city jail by Judge Cecil C. Curry on conviction of beating up a taxicab operator.

“The arrest precipitated the notorious bus strike. As a result, Jaggears walked out of jail after posting a $200 appeal bond. The appeal never got further.

“There you have the legal paradox, working two ways, but to the same purpose against prosecution. Speed when needed. Month after month of delay when that serves the better.”

Analytic note: The case arose from two editorials and a cartoon published in the Miami Herald in November 1944 by associate editor John D. Pennekamp, all directed at what the paper characterized as the systematic use of legal technicalities by the Circuit Court of Dade County to frustrate criminal prosecution. The first editorial, "Courts Are Established For The People," published November 2, 1944, alongside the cartoon, surveyed three pending matters involving rape indictments; the state's efforts to padlock a property; and a state injunction against a bookmaking operation. The editorial's core argument was that the judges were using procedural mechanisms to "subverted [the law] into a refuge for lawbreakers," with courts finding "every possible technicality of the law to protect the defendant" while the people's case was denied equal clarity of judicial vision. The second editorial, "Why People Wonder," revisited the padlock action more briefly: "After stalling along for months, the defense in the padlock case against the Brook Club appeared before Judge Marshall C. Wiseheart for a decision... The court knocked out the injunction. There was speed, dispatch, immediate attention and action for those charged with violation of the law. So fast that the people didn't get in a peep. That's one way of gumming up prosecution." The accompanying cartoon, drawn by Enright and captioned "But, Judge!," visualized similar accusations, depicting a judge ignoring the "PUBLIC INTEREST" while paying attention to a grinning figure labeled "DEFENDANT DISMISSED."

Data source: https://doi.org/10.5064/F6QK6YFW/JR1IMF

<br>AN9<br><br>Citation: Toledo Newspaper Co. v. United States, 247 U.S. 402 (1918)

Analytic note: The case arose from a franchise dispute between the City of Toledo and its street railway company, whose operating licenses were set to expire in March 1914. The railway company and its creditors sought injunctive relief in federal district court. The Toledo News-Bee, a local paper, sided with the city in an editorial and cartoon. In those materials, the paper challenged the court's authority to grant relief. The district judge, though admittedly after a long period, held the paper and its editor in criminal contempt for their publications, claiming that their publications tended to obstruct the administration of justice and undermine public confidence in the court. An image of an article is supplied here.

Data source: https://doi.org/10.5064/F6QK6YFW/HWP62G

<br>AN1<br><br>Citation: Roy, Arundhati (1999). “The Greater Common Good.” In: Outlook 16.11, pp. 1–38.

Source excerpt: "I had crossed the Narmada by boat from Jalsindhi and climbed the headland on the opposite bank from where I could see, ranged across the crowns of low, bald hills, the tribal hamlets of Sikka, Surung, Neemgavan and Domkhedi. I could see their airy, fragile, homes. I could see their fields and the forests behind them. I could see little children with littler goats scuttling across the landscape like motorized peanuts. I knew I was looking at a civilization older than Hinduism, slated -- sanctioned (by the highest court in the land) -- to be drowned this monsoon when the waters of the Sardar Sarovar reservoir will rise to submerge it."

"Why did I laugh?"

"Because I suddenly remembered the tender concern with which the Supreme Court judges in Delhi (before vacating the legal stay on further construction of the Sardar Sarovar dam) had inquired whether tribal children in the resettlement colonies would have children's parks to play in. The lawyers representing the government had hastened to assure them that indeed they would, and, what's more, that there were seesaws and slides and swings in every park. I looked up at the endless sky and down at the river rushing past and for a brief, brief moment the absurdity of it all reversed my rage and I laughed. I meant no disrespect."

Analytic note: The Supreme Court of India described the facts of the case as follows: "The respondent Arundhati Roy, who is not a party to the writ proceedings, published an article entitled "The Greater Common Good" which was published in Outlook Magazine and in some portion of a book written by her. Two judges of this Court, forming the three-judge Bench felt that the comments made by her were, prima facie, a misrepresentation of the proceedings of the court. It was observed that judicial process and institution cannot be permitted to be scandalised or subjected to contumacious violation in such a blatant manner, it had been done by her. The action of the respondent had caused the court much anguish and when the court expressed its displeasure on the action of the respondent in making distorted writing or manner in which leaders of the petitioner Ms.Meda Patkar and one Dharmadikhari despite giving assurance to the court acted in breach of the injunction, the Court observed:

"We are unhappy at the way the leaders of NBA and Ms.Arundhati Roy have attempted to undermine the dignity of the Court. We expected better behaviour from them."

Showing its magnanimity, the Court declared:

"After giving this matter our thoughtful consideration and keeping in view the importance of the issue of resettlement and rehabilitation of the PAFs, which we have been monitoring for the last five years, we are not inclined to initiate proceedings against the petitioner, its leaders or Ms.Arundhati Roy. We are of the opinion, in the larger interest of the issues pending before us, that we need not pursue the matter any further. We, however, hope that what we have said above would serve the purpose and the petitioner and its leaders would hereafter desist from acting in a manner which has the tendency to interfere with the due administration of justice or which violates the injunctions issued by this Court from time to time."

"The third learned Judge also recorded his disapproval of the statement made by the respondent herein and others and felt that as the court's shoulders are broad enough to shrug off their comments and because the focus should not shift from the resettlement and rehabilitation of the oustees, no action in contempt be taken against them." Roy republished her offending article on March 7, 2002, one day after the Supreme Court announced its decision.

<br>AN10<br><br>Citation: Johnson, "The Great Judicial Slaughter House and Mausoleum: The Lord High Executioner — 'Next!' ", Denver Rocky Mountain News, June 25, 1905, at 1, available via David Hosansky, Stolen Votes and Silenced Voices, History Colorado (Jan. 26, 2024), https://www.historycolorado.org/story/2024/01/26/stolen-votes-and-silenced-voices.

Source excerpt:

Analytic note: The case arose from a contested Colorado election for governor, where the Republican controlled legislature certified the Republican candidate as the electoral winner even though evidence existed of widespread fraud. Former U.S. Senator and owner of two newspapers (the Denver Rocky Mountain News and Denver Times), published a articles and a cartoon, as the U.S. Supreme Court put it, "intimating that the conduct of the court was unconstitutional and usurping, and alleging that it was in aid of a scheme, fully explained, to seat various Republican candidates, including the governor of the state, in place of Democrats who had been elected." The cartoon has been included here. It was drawn by an artist identified only as "Johnson" and published in the Denver Rocky Mountain News, with the caption "THE GREAT JUDICIAL SLAUGHTER HOUSE AND MAUSOLEUM. The Lord High Executioner — 'NEXT!'" It depicts the Colorado Supreme Court as a commercial butcher. The cartoon combines judicial ceremony with industrial killing, suggesting that the Colorado high court lacked any pretense of impartiality, while recasting its decisions as raw partisan butchery. The image embodied Patterson's charge that the justices were not adjudicating but executing a political program.

Data source: https://doi.org/10.5064/F6QK6YFW/C9BWOQ

<br>AN5<br><br>Citation: R. Rajagopal v. State of Tamil Nadu, (1994) 6 SCC 632

Analytic note:  An English language translation of Shankar's autobiography does not appear to exist. The depiction provided here is taken from para. 4 of the Indian Supreme Court opinion. This case involved a 300-page autobiography written by a condemned prisoner, Gauri Shankar (a.k.a. "Auto Shankar") while confined in Chengalpattu sub-jail during 1991 for a series of murders. The proposed publisher was Nakkheeran, a Tamil-language weekly magazine based in Madras. The petitioners before the Supreme Court were R. Rajagopal, the magazine's editor and publisher, and a second associated petitioner. The autobiography recounted facts alleging that senior government officials were his partners in crime, and that police officers suppressed investigations and obstructed complaints by victims’ families, who ultimately exposed Shankar's crimes.

<br>AN3<br><br>Citation: Lopes Gomes da Silva v. Portugal, App. No. 37698/97, 2000-X Eur. Ct. H.R.

Source excerpt: An unofficial Portugese version of the opinion containing quotations of the article is available the HUDOC URL: https://hudoc.echr.coe.int/eng?i=001-58817.

Source excerpt translation: "[the Chairman of the CDS/PP] has shown himself capable of exceeding even the most vulgar of caricatures ... This is clear from the CDS leadership's unthinkable choice of candidate to head the party's list in the Lisbon City Council elections. One need only read the extracts from recent articles by Mr Silva Resende in the Jornal do Dia which we publish in this issue to form an idea of the character being backed by the new Popular Party in the country's main city council elections. As ludicrous and grotesque as this will appear, it is nevertheless true. Not in the oldest or most delapidated ruins of Salazarism could an ideologically more grotesque and more buffoonish [boçal] candidate have been dug out: such an incredible mixture of crude reactionaryism [reaccionarismo alarve], fascist bigotry and coarse anti-Semitism. Any leading figure of the Salazar regime [Estado Novo] or any mayor of Lisbon from the former regime would come across as singularly progressive compared to this brilliant find ... It would all be merely an inconsequential anecdote or a surreal political oversight if it were not revelatory of a hidden facet which the CDS is trying to disguise behind the diaphanous veil of the modern Right. Incapable of finding a credible candidate for the Lisbon City Council, which is already symptomatic of the fragility of a party desirous of presenting itself as a possible party of government, the leadership of the CDS has resorted to a character who represents the most complacent, stale and ridiculous aspects of the Portuguese right-wing. A character who seems never to have really existed and that no humorist of however dubious taste would have been capable of imagining as the last of the Salazarian abencérages [salazarenta] in the 1990s. We presume that the young leader [of the CDS/PP] believes he has found, in desperation, someone capable of attracting at least football fans, which is the domain in which Mr Silva Resende has forged a remarkable career. It would appear that the majority of young Turks among the leadership of the CDS have contented themselves with reading Mr Silva Resende's football columns while remaining unaware of the rare pearls of his political beliefs...”.

“The bald-headed Jew [Mr L. Fabius] who spends his life, during his public appearances, militating in favour of secularism and the Republic (the two pillars of religious and patriotic impiety are sufficient in themselves to enable any reader of average intelligence to decode his real intentions) concluded after the elections that they [the socialists] were defeated because of their political practice and not because of their ideals.” (Jornal do Dia, 6 April 1993)

“The Clintons' past, and above all the style of their campaign for the Whitehouse, were very revelatory of a fresh conspiracy of the Left at its most deviant: war on the property of others, the cult of agnosticism, moral relativism, social hypocrisy, the inhuman secularism of life. To obtain an idea of the forces mobilised to catapult the Clintons to power, one need only mention that the Jewish lobby paid 60% of the electoral expenses whereas it represents only 5% of the electorate.” (Jornal do Dia, 16 April 1993)

“... Americans and Russians reached an agreement to inflict a blow on Portugal in Lisbon. We were betrayed by the United States, we were betrayed by NATO, which has placed a naval fleet at the gates of Lisbon in case their blow should fail.” (Jornal do Dia, 21 May 1993)

“It is no coincidence if politicians everywhere are involved in serious corruption. This moral chaos, which threatens to suffocate the world and leads to generalised perversity and attracts divine punishment, began several years ago when the machinery of ideological poisoning and agents of the propagation of error installed themselves comfortably everywhere, when they perverted youth, converting them to idols; when they tore women from the sanctuary of the home; when they flooded the world with their exhibition of vice; and, lastly, when they infiltrated political parties, placing them at the service of impiety.” (Jornal do Dia, 25 May 1993)

Analytic note: he article at issue was an editorial published in the June 10, 1993 issue of Publico, a major Lisbon daily newspaper with wide circulation. The editorial is notable for its density of invective.

<br>AN11<br><br>Citation: Sit-Strikers Convicted, L.A. Times, Dec. 21, 1937; The Fall of an Ex-Queen, L.A. Times, Apr. 14, 1938 (both reproduced in Bridges v. California, 314 U.S. 252, 274-77 n. 19, 20 (1941)).

Source excerpt:

The first editorial, entitled "Sit-Strikers Convicted," was published in the Los Angeles Times of December 21, 1937. The salient part read:

"Those were the days when Mrs. Werner was 'Queen Helen' and it is only fair to say that to her the power was much more important than the perquisites. When the inevitable turning of the political wheel brought new figures to the front and new bosses to the back, she found her grip slipping and it was hard to take. The several cases which in recent years have brought her before the courts to defend her activities seem all examples of an energetic effort to regain and reassert her onetime influence in high places. That it should ultimately have landed her behind the bars as a convicted bribe-seeker is not illogical. But if there is logic in it, the money meant less to Mrs. Werner than the name of still being a political power, one who could do things with public officials that others could not do. To herself at least she was still Queen Helen."

Portions of a telegram critical of local courts were also published January 24 and 25, 1938 were reproduced in Bridges v. California, 314 U.S. 252, 276-77 n. 20 (1941):

“This decision is outrageous considering I.L.A. has 15 members (in San Pedro) and the International Longshoremen-Warehousemen’s Union has 3000. International Longshoremen-Warehousemen Union has petitioned the labor board for certification to represent San Pedro longshoremen with International Longshoremen Association denied representation because it represents only 15 men. Board hearing held; decision now pending. Attempted enforcement of Schmidt decision will tie up port of Los Angeles and involve entire Pacific Coast. International Longshoremen-Warehousemen Union, representing over 11,000 of the 12,000 longshoremen on the Pacific Coast, does not intend to allow state courts to override the majority vote of members in choosing its officers and representatives and to override the National Labor Relations Board.”

Analytic note: Times-Mirror Co. v. Superior Court, consolidated into Bridges v. California, 314 U.S. 252 (1941), arose from two Los Angeles Times editorials published while criminal sentencing remained pending: "Sit-Strikers Convicted" (December 21, 1937), which appeared the day before sentencing of twenty-two convicted sit-down strikers and framed the court as the institutional guarantor of an anti-labor social order; and "The Fall of an Ex-Queen" (April 14, 1938), which constructed a complete moral biography of convicted political boss Helen Werner and declared it "not illogical" that she should land "behind the bars," seemingly pronouncing a sentence eight days before the court would announce its sentence.

<br>AN13<br><br>Citation: The Court drew from a series of articles that are supplied in an Appendix to Opinion of the Court in Craig v. Harney, 331 U.S. 367, 378–83 (1947).

Analytic note: The case arose from a series of newspaper articles and one editorial published in the Corpus Christi Caller-Times between May 26 and May 31, 1945, covering a civil dispute between a serviceman and a landlord over a lease option clause. The case was tried before County Judge Joe D. Browning. The factual reporting described how Browning had granted a directed verdict for Jackson without permitting argument from either side, confined the jury overnight when it twice refused to sign the verdict, and ultimately secured the jury's signature only after defense counsel Lewright advised the jurors that Browning had the legal power to jail them indefinitely. Some of the quotations from the articles are provided here, but the Supreme Court reprinted the articles in full in an appendix.

Source excerpts:

"At 7 p.m. Browning, without listening to argument from counsel for either side on a plaintiff’s motion presented by Dudley Tarlton for Jackson, and without giving the six-man jury opportunity to weigh the evidence, instructed the jury to find against Mayes."

“Browning accepted Tarlton’s one-page motion, and without permitting argument or citation of authorities to support the motion, ruled that it be granted. The effect of this ruling was that Browning took the matter from the jury.”

"That was the travesty on justice, the judge’s refusal to hear both sides. That’s where a legal background would have served him in good stead. It is difficult to believe that any lawyer, even a hack, would have followed such high handed procedure in instructing a jury. It’s no wonder that the jury balked and public opinion is outraged."

"True, the idea that only lawyers are qualified to occupy most public offices has been run into the ground, and in most instances a competent layman would be better qualified, but the county judge’s office is an exception. He should be a competent attorney as well as a competent businessman."

"It’s the tragedy in a case of this sort that the court where the controversial decision was handed down is the court of last resort. It’s too bad that appeal can’t be made to a district court and heard by a judge who is familiar with proper procedure and able to interpret and weigh motions and arguments by opposing counsel and to make his decisions accordingly . . . There is no way of knowing whether justice was done, because the first rule of justice, giving both sides an opportunity to be heard, was repudiated."

"Browning’s behavior and attitude has brought down the wrath of public opinion upon his head, properly so. Emotions have been aggravated. American people simply don’t like the idea of such goings on, especially when a man in the service of his country seems to be getting a raw deal . . . Then the plaintiff’s counsel offered a motion for an instructed verdict for his client. It was granted immediately, without having him cite his authority or without giving the defendant’s attorney a chance to argue against it."

<br>AN8<br><br>Citation: "A Direct Challenge to Police Chief Brunskill," Saturday Press (Minneapolis, Oct. 15, 1927, at 1), available at https://www.loc.gov/item/sn90060332/.

Analytic note: The arose from nine issues of The Saturday Press, a Minneapolis weekly tabloid published between September 24 and November 19, 1927 by Jay M. Near and Howard A. Guilford. The paper's stated mission was to expose organized crime and official corruption in Prohibition-era Minneapolis. One of the publishers, Guilford, had been shot (seemingly by Chicago gangsters), and both Near and Guilford alleged that Police Chief Frank W. Brunskill declined to formally investigate the attack. The paper's targets included Brunskill, Mayor George E. Leach, and Hennepin County Attorney Floyd B. Olson. Notably, the paper's journalism was filled with virulent antisemitism. A digitized version of the article can be accessed here.

<br>AN14<br><br>Citation: Steve Goldberg, "Hearing Held About Judge," Virginian-Pilot, Oct. 1979, at B1.

Analytic note: The case arose from the publication of a news article by Steve Goldberg in the Virginian-Pilot reporting on a confidential disciplinary proceeding before Virginia's Judicial Inquiry and Review Commission targeting Juvenile and Domestic Relations Court Judge H. Warrington ("Spike") Sharp. Virginia law made it a misdemeanor to disclose commission proceedings, and Landmark Communications was convicted and fined for the publication. The article itself was fairly straightforward. It identified the judge by name, described the two-day hearing at the Holiday Inn-Scope in Norfolk, noted that the charges appeared to concern general competence, and explained the commission's structure, procedures, and potential sanctions. The image provided is poor, but the legally relevant portions of the article are reproduced here. The legally relevant portions that landed the journalist in hot water was the first sentence, identifying the judge and the proceedings.

Source excerpt:

Hearing Held About Judge

By STEVE GOLDBERG Virginia-Pilot Staff Writer

"NORFOLK — A formal hearing concerning possible disciplinary action against Juvenile and Domestic Relations Court Judge H. Warrington (Spike) Sharp was held early last month.

The two-day hearing at Holiday Inn-Scope, conducted by members of the state Judicial Inquiry and Review Commission, apparently stemmed from charges of incompetence against the 55-year-old judge.

No formal complaint has been filed by the commission against Sharp, indicating either that the five-man panel found insufficient cause for action or that the case is still under review.

No commission member would say which is the case.

The review board is the state's most serious mechanism for policing judicial conduct. Its decision to press a formal complaint to the State Supreme Court could lead to retirement, censure, or removal from office."

<br>AN6<br><br>Citation: In Re: Harijai Singh, In Re: Vijay Kumar, (1996) 6 SCC 466.

Source excerpt:  "You should not be astonished if you find the names of two sons of Mr. Ahmadi, Chief Justice of India in the list of the discretionary quota."

Analytic note: The case arose from two news items published simultaneously on March 10, 1996, which included a captioned "Pumps for all!" in the English-language Sunday Tribune (Chandigarh) and a substantially similar Hindi-language piece in Punjab Kesari (Jalandhar), both written by the same journalist, Dina Nath Misra, a reporter of approximately four decades' experience. The items appeared while the Supreme Court was already addressing a matter challenging the Petroleum and Natural Gas Ministry's allegedly corrupt exercise of its discretionary power to allot retail petrol pump outlets and LPG dealerships. The articles, which appear in full in the legal opinion, alleged a pattern of nepotistic allotments by Petroleum Minister Capt. Satish Sharma, naming seventeen relatives of Prime Minister P.V. Narasimha Rao, two children of Lok Sabha Speaker Shivraj Patil, and "two sons of a Senior Judge of the Supreme Court." All three respondents admitted the falsity of the items, attributed the error to an unnamed but previously reliable source, and tendered unqualified apologies. The Court accepted them while directing front-page boxed retractions, characterizing Misra's conduct as "gross carelessness" incompatible with the professional standards of a journalist of his standing.

I think this quote shows that healing is not always just about treating something we can physically see. While plants can help with physical pain, they can also provide comfort and help someone feel better emotionally. What stands out to me is how Hazel understands that taking care of the body and taking care of the spirit are not necessarily separate things. Sometimes, the things that help us feel physically better can also give us a little strength when we are struggling internally.

I really like this way of looking at nature because it suggests that the woods offer much more than just physical resources. Nature can provide a sense of peace and comfort that is sometimes difficult to find elsewhere. I think Kimmerer is also reminding us that we have become so accustomed to looking for solutions through modern conveniences that we sometimes overlook the healing and wisdom that have always existed in the natural world.

Connects the physical shift of seasons to the sudden, overwhelming nature of sensory memory. The blooming plant acts as a bridge across time, showing how environmental cues can instantly pull buried emotional grief back to the surface.

Connects the physical shift of seasons to the sudden, overwhelming nature of sensory memory. The blooming plant acts as a bridge across time, showing how environmental cues can instantly pull buried emotional grief back to the surface.

I find the king’s decision to throw out Worcester only after he has finished speaking and Northumberland starts again to be quite interesting. If the king truly thought Worcester would be a problem during the discussion from the beginning, he would have interrupted him earlier in his lines. Instead, he waits until Northumberland starts to do so. I think both what Worcester said and Northumberland’s reaction pushed him over the edge in dismissing him, making the direction of this discussion important in any adaptation. The adaptation would have to capture the king’s observation of how the two act.

We discussed this in Lecture 22, 11/5/26.

Important words that are a part of totalitarinism

A regime that is rooted on negative emotions--obviously causes unrest

This is a large part of the perpetuality of totalitarinism---similiar themes in Orwell's novel.

a passive population that silently follows the regime whether they want to or not

Similiar to the Ministry of Truth in George Orwell's book

Examples of how a government can enforce a totalitarian regime

An ideology that is enforced upon the public against their will

eLife Assessment

This important study advances our understanding of how ongoing brain activity relates to people's choices about where to direct attention. While the evidence from the two independent datasets combining fMRI and EEG under the same willed-attention paradigm is solid, significant concerns remain regarding the rigor of the classifier analyses. This work will interest cognitive psychologists and neuroscience researchers.

Reviewer #1 (Public review):

Summary:

This study addresses a fundamental question in cognitive neuroscience regarding how the brain transitions from a reactive state of following external instructions to a proactive state of self-directed agency. The authors utilize an ambitious multimodal design by combining the spatial precision of fMRI with the temporal resolution of EEG across two independent datasets from the University of Florida and UC Davis. The work shows that while both instructed and willed attention engage the Dorsal Attention Network, willed choices additionally recruit a frontoparietal network including the dACC and anterior insula. By applying multivariate pattern analysis, the authors further demonstrate that the chosen direction of attention can be decoded from this network only on choice trials, and that pre-cue alpha patterns carry information predictive of subsequent spontaneous choices. This suggests a neural link between pre-existing brain states and intentional action, representing a significant technical effort to characterize the neural scaffolding of internal goal generation.

Strengths:

The primary strengths of this work include the integration of fMRI and EEG, which allows the authors to bridge the gap between slow metabolic signals and fast oscillatory brain states. The use of two independent cohorts is a commendable effort to ensure the reproducibility of the willed attention effect, which is often a concern in small-sample neuroimaging studies. Additionally, the move beyond univariate activation toward information-based mapping remains the strongest aspect of the work, as it shows that the identified network actually contains specific information about the direction of attention. However, the per-site decoding effects are modest and, in the UF dataset alone, do not survive correction (Table A1). The revision further adds permutation- and cluster-based inference, channel-subset and trial-balanced EEG decoding, and clearer methodological reporting, all of which improve transparency.

Weaknesses:

The revised manuscript addresses most of my earlier concerns, and the additional analyses improve the transparency of the work. The remaining points concern interpretation rather than the findings themselves. The decoding shows that the frontoparietal network carries the self-chosen direction of attention, but the present data do not establish the temporal ordering proposed in Figure 6. Similarly, the pre-cue alpha effect is consistent with a spontaneous brain-state bias, but without a measure of eye position or of when decisions are made, an oculomotor contribution or choices settled before the cue cannot be excluded. Finally, the link between pre-cue predictability and post-cue frontoparietal activity rests on a between-subject comparison, and the neural efficiency interpretation is one of several possible readings. Readers should weigh the proposed model with these limitations in mind.

Reviewer #2 (Public review):

Summary:

This manuscript combines fMRI and EEG investigations performed at two research sites to examine 'willed' or volitional visuospatial attention, as contrasted with more standard cued (or 'instructed') visuospatial attention. The primary findings are: 1) willed attention (vs. instructed attention) drives additional cortical circuitry across a broad fronto-parietal network; 2) the direction of willed attention, but not instructed attention can be decoded from the pre-cue EEG data and from MVPA analysis of the trial-level fMRI data; and 3) the subjects with high EEG decoding also exhibited high neural efficiency (i.e., high decoding with low BOLD signal change) in the fMRI data. There are significant concerns regarding the statistical rigor of the direction decoding analyses. These were incompletely addressed in the revision. These concerns are laid out in more detail below. Additionally, there is a concern over the degree to which the present research paradigm adequately examines 'willed attention,' which may mute the potential impact.

Strengths:

The focus on willed attention attempts to move beyond some of the many limitations of standard laboratory investigations of attention.

The shared paradigm across two modalities and two research sites demonstrates solid reproducibility, even though a few minor differences are observed across sites.

Weaknesses:

Major Concerns:

This revised manuscript addresses most of the concerns raised in the first set of reviews, however significant concerns still remain with regards to the 'multivariate analysis of cue-evoked BOLD activation' methods and results. This is central to many of the novel claims of this manuscript, therefore it is hoped that the authors will address this further. Two key concerns were raised by reviewers 2 and 3 about the decoding analyses reported in Figures 3 and 4. Although these concerns were addressed separately, both concerns impact both the fMRI and alpha power analyses but were not addressed within a single analysis for each data set. This appears to leave the critical decoding analysis results unresolved. The revised manuscript still states "For both datasets, decoding accuracy for the instructed trials was not significantly different from chance level (50%) for all the ROIs." However, the 50% level is not the appropriate comparison for statistical testing. Specifically, Figures 3 and 4 should be reproduced with analyses that include the appropriate corrections and controls.

There are 2 key issues: 1) Many individual subjects did not choose left or right at a 50-50 probability and these subject-level response biases provide a trivial means by which a classifier can perform above 50%; 2) Classifiers can 'perform above chance, by chance.' Empirical estimates of 'chance', generated by label swapping permutations are strongly recommended. Both issues are critical for both the MVPA and alpha power decoding analysis. In their supplemental materials of the revision the authors address point 1 for the alpha power decoding and point 2 for the MVPA decoding, but they do not address both issues together for either data set. This needs to be done if we are to believe the decoding results. Each concern appears to reduce classifier performance or significance; therefore, it is not clear which results would survive joint application of correction methods.

Figure 4: This reviewer (R2) raised concerns that individual subjects likely exhibited unequal numbers of right and left decisions, which would allow a simple classifier to perform > 50% by always guessing the biased direction. Figure A3a demonstrates that indeed many subjects exhibited biases in one direction or the other. The fact that these biases average out to close to 50% across the subject pool (Figure 3a) is irrelevant to the decoder analysis, which is performed at the individual subject level. The analysis presented for the alpha power decoding in Figure A3b addresses the imbalance by throwing out trials to balance the right/left decisions within subjects. This seems like a reasonable approach. The net effect is that the overall classifier performance drops from 56.83% accuracy to 52.81%, confirming that subject response biases were a large factor in MVPA performance. In support of the author claims, 52.81% performance is found to be significantly greater than chance in the combined data set (p=0.028). The results of this analysis should replace what is currently displayed in Figure 4, and also the contents of Figure A1. Since Figure 4 divides the data into site-specific results and into time courses, it is far from clear which of these results will remain significant.

Figure 3: The subject-level response biases are not addressed within the fMRI decoding analysis of Figure 3 but should be. Then the permutation analysis of Table A1 should be performed. Or an alternate approach could be taken that addresses both issues simultaneously. The results of the combined analysis should replace what is reported in Figure 3, which very likely overstates the effects.

Discussion: There are concerns about this experimental paradigm carrying the banner of Willed Attention, because the application of 'Will' appears quite modest. Yes, extra brain activity is exhibited for this condition vs. its control, but do the cognitive processes isolated adequately stand in for 'Willed Attention?" Willed attention, as operationally defined here, appears to involve a simple decision process prior to the shifting of spatial attention. In this revision, the authors have provided additional context that should aid future studies.

Reviewer #3 (Public review):

Summary:

This study uses two independent neuroimaging datasets to investigate the neural correlates of internally chosen spatial attention. The authors examine choice-related information in the frontoparietal regions and prediction of subsequent choices from the precue alpha patterns. They also examined the associations between precue predictability and postcue network responses. The revision and supplementary analyses improve methodological transparency and strengthen the evidence for precue alpha prediction.

Strengths:

The question is worthwhile, and the two independent datasets provide a useful assessment of consistency across sites. EEG and fMRI offer complementary information about precue activity and postcue spatial representations.

The revision clarifies ROI definitions and statistical testing, provides permutation-based fMRI results and effect sizes, and introduces cluster-based correction for the EEG time course. Importantly, precue alpha decoding remains above the empirical permutation baseline after balancing left- and right-choice trials within participants. This directly addresses the concern that individual choice biases could account for above-chance accuracy. Analyses restricted to posterior or frontal electrodes also support the conclusion that the predictive effect does not depend on using the full electrode set.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study addresses a fundamental question in cognitive neuroscience regarding how the brain transitions from a reactive state of following external instructions to a proactive state of self-directed agency. The authors utilize an ambitious multimodal design by combining the spatial precision of fMRI with the temporal resolution of EEG across two independent datasets from the University of Florida and UC Davis. By applying multivariate pattern analysis, the work demonstrates that while both instructed and willed attention engage the Dorsal Attention Network, willed choices uniquely recruit a frontoparietal decision network including the dACC and anterior insula. Furthermore, the study shows that pre-cue alpha oscillations can predict subsequent spontaneous choices. This provides a neural link between pre-existing brain states and intentional action, representing a significant technical effort to characterize the neural scaffolding of internal goal generation.

Thank you for the succinct summary of our work.

Strengths:

The primary strengths of this work include the integration of fMRI and EEG which allows the authors to bridge the gap between slow metabolic signals and fast oscillatory brain states. The use of two independent cohorts is a commendable effort to ensure the reproducibility of the willed attention effect, which is often a concern in small-sample neuroimaging studies. Additionally, the move beyond univariate activation toward information-based mapping demonstrates that the identified networks actually contain specific information about the direction of attention.

Thank you for the positive assessment of our work.

Weaknesses:

(1) However, several critical weaknesses must be addressed to support the fundamental claims made in the manuscript. There are significant behavioral differences in performance between the two sites, specifically regarding the UC Davis cohort exhibiting slower reaction times and lower accuracy compared to the UF group. These discrepancies suggest potential differences in subject populations or experimental environments that are not currently accounted for in the neural models. The fMRI analysis lacks temporal precision because the use of beta series regression collapses the complex BOLD response into a single estimate per trial. This loss of temporal information obscures the evolution of the decision process and makes it difficult to distinguish whether the identified patterns represent a truly spontaneous choice or a slow-building, pre-planned strategy.

The reviewer is correct to point out the quantitative differences in behavioral performance between the UF and UCD cohorts, with the UCD participants exhibiting slower reaction times and somewhat lower accuracy despite the use of the same willed‑attention paradigm and matched stimulus parameters. The exact source of these differences is not fully known, but one likely contributor is that at UF, EEG and fMRI were recorded simultaneously in a single session, whereas at UCD, EEG and fMRI were acquired in separate sessions, which may have affected overall task engagement and fatigue. To address this concern in our analyses, we (i) first examined each dataset separately, showing that the main qualitative findings (choice‑cue activation of the frontoparietal decision network, decoding of choice in frontoparietal regions, and precue alpha predictability of willed choices) replicate across sites, and (ii) then combined datasets only at a higher level (using meta‑analytic/summary‑statistic approaches) to increase statistical power while respecting site‑specific differences. We note the behavioral differences and emphasize the analysis strategy in the revised manuscript.

Regarding the temporal precision of the fMRI analysis, we agree that single‑trial beta estimates do not allow us to track the evolution of the decision process on a sub‑second timescale and thus cannot, by themselves, distinguish a truly spontaneous choice from a slowly developing pre‑planned strategy. Our fMRI analyses were designed to identify where willed versus instructed attention engage distinct control networks and encode decision‑relevant information, rather than to resolve the precise timing of decision formation. The temporal aspects of the decision process in this paradigm have been addressed in prior work using EEG (Rajan et al., 2018). In that study, we found that frontal theta oscillations serve as an index of decision‑making: for choice trials, a burst of frontal theta power emerged between approximately 400 and 800 ms after the cue, a pattern that was not present in instructed trials. In addition, using the onset of posterior alpha lateralization as a marker of attentional set implementation, we showed that in choice trials the deployment of the posterior attention set was delayed by about 400–500 ms relative to instructed trials. Together, these EEG findings suggest that the decision process takes place in the time period of 400 to 800 ms after the choice cue and the duration of the process is in the neighborhood of 400–500 ms, supporting the view that the decision about where to attend are formed during the cue–target interval, rather than being fully pre‑planned well in advance. We now discuss the temporal dynamics more explicitly in the revised manuscript.

(2) Furthermore, the EEG decoding approach utilized the entire topography of electrodes rather than a biologically motivated posterior region of interest. Given that alpha-mediated spatial attention is traditionally localized to parieto-occipital sensors, using the full electrode set risks the inclusion of non-neural artefacts such as microsaccades or muscle activity which can contaminate multivariate classifiers. The introduction of the neural efficiency metric also requires further validation as the current ratio is mathematically sensitive to small denominators in the BOLD contrast.

The reviewer’s point about the decoding topography is well taken. To assess whether our results depend on using the full electrode set, we re-ran the precue alpha decoding using only posterior parieto‑occipital electrodes (posterior ROI) and, separately, using only frontal electrodes (frontal ROI). In Figure A1, all three analyses (whole‑head, posterior‑only, and frontal‑only) yielded a similar pattern: for choice trials, decoding accuracies were reliably above chance, whereas for instructed trials, decoding accuracies remained at chance. Thus, the key qualitative effect does not depend on including non‑posterior channels.

We chose the whole‑topography approach because our question concerned distributed alpha patterns rather than strictly local effects. In particular, frontal structures such as dACC and DLPFC are known to monitor internal brain states and interact with posterior attention networks, making it plausible that both posterior and frontal channels can contribute to decoding the upcoming decision about where to attend. At the same time, we agree that artefacts are a concern in multivariate EEG analyses. In the present case, the decoding window is strictly precue. Given that instructed and choice trials are interleaved and subjected to identical preprocessing and artefact rejection procedures, it is unlikely that systematic differences in eye or muscle artefacts drive the choice‑specific decoding. We now report the posterior‑only and frontal‑only decoding results in the Supplementary Materials and comment on the result in the revised manuscript.

Regarding the neural efficiency metric, we agree that ratio measures can, in principle, be sensitive to small denominators. In the present data, the BOLD contrasts used in the denominator are significantly different from zero at the group level, and we interpret the neural efficiency metric as a descriptive summary of the relationship between decoding and BOLD responses rather than as a standalone biomarker. We now explicitly note this potential sensitivity and limitation in the revised manuscript.

(3) Crucially, the manuscript does not address the physiological implications of recruiting additional frontoparietal networks when behavioral performance remains identical across conditions. The activation of the anterior insula and dACC is frequently associated with increased autonomic arousal and effort. If the willed condition requires more extensive neural scaffolding to reach the same behavioral output as the instructed condition, it raises the question of whether this internal decision process is accompanied by changes in arousal levels. The authors should consider whether the lack of a behavioral tax is due to a compensatory increase in arousal, which could be reflected in the EEG data or pupil diameter if recorded, and potentially also in the amplitude of BOLD activity, which is being masked by the neural efficiency metric. Without an account of how the brain balances this increased computational demand without impacting behavioral performance, the functional significance of the willed attention network remains partially obscured.

We thank the reviewer for this comment, which prompted us to examine the behavioral and physiological data more closely for evidence of a compensatory arousal or effort mechanism.

Regarding behavior, Table 1 shows that choice trials are associated with longer reaction times but higher accuracy relative to matched instructed trials (choose-left vs. cue-left, choose-right vs. cue-right). These effects were not consistently significant across both measures and both sites (UF: RT p = .438, accuracy p = .012; UCD: RT p = .830, accuracy p = .292), so we interpret this pattern cautiously rather than as a fully established effect. Nonetheless, the direction of the pattern—slower but more accurate responses on choice trials—is consistent with a speed–accuracy trade-off associated with increased cognitive control, rather than with a straightforward behavioral cost of engaging the willed attention network. This supports the interpretation that additional recruitment of anterior insula and dACC may reflect increased effortful control that helps offset, rather than degrade, task performance.

Regarding physiological arousal more directly, pupillometry was not recorded in this study, so we cannot speak to pupil-based arousal measures. However, following the reviewer's suggestion, we examined the time course of occipital alpha power (averaged across O1, O2, and Oz, using 500-ms sliding windows in 20-ms steps, expressed as dB change from pre-cue baseline) as an EEG-based index of attentional/arousal-related engagement. In Figure A2, alpha suppression 600–1200 ms after cue onset was significantly stronger for choice trials than instructed trials in the UF dataset (p = .030), with a difference in the same direction, though not statistically significant, in the UCD dataset (p = .163). Stronger alpha suppression is generally taken to reflect greater cortical engagement/arousal, so this pattern is broadly consistent with the idea that willed attention trials involve a heightened engagement state relative to instructed trials.

Together, these behavioral and EEG results provide converging, though not uniformly robust, evidence that the additional frontoparietal (and salience network) recruitment associated with willed attention may be accompanied by a compensatory increase in effort/arousal-related engagement, which could help explain why behavioral performance is not impaired—and if anything trends toward improved accuracy—in the choice condition. We now include Figure A2 in the Supplementary Materials and note that direct physiological arousal measures (e.g., pupillometry) were not available in the present dataset and would be a valuable addition in future work directly designed to test this hypothesis.

Reviewer #2 (Public review):

Summary:

This manuscript combines fMRI and EEG investigations performed at two research sites to examine 'willed' or volitional visuospatial attention, as contrasted with more standard cued (or 'instructed') visuospatial attention. The primary findings are: 1) willed attention (vs. instructed attention) drives additional cortical circuitry across a broad fronto-parietal network; 2) the direction of willed attention, but not instructed attention can be decoded from the pre-cue EEG data and from MVPA analysis of the trial-level fMRI data; and 3) the subjects with high EEG decoding also exhibited high neural efficiency (i.e., high decoding with low BOLD signal change) in the fMRI data. The methods and data analysis are generally sound, and these results appear solid. On the negative side, it is not made clear how the present findings extend our understanding beyond prior published work from one of the senior authors. There are also three significant concerns regarding interpretation of the findings. One has to do with the causal interpretation of the pre-cue alpha EEG signal determining the direction of willed attention. The second concern is the degree to which the present research paradigm adequately examines 'willed attention.' The third is that the MVPA analysis is not sufficiently described, and Permutation testing needs to be done to validate these findings. Otherwise, this manuscript appears methodologically sound, but questions about interpretation may mute the potential impact.

Thank you for the succinct summary of our work. We address the concerns below.

Strengths:

The focus on willed attention attempts to move beyond some of the many limitations of standard laboratory investigations of attention.

The shared paradigm across two modalities and two research sites demonstrates solid reproducibility, even though a few minor differences are observed across sites.

Thank you for the positive assessment of our work.

Weaknesses:

(1) There are concerns about this experimental paradigm carrying the banner of Willed Attention, because the application of 'Will' appears quite modest. Yes, extra brain activity is exhibited for this condition vs. its control, but do the cognitive processes isolated adequately stand in for 'Willed Attention?" Willed attention, as operationally defined here, appears to involve a simple decision process prior to the shifting of spatial attention. The cue is internally generated, but after that the rest of the attentional processes appear identical to standard externally cued visuospatial attention experiments. This self-generated cue process likely involves some sort of memory/history of the recently selected cues and then some randomish selection between A and B. This appears very similar to asking the subject to guess whether a fair coin flip will be heads or tails on each trial. A mental 'coin flip' feels like a very weak version of 'will.' As a potential remedy, it would be helpful to discuss what other phenomena might fall within 'willed attention' and what some future studies might choose to focus on, along with some potential pitfalls (e.g., the reasons why the current study avoided more robust exemplars of will).

Thank you for this thoughtful comment about the implications of “willed attention” as instantiated in our paradigm. Our use of the term follows earlier work in this line of research, where attention that is endogenously directed in the absence of external attention‑directing cues has been referred to as “willed attention” (Bengson et al., 2014, 2015; Liu et al., 2017; Rajan et al., 2018; see also Nadra et al., 2023, for review). In these studies, and in the present work, participants are prompted to decide for themselves where to attend (left vs right) when a choice cue appears, rather than being instructed where to attend by an external cue.

We agree that, viewed from a broader perspective on “will,” this is a modest instantiation. The choice component can be described as a simple internally generated decision between two alternatives, and we do not claim that it captures the full richness of everyday volitional attention (e.g., spontaneously deciding what to attend, when to shift, or sustaining attention over longer time scales). Our aim here was to isolate, under tightly controlled conditions, the additional control processes that are engaged when the direction of spatial attention is chosen endogenously rather than specified by an external cue. The evidence we present— that the choice cue recruits a frontoparietal decision network, that choice direction can be decoded from this network only in choice trials, and that ongoing alpha patterns bias upcoming choices—speaks directly to this internally generated decision stage within the broader spatial attention framework.

We have revised the manuscript to emphasize the limited nature of our paradigm and discuss other phenomena that could fall under willed attention, such as self‑initiated shifts of attention without any external prompt, decisions about what feature or object category to attend, or self‑timed initiation and termination of attentional episodes, and moreover, we refer to the review by Nadra and Mangun (2023) where broader issues are discussed.

(2) The manuscript is lacking a description of the decision processes used during the willed attention paradigm and is lacking evidence as to WHEN subjects made their willed decision. Both of these points are of major concern:

These are important points. The temporal aspects of the decision process in this paradigm have been addressed in prior work using EEG (Rajan et al., 2018). In that study, we found that frontal theta oscillations serve as an index of decision‑making: for choice trials, a burst of frontal theta power emerged between approximately 400 and 800 ms after the cue, a pattern that was not present in instructed trials. In addition, using the onset of posterior alpha lateralization as a marker of attentional set implementation, we showed that in choice trials, the deployment of the posterior attention set was delayed by about 400–500 ms relative to instructed trials. Together, these EEG findings suggest that the decision process takes place in the time period of ~400–800 ms after the choice cue and it lasts on the order of 400–500 ms. We now explicitly discuss the timing of the decision process in the revised manuscript.

(a) The authors state: "For willed attention, participants were explicitly told to avoid relying on any stereotypical strategies of generating decisions, such as always attending the same/opposite side they attended during the previous trial, as well as to avoid randomizing or equalizing their decisions to choose left or right across trials; prior studies found that decisions to explicitly randomize decisions might invoke additional working memory related processes (Spence & Frith, 1999)." Subjects were instructed NOT to apply a simple heuristic and NOT to randomize or try to equalize their decisions, but exactly HOW the subjects made their decisions is not at all clear. What options does that leave? How does this strategy avoid the working memory-related processes mentioned in the Spence & Frith, 1999 citation? The brain regions that comprise the network of interest (aka Frontoparietal Decision Network) are activated by a very broad range of visual cognitive tasks, including many working memory paradigms. The Anterior Insula and dACC nodes Salience Network often simply reflect task difficulty. Obviously, making a choice is more cognitively demanding than not making a choice. The present experiments do not distinguish functional roles between different regions of the Frontoparietal Decision Network. On the whole, the study does very little to isolate the cognitive processes or neural bases of willed attention beyond calling out the set of 'Usual Suspects' for visual cognition.

These are important issues. The purpose of the instructions was to encourage subjects to make a genuinely spontaneous decision about where to attend on each choice trial, rather than relying on simple deterministic strategies (e.g., always alternating left/right) or explicitly trying to randomize or equalize their choices across the session. Spence and Frith (1999) pointed out that attempts to explicitly generate random sequences can recruit working memory and additional control processes. Our instructions were therefore designed to minimize both stereotyped patterns and explicit randomization strategies, and instead to encourage subjects to “go with their momentary choice” on each trial. While we cannot directly observe the exact decision rule each individual used, prior analyses of sequence structure in this paradigm (Bengson et al., 2014) found no evidence that first‑ or second‑order sequence effects (e.g., simple alternation or repetition biases) explained the pattern of choices, consistent with the idea that responses were not governed by a simple fixed strategy.

Regarding the frontoparietal network, prior work has indeed shown that the choice cue in this task activates regions such as dACC, DLPFC, anterior insula, and IPL (Bengson et al., 2015; Liu et al., 2017). We fully agree with the reviewer that these regions support a wide range of cognitive functions (including working memory, cognitive control, and task difficulty), and we do not claim to have dissociated all of these functions here. The contribution of the present work is to go beyond univariate “activation maps” by showing that: (i) multivoxel patterns in this frontoparietal network encode which spatial alternative is chosen on a given trial (left vs right) in willed attention, whereas no such information is decodable in instructed attention, and (ii) trial‑by‑trial patterns of precue alpha activity predict subsequent choices and frontoparietal activity. Together, these findings link this network not only to general task engagement, but specifically to the internally generated decision about where to attend in this paradigm. We have revised the manuscript to further clarify these points and emphasized that the component nodes of the frontoparietal network are not functionally decomposed in detail by the present study.

(b) The finding that pre-cue EEG signals predicted the post-cue decision is intriguing. It could mean that the seemingly irrelevant and transient state of the brain causally and unconsciously biased the subject to one direction or the other. Alternatively, it could mean that the subjects utilized the pre-cue period to make their decision and hold it in case it was needed (i.e., that it was a choice trial). While 2-8 seconds ITI variability makes sense for fMRI decoding, it is a long time for a subject to idly wait, so they might fill that time preparing for the next trial. There appears to have been a substantial amount of individual difference in the pre-cue alpha decoding, which could reflect individual differences in cognitive strategy, specifically in the use of the pre-cue period to make their decision. More efficient decision makers might have pre-decided, which might account for the neural efficiency. The experiments lack any measurement of WHEN participants made their decision. For that reason, I would ask that the authors temper their claims about the significance of the alpha decoding and its possible causality.

Thank you for this thoughtful comment. The two interpretations the reviewer raises—momentary brain state unconsciously biasing the upcoming choice versus subjects pre‑deciding during the inter‑trial period and holding that decision—are both, in principle, possible. Our design does not allow us to measure the exact moment at which each decision is made, so we cannot definitively rule out pre‑decision during the ITI. However, several considerations make a full “pre‑decide and hold” account less likely.

First, choice trials constituted only one third of all trials. Any decision formed and held throughout the pre‑cue period would have to be discarded on the majority of trials when an instruction cue appeared. This would impose a relatively inefficient strategy that we did not encourage. Second, if subjects were consistently forming decisions well before the cue and maintaining them, we would expect above‑chance decoding from alpha patterns earlier in the pre‑cue interval. Instead, see Figure 4B, only alpha activity in the last ~500 ms prior to the cue reliably predicts the upcoming choice; earlier windows do not show robust predictive information. This temporal profile is more consistent with a decision process that crystallizes in close temporal proximity to the cue rather than being stably maintained over the entire 2–8 s interval.

Regarding the broader temporal dynamics of the decision process, prior EEG work in this same paradigm (Rajan et al., 2018) showed that frontal theta activity specific to willed attention emerges 400–800 ms after the choice cue, and that the implementation of the posterior attention set (indexed by alpha lateralization) is delayed by approximately 400–500 ms in choice trials relative to instructed trials. Together, these findings place the main decision stage within the cue–target interval, rather than far in advance of the cue, and support the view that choices are formed spontaneously when the choice cue appears.

At the same time, we fully agree that the present experiments do not provide a direct measure of when each individual subject commits to a particular choice, and that alpha decoding alone does not establish a causal influence of precue brain state on behavior. In the revised manuscript we therefore temper our wording about the implications of the precue alpha decoding, explicitly describing it as evidence that ongoing brain state carries predictive information about upcoming choices.

(3) Did individual subjects exhibit a choice bias of location for the willed trials? If not, doesn't that raise concerns that subjects were trying to equalize their trials? If they do exhibit location biases, how does that impact the decoding? A simple decoder could learn to always just guess the biased direction for a subject and would perform > 50%. Consider the example in which an individual subject chooses 'Left' 55% of the time. A classifier that simply learns to choose 'Left' on every trial will be correct on 55% of trials. The training data would likely be sufficient to learn the direction of choice bias in each individual subject. So the classifiers could perform significantly above 50% without learning anything beyond the tendency of each subject. That is to say, 50% is not truly chance in this data set. It doesn't appear that Permutation testing has been performed to empirically determine chance for an individual's data. Permutation methods, scrambling the labels 1000 or 10000 times to establish a true baseline would be preferred over simply comparing to 50% and would address concerns about individual subject biases.

Thank you for this thoughtful comment. To address the possibility that individual choice biases might inflate decoding above 50% accuracy, we conducted additional analyses.

First, we examined whether subjects showed systematic left/right choice biases on willed trials. Figure A3A shows left/right choice proportions for each subject and dataset; dots indicate individual subjects’ percentages of left choices. Across the combined datasets, the mean proportion of left choices was 48.9%, which did not differ significantly from 50% (p = 0.581). At the individual-subject level, 10 of 31 subjects fell outside the 40–60% range, indicating that some degree of bias was present for a subset of participants, but that there was no consistent group-level bias toward one side.

Second, to test whether such biases might drive the decoding results, we repeated the precue alpha decoding after equating the number of choice-left and choice-right trials within each subject. We then performed 10,000 within-subject label permutations to obtain an empirical chance distribution for each subject and for the group. In Figure A3B, balanced decoding of 52.81% was significantly above the empirical permutation baseline decoding accuracy of 50.01% at p = 0.028, indicating that precue decoding remains significantly above chance after accounting for trial imbalance and subject-specific choice biases. We now include these results in the Supplementary Materials and describe them in the revised manuscript, and we explicitly state that decoding accuracy is evaluated against an empirical permutation baseline rather than assuming a fixed 50% chance level.

(4) The novel contributions of this work beyond the two prior Bengson et al papers from Dr. Mangun's lab appear quite modest. The discussion would be enhanced by specifically stating how the present work advances understanding beyond the prior Bengson studies.

The Bengson studies have indeed laid an important foundation for the present work, and we agree that it is useful to explicitly articulate how our study extends their findings. Below we highlight three main advances.

First, Bengson et al. (2015) showed that the choice cue in the willed attention paradigm activates a frontoparietal network, including regions such as dACC, DLPFC, and parietal cortex. In the present work, we replicate this activation pattern and go beyond it by using multivoxel pattern analysis to demonstrate that this network carries information about which spatial alternative is chosen (left vs right) on each willed attention trial. In other words, we attach the specific function of representing willed spatial decisions to this previously identified frontoparietal network, rather than only showing that it is engaged by the task.

Second, Bengson et al. (2014) reported that choice-left and choice-right trials are accompanied by different patterns of precue alpha lateralization. Here, we build on that result by showing, with MVPA decoding, that distributed patterns of alpha power in the precue interval systematically predict the subsequent choice, and by mapping the time course of this effect. Our decoding time-course analysis indicates that predictive information is confined to the final ~600 ms before cue onset, rather than being present throughout the entire inter-trial interval. This timing supports the interpretation that the decision about where to attend is formed relatively close in time to the cue, rather than being pre-planned early in the ITI and simply held until needed.

Third, we introduce a neural efficiency metric that links precue alpha decoding to postcue frontoparietal activation and decoding. This analysis shows that individuals with stronger precue alpha-based predictability of their choices tend to show more efficient (i.e., lower-amplitude yet still decodable) frontoparietal responses when implementing those choices. By relating ongoing brain state to subsequent decision-related network engagement, this provides a novel connection between spontaneous precue dynamics and the efficiency of the decision network that was not addressed in the earlier Bengson studies.

Taken together, these contributions extend prior work by (i) demonstrating that the frontoparietal network encodes the content of willed spatial decisions, (ii) showing that precue alpha patterns in a specific late time window bias those decisions, and (iii) linking these precue patterns to individual differences in the efficiency of decision-related neural responses. We further highlight these points in the revised manuscript to clarify the added value of the present study over the earlier Bengson et al. reports.

Reviewer #3 (Public review):

Summary:

This manuscript analyzes two independent datasets collected at different sites. Using the same willed-attention paradigm (instructional vs. choice cues) and combining fMRI and EEG analyses, the authors investigate how attentional direction is selected when no external instruction is provided. Their main claims are that the dorsal attention network is engaged by both cue types, whereas the choice cue additionally involves a frontoparietal decision network. Moreover, left-versus-right attentional decisions can be decoded in this decision network only on choice trials, and multichannel pre-stimulus alpha patterns predict the subsequent attentional choice. Finally, individuals with more predictive alpha patterns show greater neural efficiency in the decision network, i.e., higher decoding with lower BOLD activation.

The question is worthwhile and the two-site design is a genuine strength. At the same time, several central inferences rely on decoding analyses for which the statistical testing and cross-validation structure are not described in enough detail to assess robustness. In addition, using a ratio-based neural-efficiency measure make the interpretation more fragile than it needs to be. With a focused revision that tightens inference around MVPA and clarifies a few methodological points, I think the paper could become substantially more convincing.

Thank you for the succinct summary of our work and positive assessment. We address the concerns below.

Strengths:

The work extends previous willed attention studies by attempting to link pre-stimulus alpha pattern predictability to post-cue frontoparietal representations, and by testing reproducibility across two datasets. The conceptual advance beyond previous studies, e.g., Bengson et al. (2015), however, depends on how solid the decoding-based evidence is and whether alternative explanations are convincingly excluded. At present, the strength of support is limited mainly by incomplete reporting and/or controls for MVPA significance testing, as well as potential inflation of decoding estimates if folds are not independent of run structure. Concerns about statistical assessment of decoding accuracy are well documented in the literature (Combrisson & Jerbi, 2015).

Thank you for raising concerns regarding the analysis in the paper. We address these concerns below.

Weaknesses:

(1) The manuscript describes the decoding pipeline for both fMRI and EEG MVPA. However, it does not clearly specify how "significantly above chance" is determined for the fMRI ROI decoding, nor how multiple comparisons across ROIs are handled, even though p-values are reported. The same issue applies to the time-resolved EEG analysis across many time points. For each decoding analysis, please specify the inferential test (e.g., permutation test within participant, group-level test on subject accuracies, binomial test, etc.) and report effect sizes with confidence intervals (e.g., Combrisson & Jerbi, 2015). Further, for EEG decoding over time, it would be preferable to control family-wise error, e.g., cluster-based permutation, rather than thresholding pointwise p-values. A standard approach here is the nonparametric cluster framework (e.g., Maris & Oostenveld, 2007).

We thank the reviewer for this detailed and constructive comment. For the fMRI ROI decoding, each participant contributed one decoding accuracy value per ROI, obtained by averaging across cross-validation repetitions. In our original analysis, we tested whether decoding accuracy was significantly above the 50% chance level using group-level one-sample t-tests across participants, with FDR correction applied to control for multiple comparisons across ROIs. We now make this clear in the revised manuscript.

Following the reviewer's suggestion, we additionally performed a random permutation test for each ROI, following the approach of Combrisson and Jerbi (2015), and computed effect sizes. See Table A1 (now included in the Supplementary Materials), decoding accuracy in all 9 ROIs was significantly above chance at the combined-dataset level, with multiple comparisons controlled via FDR. We include this permutation-based analysis in the Supplementary Materials and comment on the result in the revised manuscript.

For the EEG time-resolved decoding, we followed the reviewer's suggestion and implemented a cluster-based permutation approach (Maris & Oostenveld, 2007) to control the family-wise error rate across time points. At each time point, decoding accuracy was compared against the 50% chance level using a one-sided dependent-samples t-test across participants. Consecutive time points exceeding an initial threshold of p < .05 were grouped into clusters, with cluster size defined as the number of consecutive significant time points. We then constructed a null distribution of the maximum cluster size using 10,000 sign-flip permutations and evaluated the observed cluster against this null distribution to control the familywise error rate. Using this approach, the cluster identified in Figure 4 was significant at pFWER = .008 at the combined-dataset level. We now report this cluster-based permutation result in the revised manuscript, along with the original analysis, in the revised manuscript.

(2) The cross-validation approach used here is appreciated and appropriate in principle. However, random 10-fold splits across trials can inflate accuracy if training and test folds share run-specific noise, scanner drift, or autocorrelated structure. The manuscript should indicate whether folds were blocked by run or randomized across the entire session. In addition, please report the number of trials per condition after artifact rejection and after removing short ITIs for the long prestimulus epochs (−2500 ms to 0 ms) for each dataset in the section of EEG preprocessing. Similarly, please report how often participants chose left vs. right on choice trials, and whether balanced folds (or an equivalent balancing procedure) were used if needed.

We thank the reviewer for this careful comment. To clarify, cross-validation folds were randomized across the entire session rather than blocked by run. We acknowledge that this approach could in principle allow training and test folds to share run-specific noise or scanner drift, which may inflate accuracy estimates relative to run-blocked cross-validation. In the revised manuscript, we note this as a limitation of our cross-validation scheme.

We have also added the requested trial-count information to the EEG preprocessing section, reporting the number of trials per condition after artifact rejection and after excluding short-ITI trials for the long prestimulus epochs (−2500 to 0 ms), separately for each dataset.

Regarding choice behavior, we now report the proportion of left versus right choices on choice trials for each dataset (see also our response to Reviewer 2's related comment on choice bias, where we found a group mean of 48.9% left choices, not significantly different from 50%). To address potential imbalance in individual subjects, we repeated the decoding analysis using trial-balanced folds (equating the number of left- and right-choice trials within each subject) and confirmed that the pattern of decoding results was consistent with our original analysis. This balanced-fold analysis is now reported in the revised manuscript.

(3) Moreover, ROI definition is not sufficiently specified and independence should be clarified. The ROIs are defined based on peaks from the choice-instructed univariate contrast (Table 2) and then used for MVPA. First, are these ROIs defined as spheres around peaks or using anatomical masks? What radius or voxel count was used? This needs to be explicit. Second, I am concerned about circularity risk. Although choice-vs-instructed selection is not identical to left-vs-right decoding, ROI selection from the same dataset can still bias descriptive estimates and encourage overinterpretation if not carefully justified (Kriegeskorte et al., 2009). At minimum, the authors should explain why their selection criterion is independent of the decoded contrast under the null, and ideally provide a robustness check using either anatomical ROIs or independently defined ROIs, e.g., from prior literature or an atlas.

We thank the reviewer for this comment. Regarding ROI definition, the ROIs were defined as 5-mm-radius spheres centered on peak voxels from the choice > instructed contrast; no anatomical masks were used. This is now stated explicitly in the revised Methods.

Regarding the concern about circularity, our ROIs were indeed defined using the choice > instructed contrast from the same dataset, and left–right decoding was subsequently performed within these ROIs. As the reviewer notes, this raises a general concern about "double dipping" (Kriegeskorte et al., 2009) whenever the selection contrast is not independent of the statistic used in the selective analysis under the null hypothesis. In our design, the choice–instructed contrast was constructed by collapsing across left and right trials within each condition, and was therefore driven by overall differences in activation magnitude between willed and instructed attention, not by the left–right spatial distinction that is the target of the decoding analysis. Under the null hypothesis of no left–right information in the multivoxel patterns, the mean activation level used for ROI selection and the spatial pattern used for decoding are distinct quantities: a region could show a large choice–instructed activation difference while carrying no left–right information whatsoever, or vice versa. This argues that the two statistics are not mechanically coupled, reducing the risk that ROI selection based on the former systematically inflates decoding accuracy for the latter. We have clarified this logic explicitly in the revised Methods.

Thanks for the comment. Regarding ROI definition, the ROIs were defined as spheres around contrast peaks, where the radius is 5 mm. No anatomical masks were used. This is now made clear in the revised manuscript. Regarding potential circularity in our ROI-based analyses, our ROIs were defined using the choice > instructed contrast from the same dataset, and we then performed left–right decoding within these ROIs. As the reviewer notes, this raises a general concern about “double dipping” (Kriegeskorte et al., 2009) if the selection contrast is not independent of the statistic used for the selective analysis under the null hypothesis. In our design, the choice–instructed contrast was constructed by collapsing across left and right trials within each condition and thus was sensitive to overall differences in activation between willed and instructed attention conditions, but not to the left–right distinction that is the target of the decoding analysis. Under the null hypothesis of no information about left vs. right in the multivoxel patterns, the choice–instructed contrast and the left–right decoding statistic are therefore orthogonal by construction, which reduces the risk that ROI selection based on the former will inflate the latter.

(4) Using an index of neural efficiency is conceptually interesting. However, if the denominator, computed as the activation difference between choice and instructional conditions, is near zero or noisy, the ratio can become unstable. I would rather see a multivariate model that treats activation and decoding as separate dependent measures, or a latent-variable approach, than a single ratio.

We appreciate the reviewer’s thoughtful comment. Our aim in using the neural efficiency metric was to provide an intuitively interpretable summary measure linking frontoparietal activation amplitude to decoding performance, but we agree that ratio measures can be problematic if not carefully evaluated. We also agree that more sophisticated multivariate or latent-variable approaches could provide a richer characterization of the joint relationships among activation, decoding, and behavior than a single ratio. Implementing and validating such models would, however, require additional analytic development that is beyond the scope of the present manuscript. We have therefore tempered our language when discussing neural efficiency, explicitly acknowledging the limitations of ratio-based measures and noting that future work could profitably apply multivariate or latent-variable modelling to more fully capture these relationships.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors should update Figure 2 to include a color bar representing t or z values and explicitly state the thresholding used for the maps. It is also essential that Figure 5B be updated to use identical scaling for both the UF and UCD subplots to ensure a transparent comparison of effect sizes across the two datasets. Regarding the statistical metrics, the authors should provide a sensitivity analysis or permutation test for the neural efficiency metric to ensure the ratio is stable and not driven by low variance BOLD denominators in the denominator of their calculation. A report of the univariate alpha asymmetry results is also recommended to validate that the multivariate patterns correspond to established raw alpha lateralization patterns in the posterior sensors.

We thank the reviewer for these comments. Figure 2 has been updated to include a color bar indicating t-values, and the figure legend now explicitly states the statistical thresholding used to generate the map (including the threshold value and correction method applied). Figure 5B has also been revised so that the UF and UCD subplots now use identical axis scaling, allowing for a transparent, direct comparison of effect sizes across the two datasets.

Regarding additional sensitivity analyses for the neural efficiency metric, our aim in using this metric was to provide an intuitively interpretable summary measure linking frontoparietal activation amplitude to decoding performance, and we agree that ratio measures can be problematic if not carefully evaluated. In line with Reviewer 3's related comment, we have tempered our interpretation of this metric in the revised manuscript and now explicitly describe it as an auxiliary, descriptive index rather than a primary inferential measure. We also note that more sophisticated multivariate or latent-variable approaches, as suggested by the reviewer, would provide a more rigorous characterization of the joint relationships among activation, decoding, and behavior, but that implementing such models is beyond the scope of the present study.

Regarding univariate alpha asymmetry, Bengson et al. (2014) have already shown that the alpha asymmetry pattern prior to the choice cue in this paradigm is consistent with established attentional modulation of posterior alpha lateralization. We now explicitly note in the revised manuscript that our multivariate precue alpha decoding builds on this prior univariate finding, and we cite Bengson et al. (2014) as providing the corresponding raw alpha lateralization results.

The methods section should be updated to explicitly state which TRs were used for the fMRI decoding and provide a justification for why a time-resolved approach was not utilized given the richness of the temporal data. Furthermore, the authors should provide a theoretical explanation for the observed behavioral parity between conditions. Specifically, it would be beneficial to discuss why the additional metabolic cost and recruitment of the willed network do not result in a behavioral tax such as slower reaction times or lower accuracy. This discussion should address whether the recruitment of the anterior insula and dACC might trigger an internal arousal shift or compensatory effort that allows the brain to maintain performance levels identical to the simpler instructed condition. Finally, the authors should clarify if site specific effects were modeled in their meta-analysis to account for the performance differences between UF and UC cohorts.

We thank the reviewer for these helpful suggestions. With respect to the fMRI decoding, we did not use TR‑level data. Instead, we modeled each trial using a single‑trial GLM and extracted one beta estimate per trial, which served as the input to the multivoxel pattern analysis. In other words, the decoding was performed on trial‑wise parameter estimates rather than on individual TRs. We have clarified this explicitly in the Methods. Because our primary question about temporal dynamics was addressed using EEG, we did not implement a time‑resolved fMRI decoding approach. We now briefly justify this choice in the Methods, noting that the richer temporal information from EEG was used to characterize time courses, whereas the fMRI analysis focused on spatial patterns at the level of trial‑wise responses.

Regarding the relation between behavior and insula/dACC activation, we agree that this is an important issue and have addressed it in detail in our response to Reviewer 1’s comment #2 in the Public View section above.

Finally, we did not model site‑specific effects in our meta‑analysis. We now state this explicitly in the Methods.

Reviewer #2 (Recommendations for the authors):

Copying key text from the above section:

(1) It would be helpful to discuss what other phenomena might fall within 'willed attention' and what some future studies might choose to focus on, along with some potential pitfalls

(2) If possible, state your understanding of what processes where engaged by the decision component of the Willed Attention trials.

(3) Discuss the timing of when subjects made decisions. Please temper claims about the significance of the alpha decoding and its possible causality.

(4) Re-run MVPA analysis with Monte Carlo Methods to rule out potential biases at the level of individual subjects and to more properly establish chance levels. That is, scramble the labels and run it at least 1000 times per subject to establish what chance actually is.

(5) The discussion would be enhanced by specifically stating how the present work advances understanding beyond the prior Bengson et al. studies.

We appreciate the reviewer’s detailed suggestions and have addressed each of the points (1–5) in our responses above. In the revised manuscript, we now (1) expand the Discussion to consider other phenomena that may fall under willed attention and potential future directions and pitfalls, (2) clarify our interpretation of the processes engaged by the decision component of the willed attention trials, (3) discuss the timing of decisions and temper our claims regarding the significance and possible causality of the precue alpha decoding, (4) add permutation-based analyses of the MVPA to better characterize empirical chance levels and potential individual-subject biases, and (5) explicitly articulate how the present work extends the prior Bengson et al. studies.

Minor Concerns:

(1) Introduction. I found this set of statements to be confusing. I ‘Think’Table 1 that the statement implies that several one-second intervals were examined. If so, changing 'sequential 1 sec period' to 'sequential 1 sec periods' would help to reduce confusion. "The previous study (Bengson et al., 2014) reported that the amplitude of left parieto-occipital EEG alpha power in the 1 sec period immediately before the unpredictable appearance of the choice cue predicted the decision about where to attend. How far does this alpha-based predictability extend before the choice cue? Bengson and colleagues (2014) investigated sequential 1 sec period prior to the choice cue, and reported no significant predictive value of the parieto-occipital alpha power earlier in time.

Thank you for pointing out this ambiguity. In the revised Introduction, we have clarified that Bengson et al. (2014) examined multiple sequential 1‑s periods prior to the choice cue, and we now use the plural “periods” to reflect this. We also rephrased the passage to more clearly distinguish their 1‑s windowed analysis from our finer‑grained time‑course decoding, which refines their result by localizing the predictive alpha pattern to approximately the final 600–700 ms before the cue.

(2) Methods - Neural Efficiency: The definition of 'Neural efficiency' appears to be novel. This is quantified by the difference in decoding accuracy (choice vs. instructional) divided by the difference in BOLD activation (choice vs. instructional). Was this Neural Efficiency measure pre-registered or only derived post-hoc? While this is an intriguing construct, it is not clear why this metric was chosen over simply looking at the numerator. Isn't fMRI decoding accuracy the more relevant measure to compare to EEG decoding accuracy?

We appreciate the reviewer’s careful comments on the neural efficiency metric. This measure was not preregistered; it was introduced post hoc as an intuitively interpretable, summary index relating frontoparietal activation amplitude to decoding performance. In defining it as the difference in decoding accuracy (choice vs. instructed) divided by the difference in BOLD activation (choice vs. instructed), our goal was to capture, in a single quantity, how much additional decodable information is obtained per unit increase in metabolic activity, in line with common informal uses of “neural efficiency” as doing more with less.

We agree that fMRI decoding accuracy alone is a highly relevant and more standard measure to compare with EEG decoding accuracy, and we do not claim that the ratio is superior to examining the numerator by itself. In the revised manuscript, we therefore (i) clarify that the neural efficiency index was exploratory and not preregistered, (ii) present the decoding results themselves as the primary inferential measure, and (iii) describe the ratio explicitly as a descriptive, auxiliary metric that combines activation and decoding in a way that is conceptually appealing but statistically more fragile. We also note that more formal multivariate or latent‑variable approaches, as suggested by the reviewer, would provide a more principled way to model the joint relationships among activation, decoding, and behavior, but that developing such models is beyond the scope of the present study.

(3) Methods - fMRI MVPA - which TRs from the trial were included in the MVPA analysis? All TRs following the onset of the cue? Does this include the actual deployment of spatial attention? Did any regions of the brain show effects for the instructed trials? One would think that even the univariate analysis would reveal right/left differences in dorsal attention network regions, including those in lateral frontal cortex.

We thank the reviewer for these insightful questions. With respect to the MVPA analysis, we did not operate directly on TR‑level time series. Instead, we modeled each trial with a single‑trial GLM, using a canonical hemodynamic response function aligned to cue onset, and extracted one beta estimate per trial. These trial‑wise parameter estimates, which summarize the cue‑evoked BOLD response over the relevant post‑cue TRs, served as the input to the multivoxel pattern analysis. In other words, the decoding was performed on trial‑wise beta images rather than on individual TRs. Because these betas reflect the cue‑locked response, they capture activity associated with the deployment of spatial attention following the choice or instruction cue.

Regarding effects in the instructed trials, the present work focused primarily on regions identified by the choice > instructed contrast, and on decoding within this willed attention network. The attention effects of instructed trials, including univariate contrasts between attending left and attending right in dorsal attention network regions and the visual cortex, are analyzed and reported in detail in Meyyappan et al. (2025). In the revised manuscript, we now clarify this focus in the Methods and refer explicitly to Meyyappan et al. (2025) for a treatment of lateralized attention effects in DAN and the visual system.

(4) Results: It is curious that RTs differed by ~100 ms across data collection sites. Could the authors offer an explanation for this difference? This doesn't seem critical for any of the paper's claims, but it is a large effect left unexplained.

The reviewer is correct to point out the quantitative differences in behavioral performance between the UF and UCD cohorts, with the UCD participants exhibiting slower reaction times and somewhat lower accuracy despite the use of the same willed‑attention paradigm and matched stimulus parameters. The exact source of these differences is not fully known, but one plausible contributor is procedural differences between sites: at UF, EEG and fMRI were recorded simultaneously in a single session, whereas at UCD, EEG and fMRI were acquired in separate sessions, which may have affected overall task engagement, familiarity with the task, and fatigue. We now comment on this site‑related behavioral difference in the revised manuscript.

Reviewer #3 (Recommendations for the authors):

Minors:

(1) The sample characteristics are somewhat imbalanced by sex in the UCD dataset. I am not suggesting that a gender analysis is essential, but this should be transparently reported and briefly noted as a limitation.

We appreciate the reviewer’s comment. In the revised manuscript, we now clearly point out the sex distribution of participants in the UCD dataset in the Methods section and explicitly note the resulting sex imbalance as a limitation.

(2) Please clarify whether any site differences in acquisition, e.g., TR, slice order, EEG montage, simultaneous vs. separate EEG recording, were modeled as moderators.

We did not model these factors as moderators. All datasets were acquired using highly similar acquisition protocols, and our primary analyses were conducted at the within-subject level, which reduces the impact of between-site differences. We now note this explicitly in the Methods.

(3) In several places the writing uses strong mechanistic language, e.g., "These results demonstrate that the network of frontal and parietal brain regions preferentially activated during willed attention is involved in deciding (choosing) the direction of attention (left vs. right)." Given the correlational nature of the evidence, I would suggest toning this down to "consistent with" unless stronger causal constraints are added.

The reviewer’s point is well taken. We have revised the manuscript to tone down mechanistic language, replacing strong causal statements with more conservative phrasing (e.g., “consistent with”) that reflects the correlational nature of our evidence.

References:

Rajan A, Siegel SN, Liu Y, Bengson L, Mangun GR, Ding M (2018). Theta Oscillations Index Frontal Decision-Making and Mediate Reciprocal Frontal–Parietal Interactions in Willed Attention. Cerebral Cortex 29(7): 2832-2843

Nadra JG, Mangun GR (2023). Placing willed attention in context: a review of attention and free will. Frontiers in Cognition 2: https://doi.org/10.3389/fcogn.2023.1205618

Bengson JJ, Kelley TA, Mangun G R (2015). The neural correlates of volitional attention: A combined fMRI and ERP study. Human Brain Mapping 36(7): 2443–2454.

Bengson JJ, Kelley TA, Zhang X, Wang JL, Mangun GR (2014). Spontaneous Neural Fluctuations Predict Decisions to Attend. Journal of Cognitive Neuroscience 26(11): 2578– 2584.

Liu Y, Hong X, Bengson JJ, Kelley TA, Ding M, Mangun GR (2017). Deciding where to attend: Large-scale network mechanisms underlying attention and intention revealed by graphtheoretic analysis. NeuroImage 157: 45–60.

Kriegeskorte N, Simmons WK, Bellgowan PSF, Baker CI (2009). Circular analysis in systems neuroscience: The dangers of double dipping. Nature Neuroscience 12(5): 535–540.

Combrisson E, Jerbi K (2015). Exceeding chance level by chance: The caveat of theoretical chance levels in brain signal classification and statistical assessment of decoding accuracy. Journal of Neuroscience Methods 250: 126–136.

Maris E, Oostenveld R (2007). Nonparametric statistical testing of EEG- and MEG-data. Journal of Neuroscience Methods 164(1): 177–190.

eLife Assessment

This study presents a helpful approach for systematically assessing the effects of disease-relevant 5′- and 3′-UTR variants on translation using massively parallel polysome profiling. The evidence supporting the ability of this method to identify variants that alter polysome association is solid. The work provides a valuable resource and methodological framework for investigating noncoding variants and will be of interest to researchers studying translational regulation and variant function.

Reviewer #1 (Public review):

The authors describe a massively parallel reporter assays (MPRA) screen focused at identifying polymorphisms in 5' and 3' UTRs that affect translation efficiency and thus might have a functional impact on cells. The topic is of timely interest, and indeed, several related efforts have recently been published and preprinted (e.g., https://pubmed.ncbi.nlm.nih.gov/37516102/ and https://www.ncbi.nlm.nih.gov/pmc/articles/PMC10635273/).

Comments on revisions:

The authors have now repeated the screen and collected new data that is high quality. From my perspective the manuscript has improved and I don't have any standing issues remaining.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

The authors describe a massively parallel reporter assays (MPRA) screen focused at identifying polymorphisms in 5' and 3' UTRs that affect translation efficiency and thus might have a functional impact on cells. The topic is of timely interest, and indeed, several related efforts have recently been published and preprinted (e.g., https://pubmed.ncbi.nlm.nih.gov/37516102/ and https://www.ncbi.nlm.nih.gov/pmc/articles/PMC10635273/). This study has several major issues with the results and their presentation.

Major comments:

The main issue remains that it appears that the screen has largely failed, and the reasons for that remain unclear, which make it difficult to interpret how useful is the resulting data. The authors mention batch effects as a potential contributor. The authors start with a library that includes ~6,000 variants, which makes it a medium-size MPRA. But then, only 483 pairs of WT/mutated UTRs yield high confidence information, which is already a small number for any downstream statistical analysis, particularly since most don't actually affect translation in the reporter screen setting (which is not unexpected). It is unclear why >90% of the library did not give high-confidence information. The profiles presented as base-case examples in Fig. 2B don't look very informative or convincing. All the subsequent analysis is done on a very small set of UTRs that have an effect, and it is unclear to this reviewer how these can yield statistically significant and/or biologically-relevant associations.

We recognize that RNA distribution within polysomes is inherently less stable than the associated protein components. This instability has been noted in previous studies, including those cited by the reviewer, which used RNA from bulk polysomes to infer the translatome without fractionation. Acknowledging this limitation, we purposely adopted a conservative strategy: (i) performing gross fractionation of polysomes, and (ii) collaborating with biostatisticians at the Institute of Statistical Science, Academia Sinica, to design a conservative yet optimized analysis pipeline that minimized batch effects.

To better illustrate the observed differences, we revised Fig. 2B to show the summarized proportions across fractions with error bars, allowing clearer visualization of the differences between genotypes.

From our high-confidence dataset, we applied a well-established statistical framework specifically designed to accommodate multiple influencing factors in relatively small datasets (Elements of Statistical Learning by Hastie, Tibshirani, and Friedman). We further conducted sensitivity analyses to select an optimal QC cutoff across a range of stringencies, ensuring maximal reliability of our results. We have therefore successfully shortlisted UTR variants which have strong effect on translation.

Building upon these conservative measures, we developed a predictive model for translation effects of UTR variants. Importantly, this model was validated not only with our internal test dataset but also with independent external datasets. In addition, the sequence features identified by the model were validated through reporter assays and in vivo CRISPR editing. These external and functional validations establish the generalizability and robustness of our approach.

From the variants that had an effect, the authors go on to carry out some protein-level validations, and see some changes, but it is not clear if those changes are in the same direction was observed in the screen. In their rebuttal the authors explain that they largely can not infer directionality of changes form the screen, which further limits its utility.

To determine the direction of polysome shifting, we repeated polysome profiling of the UTR libraries, separating transcripts into free RNA, 40S, and fractions containing 1–8 ribosomes (See Fig. 7A). Following established approaches, we used log₂ [polysome (F2–F8)/ (free + 40S)] as an estimate of translational efficiency. This measure showed a strong correlation with translational efficiency determined by luciferase activity normalized to RNA expression (Spearman r = 0.744; See Fig. 7B). We then used this measure to assign the direction of polysome shifting (increased or decreased) to the significant variants (Supplemental Table S4).

Because the contribution of 5’ UTRs to translation was more evident than that of 3’ UTRs, we further used the estimated ribosome load of WT 5’ UTR sequences to construct a multivariable model explaining variation in 5’ UTR translational efficiency (Fig. 7C). The model significantly explained ribosome load in held-out data and was further supported by independent reporter transfections, in which model-derived values correlated with luciferase output (Spearman r = 0.762; Fig. 7D, E).

We have modified the main text to describe these measurements and modeling analyses (p. 23–24):

“Modeling the polysome occupancy of 5’ UTRs

Because 5’ UTRs contain multiple features, including RBP-binding motifs and RNA folding energy, that may jointly influence translation, we next asked whether these features could explain variation in polysome occupancy. We performed high-resolution polysome profiling of the UTR library, separating transcripts into free RNA (Free), 40S, monosome (1 ribosome), and polysome fractions containing 2-8 ribosomes (Fig. 7A). We evaluated several metrics of ribosome association and found that the polysome fraction normalized to the free and 40S fractions [Poly/ (Free + 40S)] showed the strongest agreement with the change in translational efficiency between WT and mutant pairs measured using luciferase reporters (Spearman r = 0.744) (Figs. 3 and 7B). We therefore used this index as a quantitative measure of polysome occupancy and assigned the direction of occupancy change (increased or decreased) for each polysome-shifting variant (Supplemental Table S4).

To identify 5’ UTR features associated with polysome occupancy, we first selected representative features from highly correlated feature groups (for example, CG dinucleotide frequency and overall GC content) and then applied standardized multivariable regression to estimate their relative effects, statistical significance, and confidence intervals (see Methods). Of the 2,850 WT 5’ UTRs in the library, 2,362 passed the read-depth and quality-control criteria and were included in the model. The resulting model revealed positive associations of GC-rich k-mers with polysome occupancy. GA-repeat motifs recognized by SRSF-family proteins were also positively associated with polysome occupancy (Fig. 7C), consistent with their enrichment among polysome-shifting UTR variants identified independently in our variant analysis (Figs. 4 and 5).

The multivariable model significantly explained variation in the observed polysome occupancy (Fig. 7D, Supplemental Table S4). Moreover, model derived polysome occupancy highly correlated with luciferase activity measured independently across eight WT 5’ UTRs (Spearman r = 0.762) (Fig. 7E), providing functional support for the relationships captured by the model. Together, these results identify sequence and regulatory features associated with 5’ UTR-dependent ribosome loading and provide a quantitative framework linking UTR composition and RBP-binding motifs to translational output.”

The corresponding experimental and modeling details have also been added to the Methods section (p. 7-8 and 14-16).

It is particularly puzzling how the authors can build a machine learning predictor with >3,000 features when the dataset they use for training the model has just a few dozens of translation-shifting variants.

Starting with variants that passed our stringent quality-control criteria, we applied a statistical framework suited for evaluating multiple features in relatively small datasets (Hastie, Tibshirani, and Friedman, The Elements of Statistical Learning). We also systematically varied the QC threshold to assess the robustness of the results across different filtering stringencies. Importantly, the resulting findings were supported by independent reporter assays and further validated using an external dataset, demonstrating their reproducibility across experimental platforms and datasets.

Comments on revisions:

It appears that the authors have extracted the information they could from the problematic dataset they obtained. Repeating the experiments in a cleaner setting, obtaining data for the >6000 UTRs they intended will allow the authors to achieve the goals they set out to achieve in establishing the screen.

We appreciate the reviewer’s valuable comments. In response, we repeated polysome profiling of the UTR library. The repeated experiment not only reproduced the overall results of our initial screen but also provided additional information on the distribution of UTRs in the free RNA and 40S fractions. Using these data, we derived a polysome association index [Poly/ (Free + 40S)], which showed strong agreement with translational efficiency independently measured using individually transfected luciferase reporters. Together with the extensive additional analyses and revisions described above, these new data substantially strengthen the experimental foundation of our study and provide a more quantitative framework for interpreting the effects of UTR variants on translation.

We sincerely thank the reviewer for this constructive comment, which helped us improve the rigor and overall quality of the study.

eLife Assessment

This valuable study advances our understanding of how feature expectations influence visual perception and eye movements independently of presaccadic attention. The primary findings - showing that feature expectation and presaccadic attention modulate visual sensitivity through distinct, non-interacting processes - are supported by solid evidence from a carefully controlled factorial design and two psychophysical experiments. However, support for the proposed mechanistic interpretation is incomplete, as the experimental design does not fully distinguish expectation effects from stimulus repetition or separate expectation - related changes in eye-movement timing from stimulus-induced inhibition, and certain aspects of the statistical analysis and perceptual threshold procedures require clarification.

Reviewer #1 (Public review):

Summary:

Bortoluzzi and Rohenkohl investigated the interaction between presaccadic attention (PSA) and feature expectation. PSA refers to enhanced perceptual sensitivity or neural responses at the location of an upcoming saccade, and has been taken as evidence for (partial) coupling between spatial attention and the oculomotor system. Although its spatial component has been extensively studied, much less is known about how PSA interacts with feature processing, such as orientation or spatial frequency. This question is particularly interesting as some have proposed that PSA may contribute to visual stability across saccades.

In two psychophysics experiments, participants prepared a saccade to a cued location while a low-contrast grating, clockwise or counterclockwise, appeared either at the saccade target or the opposite location. One orientation was frequent (64%) and the other infrequent (16%), with 20% target-absent (catch) trials. Participants reported target presence and, when present, orientation. The authors found that sensitivity (d') was higher at the saccade target location, showing the well-known presaccadic enhancement. Surprisingly, sensitivity was lower for the high-probability orientation. Importantly, these two effects did not interact. Moreover, presaccadic enhancement increased with time, approaching saccade onset, whereas the low-probability advantage weakened. They also reported that saccade latency was prolonged for the low-probability orientation, an effect reproduced in a follow-up experiment. The authors conclude that PSA enhances perception independent of feature expectation, and additionally, feature expectation influences both perceptual sensitivity and oculomotor responses.

Strengths:

(1) The topic addressed here is important for understanding the nature of presaccadic attention (PSA), particularly how PSA interacts with feature processing. The factorial design allows a clear dissociation of the effects of PSA and feature expectation.

(2) The dissociation between PSA and feature expectation was examined in multiple ways. In addition to testing their overall interaction, the analysis of their temporal profiles provides further evidence that the two effects may reflect distinct processes. Several statistical analyses were also conducted to rule out differences in saccade latency as an explanation for the lack of interaction.

(3) The investigation of stimulus probability on saccade latency provides an interesting test of how feature information may influence oculomotor responses.

Weaknesses:

(1) The manipulation of feature expectation involves both goal-driven and stimulus-driven components. On one hand, participants were explicitly informed that one orientation was more probable throughout the experiment, which could potentially induce feature-based attention toward the more probable orientation. On the other hand, this manipulation necessarily resulted in greater exposure to one orientation than the other. This difference in exposure could potentially account for the lower sensitivity observed for the high-probability stimulus, through repetition suppression or longer-term sensory adaptation. If the feature-probability effect partly reflects such stimulus-driven mechanisms, its independence from spatially driven presaccadic attention may be less surprising. This interpretation warrants more discussion. More broadly, it remains unclear whether feature expectation would still be independent of PSA if expectation were manipulated in a way that better isolates the top-down aspect of the manipulation, or by manipulating feature-based attention cues.

(2) The effect of feature probability on saccade latency may be considered in relation to the broader literature on oculomotor interference. Previous studies have shown that visual events during saccade preparation can delay saccade initiation and even alter saccade trajectories. Although the present manipulation differs from classic findings, the interference (by the low-probability stimulus), if any, is presented at the target location. Even so, this literature may provide a framework for interpreting the latency effect. It would also be informative to examine whether feature probability affects saccade trajectories.

Importantly, the fact that stimulus probability affected saccade onset timing leads to the question regarding whether stimulus probability also affect manual reaction time, the interval between stimulus onset and the button press indicating the perceptual decision. It is important to rule out a potential speed-accuracy trade-off before concluding that stimulus probability affects perceptual sensitivity.

(3) The descriptions of the implementation of the 2-ADC model are very sparse, and largely delegate it to the reference of the original papers Sridharan et al., 2014 and 2017. I suggest that, to serve as a stand-alone paper, there should be more detailed descriptions about how the model was implemented, and how the d' and criterion were calculated from the full contingency table. I also have reservations, or uncertainty, regarding how the current experimental design can be directly fitted into Sridharan et al.'s original 2-ADC framework. In the original Sridharan et al. model, when the target is present, they consider a design where the "alternative" involves only one dimension with two mutually exclusive alternatives, which is target present at location 1 versus target present at location 2. This allows them to model the internal responses in a two-dimensional space, one dimension for one location (with possible extension to N locations/channels).

In the present study, the authors instead used the two orientation categories as the two ADC alternatives, which is in principle compatible with the feature-based extension discussed by Sridharan et al. However, the experiment is more complex, adding an additional dimension: the spatial location. Either orientation can occur at either of two locations, with target occurrences at the two locations being mutually exclusive. Thus, the complete stimulus space contains four signal states (High vs. Low probability orientation X 2 locations) plus target absence. That is, the sensory evidence that has to be considered includes four variables: oriH_loc1, oriH_loc2, oriL_loc1, oriL_loc2. It is presently unclear why and how this higher-dimensional problem is decomposed or reduced to a 2-ADC framework by assuming only the two orientations matter, while the location seems to be ignored. The authors should clarify the mapping from stimulus and response contingencies onto the 2-ADC model and justify their use of this framework.

One could potentially treat the two locations as two independent tasks and apply the 2-ADC framework separately to each location. However, this would require the two locations to be statistically independent, including allowing targets to be present at both locations. In the current design, the locations are coupled: target-absent trials require both locations to be empty, and the presence of a target at one location implies its absence at the other. Conversely, evidence that one location is target-absent increases the probability that the target is present at the other location (given the contingency described in Figure 1b). It would therefore be helpful for the authors to clarify the rationale for this design and justify the appropriateness of applying the 2-ADC model for estimating d' and criterion.

Reviewer #2 (Public review):

Summary:

This manuscript investigates a timely question concerning how expectations about visual features relate to changes in perceptual sensitivity that occur before an eye movement. The authors manipulated the probability of two target orientations while participants prepared a visually guided eye movement and measured both perceptual sensitivity and eye-movement behavior. They report enhanced sensitivity both for targets presented at the upcoming eye-movement goal and for low-probability orientations, with no interaction between these effects. Low-probability orientations additionally delayed eye-movement initiation when they appeared at the movement goal, but not when they appeared at the opposite location. A follow-up experiment reproduced the latency difference for targets presented at the movement goal.

The combination of perceptual and eye-movement measures is a strength of the study, and the reported effects are interesting. However, I think the interpretation of both the perceptual probability effect and, particularly, the eye-movement latency effect requires reconsideration. In its current form, the study provides solid evidence for effects of feature probability on perceptual sensitivity and eye-movement timing, but incomplete evidence that these effects reflect the proposed mechanisms.

Strengths:

The manuscript addresses an interesting and timely question by bringing together two areas that have largely been studied separately: expectations about visual features and changes in perceptual sensitivity associated with preparation of an eye movement. The experimental design allows the effects of feature probability and eye-movement direction to be assessed within the same task, and the authors complement their perceptual measurements with several measures of eye-movement behavior.

The main empirical effects are clear. The study reproduces the well-established enhancement of perceptual sensitivity at an upcoming eye-movement goal and demonstrates an additional effect of feature probability, with greater sensitivity for low-probability orientations. The observation that feature probability also relates to eye-movement latency is potentially particularly interesting. The authors additionally conducted a follow-up experiment specifically targeting this latency effect, and they use complementary frequentist and Bayesian analyses to quantify several of their key results.

Weaknesses:

A first concern is the interpretation of the feature-probability effect as an effect of expectation. The high-probability orientation was presented four times as frequently as the low-probability orientation. Feature probability is therefore intrinsically confounded with stimulus repetition and adaptation. Greater sensitivity for low-probability orientations could reflect enhanced processing of unexpected information, as proposed by the authors, but it could also arise from attenuation of sensitivity to the repeatedly presented high-probability orientation. The experiment convincingly demonstrates an effect of feature probability, but does not distinguish these mechanisms. This distinction is important for interpreting the effect specifically in terms of prediction or expectation.

My main concern regards the interpretation of the eye-movement latency results. The authors interpret the approximately 3-ms additional delay for low-probability features at the eye-movement goal in terms of an unexpected feature interrupting or updating the decision process underlying the prepared movement, which they describe as "oculomotor procrastination." However, a visual transient presented during eye-movement preparation is known to transiently inhibit eye-movement initiation. Stimulus-induced oculomotor inhibition therefore provides a more proximal alternative framework for the observed latency effects and is currently not considered. Indeed, the proposed description of newly arriving visual information briefly postponing movement release appears closely related to this phenomenon.

Relatedly, the spatial specificity of the probability effect does not necessarily establish that feature expectation selectively modifies the prepared action. Perceptual sensitivity is substantially enhanced at the eye-movement goal. Thus, the absence of a probability-dependent latency effect at the opposite location could potentially result from weaker processing of the stimulus there, whereas a better-processed unexpected stimulus at the eye-movement goal may produce stronger stimulus-induced inhibition. The authors show that the interaction remains after accounting for correct versus incorrect perceptual reports, but response accuracy does not equate to the strength of the underlying sensory representation across locations. This issue is particularly relevant to the authors' subsequent discussion of separate visual mechanisms for perception and action. The accumulator and dual-systems interpretations should, in my view, be reconsidered in light of the oculomotor-inhibition account.

An important related limitation is that the latency analyses compare trials in which the Gabor appeared at the eye-movement goal with trials in which it appeared at the opposite location. The finding that latencies are longer in the former condition therefore does not itself establish that presentation of the Gabor delayed eye movements. Experiment 1 includes target-absent catch trials, which could provide an informative baseline for determining whether target presentation itself produces a latency cost. Characterizing this effect is important for distinguishing the proposed account from stimulus-induced inhibition.

The interpretation of the temporal analyses also requires caution. Target presentation occurred at a fixed time after the eye-movement cue, whereas its timing relative to eye-movement onset was determined retrospectively by when the eye movement occurred. Critically, the manuscript itself demonstrates that target processing and feature probability alter eye-movement latency. The stimulus used to measure perceptual sensitivity can therefore alter the event relative to which its "presaccadic" timing is defined. Splitting trials separately within conditions avoids a simple imbalance of trials between temporal bins but does not eliminate this dependency. This is particularly relevant because estimates of the time course of perceptual sensitivity around eye movements are known to depend on the stimuli used to measure them. Consequently, the different temporal profiles reported for feature probability and presaccadic enhancement should be interpreted cautiously.

Finally, the visual stimulation itself is spatially asymmetric. A Gabor is presented at only one of the two possible locations before bilateral masks appear. Target onset therefore provides information about the location containing the perceptual signal and produces a visual transient at one location but not the other. This design makes it difficult to separate effects associated with presaccadic selection from differences in the visual input occurring at versus away from the eye-movement goal. A spatially balanced design in which visual stimuli appear simultaneously at both locations would provide a cleaner test.

Overall, the empirical findings are potentially valuable for understanding how learned feature probabilities relate to perception and eye-movement behavior. However, the present design does not uniquely attribute the perceptual effect to expectation rather than repetition-related processes, and the latency findings should be evaluated within the established framework of stimulus-induced oculomotor inhibition before stronger conclusions about distinct mechanisms for perception and action are drawn.

Reviewer #3 (Public review):

The manuscript "Dissociable effects of feature expectation on saccades and presaccadic perception" addresses an interesting and timely question. It asks whether expectations about upcoming stimulus features interact with presaccadic perceptual enhancement, or if feature-based expectations and saccade preparation influence perception and action through partly independent routes. The authors use a paradigm where saccade direction and the probability of target orientation are manipulated independently. The core finding is that perceptual sensitivity is higher at the saccade target and that sensitivity is increased for less expected feature orientations, but these two effects do not interact. Unexpected target features at the saccade goal do, however, produce longer saccade latencies, and this effect persists after accounting for perceptual reports and is reproduced in a second experiment.<br /> <br /> 

A big strength here is the design itself. By tweaking saccade direction and feature probability independently, the researchers directly tested whether expecting a feature changes how strong pre-saccadic enhancement is. They are careful about possible confounds, using ANCOVAs to control for saccade latency and endpoint accuracy, indicating that the main perceptual effects are not just due to timing or landing precision. Pre-saccadic enhancement gets stronger as the target nears saccade onset, while the perceptual peak for low-probability features is stronger earlier and fades as saccade onset gets closer.

Another positive point is the saccade-latency analysis. The finding that low-probability features push up latency when shown at the saccade target is pretty interesting. It hints that feature expectation can influence ongoing motor preparation even after a direction cue has instigated the motor plan. The generalized linear mixed-model approach is helpful, showing the location-specific feature-probability effect holds even after factoring in perceptual reports. The latency difference, roughly 3 ms in the model-adjusted estimates, is small, but it is statistically significant in the main experiment.

Trying to reproduce this latency effect in a second experiment adds value too. In that simpler setup, with very visible stimuli, no catch trials, and the target always at the saccade goal, latencies still came out longer for low-probability features. That suggests the effect is not wholly tied to the perceptual-report demands of the first study.


(1) The Experiment 2 bootstrap p-value needs clarification<br /> <br /> The authors resample latency values within each participant and condition, compute the median difference, and then average the participant-level differences. They do this 10,000 times and set the one-tailed p-value to the proportion of bootstrap iterations where the group difference is < 0. This bootstrap distribution is centered on the observed data, not on a true null distribution centered at zero. However, the proportion of bootstrap estimates {less than or equal to} 0 does not necessarily correspond to a conventional hypothesis-test p-value. Please clarify how pboot was calculated and why this approach provides valid frequentist inference for a null hypothesis of zero difference.

(2) The staircase procedure estimates a conditional detection threshold, not necessarily "50% detection performance"

The paper states that a 1-up/1-down staircase yielded 50% detection performance, but then says the staircase was updated using only the 48 signal-present trials, based on hits and misses. False alarms were not used to update the staircase.

Because the experiment includes signal-absent catch trials, this distinction is important. If false alarms are not included, the staircase is estimating the contrast tied to about 50% conditional detection when a target is present, rather than a true 50% threshold in a full signal-detection framework. The authors should clarify what they mean by "50% detection performance" and why this staircase approach is appropriate for calibrating the subsequent 2-ADC analysis.

This choice could directly affect the main perceptual finding-the sensitivity advantage (d′) for low-probability features. Since target contrast was fixed based on conditional hit rates (P("Present"∣Signal)) rather than a bias-free detection index (d′), the procedure might not guarantee that baseline sensitivity was equalized across conditions before the main task. If participants shifted their decision criterion (C) depending on feature expectation, or if not tracking false alarms biased the threshold estimate, the baseline could artificially inflate or distort the d′ differences between high- and low-probability conditions. The authors should address whether this staircase could be a potential confound for the main perceptual effects.

(3) Temporal analysis and its limitations

The timing analysis splits pre-saccadic timing into Early and Late conditions using a participant- and condition-specific median split. While simple, this reduces temporal resolution and can hide nonlinear or continuous relationships between timing and perceptual sensitivity. A continuous analysis of target offset relative to saccade onset, for example using regression or a mixed-effects model, could provide a clearer picture of the temporal dynamics. It might also reveal whether the apparent weakening of the feature-probability effect is gradual or concentrated in a specific pre-movement window.

(4) Absence of a significant interaction and Bayes factor

The lack of a significant interaction between feature probability and saccade direction is supported by a Bayes factor of about 3 in favor of the null. That is informative, but it should not be taken as definitive proof that the two mechanisms are completely independent. I would instead describe this as evidence against a substantial interaction under the tested conditions.

Author response:

We thank the Editors and reviewers for their careful reading of our manuscript and their constructive comments. We appreciate their positive assessment of our work and recognize the importance of the concerns they raise. In the revised manuscript, we will address the potential contribution of stimulus repetition and adaptation by introducing additional control analyses examining how preceding stimuli and responses influence perceptual reports. These analyses will help assess the extent to which recent stimulus and response history may contribute to our findings. Furthermore, we will provide a more detailed explanation and justification of the two-alternative detection-choice (2-ADC) model, including how sensitivity (d′) and response criteria were estimated from the stimulus–response contingencies. Additional methodological and statistical clarifications will address the staircase procedure and the calculation and interpretation of the reported bootstrap p-value in Experiment 2. The reviews also offer several suggestions for improving the presentation, terminology, and clarity of the manuscript. In particular, we will clarify our use of the terms “feature expectation” and “feature probability,” distinguishing the experimental manipulation from its interpretation in terms of expectation. Finally, we will revise the discussion of the latency results to incorporate the literature on oculomotor interference and stimulus-induced saccadic inhibition highlighted by the reviewers. A detailed response to the reviewers’ comments will accompany the revised manuscript.

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Reply to the reviewers

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Referee #3

Evidence, reproducibility and clarity

Summary

The manuscript describes an investigation into the 15q11q13 gene locus disrupted in Prader-Willi syndrome (PWS), with particular focus on the SNORD116-IPW-SNORD115 gene array. The study is presented in two parts: a phylogenetic investigation into the small nucleolar RNAs (snoRNAs) within the locus of interest, followed by the generation and analysis of a Snord116-Ipw-Snord115 mouse KO. The phylogenetic analysis of SNORD116 and its neighbouring SNORDs spanned 64 individual placental mammalian species, the most comprehensive analysis performed of this locus to date (to this reviewer's knowledge). Key findings from this were the high level of conservation of (most of) these SNORDs, and also the surprising variation in copy number of SNORD115 and particularly SNORD116 (which could vary between individuals of the same species). The study moves on to describe the generation of a Snord116-Ipw-Snord115 KO mouse. An overall phenotype consisting of poor growth coupled with metabolic and hormonal dysregulation, coinciding with (but not necessitating) increased lethality occurring shortly after birth. The authors explore ribosomal RNA modification using Nanopore direct RNA sequencing and show no significant differences between WT and KO whole-brain samples. They also detected no significant methylation of Htr2c mRNA in KO versus WT whole-brain samples. Furthermore, there were relatively few genes found to be significantly differentially expressed following transcriptomic analysis of various brain tissues, leaving the underlying mechanism behind the phenotype unclear. An Ipw-only KO mouse was also generated but showed no phenotype.

Major Comments

While the phylogenetic analysis of the SNORDs is impressively extensive, this reviewer has some concerns regarding the methodological approach taken. The authors state for SNORD115 and SNORD116, "functional conservation was inferred when at least one SNORD gene copy exhibited a perfect AE of {greater than or equal to}10 nucleotides and retained their ability to form a k-turn". The authors do not include in the figure how many of the multiple (sometimes hundreds) of copies identified for each species actually follow this rule. Secondly, the authors imply but do not state implicitly that the Htr2c and Dgkk sequences being used as the reference are 100% conserved across all the examined species. Also (perhaps more importantly), the authors emphasize "functional conservation" relies on homology with their proposed antisense elements, based on sequence complementarity to Htr2c and Dgkk for SNORD115 and SNORD116 respectively. However later in the study the authors fail to demonstrate any functional binding between SNORD115 and Htr2c or SNORD116 and Dgkk, calling into question the relevance of these sequences in determining "functional conservation". No antisense element was identified, and thereby no functional conservation was determined for the other SNORDs. Overall, this reviewer feels that there is not enough evidence in this study or the wider literature to justify using Htr2c or Dgkk sequences to determine functional conservation for SNORD115 and SNORD116, when there is not enough conclusive evidence to prove these sequences are integral to SNORD115 or SNORD116 function. The authors should further qualify the use of these sequences, or remove functional conservation from the analysis. In addition, the authors include reference to group I and group II SNORD116 sequences, denoted as Snord116-I and Snord116-II in Figure 1A. A grouping classification system does exist for SNORD116, but most systems describe three or four groups (PMID: 11726556, PMID: 29189765, PMID: 34893870), not just two. The use of the term "group" here is confusing as it is not clear whether the authors are referring to this established grouping system or their own system. OPTIONAL: No mouse model, including the one presented here, fully recapitulates the human phenotype. Reproducing a corresponding KO in a human in vitro system followed by functional metabolic or transcriptional analysis could provide important insight.

Minor Comments

The generation and analysis of the Snord116-Ipw-Snord115 mouse KO is well laid out, thorough and convincing. For the graphs in Figure 4K, the label (n=3 pups) is confusing as the graphs clearly show results gathered from greater than n=3. This label could be changed for example to litter size = 3 pups or controlled litter size etc. For the graphs in Figure 6A, weight gain as measured by percentage of starting weight should be included in the data, not just weight gain in total grams. Also, a minor point, but some readers may appreciate a visual key for the graphs in addition to the statement that WT = white and KO = Grey in the figure legend. In this reviewer's view, the data and methods are presented in a way that is otherwise clear and reproducible, and the statistical analysis is appropriate. Inclusion of details regarding statistical analysis in the figure legends is good practice, but optional.

Referees cross-commenting

I agree with the comments from Reviewer 1 and 2, particularly the suggestion to investigate off-target editing (this can sometimes be achieved using RNAseq data but depends on the depth of sequencing).

Significance

The phylogenetic analysis of the SNORDs across 64 placental mammal species is much more comprehensive than previous studies. Almost every species was found to have SNORD-corresponding sequences, indicating high conservation. SNORD116 and SNORD115 are widely known to exist as gene clusters with varying copy numbers across species, but the extreme level of variance in copy number found in this analysis was notable. In particular, the finding that SNORD116 copy number can vary greatly between individuals of the same species (demonstrated previously in mice) raises questions regarding the possibility of varying copy numbers among humans, and the potential functional consequences given that elevated SNORD116 has been associated with a number of disease conditions (PMID: 40101781). For context, this reviewer's field of expertise centers on the genetic and molecular structure of SNORD116 and its wider function in human and animal cell types. According to this reviewer's knowledge, this study is the first to analyze a KO mouse model localized specifically to the SNORD116-IPW-SNORD115 gene array, alongside an IPW-only KO. The results of this study provide further evidence that the SNORD116 gene cluster is the primary driver behind many of the metabolic-related dysfunctions that occur in PWS. However, similar to the SNORD116-specific KO mouse, this model does not fully recapitulate the PWS phenotype, and would be bolstered by evidence gathered from a human model. Furthermore, the lack of transcriptomic change is surprising, given the tissue specificity of the samples analyzed. This reviewer agrees with the author's assertion that single cell sequencing would provide enhanced resolution and clarity in deducing the underlying molecular mechanisms. This work will be of primary interest to a specialized audience in snoRNA biology and PWS/imprinting disorder research, but also has some translational relevance to clinicians and researchers working on PWS more broadly, given its implications for understanding SNORD116-driven metabolic dysfunction. The comparative phylogenetic dataset may also serve as a resource for the broader comparative genomics community studying snoRNA evolution.

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Referee #2

Evidence, reproducibility and clarity

This manuscript describes multiple lines of inquiry into the evolutionary and functional roles of the PWS non-coding RNAs, Snord115, Snord116 and Ipw. Using existing genomic data, the authors show that Snord115 and Snord116 co-evolution is limited, with Snord116 copy-number being highly variable within placental mammals, even between individuals within a species, whereas Snord115 copy number is relatively stable. Snord115 varies with respect to containing the AE/D module predicted to target a conserved segment of Htr2c, with some lineage losing this capability. The equivalent in Snord116 (targeting Dgkk) is under greater constraint. There are also novel findings of Snord109, whose absence limited only to mice & rats, and identified instances of duplication. These genomic analyses are excellent and clearly presented. The authors then describe a series of experiments with novel mouse models - a Snord116-Ipw-Snord115 deletion, and a specific Ipw-ko - the phenoptypes of which they contrast with previous analyses of other Snord116 deletions, both of which also delete Ipw. Although the findings are not ground-breaking, they are very interesting and the use of the novel models adds further granularity to our understanding of the distinct roles of genes within the broader PWS interval. I have a few, relatively minor, queries, but overall this manuscript is well presented, detailed and clear.

When discussing the failiure-to-thrive phenotype to which Snord116 contributes, the authors state (P.13) "One possibility is that loss of Snord116, either directly or indirectly, disrupts in utero development and/or activation of the hypothalamic-autonomic nervous axis, with such defects becoming mostly evident shortly after birth." In this context is the recent findings for a role for PWS in placenta function (10.1242/dmm.052833) and how it might programme the hypothalamus (10.1093/braincomms/fcac229) of relevance?

As indicated, the increased expression of Necdin seen in the Snord116/Snord115-ko mice is interesting, and the authors do an excellent job of elucidating that this is not due to reactivation of the maternal allele, and showing that the gross protein level is unaffected. However, this has been demonstrated previously in a Snord116/Ipw deletion model (https://doi.org/10.1038/s41398-021-01561-x - already cited in relation to Snord116 DEGs) and it would be good if the authors acknowledge this converging evidence in the Discussion as it strengthens the assertion that the increase in Necdin expression is a real phenomenon. This may of course weaken the conclusions in previous papers where phenotypes have been ascribed to loss of Snord116, such as learning and memory deficits (10.1016/j.nlm.2018.05.011), may be due in part to the contribution of altered expression of Necdin.

Minor issues (typos etc)

P.9 "Thus, homeostatic response to increase calories appears intact in Snord116/115-KO mice." "increase" should be "increased"

P.13 There is a rogue fullstop in the following sentence - to me it would be better as two separate sentences, but needs correcting in some way: "Indeed, the transition to extrauterine life represents one of the most physiologically demanding events experienced by placental mammals. [77,78] and perinatal phenotypes are frequently documented in mouse models disrupted for imprinted genes [79], including those at the PWS locus [40]."

Referees cross-commenting

On reading the other reviewers comments, I believe them to be fair and balanced. In particular, issues that I did not pick up relate to RNA-biology (I am not an RNA specialist), and I feel, in addition to my previous suggestions, the following should also be addressed.

As raised by both other reviewers, some clarification as to the definition of snoRNA "groups" and analysis of Group III (and iV?) snoRNAs, or robust justification as to why they have been excluded from the study. As raised by Reviewer 3, there appears to be a logical paradox to the use of Htr2c and Dgkk binding as a measure of "functional conservation", and yet then failing to demonstrate any functional binding between SNORD115 and Htr2c or SNORD116 and Dgkk. I recognise that the authors state that "absence of evidence not being evidence of absence", and, moreover, at present it seems that the Htr2c and Dgkk binding sites are probably the best measure of functionality. However, perhaps a more nuanced discussion of the "functional conservation" analyses of SNORD115 and SNORD116 is required. Finally, I also agree with reviewer 1, that as these are completely novel mouse models, further investigation into the success of the editing approach (i.e. off-target effects, assessment of larger genome rearrangements) are warranted.

Significance

Overall this is an excellent manuscript describing both genomic / bioinformatic analyses and a series of mouse physiology and behaviour experiments. It is really solid and I see very few limitations. The work is highly significant to those interested in understanding the genetics of Prader-Willi syndrome and genomic imprinting more broadly. This work will also be of interest to geneticists and physiologists more generally.

I am a neuroscientist and geneticist who uses preclinical models to understand the role of genomic imprinting in brain and behaviour.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The authors described the creation of two novel mouse models designed to assess contributions of small nucleolar RNA (snoRNA) clusters, Snord116 and Snord115, and non-coding RNA, Ipw, to Prader-Willi syndrome (PWS) relevant phenotypes, most of which have been previously observed in other mouse models. In the Snord116/Snord115-KO model, impaired growth, decreased postnatal survival, hormonal imbalances, and hypoglycemia were shown. Notably, these mice still do not exhibit a clear increase in food intake nor an obesity-like phenotype, thus failing to recapitulate the hyperphagia phenotype observed in PWS patients. The Ipw-KO mice appear to have very mild, if any, perinatal abnormalities, suggesting that the phenotypes observed in the Snord116/Snord115-KO model are not attributable to Ipw deficiency. In addition to the two mouse models, the authors also performed an evolutionary analysis spanning many divergent organisms of various snoRNAs within PWS genomic locus. Importantly, the authors note that while SNORD116 appears to display the highest conservation, there are still notable differences across species. SNORD115 shows more lineage-related patterns of evolutionary change. Interestingly, SNORD109 was identified in the majority of mammalian genomes, suggesting that its absence in mouse and rat is related to a Murinae-specific linage loss. Other single/low copy number SNORDs (SNORD64, SNORD107, and SNORD108) only show mild selective constraint and even lack characteristic RNA elements in some cases (canonical C-box in SNORD108). Overall, the work is generally well conducted and conveyed, and also both interesting and important to the field, however there are a few specific points which should be addressed prior to publication.

Major comments:

1. Given the authors describe two novel mouse models, it is important to validate the CRISPR editing was specific and that no considerable off-target editing occurred. This can be accomplished through prediction of off-targets through available online tools (such as Cas-OFFinder) followed by amplification and sequencing of those regions to demonstrate no editing has occurred. Additionally, given the highly repetitive nature of the genomic region being targeted, a more thorough analysis checking for larger chromosomal abnormalities may be warranted.
2. The authors are quite critical of the lack of shared dysregulated genes across human cell lines from different backgrounds and neuronal differentiation protocols, however, they neglect to mention that this is a well-described phenomenon (for example in DOI: 10.1016/j.stem.2017.03.009) and not specific to PWS-like models. Additionally, a similar point is highlighted within their own work in Figure 8D, which shows very few, if any, shared differentially expressed genes across brain regions from the same mouse. The authors also highlight many similarities of previously published studies using Snord116-KO mice, without noting any key differences observed across these studies. While pointing out the limitations of previously published studies is of course warranted, a more evenly balanced critical review of the most utilized model systems to study PWS is crucial to not mislead readers.
3. While the authors evaluate the presence of Group I & Group II snoRNAs, Group III snoRNAs which have been previously described (doi: 10.1093/hmg/10.23.2687 & doi: 10.1371/journal.pone.0011779) are not mentioned. It is recommended to either include these snoRNAs in analysis or explain why they have been excluded.
4. When describing the decision to evaluate Snord116 & Snord115 KO in mouse and/or when comparing it to SNORD116 & SNORD115 KO in humans, it should be noted that it is possible, or even likely, that these genomic loci - while syntenic and conserved across species - may be quite differently regulated between species. The different expression patterns of the SNORD clusters in brains of humans versus mice may exemplify this point. It is important for readers to bear this in mind when interpreting downstream results. It may be particularly interesting when considering that MAGEL2 appears to be consistently dysregulated in the human systems (doi:10.1093/nar/gkae1129) and Ndn - a neighboring gene from a similar gene family - is reported to be consistently dysregulated in this manuscript. This can also contribute to why rodent models don't display key phenotype features of PWS like hyperphagia.
5. Please explain the reasoning behind why only male mice were used in the "Indirect calorimetry and body composition" experiment.

Minor comments:

1. Page 2 & throughout - use appropriate annotation for genes when referencing if they were studied in human (all capitals), mouse (first letter capitalized), or both (perhaps indicating through using a slash, like GENE/Gene)
2. Figure 2C - would be nice to include human, mouse, and rat diagrams as comparators to the more unique or lesser studied organisms. Additionally, maybe interesting to include which direction is towards the telomere and centromere, respectively.
3. Figure 3A - would be helpful to include a graphical representation of how this deletion compares to previous mouse models (either here or as a supplemental figure)
4. Supplementary Figure 3 - would be better presented as a table (either Word Doc or Excel Sheet) listing one sequence per line.
5. Supplementary Figure 5 - similarly to Supplementary Figure 3, would be better presented by breaking it up into a figure containing the sequence logo plot & the compact sequence alignment as panels, and the individual sequences with names as a table (either Word Doc or Excel Sheet) listing one sequence per line.
6. Page 5 - "undergo" should be "undergone"
7. Page 6 - "promote" should be "promotes"

Significance

This work looks at the PWS locus from a more evolutionary perspective, something that has been gaining traction with the recent advances in sequencing technology that allows us to have a greater collection of better-quality diverse genome assemblies. The field will be interested in the new mouse models described and how they both relate to and are unique from the plethora of models already available. It is also interesting to have another work which cannot validate the long-suggested Snord115 interaction with Htr2c. I completely appreciate the sentiment the authors convey about "absence of evidence not being evidence of absence," but I am left wondering whether the technical capabilities are still lacking in being able to detect the modification, if the modification is not really occurring, if the modification is occurring but not at a biologically-relevant level, or some combination of these. While I do not have much expertise in evolutionary biology, I am a member of the PWS research community and have a dedicated time to thinking about the complexities between different organisms as models for PWS, including what we are and are not able to ask of each individual model system - both human, rodent, and otherwise. My work in the field spans both RNA- and protein-based analyses in various organisms.

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Sections 6.1 and 6.6.1 explicitly state that a research strategy is not a method, and that data generation methods (such as questionnaires, interviews, observations, and documents) are chosen within a strategy. However, in Table 6.6, the "Strategy" column literally lists data generation methods—specifically "Documents as data" for Boodraj et al. (2026) and "Qualitative — participatory workshops" for Woodruff et al. (2024)—as if they were research strategies.

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Reply to the reviewers

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

__Lenaerts et al use a cleavable recombinant SNAPtag anti-ALFA nanobody to study integrin membrane internalisation dynamics in U2Os cells with an endogenous ALFAtag CRISPR/Cas9 knock-in. They apply this approach to the study of three aspects: 1) ligand-induced activation/modulation of cell surface receptor endocytosis using known cell surface modulators, 2) a comparative study of the internalisation of two distinct receptors from the same integrin family, and 3) the study of the endocytic behaviour of TMEM123, an uncharacterised cell surface protein.____*

The authors use state-of-the-art tools to show that this approach can be used to study cell surface proteins at endogenous levels, offering a potentially generalisable strategy for probing surface protein trafficking under physiological conditions that does not rely on specific antibodies. It does, however, require genetic cell engineering.

The development of broadly applicable tools to study cell surface protein turnover is timely and of wide interest, though comparable but not identical strategies have been employed for identical purposes in the past (PMID: 15078902, 38737503, 29915061). Overall, the manuscript is clearly written, and the experiments are appropriate. However, some aspects of experimental design and validation require attention/clarification.*__

We would like to thank the reviewer for taking the time and effort to read our manuscript and for the supportive comments. You'll notice this revised version comes with a bit of a delay. We apologise for it. The leading author of our manuscript had to step away from the revisions for a while, since she is our lab manager and resident CRISPR expert, her time was needed to help with other projects and train a recent wave of new people in the lab.

We also want to thank the reviewer for pointing us to these related studies, which we had not cited and which we agree belong in the manuscript. We have now added all three. Seaman (2004) and Buser et al. (2018) are, as the reviewer notes, conceptually related to EndoNB in that both follow a surface protein through a binder directed at a heterologous extracellular epitope rather than at the protein itself, and Lim and McWilliam (2024) use a cleavable handle for the same surface-signal-removal purpose as our 3C site. We have added these references to the Introduction (lines 40-47 and 60-63) together with a new paragraph in the Discussion (lines 251-266) that places EndoNB as the next generation of these assays and states what it adds: 1) endogenous expression levels and a 15-amino-acid tag instead of an overexpressed large chimera; 2) surface signal removal built into the probe, allowing a single protease step to be used with every target without re-optimization; and 3) a single universal probe, which makes absolute uptake values comparable between different surface proteins. We also now state the corresponding limitation: that EndoNB requires genome editing and is therefore less applicable than antibody-based assays to primary or heterogeneous samples.

1) It is common for CRISPR/Cas9 homology to happen in a heterozygous fashion, where one allele is correctly knocked-in and the other is incorrectly repaired by NHEJ, resulting in only half the protein to be functional. This is due to the fact that the CRISPR cutting is high efficiency and the integration low efficiency. The authors don't show validation of the heterozygous KI ALFA-tagged site. What is the status of the other allele? Are they only assaying half the functional protein in the cell? This has major implications as if indeed it is compound heterozygous the gene dose is halved for the process being studied.

Fair point. In the revised version we have made a full characterisation of the engineered cell lines we used.

To confirm the insertions were clean and the wild-type alleles were untouched, we have now used NGS to sequence the genomic regions where the ALFA tags were inserted. The analysis showed that the clones we picked had indeed correct ALFA tag integration and no mutations in the edited and unedited alleles. All insertions were clean. Interestingly, some of clones that we thought were heterozygous (by PCR) were homozygous by NGS analysis.

Changes to the manuscript:

• New figures S1A-D, S2A-J, S4A-D and S5A-D and associated legends
• Explanation of the NGS experiment and analysis. Lines 102-104, 173-176, 186-188, 220-222 and 386-389.

  2) There is no validation of the specificity of the nanobody against ALFA-tagged proteins under the assay conditions.

To show that only cells containing the ALFA-tag on their surface uptake the EndoNB probe, we have performed experiments using naïve cells fed with our probe. For this experiment, we have used our standard probe concentration (1µg/ml) and 10 times more. These uptake conditions were compared side-by-side with ITGB5, our slowest endocytosed receptor. As shown in figure S1F, barely any uptake or surface attachment is detectable at standard conditions with a slight increase (but still one order of magnitude lower) when using 10 times more EndoNB probe.

Changes to the manuscript:

• New figure S1F and associated legend
• Explanation of the experiment and analysis. Lines 113-120

  3) The nanobody assay does not include a control to distinguish receptor-specific internalisation from general bulk endocytosis. How can the authors be sure the SNAP-tagged nanobody is not being passively internalised throughout the duration of the assay?

As explained above, Figure S1F addresses this directly. Unedited cells were fed the EndoNB probe for up to 3 hours (the full duration of our longest assay) at the standard concentration and at a 10-fold excess, and deliberately without 3C treatment, so that the measurement captures both fluid-phase uptake and non-specific surface attachment. At the concentration used throughout the paper (1 µg/ml) the signal was indistinguishable from cells never exposed to the probe. Only at a 10-fold excess did a signal appear, and it remained far below the uptake of integrin β5, the slowest receptor in our study.

*Changes to the manuscript: *

• New figure S1F and associated legend
• Explanation at lines 113-120.

  4) It is unclear whether the statistical comparison shown in Fig. 1F was based on all biological repeats or a single representative experiment. Data should be normalised to show all three biological replicates, and appropriate statistical analysis across replicates should be provided.

For clarification. The experiment in figure 1f is from 3 independent experiments. The reason we have plotted it as individual cells is to reflect what is typically done in the field, where each “n” is a cell. We did the experiments in 3 consecutive days and took all the images in a single microscopy session, to reduce too much signal variation. The raw values for the three experiments were just put together in the same graph. The comparison is using each cell as a single “n”.

We agree with the reviewers (this was also pointed out by reviewer 2) that with high “n” numbers, the stats become a bit meaningless. The implementation of high throughput microscopy and cell segmentation (with Cellpose) has indeed brought the same “n-flation” issue to microscopy analysis.

To cater for both sides of the discussion, the “1 cell = 1 n” purists and the statistical realists, we have now added the statistically correct graph (1n = 1 experiment) in the main figure (figure 1F) and the per cell graph in the supplementary material (figure S1E).

Changes to the manuscript:

• New figure 1F and S1E and associated legends

  5) In Fig. 4, Pearson's coefficient is used to report colocalization, but no experimental control is included to contextualise the coefficient.

This is a good point. We have now expanded this experiment to contextualise it. In this experiment, we make 3 comparisons at 5 and 15 minutes of uptake: 1) The colocalization of Transferrin (TF)-488 with Transferrin (TF)-647. This gives us a methodological baseline of how two equal ligands colocalise overtime under our experimental conditions.

2) The colocalization of TF-488 with EndoNB-646 in TFRC ALFA-tagged cells. This shows us how the EndoNB probe co-endocytose/co-traffics with the ligand.

3) The colocalization of TF-488 with EndoNB-646 in TMEM123 ALFA-tagged cells. This shows us how much TFRC and TMEM co-endocytose/co-traffic.

This analysis showed a lot of interesting results. First, the TF-TF and TF-EndoNB probe in TFRC cells behave the same (colocalising around 70% of the time). This is a nice confirmation that the EndoNB probe, as expected, behaves the same way as a native ligand. Second, the EndoNB probe in TMEM123 ALFA-tagged cells showed a smaller, but still rather high (46%) colocalization with TF-488. These results contextualise the colocalization of TF and TMEM123 and show that these receptors, albeit having the same internalisation kinetics, are not obligatorily internalised and/or trafficked together. The 46% colocalization of these cargoes fits a model where two relatively abundant cargoes are randomly recruited to pits. We have added this possible explanation to the discussion of the manuscript.

Changes to the manuscript:

• New figures 4D-F and associate legends.
• New experimental explanation, discussion and methods: Lines 230-241, 275-279, 492-504 and 520-528.

  6). Several figures would benefit from improved clarity and more precise labelling. For example, in Fig. 1F, clarify whether the incubation time refers to EndoNB exposure or 3C protease treatment. In Fig. 2H, the legend is not clear, and in Fig. 4E-F the Y-axis label is serving as both axis label and legend.

Thanks for pointing this out. We have changed many of the figure legends in the manuscript to provide clearer information on the experiments.

Changes to the manuscript:

• New figures legends for figure 1F, 1G, 2C, 2H, 3B, 4B and 4C (previously 4e-f), and 4F.

  Reviewer #1 (Significance (Required)):

The development of broadly applicable tools to study cell surface protein turnover is timely and of wide interest, though comparable but not identical strategies have been employed for identical purposes in the past (PMID: 15078902, 38737503, 29915061). Overall, the manuscript is clearly written, and the experiments are appropriate. However, some aspects of experimental design and validation require attention/clarification.

Thanks for the support. We agree that some of the features of our assay have been used previously. As discussed in your opening comments, we have now incorporated the suggested references to the manuscript and discussed how EndoNB compares to those. We strongly believe that EndoNB is superior to these previous assays in its wider applicability (especially for receptors without available antibodies) and minimal interference (using endogenously tagged receptors instead of overexpression of GFP tagged ones).

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

We would like to thank the reviewer for the supportive and constructive comments on our manuscript. We believe it has helped us to build a better story. We apologise for the delays in this revised version. The leading author of our manuscript had to step away from the revisions for a while, since she is our lab manager and CRISPR expert, her time was needed to help with other projects and train a recent wave of new people in the lab.

__Lenaerts et al report a method for labelling surface proteins and monitoring their internalisation. The method involves CRISPR knock-in of an ALFA tag on the extracellular face of a receptor of interest (several are shown) and then using a recombinant, cleavable nanobody-SNAP tag fusion to label surface proteins and strip the surface label to only visualise the internalised receptors. This is a neat approach and the authors show a few use cases to demonstrate for example how the method allows a researcher to assess the effect of antibodies on internalisation, as an independent readout of receptor trafficking. I found the paper and the method very interesting and thought the study was very useful. I have some comments that are straightforward to address.

• I was sceptical that TMEM123 and the transferrin receptor were so similar. The authors say that in U2OS the expression of both are similar, but I'm worried that the authors have simply mixed up the edited cell lines here. Can the authors show convincingly that TMEM123 is the tagged protein in this line? It's an unfamiliar protein and even just showing the whole cell distribution would help. Coloc stats for Tf vs Tf to compare with those shown is another possibility.__

This is a fair comment and, to be honest, we suspected the same thing when we got the first results on TMEM123.

In this revision, we have added multiple pieces of evidence to show that TMEM123 is indeed an independent surface protein. First, we have used NGS to validate the integration region of all our clones used in the study (Figures S1A-D, S2A-J, S4A-D and S5A-D). As you will see, TMEM123 is the tagged protein. More importantly, we did a crucial experiment, where we knocked down the transferrin receptor in TFRC and TMEM123 ALFA-tagged cells and measured both TF-488 and EndoNB-646 internalisation. As you will see from the graphs in figure S5E, TFRC cells show a significant reduction of TF-488 and EndoNB uptake in KD cells, while TMEM123 cells show a reduction only in TF-488. Crucially, you will notice that the absolute internalisation of EndoNB in TFR-Alfa and TMEM123-Alfa cells is still similar in the control, non-targetting shRNA conditions. As the reviewer will notice, the internalisation of TMEM123 in TFRC KD cells is slightly (but not significantly) higher. This is a phenomenon that we have observed a few times. TMEM123 internalisation, and probably expression, is highly affected by the cell state. We have noticed substantial variations in our results when cells were serum-starved for more than 1h, when cultures were overconfluent or with the TFRC knockdowns. We don’t know the exact reason for this phenomenon, but there is certainly some interesting biology to be discovered in another study. As we could not nail down the exact conditions for these observations, we opted to avoid discussing this in the manuscript. If the reviewer thinks it is relevant to the results, we would gladly add a few sentences in the discussion.

And regarding the colocalization studies, thanks for your great suggestion of using TF-TF as a baseline. The other reviewer has also raised concerns about these experiments, and we have completely changed them to better contextualize the TF-TMEM123 relationship. In this experiment, we make 3 comparisons at 5 and 15 minutes of uptake: 1) The colocalization of Transferrin (TF)-488 with Transferrin (TF)-647. This gives us a baseline of how two equal ligands colocalise overtime under our experimental conditions.

2) The colocalization of TF-488 with EndoNB-646 in TFRC ALFA-tagged cells. This shows us how the EndoNB probe co-endocytose/co-traffics with the ligand.

3) The colocalization of TF-488 with EndoNB-646 in TMEM123 ALFA-tagged cells. This shows us how much TFRC and TMEM123 co-endocytose/co-traffics.

This analysis showed a lot of interesting results. First, the TF-TF and TF-EndoNB probe in TFRC cells behave the same (colocalising around 70% of the time). This is a nice confirmation that the EndoNB probe, as expected, behaves the same way as a native ligand. Second, the EndoNB probe in TMEM123 ALFA-tagged cells showed a smaller, but still rather high (46%) colocalization with TF-488. These results contextualise the colocalization of TF and TMEM123 and shows that these receptors, albeit having the same internalisation kinetics, are not obligatorily internalised and/or trafficked together. The 46% colocalization of these cargoes fits a model where two relatively abundant cargoes are randomly recruited to pits. We have added this possible explanation to the discussion of the manuscript.

Changes to the manuscript:

• Confirmation of clones by NGS:
• New figures S1A-D, S2A-J, S4A-D and S5A-D and associated legends

• Explanation of the NGS experiment and analysis. Lines 102-104, 173-176, 186-188, 220-222 and 386-389.

• TFRC knockdown experiment

• Figure S5E and associate legend

• Explanation of the experiments, analysis and methods: Lines 238-240, 361-363 and 449-459

• TMEM123-TFR colocalization:

• New figures 4D-F and associate legends.
• New experimental explanation, discussion and methods: Lines 230-241, 275-279, 492-504 and 520-528.

- Related to this, there is no validation of the knock-ins shown. Westerns or PCR to show how many alleles have been tagged would be useful. It says in the methods that the cell lines were all heterozygous. I guess with U2OS, which are not chromosomally stable it is unknown how many alleles are actually tagged. It seems incomplete without some validation, even if it is just for one model cell line.

This is a fair point, also raised by the other reviewer. In the revised version we have made a full characterisation of the engineered cell lines we used.

To confirm the insertions were clean and the wild-type alleles were untouched, we have now used NGS to sequence the genomic regions where the ALFA tags were inserted. The analysis showed that the clones we picked had indeed correct ALFA tag integration and no mutations. Interestingly, some of clones that we thought were heterozygous (by PCR) were homozygous by NGS analysis.

Changes to the manuscript:

• New figures S1A-D, S2A-J, S4A-D and S5A-D and associated legends
• Explanation of the NGS experiment and analysis. Lines 102-104, 173-176, 186-188, 220-222 and 386-389.

  - The methods are reasonably clear about the way the stats have been done, but in Fig 1f, n number of cells are presented. This is either from a single experiment, in which case it should say so. If they are pooled from several experiments, this is an incorrect way of applying the ANOVA and Tukey's test, since the n number is falsely inflated and the stats should be done on a summary stat of the experimental repeats (as in 1g).

For clarification. The experiment in figure 1f is from 3 independent experiments. The reason we have plotted it as individual cells is to reflect what is typically done in the field, where each “n” is a cell. We did the experiments in 3 consecutive days and took all the images in a single microscopy session, to reduce too much signal variation. The raw values for the three experiments were just put together in the same graph.

We agree with the reviewer that with high “n” numbers, the stats become a bit meaningless and that’s why we use medians for each replicate (>2000 cells) for FACS experiments. The implementation of high throughput microscopy and cell segmentation (with Cellpose) has indeed brought the same “n-flation” issue to microscopy analysis.

To cater for both sides of the discussion, the “1 cell = 1 n” purists and the statistical realists, we have now added the statistically correct graph (1n = 1 experiment) in the main figure (figure 1F) and the per cell graph in the supplementary material (figure S1E)

Changes to the manuscript:

• New figure 1F and S1E and associated legends

  - In the Discussion the authors say that 30-50 nTPM is required. This seems like a "data not shown". Can they say a bit more or is this statement about unpublished work?

This is a very fair comment. The value we show in the discussion is not derived from a dedicated analysis. It rather reflects our experience in the last years with endogenous tagging of surface proteins, both for EndoNB and in other projects using Halo and GFP. In these efforts, targets expressed below ~30–50 nTPM in the respective cell line (based on the Human Protein Atlas) rarely gave a detectable signal by flow cytometry. Because we did not systematically determine whether individual failures were due to low expression, gRNA efficiency or effects of the tag on expression, we do not present these attempts as data. Our intention is to give readers a practical reference for the likelihood of success. We have rephrased the Discussion to make the empirical nature of these values explicit.

Changes to the manuscript:

• New lines (286-292) in the discussion

  - Fig 2f, scaling the axes from 0 would be a more honest way to show the data.

When putting both X- and Y-axis from 0, the graph ends up dominated by a lot of empty space and looking very weird and hard to see the actual data, as you can see below.

As a compromise, we have plotted the graph with a split axis. This makes the graph honest and easy to visualise the curves.

Changes to the manuscript:

• New figure 2F

  Presentation:____ - The magenta on black is terrible for contrast (Fig 1e, 4c). It also can't be compared with yellow-on-black, cyan-on black or anything else-on black, because of the way our eyes perceive colour. Single channel images should always be presented in greyscale so they can be compared. In fact, the views shown in Fig S2 (inverted as black-on-white) look great and the authors should switch to this or go with white-on-black. There's only one merge image in the whole paper (Fig 4c bottom right panel) which requires colour.

Fair comment. We have converted the EndoNB channel to inverted greyscale in Figures 1E and 4E, and all single channels in Figure 4E are now greyscale. We have kept the actin counterstain in Figure 1E, and the counterstains in Figure S4E, in colour: these channels are never compared quantitatively between panels and serve only to mark the cell outline and the adhesion marker, and in our hands the colour makes the overlay easier to read. We are happy to convert them as well if the reviewer prefers.

Changes to the manuscript:

• New figures 1E and 4E.

  - Personal opinion: Fig 1f and 1g. I don't think we need a picture of a microscope and FACS machine here. This is maybe OK on a poster, but in a paper I don't think it's appropriate. Anyway, they're biorender-made which just looks bad anyway.

To be honest, we added the microscope and the flow cytometer drawings to the figure to fill up an awkward empty space in the figure. They are now gone.

- I wasn't so taken with the blind men and elephant analogy at the end of the paper. The analogy didn't work for me and they can make their point equally well without it. But it's not my paper!

That was an analogy made by a student when I was explaining this project for him, many years ago. I liked it so much that I use it very frequently on my talks since then. However, we do understand that the briefness of how it is presented in the paper may not do justice to the idea. We have removed it from the revised version.

- Typo in Transferrin in Fig S3.

Thanks. It is now corrected.

- The AlphaFold prediction for TMEM123 is probably just a ball of string but it would match the other figures if it was shown like that.

We have added the predicted structure to fit the rest of the figures.

Reviewer #2 (Significance (Required)):

This is a cool new method to study receptor trafficking. There are several novel aspects to it, however it represents the implementation of existing technologies in a similar way (conceptually) to previous methods; so it's not revolutionary. Nonetheless, this method will be very useful to those of us in the field. The authors contribute some interesting data, e.g. on whether transferrin influences the trafficking of the receptor (it doesn't) which are useful advances. The audience is cell biologists, although the range of proteins at the cell surface including many clinically relevant targets mean that the method could have broader appeal outside of the cell biology field.

Thanks for the support. We agree that some of the features of our assay have been used previously,

We have now added a bit more context on how EndoNB compares to other similar efforts (as suggested by Reviewer #1) to measure surface protein internalisation. We now discuss how the work of Seaman (2004) and Buser et al. (2018) are conceptually related to EndoNB in that both follow a surface protein through a binder directed at a heterologous extracellular epitope rather than at the protein itself. We also disscuss the work of and Lim and McWilliam (2024), which use a cleavable handle for the same surface-signal-removal purpose as our 3C site. We have added these references to the Introduction (lines 40-47 and 60-63) together with a new paragraph in the Discussion (lines 251-266). We argue that these comparisons place EndoNB as the next generation of these assays and states what it adds: 1) endogenous expression levels and a 15-amino-acid tag instead of an overexpressed large chimera; 2) surface signal removal built into the probe, allowing a single protease step to be used with every target without re-optimization; and 3) a single universal probe, which makes absolute uptake values comparable between different surface proteins. We also now state the corresponding limitation: that EndoNB requires genome editing and is therefore less applicable than antibody-based assays to primary or heterogeneous samples.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

Lenaerts et al report a method for labelling surface proteins and monitoring their internalisation. The method involves CRISPR knock-in of an ALFA tag on the extracellular face of a receptor of interest (several are shown) and then using a recombinant, cleavable nanobody-SNAP tag fusion to label surface proteins and strip the surface label to only visualise the internalised receptors. This is a neat approach and the authors show a few use cases to demonstrate for example how the method allows a researcher to assess the effect of antibodies on internalisation, as an independent readout of receptor trafficking. I found the paper and the method very interesting and thought the study was very useful. I have some comments that are straightforward to address.

• I was sceptical that TMEM123 and the transferrin receptor were so similar. The authors say that in U2OS the expression of both are similar, but I'm worried that the authors have simply mixed up the edited cell lines here. Can the authors show convincingly that TMEM123 is the tagged protein in this line? It's an unfamiliar protein and even just showing the whole cell distribution would help. Coloc stats for Tf vs Tf to compare with those shown is another possibility.
• Related to this, there is no validation of the knock-ins shown. Westerns or PCR to show how many alleles have been tagged would be useful. It says in the methods that the cell lines were all heterozygous. I guess with U2OS, which are not chromosomally stable it is unknown how many alleles are actually tagged. It seems incomplete without some validation, even if it is just for one model cell line.
• The methods are reasonably clear about the way the stats have been done, but in Fig 1f, n number of cells are presented. This is either from a single experiment, in which case it should say so. If they are pooled from several experiments, this is an incorrect way of applying the ANOVA and Tukey's test, since the n number is falsely inflated and the stats should be done on a summary stat of the experimental repeats (as in 1g).
• In the Discussion the authors say that 30-50 nTPM is required. This seems like a "data not shown". Can they say a bit more or is this statement about unpublished work?
• Fig 2f, scaling the axes from 0 would be a more honest way to show the data.

Presentation:

• The magenta on black is terrible for contrast (Fig 1e, 4c). It also can't be compared with yellow-on-black, cyan-on black or anything else-on black, because of the way our eyes perceive colour. Single channel images should always be presented in greyscale so they can be compared. In fact, the views shown in Fig S2 (inverted as black-on-white) look great and the authors should switch to this or go with white-on-black. There's only one merge image in the whole paper (Fig 4c bottom right panel) which requires colour.
• Personal opinion: Fig 1f and 1g. I don't think we need a picture of a microscope and FACS machine here. This is maybe OK on a poster, but in a paper I don't think it's appropriate. Anyway, they're biorender-made which just looks bad anyway.
• I wasn't so taken with the blind men and elephant analogy at the end of the paper. The analogy didn't work for me and they can make their point equally well without it. But it's not my paper!
• Typo in Transferrin in Fig S3.
• The AlphaFold prediction for TMEM123 is probably just a ball of string but it would match the other figures if it was shown like that.

Significance

This is a cool new method to study receptor trafficking. There are several novel aspects to it, however it represents the implementation of existing technologies in a similar way (conceptually) to previous methods; so it's not revolutionary. Nonetheless, this method will be very useful to those of us in the field. The authors contribute some interesting data, e.g. on whether transferrin influences the trafficking of the receptor (it doesn't) which are useful advances. The audience is cell biologists, although the range of proteins at the cell surface including many clinically relevant targets mean that the method could have broader appeal outside of the cell biology field.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #1

Evidence, reproducibility and clarity

Lenaerts et al use a cleavable recombinant SNAPtag anti-ALFA nanobody to study integrin membrane internalisation dynamics in U2Os cells with an endogenous ALFAtag CRISPR/Cas9 knock-in. They apply this approach to the study of three aspects: 1) ligand-induced activation/modulation of cell surface receptor endocytosis using known cell surface modulators, 2) a comparative study of the internalisation of two distinct receptors from the same integrin family, and 3) the study of the endocytic behaviour of TMEM123, an uncharacterised cell surface protein.

The authors use state-of-the-art tools to show that this approach can be used to study cell surface proteins at endogenous levels, offering a potentially generalisable strategy for probing surface protein trafficking under physiological conditions that does not rely on specific antibodies. It does, however, require genetic cell engineering.

The development of broadly applicable tools to study cell surface protein turnover is timely and of wide interest, though comparable but not identical strategies have been employed for identical purposes in the past (PMID: 15078902, 38737503, 29915061). Overall, the manuscript is clearly written, and the experiments are appropriate. However, some aspects of experimental design and validation require attention/clarification.

1) It is common for CRISPR/Cas9 homology to happen in a heterozygous fashion, where one allele is correctly knocked-in and the other is incorrectly repaired by NHEJ, resulting in only half the protein to be functional. This is due to the fact that the CRISPR cutting is high efficiency and the integration low efficiency. The authors don't show validation of the heterozygous KI ALFA-tagged site. What is the status of the other allele? Are they only assaying half the functional protein in the cell? This has major implications as if indeed it is compound heterozygous the gene dose is halved for the process being studied.

2) There is no validation of the specificity of the nanobody against ALFA-tagged proteins under the assay conditions.

3) The nanobody assay does not include a control to distinguish receptor-specific internalisation from general bulk endocytosis. How can the authors be sure the SNAP-tagged nanobody is not being passively internalised throughout the duration of the assay?

4) It is unclear whether the statistical comparison shown in Fig. 1F was based on all biological repeats or a single representative experiment. Data should be normalised to show all three biological replicates, and appropriate statistical analysis across replicates should be provided.

5) In Fig. 4, Pearson's coefficient is used to report colocalization, but no experimental control is included to contextualise the coefficient.

6). Several figures would benefit from improved clarity and more precise labelling. For example, in Fig. 1F, clarify whether the incubation time refers to EndoNB exposure or 3C protease treatment. In Fig. 2H, the legend is not clear, and in Fig. 4E-F the Y-axis label is serving as both axis label and legend.

Significance

The development of broadly applicable tools to study cell surface protein turnover is timely and of wide interest, though comparable but not identical strategies have been employed for identical purposes in the past (PMID: 15078902, 38737503, 29915061). Overall, the manuscript is clearly written, and the experiments are appropriate. However, some aspects of experimental design and validation require attention/clarification.

does not leverage

https://ipfs.indy0.net/ipfs/bafybeiaqsth6zstxoest6hbvs6pcp5wrwla4bqez5jsu5bhtxuxu5xydk4/PCWorld.html

indy 🌐 📓 2026 11 = facebok.is.toast~said.by-ForresterCEO

leverage the power in your pocket

that's the only way

https://ipfs.indy0.net/ipfs/bafybeiaqsth6zstxoest6hbvs6pcp5wrwla4bqez5jsu5bhtxuxu5xydk4/PCWorld.html

cloud computing

does no leverage the power in your pocket

https://hyp.is/w_OCht0AEfGZNoezj5HvhQ/web.archive.org/web/20120623225210/http://www.computerworlduk.com/news/mobile-wireless/3364899/forrester-ceo-facebook-is-toast/

This source illustrates the discrepancies that arise during transmission, yet its effect is extraordinary—it splits like nuclear fusion.

“Viral”—when applied to information—means that the information spreads and proliferates like a virus. It is rapidly replicated and transmitted to tens of thousands or even millions of viewers; it can penetrate people’s minds like a virus, replicate quickly, spread rapidly, and reach a wider audience in a short period of time.

meaning we will start to hsv to pay back the principal on this

likely been some pushback as to why theyre keeping these stores thats why they are justifying it so much here

roughly even domestic/intl in store count

99% participation, why not mandate?

highly concentrated in us market may change in next report

Acaso descumprida a comprovação da exportação através do registro do órgão competente ou pela documentação expressa na legislação aduaneira, a lei presume a ocorrência de operação onerosa em detrimento de exportação; com isso serão exigidos todos os tributos inerentes à operação.

A imunidade referente às exportações é aplicável ainda que o bem material não saia do território nacional, como por exemplo, a venda de aeronave a empresa sediada no exterior e posterior leasing efetuado com empresa brasileira (aeronave nunca saiu do território nacional).

设置成窗外乌云被风吹散，满月显露，男主发情期彻底到来，面色潮红，拉着女主手蹭，啄吻女主，表露爱意，女主回想起封印记忆，虽然没想起来爱但是感觉愧疚想推开，男主强势压过来。makelove写细节一些

?

The conplex of which any named saved web page is part of in 1's TrailsMapped indra net workspace

is actually maintained at the Peergos side

access to which is under the conrols of the resource creator, yet it can be linked to publically available resources

indy 🌐 📓 2026 11 query morning.evening.star.equivalence ~ discovered.when to

Earler I tried to maintain all that as part of the name for a saved resource

Splitting into these technically different parts makes perfect snse and

serves the oriinal putpose much better

This one is a nice example how inter rellated concerns give rise naturally to mutually arising ways and means

Started creating chronolarchic folder structures in my loacl User's Download folder named for te current moth

like 2026-11

and within there creating intentionally transparent named folder structures

where Web Pages that are saved using single Page with Single file

Chrome extensions are then saved

for a long time I used a local IPFS node

but since all these things are intended to be shared in the open might as well rely on Pinning services like Pinata to uplad them to IPFS space

All these I also make an effort to replicate these monthly folders using IPFS across all my laptops

so even if the gateway goes aways running say IPFS Descktop or any other ways

all these Oermanent IPFS resources could be accessed

So alll in all,

te way information is stored using folder trails

and assume that all resource of interest will have meaning ful names and belong to some folder

The full Hyper Trail Map is not shared outright publically

so make a virtue of the fact that te root folder that is uploaded to IPFS will not have itse name shown only the file/folder names that are under it

that messhes well with over all sstorge searc and retrieval stategies

EveningStar-Universe-Today

from: https://hyp.is/MgAtYtz1EfGntM_PO9U6uQ/search.brave.com/search?q=morning+evening+star+equivalence+discovered+when&source=web&conversation=09c9557b7853ce4bad4adac8fcccb741255b

It should remind me what shares were preserved and where the drops happened.

to: https://hyp.is/9VeD7Nz0EfG8RqvTR6AkJQ/www.universetoday.com/articles/evening-star