This work has been peer reviewed in GigaScience (see https://doi.org/10.1093/gigascience/giaf126), which carries out open, named peer-review. These reviews are published under a CC-BY 4.0 license and were as follows:

Reviewer 2: Jérôme Salignon

This manuscript presents tcga-data-nf, a Nextflow-based pipeline for downloading, preprocessing, and analyzing TCGA multi-omic data, with a focus on gene regulatory network (GRN) inference. The workflow integrates established bioinformatics tools (PANDA, DRAGON, and LIONESS) and adheres to best practices for reproducibility through containerization (Docker, Conda, and Nextflow profiles). The authors demonstrate the utility of their pipeline by applying it to colorectal cancer subtypes, identifying potential regulatory interactions in TGF-β signaling. The manuscript is well-written and well-structured and provides sufficient methodological details, as well as Jupyter notebooks, for reproducibility. However, there are some areas that require clarification and improvement for acceptance in GigaScience, particularly regarding the scope of the tool, the quality of the inferred regulatory networks, the case study figure, benchmarking, statistical validation, and parameters.

Major comments:

• While the pipeline is well designed and executed, the overall impact of the tool feels somewhat limited, especially for a journal like GigaScience, due to its pretty specific application to building GRNs in TCGAs, the relatively small number of parameters, the support of only 2 omics type, and the lack of novel algorithms. To increase the impact of this tool I would recommend adding functionalities, such as:

o Supporting additional tools. A great strength of the pipeline is the integration with the Network Zoo (NetZoo) ecosystem. However, only three tools are included from NetZoo. Including additional tools would likely increase the scope of users interested in using the pipeline. In particular, an important weakness of the current pipeline is that it is not possible to conduct differential analysis between different networks, which prevents users from identifying the most significant differences between two networks of interest (e.g., CMS2 vs CMS4). The NetZoo contains different tools to conduct such analyses, such as Alpaca 1 or Crane 2, thus this may be implemented to make the pipeline more useful to a broader user base.

o Adding parameters. A strength of the pipeline is the ability to customize it using various parameters. However, as such the pipeline does not offer many parameters. It would be beneficial to make the pipeline a bit more customizable. For example, novel parameters could be: adding options for excluding selected samples, using different batch correction methods, different methods to map CpGs to genes, additional normalization methods, and additional quality controls (e.g., PCA for methylation samples, md5sum checks). These are just examples and do not need to be all implemented but adding some extra parameters would help make the pipeline more appealing and customizable to various users.

• The quality of the inferred regulatory networks is hard to judge. There are no direct comparisons with any other tools.

o For instance, it is mentioned in the text that GRAND networks were derived using a fixed set of parameters, but it could be helpful to show a direct comparison between GRNs built from your tools with those from GRAND. This could reveal how the ability to customize GRNs using the pipeline's parameters helps in getting better biological insights.

o Alternatively, or in addition, one could compare how networks built by your method fare in comparison to networks built from other methods, like RegEnrich 3 or NetSeekR 4, in terms of biological insights, accuracy, scalability, speed, functionalities and/or memory usage.

o Another angle to judge the regulatory networks would be to check in a case study if the predicted gene interactions between disease and control networks are enriched in disease and gene-gene interactions databases, such as DisGeNet 5.

• Figure 2 needs re-work:

o Panel A and C: text is too small. "tf" should be written TF. "oi" should have another name. These panels might be moved to the supplements.

o Panel D is confusing. Without significance it is hard to understand what the point of this panel is. I can see that certain TFs are cited in the main text but without information about significance, these may seem like cherry-picking. The legends states: Annotation of all TFs in cluster D (columns) to the Reactome parent term. "Immune system" and "Cellular respondes to stimuli" are more consistenly involved in cluster D, in comparison to cluster A.. However, this is a key result which should be shown in a main figure, not in Figure S6. I would also recommend using a -log scale when displaying the p-values to highlight the most significant entries.

o Panel E is quite confusing; first, the color coding is unclear. For instance, what represents blue, purple and red colors? Second, what represents the edges' widths? I would recommend using different shapes for the methylation and expression nodes to reduce the number of colors, and adding a color legend. I would also consider merging the two graphs and representing in color the difference in the edge values so the reader can directly see the key differences.

• Benchmarking analysis could be included to show the runtime and memory requirement for each pipeline step. It would also be beneficial to analyze a larger dataset than colon cancer to assess the scalability.

• Statistical analysis: If computationally feasible, permutation testing could be implemented to quantify the robustness of inferred regulatory interactions. Also, in the method section, it should be clarified that FDR correction was applied for pathway enrichment analysis.

Minor comments:

• I am not sure why duplicate samples are discarded in the pipeline. Why not add counts for RNA-Seq and averaging beta values? I would expect that to yield more robust results.

• It is a bit unclear in what context the NetworkDataCompanion tool could be used outside the workflow. It is also unclear how it helps with quality controls. Please clarify these aspects.

• The manuscript is well-written, but words are sometimes missing or wrongly written, it needs careful re-read.

• The expression '"same-same"' is unclear to me.

• In this sentence: "Some of "same-same" genes (STAT5A, CREB3L1"…, I am not sure in which table or figure I can find this result?

• Text is too small in the Directed Acyclic Graph, especially in Figure S4. Also, I would recommend adding the Directed Acyclic Graphs from Figure S1-S4 to the online documentation.

• Regarding the code, I was puzzled to see a copyConfigFiles process. Also, there are files in bin/r/local_assets, these should be located in assets. And the container for the singularity and docker profile is likely the same, this should be clarified in the code.

• It is recommended to remove the "defaults" channel from the list of channels declared in the containers/conda_envs/analysis.yml file. Please see information about that here https://www.anaconda.com/blog/is-conda-free and here https://www.theregister.com/2024/08/08/anaconda_puts_the_squeeze_on/.

Additional comments (which do not need to be addressed):

• Future work may consider enabling the use of the pipeline to build GRNs from other data sources than TCGA (i.e., nf-netzoo). Recount3 data is already being parsed for GTEx and TCGA samples, so it might be relatively easy to adapt the pipeline so that it can be used on any arbitrary recount3 dataset. Similarly, it could be useful if one could specify a dataset on the recountmethylation database 6 to build GRNs. While these unimodal datasets could not be used with the DRAGON method they would still benefit from all other features of the pipeline.

• Using a nf-core template would enable better structure of the code and increase the visibility of the tool. Also using multiple containers is usually easier to maintain and update than a single large container, especially when a single tool needs to be updated or when modifying part of the pipeline. Another comment is that the code contains many comments which are not to explain the code but more like quick draft which makes the code harder to read by others.

References 1. Padi, M., and Quackenbush, J. (2018). Detecting phenotype-driven transitions in regulatory network structure. npj Syst Biol Appl 4, 1-12. https://doi.org/10.1038/s41540-018-0052-5. 2. Lim, J.T., Chen, C., Grant, A.D., and Padi, M. (2021). Generating Ensembles of Gene Regulatory Networks to Assess Robustness of Disease Modules. Front. Genet. 11. https://doi.org/10.3389/fgene.2020.603264. 3. Tao, W., Radstake, T.R.D.J., and Pandit, A. (2022). RegEnrich gene regulator enrichment analysis reveals a key role of the ETS transcription factor family in interferon signaling. Commun Biol 5, 1-12. https://doi.org/10.1038/s42003-021-02991-5. 4. Srivastava, H., Ferrell, D., and Popescu, G.V. (2022). NetSeekR: a network analysis pipeline for RNA-Seq time series data. BMC Bioinformatics 23, 54. https://doi.org/10.1186/s12859-021-04554-1. 5. Hu, Y., Guo, X., Yun, Y., Lu, L., Huang, X., and Jia, S. (2025). DisGeNet: a disease-centric interaction database among diseases and various associated genes. Database 2025, baae122. https://doi.org/10.1093/database/baae122. 6. Maden, S.K., Walsh, B., Ellrott, K., Hansen, K.D., Thompson, R.F., and Nellore, A. (2023). recountmethylation enables flexible analysis of public blood DNA methylation array data. Bioinformatics Advances 3, vbad020. https://doi.org/10.1093/bioadv/vbad020.

This work has been peer reviewed in GigaScience (see https://doi.org/10.1093/gigascience/giaf118), which carries out open, named peer-review. These reviews are published under a CC-BY 4.0 license and were as follows:

Reviewer 2: Jan Voges

Comments to Author: Synopsis: The manuscript builds on the authors' previous work introducing the SLOW5 format for Oxford Nanopore signal data as an improvement over the FAST5 format. Since then, Oxford Nanopore Technologies (ONT) has introduced its own new format, POD5. This paper directly compares SLOW5 and POD5. The authors claim that SLOW5 provides higher reading speeds for both sequential and random access, writing speeds sufficient to keep pace with data acquisition in sequencing machines, comparable file sizes with no significant storage penalty, a simpler implementation with fewer dependencies. The paper is clearly written, includes extensive supplementary information, and references the source code for all tools used in the experiments. Comments: - Sequential access performance: To me it is unclear whether SLOW5's advantage in sequential access originates from its file layout or from the use of mmap I/O versus traditional I/O. A small ablation study, forcing both SLOW5 and POD5 tools to use the same I/O method on platforms with currently large performance differences, would clarify where the performance gain originates from. - Figure 4: While POD5's dependency structure is indeed more complex than that of slow5lib, the current tree representation exaggerates this complexity. Many common packages (e.g., Python, zlib) appear multiple times as dependency of multiple other packages. A dependency graph where each package appears only once would be a more informative representation. - Figure 5: POD5 versions prior to 0.1.0 appear to be preview releases (and are even marked as such on GitHub). Breaking changes during early previews are normal, so including them in the same visual space as stable versions risks being misleading. - Figure 5: Breaking change at version 0.1.12: The timeline indicates a breaking change at POD5 version 0.1.12 which seems particularly relevant as the latest breaking change after version 0.1.0. However, this change is not reflected in the POD5 compatibility matrix on the right. An explanation of what type of breaking change occurred would clarify its impact and help readers assess compatibility risk. - Random access "walker strategy": A brief explanation comparing it to SLOW5's index-file approach would improve accessibility without requiring readers to consult external documentation.

Reviewer #1 (Public review):

The authors have implemented several clarifications in the text and improved the connection between their findings and previous work. As stated in my initial review, I had no major criticisms of the previous version of the manuscript, and I continue to consider this a solid and well-written study. However, the revised manuscript still largely reiterates existing findings and does not offer novel conceptual or experimental advances. It supports previous conclusions suggesting a likely conserved sex determination locus in aculeate hymenopterans, but does so without functional validation (i.e., via experimental manipulation) of the candidate locus in O. biroi. I also wish to clarify that I did not intend to imply that functional assessments in the Pan et al. study were conducted in more than one focal species; my previous review explicitly states that the locus's functional role was validated in the Argentine ant.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

This study investigates the sex determination mechanism in the clonal ant Ooceraea biroi, focusing on a candidate complementary sex determination (CSD) locus-one of the key mechanisms supporting haplodiploid sex determination in hymenopteran insects. Using whole genome sequencing, the authors analyze diploid females and the rarely occurring diploid males of O. biroi, identifying a 46 kb candidate region that is consistently heterozygous in females and predominantly homozygous in diploid males. This region shows elevated genetic diversity, as expected under balancing selection. The study also reports the presence of an lncRNA near this heterozygous region, which, though only distantly related in sequence, resembles the ANTSR lncRNA involved in female development in the Argentine ant, Linepithema humile (Pan et al. 2024). Together, these findings suggest a potentially conserved sex determination mechanism across ant species. However, while the analyses are well conducted and the paper is clearly written, the insights are largely incremental. The central conclusion - that the sex determination locus is conserved in ants - was already proposed and experimentally supported by Pan et al. (2024), who included O. biroi among the studied species and validated the locus's functional role in the Argentine ant. The present study thus largely reiterates existing findings without providing novel conceptual or experimental advances.

Although it is true that Pan et al., 2024 demonstrated (in Figure 4 of their paper) that the synteny of the region flanking ANTSR is conserved across aculeate Hymenoptera (including O. biroi), Reviewer 1’s claim that that paper provides experimental support for the hypothesis that the sex determination locus is conserved in ants is inaccurate. Pan et al., 2024 only performed experimental work in a single ant species (Linepithema humile) and merely compared reference genomes of multiple species to show synteny of the region, rather than functionally mapping or characterizing these regions.

Other comments:

The mapping is based on a very small sample size: 19 females and 16 diploid males, and these all derive from a single clonal line. This implies a rather high probability for false-positive inference. In combination with the fact that only 11 out of the 16 genotyped males are actually homozygous at the candidate locus, I think a more careful interpretation regarding the role of the mapped region in sex determination would be appropriate. The main argument supporting the role of the candidate region in sex determination is based on the putative homology with the lncRNA involved in sex determination in the Argentine ant, but this argument was made in a previous study (as mentioned above).

Our main argument supporting the role of the candidate region in sex determination is not based on putative homology with the lncRNA in L. humile. Instead, our main argument comes from our genetic mapping (in Fig. 2), and the elevated nucleotide diversity within the identified region (Fig. 4). Additionally, we highlight that multiple genes within our mapped region are homologous to those in mapped sex determining regions in both L. humile and Vollenhovia emeryi, possibly including the lncRNA.

In response to the Reviewer’s assertion that the mapping is based on a small sample size from a single clonal line, we want to highlight that we used all diploid males available to us. Although the primary shortcoming of a small sample size is to increase the probability of a false negative, small sample sizes can also produce false positives. We used two approaches to explore the statistical robustness of our conclusions. First, we generated a null distribution by randomly shuffling sex labels within colonies and calculating the probability of observing our CSD index values by chance (shown in Fig. 2). Second, we directly tested the association between homozygosity and sex using Fisher’s Exact Test (shown in Supplementary Fig. S2). In both cases, the association of the candidate locus with sex was statistically significant after multiple-testing correction using the Benjamini-Hochberg False Discovery Rate. These approaches are clearly described in the “CSD Index Mapping” section of the Methods.

We also note that, because complementary sex determination loci are expected to evolve under balancing selection, our finding that the mapped region exhibits a peak of nucleotide diversity lends orthogonal support to the notion that the mapped locus is indeed a complementary sex determination locus.

The fourth paragraph of the results and the sixth paragraph of the discussion are devoted to explaining the possible reasons why only 11/16 genotyped males are homozygous in the mapped region. The revised manuscript will include an additional sentence (in what will be lines 384-388) in this paragraph that includes the possible explanation that this locus is, in fact, a false positive, while also emphasizing that we find this possibility to be unlikely given our multiple lines of evidence.

In response to Reviewer 1’s suggestion that we carefully interpret the role of the mapped region in sex determination, we highlight our careful wording choices, nearly always referring to the mapped locus as a “candidate sex determination locus” in the title and throughout the manuscript. For consistency, the revised manuscript version will change the second results subheading from “The O. biroi CSD locus is homologous to another ant sex determination locus but not to honeybee csd” to “O. biroi’s candidate CSD locus is homologous to another ant sex determination locus but not to honeybee csd,” and will add the word “candidate” in what will be line 320 at the beginning of the Discussion, and will change “putative” to “candidate” in what will be line 426 at the end of the Discussion.

In the abstract, it is stated that CSD loci have been mapped in honeybees and two ant species, but we know little about their evolutionary history. But CSD candidate loci were also mapped in a wasp with multi-locus CSD (study cited in the introduction). This wasp is also parthenogenetic via central fusion automixis and produces diploid males. This is a very similar situation to the present study and should be referenced and discussed accordingly, particularly since the authors make the interesting suggestion that their ant also has multi-locus CSD and neither the wasp nor the ant has tra homologs in the CSD candidate regions. Also, is there any homology to the CSD candidate regions in the wasp species and the studied ant?

In response to Reviewer 1’s suggestion that we reference the (Matthey-Doret et al. 2019) study in the context of diploid males being produced via losses of heterozygosity during asexual reproduction, the revised manuscript will include (in what will be lines 123-126) the highlighted portion of the following sentence: “Therefore, if O. biroi uses CSD, diploid males might result from losses of heterozygosity at sex determination loci (Fig. 1C), similar to what is thought to occur in other asexual Hymenoptera that produce diploid males (Rabeling and Kronauer 2012; Matthey-Doret et al. 2019).”

We note, however, that in their 2019 study, Matthey-Doret et al. did not directly test the hypothesis that diploid males result from losses of heterozygosity at CSD loci during asexual reproduction, because the diploid males they used for their mapping study came from inbred crosses in a sexual population of that species.

We address this further below, but we want to emphasize that we do not intend to argue that O. biroi has multiple CSD loci. Instead, we suggest that additional, undetected CSD loci is one possible explanation for the absence of diploid males from any clonal line other than clonal line A. In response to Reviewer 1’s suggestion that we reference the (Matthey-Doret et al. 2019) study in the context of multilocus CSD, the revised manuscript version will include the following additional sentence in the fifth paragraph of the discussion (in what will be lines 372-374): “Multi-locus CSD has been suggested to limit the extent of diploid male production in asexual species under some circumstances (Vorburger 2013; Matthey-Doret et al. 2019).”

Regarding Reviewer 2’s question about homology between the putative CSD loci from the (Matthey-Doret et al. 2019) study and O. biroi, we note that there is no homology. The revised manuscript version will have an additional Supplementary Table (which will be the new Supplementary Table S3) that will report the results of this homology search. The revised manuscript will also include the following additional sentence in the Results, in what will be lines 172-174: “We found no homology between the genes within the O. biroi CSD index peak and any of the genes within the putative L. fabarum CSD loci (Supplementary Table S3).”

The authors used different clonal lines of O. biroi to investigate whether heterozygosity at the mapped CSD locus is required for female development in all clonal lines of O. biroi (L187-196). However, given the described parthenogenesis mechanism in this species conserves heterozygosity, additional females that are heterozygous are not very informative here. Indeed, one would need diploid males in these other clonal lines as well (but such males have not yet been found) to make any inference regarding this locus in other lines.

We agree that a full mapping study including diploid males from all clonal lines would be preferable, but as stated earlier in that same paragraph, we have only found diploid males from clonal line A. We stand behind our modest claim that “Females from all six clonal lines were heterozygous at the CSD index peak, consistent with its putative role as a CSD locus in all O. biroi.” In the revised manuscript version, this sentence (in what will be lines 199-201) will be changed slightly in response to a reviewer comment below: “All females from all six clonal lines (including 26 diploid females from clonal line B) were heterozygous at the CSD index peak, consistent with its putative role as a CSD locus in all O. biroi.”

Reviewer #2 (Public review):

The manuscript by Lacy et al. is well written, with a clear and compelling introduction that effectively conveys the significance of the study. The methods are appropriate and well-executed, and the results, both in the main text and supplementary materials, are presented in a clear and detailed manner. The authors interpret their findings with appropriate caution.

This work makes a valuable contribution to our understanding of the evolution of complementary sex determination (CSD) in ants. In particular, it provides important evidence for the ancient origin of a non-coding locus implicated in sex determination, and shows that, remarkably, this sex locus is conserved even in an ant species with a non-canonical reproductive system that typically does not produce males. I found this to be an excellent and well-rounded study, carefully analyzed and well contextualized.

That said, I do have a few minor comments, primarily concerning the discussion of the potential 'ghost' CSD locus. While the authors acknowledge (line 367) that they currently have no data to distinguish among the alternative hypotheses, I found the evidence for an additional CSD locus presented in the results (lines 261-302) somewhat limited and at times a bit difficult to follow. I wonder whether further clarification or supporting evidence could already be extracted from the existing data. Specifically:

We agree with Reviewer 2 that the evidence for a second CSD locus is limited. In fact, we do not intend to advocate for there being a second locus, but we suggest that a second CSD locus is one possible explanation for the absence of diploid males outside of clonal line A. In our initial version, we intentionally conveyed this ambiguity by titling this section “O. biroi may have one or multiple sex determination loci.” However, we now see that this leads to undue emphasis on the possibility of a second locus. In the revised manuscript, we will split this into two separate sections: “Diploid male production differs across O. biroi clonal lines” and “O. biroi lacks a tra-containing CSD locus.”

(1) Line 268: I doubt the relevance of comparing the proportion of diploid males among all males between lines A and B to infer the presence of additional CSD loci. Since the mechanisms producing these two types of males differ, it might be more appropriate to compare the proportion of diploid males among all diploid offspring. This ratio has been used in previous studies on CSD in Hymenoptera to estimate the number of sex loci (see, for example, Cook 1993, de Boer et al. 2008, 2012, Ma et al. 2013, and Chen et al., 2021). The exact method might not be applicable to clonal raider ants, but I think comparing the percentage of diploid males among the total number of (diploid) offspring produced between the two lineages might be a better argument for a difference in CSD loci number.

We want to re-emphasize here that we do not wish to advocate for there being two CSD loci in O. biroi. Rather, we want to explain that this is one possible explanation for the apparent absence of diploid males outside of clonal line A. We hope that the modifications to the manuscript described in the previous response help to clarify this.

Reviewer 2 is correct that comparing the number of diploid males to diploid females does not apply to clonal raider ants. This is because males are vanishingly rare among the vast numbers of females produced. We do not count how many females are produced in laboratory stock colonies, and males are sampled opportunistically. Therefore, we cannot report exact numbers. However, we will add the highlighted portion of the following sentence (in what will be lines 268-270) to the revised manuscript: “Despite the fact that we maintain more colonies of clonal line B than of clonal line A in the lab, all the diploid males we detected came from clonal line A.”

(2) If line B indeed carries an additional CSD locus, one would expect that some females could be homozygous at the ANTSR locus but still viable, being heterozygous only at the other locus. Do the authors detect any females in line B that are homozygous at the ANTSR locus? If so, this would support the existence of an additional, functionally independent CSD locus.

We thank the reviewer for this suggestion, and again we emphasize that we do not want to argue in favor of multiple CSD loci. We just want to introduce it as one possible explanation for the absence of diploid males outside of clonal line A.

The 26 sequenced diploid females from clonal line B are all heterozygous at the mapped locus, and the revised manuscript will clarify this in what will be lines 199-201. Previously, only six of those diploid females were included in Supplementary Table S2, and that will be modified accordingly.

(3) Line 281: The description of the two tra-containing CSD loci as "conserved" between Vollenhovia and the honey bee may be misleading. It suggests shared ancestry, whereas the honey bee csd gene is known to have arisen via a relatively recent gene duplication from fem/tra (10.1038/nature07052). It would be more accurate to refer to this similarity as a case of convergent evolution rather than conservation.

In the sentence that Reviewer 2 refers to, we are representing the assertion made in the (Miyakawa and Mikheyev 2015) paper in which, regarding their mapping of a candidate CSD locus that contains two linked tra homologs, they write in the abstract: “these data support the prediction that the same CSD mechanism has indeed been conserved for over 100 million years.” In that same paper, Miyakawa and Mikheyev write in the discussion section: “As ants and bees diverged more than 100 million years ago, sex determination in honey bees and V. emeryi is probably homologous and has been conserved for at least this long.”

As noted by Reviewer 2, this appears to conflict with a previously advanced hypothesis: that because fem and csd were found in Apis mellifera, Apis cerana, and Apis dorsata, but only fem was found in Mellipona compressipes, Bombus terrestris, and Nasonia vitripennis, that the csd gene evolved after the honeybee (Apis) lineage diverged from other bees (Hasselmann et al. 2008). However, it remains possible that the csd gene evolved after ants and bees diverged from N. vitripennis, but before the divergence of ants and bees, and then was subsequently lost in B. terrestris and M. compressipes. This view was previously put forward based on bioinformatic identification of putative orthologs of csd and fem in bumblebees and in ants [(Schmieder et al. 2012), see also (Privman et al. 2013)]. However, subsequent work disagreed and argued that the duplications of tra found in ants and in bumblebees represented convergent evolution rather than homology (Koch et al. 2014). Distinguishing between these possibilities will be aided by additional sex determination locus mapping studies and functional dissection of the underlying molecular mechanisms in diverse Aculeata.

Distinguishing between these competing hypotheses is beyond the scope of our paper, but the revised manuscript will include additional text to incorporate some of this nuance. We will include these modified lines below (in what will be lines 287-295), with the additions highlighted:

“A second QTL region identified in V. emeryi (V.emeryiCsdQTL1) contains two closely linked tra homologs, similar to the closely linked honeybee tra homologs, csd and fem (Miyakawa and Mikheyev 2015). This, along with the discovery of duplicated tra homologs that undergo concerted evolution in bumblebees and ants (Schmieder et al. 2012; Privman et al. 2013) has led to the hypothesis that the function of tra homologs as CSD loci is conserved with the csd-containing region of honeybees (Schmieder et al. 2012; Miyakawa and Mikheyev 2015). However, other work has suggested that tra duplications occurred independently in honeybees, bumblebees, and ants (Hasselmann et al. 2008; Koch et al. 2014), and it remains to be demonstrated that either of these tra homologs acts as a primary CSD signal in V. emeryi.”

(4) Finally, since the authors successfully identified multiple alleles of the first CSD locus using previously sequenced haploid males, I wonder whether they also observed comparable allelic diversity at the candidate second CSD locus. This would provide useful supporting evidence for its functional relevance.

As is already addressed in the final paragraph of the results and in Supplementary Fig. S4, there is no peak of nucleotide diversity in any of the regions homologous to V.emeryiQTL1, which is the tra-containing candidate sex determination locus (Miyakawa and Mikheyev 2015). In the revised manuscript, the relevant lines will be 307-310. We want to restate that we do not propose that there is a second candidate CSD locus in O. biroi, but we simply raise the possibility that multi-locus CSD *might* explain the absence of diploid males from clonal lines other than clonal line A (as one of several alternative possibilities).

Overall, these are relatively minor points in the context of a strong manuscript, but I believe addressing them would improve the clarity and robustness of the authors' conclusions.

Reviewer #3 (Public review):

Summary:

The sex determination mechanism governed by the complementary sex determination (CSD) locus is one of the mechanisms that support the haplodiploid sex determination system evolved in hymenopteran insects. While many ant species are believed to possess a CSD locus, it has only been specifically identified in two species. The authors analyzed diploid females and the rarely occurring diploid males of the clonal ant Ooceraea biroi and identified a 46 kb CSD candidate region that is consistently heterozygous in females and predominantly homozygous in males. This region was found to be homologous to the CSD locus reported in distantly related ants. In the Argentine ant, Linepithema humile, the CSD locus overlaps with an lncRNA (ANTSR) that is essential for female development and is associated with the heterozygous region (Pan et al. 2024). Similarly, an lncRNA is encoded near the heterozygous region within the CSD candidate region of O. biroi. Although this lncRNA shares low sequence similarity with ANTSR, its potential functional involvement in sex determination is suggested. Based on these findings, the authors propose that the heterozygous region and the adjacent lncRNA in O. biroi may trigger female development via a mechanism similar to that of L. humile. They further suggest that the molecular mechanisms of sex determination involving the CSD locus in ants have been highly conserved for approximately 112 million years. This study is one of the few to identify a CSD candidate region in ants and is particularly noteworthy as the first to do so in a parthenogenetic species.

Strengths:

(1) The CSD candidate region was found to be homologous to the CSD locus reported in distantly related ant species, enhancing the significance of the findings.

(2) Identifying the CSD candidate region in a parthenogenetic species like O. biroi is a notable achievement and adds novelty to the research.

Weaknesses

(1) Functional validation of the lncRNA's role is lacking, and further investigation through knockout or knockdown experiments is necessary to confirm its involvement in sex determination.

See response below.

(2) The claim that the lncRNA is essential for female development appears to reiterate findings already proposed by Pan et al. (2024), which may reduce the novelty of the study.

We do not claim that the lncRNA is essential for female development in O. biroi, but simply mention the possibility that, as in L. humile, it is somehow involved in sex determination. We do not have any functional evidence for this, so this is purely based on its genomic position immediately adjacent to our mapped candidate region. We agree with the reviewer that the study by Pan et al. (2024) decreases the novelty of our findings. Another way of looking at this is that our study supports and bolsters previous findings by partially replicating the results in a different species.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

L307-308 should state homozygous for either allele in THE MAJORITY of diploid males.

This will be fixed in the revised manuscript, in what will be line 321.

Reviewer #3 (Recommendations for the authors):

The association between heterozygosity in the CSD candidate region and female development in O. biroi, along with the high sequence homology of this region to CSD loci identified in two distantly related ant species, is not sufficient to fully address the evolution of the CSD locus and the mechanisms of sex determination.

Given that functional genetic tools, such as genome editing, have already been established in O. biroi, I strongly recommend that the authors investigate the role of the lncRNA through knockout or knockdown experiments and assess its impact on the sex-specific splicing pattern of the downstream tra gene.

Although knockout experiments of the lncRNA would be illuminating, the primary signal of complementary sex determination is heterozygosity. As is clearly stated in our manuscript and that of (Pan et al. 2024), it does not appear to be heterozygosity within the lncRNA that induces female development, but rather heterozygosity in non-transcribed regions linked to the lncRNA. Therefore, future mechanistic studies of sex determination in O. biroi, L. humile, and other ants should explore how homozygosity or heterozygosity of this region impacts the sex determination cascade, rather than focusing (exclusively) on the lncRNA.

With this in mind, we developed three sets of guide RNAs that cut only one allele within the mapped CSD locus, with the goal of producing deletions within the highly variable region within the mapped locus. This would lead to functional hemizygosity or homozygosity within this region, depending on how the cuts were repaired. We also developed several sets of PCR primers to assess the heterozygosity of the resultant animals. After injecting 1,162 eggs over several weeks and genotyping the hundreds of resultant animals with PCR, we confirmed that we could induce hemizygosity or homozygosity within this region, at least in ~1/20 of the injected embryos. Although it is possible to assess the sex-specificity of the splice isoform of tra as a proxy for sex determination phenotypes (as done by (Pan et al. 2024)), the ideal experiment would assess male phenotypic development at the pupal stage. Therefore, over several more weeks, we injected hundreds more eggs with these reagents and reared the injected embryos to the pupal stage. However, substantial mortality was observed, with only 12 injected eggs developing to the pupal stage. All of these were female, and none of them had been successfully mutated.

In conclusion, we agree with the reviewer that functional experiments would be useful, and we made extensive attempts to conduct such experiments. However, these experiments turned out to be extremely challenging with the currently available protocols. Ultimately, we therefore decided to abandon these attempts.  

We opted not to include these experiments in the paper itself because we cannot meaningfully interpret their results. However, we are pleased that, in this response letter, we can include a brief description for readers interested in attempting similar experiments.

Since O. biroi reproduces parthenogenetically and most offspring develop into females, observing a shift from female- to male-specific splicing of tra upon early embryonic knockout of the lncRNA would provide much stronger evidence that this lncRNA is essential for female development. Without such functional validation, the authors' claim (lines 36-38) seems to reiterate findings already proposed by Pan et al. (2024) and, as such, lacks sufficient novelty.

We have responded to the issue of “lack of novelty” above. But again, the actual CSD locus in both O. biroi and L. humile appears to be distinct from (but genetically linked to) the lncRNA, and we have no experimental evidence that the putative lncRNA in O. biroi is involved in sex determination at all. Because of this, and given the experimental challenges described above, we do not currently intend to pursue functional studies of the lncRNA.

References

Hasselmann M, Gempe T, Schiøtt M, Nunes-Silva CG, Otte M, Beye M. 2008. Evidence for the evolutionary nascence of a novel sex determination pathway in honeybees. Nature 454:519–522.

Koch V, Nissen I, Schmitt BD, Beye M. 2014. Independent Evolutionary Origin of fem Paralogous Genes and Complementary Sex Determination in Hymenopteran Insects. PLOS ONE 9:e91883.

Matthey-Doret C, van der Kooi CJ, Jeffries DL, Bast J, Dennis AB, Vorburger C, Schwander T. 2019. Mapping of multiple complementary sex determination loci in a parasitoid wasp. Genome Biology and Evolution 11:2954–2962.

Miyakawa MO, Mikheyev AS. 2015. QTL mapping of sex determination loci supports an ancient pathway in ants and honey bees. PLOS Genetics 11:e1005656.

Pan Q, Darras H, Keller L. 2024. LncRNA gene ANTSR coordinates complementary sex determination in the Argentine ant. Science Advances 10:eadp1532.

Privman E, Wurm Y, Keller L. 2013. Duplication and concerted evolution in a master sex determiner under balancing selection. Proceedings of the Royal Society B: Biological Sciences 280:20122968.

Rabeling C, Kronauer DJC. 2012. Thelytokous parthenogenesis in eusocial Hymenoptera. Annual Review of Entomology 58:273–292.

Schmieder S, Colinet D, Poirié M. 2012. Tracing back the nascence of a new sex-determination pathway to the ancestor of bees and ants. Nature Communications 3:1–7.

Vorburger C. 2013. Thelytoky and Sex Determination in the Hymenoptera: Mutual Constraints. Sexual Development 8:50–58.

téměř

Bylo by lepší dát sem nejdřív nějaký přehled, o jaké výdaje se jedná, jaký mají vztah k bydlení, jaký resort to má na starosti. Čtenář by se pak lépe zorientoval v tom grafu. (mj. tápu v tom propojení resort/typ výdaje: bylo by vhodné to více vysvětlit právě úvodním podrobnějším popisem).

Author response:

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

Reviewer #1 (Public Review):

In the current article, Octavia Soegyono and colleagues study "The influence of nucleus accumbens shell D1 and D2 neurons on outcome-specific Pavlovian instrumental transfer", building on extensive findings from the same lab. While there is a consensus about the specific involvement of the Shell part of the Nucleus Accumbens (NAc) in specific stimulus-based actions in choice settings (and not in General Pavlovian instrumental transfer - gPIT, as opposed to the Core part of the NAc), mechanisms at the cellular and circuitry levels remain to be explored. In the present work, using sophisticated methods (rat Cre-transgenic lines from both sexes, optogenetics, and the well-established behavioral paradigm outcome-specific PIT-sPIT), Octavia Soegyono and colleagues decipher the diNerential contribution of dopamine receptors D1 and D2 expressing spiny projection neurons (SPNs). 

After validating the viral strategy and the specificity of the targeting (immunochemistry and electrophysiology), the authors demonstrate that while both NAc Shell D1- and D2SPNs participate in mediating sPIT, NAc Shell D1-SPNs projections to the Ventral Pallidum (VP, previously demonstrated as crucial for sPIT), but not D2-SPNs, mediates sPIT. They also show that these eNects were specific to stimulus-based actions, as valuebased choices were left intact in all manipulations. 

This is a well-designed study, and the results are well supported by the experimental evidence. The paper is extremely pleasant to read and adds to the current literature.

We thank the Reviewer for their positive assessment. 

Reviewer 2 (Public Review):

Summary: 

This manuscript by Soegyono et al. describes a series of experiments designed to probe the involvement of dopamine D1 and D2 neurons within the nucleus accumbens shell in outcome-specific Pavlovian-instrumental transfer (osPIT), a well-controlled assay of cueguided action selection based on congruent outcome associations. They used an optogenetic approach to phasically silence NAc shell D1 (D1-Cre mice) or D2 (A2a-Cre mice) neurons during a subset of osPIT trials. Both manipulations disrupted cue-guided action selection but had no eNects on negative control measures/tasks (concomitant approach behavior, separate valued guided choice task), nor were any osPIT impairments found in reporter-only control groups. Separate experiments revealed that selective inhibition of NAc shell D1 but not D2 inputs to ventral pallidum was required for osPIT expression, thereby advancing understanding of the basal ganglia circuitry underpinning this important aspect of decision making.

Strengths: 

The combinatorial viral and optogenetic approaches used here were convincingly validated through anatomical tract-tracing and ex vivo electrophysiology. The behavioral assays are sophisticated and well-controlled to parse cue and value-guided action selection. The inclusion of reporter-only control groups is rigorous and rules out nonspecific eNects of the light manipulation. The findings are novel and address a critical question in the literature. Prior work using less decisive methods had implicated NAc shell D1 neurons in osPIT but suggested that D2 neurons may not be involved. The optogenetic manipulations used in the current study provide a more direct test of their involvement and convincingly demonstrate that both populations play an important role. Prior work had also implicated NAc shell connections to ventral pallidum in osPIT, but the current study reveals the selective involvement of D1 but not D2 neurons in this circuit. The authors do a good job of discussing their findings, including their nuanced interpretation that NAc shell D2 neurons may contribute to osPIT through their local regulation of NAc shell microcircuitry. 

We thank the Reviewer for their positive assessment. 

Weaknesses: 

The current study exclusively used an optogenetic approach to probe the function of D1 and D2 NAc shell neurons. Providing a complementary assessment with chemogenetics or other appropriate methods would strengthen conclusions, particularly the novel demonstration of D2 NAc shell involvement. Likewise, the null result of optically inhibiting D2 inputs to the ventral pallidum leaves open the possibility that a more complete or sustained disruption of this pathway may have impaired osPIT.

We acknowledge the reviewer's valuable suggestion that demonstrating NAc-S D1- and D2-SPNs engagement in outcome-specific PIT through another technique would strengthen our optogenetic findings. Several approaches could provide this validation. Chemogenetic manipulation, as the reviewer suggested, represents one compelling option. Alternatively, immunohistochemical assessment of phosphorylated histone H3 at serine 10 (P-H3) oMers another promising avenue, given its established utility in reporting striatal SPNs plasticity in the dorsal striatum (Matamales et al., 2020). We hope to complete such an assessment in future work since it would address the limitations of previous work that relied solely on ERK1/2 phosphorylation measures in NAc-S SPNs (Laurent et al., 2014). The manuscript was modified to report these future avenues of research (page 12). 

Regarding the null result from optical silencing of D2 terminals in the ventral pallidum, we agree with the reviewer's assessment. While we acknowledge this limitation in the current manuscript (page 13), we aim to address this gap in future studies to provide a more complete mechanistic understanding of the circuit.

Reviewer 3 (Public Review):

Summary:

The authors present data demonstrating that optogenetic inhibition of either D1- or D2MSNs in the NAc Shell attenuates expression of sensory-specific PIT while largely sparing value-based decision on an instrumental task. They also provide evidence that SS-PIT depends on D1-MSN projections from the NAc-Shell to the VP, whereas projections from D2-MSNs to the VP do not contribute to SS-PIT.

Strengths:

This is clearly written. The evidence largely supports the authors' interpretations, and these eNects are somewhat novel, so they help advance our understanding of PIT and NAc-Shell function.

We thank the Reviewer for their positive assessment. 

Weaknesses:

I think the interpretation of some of the eNects (specifically the claim that D1-MSNs do not contribute to value-based decision making) is not fully supported by the data presented.

We appreciate the reviewer's comment regarding the marginal attenuation of valuebased choice observed following NAc-S D1-SPN silencing. While this manipulation did produce a slight reduction in choice performance, the behavior remained largely intact. We are hesitant to interpret this marginal eMect as evidence for a direct role of NAc-S D1SPNs in value-based decision-making, particularly given the substantial literature demonstrating that NAc-S manipulations typically preserve such choice behavior (Corbit et al., 2001; Corbit & Balleine, 2011; Laurent et al., 2012). Furthermore, previous work has shown that NAc-S D1 receptor blockade impairs outcome-specific PIT while leaving value-based choice unaMected (Laurent et al., 2014). We favor an alternative explanation for our observed marginal reduction. As documented in Supplemental Figure 1, viral transduction extended slightly into the nucleus accumbens core (NAc-C), a region established as critical for value-based decision-making (Corbit et al., 2001; Corbit & Balleine, 2011; Laurent et al., 2012; Parkes et al., 2015). The marginal impairment may therefore reflect inadvertent silencing of a small number of  NAc-C D1-SPNs rather than a functional contribution from NAc-S D1-SPNs. Future studies specifically targeting larger NAc-C D1-SPN populations would help clarify this possibility and provide definitive resolution of this question.

Reviewer 1 (Recommendations for the Author):

My main concerns and comments are listed below.

(1) Could the authors provide the "raw" data of the PIT tests, such as PreSame vs Same vs PreDiNerent vs DiNerent? Could the authors clarify how the Net responding was calculated? Was it Same minus PreSame & DiNerent minus PreDiNerent, or was the average of PreSame and PreDiNerent used in this calculation?

The raw data for PIT testing across all experiments are now included in the Supplemental Figures (Supplemental Figures S1E, S2E, S3E, and S4E). Baseline responding was quantified as the average number of lever presses per minute for both actions during the two-minute period (i.e., average of PreSame and PreDiMerent) preceding each stimulus presentation. This methodology has been clarified in the revised manuscript (page 7).

(2) While both sexes are utilized in the current study, no statistical analysis is provided. Can the authors please comment on this point and provide these analyses (for both training and tests)?

As noted in the original manuscript, the final sample sizes for female and male rats were insuMicient to provide adequate statistical power for sex-based analyses (page 15). To address this limitation, we have now cited a previous study from our laboratory (Burton et al., 2014) that conducted such analyses with suMicient power in identical behavioural tasks. That study identified only marginal sex diMerences in performance, with female rats exhibiting slightly higher magazine entry rates during Pavlovian conditioning. Importantly, no diMerences were observed in outcome-specific PIT or value-based choice performance between sexes.

(3) Regarding Figure 1 - Anterograde tracing in D1-Cre and A2a-Cre rats (from line 976), I have one major and one minor question:

(3.1) I do not understand the rationale of showing anterograde tracing from the Dorsal Striatum (DS) as this region is not studied in the current work. Moreover, sagittal micrographs of D1-Cre and A2a-Cre would be relevant here. Could the authors please provide these micrographs and explain the rationale for doing tracing in DS?

We included dorsal striatum (DS) tracing data as a reference because the projection patterns of D1 and D2 SPNs in this region are well-established and extensively characterized, in contrast to the more limited literature on these cell types in the NAc-S. Regarding the comment about sagittal micrographs, we are uncertain of the specific concern as these images are presented in Figure 1B.

If the reviewer is requesting sagittal micrographs for NAc-S anterograde tracing, we did not employ this approach because: (1) the NAc-S and ventral pallidum are anatomically adjacent regions and (2) the medial-lateral coordinates of the ventral pallidum and lateral hypothalamus do not align optimally with those of the NAc-S, limiting the utility of sagittal analysis for these projections.

(3.2) There is no description about how the quantifications were done: manually? Automatically? What script or plugin was used? If automated, what were the thresholding conditions? How many brain sections along the anteroposterior axis? What was the density of these subpopulations? Can the authors include a methodological section to address this point?

We apologize for the omission of quantification methods used to assess viral transduction specificity. This methodological description has now been added to the revised manuscript (page 22). Briefly, we employed a manual procedure in two sections per rat, and cell counts were completed in a defined region of interest located around the viral infusion site.

(4) Lex A & Hauber (2008) Dopamine D1 and D2 receptors in the nucleus accumbens core and shell mediate Pavlovian-instrumental transfer. Learning & memory 15:483- 491, should be cited and discussed. It also seems that the contribution of the main dopaminergic source of the brain, the ventral tegmental area, is not cited, while it has been investigated in PIT in at least 3 studies regarding sPIT only, notably the VP-VTA pathway (Leung & Balleine 2015, accurately cited already).

We did not include the Lex & Hauber (2008) study because its experimental design (single lever and single outcome) prevents diMerentiation between the eMects of Pavlovian stimuli on action performance (general PIT) versus action selection (outcome-specific PIT, as examined in the present study). Drawing connections between their findings and our results would require speculative interpretations regarding whether their observed eMects reflect general or outcome-specific PIT mechanisms, which could distract from the core findings reported in the article.

Several studies examining the role of the VTA in outcome-specific PIT were referenced in the manuscript's introduction. Following the reviewer's recommendation, these references have also been incorporated into the discussion section (page 13). 

(5) While not directly the focus of this study, it would be interesting to highlight the accumbens dissociation between General vs Specific PIT, and how the dopaminergic system (diNerentially?) influences both forms of PIT.

We agree with the reviewer that the double dissociation between nucleus accumbens core/shell function and general/specific PIT is an interesting topic. However, the present manuscript does not examine this dissociation, the nucleus accumbens core, or general PIT. Similarly, our study does not directly investigate the dopaminergic system per se. We believe that discussing these topics would distract from our core findings and substantially increase manuscript length without contributing novel data directly relevant to these areas. 

(6) While authors indicate that conditioned response to auditory stimuli (magazine visits) are persevered in all groups, suggesting intact sensitivity to the general motivational properties of reward-predictive stimuli (lines 344, 360), authors can't conclude about the specificity of this behavior i.e. does the subject use a mental representation of O1 when experiencing S1, leading to a magazine visits to retrieve O1 (and same for S2-O2), or not? Two food ports would be needed to address this question; also, authors should comment on the fact that competition between instrumental & pavlovian responses does not explain the deficits observed.

We agree with the Reviewer that magazine entry data cannot be used to draw conclusions about specificity, and we do not make such claims in our manuscript. We are therefore unclear about the specific concern being raised. Following the Reviewer’s recommendation, we have commented on the fact that response competition could not explain the results obtained (page 11, see also supplemental discussion). 

The minor comments are listed below.

(7) A high number of rats were excluded (> 32 total), and the number of rats excluded for NAc-S D1-SPNs-VP is not indicated.

We apologize for omitting the number of rats excluded from the experiment examining NAc-S D1-SPN projections to the ventral pallidum. This information has been added to the revised manuscript (page 22).

(7.1) Can authors please comment on the elevated number of exclusions?

A total of 133 rats were used across the reported experiments, with 40 rats excluded based on post-mortem analyses. This represents an attrition rate of approximately 30%, which we consider reasonable given that most animals received two separate viral infusions and two separate fiber-optic cannula implantations, and that the inclusion of both female and male rats contributed to some variability in coordinates and so targeting. 

(7.2) Can authors please present the performance of these animals during the tasks (OFF conditions, and for control ones, both ON & OFF conditions)?

Rats were excluded after assessing the spread of viral infusions, placement of fibre-optic cannulas and potential damage due to the surgical procedures (page 21). The requested data are presented below and plotted in the same manner as in Figures 3-6. The pattern of performance in excluded animals was highly variable. 

Author response image 1.

(8) For tracing, only males were used, and for electrophysiology, only females were used.

(8.1) Can authors please comment on not using both sexes in these experiments? 

We agree that equal allocation of female and male rats in the experiments presented in Figures 1-2 would have been preferable. Animal availability was the sole factor determining these allocations. Importantly, both female and male D1-Cre and A2A-Cre rats were used for the NAc-S tracing studies, and no sex diMerences were observed in the projection patterns. The article describing the two transgenic lines of rats did not report any sex diMerence (Pettibone et al., 2019). 

(8.2) Is there evidence in the literature that the electrophysiological properties of female versus male SPNs could diNer?

The literature indicates that there is no sex diMerence in the electrophysiological properties of NAc-S SPNs (Cao et al., 2018; Willett et al., 2016).  

(8.3) It seems like there is a discrepancy between the number of animals used as presented in the Figure 2 legend versus what is described in the main text. In the Figure legend, I understand that 5 animals were used for D1-Cre/DIO-eNpHR3.0 validation, and 7 animals for A2a-Cre/DIO-eNpHR3.0; however, the main text indicates the use of a total of 8 animals instead of the 12 presented in the Figure legend. Can authors please address this mismatch or clarify?

The number of rats reported in the main text and Figure 2 legend was correct. However, recordings sometimes involved multiple cells from the same animal, and this aspect of the data was incorrectly reported and generated confusion. We have clarified the numbers in both the main text and Figure 2 legend to distinguish between animal counts and cell counts. 

(9) Overall, in the study, have the authors checked for outliers?

Performance across all training and testing stages was inspected to identify potential behavioral outliers in each experiment. Abnormal performance during a single session within a multi-session stage was not considered suMicient grounds for outlier designation. Based on these criteria, no subjects remaining after post-mortem analyses exhibited performance patterns warranting exclusion through statistical outlier analysis. However, we have conducted the specific analyses requested by the Reviewer, as described below. 

(9.1) In Figure 3, it seems that one female in the eYFP group, in the OFF situation, for the diNerent condition, has a higher level of responding than the others. Can authors please confirm or refute this visual observation with the appropriate statistical analysis?

Statistical analysis (z-score) confirmed the reviewer's observation regarding responding of the diMerent action in the OFF condition for this subject (|z| = 2.58). Similar extreme responding was observed in the ON condition (|z| = 2.03). Analyzing responding on the diMerent action in isolation is not informative in the context of outcome-specific PIT. Additional analyses revealed |z| < 2 when examining the magnitude of choice discrimination in outcome-specific PIT (i.e., net same versus net diMerent responding) in both ON and OFF conditions. Furthermore, this subject showed |z| < 2 across all other experimental stages. Based on these analyses, we conclude that the subject should be kept in all analyses. 

(9.2) In Figure 5, it seems that one male, in the ON situation, in the diNerent condition, has a quite higher level of responding - is this subject an outlier? If so, how does it aNect the statistical analysis after being removed? And who is this subject in the OFF condition?

The reviewer has identified two diMerent male rats infused with the eNpHR3.0 virus and has asked closer examination of their performance.

The first rat showed outlier-level responding on the diMerent action in the ON condition (|z| = 2.89) but normal responding for all other measures across LED conditions (|z| < 2). Additional analyses revealed |z| = 2.55 when examining choice discrimination magnitude in outcome-specific PIT during the ON condition but not during the OFF condition (|z| = 0.62). This subject exhibited |z| < 2 across all other experimental stages.

The second rat showed outlier-level responding on the same action in the OFF condition (|z| = 2.02) but normal responding for all other measures across LED conditions (|z| < 2). Additional analyses revealed |z| = 2.12 when examining choice discrimination magnitude in outcome-specific PIT during the OFF condition but not during the ON condition (|z| = 0.67). This subject also exhibited |z| < 2 across all other experimental stages.

We excluded these two subjects and conducted the same analyses as described in the original manuscript. Baseline responding did not diMer between groups (p = 0.14), allowing to look at the net eMect of the stimuli. Overall lever presses were greater in the eYFP rats (Group: F(1,16) = 6.08, p < 0.05; η² = 0.28) and were reduced by LED activation (LED: F(1,16) = 9.52, p < 0.01; η² = 0.44) and this reduction depended on the group considered (Group x LED: F(1,16) = 12.125, p < 0.001; η² = 0.43). Lever press rates were higher on the action earning the same outcome as the stimuli compared to the action earning the diMerent outcome (Lever: F(1,16)= 49.32; η² = 0.76; p < 0.001), regardless of group (Group x Lever: p = 0.14). There was a Lever by LED light condition interaction (Lever x LED: F(1,16)= 5.25; η² = 0.24; p < 0.05) but no an interaction between group, LED light condition, and Lever during the presentation of the predictive stimuli (p = 0.10). Given the significant Group x LED and Lever x LED interactions, additional analyses were conducted to determine the source of these interactions. In eYFP rats, LED activation had no eMect (LED: p = 0.70) and lever presses were greater on the same action (Lever: (F(1,9) = 23.94, p < 0.001; η² = 0.79) regardless of LED condition (LED x Lever: p = 0.72). By contrast, in eNpHR3.0 rats, lever presses were reduced by LED activation (LED: F(1,9) = 23.97, p < 0.001; η² = 0.73), were greater on the same action (Lever: F(1,9) = 16.920, p < 0.001; η² = 0.65) and the two factors interacted (LED x Lever: F(1,9) = 9.12, p < 0.01; η² = 0.50). These rats demonstrated outcome-specific PIT in the OFF condition (F(1,9) = 27.26, p < 0.001; η² = 0.75) but not in the ON condition (p = 0.08).

Overall, excluding these two rats altered the statistical analyses, but both the original and revised analyses yielded the same outcome: silencing the NAc-S D1-SPN to VP pathway disrupted PIT. More importantly, we do not believe there are suMicient grounds to exclude the two rats identified by the reviewer. These animals did not display outlier-level responding across training stages or during the choice test. Their potential classification as outliers would be based on responding during only one LED condition and not the other, with notably opposite patterns between the two rats despite belonging to the same experimental group. 

(10) I think it would be appreciable if in the cartoons from Figure 5.A and 6.A, the SPNs neurons were color-coded as in the results (test plots) and the supplementary figures (histological color-coding), such as D1- in blue & D2-SPNs in red.

Our current color-coding system uses blue for D1-SPNs transduced with eNpHR3.0 and red for D2-SPNs transduced with eNpHR3.0. The D1-SPNs and D2-SPNs shown in Figures 5A and 6A represent cells transduced with either eYFP (control) or eNpHR3.0 virus and therefore cannot be assigned the blue or red color, which is reserved for eNpHR3.0transduced cells specifically. The micrographs in the Supplemental Figures maintain consistency with the color-coding established in the main figures.

(11) As there are (relatively small) variations in the control performance in term of Net responding (from ~3 to ~7 responses per min), I wonder what would be the result of pooling eYFP groups from the two first experiments (Figures 3 & 4) and from the two last ones (Figures 5 & 6) - would the same statically results stand or vary (as eYFP vs D1-Cre vs A2a-Cre rats)? In particular for Figures 3 & 4, with and without the potential outlier, if it's indeed an outlier.

We considered the Reviewer’s recommendation but do not believe the requested analysis is appropriate. The Reviewer is requesting the pooling of data from subjects of distinct transgenic strains (D1-Cre and A2A-Cre rats) that underwent surgical and behavioral procedures at diMerent time points, sometimes months apart. Each experiment was designed with necessary controls to enable adequate statistical analyses for testing our specific hypotheses. 

(12) Presence of cameras in operant cages is mentioned in methods, but no data is presented regarding recordings, though authors mention that they allow for real-time observations of behavior. I suggest removing "to record" or adding a statement about the fact that no videos were recorded or used in the present study.

We have removed “to record” from the manuscript (page 18). 

(13) In all supplementary Figures, "F" is wrongly indicated as "E".

We thank the Reviewer for reporting these errors, which have been corrected. 

(14) While the authors acknowledge that the eNicacy of optogenetic inhibition of terminals is questionable, I think that more details are required to address this point in the discussion (existing literature?). Maybe, the combination of an anterograde tracer from SPNs to VP, to label VP neurons (to facilitate patching these neurons), and the Credependent inhibitory opsin in the NAc Shell, with optogenetic illumination at the level of the VP, along with electrophysiological recordings of VP neurons, could help address this question but may, reasonably, seem challenging technically.

Our manuscript does not state that optogenetic inhibition of terminals is questionable. It acknowledges that we do not provide any evidence about the eMicacy of the approach. Regardless, we have provided additional details and suggestions to address this lack of evidence (page 13). 

(15) A nice addition could be an illustration of the proposed model (from line 374), but it may be unnecessary.

We have carefully considered the reviewer's recommendation. The proposed model is detailed in three published articles, including one that is freely accessible, which we have cited when presenting the model in our manuscript (page 14). This reference should provide interested readers with easy access to a comprehensive illustration of the model.

Reviewer 2 (Recommendations for the Author):

As noted in my public comments, this is a truly excellent and compelling study. I have only a few minor comments.

(1) I could not find the coordinates/parameters for the dorsal striatal AAV injections for that component of the tract tracing experiment.

We apologize for this omission, which has now been corrected (page 16). 

(2) Please add the final group sizes to the figure captions.

We followed the Reviewer’s recommendation and added group sizes in the main figure captions. 

(3) The discussion of group exclusions (p 21 line 637) seems to accidentally omit (n = X) the number of NAc-S D1-SPNs-VP mice excluded.

We apologize for this omission, which has now been corrected (page 22). 

(4) There were some labeling issues in the supplementary figures (perhaps elsewhere, too). Specifically, panel E was listed twice (once for F) in captions.

We apologize for this error, which has now been corrected.  

(5) Inspection of the magazine entry data from PIT tests suggests that the optogenetic manipulations may have had some eNects on this behavior and would encourage the authors to probe further. There was a significant group diNerence for D1-SPN inhibition and a marginal group eNect for D2-SPNs. The fact that these eNects were in opposite directions is intriguing, although not easily interpreted based on the canonical D1/D2 model. Of course, the eNects are not specific to the light-on trials, but this could be due to carryover into light-oN trials. An analysis of trial-order eNects seems crucial for interpreting these eNects. One might also consider normalizing for pre-test baseline performance. Response rates during Pavlovian conditioning seem to suggest that D2eNpHR mice showed slightly higher conditioned responding during training, which contrasts with their low entry rates at test. I don't see any of this as problematic -- but more should be done to interpret these findings.

We thank the reviewer for raising this interesting point regarding magazine entry rates. Since these data are presented in the Supplemental Figures, we have added a section in the Supplemental Material file that elaborates on these findings. This section does not address trial order eMects, as trial order was fully counterbalanced in our experiments and the relevant statistical analyses would lack adequate power. Baseline normalization was not conducted because the reviewer's suggestion was based on their assumption that eNpHR3.0 rats in the D2-SPNs experiment showed slightly higher magazine entries during Pavlovian training. However, this was not the case. In fact, like the eNpHR3.0 rats in the D1-SPNs experiment, they tended to display lower magazine entries during training. The added section therefore focuses on the potential role of response competition during outcome-specific PIT tests. Although we concluded that response competition cannot explain our findings, we believe it may complicate interpretation of magazine entry behavior. Thus, we recommend that future studies examine the role of NAc-S SPNs using purely Pavlovian tasks. It is worth nothing that we have recently completed experiments (unpublished) examining NAc-S D1- and D2-SPN silencing during stimulus presentation in a Pavlovian task identical to the one used here. Silencing of either SPN population had no eMect on magazine entry behavior.

Reviewer 3 (Recommendations for the Author):

Broad comments:

Throughout the manuscript, the authors draw parallels between the eNect established via pharmacological manipulations and those shown here with optogenetic manipulation. I understand using the pharmacological data to launch this investigation, but these two procedures address very diNerent physiological questions. In the case of a pharmacological manipulation, the targets are receptors, wherever they are expressed, and in the case of D2 receptors, this means altering function in both pre-synaptically expressed autoreceptors and post-synaptically expressed D2 MSN receptors. In the case of an optogenetic approach, the target is a specific cell population with a high degree of temporal control. So I would just caution against comparing results from these types of studies too closely.

Related to this point is the consideration of the physiological relevance of the manipulation. Under normal conditions, dopamine acts at D1-like receptors to increase the probability of cell firing via Ga signaling. In contrast, dopamine binding of D2-like receptors decreases the cell's firing probability (signaling via Gi/o). Thus, shunting D1MSN activation provides a clear impression of the role of these cells and, putatively, the role of dopamine acting on these cells. However, inhibiting D2-MSNs more closely mimics these cells' response to dopamine (though optogenetic manipulations are likely far more impactful than Gi signaling). All this is to say that when we consider the results presented here in Experiment 2, it might suggest that during PIT testing, normal performance may require a halting of DA release onto D2-MSNs. This is highly speculative, of course, just a thought worth considering.

We agree with the comments made by the Reviewer, and the original manuscript included statements acknowledging that pharmacological approaches are limited in the capacity to inform about the function of NAc-S SPNs (pages 4 and 9). As noted by the Reviewer, these limitations are especially salient when considering NAc-S D2-SPNs. Based on the Reviewer’s comment, we have modified our discussion to further underscore these limitations (page 12). Finally, we agree with the suggestion that PIT may require a halting of DA release onto D2-SPNs. This is consistent with the model presented, whereby D2-SPNs function is required to trigger enkephalin release (page 13).     

Section-Specific Comments and Questions:

Results:

Anterograde tracing and ex vivo cell recordings in D1 Cre and A2a Cre rats: Why are there no statistics reported for the e-phys data in this section? Was this merely a qualitative demonstration? I realize that the A2a-Cre condition only shows 3 recordings, so I appreciate the limitations in analyzing the data presented.

The reviewer is correct that we initially intended to provide a qualitative demonstration. However, we have now included statistical analyses for the ex vivo recordings. It is important to note that there were at least 5 recordings per condition, though overlapping data points may give the impression of fewer recordings in certain conditions. We have provided the exact number of recordings in both the main text (page 5) and figure legend. 

What does trial by trial analysis look like, because in addition to the eNects of extinction, do you know if the responsiveness of the opsin to light stimulation is altered after repeated exposures, or whether the cells themselves become compromised in any way with repeated light-inhibition, particularly given the relatively long 2m duration of the trial.

The Reviewer raises an interesting point, and we provide complete trial-by-trial data for each experiment below. As identified by the Reviewer, there is some evidence for extinction, although it remained modest. Importantly, the data suggest that light stimulation did not aMect the physiology of the targeted cells. In eNpHR3.0 rats, performance across OFF trials remained stable (both for Same and DiMerent) even though they were preceded by ON trials, indicating no carryover eMects from optical stimulation.

Author response image 2.

The statistics for the choice test are not reported for eNpHR-D1-Cre rats, but do show a weakening of the instrumental devaluation eNect "Group x Lever x LED: F1,18 = 10.04, p < 0.01, = 0.36". The post hoc comparisons showed that all groups showed devaluation, but it is evident that there is a weakening of this eNect when the LED was on (η² = 0.41) vs oN (η² = 0.78), so I think the authors should soften the claim that NAcS-D1s are not involved in value-based decision-making. (Also, there is a typo in the legend in Figure S1, where the caption for panel "F" is listed as "E".) I also think that this could be potentially interesting in light of the fact that with circuit manipulation, this same weakening of the instrumental devaluation eNect was not observed. To me, this suggests that D1-NAcS that project to a diNerent region (not VP) contribute to value-based decision making.

This comment overlaps with one made in the Public Review, for which we have already provided a response. Given its importance, we have added a section addressing this point in the supplemental discussion of the Supplementary Material file, which aligns with the location of the relevant data. The caption labelling error has been corrected.

Materials and Methods:

Subjects:

Were these heterozygous or homozygous rats? If hetero, what rats were used for crossbreeding (sex, strain, and vendor)? Was genotyping done by the lab or outsourced to commercial services? If genotyping was done within the lab, please provide a brief description of the protocol used. How was food restriction established and maintained (i.e., how many days to bring weights down, and was maintenance achieved by rationing or by limiting ad lib access to food for some period in the day)?

The information requested by the Reviewer have been added to the subjects section (pages 15-16).  

Were rats pair/group housed after implantation of optic fibers?

We have clarified that rats were group houses throughout (see subjects section; pages 15-16). 

Behavioral Procedures:

How long did each 0.2ml sucrose infusion take? For pellets, for each US delivery, was it a single pellet or two in quick succession?

We have modified the method section to indicate that the sucrose was delivered across 2 seconds and that a single pellet was provided (page 17). 

The CS to ITI duration ratio is quite low. Is there a reason such a short ratio was used in training?

These parameters are those used in all our previous experiments on outcome-specific PIT. There is no specific reason for using such a ratio, except that it shortens the length of the training session. 

Relative to the end of training, when were the optical implantation surgeries conducted, and how much recovery time was given before initiating reminder training and testing?

Fibre-optic implantation was conducted 3-4 days after training and another 3-4 days were given for recovery. This has been clarified in the Materials and methods section (pages 15-16).

I think a diagram or schematic showing the timeline for surgeries, training, and testing would be helpful to the audience.

We opted for a text-based experimental timeline rather than a diagram due to slight temporal variations across experiments (page 15).

On trials, when the LED was on, was light delivered continuously or pulsed? Do these opto-receptors 'bleach' within such a long window?

We apologize for the lack of clarity; the light was delivered continuously. We have modified the manuscript (pages 6 and 19) and figure legend accordingly. The postmortem analysis did not provide evidence for photobleaching (Supplemental Figures) and as noted above, the behavioural results do not indicate any negative physiological impact on cell function.  

Immunofluorescence: The blocking solution used during IHC is described as "NHS"; is this normal horse serum?

The Reviewer is correct; NHS stands for normal horse serum. This has been added (page 21). 

Microscopy and imaging:

For the description of rats excluded due to placement or viral spread problems, an n=X is listed for the NAc S D1 SPNs --> VP silencing group. Is this a typo, or was that meant to read as n=0? Also, was there a major sex diNerence in the attrition rate? If so, I think reporting the sex of the lost subjects might be beneficial to the scientific community, as it might reflect a need for better guidance on sex-specific coordinates for targeting small nuclei.

We apologize for the error regarding the number of excluded animals. This error has been corrected (page 23). There were no major sex diMerences in the attrition rate. The manuscript has been updated to provide information about the sex of excluded animals (page 23). 

References

Cao, J., Willett, J. A., Dorris, D. M., & Meitzen, J. (2018). Sex DiMerences in Medium Spiny Neuron Excitability and Glutamatergic Synaptic Input: Heterogeneity Across Striatal Regions and Evidence for Estradiol-Dependent Sexual DiMerentiation. Front Endocrinol (Lausanne), 9, 173. https://doi.org/10.3389/fendo.2018.00173

Corbit, L. H., Muir, J. L., Balleine, B. W., & Balleine, B. W. (2001). The role of the nucleus accumbens in instrumental conditioning: Evidence of a functional dissociation between accumbens core and shell. J Neurosci, 21(9), 3251-3260. http://eutils.ncbi.nlm.nih.gov/entrez/eutils/elink.fcgi?dbfrom=pubmed&id=11312 310&retmode=ref&cmd=prlinks

Corbit, L. H., & Balleine, B. W. (2011). The general and outcome-specific forms of Pavlovian-instrumental transfer are diMerentially mediated by the nucleus accumbens core and shell. J Neurosci, 31(33), 11786-11794. https://doi.org/10.1523/JNEUROSCI.2711-11.2011

Laurent, V., Bertran-Gonzalez, J., Chieng, B. C., & Balleine, B. W. (2014). δ-Opioid and Dopaminergic Processes in Accumbens Shell Modulate the Cholinergic Control of Predictive Learning and Choice. J Neurosci, 34(4), 1358-1369. https://doi.org/10.1523/JNEUROSCI.4592-13.2014

Laurent, V., Leung, B., Maidment, N., & Balleine, B. W. (2012). μ- and δ-opioid-related processes in the accumbens core and shell diMerentially mediate the influence of reward-guided and stimulus-guided decisions on choice. J Neurosci, 32(5), 1875-1883. https://doi.org/10.1523/JNEUROSCI.4688-11.2012

Matamales, M., McGovern, A. E., Mi, J. D., Mazzone, S. B., Balleine, B. W., & BertranGonzalez, J. (2020). Local D2- to D1-neuron transmodulation updates goal-directed learning in the striatum. Science, 367(6477), 549-555. https://doi.org/10.1126/science.aaz5751

Parkes, S. L., Bradfield, L. A., & Balleine, B. W. (2015). Interaction of insular cortex and ventral striatum mediates the eMect of incentive memory on choice between goaldirected actions. J Neurosci, 35(16), 6464-6471. https://doi.org/10.1523/JNEUROSCI.4153-14.2015

Pettibone, J. R., Yu, J. Y., Derman, R. C., Faust, T. W., Hughes, E. D., Filipiak, W. E., Saunders, T. L., Ferrario, C. R., & Berke, J. D. (2019). Knock-In Rat Lines with Cre Recombinase at the Dopamine D1 and Adenosine 2a Receptor Loci. eNeuro, 6(5). https://doi.org/10.1523/ENEURO.0163-19.2019

Willett, J. A., Will, T., Hauser, C. A., Dorris, D. M., Cao, J., & Meitzen, J. (2016). No Evidence for Sex DiMerences in the Electrophysiological Properties and Excitatory Synaptic Input onto Nucleus Accumbens Shell Medium Spiny Neurons. eNeuro, 3(1), ENEURO.0147-15.2016. https://doi.org/10.1523/ENEURO.0147-15.2016

“O PEST F” is a a good way to remember the structure of the skull

Author response:

The following is the authors’ response to the original reviews

Public Reviews: 

Reviewer #1 (Public review): 

This study presents evidence that remote memory in the APP/PS1 mouse model of Alzheimer's disease (AD) is associated with PV interneuron hyperexcitability and increased inhibition of cortical engram cells. Its strength lies in the fact that it explores a neglected aspect of memory research - remote memory impairments related to AD (for which the primary research focus is usually on recent memory impairments) -which has received minimal attention to date. While the findings are intriguing, the weakness of the paper hovers around purely correlational types of evidence and superficial data analyses, which require substantial revisions as outlined below. 

We thank the reviewer for their feedback, and we appreciate the recognition of the study’s novelty in addressing remote memory impairments in AD. We acknowledge the reviewer’s concerns and have implemented revisions to strengthen the manuscript.

Major concerns: 

(1) In light of previous work, including that by the authors themselves, the data in Figure 1 should be implemented by measurements of recent memory recall in order to assess whether remote memories are exclusively impaired or whether remote memory recall merely represents a continuation of recent memory impairments.

We agree with the reviewer that is an important point. In line with their suggestion in minor comment 1, we now omitted the statement on recent memory in the results (previously on lines 109-111 and 117). Nonetheless, previous independent experiments from our group have repeatedly shown recent memory deficits in APP/PS1 mice at 12 weeks of age, including a recent article published in 2023. We refer the reviewer to figure 2c in Végh et al. (2014) and figure 2i in Kater et al. (2023). We have added a reference of the latter paper to our discussion section (line 458-459). Therefore, we are confident that the recent memory deficit at 12 weeks of age is a stable phenotype in our APP/PS1 mice.

With these data in mind, we argue that the remote memory recall impairment is not a continuation of recent memory impairments. Recent memory deficits emerge already at 12 weeks of age, and when remote memory is assessed at 16 weeks (4 weeks after training at 12 weeks of age), APP/PS1 mice are still capable of forming and retrieving a remote memory. This suggests that remote memory retrieval can occur even when recent memory is compromised, arguing against the idea that the remote memory deficit observed at 20 weeks is a continuation of earlier recent memory impairments. We have clarified this point in the revised manuscript by adding the following sentence to the discussion section (line 462-465): 

‘This suggests that a remote memory can be formed even when recent memory expression is already compromised, indicating that the remote memory deficit in 20-week-old APP/PS1 mice is not a continuation of earlier recent memory impairments.’

(2) Figure 2 shows electrophysiological properties of PV cells in the mPFC that correlate with the behavior shown in Figure 1. However, the mice used in Figure 2 are different than the mice used in Figure 1. Thus, the data are correlative at best, and the authors need to confirm that behavioral impairments in the APP/PS1 mice crossed to PV-Cre (and SST-Cre mice) used in Figure 2 are similar to those of the APP/PS1 mice used in Figure 1. Without that, no conclusions between behavioral impairments and electrophysiological as well as engram reactivation properties can be made, and the central claims of the paper cannot be upheld. 

We thank the reviewer for raising this concern. Indeed, the remote memory impairment and PV hyperexcitability are correlative data, and therefore we do not make causal claims based on these data. However, please note that most of our key findings, including behavioural impairments, characterization of the engram ensemble and reactivation thereof, as well as inhibitory input measurements, were acquired using the same mouse line (APP/PS1), strengthening the coherence of our conclusions. Also, our electrophysiological findings in APP/PS1 (enhanced sIPSC frequency) and APP/PS1-PV-Cre-tdTomato (enhanced PV cell excitability) mice align well. Direct comparisons between the transgenic mouse lines APP/PS1 and APP/PS1 Parv-Cre were performed in our previous studies, confirming that these lines are similar in terms of behaviour and pathology. Specifically, we demonstrated that APP/PS1 mice display spatial memory impairments at 16 weeks of age, Fig 4a-d, consistent with the deficits observed in APP/PS1 Parv-Cre mice at 16 weeks of age, Fig 5a-c (Hijazi et al., 2020a). Additionally, Hijazi et al. (2020a) showed that soluble and insoluble Aβ levels do not differ between APP/PS1 Parv-Cre and APP/PS1 mice (sFig. 1), indicating comparable levels of pathology between these lines. While we do not have a similar characterization of the APP/PS1 SST-Cre line, we should mention that we also did not observe excitability differences in SST cells. We now acknowledge the limitation in the revised discussion section (line 480-487), and stress that our electrophysiology and behavioural findings are correlative in nature:

‘Although the excitability measurements were performed in APP/PS1-PV-Cre-tdTomato mice, and not in the APP/PS1 parental line, we previously found that these transgenic mouse lines exhibit comparable amyloid pathology (both soluble and insoluble amyloid beta levels) as well as similar spatial memory deficits (Hijazi et al., 2020a; Kater et al., 2023). Thus, our observations indicate that the APP/PS1 PV-Cre-tdTomato and APP/PS1 lines are similar in terms of pathology and behaviour. Nonetheless, further work is needed to identify a causal link between PV cell hyperexcitability and remote memory impairment.’ 

(3) The reactivation data starting in Figure 3 should be analysed in much more depth: 

a) The authors restrict their analysis to intra-animal comparisons, but additional ones should be performed, such as inter-animal (WT vs APP/PS1) as well as inter-age (12-16w vs 16-20w). In doing so, reactivation data should be normalized to chance levels per animal, to account for differences in labelling efficiency - this is standard in the field (see original Tonegawa papers and for a reference). This could highlight differences in total reactivation that are already apparent, such as for instance in WT vs APP/PS1 at 20w (Figure 3o) and highlight a decrease in reactivation in AD mice at this age, contrary to what is stated in lines 213-214. 

We would like to thank the reviewer for the valuable input on the reactivation data in Figure 3. 

We agree with the reviewer and now depict the data as normalized to chance levels (Figure 3). The original figures are now supplemental (sFig. 5). The reactivation data normalized to chance are similar to the original results, i.e. no difference was observed in the reactivation of the mPFC engram ensemble between genotypes. The reviewer may have overlooked that we did perform inter-animal (WT vs. APP/PS1) comparisons, however these were not significantly different. We have made this clearer in the main text, lines 277, 288-289, 294-295 and 303-304. Moreover, the reviewer recommended including inter-age group comparisons, which have now been added to the supplemental figures (sFig. 6). No genotype-dependent differences were observed. While a main effect of age group did emerge, indicating that there is a potential increased overlap between Fos+ and mCherry+ in animals aged 16-20 weeks, we caution against overinterpreting this finding. These experimental groups were processed in separate cohorts, with viral injection and 4TM-induced tagging performed at different moments in time, which may have contributed to the observed differences in overlap. We have addressed this point in the revised discussion (line 612-617):

‘Furthermore, we also observed an increase in the amount overlap between Fos+ and mCherry+ engram cells when comparing the 12-16w and 16-20w age groups. This finding should be interpreted with caution, as the experimental groups were processed in separate cohorts, with viral injections and 4TM-induced tagging performed at different moments in time. This may have contributed to the observed differences between ages.’

b) Comparing the proportion of mcherry+ cells in PV- and PV+ is problematic, considering that the PV- population is not "pure" like the PV+, but rather likely to represent a mix of different pyramidal neurons (probably from several layers), other inhibitory neurons like SST and maybe even glial cells. Considering this, the statement on line 218 is misleading in saying that PVs are overrepresented. If anything, the same populations should be compared across ages or groups.  

We thank the reviewer for their insightful comment and agree that the PV- population of cells is likely more heterogenous than the PV+ population. However, we would like to clarify that all quantified cells were selected based on Nissl immunoreactivity, and to exclude non-neuronal cells, stringent thresholding was applied in the script that was used to identify Nissl+ cells. The threshold information has now been added to the methods section (line 758-760). Thus, although heterogenous, the analysed PV- population reflects a neuronal subset. In response to the reviewer’s suggestion, we have now included overlap measurements relative to chance levels (Figure 3). These analyses did not reveal differences with the original analyses, i.e., there are no genotype specific differences. We have also incorporated the suggested inter-age group comparisons (sFig. 6) and found no differences between age groups. In light of the raised concerns, we have removed the statement that PV cells were overrepresented in the engram ensemble.

c) A similar concern applies to the mcherry- population in Figure 4, which could represent different types of neurons that were never active, compared to the relatively homogeneous engram mcherry+ population. This could be elegantly fixed by restricting the comparison to mCherry+Fos+ vs mCherry+Fos- ensembles and could indicate engram reactivation-specific differences in perisomatic inhibition by PV cells. 

The comparison the reviewer suggests, comparing mCherry+Fos+ to mCherry+Fos- is indeed conceptually interesting and could provide more insight into engram reactivation and PV input. However, there are practical limitations to performing this analysis, as neurons in close proximity need to be compared in a pairwise manner to account for local variability in staining intensity. As shown in Figure 3c+k and Figure 4a+b, d+e, PV immunostaining intensity varies to a certain extend within a given image. While pairwise comparisons of neighbouring neurons were feasible when analysing mCherry+ and mCherry- cells, they are unfortunately not feasible for the mCherry+Fos+ vs. mCherry+Fos- comparison. The occurrence of spatially adjacent mCherry+Fos+ and mCherry+Fos- neurons is too sparse for a pairwise comparison. This analysis would therefore result in substantial under-sampling and limit the reliability of the analysis. Nonetheless, we agree with the reviewer that the mCherry- population may be more heterogenous than the mCherry+ population, despite the fact that PV+ neurons and that non-neuronal cells were excluded from both populations in the analyses. We therefore added a statement to the discussion to acknowledge this limitation (line 536-539): 

‘Although PV+ cells were not included in this analysis and we excluded non-neuronal cells based on the area of the Nissl stain, the mCherry- population was potentially more heterogenous than the mCherry+ population, which may have contributed to the differences we observed.’

(4) At several instances, there are some doubts about the statistical measures having been employed: 

a) In Figure 4f, it is unclear why a repeated measurement ANOVA was used as opposed to a regular ANOVA. 

b) In Supplementary Figure 2b, a Mann-Whitney test was used, supposedly because the data were not normally distributed. However, when looking at the individual data points, the data does seem to be normally distributed. Thus, the authors need to provide the test details as to how they measured the normalcy of distribution. 

a) Based on the pairwise comparison of neighbouring neurons within animals, the data in Figure 4f was analysed with a repeated measure ANOVA. 

b) We thank the author for their comment on Supplementary Figure 2b. The data is indeed normally distributed, and we have analysed it using a D’Agostino & Pearson test. We have corrected this in the supplemental figure. 

Minor concerns: 

(1) Line 117: The authors cite a recent memory impairment here, as shown by another paper. However, given the notorious difficulty in replicating behavioral findings, in particular in APP/PS1 mice (number of backcrossings, housing conditions, etc., might differ between laboratories), such a statement cannot be made. The authors should either show in their own hands that recent memory is indeed affected at 12 weeks of age, or they should omit this statement. 

We thank the reviewer for this thoughtful comment. As noted in our response to major concern (1), we have addressed this concern by providing additional information and clarification in the discussion (line 462-465) regarding the possibility that remote memory impairments are a continuation of recent memory impairments. As mentioned in our response, we have added a reference to a more recent study from our lab (Kater et al. (2023). These findings are consistent with the earlier report from our lab (Végh et al. (2014), underscoring the reproducibility of this phenotype across independent cohorts and time. Notably, the experiments in the 2023 and present study were performed using the same housing and experimental conditions. Nevertheless, in light of the reviewer’s suggestion, and to avoid overstatement or speculation, we have now omitted the sentence referring to recent memory impairments at 12 weeks of age from the results section.

(2) Pertaining to Figure 3, low-resolution images of the mPFC should be provided to assess the spread of injection and the overall degree of double-positive cells.  

We agree with the reviewer and have added images of the mPFC as a supplemental figure (sFig. 3) that show the spread of the injection. Unfortunately, it is not possible to visualize the overall degree of double-positive cells at a lower magnification (or low-resolution). Representative examples of colocalization are presented in Figure 3.

Reviewer #2 (Public review): 

This study presents a comprehensive investigation of remote memory deficits in the APP/PS1 mouse model of Alzheimer's disease. The authors convincingly show that these deficits emerge progressively and are paralleled by selective hyperexcitability of PV interneurons in the mPFC. Using viral-TRAP labeling and patch-clamp electrophysiology, they demonstrate that inhibitory input onto labeled engram cells is selectively increased in APP/PS1 mice, despite unaltered engram size or reactivation. These findings support the idea that alterations in inhibitory microcircuits may contribute to cognitive decline in AD. 

However, several aspects of the study merit further clarification. Most critically, the central paradox, i.e., increased inhibitory input without an apparent change in engram reactivation, remains unresolved. The authors propose possible mechanisms involving altered synchrony or impaired output of engram cells, but these hypotheses require further empirical support. Additionally, the study employs multiple crossed transgenic lines without reporting the progression of amyloid pathology in the mPFC, which is important for interpreting the relationship between circuit dysfunction and disease stage. Finally, the potential contribution of broader network dysfunction, such as spontaneous epileptiform activity reported in APP/PS1 mice, is also not addressed. 

We thank the reviewer for their evaluation and appreciate the positive assessment of our study’s contributing to understanding remote memory deficits and the dysfunction of inhibitory microcircuits in AD. We also acknowledge the relevant points raised and have revised the manuscript to clarify our interpretations. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

(1) Line 68: What are "APP23xPS45" mice? This is most likely a typo.

This line is a previously reported double transgenic amyloid beta mouse model that was obtained by crossing APP23 (overexpressing human amyloid precursor protein with the Swedish double mutation at position 670/671) with PS45 (carrying a transgene for mutant Presenilin 1, G384A mutation) (Busche et al., 2008; Grienberger et al., 2012). 

(2) Line 148: The authors should also briefly describe in the main text that APP/PS1 x SST-Cre mice were generated and used here.  

We thank the reviewer for their comment and have added their suggestion to the main text (line 166-168):

‘To do this, APP/PS1 mice were crossed with SST-Cre mice to generate APP/PS1 SST-Cre mice. Following microinjection of AAV-hSyn::DIO-mCherry into the mPFC, recordings were obtained from SST neurons.’

(3) The discussion should be condensed because of redundancies on several occasions. For example, memory allocation is discussed starting on line 371, then again on line 392. This should be combined. Likewise, how the correlative nature of the findings about PV interneurons could be further functionally addressed is discussed on lines 413 and 454, and should be condensed into one paragraph. 

We thank the reviewer for this suggestion and have revised the discussion to remove the redundancies as proposed.  

Reviewer #2 (Recommendations for the authors): 

To strengthen the manuscript, the following points should be addressed: 

(1) Quantify amyloid pathology: It is essential to assess amyloid-β levels (soluble and insoluble) in the mPFC of APP/PS1-PV-Cre-tdTomato mice at the studied ages. This would help determine whether the observed circuitlevel changes track with disease progression as seen in canonical APP/PS1 models. 

We thank the reviewer for this valuable suggestion and agree that assessing Aβ levels in the mPFC is important to determine whether the observed circuit level alterations in APP/PS1 mice coincide with the progression of amyloid pathology. Therefore, we assessed the amyloid plaque load in the mPFC of APP/PS1 mice at 16 and 20 weeks of age (new supplemental figure sFig. 1) and observed no difference in plaque load between these two time points. This suggests that the increased excitability in the mPFC cannot be attributed to differences in plaque load (insoluble amyloid beta).

In line with this, we previously studied both soluble and insoluble Aβ levels in the CA1 and reported that there are no differences between 12 and 16 weeks of age (Kater et al., 2023), while PV cell hyperexcitability is present at 16 weeks of age (Hijazi et al., 2020a). From 24 weeks onwards, the level of amyloid beta increases. Similarly, Végh et al. (2014) showed using immunoblotting that monomeric and low molecular weight oligomeric forms of soluble Aβ are already present as early as 6 weeks of age and become more prominent at 24 weeks of age. Although the soluble Aβ measurements were performed in the hippocampus, we think these findings can be extrapolated to cortical regions, as the APP and PS1 mutations in APP/PS1 mice are driven by a prion promotor, which should induce consistent expression across brain regions. Data from other research groups support this hypothesis (Kim et al., 2015; Zhang et al., 2011). Thus, large regional differences in soluble Aβ are not expected. The temporal progression suggests that increasing levels of soluble amyloid beta might contribute to the emergence of PV cell hyperexcitability. We have added this point to the manuscript (line 585-591):

‘Since amyloid beta plaque load in the mPFC remains comparable between 16- and 20-week-old APP/PS1 mice, the observed increased excitability is unlikely the result of changes in insoluble amyloid beta levels. Previous data from our lab show that soluble amyloid beta is already present as early as 6 weeks of age and becomes more prominent at 24 weeks of age (Kater et al., 2023; Végh et al., 2014). The progressive increase in soluble amyloid beta levels may contribute to the emergence of PV cell hyperexcitability.’

Finally, we previously compared soluble and insoluble amyloid beta levels in APP/PS1 and APP/PS1 Parv Cre mice and show that these are similar (Hijazi et al., 2020a). While our current study shows the progression of amyloid beta accumulation in APP/PS1 mice, these mice also exhibit altered microcircuitry (enhanced sIPSC frequency on engram cells) at 20 weeks of age, the same age at which we observed PV cell hyperexcitability in APP/PS1 Parv Cre tdTomato mice. This further supports the generalizability of our findings across genotypes, between APP/PS1 and APP/PS1 Parv Cre tdTomato mice. 

(2) Examine later disease stages: Since the current effects are modest, assessing memory performance, PV cell excitability, and engram inhibition at more advanced stages could clarify whether these alterations become more pronounced with disease progression. 

We thank the reviewer for this thoughtful suggestion. Investigating advanced disease stages could indeed provide valuable insights into whether the observed alterations in memory performance, PV cell hyperexcitability and engram inhibition become more pronounced over time. Our previous work has shown that changes in pyramidal cell excitability emerge at a later stage than in PV cells, supporting the idea of progressive circuit dysfunction (Hijazi et al., 2020a). However, at these more advanced stages, additional pathological processes, such as an increased gliosis (Janota, Brites, Lemere, & Brito, 2015; Kater et al., 2023) and synaptic loss (Alonso-Nanclares, MerinoSerrais, Gonzalez, & DeFelipe, 2013; Bittner et al., 2012), will likely contribute to both electrophysiological and behavioural measurements. Furthermore, we would like to point out that the current changes observed in memory performance, PV hyperexcitability and increased inhibitory input on engram cells at 16-20 weeks of age are not modest, but already quite substantial. Our focus on these early time points in APP/PS1 mice were intentional, as it helps us understand the initial changes in Alzheimer’s disease at a circuit level and to identify therapeutic targets early intervention. What happens at later stages is certainly of interest, but beyond the scope of this study and should therefore be addressed in future studies. We have incorporated a discussion related to this point into the revised manuscript (line 602-606):

‘Moreover, it is relevant to investigate whether changes in PV and PYR cell excitability, as well as input onto engram cells in the mPFC, become more pronounced at later disease stages. Nonetheless, by focussing on early disease timepoints in the present study, we aimed to understand the initial circuit-level changes in AD and identify targets for early therapeutic intervention.’

(3) Address network hyperexcitability: Spontaneous epileptiform activity has been reported in APP/PS1 mice from 4 months of age (Reyes-Marin & Nuñez, 2017). Including EEG data or discussing this point in relation to your findings would help contextualize the observed inhibitory remodeling within broader network dysfunction. 

We thank the reviewer for this valuable input and for highlighting the study by Reyes-Marin and Nuñez (2017). In line with this, we recently reported longitudinal local field potential (LFP) recordings in freely behaving APP/PS1 Parv-Cre mice and wild type control animals between the ages of 3 to 12 months (van Heusden et al., 2023). Weekly recordings were performed in the home cage under awake mobile conditions. These data showed no indications of epileptiform activity during wakefulness, consistent with previous findings that epileptic discharges in APP/PS1 mice predominantly occur during sleep (Gureviciene et al., 2019). Recordings were obtained from the prefrontal cortex (PFC), parietal cortex and the hippocampus. In contrast, the study by Reyes-Marin and Nuñez (2017) recorded from the somatosensory cortex in anesthetized animals. Here, during spontaneous recordings, no differences were observed in delta, theta or alpha frequency bands between APP/PS1 and WT mice. Interestingly, we observed an early increase in absolute power, particularly in the hippocampus and parietal cortex from 12 to 24 weeks of age in APP/PS1 mice. In the PFC we found a shift in relative power from lower to higher frequencies and a reduction in theta power. Connectivity analyses revealed a progressive, age-dependent decline in theta/alpha coherence between the PFC and both the parietal cortex and hippocampus. Given the well-established role of PV interneurons network synchrony and coordinating theta and gamma oscillations critical for cognitive function (Sohal, Zhang, Yizhar, & Deisseroth, 2009; Xia et al., 2017), these findings support the idea of early circuit dysfunction in APP/PS1 mice. Our findings, i.e. hyperexcitability of PV cells, align with these LFP based networklevel observations. These data suggest an early shift in the E/I balance, contributing to altered oscillatory dynamics and impaired inter-regional connectivity, possibly leading to alterations in memory. However, whether the observed PV hyperexcitability in our study directly contributes to alterations in power and synchrony remains to be elucidated. Furthermore, it would be interesting to determine the individual contribution of PV cell hyperexcitability in the hippocampus versus the mPFC to network changes and concurrent memory deficits. We have added a statement on network hyperexcitability to the discussion (line 561-565). 

‘Interestingly, we recently found a progressive disruption of oscillatory network synchrony between the mPFC and hippocampus in APP/PS1 Parv-Cre mice (van Heusden et al., 2023). However, whether the observed PV cell hyperexcitability directly contributes to changes in inter-regional synchrony, and whether this leads to alterations at a network level, i.e. increased inhibitory input on engram cells, and consequently to memory deficits, remains to be elucidated in future studies.’ 

(4) Mechanisms responsible for PV hyperexcitability: Related to the previous point, a discussion of the possible underlying mechanisms, e.g., direct effects of amyloid-β, inflammatory processes, or compensatory mechanisms, would strengthen the discussion. 

We agree with the reviewer that this will strengthen the discussion. We have now added a comprehensive discussion in the revised manuscript to address potential mechanisms responsible for PV cell hyperexcitability (line 579-594).:

‘Prior studies have shown that neurons in the vicinity of amyloid beta plaques show increased excitability (Busche et al., 2008). We demonstrated that PV neurons in the CA1 are hyperexcitable and that treatment with a BACE1 inhibitors, i.e. reducing amyloid beta levels, rescues PV excitability (Hijazi et al., 2020a). In line with this, we also reported that addition of amyloid beta to hippocampal slices increases PV excitability, without altering pyramidal cell excitability (Hijazi et al., 2020a). Finally, applying amyloid beta to an induced mouse model of PV hyperexcitability further impairs PV function (Hijazi et al., 2020b). Since amyloid beta plaque load in the mPFC remains comparable between 16- and 20-week-old APP/PS1 mice, the observed increased excitability is unlikely the result of changes in insoluble amyloid beta levels. Previous data from our lab show that soluble amyloid beta is already present as early as 6 weeks of age and becomes more prominent at 24 weeks of age (Kater et al., 2023; Végh et al., 2014). The progressive increase in soluble amyloid beta levels may contribute to the emergence of PV cell hyperexcitability. We hypothesize that the hyperexcitability induced by amyloid beta may result from disrupted ion channel function, as PV neuron dysfunction can result from altered potassium (Olah et al., 2022) and sodium channel activity (Verret et al., 2012).’

(5) Excitatory-inhibitory balance: While the main focus is on increased inhibition onto engram cells, the reported increase in sEPSC frequency (Figure 5g) across genotypes suggests the presence of excitatory remodelling as well. A brief discussion of how this may interact with increased inhibition would be valuable.  

We thank the reviewer for this comment regarding the interaction between excitatory and inhibitory remodelling. We have now incorporated this discussion point into the revised manuscript (line 528-534):

‘Interestingly, both WT and APP/PS1 mice showed an increase in sEPSC frequency onto engram cells, suggesting that increased excitatory input is a consequence of memory retrieval and not affected by genotype. However, only in APP/PS1 mice, the augmented excitatory input coincided with an elevation of inhibitory input onto engram cells. The resulting imbalance between excitation and inhibition could therefore potentially disrupt the precise control of engram reactivation and contribute to the observed remote memory impairment.’

References

Alonso-Nanclares, L., Merino-Serrais, P., Gonzalez, S., & DeFelipe, J. (2013). Synaptic changes in the dentate gyrus of APP/PS1 transgenic mice revealed by electron microscopy. J Neuropathol Exp Neurol, 72(5), 386-395. doi:10.1097/NEN.0b013e31828d41ec

Bittner, T., Burgold, S., Dorostkar, M. M., Fuhrmann, M., Wegenast-Braun, B. M., Schmidt, B., . . . Herms, J. (2012). Amyloid plaque formation precedes dendritic spine loss. Acta Neuropathologica, 124(6), 797807. doi:10.1007/s00401-012-1047-8

Busche, M. A., Eichhoff, G., Adelsberger, H., Abramowski, D., Wiederhold, K. H., Haass, C., . . . Garaschuk, O. (2008). Clusters of hyperactive neurons near amyloid plaques in a mouse model of Alzheimer's disease. Science, 321(5896), 1686-1689. doi:10.1126/science.1162844

Grienberger, C., Rochefort, N. L., Adelsberger, H., Henning, H. A., Hill, D. N., Reichwald, J., . . . Konnerth, A. (2012). Staged decline of neuronal function in vivo in an animal model of Alzheimer's disease. Nat Commun, 3, 774. doi:10.1038/ncomms1783

Gureviciene, I., Ishchenko, I., Ziyatdinova, S., Jin, N., Lipponen, A., Gurevicius, K., & Tanila, H. (2019). Characterization of Epileptic Spiking Associated With Brain Amyloidosis in APP/PS1 Mice. Front Neurol, 10, 1151. doi:10.3389/fneur.2019.01151

Hijazi, S., Heistek, T. S., Scheltens, P., Neumann, U., Shimshek, D. R., Mansvelder, H. D., . . . van Kesteren, R. E. (2020a). Early restoration of parvalbumin interneuron activity prevents memory loss and network hyperexcitability in a mouse model of Alzheimer's disease. Mol Psychiatry, 25(12), 3380-3398. doi:10.1038/s41380-019-0483-4

Hijazi, S., Heistek, T. S., van der Loo, R., Mansvelder, H. D., Smit, A. B., & van Kesteren, R. E. (2020b). Hyperexcitable Parvalbumin Interneurons Render Hippocampal Circuitry Vulnerable to Amyloid Beta. iScience, 23(7), 101271. doi:10.1016/j.isci.2020.101271

Janota, C. S., Brites, D., Lemere, C. A., & Brito, M. A. (2015). Glio-vascular changes during ageing in wild-type and Alzheimer's disease-like APP/PS1 mice. Brain Res, 1620, 153-168. doi:10.1016/j.brainres.2015.04.056

Kater, M. S. J., Huffels, C. F. M., Oshima, T., Renckens, N. S., Middeldorp, J., Boddeke, E., . . . Verheijen, M. H. G. (2023). Prevention of microgliosis halts early memory loss in a mouse model of Alzheimer's disease. Brain Behav Immun, 107, 225-241. doi:10.1016/j.bbi.2022.10.009

Kim, H. Y., Kim, H. V., Jo, S., Lee, C. J., Choi, S. Y., Kim, D. J., & Kim, Y. (2015). EPPS rescues hippocampus-dependent cognitive deficits in APP/PS1 mice by disaggregation of amyloid-β oligomers and plaques. ature Communications, 6(1), 8997. doi:10.1038/ncomms9997

Olah, V. J., Goettemoeller, A. M., Rayaprolu, S., Dammer, E. B., Seyfried, N. T., Rangaraju, S., . . . Rowan, M. J. M. (2022). Biophysical Kv3 channel alterations dampen excitability of cortical PV interneurons and contribute to network hyperexcitability in early Alzheimer’s. Elife, 11, e75316. doi:10.7554/eLife.75316

Reyes-Marin, K. E., & Nuñez, A. (2017). Seizure susceptibility in the APP/PS1 mouse model of Alzheimer's disease and relationship with amyloid β plaques. Brain Res, 1677, 93-100. doi:10.1016/j.brainres.2017.09.026

Sohal, V. S., Zhang, F., Yizhar, O., & Deisseroth, K. (2009). Parvalbumin neurons and gamma rhythms enhance cortical circuit performance. Nature, 459(7247), 698-702. doi:10.1038/nature07991

van Heusden, F. C., van Nifterick, A. M., Souza, B. C., França, A. S. C., Nauta, I. M., Stam, C. J., . . . van Kesteren, R. E. (2023). Neurophysiological alterations in mice and humans carrying mutations in APP and PSEN1 genes. Alzheimers Res Ther, 15(1), 142. doi:10.1186/s13195-023-01287-6

Végh, M. J., Heldring, C. M., Kamphuis, W., Hijazi, S., Timmerman, A. J., Li, K. W., . . . van Kesteren, R. E. (2014). Reducing hippocampal extracellular matrix reverses early memory deficits in a mouse model of Alzheimer's disease. Acta Neuropathol Commun, 2, 76. doi:10.1186/s40478-014-0076-z

Verret, L., Mann, E. O., Hang, G. B., Barth, A. M., Cobos, I., Ho, K., . . . Palop, J. J. (2012). Inhibitory interneuron deficit links altered network activity and cognitive dysfunction in Alzheimer model. Cell, 149(3), 708-721. doi:10.1016/j.cell.2012.02.046

Xia, F., Richards, B. A., Tran, M. M., Josselyn, S. A., Takehara-Nishiuchi, K., & Frankland, P. W. (2017). Parvalbumin-positive interneurons mediate neocortical-hippocampal interactions that are necessary for memory consolidation. Elife, 6. doi:10.7554/eLife.27868

Zhang, W., Hao, J., Liu, R., Zhang, Z., Lei, G., Su, C., . . . Li, Z. (2011). Soluble Aβ levels correlate with cognitive deficits in the 12-month-old APPswe/PS1dE9 mouse model of Alzheimer's disease. Behavioural Brain Research, 222(2), 342-350. doi:https://doi.org/10.1016/j.bbr.2011.03.072

My favorite law is LAW, love always wins.

1. “al no incorporar una perspectiva de género en los cuestionarios, retratan una realidad equivocada.” pág. 181 Si bien la autora señala que la falta de incorporación de la perspectiva de género en los instrumentos de medición conduce a que los cuestionarios de las encuestas sobre migración y discriminación produzcan datos incompletos. Esto quiere decir, que, los resultados no reflejan diferencias sistemáticas entre hombres y mujeres migrantes, lo que a su vez limita la capacidad de conocer plenamente las dinámicas de discriminación basada en género dentro del fenómeno migratorio. En pocas palabras, si las encuestas no preguntan ¿Eres hombre o mujer migrante? o ¿Cómo afecta tu género tu experiencia migratoria?, entonces pasan por alto que las mujeres migrantes podrían estar viviendo discriminaciones distintas o adicionales. Es como si miráramos sólo la parte visible del iceberg y creyéramos que todo lo que importa está ahí arriba.

2. “no se considera la manera en que el género interseca con otras formas de desigualdad, como la nacionalidad o la clase social.” pág. 180 El texto resalta que la ceguera de género no sólo ignora las diferencias entre hombres y mujeres, sino que también desconoce la interseccionalidad. Es decir, el género se cruza con otros factores estructurales (como clase, etnicidad o estatus migratorio) que agravan las condiciones de vulnerabilidad. Su omisión impide comprender cómo las mujeres migrantes enfrentan formas múltiples y simultáneas de discriminación. Esto me parece clave, porque no todas las mujeres migrantes viven lo mismo, pues no es igual una mujer centroamericana pobre que una extranjera con más recursos. Ignorar esas diferencias es como decir que la discriminación afecta a todos igual, y eso borra las desigualdades que más pesan en la vida real.

3. “la de un país al que sólo llegan y por el que sólo transita una migración masculina.” pág. 180 Ahora bien, al describir el efecto de la “ceguera de género”, la autora observa que las encuestas reproducen un imaginario migratorio masculinizado, ya que, se asume implícitamente que la migración es mayoritariamente masculina. Esta visión sesgada impide reconocer la presencia, la situación y las necesidades específicas de las mujeres migrantes, reproduciendo una invisibilidad de género en los datos y, por ende, en las políticas públicas que podrían derivar de esos datos. Me hace pensar que muchas veces cuando escuchamos la palabra “los migrantes”, quizás pensamos automáticamente en hombres jóvenes. Pero, ¿Qué pasa con las mujeres que migran solas o en contexto familiar? Si los instrumentos no lo captan, es como si ni siquiera estuvieran consideradas. Y eso tiene consecuencias porque si no se mide, no se visibiliza, y si no se visibiliza, difícilmente se atiende.

De los muchos mitos que existen respecto a México y su sociedad, quizá dos de los más perversos son que el racismo no existe y que somos un país de puertas abiertas frente a la inmigración extranjera.

Estoy de acuerdo es un mito que no existe el racismo, aunque muchas personas creen esto o están escépticas a la idea , es importante verlo de manera mas critica ya que en México sí hay racismo y discriminación.

REsp 1747637 / SP

DIREITO CIVIL. RECURSO ESPECIAL. AÇÃO DE INDENIZAÇÃO POR DANOS MORAIS. ATO LIBIDINOSO PRATICADO CONTRA PASSAGEIRA NO INTERIOR DE UMA COMPOSIÇÃO DE METRÔ NA CIDADE DE SÃO PAULO/SP ("ASSÉDIO SEXUAL"). RESPONSABILIDADE DA TRANSPORTADORA. NEXO CAUSAL. ROMPIMENTO. FATO EXCLUSIVO DE TERCEIRO. CONEXIDADE COM A ATIVIDADE DE TRANSPORTE. RESPONSABILIDADE DA CPTM. 1. Ação ajuizada em 02/07/2014. Recurso especial interposto em 28/10/2015 e distribuído ao Gabinete em 31/03/2017. 2. O propósito recursal consiste em definir se a concessionária do metrô da cidade de São Paulo/SP deve responder pelos danos morais sofridos por passageira que foi vítima de ato libidinoso ou assédio sexual praticado por outro usuário, no interior de um vagão. 3. A cláusula de incolumidade é ínsita ao contrato de transporte, implicando <u>obrigação de resultado</u> do transportador, consistente em levar o passageiro com conforto e segurança ao seu destino, salvo se demonstrada causa de exclusão do nexo de causalidade, notadamente o caso fortuito, a força maior ou a culpa exclusiva da vítima ou de terceiro. 4. O fato de terceiro, conforme se apresente, pode ou não romper o nexo de causalidade. Exclui-se a responsabilidade do transportador quando a conduta praticada por terceiro, sendo causa única do evento danoso, não guarda relação com a organização do negócio e os riscos da atividade de transporte, equiparando-se a fortuito externo. De outro turno, a culpa de terceiro não é apta a romper o nexo causal quando se mostra conexa à atividade econômica e aos riscos inerentes à sua exploração, caracterizando fortuito interno. 5. Na hipótese, conforme consta no acórdão recorrido, a recorrente foi vítima de ato libidinoso praticado por outro passageiro do trem durante a viagem, isto é, um conjunto de atos referidos como assédio sexual. 6. É evidente que ser exposta a assédio sexual viola a cláusula de incolumidade física e psíquica daquele que é passageiro de um serviço de transporte de pessoas. 7. Na hipótese em julgamento, a ocorrência do assédio sexual guarda conexidade com os serviços prestados pela recorrida CPTM e, por se tratar de fortuito interno, a transportadora de passageiros permanece objetivamente responsável pelos danos causados à recorrente. Precedente. 8. Recurso especial não provido.

AgInt no AgInt no AREsp 2152026 / CE

CIVIL. AGRAVO INTERNO NO AGRAVO INTERNO NO AGRAVO EM RECURSO ESPECIAL. AUSÊNCIA DE VIOLAÇÃO DOS ARTS. 489 E 1.022 DO CPC. OMISSÕES INEXISTENTES. INDENIZAÇÃO POR DANOS MORAIS E ESTÉTICOS. ACIDENTE DE TRÂNSITO. TRANSPORTE COLETIVO. RESPONSABILIDADE CONTRATUAL OBJETIVA. CLÁUSULA DE INCOLUMIDADE DOS PASSAGEIROS. EXCLUDENTE DE RESPONSABILIDADE INEXISTENTE NO CASO CONCRETO. CULPA DE TERCEIRO. FORTUITO INTERNO. RISCO DA ATIVIDADE. VALOR DA INDENIZAÇÃO. EXCESSO NÃO CARACTERIZADO. REEXAME DE FATOS E PROVAS. IMPOSSIBILIDADE. SÚMULA N. 7/STJ. 1. Não se reconhecem a omissão e negativa de prestação jurisdicional quando há o exame, de forma fundamentada, de todas as questões submetidas à apreciação judicial na medida necessária para o deslinde da controvérsia, ainda que em sentido contrário à pretensão da parte. Ausência de violação dos arts. 489 e 1.022 do CPC. 2. Nos termos da jurisprudência desta Corte, a responsabilidade do transportador em relação aos passageiros é contratual e objetiva, somente podendo ser elidida por fortuito externo, força maior, fato exclusivo da vítima ou por fato doloso e exclusivo de terceiro - quando este não guardar conexão com a atividade de transporte. Precedentes. 3. O ato culposo de terceiro, conexo com a atividade do transportador e relacionado com os riscos próprios do negócio, caracteriza o fortuito interno, inapto a excluir a responsabilidade do transportador. 4. Hipótese em que o acidente de trânsito é risco inerente à exploração da atividade econômica de modo que, mesmo que causados exclusivamente por ato culposo de terceiro, são considerados fortuitos internos, incapazes de excluir a responsabilidade civil do transportador quanto à incolumidade dos passageiros. 5. O valor arbitrado a título de reparação civil observou os critérios de proporcionalidade e de razoabilidade, além de estar compatível com as circunstâncias narradas no acórdão e sua eventual redução demandaria, por consequência, o reexame de fatos e provas, o que é vedado em recurso especial ante o óbice da Súmua n. 7/STJ. Agravo interno improvido.

1. "Na linha dos precedentes desta Corte, acidentes ocorridos em auto-estradas, mesmo por culpa exclusiva de terceiros, são considerados fortuitos internos, incapazes, por isso, de afastar a responsabilidade Civil do transportador." (AgRg nos EDcl no REsp 1318095/MG, Rel. Ministro SIDNEI BENETI, TERCEIRA TURMA, julgado em 19/06/2012, DJe 27/06/2012).

Observe que o trespasse, por si só, importa, automaticamente, em vedação ao alienante em fazer concorrência.

Não é o contrato que proíbe a concorrência, mas a própria lei. As partes podem, no entanto, autorizar que o alienante faça concorrência.

Tratando-se de hipoteca, excepciona-se a regra do art. 299, pú, visto que o silêncio nessa situação será interpretado como assentimento.

No contexto de transmissão de obrigação, no que tange à assunção de dívida, o silêncio protege o credor. Isto é, acaso não manifeste expressa concordância quanto à assunção da dívida, será interpretado como recusa.

Se comprador ordenar o transporte da coisa, será por sua conta e risco. A exceção é quando o vendedor não cumprir com as determinações e causar prejuízo.

Contrato de compra e venda que não estipular o local da tradição, será presumido que esse local é onde a está a coisa.

PROCESSUAL CIVIL. RECURSO ESPECIAL. AÇÃO REVISIONAL DE CONTRATO DE ALUGUEL ENTRE SHOPPING CENTER E LOJISTA. SUPERVENIÊNCIA DA PANDEMIA DECORRENTE DA COVID-19. CONTRATOS PARITÁRIOS. REGRA GERAL. PRINCÍPIO DO PACTA SUNT SERVANDA. POSSIBILIDADE DE REVISÃO. HIPÓTESES EXCEPCIONAIS. PREVISÃO DO ART. 317 DO CÓDIGO CIVIL. TEORIA DA IMPREVISÃO. ART. 478 DO CÓDIGO CIVIL. TEORIA DA ONEROSIDADE EXCESSIVA. RESOLUÇÃO. INTERPRETAÇÃO SISTEMÁTICA E TELEOLÓGICA DO DISPOSITIVO QUE AUTORIZA TAMBÉM A REVISÃO. PANDEMIA DA COVID-19 QUE CONFIGURA, EM TESE, EVENTO IMPREVISÍVEL E EXTRAORDINÁRIO APTO A POSSIBILITAR A REVISÃO DO CONTRATO DE ALUGUEL, DESDE QUE PREENCHIDOS OS DEMAIS REQUISITOS LEGAIS. HIPÓTESE DOS AUTOS. AUSÊNCIA DE COMPROVAÇÃO. MANUTENÇÃO DA DECISÃO RECORRIDA.

• 1. Ação revisional de contrato de aluguel entre shopping center e lojista, ajuizada em 20/4/2020, da qual foi extraído o presente recurso especial, interposto em 30/8/2022 e concluso ao gabinete em 20/10/2022.

• 2. O propósito recursal consiste em decidir se é cabível a revisão de contrato de aluguel firmado entre shopping center e lojista, com fundamento nas teorias da imprevisão (art. 317 do CC) e onerosidade excessiva (art. 478 do CC), em razão da superveniência da pandemia do coronavírus.

• 3. Nos contratos empresariais deve ser conferido especial prestígio aos princípios da liberdade contratual e do pacta sunt servanda, diretrizes positivadas no art. 421, caput, e 421-A do Código Civil, incluídas pela Lei nº 13.874/2019.

• 4. Nada obstante, o próprio diploma legal consolidou hipóteses de revisão e resolução dos contratos (317, 478, 479 e 480 do CC). Com amparo doutrinário, verifica-se que o art. 317 configura cláusula geral de <u>revisão</u> da prestação contratual e que a interpretação sistêmica e teleológica dos arts. 478, 479 e 480 autorizam também a revisão judicial do pactuado.

• 5. A <u>Teoria da Imprevisão</u> (art. 317 do CC), de matriz francesa, exige a comprovação dos seguintes requisitos: (I) obrigação a ser adimplida em momento posterior ao de sua origem; (II) superveniência de evento imprevisível; (III) que acarrete desproporção manifesta entre o valor da prestação devida e o do momento de sua execução. A pedido da parte, o juiz poderá corrigir o valor da prestação, de modo a assegurar, quanto possível, o seu valor real.

• 6. A <u>Teoria da Onerosidade Excessiva</u> (art. 478 do CC), de origem italiana, pressupõe (I) contratos de execução continuada ou diferida; (II) superveniência de acontecimento extraordinário e imprevisível; (III) que acarrete prestação excessivamente onerosa para uma das partes; (IV) extrema vantagem para a outra; e (V) inimputabilidade da excessiva onerosidade da prestação ao lesado.

Possibilidade de flexibilização da "extrema vantagem".

• 7. A pandemia da Covid-19 configura crise sanitária sem precedentes, que não apenas colocou em risco, mas também resultou, lamentavelmente, na perda de incontáveis vidas. Diante do cenário emergencial, garantiu-se às autoridades públicas, no âmbito de suas competências, a adoção de medidas necessárias para tentar preservar, ao máximo, a saúde e a vida das pessoas (Lei nº 13.979/2020). Nesse contexto, entes da Federação decretaram a suspensão de atividades e do funcionamento de estabelecimentos comerciais e industriais (lockdown), entre os quais se destacam, por exemplo, o atendimento ao público em shopping centers - excepcionados, muitas vezes, os supermercados, laboratórios, clínicas de saúde e farmácias neles existentes.

• 8. A situação de pandemia não constitui, por si só, justificativa para o inadimplemento da obrigação, mas é circunstância que, por sua imprevisibilidade, extraordinariedade e por seu grave impacto na situação socioeconômica mundial, não pode ser desprezada pelos contratantes, tampouco pelo Poder Judiciário. Desse modo, a revisão de contratos paritários com fulcro nos eventos decorrentes da pandemia não pode ser concebida de maneira abstrata, mas depende, sempre, da análise da relação contratual estabelecida entre as partes, sendo imprescindível que a pandemia tenha interferido de forma substancial e prejudicial na relação negocial.

• 9. A superveniência de doença disseminada mundialmente, que, na tentativa de sua contenção, ocasionou verdadeiro lockdown econômico e isolamento social, qualifica-se como evento imprevisível, porquanto não foi prevista, conhecida ou examinada pelos contratantes quando da celebração do negócio jurídico, e extraordinário, pois distante da álea e das consequências ínsitas e objetivamente vinculadas ao contrato.

• 10. Conclui-se que a pandemia ocasionada pela Covid-19 pode ser qualificada como evento imprevisível e extraordinário apto a autorizar a revisão dos aluguéis em contratos estabelecidos pelo shopping center e seus lojistas, desde que verificados os demais requisitos legais estabelecidos pelo art. 317 ou 478 do Código Civil.

• 11. Na mesma linha de raciocínio, esta Corte permitiu a revisão proporcional de aluguel em razão das consequências particulares da pandemia da Covid-19 em relação à empresa de coworking, cujo faturamento foi drasticamente reduzido no período pandêmico (REsp 1.984.277/DF, Quarta Turma, DJe 9/9/2022).

• 12. Hipótese em que o contexto fático delineado pelo Tribunal de origem, soberano no exame do acervo fático-probatório, demostra não estar caracterizado o desequilíbrio na relação locatícia no contrato estabelecido entre o shopping center (recorrido) e o lojista (recorrente), pois não verificada a desproporção (art. 317) ou a excessiva onerosidade (art. 478) na prestação in concreto. Ao contrário, o acórdão estadual afirma que o recorrido concedeu desconto substancial no valor do aluguel em razão do cenário pandêmico de suspensão das atividades econômicas. Ausentes os requisitos legais, não há possibilidade de revisão do contrato. Necessidade de manutenção da decisão.

• 13. Recurso especial conhecido e desprovido.

(REsp n. 2.032.878/GO, relatora Ministra Nancy Andrighi, Terceira Turma, julgado em 18/4/2023, DJe de 20/4/2023.)

CONDIÇÕES IMPOSSÍVEIS

• Se suspensi<u>V</u>as: in<u>V</u>alidam o negócio jurídico;
• Se resolu<u>T</u>ivas: são inexis<u>T</u>en<u>T</u>es no negócio jurídico.

Essa lógica faz todo o sentido, considerando que:

• A cláusula resolutiva não impede o exercício ou a aquisição do direito. Implementada a condição resolutiva, o negócio é extinto. Com isso, se a cláusula resolutiva é impossível, apenas se risca do negócio jurídico, já que não o afetará e jamais ocorrerá de fato.

• Situação é outra quanto à cláusula suspensiva, a qual impede a aquisição do direito até a sua implementação. Logo, se negócio jurídico é subordinado à cláusula suspensiva impossível, ele jamais se concretizará, razão pela qual a lei decreta a invalidade da avença.

section header says 2025, but 6.0 was released in October 2022. still, exciting shift, and phase shifts tend to happen slower.

S ohledem na to, k čemu zpráva nakonec došla, by bylo taktičtější trochu mírnit tyto cíle.

Assim como no CPC, comparecimento espontâneo supre nulidade de intimação.

Mesma disposição do CPC quanto à inexistência de prazo específico. Com isso, o ato deve ser praticado em até 5 dias.

ADMINISTRATIVO. ENUNCIADO ADMINISTRATIVO N. 2/STJ. SERVIDOR PÚBLICO ESTADUAL. APOSENTADORIA POR INVALIDEZ. REVERSÃO. INSUBSISTÊNCIA DOS MOTIVOS GERADORES DA INCAPACIDADE LABORAL. POSSIBILIDADE. DECADÊNCIA. INOCORRÊNCIA. TEORIA DA ACTIO NATA. - 1. Não há óbices ao conhecimento dos recursos especiais submetidos a esta Corte Superior pelo Estado e pela Assembleia recorrente. - 2. A aposentadoria por invalidez é de ordem <u>temporária</u>. - 3. Verificada a insubsistência dos motivos geradores da incapacidade laboral, deve a Administração Pública proceder à reversão ao serviço público de servidor aposentado por invalidez. - 4. "O servidor aposentado por invalidez poderá ser convocado a qualquer momento para reavaliação das condições que ensejaram a aposentadoria, procedendo-se à reversão, com o seu retorno à atividade, quando a junta médica oficial declarar insubsistentes os motivos da aposentadoria (...)" (MS 15.141/DF, Rel. Ministro HAMILTON CARVALHIDO, CORTE ESPECIAL, DJe 24/05/2011), - 5. A pretensão somente se inicia com a <u>ciência da insubsistência dos motivos</u> que ensejaram a aposentadoria, uma vez que, aqui, não se está diante de anulação ou revogação do ato originário concessivo. - 6. "O curso do prazo prescricional do direito de reclamar inicia-se somente quando o titular do direito subjetivo violado passa a conhecer o fato e a extensão de suas conseqüências, conforme o princípio da 'actio nata'" (REsp 1257387/RS, Rel. Ministra ELIANA CALMON, SEGUNDA TURMA, DJe 17/09/2013). - 7. Embargos de declaração acolhidos como agravos regimentais, agravos regimentais não providos.

(EDcl no REsp n. 1.443.365/SC, relator Ministro Mauro Campbell Marques, Segunda Turma, julgado em 10/5/2016, DJe de 16/5/2016.)

Author response:

Reviewer #1 (Public review):

Major Concerns:

(1) Lack of Direct Evidence for RadD-NKp46 Interaction

The central claim that RadD interacts with NKp46 is not formally demonstrated. A direct binding assay (e.g., Biacore, ELISA, or pull-down with purified proteins) is essential to support this assertion. The absence of this fundamental experiment weakens the mechanistic conclusions of the study.

The reviewer is correct. Direct assays are currently quite impossible because RadD is huge protein and it will take years to purify it. Instead, we used immunoprecipitation assays using NKp46-Ig (Author response images 1 and 2). Fusobacteria were lysed using RIPA buffer, and the lysates were centrifuged twice to separate the supernatant from the pellet (which contains the bacterial membranes). The resulting lysates were incubated overnight with 2.5 µg of purified NKp46 and protein G-beads. After thorough washing, the bound proteins were placed in sample buffer and heated at 95 °C for 8 minutes. The eluates were run on a 10% acrylamide gel and visualized by Coomassie blue staining. As can be seen the NKp46-Ig was able to precipitate protein band around 350Kd in both F. polymorphum ATCC10953 (Author response image 1) and in F. nucleatum ATCC23726 (Author response image 2).

Author response image 1. NKp46 immunoprecipitation with Fusobacterium polymorphum (ATCC 10953) lysates. The resulting lysates of supernatant and pellet of Fusobacterium were immunoprecipitated (IP) with 2.5 μg of control fusion protein (RBD-Ig) or with NKp46-Ig. A 2.5 μg of purified fusion proteins were also run on gel.

Author response image 2. NKp46 immunoprecipitation with Fusobacterium nucleatum (ATCC 23726) lysates. The resulting lysates of supernatant and pellet of Fusobacterium were immunoprecipitated (IP) with 2.5 μg of Control fusion protein (RBD-Ig) or with NKp46-Ig. 2.5 μg of purified fusion proteins were also run on gel.

(2) Figure 2: Binding Specificity and Bacterial Strains

A CEACAM1-Ig control should be included in all binding experiments to distinguish between specific and non-specific Ig interactions. There is differential Ig binding between strains ATCC 23726 and 10953. The authors should quantify RadD expression in each strain to determine if the difference in binding is due to variation in RadD levels.

No significant difference in mCEACAM-1-Ig binding was observed across multiple independent experiments. Author response image 3 shows a representative histogram showing mCEACAM-1-Ig binding to F. nucleatum ATCC 23726 and F. polymorphum ATCC 10953. Comparable binding levels were detected in both bacterial species (upper histogram). Similarly, NKp46-Ig and Ncr1-Ig fusion proteins exhibited comparable binding patterns (lower histogram). It is currently not possible to quantify RadD expression directly, as no anti-RadD antibody is available.

Author response image 3. CEACAM-1 Ig binding to Fusobacterium ATCC 23726 and ATCC 10953. Upper histograms show staining with secondary antibody alone (gray) compared to CEACAM-1 Ig (black line). Lower histograms show binding of NKp46 and Ncr1 fusion proteins to the two Fusobacterium strains. Gray represent secondary antibody controls.

(3) Figure 3: Flow Cytometry Inconsistencies and Missing Controls

What do the FITC-negative, Ig-negative events represent? The authors should clarify whether these are background signals, bacterial aggregates, or debris.

We now present the gating strategy used in these experiments (Author response image 4). Fusion negative Ig samples were the bacterial samples stained only with the secondary antibody APC (anti-human AF647). The TITC-negative represent unlabeled bacteria.

Author response image 4. Gating strategy for FITC-labeled Fusobacterium stained with fusion proteins. Bacteria were first gated as shown in the left panel. The gated population was then further analyzed in the right plot: the lower-left quadrant represents bacterial debris, the upper-left quadrant corresponds to FITC-stained bacteria only, and the upper-right quadrant shows bacteria double-positive for FITC and APC, indicating binding of the fusion proteins.

Panel B, CEACAM1-Ig binding appears markedly increased compared to WT bacteria. The reason for this enhancement should be discussed-does it reflect upregulation of the bacterial ligand or an artifact of overexpression? Fluorescence compensation should be carefully reviewed for the NKp46/NCR1-Ig binding assays to ensure that the signals are not due to spectral overlap or nonspecific binding. Importantly, binding experiments using the FadI/RadD double knockout strain are missing and should be included. This control is essential.

We don’t know why expression of CEACAM1-Ig binding is increased. Indeed, it will be nice to have the FadI/RadD double knockout strain which we currently don’t have.

In Panel E, the basis for calculating fold-change in MFI is unclear. Please indicate the reference condition to which the change is normalized.

The mean fluorescence intensity (MFI) fold change was calculated by dividing the MFI obtained from staining with the fusion proteins by the MFI of the corresponding secondary antibody control (bacteria incubated without fusion proteins).

(4) Figure 4: Binding Inhibition and Receptor Sensitivity

Panel A lacks representative FACS plots and is currently difficult to interpret.

Fusobacteria binding to CEACAM-1, NKp46, and NCR1 fusion proteins was tested in the presence of 5 and 10 mM L-arginine (Author response image 5). L-arginine inhibited the binding of NKp46-Ig and NCR1-Ig, whereas no effect was observed on CEACAM-1-Ig binding.

Author response image 5. Fusobacterium binding inhibition by L-Arginine. The figure shows the binding of CEACAM1-Ig (left panel), NKp46-Ig (middle panel), and Ncr1-Ig (right panel) in the presence of 0 mM (black), 5 mM (red), and 10 mM (blue) L-arginine.

Differences in the sensitivity of human vs. mouse NKp46 to arginine inhibition should be discussed, given species differences in receptor-ligand interactions.

Ncr1, the murine orthologue of human NKp46, shares approximately 58% sequence identity with its human counterpart (1). The observed differences in arginine-mediated inhibition of bacterial binding between mouse and human NKp46 might stem from structural differences or distinct posttranslational modifications, such as glycosylation. Indeed, prediction algorithms combined with high-performance liquid chromatography analysis revealed that Ncr1 possesses two putative novel O-glycosylation sites, of which only one is conserved in humans (2).

References

(1) Biassoni R., Pessino A., Bottino C., Pende D., Moretta L., Moretta A. The murine homologue of the human NKp46, a triggering receptor involved in the induction of natural cytotoxicity. Eur J Immunol. 1999 Mar; 29(3).

(2) Glasner A., Roth Z., Varvak A., Miletic A., Isaacson B., Bar-On Y., Jonjić S., Khalaila I., Mandelboim O. Identification of putative novel O-glycosylations in the NK killer receptor Ncr1 essential for its activity. Cell Discov. 2015 Dec 22; 1:15036.

What are the inhibition results using F. nucleatum strains deficient in FadI?

The inhibition pattern observed in the F. nucleatum ΔFadI mutant was comparable to that of the wild-type strain (Author response image 6). When cultured under identical conditions and exposed to increasing concentrations of arginine (0, 5, and 10 mM), the F. nucleatum ΔFadI strain also demonstrated a dose-dependent reduction in binding to NKp46 and Ncr1.

Author response image 6. Arginine inhibition of NKp46-Ig and Ncr1-Ig binding in F. nucleatum ΔFadI. Histograms show NKp46-Ig (A, C) and Ncr1-Ig (B, D) binding to F. nucleatum ATCC10953 ΔFadI (A and B) and to F. nucleatum ATCC23726 ΔFadI (A and B) following exposure to 5 mM and 10 mM L-Arginine. Panels (E) and (F) display the mean fluorescence intensity (MFI) quantification corresponding to (A and B) and (C and D), respectively.

In Panel B, CEACAM1-Ig and RadD-deficient bacteria must be included as negative controls for binding specificity upon anti-NKp46 blocking.

We appreciate the request to include CEACAM1-Ig and RadD-deficient bacteria as negative controls for specificity under anti-NKp46 blocking. We don’t not think it is necessary since the 02 antibody is specific for NKp46, we used other anti0NKp46 antibodies that did not block the interaction and an irrelevant antibofy, we showed that arginine produced a dose-dependent reduction in NKp46/Ncr1 binding, consistent with an arginine-inhibitable RadD interaction already shown in our manuscript (Fig. 4A). The ΔRadD strains we used already demonstrate loss of NKp46/Ncr1 binding and loss of NK-boosting activity (Figs. 3, 5). Collectively, these data establish that NKp46/Ncr1 recognition of a high-molecular-weight ligand consistent with RadD is specific and functionally relevant.

Figure 5: Functional NK Activation and Tumor Killing

In Panels B and C, the key control condition (NK cells + anti-NKp46, without bacteria) is missing. This is needed to evaluate if NKp46 recognition is involved in tumor killing. The authors should explicitly test whether pre-incubation of NK cells with bacteria enhances their anti-tumor activity.

No significant difference in NK cell cytotoxicity was observed between untreated NK cells and NK cells incubated with anti-NKp46 antibody in the absence of bacteria. Therefore, the NK + anti-NKp46 (O2) group was included as an additional control alongside the other experimental conditions shown in Figures 5b and 5c, and is presented in Author response image 7 below.

Author response image 7. NK cytotoxicity against breast cancer cell lines. NK cell cytotoxicity against T47D (left) and MCF7 (right) breast cancer cell lines. This experiment follows the format of Figure 5b and 5c, with the addition of the NK cells + O2 antibody group. No significant differences were observed when values were normalized to NK cells alone.

Could bacteria induce stress signals in tumor cells that sensitize them to NK killing? This distinction is critical.

It remains unclear whether the bacteria induce stress-related signals in tumor cells that render them more susceptible to NK cell–mediated cytotoxicity.

(6) Figure 5D: Mechanism of Peripheral Activation

It is suggested that contact between bacteria and NK cells in the periphery leads to their activation. Can the authors confirm whether this pre-activation leads to enhanced killing of tumor targets, or if bacteria-tumor co-localization is required? The literature indicates that F. nucleatum localizes intracellularly within tumor cells. If so, how is RadD accessible to NKp46 on infiltrating NK cells?

We do not expect that pre-activation of NK cells with bacteria would enhance their tumor-killing capacity. In fact, when NK cells were co-incubated with bacteria, we occasionally observed NK cell death. Although F. nucleatum can reside intracellularly, bacterial entry requires prior adhesion to tumor cells. At this stage—before internalization—the bacteria are accessible for recognition and binding by NK cells.

(8) Figure 5E and In Vivo Relevance

Surprisingly, F. nucleatum infection is associated with increased tumor burden. Does this reflect an immunosuppressive effect? Are NK cells inhibited or exhausted in infected mice (TGIT, SIGLEC7...)? If NK cell activation leads to reduced tumor control in the infected context, the role of RadD-induced activation needs further explanation. RadD-deficient bacteria, which do not activate NK cells, result in even poorer tumor control. This paradox needs to be addressed: how can NK activation impair tumor control while its absence also reduces tumor control?

Siglec-7 lacks a direct orthologue in mice, and neither mouse TIGIT nor CEACAM1 bind F. nucleatum. The increased tumor burden observed in infected mice may therefore result from bacterial interference with immune cell infiltration and accumulation within the tumor microenvironment (Parhi, L., Alon-Maimon, T., Sol, A. et al. Breast cancer colonization by Fusobacterium nucleatum accelerates tumor growth and metastatic progression. Nat Commun 11, 3259 (2020)). Consequently, the NK cells that do reach the tumor site can recognize and kill F. nucleatum–bearing tumor cells through RadD–NKp46 interactions. In the absence of RadD, this recognition is impaired, leading to reduced NK-mediated cytotoxicity and increased tumor growth.

(9) NKp46-Deficient Mice: Inconsistencies

In Ncr1⁻/⁻ mice, infection with WT or RadD-deficient F. nucleatum has no impact on tumor burden. This suggests that NKp46 is dispensable in this context and casts doubt on the physiological relevance of the proposed mechanism. This contradiction should be discussed more thoroughly.

Ncr1 is also directly involved in mediating NK cell–dependent killing of tumor cells, even in the absence of bacterial infection. Therefore, in Ncr1-deficient mice, F. nucleatum has no additional effect on tumor progression (Glasner, A., Ghadially, H., Gur, C., Stanietsky, N., Tsukerman, P., Enk, J., Mandelboim, O. Recognition and prevention of tumor metastasis by the NK receptor NKp46/NCR1. J Immunol. 2012).

Reviewer #2 (Public review):

Weaknesses:

(1) A previous study by this group (PMID: 38952680) demonstrated that RadD of F. nucleatum binds to NK cells via Siglec-7, thereby diminishing their cytotoxic potential. They further proposed that the RadD-Siglec-7 interaction could act as an immune evasion mechanism exploited by tumor cells. In contrast, the present study reports that RadD of F. nucleatum can also bind to the activating receptor NKp46 on NK cells, thereby enhancing their cytotoxic function.

Siglec-7 lacks a direct orthologue in mice, and neither mouse TIGIT nor CEACAM1 bind F. nucleatum. In contrast, NKp46 and its murine homologue, Ncr1, both recognize and bind the bacterium.

While F. nucleatum-mediated tumor progression has been documented in breast and colon cancers, the current study proposes an NK-activating role for F. nucleatum in HNSC. However, it remains unclear whether tumor-infiltrating NK cells in HNSC exhibit differential expression of NKp46 compared to Siglec-7. Furthermore, heterogeneity within the NK cell compartment, particularly in the relative abundance of NKp46⁺ versus Siglec-7⁺ subsets, may differ substantially among breast, colon, and HNSC tumors. Such differences could have been readily investigated using publicly available single-cell datasets. A deeper understanding of this subset heterogeneity in NK cells would better explain why F. nucleatum is passively associated with a favorable prognosis in HNSC but correlates with poor outcomes in breast and colon cancers.

Currently, there are no publicly available single-cell datasets suitable for characterizing NK cell heterogeneity in the context of F. nucleatum infection—particularly regarding the expression of Siglec-7, NKp46, or CEACAM1 and their potential association with poor clinical outcomes in breast, head and neck squamous cell carcinoma (HNSC), or colorectal cancer (CRC). Furthermore, no RNA-seq datasets are available for breast cancer cases specifically associated with F. nucleatum infection and poor prognosis. Therefore, we analyzed bulk RNA expression datasets for Siglec-7 and CEACAM1 and evaluated their associations with HNSC and CRC using the same patient databases utilized in our manuscript (Author response image 8). No significant differences in Siglec-7 expression were detected between HNSC and CRC samples (Author response image 8A). Although CEACAM1 mRNA levels did not differ between F. nucleatum–positive and –negative cases within either cancer type, its overall expression was higher in CRC compared to HNSC (Author response image 8B).

Author response image 8. Siglec7 and Ceacam1 expression and the prognostic effect of F. nucleatum in a tumor-type-specific manner. Comparison of Siglec7 (A) and Ceacam1 (B) expression across HNSC and CRC tumors. Log₂ expression levels of NKp46 mRNA were compared across HNSC and CRC cohorts, stratified by F. nucleatum positive and negative. Results were analyzed by one-way ANOVA with Bonferroni post hoc correction.

(2) The in vivo tumor data (Figure 5D-F) appear to contradict the authors' claims. Specifically, Figure 5E suggests that WT mice engrafted with AT3 breast tumors and inoculated with WT F. nucleatum exhibited an even greater tumor burden compared to mice not inoculated with F. nucleatum, indicating a tumor-promoting effect. This finding conflicts with the interpretation presented in both the results and discussion sections.

Siglec-7 lacks a direct orthologue in mice, and neither mouse TIGIT nor CEACAM1 bind F. nucleatum. The increased tumor burden observed in infected mice may therefore result from bacterial interference with immune cell infiltration and accumulation within the tumor microenvironment (Parhi, L., Alon-Maimon, T., Sol, A. et al. Breast cancer colonization by Fusobacterium nucleatum accelerates tumor growth and metastatic progression. Nat Commun 11, 3259 (2020)). Consequently, the NK cells that do reach the tumor site can recognize and kill F. nucleatum–bearing tumor cells through RadD–NKp46 interactions. In the absence of RadD, this recognition is impaired, leading to reduced NK-mediated cytotoxicity and increased tumor growth.

(3) Although the authors acknowledge that F. nucleatum may have tumor context-specific roles in regulating NK cell responses, it is unclear why they chose a breast cancer model in which F. nucleatum has been reported to promote tumor growth. A more appropriate choice would have been the well-established preclinical oral cancer model, such as the 4-nitroquinoline 1-oxide (4NQO)-induced oral cancer model in C57BL/6 mice, which would more directly relate to HNSC biology.

The tumor model we employed is, to date, the only model in which F. nucleatum has been shown to exert a measurable effect, which is why we selected it for our study (Parhi, L., Alon-Maimon, T., Sol, A. et al. Breast cancer colonization by Fusobacterium nucleatum accelerates tumor growth and metastatic progression. Nat Commun. 2020; 11: 3259). We have not tested the 4-nitroquinoline-1-oxide (4NQO)–induced oral cancer model, and we are uncertain whether its use would be ethically justified.

(4) Since RadD of F. nucleatum can bind to both Siglec-7 and NKp46 on NK cells, exerting opposing functional effects, the expression profiles of both receptors on intratumoral NK cells should be evaluated. This would clarify the balance between activating and inhibitory signals in the tumor microenvironment and provide a more mechanistic explanation for the observed tumor context-dependent outcomes.

This question was answered in Author response image 8 above.

Lo que más me llamó la atención de la lectura fue la comparación entre la desconfianza de Sócrates hacia la escritura y las críticas actuales hacia la inteligencia artificial. Me pareció muy interesante cómo el autor muestra que, aunque una tecnología pueda generar temor o resistencia, finalmente termina transformando la manera en que pensamos y vivimos, tal como ocurrió con la escritura o las redes sociales. La frase que más me impactó fue: “Si absolutamente todos adoptáramos su uso en todas las áreas de la vida, pronto nadie tendría habilidades.” Me hizo reflexionar sobre la dependencia que estamos desarrollando hacia la inteligencia artificial y sobre el riesgo de perder la capacidad de aprender y crear por nosotros mismos. Creo que el texto podría mejorar si el autor profundizara un poco más en las posibles formas de integrar la IA sin perder el valor del aprendizaje humano, por ejemplo, mostrando ejemplos positivos de cómo esta tecnología puede complementar nuestras capacidades en lugar de reemplazarlas. También sería interesante incluir una perspectiva más global, considerando cómo distintos contextos culturales enfrentan la adopción de la IA.

Author response:

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

Reviewer #3 (Public review): 

Summary: 

The manuscript explores behavioral responses of C. elegans to hydrogen sulfide, which is known to exert remarkable effects on animal physiology in a range of contexts. The possibility of genetic and precise neuronal dissection of responses to H2S motivates the study of responses in C. elegans. The revised manuscript does not seem to have significantly addressed what was lacking in the initial version. 

The authors have added further characterization of possible ASJ sensing of H2S by calcium imaging but ASJ does not appear to be directly involved. Genetic and parallel analysis of O2 and CO2 responsive pathways do not reveal further insights regarding potential mechanisms underlying H2S sensing. Gene expression analysis extends prior work. Finally, the authors have examined how H2S-evoked locomotory behavioral responses are affected in mutants with altered stress and detoxification response to H2S, most notably hif-1 and egl-9. These data, while examining locomotion, are more suggestive that observed effects on animal locomotion are secondary to altered organismal toxicity as opposed to specific behavioral responedse 

Overall, the manuscript provides a wide range of intriguing observations, but mechanistic insight or a synthesis of disparate data is lacking. 

We thank the reviewer for the valuable feedback. We agree that while our investigation provides broad coverage, it does not fully resolve the mechanisms of H₂S perception. As both reviewers noted, the avoidance response to high levels of H₂S is most likely driven by its toxicity, particularly at the level of mitochondria, rather than by direct perception of H₂S. We also favor this model and have revised the results and discussion to highlight this interpretation, while acknowledging that other mechanisms cannot be excluded (main changes lines 387-402 and 535-547).

Building on this view, our observations point toward mitochondrial ROS transients as the trigger for H₂S avoidance. First, toxic levels of H₂S are known to promote ROS production (1). Second, similar to acute H₂S, brief exposure to rotenone, an ETC complex I inhibitor that rapidly generates mitochondrial ROS, triggers locomotory responses (Figure 7E) (Lines 393-396). Third, regardless of duration, rotenone exposure inhibits H₂S-evoked avoidance (Figure 7E) (Lines 389-391), likely by preventing or dampening H₂S-evoked mitochondrial ROS bursts when ETC function is impaired and ROS is already high. Notably, animals subjected to prolonged rotenone exposure, ETC mutants, and quintuple sod mutants, each experiencing chronically high ROS levels, fail to respond to H₂S and display reduced locomotory activity, presumably due to ROS toxicity and/or activation of stress-adaptive mechanisms (Figure 7).

Consistent with the activation of stress-responsive pathways, H₂S exposure alters expression of genes controlled by SKN-1 and HIF-1 signaling. Both pathways are ROS-sensitive and promote adaptation to chronic ROS production (2-4). Their activation, as in egl-9, render these animals insensitive to H₂S-evoked ROS transients (Figure 5B) (Lines 303-305). Conversely, mutants defective in these adaptive pathways, such as hif-1, still show initial locomotory responses to H₂S, but rapidly lose activity during prolonged H₂S exposure (Figure 5D) (Lines 318-319). These observations suggest that HIF-1 pathway is dispensable for initiating the response to H₂S evoked ROS transients, but essential for protecting against ROS toxicity.

In this context, the neural circuit we examined, such as ASJ neurons, is not directly involved in H₂S perception (Line 165-169 and 448-457). Instead, it likely modulates a circuit that is responsive to ROS toxicity. This circuit is also influenced by ambient O₂ levels, the state of O₂ sensing circuit, and nutrient status, in a manner reminiscent of the CO₂ responses (5, 6).

Reviewer #4 (Public review): 

Summary: 

The authors establish a behavioral paradigm for avoidance of H2S and conduct a large candidate screen to identify genetic requirements. They follow up by genetically dissecting a large number of implicated pathways - insulin, TGF-beta, oxygen/HIF-1, and mitochondrial ROS, which have varied effects on H2S avoidance. They additionally assay whole-animal gene expression changes induced by varying concentrations and durations of H2S exposure. 

Strengths: 

The implicated pathways are tested extensively through mutants of multiple pathway molecules. The authors address previous reviewer concerns by directly testing the ability of ASJ to respond to H2S via calcium imaging. This allows the authors to revise their previous conclusion and determine that ASJ does not directly respond to H2S and likely does not initiate the behavioral response. 

We thank the reviewer for the supportive comments.

Weaknesses: 

Despite the authors focus on acute perception of H2S, I don't think the experiments tell us much about perception. I think they indicate pathways that modulate the behavior when disrupted, especially because most manipulations used broadly affect physiology on long timescales. For instance, genetic manipulation of ASJ signaling, oxygen sensing, HIF-1 signaling, mitochondrial function, as well as starvation are all expected to constitutively alter animal physiology, which could indirectly modulate responses to H2S. The authors rule out effects on general locomotion in some cases, but other physiological changes could relatively specifically modulate the H2S response without being involved in its perception. 

I am actually not convinced that H2S is directly perceived by the C. elegans nervous system at all. As far as I can tell, the avoidance behavior could be a response to H2S-induced tissue damage rather than the gas itself. 

We thank the reviewer for the valuable insights, and fully agree that the H₂S may not be directly perceived by C. elegans. Please see detailed responses below.

Reviewer #4 (Recommendations for the authors): 

The clarity of the paper is improved in this version. My main issue has to do with "perception" of H2S. At times the authors suggest that hydrogen sulfide should be perceived by a neural circuit ("we did not specifically identify the neural circuit mediating H2S signaling"), while at other times they discuss the possibility that it is not directly perceived neuronally ("Supporting the idea that acute mitochondrial ROS generation initiates avoidance of high H2S levels,"). The authors should clearly state their model for H2S perception. Do they think there is a receptor and sensory neuron for H2S (not identified in this paper)? If not, what does it mean for there to be a neural circuit mediating the response? To me, it looks more like what is being "perceived" by a neural circuit is ROS-induced toxicity, not H2S itself. 

To drill down on direct modulation of acute perception, are any of the pathway manipulations used in this paper performed on the timescale of perception? Rotenone for 10 mins is close to that timescale, and in fact it increases speed independently of H2S, consistent with ROSinduced toxicity, not H2S being the signal that induces the behavior. Optogenetic activation of RMG could also be on the acute timescale. Can the authors clarify for how long blue light was on the worms before the start of the assay? Or was it turned on at the same time as video acquisition commenced? This could be evidence that RMG acutely modulates this behavioral response. 

I feel that the ASJ calcium imaging data should be in the main figure given its importance in revising the original model. 

We thank the reviewer for the valuable advice.

As suggested, ASJ calcium imaging data are displayed in the main figure (Figure 2I) (Line 167).

As both reviewers noted, our initial presentation was not sufficiently clear regarding the mechanism underlying H₂S avoidance. We agree with the reviewer that H₂S avoidance is unlikely mediated by direct perception via a H₂S-specific receptor, but likely arises from acute mitochondrial dysfunction and ROS generation. 

ROS

In line with the reviewer’s perspective, our observations point toward mitochondrial ROS transients as the trigger for H₂S avoidance. First, toxic levels of H₂S are known to promote ROS production (1). Second, similar to acute H₂S, brief exposure to rotenone, an ETC complex I inhibitor that rapidly generates mitochondrial ROS, triggers locomotory responses (Figure 7E) (Lines 393-396). Third, regardless of duration, rotenone exposure inhibits H₂S-evoked avoidance (Figure 7E) (Lines 389-391), likely by preventing or dampening H₂S-evoked mitochondrial ROS bursts when ETC function is impaired and ROS is already high. Notably, animals subjected to prolonged rotenone exposure, ETC mutants, and quintuple sod mutants, each experiencing chronically high ROS levels, fail to respond to H₂S and display reduced locomotory activity, presumably due to ROS toxicity and/or activation of stress-adaptive mechanisms (Figure 7). We revised the Results and Discussion to present the model more consistently (main changes lines 387-402 and 535-547).

Consistent with the activation of stress-responsive pathways, H₂S exposure alters expression of genes controlled by SKN-1 and HIF-1 signaling. Both pathways are ROS-sensitive and promote adaptation to chronic ROS production (2-4). Their activation, as in egl-9, render these animals insensitive to H₂S-evoked ROS transients (Figure 5B) (Lines 303-305). Conversely, mutants defective in these adaptive pathways, such as hif-1, still show initial locomotory responses to H₂S, but rapidly lose activity during prolonged H₂S exposure (Figure 5D) (Lines 318-319). These observations suggest that HIF-1 pathway is dispensable for initiating the response to H₂ Sevoked ROS transients, but essential for protecting against ROS toxicity.

ASJ neurons

ASJ neurons and DAF-11 signaling are required for H₂S-evoked behavioral responses. However, ASJ does not exhibit an H₂S-evoked calcium transient. It suggests that ASJ neurons do not directly detect H₂S (Line 165-169 and 448-457), but likely modulate the circuit responsive to ROS toxicity. This circuit can also be modulated by ambient O₂ levels, the state of O₂ sensing circuit, and nutrient status, in a manner reminiscent of the CO₂ responses (5, 6). 

O₂ sensing circuit

Consistent with the reviewer’s view, we favor the model that H₂S avoidance is likely induced by ROS transients. We believe that the state of O₂ sensing circuit, similar to ASJ neurons, modulates the neural circuit that is responsive to H₂S-evoked ROS toxicity. This circuit is inhibited as long as O₂ sensing circuit is active. In the RMG optogenetic experiment, channelrhodopsin was photo-stimulated as soon as the assay was initiated at 7% O₂ (Methods Lines 633-634 and Figure legend Lines 1177-1178), therefore RMG remained active throughout the assay including at 7% O₂. Our interpretation is that RMG activation inhibits this ROSresponsive circuit and H₂S avoidance. However, these observations do not resolve if H₂S is acutely and directly perceived. The modulation of H₂S response by O₂ circuit was discussed between Lines 437-447.

References

(1) J. Jia et al., SQR mediates therapeutic effects of H(2)S by targeting mitochondrial electron transport to induce mitochondrial uncoupling. Sci Adv 6, eaaz5752 (2020).

(2) S. J. Lee, A. B. Hwang, C. Kenyon, Inhibition of Respiration Extends C. elegans Life Span via Reactive Oxygen Species that Increase HIF-1 Activity. Current Biology 20, 2131-2136 (2010).

(3) C. Lennicke, H. M. Cocheme, Redox metabolism: ROS as specific molecular regulators of cell signaling and function. Mol Cell 81, 3691-3707 (2021).

(4) D. A. Patten, M. Germain, M. A. Kelly, R. S. Slack, Reactive oxygen species: stuck in the middle of neurodegeneration. J Alzheimers Dis 20 Suppl 2, S357-367 (2010).

(5) A. J. Bretscher, K. E. Busch, M. de Bono, A carbon dioxide avoidance behavior is integrated with responses to ambient oxygen and food in Caenorhabditis elegans. Proc Natl Acad Sci U S A 105, 8044-8049 (2008).

(6) E. A. Hallem, P. W. Sternberg, Acute carbon dioxide avoidance in Caenorhabditis elegans. Proc Natl Acad Sci U S A 105, 8038-8043 (2008).

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Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

Summary:

The manuscript characterizes a functional peptidergic system in the echinoderm Apostichopus japonicus that is related to the widely conserved family of calcitonin/diuretic hormone 31 (CT/DH31) peptides in bilaterian animals. In vitro analysis of receptor-ligand interactions, using multiple receptor activation assays, identifies three cognate receptors for two CT-like peptides in the sea cucumber, which stimulate cAMP, calcium, and ERK signaling. Only one of these receptors clusters within the family of calcitonin and calcitonin-like receptors (CTR/CLR) in bilaterian animals, whereas two other receptors cluster with invertebrate pigment dispersing factor receptors (PDFRs). In addition, this study sheds light on the expression and in vivo functions of CT-like peptides in A. japonicus, by quantitative real-time PCR, immunohistochemistry, pharmacological experiments on body wall muscle and intestine preparations, and peptide injection and RNAi knockdown experiments. This reveals a conserved function of CT-like peptides as muscle relaxants and growth regulators in A. japonicus.

Strengths:

This work combines both in vitro and in vivo functional assays to identify a CT-like peptidergic system in an economically relevant echinoderm species, the sea cucumber A. japonicus. A major strength of the study is that it identifies three G protein-coupled receptors for AjCT-like peptides, one related to the CTR/CLR family and two related to the PDFR family. A similar finding was previously reported for the CT-related peptide DH31 in Drosophila melanogaster that activates both CT-type and PDF-type receptors. Here, the authors expand this observation to a deuterostomian animal, which suggests that receptor promiscuity is a more general feature of the CT/DH31 peptide family and that CT/DH31-like peptides may activate both CT-type and PDF-type receptors in other animals as well.

Besides the identification of receptor-ligand pairs, the downstream signaling pathways of AjCT receptors have been characterized, revealing broad and in some cases receptor-specific effects on cAMP, calcium, and ERK signaling.

Functional characterization of the CT-related peptide system in heterologous cells is complemented with ex vivo and in vivo experiments. First, peptide injection and RNAi knockdown experiments establish transcriptional regulation of all three identified receptors in response to changing AjCT peptide levels. Second, ex vivo experiments reveal a conserved role for the two CT-like peptides as muscle relaxants, which have differential effects on body wall muscle and intestine preparations. Finally, peptide injection and knockdown experiments uncover a growth-promoting role for one CT-like peptide (AjCT2). Injection of AjCT2 at high concentration, or long-term knockdown of the AjCT precursor, affects diverse growth-related parameters including weight gain rate, specific growth rate, and transcript levels of growth-regulating transcription factors. The authors also reveal a growth-promoting function for the PDFR-like receptor AjPDFR2, suggesting that this receptor mediates the effects of AjCT2 on growth.

Weaknesses:

The authors present a more detailed phylogenetic analysis in the revised version, including a larger number of species. But some clusters in the analysis are not well supported because they have only low bootstrap values. This makes it difficult to interpret the clustering in some parts of the tree.

Thank you for the reviewer’s comments. In response, we have produced a new phylogenetic analysis using the maximum likelihood method. This was done by Nayeli Escudero Castelán and Kite Jones in the Elphick group at QMUL and therefore they have been added as co-authors of this paper. The new phylogenetic tree (Figure 2, line 206) includes broad taxonomic sampling of CT-type receptors and PDF-type receptors. CRH-type receptors, which are also members of the secretin-type GPCR sub-family, have been included as an outgroup to root the tree. In the previous version the much more distantly related vasopressin/oxytocin-type receptors, which are rhodopsin-type GPCRs, were included as an outgroup. Furthermore, VIP-type receptors were also included in the previous tree but these have been omitted from the new tree because VIP receptor orthologs only occur in vertebrates and therefore they are not representative of a bilaterian GPCR family. The new tree shows high bootstrap support for key clades, notably achieving a bootstrap value of 100 for a clade comprising both deuterostomian and protostomian PDF receptors. This provides important evidence that the A. japonicus PDF-type receptors characterised in this study (AjPDFR1, AjPDFR2) are co-orthologs of the PDF-type receptor that has been characterised previously in Drosophila. Similarly, there is strong bootstrap support (100) for a clade comprising CT/DH31-type receptors and, importantly, the CT-type receptor characterised in this study (AjCTR) is positioned in a branch of this clade that comprises deuterostomian CT-type receptors (with bootstrap support of 100). Details of methods employed to produce the new receptor tree are included in lines 727-739. The new phylogenetic tree is shown below and has been incorporated into the revised manuscript (Figure 2, line 206). The description of new phylogenetic tree has also been modified accordingly in the revised manuscript (line 169-183).

References:

Bauknecht P, Jékely G. Large-Scale Combinatorial Deorphanization of Platynereis Neuropeptide GPCRs. Cell reports, 2015, 12(4), 684–693. doi:  10.1016/j.celrep.2015.06.052.

Beets I, Zels S, Vandewyer E, Demeulemeester J, et al. System-wide mapping of peptide-GPCR interactions in C. elegans. Cell reports, 2023, 42(9), 113058. doi: 10.1016/j.celrep.2023.113058.

Cardoso J C, Mc Shane J C, Li Z, et al. Revisiting the evolution of Family B1 GPCRs and ligands: Insights from mollusca. Molecular and cellular endocrinology, 2024, 586, 112192. doi: 10.1016/j.mce.2024.112192.

Gorn A H, Lin H Y, Yamin M, et al. Cloning, characterization, and expression of a human calcitonin receptor from an ovarian carcinoma cell line. The Journal of clinical investigation, 1992, 90(5), 1726–1735. doi: 10.1172/JCI116046.

Huang T, Su J, Wang X, et al. Functional Analysis and Tissue-Specific Expression of Calcitonin and CGRP with RAMP-Modulated Receptors CTR and CLR in Chickens. Animals: an open access journal from MDPI, 2024, 14(7), 1058. doi: 10.3390/ani14071058.

Johnson E C, Shafer O T, Trigg J S, et al. A novel diuretic hormone receptor in Drosophila: evidence for conservation of CGRP signaling. Journal of Experimental Biology, 2005, 208(7): 1239-1246. doi: 10.1242/jeb.01529.

McLatchie L M, Fraser N J, Main M J, et al. RAMPs regulate the transport and ligand specificity of the calcitonin-receptor-like receptor. Nature, 1998, 393(6683): 333-339. doi: 10.1038/30666.

Schwartz J, Réalis-Doyelle E, Dubos M P, et al. Characterization of an evolutionarily conserved calcitonin signaling system in a lophotrochozoan, the Pacific oyster (Crassostrea gigas). Journal of Experimental Biology, 2019, 222(13): jeb201319. doi: 10.1242/jeb.201319.

Sekiguchi T, Kuwasako K, Ogasawara M, et al. Evidence for conservation of the calcitonin superfamily and activity-regulating mechanisms in the basal chordate Branchiostoma floridae: insights into the molecular and functional evolution in chordates. Journal of Biological Chemistry, 2016, 291(5): 2345-2356. doi: 10.1074/jbc.M115.664003.

Expression of CT-like peptides was investigated both at transcript and protein level, but insight into the expression of the three peptide receptors is limited. This makes it difficult to understand the mechanism underlying the (different) functions of the two CT-like peptides in vivo. The authors identify differences in signal transduction cascades activated by each peptide, which might underpin distinct functions, but these differences were established only in heterologous cells.

We appreciate the reviewer's insightful comments. Regarding expression of CT-like peptide receptors, we have quantitatively analyzed the mRNA expression levels of the three receptors in key tissues using qRT-PCR (Figure 6, line 319) and receptor expression exhibits significant tissue-specific differences. Combined with the heterologous expression assays and In vivo functional validation, we believe our findings have provided clear mechanistic insights into the functional divergence of the two CT-like peptides. Investigation of the expression of the three receptor proteins in A. japonicus would require generation of specific antibodies, which was beyond the scope of this study. Furthermore, immunohistochemical visualization of neuropeptide receptor expression in other invertebrates has not been reported widely, which likely reflects technical difficulties in generation of antibodies that can be used to specifically detect receptor proteins that are typically expressed a low level in comparison to the neuropeptides that act as their ligands. 

We acknowledge that investigating signal transduction cascades in heterologous cells (rather than native A. japonicus cells) is a limitation. However, as a non-model organism, A. japonicus currently lacks established cell lines for such research. Therefore, using heterologous cells was the most feasible approach to examine the differential signaling cascades activated by the peptides through the three receptors. Importantly, our in vivo experiments demonstrated that long-term knockdown of either the AjCT precursor or AjPDFR2 resulted in similar and significant growth defects. The phenotypic consistency strongly suggests that AjCT2 and AjPDFR2 function within the same signaling pathway, with AjPDFR2 serving as the key receptor functionally activated by AjCT2.

The authors show overlapping phenotypes for a long-term knockdown of the AjCT precursor and the AjPDFR2 receptor, suggesting that the growth-regulating functions of AjCT2 are mediated by this receptor pathway. However, it remains unclear whether this mechanism underpins the growth-regulating function of AjCT2, until further in vivo evidence for this ligand-receptor interaction is presented. For example, the authors could investigate whether knockdown of AjPDFR2 attenuates the effects of AjCT2 peptide injection. In addition, a functional PDF system in this species remains uncharacterized, and a potential role of PDF-like peptides in growth regulation has not yet been investigated in A. japonicus. Therefore, it also remains unclear whether the ability of CT-like peptides to activate PDFRs is an evolutionary ancient property of this peptide family or whether this is an example of convergent evolution in some protostomian (Drosophila) and deuterostomian (sea cucumber) species.

Thank you for the reviewer’s insightful comments and constructive questions. We acknowledge the request for more direct evidence to demonstrate how AjCT2 functions in vivo through AjPDFR2. However, long-term knockdown of the AjCT precursor and AjPDFR2 both resulted in identical and significant growth defect phenotypes. The high phenotypic consistency, combined with the activation effect of AjCT2 on AjPDFR2 in heterologous cells, strongly suggests that they function within the same signaling pathway, with AjPDFR2 serving as the key receptor functionally activated by AjCT2. While exogenous peptide injection combined with receptor knockdown is a classic method for verifying receptor activation, phenotypic overlap itself is widely accepted in genetic research as robust evidence for pathway association (Shafer and Taghert, 2009; Van Sinay et al., 2017). A. japonicus is a non-model organism with a 3-month aestivation period in summer followed shortly by winter hibernation. During these periods, we are unable to conduct in vivo experiments. Any single experimental suggestion from reviewers could potentially require one more year of research and we have already conducted an additional year of research, in response to reviewer feedback, since submitting the original manuscript. We hope therefore that these challenges associated with working with aquatic invertebrate non-model organisms is recognized by the reviewers.

We fully agree that the functional PDF/PDFR system in A. japonicus and its potential role in growth regulation remain uncharacterized. Currently, the precursors of the PDF-type neuropeptide in echinoderms remain unidentified, which precludes clear pharmacological characterization of the two receptors. While further exploration of echinoderm PDF-type neuropeptides is still needed, our phylogenetic analysis-conducted using the maximum likelihood method with optimized parameters and rigorous sequence curation-demonstrates that the deuterostomian PDFRs (including AjPDFR1 and AjPDFR2) are positioned in a clade with the well-characterized protostomian PDFR clades with extremely high bootstrap support (value=100). Therefore, these two receptors in A. japonicus clearly belong to the PDF receptor family and our findings clearly indicate that the ability of CT-like peptides to activate PDFRs is either an evolutionarily ancient and conserved property or has arisen independently in different lineages. Details of methods employed to produce the new receptor tree are included in line 727-739. The new phylogenetic tree is shown below and has been incorporated into the revised manuscript (Figure 2, line 206). The description of new phylogenetic tree has also been modified accordingly in the revised manuscript (line 169-183).

References:

Bauknecht P, Jékely G. Large-Scale Combinatorial Deorphanization of Platynereis Neuropeptide GPCRs. Cell reports, 2015, 12(4), 684–693. doi:  10.1016/j.celrep.2015.06.052.

Beets I, Zels S, Vandewyer E, Demeulemeester J, et al. System-wide mapping of peptide-GPCR interactions in C. elegans. Cell reports, 2023, 42(9), 113058. doi: 10.1016/j.celrep.2023.113058.

Cardoso J C, Mc Shane J C, Li Z, et al. Revisiting the evolution of Family B1 GPCRs and ligands: Insights from mollusca. Molecular and cellular endocrinology, 2024, 586, 112192. doi: 10.1016/j.mce.2024.112192.

Gorn A H, Lin H Y, Yamin M, et al. Cloning, characterization, and expression of a human calcitonin receptor from an ovarian carcinoma cell line. The Journal of clinical investigation, 1992, 90(5), 1726–1735. doi: 10.1172/JCI116046.

Huang T, Su J, Wang X, et al. Functional Analysis and Tissue-Specific Expression of Calcitonin and CGRP with RAMP-Modulated Receptors CTR and CLR in Chickens. Animals: an open access journal from MDPI, 2024, 14(7), 1058. doi: 10.3390/ani14071058.

Johnson E C, Shafer O T, Trigg J S, et al. A novel diuretic hormone receptor in Drosophila: evidence for conservation of CGRP signaling. Journal of Experimental Biology, 2005, 208(7): 1239-1246. doi: 10.1242/jeb.01529.

McLatchie L M, Fraser N J, Main M J, et al. RAMPs regulate the transport and ligand specificity of the calcitonin-receptor-like receptor. Nature, 1998, 393(6683): 333-339. doi: 10.1038/30666.

Schwartz J, Réalis-Doyelle E, Dubos M P, et al. Characterization of an evolutionarily conserved calcitonin signaling system in a lophotrochozoan, the Pacific oyster (Crassostrea gigas). Journal of Experimental Biology, 2019, 222(13): jeb201319. doi: 10.1242/jeb.201319.

Sekiguchi T, Kuwasako K, Ogasawara M, et al. Evidence for conservation of the calcitonin superfamily and activity-regulating mechanisms in the basal chordate Branchiostoma floridae: insights into the molecular and functional evolution in chordates. Journal of Biological Chemistry, 2016, 291(5): 2345-2356. doi: 10.1074/jbc.M115.664003.

Shafer, O. T., & Taghert, P. H. (2009). RNA-interference knockdown of Drosophila pigment dispersing factor in neuronal subsets: the anatomical basis of a neuropeptide's circadian functions. PloS one, 4(12), e8298. doi: 10.1371/journal.pone.0008298.

Van Sinay, E., Mirabeau, O., Depuydt, G., Van Hiel, M. B., Peymen, K., Watteyne, J., Zels, S., Schoofs, L., & Beets, I. (2017). Evolutionarily conserved TRH neuropeptide pathway regulates growth in Caenorhabditis elegans. Proceedings of the National Academy of Sciences of the United States of America, 114(20), E4065–E4074. doi: 10.1073/pnas.1617392114.

Reviewer #2 (Public review):

Summary:

The authors show that A. japonicus calcitonins (AjCT1 and AjCT2) activate not only the calcitonin/calcitonin-like receptor, but they also activate the two "PDF receptors", ex vivo. They also explore secondary messenger pathways that are recruited following receptor activation. They determine the source of CT1 and CT2 using qPCR and in situ hybridization and finally test the effects of these peptides on tissue contractions, feeding and growth. This study provides solid evidence that CT1 and CT2 act as ligands for calcitonin receptors; however, evidence supporting cross-talk between CT peptides and "PDF receptors" is weak.

Strengths:

This is the first study to report pharmacological characterization of CT receptors in an echinoderm. Multiple lines of evidence in cell culture (receptor internalization and secondary messenger pathways) support this conclusion.

Weaknesses:

The authors claim that A. japonicus CTs activate "PDF" receptors and suggest that this cross-talk is evolutionary ancient since similar phenomenon also exists in the fly Drosophila melanogaster. These conclusions are not fully supported. The authors perform phylogenetic analysis to show that the two "PDF" receptors form an independent clade. The bootstrap support is quite low in a lot of instances, especially for the deuterostomian and protostomian PDFR clades which is below 30. With such low support, it is unclear if the clade comprising deuterostomian "PDFR" is in fact PDFRs and not another receptor type whose endogenous ligand (besides CT) remains to be discovered.

Thank you for the reviewer’s comments. In response, we have produced a new phylogenetic analysis using the maximum likelihood method. This was done by Nayeli Escudero Castelán and Kite Jones in the Elphick group at QMUL and therefore they have been added as co-authors of this paper. The new phylogenetic tree (Figure 2, line 206) includes broad taxonomic sampling of CT-type receptors and PDF-type receptors. CRH-type receptors, which are also members of the secretin-type GPCR sub-family, have been included as an outgroup to root the tree. In the previous version the much more distantly related vasopressin/oxytocin-type receptors, which are rhodopsin-type GPCRs, were included as an outgroup. Furthermore, VIP-type receptors were also included in the previous tree but these have been omitted from the new tree because VIP receptor orthologs only occur in vertebrates and therefore they are not representative of a bilaterian GPCR family. The new tree shows high bootstrap support for key clades, notably achieving a bootstrap value of 100 for a clade comprising both deuterostomian and protostomian PDF receptors. This provides important evidence that the A. japonicus PDF-type receptors characterized in this study (AjPDFR1, AjPDFR2) are co-orthologs of the PDF-type receptor that has been characterized previously in Drosophila. Similarly, there is strong bootstrap support (100) for a clade comprising CT/DH31-type receptors and, importantly, the CT-type receptor characterized in this study (AjCTR) is positioned in a branch of this clade that comprises deuterostomian CT-type receptors (with bootstrap support of 100). Details of methods employed to produce the new receptor tree are included in lines 727-739. The new phylogenetic tree is shown below and has been incorporated into the revised manuscript (Figure 2, line 206). The description of new phylogenetic tree has also been modified accordingly in the revised manuscript (line 169-183).

References:

Bauknecht P, Jékely G. Large-Scale Combinatorial Deorphanization of Platynereis Neuropeptide GPCRs. Cell reports, 2015, 12(4), 684–693. doi:  10.1016/j.celrep.2015.06.052.

Beets I, Zels S, Vandewyer E, Demeulemeester J, et al. System-wide mapping of peptide-GPCR interactions in C. elegans. Cell reports, 2023, 42(9), 113058. doi: 10.1016/j.celrep.2023.113058.

Cardoso J C, Mc Shane J C, Li Z, et al. Revisiting the evolution of Family B1 GPCRs and ligands: Insights from mollusca. Molecular and cellular endocrinology, 2024, 586, 112192. doi: 10.1016/j.mce.2024.112192.

Gorn A H, Lin H Y, Yamin M, et al. Cloning, characterization, and expression of a human calcitonin receptor from an ovarian carcinoma cell line. The Journal of clinical investigation, 1992, 90(5), 1726–1735. doi: 10.1172/JCI116046.

Huang T, Su J, Wang X, et al. Functional Analysis and Tissue-Specific Expression of Calcitonin and CGRP with RAMP-Modulated Receptors CTR and CLR in Chickens. Animals: an open access journal from MDPI, 2024, 14(7), 1058. doi: 10.3390/ani14071058.

Johnson E C, Shafer O T, Trigg J S, et al. A novel diuretic hormone receptor in Drosophila: evidence for conservation of CGRP signaling. Journal of Experimental Biology, 2005, 208(7): 1239-1246. doi: 10.1242/jeb.01529.

McLatchie L M, Fraser N J, Main M J, et al. RAMPs regulate the transport and ligand specificity of the calcitonin-receptor-like receptor. Nature, 1998, 393(6683): 333-339. doi: 10.1038/30666.

Schwartz J, Réalis-Doyelle E, Dubos M P, et al. Characterization of an evolutionarily conserved calcitonin signaling system in a lophotrochozoan, the Pacific oyster (Crassostrea gigas). Journal of Experimental Biology, 2019, 222(13): jeb201319. doi: 10.1242/jeb.201319.

Sekiguchi T, Kuwasako K, Ogasawara M, et al. Evidence for conservation of the calcitonin superfamily and activity-regulating mechanisms in the basal chordate Branchiostoma floridae: insights into the molecular and functional evolution in chordates. Journal of Biological Chemistry, 2016, 291(5): 2345-2356. doi: 10.1074/jbc.M115.664003.

Reviewer #2 (Recommendations for the authors):

Figure 1C: The bootstrap support is quite low in a lot of instances, especially for the deuterostomian and protostomian PDFR clades which is below 30. With such support, I would be hesitant to label the blue clade as deuterostomian PDFR for two reasons: 1) no members of this clade have been shown to be activated by a PDF-like substance and 2) the current study shows that these receptors are activated by CT-type peptides. Therefore, the phylogenetic analyses do not support the conclusions of this paper. What is the basis for calling these receptors PDFR and not CTR in light of weak phylogenetic support?

Thank you for the reviewer’s comments. In response, we have produced a new phylogenetic analysis using the maximum likelihood method. This was done by Nayeli Escudero Castelán and Kite Jones in the Elphick group at QMUL and therefore they have been added as co-authors of this paper. The new phylogenetic tree (Figure 2, line 206) includes broad taxonomic sampling of CT-type receptors and PDF-type receptors. CRH-type receptors, which are also members of the secretin-type GPCR sub-family, have been included as an outgroup to root the tree. In the previous version the much more distantly related vasopressin/oxytocin-type receptors, which are rhodopsin-type GPCRs, were included as an outgroup. Furthermore, VIP-type receptors were also included in the previous tree but these have been omitted from the new tree because VIP receptor orthologs only occur in vertebrates and therefore they are not representative of a bilaterian GPCR family. The new tree shows high bootstrap support for key clades, notably achieving a bootstrap value of 100 for a clade comprising both deuterostomian and protostomian PDF receptors. This provides important evidence that the A. japonicus PDF-type receptors characterized in this study (AjPDFR1, AjPDFR2) are co-orthologs of the PDF-type receptor that has been characterized previously in Drosophila. Similarly, there is strong bootstrap support (100) for a clade comprising CT/DH31-type receptors and, importantly, the CT-type receptor characterized in this study (AjCTR) is positioned in a branch of this clade that comprises deuterostomian CT-type receptors (with bootstrap support of 100). Details of methods employed to produce the new receptor tree are included in lines 727-739 The new phylogenetic tree is shown below and has been incorporated into the revised manuscript (Figure 2, line 206). The description of new phylogenetic tree has also been modified accordingly in the revised manuscript (line 169-183).

We agree with the reviewer that no members of the PDF-type receptor clade in deuterostomes have yet been shown to be activated by a PDF-like substance. That is because the precursors of the PDF-type neuropeptides in echinoderms remain unidentified so far, which precludes clear pharmacological characterization of these receptors within the deuterostomian PDFR clade. However, the new phylogenetic tree now provides strong support (bootstrap value = 100) for the clade comprising deuterostomian and protostomian PDFRs, confirming the classification of AjPDFR1 and AjPDFR2 as PDF-type receptors. 

References:

Bauknecht P, Jékely G. Large-Scale Combinatorial Deorphanization of Platynereis Neuropeptide GPCRs. Cell reports, 2015, 12(4), 684–693. doi:  10.1016/j.celrep.2015.06.052.

Beets I, Zels S, Vandewyer E, Demeulemeester J, et al. System-wide mapping of peptide-GPCR interactions in C. elegans. Cell reports, 2023, 42(9), 113058. doi: 10.1016/j.celrep.2023.113058.

Cardoso J C, Mc Shane J C, Li Z, et al. Revisiting the evolution of Family B1 GPCRs and ligands: Insights from mollusca. Molecular and cellular endocrinology, 2024, 586, 112192. doi: 10.1016/j.mce.2024.112192.

Gorn A H, Lin H Y, Yamin M, et al. Cloning, characterization, and expression of a human calcitonin receptor from an ovarian carcinoma cell line. The Journal of clinical investigation, 1992, 90(5), 1726–1735. doi: 10.1172/JCI116046.

Huang T, Su J, Wang X, et al. Functional Analysis and Tissue-Specific Expression of Calcitonin and CGRP with RAMP-Modulated Receptors CTR and CLR in Chickens. Animals: an open access journal from MDPI, 2024, 14(7), 1058. doi: 10.3390/ani14071058.

Johnson E C, Shafer O T, Trigg J S, et al. A novel diuretic hormone receptor in Drosophila: evidence for conservation of CGRP signaling. Journal of Experimental Biology, 2005, 208(7): 1239-1246. doi: 10.1242/jeb.01529.

McLatchie L M, Fraser N J, Main M J, et al. RAMPs regulate the transport and ligand specificity of the calcitonin-receptor-like receptor. Nature, 1998, 393(6683): 333-339. doi: 10.1038/30666.

Schwartz J, Réalis-Doyelle E, Dubos M P, et al. Characterization of an evolutionarily conserved calcitonin signaling system in a lophotrochozoan, the Pacific oyster (Crassostrea gigas). Journal of Experimental Biology, 2019, 222(13): jeb201319. doi: 10.1242/jeb.201319.

Sekiguchi T, Kuwasako K, Ogasawara M, et al. Evidence for conservation of the calcitonin superfamily and activity-regulating mechanisms in the basal chordate Branchiostoma floridae: insights into the molecular and functional evolution in chordates. Journal of Biological Chemistry, 2016, 291(5): 2345-2356. doi: 10.1074/jbc.M115.664003.

The new results following AjCT and AjPDFR2 knockdown are a welcome addition. While this additional evidence supports the claim that AjCT could mediate its effects via AjPDFR2, this evidence does not show that AjCT acts as an endogenous ligand for PDFR in vivo. In combination with the weak phylogenetic analyses, I would recommend the authors to key down their claims that they have functionally characterized a PDFR (in the title and text).

Thank you for your insightful comments and we do understand the reviewer’s concern. 

Regarding “the weak phylogenetic analyses”, as highlighted above, we have produced a new phylogenetic tree (Fig 2, line 206) that provides strong bootstrap support for the clade comprising deuterostome and protostome PDF-type receptors. For this reason, it is our opinion that inclusion of “pigment-dispersing factor-type receptors” in the title of the paper is appropriate. The details of phylogenetic analysis method were added in line 727-739, and the updated phylogenetic tree has been incorporated into the revised manuscript (Figure 2, line 206). The description of new phylogenetic tree has also been modified accordingly in the revised manuscript (line 169-183). Besides, long-term knockdown of the AjCT precursor and AjPDFR2 both resulted in identical and significant growth defect phenotypes. And the observation of phenotypic overlap is widely accepted in genetic research as strong evidence for pathway association (Shafer and Taghert, 2009; Van Sinay et al., 2017). This high degree of phenotypic consistency, coupled with our in vitro finding that AjCT2 specifically activates AjPDFR2, strongly supports the conclusion that AjCT2 and AjPDFR2 function within the same signaling pathway in vivo, with AjPDFR2 serving as the key receptor functionally activated by AjCT2.

References:

Shafer, O. T., & Taghert, P. H. (2009). RNA-interference knockdown of Drosophila pigment dispersing factor in neuronal subsets: the anatomical basis of a neuropeptide's circadian functions. PloS one, 4(12), e8298. doi: 10.1371/journal.pone.0008298.

Van Sinay, E., Mirabeau, O., Depuydt, G., Van Hiel, M. B., Peymen, K., Watteyne, J., Zels, S., Schoofs, L., & Beets, I. (2017). Evolutionarily conserved TRH neuropeptide pathway regulates growth in Caenorhabditis elegans. Proceedings of the National Academy of Sciences of the United States of America, 114(20), E4065–E4074. doi: 10.1073/pnas.1617392114.

Since there is no formal logic defining the use of "type" vs "like" vs "related", I would encourage the authors to use one term (of their choice) to avoid unnecessary confusion. Or another possibility is that these relationships are defined at some point in the manuscript so that it becomes clear to the reader.

Thank you for the reviewer’s comments. The “CT-related peptides” has defined in the Introduction (line 54-58). As per your suggestion, we have now defined both “CT-type peptides” and “CT-like peptides” in the Introduction (line 76-79). “CT-type peptides” are characterized by an N-terminal disulphide bridge, whereas “CT-like peptides” (diuretic hormone 31 (DH31)-type peptides) lack this feature. Additionally, in accordance with the definitions, we have corrected these three descriptions in the revised manuscript (line 80, 83, 88 for “CT-type peptides”) to ensure consistent and accurate usage of these terms.

"To provide in vivo evidence supporting CT-mediated activation of "PDF" receptors, we conducted the following experiments: Firstly, we confirmed that AjPDFR1 and AjPDFR2were the functional receptors of AjCT1and AjCT2 (Figure 2, 3 and 4). Secondly, injection of AjCT2 and siAjCTP1/2-1 in vivo induced corresponding changes in AjPDFR1and AjPDFR2expression levels in the intestine (Figure 8C, 9A, 9B and 9C)."

None of these experiments provide direct evidence that CT activates PDFR in vivo. The functional studies are indeed a welcome addition but they cannot discriminate between correlation and causation.

Thank you for the reviewer’s insightful comments. We agree that the functional studies do not constitute direct proof that CT’s activation of PDFR in vivo. However, we observed identical and significant growth defect phenotypes following long-term knockdown of the AjCT precursor and the AjPDFR2. This high degree of phenotypic congruence, combined with the established in vitro activation of AjPDFR2 by AjCT2, provides strong support for the conclusion that AjCT2 acts as the key endogenous ligand activating the AjPDFR2 signaling pathway in vivo. Importantly, such phenotypic overlap has been widely accepted in genetic research as strong evidence for functional pathway association (Shafer and Taghert, 2009; Van Sinay et al., 2017).

References:

Shafer, O. T., & Taghert, P. H. (2009). RNA-interference knockdown of Drosophila pigment dispersing factor in neuronal subsets: the anatomical basis of a neuropeptide's circadian functions. PloS one, 4(12), e8298. doi: 10.1371/journal.pone.0008298.

Van Sinay, E., Mirabeau, O., Depuydt, G., Van Hiel, M. B., Peymen, K., Watteyne, J., Zels, S., Schoofs, L., & Beets, I. (2017). Evolutionarily conserved TRH neuropeptide pathway regulates growth in Caenorhabditis elegans. Proceedings of the National Academy of Sciences of the United States of America, 114(20), E4065–E4074. doi: 10.1073/pnas.1617392114.

DOI: 10.1371/journal.pgen.1011247

Resource: (WB Cat# WBStrain00000001,RRID:WB-STRAIN:WBStrain00000001)

Curator: @Apiekniewska

SciCrunch record: RRID:WB-STRAIN:WBStrain00000001

What is this?

Las semillas inmaduras fueron tratadas con una mezcla de hormonas y sales para romper la dormancia, estimular la germinación y fortalecer el embrión, permitiendo sembrar la siguiente generación en menos de un día.

Es un método usado en mejoramiento genético de cultivos para que las plantas crezcan, florezcan y produzcan semillas mucho más rápido. En lugar de esperar una sola cosecha al año, con la cría rápida se pueden lograr 4 o 5 generaciones de plantas en un mismo año.

Considero que es esencial el recalcar esto, púes efectivamente cada empresa al tener diferentes giros, debe de efectuar diferentes estrategias, aunque todas deben de guiar hacia el mismo objetivo que es la buena comunicación bidireccional.

Función Clave de la Comunicación: Su rol principal es permitir que el plan estratégico se ejecute eficientemente en todos los niveles jerárquicos, optimizando tiempo, recursos (humanos y económicos) y esfuerzo.

Necesidad de Planificación: La comunicación no debe ser un proceso improvisado. El artículo subraya que debe ser estructurada, ordenada y planificada desde la alta dirección, e integrada en el plan estratégico general de la compañía.

Coincido plenamente con la observación de que la globalización y la competencia obligan a las empresas a diferenciarse mediante estrategias comunicacionales efectivas. Desde mi punto de vista, esta sección destaca un punto clave: la comunicación no solo influye en el marketing o la imagen corporativa, sino también en la eficiencia operativa interna, ya que una información mal transmitida puede generar retrasos o duplicación de esfuerzos. En este sentido, la gestión comunicacional actúa como un sistema nervioso de la empresa, permitiendo la coordinación entre sus distintas áreas.

Me parece muy acertada la relación que los autores establecen entre la deficiente comunicación y el deterioro del clima laboral. Un entorno donde los mensajes no fluyen o son ambiguos tiende a generar desmotivación, frustración y alta rotación de empleados. En mi experiencia, la comunicación organizacional no solo busca informar, sino también dar sentido al trabajo. Cuando el personal entiende el propósito de sus tareas y percibe coherencia entre lo que se dice y lo que se hace, aumenta su compromiso y satisfacción. Esto convierte la comunicación en un pilar de la cultura organizacional.

Termo inicial do auxílio por incapacidade temporária: - 16º dia de afastamento, se empregado; - O dia que iniciar a incapacidade, para os demais segurados afastados por mais de 15 dias; - A data de entrada do requerimento, se afastado por 30 dias após o

I looked at Sasha Costanza-Chock’s Design Justice book [j22], and I really liked how it focuses on who actually gets to be part of the design process. The author talks about how design should be led by the people who are most affected by it, instead of just big companies or tech experts. That connects really well to what the chapter said about “who gets to be designers.” It made me think that if more people from different backgrounds helped design technology, things like the soap dispenser problem probably wouldn’t happen.

Súmula 576/STJ - Ausente requerimento administrativo no INSS, o termo inicial para a implantação da aposentadoria por invalidez concedida judicialmente será a data da citação válida.

Como conciliar a Súmula 576 do STJ com a decisão do STF que impõe o prévio requerimento administrativo (RE 631240/MG)?

• Se formos analisar os precedentes que deram origem à Súmula 576-STJ, iremos perceber que eles envolvem processos judiciais iniciados antes da decisão do STF no RE 631240/MG, ou seja, na época em que a jurisprudência majoritária não exigia o prévio requerimento administrativo para que o segurado pudesse ingressar com a ação.
• Portanto, os debates que envolveram a Súmula 576-STJ ocorreram em processos surgidos em dado momento histórico em que o segurado ainda podia escolher se primeiro iria tentar requerer o benefício na via administrativa ou se já queria propor diretamente a ação judicial pleiteando a aposentadoria por invalidez. Assim, a Súmula 576-STJ surgiu principalmente para dirimir estes processos.

(CAVALCANTE, Márcio André Lopes. Súmula 576-STJ. Buscador Dizer o Direito, Manaus. Disponível em: https://buscadordizerodireito.com.br/jurisprudencia/3660/sumula-576-stj.)

Não necessariamente o processo será anulado desde o começo, mas tão somente a partir do momento em que o MP deveria ter intervindo.

Observe que a nulidade relativa à ausência de intimação do MP não é automática. O próprio MP deve se pronunciar a respeito da existência ou não de prejuízo antes da decretação da nulidade.

• Informativo nº 731
• 4 de abril de 2022.
• QUARTA TURMA
• Processo: REsp 1.978.138-SP, Rel. Min. Antonio Carlos Ferreira, Quarta Turma, por unanimidade, julgado em 22/03/2022.

Ramo do Direito DIREITO PROCESSUAL CIVIL

TemaPaz, Justiça e Instituições Eficazes <br /> Ação civil pública. Legitimidade ativa ad causam. Administração pública indireta. Pertinência temática. Necessidade.

Destaque - A legitimidade ativa na ação civil pública das pessoas jurídicas da administração pública indireta depende da pertinência temática entre suas finalidades institucionais e o interesse tutelado.

Informações do Inteiro Teor - Inicialmente, a pertinência temática consiste na "harmonização entre as finalidades institucionais das associações civis ou dos órgãos públicos legitimados e o objeto a ser tutelado na ação civil pública. Em outras palavras, mencionadas pessoas somente poderão propor a ação civil pública em defesa de um interesse cuja tutela seja de sua finalidade institucional"

• É fato que o art. 5º da Lei n. 7.347/1985 apenas exige expressamente da associação, pessoa jurídica de direito privado, a comprovação de pertinência temática para propositura de ação civil pública.

• Por conseguinte, em uma interpretação literal, não seria necessária a comprovação da pertinência temática para que as autarquias, empresas públicas, fundações públicas e sociedades de economia mista ajuizassem ações coletivas.

• Nessa perspectiva, os integrantes da administração pública indireta passariam a ter amplos poderes, concorrendo, inclusive, com as finalidades institucionais do Ministério Público e da Defensoria Pública, convertendo-se em verdadeiros "procuradores universais", com legitimidade para ajuizamento das mais variadas demandas coletivas, independentemente de sua área de atuação.

• Tal concepção <u>ignora</u> as competências legais e estatutárias das instituições, as quais delimitam o campo de atuação das pessoas jurídicas integrantes da administração pública indireta. Sob o mesmo raciocínio, a doutrina entende que "*não basta a existência fática de uma pessoa da Administração Pública indireta: necessário se faz o exame de seu regime estatutário* (lei, regulamento, contrato ou ato de constituição etc.). Será o seu estatuto que conferirá legitimidade adequada (ou não) à pessoa jurídica, com densidades diferentes: uma coisa é uma autarquia; outra, uma sociedade de economia mista com capital aberto na bolsa de valores".

• Portanto, não há como considerar titular do interesse, na propositura da ação coletiva, pessoa jurídica da administração pública indireta sem nenhum vínculo com a tese jurídica deduzida, cujo objeto litigioso não se encontra entre aqueles a serem protegidos por sua finalidade institucional.

Kẻ tấn công có thể dễ dàng thiết lập một cuộc tấn công ET ở những nơi công cộng khi mạng sử dụng Wi-Fi mở.

apostrophizing “Romance”—ideal muse

• Informativo 1143
• ADPF 1011 / PE
• Órgão julgador: Tribunal Pleno
• Relator(a): Min. GILMAR MENDES
• Julgamento: 28/06/2024 (Virtual)
• Ramo do Direito: Processual Civil, Constitucional
• Matéria: Execução; Multa Simples; Tribunal De Contas; Legitimidade Ad Causam/Fiscalização Contábil, Financeira e Orçamentária; Controle Externo; Tribunal de Contas

Multas aplicadas pelo Tribunal de Contas estadual: legitimidade dos entes públicos para executá-las

Tese fixada - 1. O Município prejudicado é o legitimado para a execução de crédito decorrente de multa aplicada por Tribunal de Contas estadual a agente público municipal, em razão de danos causados ao erário municipal.

• 2. Compete ao Estado-membro a execução de crédito decorrente de multas simples, aplicadas por Tribunais de Contas estaduais a agentes públicos municipais, em razão da inobservância das normas de Direito Financeiro ou, ainda, do descumprimento dos deveres de colaboração impostos, pela legislação, aos agentes públicos fiscalizados.

Resumo - Os estados possuem legitimidade ativa para executar multas meramente sancionatórias aplicadas por seus Tribunais de Contas em face de agentes públicos municipais que, por seus atos, infrinjam as normas de Direito Financeiro ou violem os deveres de colaboração com o órgão de controle, impostos pela legislação.

• A Constituição Federal de 1988 confere aos Tribunais de Contas em todo o País a competência para aplicar as sanções previstas em lei aos responsáveis por ilegalidades de despesas ou irregularidades nas contas (1).

• Consoante o julgamento que originou a fixação da tese do Tema 642 da repercussão geral, o que determina o ente competente para executar a multa aplicada pelas Cortes de Contas estaduais é a natureza jurídica dessa sanção. A multa simples imposta ao agente público municipal — que diz respeito à modalidade sancionatória de responsabilidade financeira — em razão da grave inobservância de normas financeiras, contábeis e orçamentárias, ou como consequência direta da violação de deveres de colaboração que os agentes fiscalizados devem guardar com o órgão de controle (obrigações acessórias), configura ferramenta de desincentivo à prática de futuras transgressões dessas normas e, em certos casos, de reafirmação da autoridade das decisões ou diligências determinadas pelos Tribunais de Contas.

• Por outro lado, as penalidades de imputação de débito e de multa proporcional ao dano abrangem a modalidade reintegratória de responsabilidade financeira, eis que visam recompor o erário em virtude de desvio, pagamento indevido ou falta de cobrança ou liquidação, nos termos da lei.

• Nesse contexto, quando as sanções aplicadas pelo Tribunal de Contas estadual a agente público municipal referirem-se ao ressarcimento ao erário, a legitimidade para executá-las é do município cujo patrimônio público foi atingido (2), ao passo que é o próprio estado o legitimado ativo para executar as multas que decorrem do poder sancionador da Corte de Contas (sanção pecuniária e que não possui qualquer relação com a existência de dano ao erário) (3).

• Com base nesses e em outros entendimentos, o Plenário, por unanimidade, julgou procedente a ação, bem como (i) assentou que a presente decisão não afeta automaticamente a coisa julgada formada em momento anterior à publicação da ata deste julgamento; e (ii) determinou o acréscimo de uma nova proposição (item 2) à tese do Tema 642 da repercussão geral, a fim de abranger o novo entendimento do Tribunal.

• Informativo 1029
• RE 1003433 / RJ - Tema 642
• Órgão julgador: Tribunal Pleno
• Relator(a): Min. MARCO AURÉLIO
• Redator(a) do acórdão: Min. ALEXANDRE DE MORAES
• Julgamento: 14/09/2021 (Virtual)
• Ramo do Direito: Processual Civil, Administrativo
• Matéria: Execução; Controle externo

Legitimidade para executar multa por danos causados a erário municipal

Tese fixada - O Município prejudicado é o legitimado para a execução de crédito decorrente de multa aplicada por Tribunal de Contas estadual a agente público municipal, em razão de danos causados ao erário municipal.

Resumo - Os estados não têm legitimidade ativa para a execução de multas aplicadas, por Tribunais de Contas estaduais, em face de agentes públicos municipais, que, por seus atos, tenham causado prejuízos a municípios.

• Se a multa aplicada pelo Tribunal de Contas decorre da prática de atos que causaram prejuízo ao erário municipal, o legitimado ativo para a execução do crédito fiscal é o município lesado, e não o estado (1). Entendimento diverso caracterizaria hipótese de enriquecimento sem causa.

• Com base nesse entendimento, o Plenário, por maioria, ao julgar o Tema 642 da RG, negou provimento a recurso extraordinário. Vencidos os ministros Marco Aurélio (relator) e Edson Fachin.

Precedentes: RE 525.663 AgR e RE 223.037

• Informativo 1007
• ADI 1668 / DF
• Órgão julgador: Tribunal Pleno
• Relator(a): Min. EDSON FACHIN
• Julgamento: 27/02/2021 (Virtual)
• Ramo do Direito: Administrativo
• Matéria: AGÊNCIAS REGULADORAS

Serviços de telecomunicações: criação da ANATEL e competências do órgão regulador

Resumo - A competência atribuída ao chefe do Poder Executivo para expedir decreto em ordem a instituir ou eliminar a prestação do serviço em regime público, em concomitância ou não com a prestação no regime privado, aprovar o plano geral de outorgas do serviço em regime público e o plano de metas de universalização do serviço prestado em regime público está em perfeita consonância com o poder regulamentar previsto no art. 84, IV, parte final, e VI, da Constituição Federal (CF). O art. 18, I, II e III da Lei 9.472/1997 é compatível com os arts. 21, XI, e 48, XII, da Constituição Federal (CF).

• A competência da Agência Nacional de Telecomunicações (ANATEL) para expedir normas subordina-se aos preceitos legais e regulamentares que regem a outorga, prestação e fruição dos serviços de telecomunicações no regime público e no regime privado. O art. 19, IV e X, da Lei 9.472/1997, desse modo, é constitucional.

• A busca e posterior apreensão efetuada sem ordem judicial, com base apenas no poder de polícia de que é investida a ANATEL, mostra-se <u>inconstitucional</u> diante da violação ao disposto no princípio da inviolabilidade de domicílio, à luz do art. 5º, XI, da Constituição Federal. Logo, o art. 19, XV, da Lei 9.472/1997 é inconstitucional. A competência atribuída ao Conselho Diretor da ANATEL para editar normas próprias de licitação e contratação (Lei 9.472/1997, art. 22, II) deve observar o arcabouço normativo atinente às licitações e aos contratos, em respeito ao princípio da legalidade.

• Diante da especificidade dos serviços de telecomunicações, é válida a criação de novas modalidades licitatórias por <u>lei de mesma hierarquia</u> da Lei Geral de Licitações (Lei 8.666/1993). Portanto, sua disciplina deve ser feita por meio de lei, e não de atos infralegais, em obediência aos artigos 21, XI, e 22, XXVII, do texto constitucional. Em razão disso, é inconstitucional a expressão “serão disciplinados pela Agência” contida no art. 55 da Lei 9.472/1997.

• A contratação, a que se refere o art. 59 da Lei 9.472/1997, de técnicos ou empresas especializadas, inclusive consultores independentes e auditores externos, para executar atividades de competência da ANATEL, deve observar o regular procedimento licitatório previsto pelas leis de regência.

• A possibilidade de concomitância de regimes público e privado de prestação do serviço, assim como a definição das modalidades do serviço são questões estritamente técnicas, da alçada da agência, a quem cabe o estabelecimento das bases normativas de cada matéria relacionada à execução, à definição e ao estabelecimento das regras peculiares a cada serviço.

• A ANATEL não pode disciplinar procedimento licitatório simplificado por meio de norma de hierarquia inferior à Lei Geral de Licitações, sob pena de ofensa ao princípio da reserva legal. Por isso, são inconstitucionais as expressões “simplificado” e “nos termos por ela regulados” do art. 119, da Lei 9.472/1997.

• A competência atribuída ao chefe do Poder Executivo para expedir decreto em ordem a instituir ou eliminar a prestação do serviço em regime público, em concomitância ou não com a prestação no regime privado, aprovar o plano geral de outorgas do serviço em regime público e o plano de metas de universalização do serviço prestado em regime público está em perfeita consonância com o poder regulamentar previsto no art. 84, IV, parte final, e VI, da Constituição Federal (CF). O art. 18, I, II e III da Lei 9.472/1997 (1) é compatível com os arts. 21, XI, e 48, XII, da Constituição Federal (CF) (2).

• De fato, as medidas previstas no art. 18 são atinentes à execução da política de telecomunicações definidas no corpo da Lei 9.472/1997 e estão condicionadas por várias normas desse diploma.

• O caput do art. 18 da Lei 9.472/1997 observa, portanto, esses dispositivos constitucionais, que atribuem ao Presidente da República a competência para expedir decretos e regulamentos destinados à fiel execução de lei, e a ele outorgam o poder de dispor, mediante decreto, sobre a organização e funcionamento da administração federal.

• É ínsito ao poder regulamentar atuar secundum legem e intra legem. Assim, atendidos os limites da legislação que rege a matéria, a Lei 9.472/1997, ao tempo em que confere tal poder ao Presidente da República, também fixa parâmetros para o seu exercício.

• A competência da Agência Nacional de Telecomunicações (ANATEL) para expedir normas subordina-se aos preceitos legais e regulamentares que regem a outorga, prestação e fruição dos serviços de telecomunicações no regime público e no regime privado. O art. 19, IV e X, da Lei 9.472/1997 (3), desse modo, é constitucional.

• Na esteira da jurisprudência do Supremo Tribunal Federal (STF) (4), cabe às agências reguladoras, como a ANATEL, desempenhar a tarefa ordenadora e fiscalizatórias dos setores a elas submetidos. E, para a adequada execução dessa função, exsurge o poder de expedir normas como imanente à atividade regulatória das agências, a quem compete, no âmbito de sua atuação e nos limites do arcabouço normativo sobre o tema, disciplinar a prestação dos serviços.

• Não se trata, portanto, de delegação de poderes legislativos, pois a expedição de normas regulatórias é sempre exercida com fundamento na lei, que também lhe serve de limite, mas que não esgota as possibilidades de mediação dos interesses diversos colocados para composição pelos órgãos reguladores.

• A busca e posterior apreensão efetuada sem ordem judicial, com base apenas no poder de polícia de que é investida a ANATEL, mostra-se inconstitucional diante da violação ao disposto no princípio da inviolabilidade de domicílio, à luz do art. 5º, XI, da Constituição Federal (5). Logo, o art. 19, XV, da Lei 9.472/1997 (6) é inconstitucional.

• A possibilidade de promoção de interdição de estabelecimentos, instalações ou equipamentos, e apreensão de bens ou produtos, nos termos do art. 3º, parágrafo único, da Lei 10.871/2004 (que dispõe sobre a criação de carreiras e organização de cargos efetivos das autarquias especiais, denominadas agências reguladoras), constitui exercício do poder de polícia da Administração Pública, dotado de autoexecutoriedade, inerente ao exercício dessa função (7).

• Ocorre que o art. 19, XV, da Lei 9.472/1997, que estabelece a busca e apreensão de bens, tem uma dimensão distinta. Frise-se que, segundo orientação do STF, o conceito de domicílio não está limitado à residência domiciliar, mas abarca também qualquer compartimento privado onde alguém exerce profissão ou atividade (8).

• A competência atribuída ao Conselho Diretor da ANATEL para editar normas próprias de licitação e contratação (Lei 9.472/1997, art. 22, II) (9) deve observar o arcabouço normativo atinente às licitações e aos contratos, em respeito ao princípio da legalidade.

• Com efeito, as agências reguladoras não possuem a prerrogativa de legislar em matéria de licitação. Primeiro, porque isso viola a competência legislativa privativa da União (CF, art. 22, XXVII). Segundo, porque inovar no ordenamento jurídico não se encontra dentre os atributos que a função regulatória desses órgãos detêm, uma vez que eles colmatam lacunas propositais de natureza técnica na legislação, mas não podem estabelecer, de forma originária e primária, deveres e obrigações aos particulares, menos ainda exercer atividade criativa no que concerne a modalidades licitatórias e contratuais.

• Diante da especificidade dos serviços de telecomunicações, é válida a criação de novas modalidades licitatórias por lei de mesma hierarquia da Lei Geral de Licitações (Lei 8.666/1993). Portanto, sua disciplina deve ser feita por meio de lei, e não de atos infralegais, em obediência aos artigos 21, XI, e 22, XXVII, do texto constitucional. Em razão disso, é inconstitucional a expressão “serão disciplinados pela Agência” contida no art. 55 da Lei 9.472/1997 (10).

• A inserção, no ordenamento jurídico, de novas modalidades licitatórias, por lei que tem o mesmo status que a Lei Geral de Licitações não viola a Carta Magna. Todavia, para que seja respeitado o princípio da reserva legal e, ainda, tendo em vista que a consulta é instituto que não está restrito à ANATEL, mas cuja aplicação foi estendida, por meio do art. 37 da Lei 9.986/2000, a todas as agências reguladoras, a disciplina deve dar-se mediante lei.

• A contratação, a que se refere o art. 59 da Lei 9.472/1997 (11), de técnicos ou empresas especializadas, inclusive consultores independentes e auditores externos, para executar atividades de competência da ANATEL, deve observar o regular procedimento licitatório previsto pelas leis de regência.

• Efetivamente, a contratação sem o procedimento licitatório previsto pelas leis de regência fere o art. 22, XXVII, da CF.

• A possibilidade de concomitância de regimes público e privado de prestação do serviço, assim como a definição das modalidades do serviço são questões estritamente técnicas, da alçada da agência, a quem cabe o estabelecimento das bases normativas de cada matéria relacionada à execução, à definição e ao estabelecimento das regras peculiares a cada serviço.

• Diante da existência de parâmetros definidores na legislação, e da permissão constitucional para a prestação do serviço de telecomunicações pelo regime privado, por meio de autorização, não se vislumbra inconstitucionalidade nos artigos 65, III, §§ 1º e 2º, 66 e 69 da Lei 9.472/1997 (12).

• A atribuição à agência da competência para definir os serviços não desborda dos limites de seu poder regulatório.

• A previsão constitucional do art. 21, XI, permite a exploração “diretamente ou mediante autorização, concessão ou permissão, os serviços de telecomunicações, nos termos da lei ”.

• Portanto, a despeito da previsão mais genérica do art. 175 da CF (13), no caso dos serviços de telecomunicações, é o texto constitucional que permite a exploração por meio de autorização, o que significa conferir à Administração a faculdade de instituir um regime privado, submetido à livre concorrência, ainda que derrogado parcialmente pela regulação estabelecida pela ANATEL (14).

• A ANATEL não pode disciplinar procedimento licitatório simplificado por meio de norma de hierarquia inferior à Lei Geral de Licitações, sob pena de ofensa ao princípio da reserva legal. Por isso, são inconstitucionais as expressões “simplificado” e “nos termos por ela regulados” do art. 119, da Lei 9.472/1997 (15).

• As normas licitatórias são cogentes, não viabilizando atuação livre deste ou daquele administrador, por maior que lhe seja a envergadura.

• Com base nesse entendimento, o Plenário, por maioria, julgou parcialmente procedente pedido formulado em ação direta ajuizada contra dispositivos da Lei 9.472/1997, que dispõe sobre a organização dos serviços de telecomunicações, a criação e o funcionamento de um órgão regulador e outros aspectos institucionais, nos termos da Emenda Constitucional 8/1995. Vencido o ministro Roberto Barroso.

• ADI 429
• Órgão julgador: Tribunal Pleno
• Relator(a): Min. LUIZ FUX
• Julgamento: 20/08/2014
• Publicação: 30/10/2014

AÇÃO DIRETA DE INCONSTITUCIONALIDADE. TRIBUTÁRIO. NORMAS GERAIS DE DIREITO TRIBUTÁRIO. ICMS. CONSTITUIÇÃO DO ESTADO DO CEARÁ. IMPUGNAÇÃO AOS ARTIGOS 192, §§ 1º E 2º; 193 E SEU PARÁGRAFO ÚNICO; 201 E SEU PARÁGRAFO ÚNICO; 273, PARÁGRAFO ÚNICO; E 283, III, DA CONSTITUIÇÃO ESTADUAL. ADEQUADO TRATAMENTO TRIBUTÁRIO AO ATO COOPERATIVO E ISENÇÃO DE TRIBUTOS ESTADUAIS ÀS PEQUENAS E MICROEMPRESAS; PEQUENOS E MICROPRODUTORES RURAIS; BEM COMO PARA AS EMPRESAS QUE ABSORVAM CONTINGENTES DE DEFICIENTES NO SEU QUADRO FUNCIONAL OU CONFECCIONE E COMERCIALIZE APARELHOS DE FABRICAÇÃO ALTERNATIVA PARA PORTADORES DE DEFICIÊNCIA. DISPOSIÇÕES PREVISTAS NA CONSTITUIÇÃO ESTADUAL. VIOLAÇÃO AO DISPOSTO NO ARTIGO 146, INCISO III, ALÍNEA “C”, DA CRFB/88. COMPETÊNCIA CONCORRENTE DA UNIÃO, ESTADOS E DISTRITO FEDERAL PARA LEGISLAR SOBRE DIREITO TRIBUTÁRIO. ARTIGO 24, INCISO I, DA CRFB/88. AUSÊNCIA DE INCONSTITUCIONALIDADE. DEMAIS DISPOSITIVOS OBJURGADOS. CONCESSÃO UNILATERAL DE BENEFÍCIOS E INCENTIVOS FISCAIS. ICMS. AUSÊNCIA DE CONVÊNIO INTERESTADUAL. AFRONTA AO DISPOSTO NO ARTIGO 155, § 2º, INCISO XII, “G”, DA CRFB/88. CAPUT DO ART. 193 DA CONSTITUIÇÃO ESTADUAL. INTERPRETAÇÃO CONFORME À CONSTITUIÇÃO SEM DECLARAÇÃO DE NULIDADE. EXCLUSÃO DO ICMS DO SEU CAMPO DE INCIDÊNCIA. - 1. O Federalismo brasileiro exterioriza-se, dentre outros campos, no segmento tributário pela previsão de competências legislativo-fiscais privativas dos entes políticos, reservada à Lei Complementar estabelecer normas gerais.

• 2. A concessão de benefícios fiscais não é matéria relativa à inciativa legislativa privativa do Chefe do Poder Executivo, nos termos do estabelecido no artigo 61, § 1º, inciso II, alínea b, da CRFB/88.

• 3. O poder de exonerar corresponde a uma derivação do poder de tributar, assim, presente este, não há impedimentos para que as entidades investidas de competência tributária, como o são os Estados-membros, definam hipóteses de isenção ou de não-incidência das espécies tributárias em geral, à luz das regras de competência tributária, o que não interdita a Constituição estadual de dispor sobre o tema.

• 4. O art. 146, III, “c”, da CRFB/88 determina que lei complementar estabeleça normas gerais sobre matéria tributária e, em especial, quanto ao adequado tratamento tributário a ser conferido ao ato cooperativo praticado pelas sociedades cooperativas.

• 5. Não há a alegada inconstitucionalidade da Constituição estadual, porquanto a competência para legislar sobre direito tributário é concorrente, cabendo à União estabelecer normas gerais, aos Estados-membros e o Distrito Federal suplementar as lacunas da lei federal sobre normas gerais, afim de afeiçoá-las às particularidades locais, por isso que inexistindo lei federal de normas gerais, acerca das matérias enunciadas no citado artigo constitucional, os Estados podem exercer a competência <u>legislativa plena</u> (§ 3º, do art. 24 da CRFB/88).

• 6. Consectariamente, o § 1º do artigo 192 da Constituição cearense que estabelece que “o ato cooperativo, praticado entre o associado e sua cooperativa, não implica em operação de mercado”, não é inconstitucional.

• 7. É que a Suprema Corte, ao apreciar situação análoga, assentou que, enquanto não promulgada a lei complementar a que se refere o art. 146, III, “c”, da CRFB/88, não se pode pretender que, com base na legislação local, não possa o Estado-membro, que tem competência concorrente em se tratando de direito tributário (artigo 24, I e § 3º, da Carta Magna), dê às cooperativas o tratamento que julgar adequado, até porque tratamento adequado <u>não significa necessariamente tratamento privilegiado</u>, verbis: “Inexiste, no caso, ofensa ao artigo 146, III, ‘c’, da Constituição, porquanto esse dispositivo constitucional não concedeu às cooperativas imunidade tributária, razão por que, enquanto não for promulgada a lei complementar a que ele alude, não se pode pretender que, com base na legislação local mencionada no aresto recorrido, não possa o Estado-membro, que tem competência concorrente em se tratando de direito tributário (artigo 24, I e § 3º, da Carta Magna), dar às Cooperativas o tratamento que julgar adequado, até porque tratamento adequado não significa necessariamente tratamento privilegiado.”(RE 141.800, Rel. Min. MOREIRA ALVES, DJ de 30.10.97).

• 8. A concessão unilateral de benefícios fiscais relativos ao ICMS, sem a prévia celebração de convênio intergovernamental, nos termos do que dispõe a LC nº 24/75, recepcionada inequivocamente consoante jurisprudência da Corte, afronta ao disposto no artigo 155, § 2º, XII, “g”, da CRFB/88.

• 9. O comando constitucional contido no art. 155, § 2º, inciso “g”, que reserva à lei complementar federal “regular a forma como, mediante deliberação dos Estados e do Distrito Federal, isenções, incentivos e benefícios fiscais serão concedidos e revogados” aplicado, in casu, revela manifesta a inconstitucionalidade material dos dispositivos da Constituição cearense que outorga incentivo fiscal incompatível com a CRFB/88. Precedentes: ADI 84, Rel. Min. ILMAR GALVÃO, Tribunal Pleno, julgado em 15/02/1996, DJ 19-04-1996).

• 10. A outorga de benefícios fiscais relativos ao ICMS, sem a prévia e necessária celebração de convênio entre os Estados e o Distrito Federal é manifestamente inconstitucional. Precedentes: ADI 2906/RJ, rel. Min. Marco Aurélio, 1º.6.2011; ADI 2376/RJ, rel. Min. Marco Aurélio, 1º.6.2011; ADI 3674/RJ, rel. Min. Marco Aurélio, 1º.6.2011; ADI 3413/RJ, rel. Min. Marco Aurélio, 1º.6.2011; ADI 4457/PR, rel. Min. Marco Aurélio, 1º.6.2011; ADI 3794/PR, rel. Min. Joaquim Barbosa, 1º.6.2011; ADI 2688/PR, rel. Min. Joaquim Barbosa, 1º.6.2011; ADI 1247/PA, rel. Min. Dias Toffolli, 1º.6.2011; ADI 3702/ES, rel. Min. Dias Toffoli, 1º.6.2011; ADI 4152/SP, rel. Min. Cezar Peluso, 1º.6.2011; ADI 3664/RJ, rel. Min. Cezar Peluso, 1º.6.2011; ADI 3803/PR, rel. Min. Cezar Peluso, 1º.6.2011; ADI 2549/DF, rel. Min. Ricardo Lewandowski, 1º.6.2011.

• 11. Calcado nessas premissas, forçoso concluir que: a) O § 2º do art. 192 da Constituição cearense concede isenção tributária de ICMS aos implementos e equipamentos destinados aos deficientes físicos auditivos, visuais, mentais e múltiplos, bem como aos veículos automotores de fabricação nacional com até 90 HP de potência adaptados para o uso de pessoas portadoras de deficiência, o que acarreta a declaração de sua inconstitucionalidade, sem a pronúncia de nulidade, por um prazo de doze meses. b) O caput do artigo 193 da Constituição cearense isenta as microempresas de tributos estaduais, ao passo que seu parágrafo único estende a isenção, de forma expressa, ao ICMS, o que acarreta a declaração de inconstitucionalidade do parágrafo único e do caput, este por interpretação conforme para excluir de seu âmbito de incidência o ICMS. c) A Inconstitucionalidade do artigo 201 e seu parágrafo único, da Constituição cearense é manifesta, porquanto pela simples leitura dos dispositivos verifica-se que o imposto estadual com tal campo de incidência é o ICMS, verbis: “Art. 201. Não incidirá imposto, conforme a lei dispuser, sobre todo e qualquer produto agrícola pertencente à cesta básica , produzido por pequenos e microprodutores rurais que utilizam apenas a mão-de-obra familiar, vendido diretamente aos consumidores finais. Parágrafo único. A não-incidência abrange produtos oriundos de associações e cooperativas de produção e de produtores, cujos quadros sociais sejam compostos exclusivamente por pequenos e microprodutores e trabalhadores rurais sem terra. d) O parágrafo único do art. 273 e o inciso III do art. 283, da Constituição cearense incidem na mesma inconstitucionalidade, verbis: “Art. 273. Toda entidade pública ou privada que inclua o atendimento à criança e ao adolescente, inclusive os órgãos de segurança, tem por finalidade prioritária assegurar-lhes os direitos fundamentais. Parágrafo único. As empresas privadas que absorvam contingentes de até cinco por cento de deficientes no seu quadro funcional gozarão de incentivos fiscais de redução de um por cento no ICMS. (…) Art. 283. Para estimular a confecção e comercialização de aparelhos de fabricação alternativa para as pessoas portadoras de deficiência, o Estado concederá: (…) III - isenção de cem por cento do ICMS.

• 12. Pedido de inconstitucionalidade julgado parcialmente procedente para declarar: (i) inconstitucional o parágrafo 2º do art. 192, sem a pronúncia de nulidade, por um prazo de doze meses (ii) parcialmente inconstitucional o caput do art. 193, dando-lhe interpretação conforme para excluir de seu âmbito de incidência o ICMS; (iii) inconstitucional o parágrafo único do artigo 193; (iv) inconstitucional o artigo 201, caput, e seu parágrafo único; (v) inconstitucional o parágrafo único do artigo 273; (vi) inconstitucional o inciso III do artigo 283; julgar improcedente o pedido quanto ao caput e §1º do artigo 192, todos os artigos da Constituição cearense.

Observação - Acórdão(s) citado(s): (COMPETÊNCIA, LEI COMPLEMENTAR FEDERAL, REGULAÇÃO, BENEFÍCIO FISCAL, ICMS) ADI 84 (TP). (INCONSTITUCIONALIDADE, ESTADO-MEMBRO, CONCESSÃO UNILATERAL, BENEFÍCIO FISCAL, ICMS) ADI 1247 (TP), ADI 2376 (TP), ADI 2549 (TP), ADI 2688 (TP), ADI 2906 (TP), ADI 3413 (TP), ADI 3664 (TP), ADI 3674 (TP), ADI 3702 (TP), ADI 3794 (TP), ADI 3803 (TP), ADI 3809 (TP), ADI 4152 (TP), ADI 4457 (TP). (COMPETÊNCIA, ESTADO-MEMBRO, REGULAÇÃO, TRATAMENTO TRIBUTÁRIO, COOPERATIVA) RE 141800 (2ªT). (ISENÇÃO TRIBUTÁRIA, ICMS, TEMPLO RELIGIOSO) ADI 3421 (TP). Número de páginas: 44. Análise: 12/12/2014, RAF.

Doutrina Ferreira. BRANCO, Paulo Gustavo Gonet. Curso de Direito Constitucional. 8. ed. São Paulo: Saraiva, 2013. p. 803/804. PYRRHO, Sérgio. Soberania, ICMS e isenções os convênios e os tratados internacionais. Rio de Janeiro: Lumen Juris, 2008. p. 32. TORRES, Ricardo Lobo. Tratado de direito constitucional financeiro

Obs.: Muito embora a CF preveja lei complementar federal para conferir qual será o tratamento adequado ao ato cooperativo, isso não significa que os Estados-Membros estarão impedidos de legislar plenamente quanto à matéria enquanto não houve a necessária lei complementar federal. Isso é, segue-se a regra geral do art. 24, § 3º, CF que estabelece competência legislativa plena aos Estados acaso União não edite regras gerais.

• Informativo 991
• RE 784439 / DF
• Órgão julgador: Tribunal Pleno
• Relator(a): Min. ROSA WEBER
• Julgamento: 26/06/2020 (Virtual)
• Ramo do Direito: Tributário
• Matéria: ISS; Impostos

Natureza taxativa da lista do rol de serviços sujeitos a ISS

Tese fixada

• É taxativa a lista de serviços sujeitos ao ISS a que se refere o art. 156, III, da Constituição Federal, admitindo-se, contudo, a incidência do tributo sobre as atividades inerentes aos serviços elencados em lei em razão da interpretação extensiva.

Resumo - As listas de serviços preveem ser irrelevante a nomenclatura dada ao serviço e trazem expressões para permitir a interpretação extensiva de alguns de seus itens, notadamente se socorrendo da fórmula “e congêneres”. Não existe obstáculo constitucional contra esta sistemática legislativa e excessos interpretativos que venham a ocorrer serão dirimíveis pelo Poder Judiciário.

Legislação: CF/1988, art. 5º, LV, art. 156, III.

Precedentes: RE 592.905/SC, relator Min. Eros Grau, DJe de 5.3.2010 (Tema 125 RG)RE 651.703/PR, relator Min. Luiz Fux, DJe de 26.4.2017 (Tema 581 RG)

Observação: Clipping das sessões virtuais. Acórdão publicado no DJe de 15.9.2020.

• Informativo 1110
• ADI 5674 / DF
• Órgão julgador: Tribunal Pleno
• Relator(a): Min. ANDRÉ MENDONÇA
• Julgamento: 29/09/2023 (Virtual)
• Ramo do Direito: Tributário, Constitucional
• Matéria: Impostos; ISS; Hipóteses de Incidência; Hospedagem / Sistema Tributário Nacional; Impostos dos Municípios; ISS

ISS: incidência sobre atividades relativas à hospedagem

Resumo - É constitucional a incidência do Imposto sobre Serviços de Qualquer Natureza (ISS) sobre as atividades relativas à hospedagem de qualquer natureza, prevista no subitem 9.01 da lista de serviços anexa à Lei Complementar 116/2003.

• Os contratos que veiculam hospedagem de qualquer natureza, nos meios dispostos na referida lista, são preponderantemente de serviços. Ademais, o ISS incide sobre as atividades que representam obrigações de fazer e obrigações mistas, que incluem obrigação de dar (1).

• Não se pode fazer confusão entre a relação negocial de hospedagem e o contrato de locação de bem imóvel, de modo que é indevido excluir da base de cálculo desse tributo municipal a parcela da locação da unidade habitacional, visto que a circulação de serviço prevista contratualmente tem caráter singular e ganha sentido econômico com sua visualização unitária.

• Assim, dada a prevalência da uniformização da legislação federal, reforça-se o entendimento do STJ de que todas as parcelas que integram o preço do serviço de hotelaria compõem a base de cálculo do ISS.

• Com base nesses e em outros entendimentos, o Plenário, por unanimidade, julgou improcedente a ação, para assentar a constitucionalidade do subitem 9.01 da lista de serviços anexa à Lei Complementar 116/2003 (2).(1) Precedentes citados: RE 651.703 (Tema 581 RG); RE 603.136 (Tema 300 RG) e RE 784.439 (Tema 296 RG). (2) Lista de serviços anexa à Lei Complementar 116/2003: “9 – Serviços relativos a hospedagem, turismo, viagens e congêneres. 9.01 – Hospedagem de qualquer natureza em hotéis, apart-service condominiais, flat, apart-hotéis, hotéis residência, residence-service, suite service, hotelaria marítima, motéis, pensões e congêneres; ocupação por temporada com fornecimento de serviço (o valor da alimentação e gorjeta, quando incluído no preço da diária, fica sujeito ao Imposto Sobre Serviços).”

Legislação: Lista de serviços anexa à Lei Complementar 116/2003: subitem 9.01.

Precedentes: RE 651.703 (Tema 581 RG); RE 603.136 (Tema 300 RG) e RE 784.439 (Tema 296 RG).

Why does it hold for this interval? Is it the error in approximation because the function may require more than 3 Taylor terms? If so, why did they not use Big O notation as above?

Com efeito, vide do acórdão da ADI 5938, que o afastamento deve ser automático e incondicionado. Determinar à gestante que apresente laudo médico para afastamento vulnera a proteção à maternidade e à integral proteção à criança, criando hipóteses em que - por desconhecimento, receio de demissão ou algo do gênero - a mulher tenha contato com ambiente potencialmente insalubre em grau máximo, inclusive durante a amamentação.

• Informativo 942
• ADI 5938 / DF
• Órgão julgador: Tribunal Pleno
• Relator(a): Min. ALEXANDRE DE MORAES
• Julgamento: 29/05/2019 (Presencial)
• Ramo do Direito: Trabalho
• Matéria: PROTEÇÃO À MATERNIDADE

CLT, art. 394-A: atividade insalubre e afastamento de gestante e de lactante

Resumo - O Plenário, por maioria, confirmou medida cautelar deferida pelo ministro Alexandre de Moraes (relator) em decisão monocrática e julgou parcialmente procedente pedido formulado em ação direta para declarar a inconstitucionalidade da expressão “quando apresentar atestado de saúde, emitido por médico de confiança da mulher, que recomende o afastamento”, contida nos incisos II e III do art. 394-A da Consolidação das Leis do Trabalho (CLT) (1), inseridos pelo art. 1º da Lei 13.467/2017.

• O colegiado registrou que, na redação anterior, o preceito estabelecia que a empregada gestante ou lactante seria afastada, enquanto durasse a gestação e a lactação, de quaisquer atividades, operações ou locais insalubres e deveria exercer suas atividades em local salubre.

• Com a alteração implementada pela Lei 13.467/2017, que promoveu a “Reforma Trabalhista” de 2017, o art. 394-A passou a permitir que a mulher gestante continuasse a realizar suas atividades mesmo em condições insalubres em grau mínimo ou médio. Ainda mais grave, no caso da lactação, que ela permanecesse a desempenhá-las inclusive em grau máximo de insalubridade. Ademais, criou o ônus à gestante ou à lactante da apresentação de atestado de saúde, emitido por médico de sua confiança, que certificasse a necessidade do afastamento. Essa mudança trouxe a exposição dessas trabalhadoras a atividades insalubres.

• A Corte assinalou que a Constituição Federal (CF) proclama, no caput do art. 6º, a proteção à maternidade como direito social, ligado à dignidade da pessoa humana. Essa proteção é a ratio para inúmeros outros direitos sociais instrumentais, como a licença-gestante, o direito à segurança no emprego, que compreende a tutela da relação de emprego contra dispensa arbitrária sem justa causa da gestante, e, nos termos do art. 7º, a proteção do mercado de trabalho da mulher, mediante incentivos específicos (inciso XX), e a redução dos riscos inerentes ao trabalho, por meio de normas de saúde, higiene e segurança (inciso XXII).

• Sob essa ótica, a proteção da mulher grávida ou lactante contra o trabalho insalubre caracteriza-se como importante direito social instrumental protetivo tanto da mulher quanto da criança. Trata-se de normas de salvaguarda dos direitos sociais da mulher e de efetivação de integral proteção ao recém-nascido, possibilitando sua convivência com a mãe, nos primeiros meses de vida, de maneira harmônica e segura, sem os perigos de um ambiente insalubre. A imprescindibilidade da máxima eficácia desse direito social também decorre da absoluta prioridade que o art. 227 do texto constitucional (2) estabelece à integral proteção à criança, inclusive ao nascituro e ao recém-nascido lactente.

• Há, na hipótese, direito de dupla titularidade. A proteção à maternidade e a integral proteção à criança são direitos irrenunciáveis e não podem ser afastados pelo desconhecimento, pela impossibilidade decorrente da distância de centros médicos ou pela própria negligência da gestante ou lactante em apresentar atestado médico, sob pena de prejudicá-la e de prejudicar o recém-nascido. Outras razões poderiam levar a mulher a não apresentar o documento, como, por exemplo, o medo de vir a ser demitida posteriormente ou a pressão para não entregar o atestado.

• Dessa forma, as expressões impugnadas não estão em consonância com os dispositivos constitucionais. A previsão do <u>afastamento automático</u> da mulher gestante ou lactante do ambiente insalubre está de acordo com a jurisprudência do Supremo Tribunal Federal (STF) em relação à integral proteção à maternidade e à saúde da criança.

• Na espécie, a mudança trazida pela lei pretendeu a inversão do ônus da demonstração probatória e documental da circunstância insalubre, a inversão da proteção à maternidade e ao nascituro ou recém-nascido. Partiu-se erroneamente da lógica de que, em regra, a insalubridade mínima e a média, durante a gestação, e mesmo a máxima, durante a lactação, não causam riscos. Isso desfavorece a plena proteção do interesse constitucionalmente protegido, na medida em que sujeita a empregada a maior embaraço para o exercício de seus direitos. O caso guarda relação com julgado recente em que apreciado o Tema 497 da repercussão geral (RE 629.053) sobre a estabilidade de empregada gestante.

• Naquele julgamento, o STF consignou que o conjunto dos direitos sociais foi consagrado constitucionalmente como uma das espécies de direitos fundamentais, caracterizando-se como verdadeiras liberdades positivas, de observância obrigatória em um Estado Social de Direito, visando à melhoria das condições de vida dos hipossuficientes e à concretização da igualdade social.

• O ministro Edson Fachin frisou que não se trata de reconhecer às mulheres qualquer benesse do ponto de vista constitucional. Por sua vez, o ministro Roberto Barroso acrescentou que a exigência viola o princípio da precaução, que vale também para o ambiente do trabalho, pelo qual, sempre que houver risco ou incerteza, deve ser favorecida a posição mais conservadora e protetiva.

• A ministra Rosa Weber expôs o histórico do direito e os principais instrumentos internacionais a respeito. Aduziu que a alteração implica inegável retrocesso social, uma vez que revoga anterior norma proibitória desse trabalho da gestante e lactante, além do menoscabo ao direito fundamental à saúde da mãe trabalhadora, pois transfere ao próprio sujeito tutelado a responsabilidade pela conveniência de atestado indicando a necessidade de afastamento do trabalho. Por seu turno, o ministro Luiz Fux também apontou a inconstitucionalidade por violação à igualdade de gênero, acompanhando o que destacado pelo ministro Alexandre de Moraes (relator) e pela ministra Rosa Weber.

• Já o ministro Celso de Mello reforçou os fundamentos trazidos e registrou que a cláusula que proíbe o retrocesso em matéria social traduz, no processo de sua concretização, verdadeira dimensão negativa pertinente aos direitos sociais, a impedir que os níveis de concretização dessas prerrogativas, uma vez atingidos, venham a ser reduzidos, degradados ou suprimidos.

• Vencido o ministro Marco Aurélio, que reputou improcedente o pleito formulado na ação. A seu ver, os preceitos encerram tão somente liberdade da mulher prestadora dos serviços, no que prevista a possibilidade de afastamento do ambiente insalubre, e visam atender às exigências do mercado de trabalho para não se criarem óbices à contratação da mão de obra feminina. O ministro afirmou não ser desarrazoada a imposição do atestado médico.

(1) CLT: “Art. 394-A. Sem prejuízo de sua remuneração, nesta incluído o valor do adicional de insalubridade, a empregada deverá ser afastada de: (...) II – atividades consideradas insalubres em grau médio ou mínimo, quando apresentar atestado de saúde, emitido por médico de confiança da mulher, que recomende o afastamento durante a gestação; III – atividades consideradas insalubres em qualquer grau, quando apresentar atestado de saúde, emitido por médico de confiança da mulher, que recomende o afastamento durante a lactação.” (2) CF/1988: “Art. 227. É dever da família, da sociedade e do Estado assegurar à criança, ao adolescente e ao jovem, com absoluta prioridade, o direito à vida, à saúde, à alimentação, à educação, ao lazer, à profissionalização, à cultura, à dignidade, ao respeito, à liberdade e à convivência familiar e comunitária, além de colocá-los a salvo de toda forma de negligência, discriminação, exploração, violência, crueldade e opressão.” (3) CF/1988: “Art. 1º A República Federativa do Brasil, formada pela união indissolúvel dos Estados e Municípios e do Distrito Federal, constitui-se em Estado Democrático de Direito e tem como fundamentos: (...) IV – os valores sociais do trabalho e da livre iniciativa;”

Legislação: CF, arts. 1º, IV e 227. CLT, art. 394-A, II e III.

Precedentes: RE 629.053

Mediante simples aditamento, o Presidente, por despacho, poderá estender os efeitos da suspensão a liminares supervenientes cujo objeto seja idêntico. Ou seja, em virtude da celeridade processual, é prescindível processos autônomos para a suspensão de liminares análogas, desde que haja aditamento da inicial.

Observe que, assim, a suspensão, em regra, não é para liminares futuras, para as quais necessita-se de <u>aditamento</u> à inicial.

Leibniz se da un tiro en el pie. Si Dios es necesario pero también es perfecto, el mundo como creación suya no pudo ser de otra manera y no pudo no existir porque Dios no pudo no haberlo creado ya que su decisión de crear el mundo es perfecta y no hay otra decisión posible derivada de su perfección, por lo tanto el mundo es necesario, no contingente ya que es una consecuencia necesaria de un ser necesario por lo tanto ambos existen necesariamente. Además, si no pudo haber momento ni instancia en la que el mundo no existiera porque dios no pudo haber permanecido en un estado de imperfección (ya que crear el mundo y coexistir con el es perfecto, entonces su contrario es imperfecto) el mundo tiene que existir desde siempre con Dios mismo por lo que no comenzó a existir.

Heidegger se apropia del concepto de "nada" para dar su explicación de la experiencia mental humana de imaginar la nada y sus consecuencias, derivando en un aprecio profundo por el ser. Parlotea sobre el concepto de nada deformandolo dificultando la comprensión de su idea. El lector de por sí siempre da su toque de deformación de la idea, pero elegir el parloteo por sobre la expresión explícita añade una capa inecesaria mas sobre la interpretación de la idea.

O locatário tem direito de preferência na compra do imóvel que locatário pretenda vender. Acaso haja preterição, o locatário ainda possui meios para obter a propriedade do bem.

Para tanto, os requisitos para a constituição de Direito Real a favor do locatário:

• Requerer, em até 6 (seis) meses, o imóvel para si, contado da data do registro em cartório de imóveis;
• Depositar o valor do imóvel e demais despesas de transferências;
• Averbação junto à matrícula do imóvel do contrato de locação, desde que averbado em, no mínimo, 30 (trinta) dias da data da alienação junto à matrícula;

Observe que a lei estabelece que a averbação do contrato de locação na matrícula do imóvel tem 2 importantes efeitos: - Assegurar que eventual novo locatário observe o prazo de locação, proibindo a denúncia do contrato sem antes decorrer o prazo contratual; - Assegurar a aquisição do imóvel acaso haja preterição do locador quanto ao direito de preferência do locatário.

Por fim, cabível destacar que a averbação, enquanto manifestação da publicidade dos atos relativos a direitos reais, é essencial para geração de efeito erga omnes. Com efeito, para garantir o direito real de aquisição, é imprescindível a averbação do contrato de locação.

Lado outro, tratando-se da outra hipótese referente ao prejuízo do direito de preferência do locatário, o pleito de perdas e danos não se submete a registro público como condição.

STF Súmula 442 A inscrição do contrato de locação no Registro de Imóveis, para a validade da cláusula de vigência contra o adquirente do imóvel, ou perante terceiros, dispensa a transcrição no Registro de Títulos e Documentos.

Observe que o direito de vigência da locação, na hipótese de alienação do imóvel a terceiros, tem 3 requisitos: - Existir no contrato de locação a cláusula de vigência; - Haver averbação do contrato de locação na matrícula do imóvel. - Locação por prazo determinado.

Com isso, inexistindo algum dos requisitos acima, não haverá direito à vigência.

working towards a sweet-spot

achive what's above the threshold that is required

working towards a sweet-spot

achive what's above the threshold that is required

https://hyp.is/95kSDrJPEfCvcauZZHECLg/www.futuresplatform.com/blog/s-curve-analysis-foresight

working towards a sweet-spot

REALize what's just above the threshold that is required

groan zone of perseverance where progress appears to be stalled for a long long time

working towards a sweet-spot

achive what's above the threshold that is required

from

O jaká kritéria se, například, jedná?

DOI: 10.1523/JNEUROSCI.0539-25.2025

Resource: (Jackson ImmunoResearch Labs Cat# 705-545-147, RRID:AB_2336933)

Curator: @scibot

SciCrunch record: RRID:AB_2336933

What is this?

DOI: 10.1038/s41467-025-64341-x

Resource: Cornell University BRC Genomics Core Facility (RRID:SCR_021727)

Curator: @scibot

SciCrunch record: RRID:SCR_021727

What is this?

Duzentos anos atrás, antes do advento do capitalismo, o status social de um homem permanecia inalterado do princípio ao fim de sua existência: era herdado dos seus ancestrais e nunca mudava. Se nascesse pobre, pobre seria para sempre; se rico – lorde ou duque –, manteria seu ducado, e a propriedade que o acompanhava, pelo resto dos seus dias

Tady bych tu logiku sdělení otočila

V posledních 15 letech došlo k velkému posunu ve struktuře podle právního důvodu užívání bytu. Zatímco v roce 2011 žilo 63 % mladých domácností ve vlastnické formě bydlení (vlastnickém, nebo družstevním) a 32 % v nájemním bydlení, v roce 2024 byl tento poměr již téměř vyrovnaný (48 %, resp. 42 %), přičemž podíl domácností ve vlastnické formě se snížil o 15 p.b.

...potřeba soukromí nebo snaha o posun k dospělému životu.

...což je přibližně 2x více, než musely vynaložit domácnosti v produktivním věku.

Z porovnání mladých domácností v nájemním bydlení s domácnostmi v produktivním věku v nájemním bydlení je zřejmé, že zejména v krajských městech se odlišný vývojový trend těchto dvou skupin neustále prohlubuje; zatímco podíl domácností v produktivním věku, které jsou v nájemním bydlení, se mezi lety 2008 a 2024 snížil z 24 na 17 % (snížení o 7 p.b.), u mladých domácností se ve stejném období zvýšil z 43 na 59 % (zvýšení o 16 p.b.).

Zároveň by mi tady přišlo jednodušší mluvit o domácnostech a ne o těch osobách, protože

a) to je formulačně trochu krkolomné

b) o osobách mluvíš v tom předchozím grafu/textu a čtenář musí být superpozorný, aby odlišil mladé osoby a osoby žijící v domácnostech mladých ;)

formulaci v předchozím komentu už jsem upravila na domácnosti - zvaž podle sebe

Traduce en tu mente el siguiente extracto al español sin mirar el texto y luego comprueba si lo has hecho correctamente o si existen otras alternativas de vocabulario:

The advantages of sharing housing are extensive: the most prominent is the savings you have by paying only for a room and not for the whole house. By sharing expenses, there is the possibility of having a larger space for a lower price. As if that were not enough, following the roommate guide that you can see in the video, it is most likely that no misunderstandings will be generated between the cohabitants and you can even make plans together.

Although there are also disadvantages, the list of advantages can be longer than the list of problems. It is up to the individual to decide which lifestyle he or she prefers to lead.

Di si las siguientes frases sobre el juego de las damas son verdaderas o falsas: 1. Se juega con el mismo tablero que el ajedrez. 2. Gana quien coma el mayor número de fichas del contrario.

Relaciona cada juego con su objetivo: 1. Gana quien consigue mayor puntuación al sumar el valor de las letras y/o palabras. 2. Gana quien saca las fichas fuera del tablero antes. 3. Gana quien lleva las fichas al centro del tablero. 4. Gana quien adivina el mayor número de palabras representadas.

Encuentra en este extracto un sinónimo de amenazar, adversario, misión, enganchar.

Explica esta frase en tus propias palabras y di si estás de acuerdo o no y por qué.

¿Cómo explicas esta cita de Rawlings en tus propias palabras?

Relaciona estas frases con los siguientes platos: quesadilla, tamal, burrito, tacos:

1. Este plato tiene su origen en las minas de plata del siglo dieciocho en México.
2. Este plato consiste en tortillas que se pueden doblar y rellenar de frijoles, guacamole y queso.
3. Este plato tradicionalmente se envuelve en hojas de maíz y se basa en una masa de maíz rellena.
4. Este plato consiste en tortillas de harina dobladas por la mutad con papas, frijoles o carne y queso fundido por dentro.

Encuentra un sinónimo de: trozos, destemplado, aderezar, adobar

Preguntas de comprensión:

1. "Cambiar el rumbo, transformar la educación". ¿Cómo explicarías este lema en tus propias palabras?

2. ¿Verdadero o falso? Canadá es líder entre las potencias mundiales en destinar más dinero para la educación.

3. ¿Verdadero o falso? En Finlandia los padres intervienen con frecuencia en la toma de decisiones escolares.

4. ¿Verdadero o falso? En Hong Kong se pone énfasis en la memorización y en la creatividad.

¿Verdadero o falso? En Finlandia los padres intervienen con frecuencia en la toma de decisiones escolares.

¿Verdadero o falso? En Hong Kong se pone énfasis en la memorización y en la creatividad.

¿Verdadero o falso? Canadá es líder entre las potencias mundiales en destinar más dinero para la educación.

Busca en el texto una expresión idiomática que significa lo siguiente: Acabar con una situación de indiferencia, desconfianza o tensión con otra persona, iniciando la conversación con ella y procurando crear un ambiente agradable.

Decimos que algo es un _ cuando pensamos que es muy bueno, algo genial, y decimos ¡Qué __! como reacción ante algo gracioso, muy oportuno o ingenioso.

¿Estás de acuerdo con esta afirmación? ¿Por qué?

Author response:

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

Reviewer #1 (Public Review):

In this paper, the authors evaluate the utility of brain age derived metrics for predicting cognitive decline by performing a 'commonality' analysis in a downstream regression that enables the different contribution of different predictors to be assessed. The main conclusion is that brain age derived metrics do not explain much additional variation in cognition over and above what is already explained by age. The authors propose to use a regression model trained to predict cognition ('brain cognition') as an alternative suited to applications of cognitive decline. While this is less accurate overall than brain age, it explains more unique variance in the downstream regression.  

Importantly, in this revision, we clarified that we did not intend to use Brain Cognition as an alternative approach. This is because, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Here we made this point more explicit and further stated that the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. By examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. 

REVISED VERSION: while the authors have partially addressed my concerns, I do not feel they have addressed them all. I do not feel they have addressed the weight instability and concerns about the stacked regression models satisfactorily.

Please see our responses to Reviewer #1 Public Review #3 below

I also must say that I agree with Reviewer 3 about the limitations of the brain age and brain cognition methods conceptually. In particular that the regression model used to predict fluid cognition will by construction explain more variance in cognition than a brain age model that is trained to predict age. This suffers from the same problem the authors raise with brain age and would indeed disappear if the authors had a separate measure of cognition against which to validate and were then to regress this out as they do for age correction. I am aware that these conceptual problems are more widespread than this paper alone (in fact throughout the brain age literature), so I do not believe the authors should be penalised for that. However, I do think they can make these concerns more explicit and further tone down the comments they make about the utility of brain cognition. I have indicated the main considerations about these points in the recommendations section below. 

Thank you so much for raising this point. We now have the following statement in the introduction and discussion to address this concern (see below). 

Briefly, we made it explicit that, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. That is, the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. More importantly, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. And this is the third goal of this present study. 

From Introduction:

“Third and finally, certain variation in fluid cognition is related to brain MRI, but to what extent does Brain Age not capture this variation? To estimate the variation in fluid cognition that is related to the brain MRI, we could build prediction models that directly predict fluid cognition (i.e., as opposed to chronological age) from brain MRI data. Previous studies found reasonable predictive performances of these cognition-prediction models, built from certain MRI modalities (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). Analogous to Brain Age, we called the predicted values from these cognition-prediction models, Brain Cognition. The strength of an out-of-sample relationship between Brain Cognition and fluid cognition reflects variation in fluid cognition that is related to the brain MRI and, therefore, indicates the upper limit of Brain Age’s capability in capturing fluid cognition. This is, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Consequently, if we included Brain Cognition, Brain Age and chronological age in the same model to explain fluid cognition, we would be able to examine the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age. These unique effects of Brain Cognition, in turn, would indicate the amount of co-variation between brain MRI and fluid cognition that is missed by Brain Age.”

From Discussion:

“Third, by introducing Brain Cognition,  we showed the extent to which Brain Age indices were not able to capture the variation in fluid cognition that is related to brain MRI. More specifically, using Brain Cognition allowed us to gauge the variation in fluid cognition that is related to the brain MRI, and thereby, to estimate the upper limit of what Brain Age can do. Moreover, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age.

From our results, Brain Cognition, especially from certain cognition-prediction models such as the stacked models, has relatively good predictive performance, consistent with previous studies (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). We then examined Brain Cognition using commonality analyses (Nimon et al., 2008) in multiple regression models having a Brain Age index, chronological age and Brain Cognition as regressors to explain fluid cognition. Similar to Brain Age indices, Brain Cognition exhibited large common effects with chronological age. But more importantly, unlike Brain Age indices, Brain Cognition showed large unique effects, up to around 11%. As explained above, the unique effects of Brain Cognition indicated the amount of co-variation between brain MRI and fluid cognition that was missed by a Brain Age index and chronological age. This missing amount was relatively high, considering that Brain Age and chronological age together explained around 32% of the total variation in fluid cognition. Accordingly, if a Brain Age index was used as a biomarker along with chronological age, we would have missed an opportunity to improve the performance of the model by around one-third of the variation explained.” 

This is a reasonably good paper and the use of a commonality analysis is a nice contribution to understanding variance partitioning across different covariates. I have some comments that I believe the authors ought to address, which mostly relate to clarity and interpretation 

Reviewer #1 Public Review #1

First, from a conceptual point of view, the authors focus exclusively on cognition as a downstream outcome. I would suggest the authors nuance their discussion to provide broader considerations of the utility of their method and on the limits of interpretation of brain age models more generally. 

Thank you for your comments on this issue. 

We now discussed the broader consideration in detail:

(1) the consistency between our findings on fluid cognition and other recent works on brain disorders, 

(2) the difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021)

and 

(3) suggested solutions we and others made to optimise the utility of Brain Age for both cognitive functioning and brain disorders.

From Discussion:

“This discrepancy between the predictive performance of age-prediction models and the utility of Brain Age indices as a biomarker is consistent with recent findings (for review, see Jirsaraie, Gorelik, et al., 2023), both in the context of cognitive functioning (Jirsaraie, Kaufmann, et al., 2023) and neurological/psychological disorders (Bashyam et al., 2020; Rokicki et al., 2021). For instance,  combining different MRI modalities into the prediction models, similar to our stacked models, ocen leads to the highest performance of age prediction models, but does not likely explain the highest variance across different phenotypes, including cognitive functioning and beyond (Jirsaraie, Gorelik, et al., 2023).”

“There is a notable difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021). We consider the former as a normative type of study and the lader as a case-control type of study (Insel et al., 2010; Marquand et al., 2016). Those case-control Brain Age studies focusing on neurological/psychological disorders often build age-prediction models from MRI data of largely healthy participants (e.g., controls in a case-control design or large samples in a population-based design), apply the built age-prediction models to participants without vs. with neurological/psychological disorders and compare Brain Age indices between the two groups. On the one hand, this means that case-control studies treat Brain Age as a method to detect anomalies in the neurological/psychological group (Hahn et al., 2021). On the other hand, this also means that case-control studies have to ignore underfided models when applied prediction models built from largely healthy participants to participants with neurological/psychological disorders (i.e., Brain Age may predict chronological age well for the controls, but not for those with a disorder). On the contrary, our study and other normative studies focusing on cognitive functioning often build age prediction models from MRI data of largely healthy participants and apply the built age prediction models to participants who are also largely healthy. Accordingly, the age prediction models for explaining cognitive functioning in normative studies, while not allowing us to detect group-level anomalies, do not suffer from being under-fided. This unfortunately might limit the generalisability of our study into just the normative type of study. Future work is still needed to test the utility of brain age in the case-control case.”

“Next, researchers should not select age-prediction models based solely on age-prediction performance. Instead, researchers could select age-prediction models that explained phenotypes of interest the best. Here we selected age-prediction models based on a set of features (i.e., modalities) of brain MRI. This strategy was found effective not only for fluid cognition as we demonstrated here, but also for neurological and psychological disorders as shown elsewhere (Jirsaraie, Gorelik, et al., 2023; Rokicki et al., 2021). Rokicki and colleagues (2021), for instance, found that, while integrating across MRI modalities led to age prediction models with the highest age-prediction performance, using only T1 structural MRI gave age-prediction models that were better at classifying Alzheimer’s disease. Similarly, using only cerebral blood flow gave age-prediction models that were better at classifying mild/subjective cognitive impairment, schizophrenia and bipolar disorder. 

As opposed to selecting age-prediction models based on a set of features, researchers could also select age-prediction models based on modelling methods. For instance, Jirsaraie and colleagues (2023) compared gradient tree boosting (GTB) and deep-learning brain network (DBN) algorithms in building age-prediction models. They found GTB to have higher age prediction performance but DBN to have better utility in explaining cognitive functioning. In this case, an algorithm with better utility (e.g., DBN) should be used for explaining a phenotype of interest. Similarly, Bashyam and colleagues (2020) built different DBN-based age-prediction models, varying in age-prediction performance. The DBN models with a higher number of epochs corresponded to higher age-prediction performance. However, DBN-based age-prediction models with a moderate (as opposed to higher or lower) number of epochs were better at classifying Alzheimer’s disease, mild cognitive impairment and schizophrenia. In this case, a model from the same algorithm with better utility (e.g., those DBN with a moderate epoch number) should be used for explaining a phenotype of interest.

Accordingly, this calls for a change in research practice, as recently pointed out by Jirasarie and colleagues (2023, p7), “Despite mounting evidence, there is a persisting assumption across several studies that the most accurate brain age models will have the most potential for detecting differences in a given phenotype of interest”. Future neuroimaging research should aim to build age-prediction models that are not necessarily good at predicting age, but at capturing phenotypes of interest.”

Reviewer #1 Public Review #2

Second, from a methods perspective, there is not a sufficient explanation of the methodological procedures in the current manuscript to fully understand how the stacked regression models were constructed. I would request that the authors provide more information to enable the reader to beUer understand the stacked regression models used to ensure that these models are not overfit. 

Thank you for allowing us an opportunity to clarify our stacked model. We made additional clarification to make this clearer (see below). We wanted to confirm that we did not use test sets to build a stacked model in both lower and higher levels of the Elastic Net models. Test sets were there just for testing the performance of the models.  

From Methods:

“We used nested cross-validation (CV) to build these prediction models (see Figure 7). We first split the data into five outer folds, leaving each outer fold with around 100 participants. This number of participants in each fold is to ensure the stability of the test performance across folds. In each outer-fold CV loop, one of the outer folds was treated as an outer-fold test set, and the rest was treated as an outer-fold training set. Ultimately, looping through the nested CV resulted in a) prediction models from each of the 18 sets of features as well as b) prediction models that drew information across different combinations of the 18 separate sets, known as “stacked models.” We specified eight stacked models: “All” (i.e., including all 18 sets of features),  “All excluding Task FC”, “All excluding Task Contrast”, “Non-Task” (i.e., including only Rest FC and sMRI), “Resting and Task FC”, “Task Contrast and FC”, “Task Contrast” and “Task FC”. Accordingly, there were 26 prediction models in total for both Brain Age and Brain Cognition.

To create these 26 prediction models, we applied three steps for each outer-fold loop. The first step aimed at tuning prediction models for each of 18 sets of features. This step only involved the outer-fold training set and did not involve the outer-fold test set. Here, we divided the outer-fold training set into five inner folds and applied inner-fold CV to tune hyperparameters with grid search. Specifically, in each inner-fold CV, one of the inner folds was treated as an inner-fold validation set, and the rest was treated as an inner-fold training set. Within each inner-fold CV loop, we used the inner-fold training set to estimate parameters of the prediction model with a particular set of hyperparameters and applied the estimated model to the inner-fold validation set. Acer looping through the inner-fold CV, we, then, chose the prediction models that led to the highest performance, reflected by coefficient of determination (R2), on average across the inner-fold validation sets. This led to 18 tuned models, one for each of the 18 sets of features, for each outer fold.

The second step aimed at tuning stacked models. Same as the first step, the second step only involved the outer-fold training set and did not involve the outer-fold test set. Here, using the same outer-fold training set as the first step, we applied tuned models, created from the first step, one from each of the 18 sets of features, resulting in 18 predicted values for each participant. We, then, re-divided this outer-fold training set into new five inner folds. In each inner fold, we treated different combinations of the 18 predicted values from separate sets of features as features to predict the targets in separate “stacked” models. Same as the first step, in each inner-fold CV loop, we treated one out of five inner folds as an inner-fold validation set, and the rest as an inner-fold training set. Also as in the first step, we used the inner-fold training set to estimate parameters of the prediction model with a particular set of hyperparameters from our grid. We tuned the hyperparameters of stacked models using grid search by selecting the models with the highest R2 on average across the inner-fold validation sets. This led to eight tuned stacked models.

The third step aimed at testing the predictive performance of the 18 tuned prediction models from each of the set of features, built from the first step, and eight tuned stacked models, built from the second step. Unlike the first two steps, here we applied the already tuned models to the outer-fold test set. We started by applying the 18 tuned prediction models from each of the sets of features to each observation in the outer-fold test set, resulting in 18 predicted values. We then applied the tuned stacked models to these predicted values from separate sets of features, resulting in eight predicted values. 

To demonstrate the predictive performance, we assessed the similarity between the observed values and the predicted values of each model across outer-fold test sets, using Pearson’s r, coefficient of determination (R2) and mean absolute error (MAE). Note that for R2, we used the sum of squares definition (i.e., R2 \= 1 – (sum of squares residuals/total sum of squares)) per a previous recommendation (Poldrack et al., 2020). We considered the predicted values from the outer-fold test sets of models predicting age or fluid cognition, as Brain Age and Brain Cognition, respectively.”

Author response image 1.

Diagram of the nested cross-validation used for creating predictions for models of each set of features as well as predictions for stacked models. 

Note some previous research, including ours (Tetereva et al., 2022), splits the observations in the outer-fold training set into layer 1 and layer 2 and applies the first and second steps to layers 1 and 2, respectively. Here we decided against this approach and used the same outer-fold training set for both first and second steps in order to avoid potential bias toward the stacked models. This is because, when the data are split into two layers, predictive models built for each separate set of features only use the data from layer 1, while the stacked models use the data from both layers 1 and 2. In practice with large enough data, these two approaches might not differ much, as we demonstrated previously (Tetereva et al., 2022).

Reviewer #1 Public Review #3

Please also provide an indication of the different regression strengths that were estimated across the different models and cross-validation splits. Also, how stable were the weights across splits? 

The focus of this article is on the predictions. Still, it is informative for readers to understand how stable the feature importance (i.e., Elastic Net coefficients) is. To demonstrate the stability of feature importance, we now examined the rank stability of feature importance using Spearman’s ρ (see Figure 4). Specifically, we correlated the feature importance between two prediction models of the same features, used in two different outer-fold test sets. Given that there were five outer-fold test sets, we computed 10 Spearman’s ρ for each prediction model of the same features.  We found Spearman’s ρ to be varied dramatically in both age-prediction (range\=.31-.94) and fluid cognition-prediction (range\=.16-.84) models. This means that some prediction models were much more stable in their feature importance than others. This is probably due to various factors such as a) the collinearity of features in the model, b) the number of features (e.g., 71,631 features in functional connectivity, which were further reduced to 75 PCAs, as compared to 19 features in subcortical volume based on the ASEG atlas), c) the penalisation of coefficients either with ‘Ridge’ or ‘Lasso’ methods, which resulted in reduction as a group of features or selection of a feature among correlated features, respectively, and d) the predictive performance of the models. Understanding the stability of feature importance is beyond the scope of the current article. As mentioned by Reviewer 1, “The predictions can be stable when the coefficients are not,” and we chose to focus on the prediction in the current article.   

Author response image 2.

Stability of feature importance (i.e., Elastic Net Coefficients) of prediction models. Each dot represents rank stability (reflected by Spearman’s ρ) in the feature importance between two prediction models of the same features, used in two different outer-fold test sets. Given that there were five outer-fold test sets, there were 10 Spearman’s ρs for each prediction model.  The numbers to the right of the plots indicate the mean of Spearman’s ρ for each prediction model.  

Reviewer #1 Public Review #4

Please provide more details about the task designs, MRI processing procedures that were employed on this sample in addition to the regression methods and bias correction methods used. For example, there are several different parameterisations of the elastic net, please provide equations to describe the method used here so that readers can easily determine how the regularisation parameters should be interpreted.  

Thank you for the opportunity for us to provide more methodical details.

First, for the task design, we included the following statements:

From Methods:

“HCP-A collected fMRI data from three tasks: Face Name (Sperling et al., 2001), Conditioned Approach Response Inhibition Task (CARIT) (Somerville et al., 2018) and VISual MOTOR (VISMOTOR) (Ances et al., 2009). 

First, the Face Name task (Sperling et al., 2001) taps into episodic memory. The task had three blocks. In the encoding block [Encoding], participants were asked to memorise the names of faces shown. These faces were then shown again in the recall block [Recall] when the participants were asked if they could remember the names of the previously shown faces. There was also the distractor block [Distractor] occurring between the encoding and recall blocks. Here participants were distracted by a Go/NoGo task. We computed six contrasts for this Face Name task: [Encode], [Recall], [Distractor], [Encode vs. Distractor], [Recall vs. Distractor] and [Encode vs. Recall].

Second, the CARIT task (Somerville et al., 2018) was adapted from the classic Go/NoGo task and taps into inhibitory control. Participants were asked to press a budon to all [Go] but not to two [NoGo] shapes. We computed three contrasts for the CARIT task: [NoGo], [Go] and [NoGo vs. Go]. 

Third, the VISMOTOR task (Ances et al., 2009) was designed to test simple activation of the motor and visual cortices. Participants saw a checkerboard with a red square either on the lec or right. They needed to press a corresponding key to indicate the location of the red square. We computed just one contrast for the VISMOTOR task: [Vismotor], which indicates the presence of the checkerboard vs. baseline.” 

Second, for MRI processing procedures, we included the following statements.

From Methods:

“HCP-A provides details of parameters for brain MRI elsewhere (Bookheimer et al., 2019; Harms et al., 2018). Here we used MRI data that were pre-processed by the HCP-A with recommended methods, including the MSMALL alignment (Glasser et al., 2016; Robinson et al., 2018) and ICA-FIX (Glasser et al., 2016) for functional MRI. We used multiple brain MRI modalities, covering task functional MRI (task fMRI), resting-state functional MRI (rsfMRI) and structural MRI (sMRI), and organised them into 19 sets of features.”

“Sets of Features 1-10: Task fMRI contrast (Task Contrast)

Task contrasts reflect fMRI activation relevant to events in each task. Bookheimer and colleagues (2019) provided detailed information about the fMRI in HCP-A. Here we focused on the pre-processed task fMRI Connectivity Informatics Technology Initiative (CIFTI) files with a suffix, “_PA_Atlas_MSMAll_hp0_clean.dtseries.nii.” These CIFTI files encompassed both the cortical mesh surface and subcortical volume (Glasser et al., 2013). Collected using the posterior-to-anterior (PA) phase, these files were aligned using MSMALL (Glasser et al., 2016; Robinson et al., 2018), linear detrended (see hdps://groups.google.com/a/humanconnectome.org/g/hcp-users/c/ZLJc092h980/m/GiihzQAUAwAJ) and cleaned from potential artifacts using ICA-FIX (Glasser et al., 2016). 

To extract Task Contrasts, we regressed the fMRI time series on the convolved task events using a double-gamma canonical hemodynamic response function via FMRIB Software Library (FSL)’s FMRI Expert Analysis Tool (FEAT) (Woolrich et al., 2001). We kept FSL’s default high pass cutoff at 200s (i.e., .005 Hz). We then parcellated the contrast ‘cope’ files, using the Glasser atlas (Gordon et al., 2016) for cortical surface regions and the Freesurfer’s automatic segmentation (aseg) (Fischl et al., 2002) for subcortical regions. This resulted in 379 regions, whose number was, in turn, the number of features for each Task Contrast set of features. “ 

“Sets of Features 11-13: Task fMRI functional connectivity (Task FC)

Task FC reflects functional connectivity (FC ) among the brain regions during each task, which is considered an important source of individual differences (Elliod et al., 2019; Fair et al., 2007; Gradon et al., 2018). We used the same CIFTI file “_PA_Atlas_MSMAll_hp0_clean.dtseries.nii.” as the task contrasts. Unlike Task Contrasts, here we treated the double-gamma, convolved task events as regressors of no interest and focused on the residuals of the regression from each task (Fair et al., 2007). We computed these regressors on FSL, and regressed them in nilearn (Abraham et al., 2014). Following previous work on task FC (Elliod et al., 2019), we applied a highpass at .008 Hz. For parcellation, we used the same atlases as Task Contrast (Fischl et al., 2002; Glasser et al., 2016). We computed Pearson’s correlations of each pair of 379 regions, resulting in a table of 71,631 non-overlapping FC indices for each task. We then applied r-to-z transformation and principal component analysis (PCA) of 75 components (Rasero et al., 2021; Sripada et al., 2019, 2020). Note to avoid data leakage, we conducted the PCA on each training set and applied its definition to the corresponding test set. Accordingly, there were three sets of 75 features for Task FC, one for each task. 

Set of Features 14: Resting-state functional MRI functional connectivity (Rest FC) Similar to Task FC, Rest FC reflects functional connectivity (FC ) among the brain regions, except that Rest FC occurred during the resting (as opposed to task-performing) period. HCPA collected Rest FC from four 6.42-min (488 frames) runs across two days, leading to 26-min long data (Harms et al., 2018). On each day, the study scanned two runs of Rest FC, starting with anterior-to-posterior (AP) and then with posterior-to-anterior (PA) phase encoding polarity. We used the “rfMRI_REST_Atlas_MSMAll_hp0_clean.dscalar.nii” file that was preprocessed and concatenated across the four runs.  We applied the same computations (i.e., highpass filter, parcellation, Pearson’s correlations, r-to-z transformation and PCA) with the Task FC. 

Sets of Features 15-18: Structural MRI (sMRI)

sMRI reflects individual differences in brain anatomy. The HCP-A used an established preprocessing pipeline for sMRI (Glasser et al., 2013). We focused on four sets of features: cortical thickness, cortical surface area, subcortical volume and total brain volume. For cortical thickness and cortical surface area, we used Destrieux’s atlas (Destrieux et al., 2010; Fischl, 2012) from FreeSurfer’s “aparc.stats” file, resulting in 148 regions for each set of features. For subcortical volume, we used the aseg atlas (Fischl et al., 2002) from FreeSurfer’s “aseg.stats” file, resulting in 19 regions. For total brain volume, we had five FreeSurfer-based features: “FS_IntraCranial_Vol” or estimated intra-cranial volume, “FS_TotCort_GM_Vol” or total cortical grey mader volume, “FS_Tot_WM_Vol” or total cortical white mader volume, “FS_SubCort_GM_Vol” or total subcortical grey mader volume and “FS_BrainSegVol_eTIV_Ratio” or ratio of brain segmentation volume to estimated total intracranial volume.”

Third, for regression methods and bias correction methods used, we included the following statements:

From Methods:

“For the machine learning algorithm, we used Elastic Net (Zou & Hastie, 2005). Elastic Net is a general form of penalised regressions (including Lasso and Ridge regression), allowing us to simultaneously draw information across different brain indices to predict one target variable. Penalised regressions are commonly used for building age-prediction models (Jirsaraie, Gorelik, et al., 2023). Previously we showed that the performance of Elastic Net in predicting cognitive abilities is on par, if not better than, many non-linear and morecomplicated algorithms (Pat, Wang, Bartonicek, et al., 2022; Tetereva et al., 2022). Moreover, Elastic Net coefficients are readily explainable, allowing us the ability to explain how our age-prediction and cognition-prediction models made the prediction from each brain feature (Molnar, 2019; Pat, Wang, Bartonicek, et al., 2022) (see below). 

Elastic Net simultaneously minimises the weighted sum of the features’ coefficients. The degree of penalty to the sum of the feature’s coefficients is determined by a shrinkage hyperparameter ‘a’: the greater the a, the more the coefficients shrink, and the more regularised the model becomes. Elastic Net also includes another hyperparameter, ‘ℓ! ratio’, which determines the degree to which the sum of either the squared (known as ‘Ridge’; ℓ! ratio=0) or absolute (known as ‘Lasso’; ℓ! ratio=1) coefficients is penalised (Zou & Hastie, 2005). The objective function of Elastic Net as implemented by sklearn (Pedregosa et al., 2011) is defined as:

where X is the features, y is the target, and b is the coefficient. In our grid search, we tuned two Elastic Net hyperparameters: a using 70 numbers in log space, ranging from .1 and 100, and ℓ!-ratio using 25 numbers in linear space, ranging from 0 and 1.

To understand how Elastic Net made a prediction based on different brain features, we examined the coefficients of the tuned model. Elastic Net coefficients can be considered as feature importance, such that more positive Elastic Net coefficients lead to more positive predicted values and, similarly, more negative Elastic Net coefficients lead to more negative predicted values (Molnar, 2019; Pat, Wang, Bartonicek, et al., 2022). While the magnitude of Elastic Net coefficients is regularised (thus making it difficult for us to interpret the magnitude itself directly), we could still indicate that a brain feature with a higher magnitude weights relatively stronger in making a prediction. Another benefit of Elastic Net as a penalised regression is that the coefficients are less susceptible to collinearity among features as they have already been regularised (Dormann et al., 2013; Pat, Wang, Bartonicek, et al., 2022).

Given that we used five-fold nested cross validation, different outer folds may have different degrees of ‘a’ and ‘ℓ! ratio’, making the final coefficients from different folds to be different. For instance, for certain sets of features, penalisation may not play a big part (i.e., higher or lower ‘a’ leads to similar predictive performance), resulting in different ‘a’ for different folds. To remedy this in the visualisation of Elastic Net feature importance, we refitted the Elastic Net model to the full dataset without spli{ng them into five folds and visualised the coefficients on brain images using Brainspace (Vos De Wael et al., 2020) and Nilern (Abraham et al., 2014) packages. Note, unlike other sets of features, Task FC and Rest FC were modelled acer data reduction via PCA. Thus, for Task FC and Rest FC, we, first, multiplied the absolute PCA scores (extracted from the ‘components_’ attribute of ‘sklearn.decomposition.PCA’) with Elastic Net coefficients and, then, summed the multiplied values across the 75 components, leaving 71,631 ROI-pair indices. “

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Author response:

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

eLife Assessment

This neuroimaging and electrophysiology study in a small cohort of congenital cataract patients with sight recovery aims to characterize the effects of early visual deprivation on excitatory and inhibitory balance in visual cortex. While contrasting sight-recovery with visually intact controls suggested the existence of persistent alterations in Glx/GABA ratio and aperiodic EEG signals, it provided only incomplete evidence supporting claims about the effects of early deprivation itself. The reported data were considered valuable, given the rare study population. However, the small sample sizes, lack of a specific control cohort and multiple methodological limitations will likely restrict usefulness to scientists working in this particular subfield.

We thank the reviewing editors for their consideration and updated assessment of our manuscript after its first revision.

In order to assess the effects of early deprivation, we included an age-matched, normally sighted control group recruited from the same community, measured in the same scanner and laboratory. This study design is analogous to numerous studies in permanently congenitally blind humans, which typically recruited sighted controls, but hardly ever individuals with a different, e.g. late blindness history. In order to improve the specificity of our conclusions, we used a frontal cortex voxel in addition to a visual cortex voxel (MRS). Analogously, we separately analyzed occipital and frontal electrodes (EEG).

Moreover, we relate our findings in congenital cataract reversal individuals to findings in the literature on permanent congenital blindness. Note, there are, to the best of our knowledge, neither MRS nor resting-state EEG studies in individuals with permanent late blindness.

Our participants necessarily have nystagmus and low visual acuity due to their congenital deprivation phase, and the existence of nystagmus is a recruitment criterion to diagnose congenital cataracts.

It might be interesting for future studies to investigate individuals with transient late blindness. However, such a study would be ill-motivated had we not found differences between the most “extreme” of congenital visual deprivation conditions and normally sighted individuals (analogous to why earlier research on permanent blindness investigated permanent congenitally blind humans first, rather than permanently late blind humans, or both in the same study). Any result of these future work would need the reference to our study, and neither results in these additional groups would invalidate our findings.

Since all our congenital cataract reversal individuals by definition had visual impairments, we included an eyes closed condition, both in the MRS and EEG assessment. Any group effect during the eyes closed condition cannot be due to visual acuity deficits changing the bottom-up driven visual activation.

As we detail in response to review 3, our EEG analyses followed the standards in the field.

Public Reviews:

Reviewer #1 (Public review):

Summary

In this human neuroimaging and electrophysiology study, the authors aimed to characterise effects of a period of visual deprivation in the sensitive period on excitatory and inhibitory balance in the visual cortex. They attempted to do so by comparing neurochemistry conditions ('eyes open', 'eyes closed') and resting state, and visually evoked EEG activity between ten congenital cataract patients with recovered sight (CC), and ten age-matched control participants (SC) with normal sight.

First, they used magnetic resonance spectroscopy to measure in vivo neurochemistry from two locations, the primary location of interest in the visual cortex, and a control location in the frontal cortex. Such voxels are used to provide a control for the spatial specificity of any effects, because the single-voxel MRS method provides a single sampling location. Using MR-visible proxies of excitatory and inhibitory neurotransmission, Glx and GABA+ respectively, the authors report no group effects in GABA+ or Glx, no difference in the functional conditions 'eyes closed' and 'eyes open'. They found an effect of group in the ratio of Glx/GABA+ and no similar effect in the control voxel location. They then perform multiple exploratory correlations between MRS measures and visual acuity, and report a weak positive correlation between the 'eyes open' condition and visual acuity in CC participants.

The same participants then took part in an EEG experiment. The authors selected two electrodes placed in the visual cortex for analysis and report a group difference in an EEG index of neural activity, the aperiodic intercept, as well as the aperiodic slope, considered a proxy for cortical inhibition. Control electrodes in the frontal region did not present with the same pattern. They report an exploratory correlation between the aperiodic intercept and Glx in one out of three EEG conditions.

The authors report the difference in E/I ratio, and interpret the lower E/I ratio as representing an adaptation to visual deprivation, which would have initially caused a higher E/I ratio. Although intriguing, the strength of evidence in support of this view is not strong. Amongst the limitations are the low sample size, a critical control cohort that could provide evidence for higher E/I ratio in CC patients without recovered sight for example, and lower data quality in the control voxel. Nevertheless, the study provides a rare and valuable insight into experience-dependent plasticity in the human brain.

Strengths of study

How sensitive period experience shapes the developing brain is an enduring and important question in neuroscience. This question has been particularly difficult to investigate in humans. The authors recruited a small number of sight-recovered participants with bilateral congenital cataracts to investigate the effect of sensitive period deprivation on the balance of excitation and inhibition in the visual brain using measures of brain chemistry and brain electrophysiology. The research is novel, and the paper was interesting and well written.

Limitations

Low sample size. Ten for CC and ten for SC, and further two SC participants were rejected due to lack of frontal control voxel data. The sample size limits the statistical power of the dataset and increases the likelihood of effect inflation.

In the updated manuscript, the authors have provided justification for their sample size by pointing to prior studies and the inherent difficulties in recruiting individuals with bilateral congenital cataracts. Importantly, this highlights the value the study brings to the field while also acknowledging the need to replicate the effects in a larger cohort.

Lack of specific control cohort. The control cohort has normal vision. The control cohort is not specific enough to distinguish between people with sight loss due to different causes and patients with congenital cataracts with co-morbidities. Further data from a more specific populations, such as patients whose cataracts have not been removed, with developmental cataracts, or congenitally blind participants, would greatly improve the interpretability of the main finding. The lack of a more specific control cohort is a major caveat that limits a conclusive interpretation of the results.

In the updated version, the authors have indicated that future studies can pursue comparisons between congenital cataract participants and cohorts with later sight loss.

MRS data quality differences. Data quality in the control voxel appears worse than in the visual cortex voxel. The frontal cortex MRS spectrum shows far broader linewidth than the visual cortex (Supplementary Figures). Compared to the visual voxel, the frontal cortex voxel has less defined Glx and GABA+ peaks; lower GABA+ and Glx concentrations, lower NAA SNR values; lower NAA concentrations. If the data quality is a lot worse in the FC, then small effects may not be detectable.

In the updated version, the authors have added more information that informs the reader of the MRS quality differences between voxel locations. This increases the transparency of their reporting and enhances the assessment of the results.

Because of the direction of the difference in E/I, the authors interpret their findings as representing signatures of sight improvement after surgery without further evidence, either within the study or from the literature. However, the literature suggests that plasticity and visual deprivation drives the E/I index up rather than down. Decreasing GABA+ is thought to facilitate experience dependent remodelling. What evidence is there that cortical inhibition increases in response to a visual cortex that is over-sensitised to due congenital cataracts? Without further experimental or literature support this interpretation remains very speculative.

The updated manuscript contains key reference from non-human work to justify their interpretation.

Heterogeneity in patient group. Congenital cataract (CC) patients experienced a variety of duration of visual impairment and were of different ages. They presented with co-morbidities (absorbed lens, strabismus, nystagmus). Strabismus has been associated with abnormalities in GABAergic inhibition in the visual cortex. The possible interactions with residual vision and confounds of co-morbidities are not experimentally controlled for in the correlations, and not discussed.

The updated document has addressed this caveat.

Multiple exploratory correlations were performed to relate MRS measures to visual acuity (shown in Supplementary Materials), and only specific ones shown in the main document. The authors describe the analysis as exploratory in the 'Methods' section. Furthermore, the correlation between visual acuity and E/I metric is weak, not corrected for multiple comparisons. The results should be presented as preliminary, as no strong conclusions can be made from them. They can provide a hypothesis to test in a future study.

This has now been done throughout the document and increases the transparency of the reporting.

P.16 Given the correlation of the aperiodic intercept with age ("Age negatively correlated with the aperiodic intercept across CC and SC individuals, that is, a flattening of the intercept was observed with age"), age needs to be controlled for in the correlation between neurochemistry and the aperiodic intercept. Glx has also been shown to negatively correlates with age.

This caveat has been addressed in the revised manuscript.

Multiple exploratory correlations were performed to relate MRS to EEG measures (shown in Supplementary Materials), and only specific ones shown in the main document. Given the multiple measures from the MRS, the correlations with the EEG measures were exploratory, as stated in the text, p.16, and in Fig.4. yet the introduction said that there was a prior hypothesis "We further hypothesized that neurotransmitter changes would relate to changes in the slope and intercept of the EEG aperiodic activity in the same subjects." It would be great if the text could be revised for consistency and the analysis described as exploratory.

This has been done throughout the document and increases the transparency of the reporting.

The analysis for the EEG needs to take more advantage of the available data. As far as I understand, only two electrodes were used, yet far more were available as seen in their previous study (Ossandon et al., 2023). The spatial specificity is not established. The authors could use the frontal cortex electrode (FP1, FP2) signals as a control for spatial specificity in the group effects, or even better, all available electrodes and correct for multiple comparisons. Furthermore, they could use the aperiodic intercept vs Glx in SC to evaluate the specificity of the correlation to CC.

This caveat has been addressed. The authors have added frontal electrodes to their analysis, providing an essential regional control for the visual cortex location.

Comments on the latest version:

The authors have made reasonable adjustments to their manuscript that addressed most of my comments by adding further justification for their methodology, essential literature support, pointing out exploratory analyses, limitations and adding key control analyses. Their revised manuscript has overall improved, providing valuable information, though the evidence that supports their claims is still incomplete.

We thank the reviewer for suggesting ways to improve our manuscript and carefully reassessing our revised manuscript.

Reviewer #2 (Public review):

Summary:

The study examined 10 congenitally blind patients who recovered vision through the surgical removal of bilateral dense cataracts, measuring neural activity and neuro chemical profiles from the visual cortex. The declared aim is to test whether restoring visual function after years of complete blindness impacts excitation/inhibition balance in the visual cortex.

Strengths:

The findings are undoubtedly useful for the community, as they contribute towards characterising the many ways in which this special population differs from normally sighted individuals. The combination of MRS and EEG measures is a promising strategy to estimate a fundamental physiological parameter - the balance between excitation and inhibition in the visual cortex, which animal studies show to be heavily dependent upon early visual experience. Thus, the reported results pave the way for further studies, which may use a similar approach to evaluate more patients and control groups.

Weaknesses:

The main methodological limitation is the lack of an appropriate comparison group or condition to delineate the effect of sight recovery (as opposed to the effect of congenital blindness). Few previous studies suggested that Excitation/Inhibition ratio in the visual cortex is increased in congenitally blind patients; the present study reports that E/I ratio decreases instead. The authors claim that this implies a change of E/I ratio following sight recovery. However, supporting this claim would require showing a shift of E/I after vs. before the sight-recovery surgery, or at least it would require comparing patients who did and did not undergo the sight-recovery surgery (as common in the field).

We thank the reviewer for suggesting ways to improve our manuscript and carefully reassessing our revised manuscript.

Since we have not been able to acquire longitudinal data with the experimental design of the present study in congenital cataract reversal individuals, we compared the MRS and EEG results of congenital cataract reversal individuals  to published work in congenitally permanent blind individuals. We consider this as a resource saving approach. We think that the results of our cross-sectional study now justify the costs and enormous efforts (and time for the patients who often have to travel long distances) associated with longitudinal studies in this rare population.

There are also more technical limitations related to the correlation analyses, which are partly acknowledged in the manuscript. A bland correlation between GLX/GABA and the visual impairment is reported, but this is specific to the patients group (N=10) and would not hold across groups (the correlation is positive, predicting the lowest GLX/GABA ratio values for the sighted controls - opposite of what is found). There is also a strong correlation between GLX concentrations and the EEG power at the lowest temporal frequencies. Although this relation is intriguing, it only holds for a very specific combination of parameters (of the many tested): only with eyes open, only in the patients group.

Given the exploratory nature of the correlations, we do not base the majority of our conclusions on this analysis. There are no doubts that the reported correlations need replication; however, replication is only possible after a first report. Thus, we hope to motivate corresponding analyses in further studies.

It has to be noted that in the present study significance testing for correlations were corrected for multiple comparisons, and that some findings replicate earlier reports (e.g. effects on EEG aperiodic slope, alpha power, and correlations with chronological age).

Conclusions:

The main claim of the study is that sight recovery impacts the excitation/inhibition balance in the visual cortex, estimated with MRS or through indirect EEG indices. However, due to the weaknesses outlined above, the study cannot distinguish the effects of sight recovery from those of visual deprivation. Moreover, many aspects of the results are interesting but their validation and interpretation require additional experimental work.

We interpret the group differences between individuals tested years after congenital visual deprivation and normally sighted individuals as supportive of the E/I ratio being impacted by congenital visual deprivation. In the absence of a sensitive period for the development of an E/I ratio, individuals with a transient phase of congenital blindness might have developed a visual system indistinguishable  from normally sighted individuals. As we demonstrate, this is not so. Comparing the results of congenitally blind humans with those of congenitally permanently blind humans (from previous studies) allowed us to identify changes of E/I ratio, which add to those found for congenital blindness.  

We thank the reviewer for the helpful comments and suggestions related to the first submission and first revision of our manuscript. We are keen to translate some of them into future studies.

Reviewer #3 (Public review):

This manuscript examines the impact of congenital visual deprivation on the excitatory/inhibitory (E/I) ratio in the visual cortex using Magnetic Resonance Spectroscopy (MRS) and electroencephalography (EEG) in individuals whose sight was restored. Ten individuals with reversed congenital cataracts were compared to age-matched, normally sighted controls, assessing the cortical E/I balance and its interrelationship and to visual acuity. The study reveals that the Glx/GABA ratio in the visual cortex and the intercept and aperiodic signal are significantly altered in those with a history of early visual deprivation, suggesting persistent neurophysiological changes despite visual restoration.

First of all, I would like to disclose that I am not an expert in congenital visual deprivation, nor in MRS. My expertise is in EEG (particularly in the decomposition of periodic and aperiodic activity) and statistical methods.

Although the authors addressed some of the concerns of the previous version, major concerns and flaws remain in terms of methodological and statistical approaches along with the (over)interpretation of the results. Specific concerns include:

(1 3.1) Response to Variability in Visual Deprivation<br /> Rather than listing the advantages and disadvantages of visual deprivation, I recommend providing at least a descriptive analysis of how the duration of visual deprivation influenced the measures of interest. This would enhance the depth and relevance of the discussion.

Although Review 2 and Review 3 (see below) pointed out problems in interpreting multiple correlational analyses in small samples, we addressed this request by reporting such correlations between visual deprivation history and measured EEG/MRS outcomes.

Calculating the correlation between duration of visual deprivation and behavioral or brain measures is, in fact, a common suggestion. The existence of sensitive periods, which are typically assumed to not follow a linear gradual decline of neuroplasticity, does not necessary allow predicting a correlation with duration of blindness. Daphne Maurer has additionally worked on the concept of “sleeper effects” (Maurer et al., 2007), that is, effects on the brain and behavior by early deprivation which are observed only later in life when the function/neural circuits matures.

In accordance with this reasoning, we did not observe a significant correlation between duration of visual deprivation and any of our dependent variables.

(2 3.2) Small Sample Size<br /> The issue of small sample size remains problematic. The justification that previous studies employed similar sample sizes does not adequately address the limitation in the current study. I strongly suggest that the correlation analyses should not feature prominently in the main manuscript or the abstract, especially if the discussion does not substantially rely on these correlations. Please also revisit the recommendations made in the section on statistical concerns.

In the revised manuscript, we explicitly mention that our sample size is not atypical for the special group investigated, but that a replication of our results in larger samples would foster their impact. We only explicitly mention correlations that survived stringent testing for multiple comparisons in the main manuscript.

Given the exploratory nature of the correlations, we have not based the majority of our claims on this analysis.

(3 3.3) Statistical Concerns<br /> While I appreciate the effort of conducting an independent statistical check, it merely validates whether the reported statistical parameters, degrees of freedom (df), and p-values are consistent. However, this does not address the appropriateness of the chosen statistical methods.

We did not intend for the statcheck report to justify the methods used for statistics, which we have done in a separate section with normality and homogeneity testing (Supplementary Material S9), and references to it in the descriptions of the statistical analyses (Methods, Page 13, Lines 326-329 and Page 15, Lines 400-402).

Several points require clarification or improvement:<br /> (4) Correlation Methods: The manuscript does not specify whether the reported correlation analyses are based on Pearson or Spearman correlation.

The depicted correlations are Pearson correlations. We will add this information to the Methods.

(5) Confidence Intervals: Include confidence intervals for correlations to represent the uncertainty associated with these estimates.

We have added the confidence intervals for all measured correlations to the second revision of our manuscript.

(6) Permutation Statistics: Given the small sample size, I recommend using permutation statistics, as these are exact tests and more appropriate for small datasets.

Our study focuses on a rare population, with a sample size limited by the availability of participants. Our findings provide exploratory insights rather than make strong inferential claims. To this end, we have ensured that our analysis adheres to key statistical assumptions (Shapiro-Wilk as well as Levene’s tests, Supplementary Material S9), and reported our findings with effect sizes, appropriate caution and context.

(7) Adjusted P-Values: Ensure that reported Bonferroni corrected p-values (e.g., p > 0.999) are clearly labeled as adjusted p-values where applicable.

In the revised manuscript, we have changed Figure 4 to say ‘adjusted p,’  which we indeed reported.

(8) Figure 2C

Figure 2C still lacks crucial information that the correlation between Glx/GABA ratio and visual acuity was computed solely in the control group (as described in the rebuttal letter). Why was this analysis restricted to the control group? Please provide a rationale.

Figure 2C depicts the correlation between Glx/GABA+ ratio and visual acuity in the congenital cataract reversal group, not the control group. This is mentioned in the Figure 2 legend, as well as in the main text where the figure is referred to (Page 18, Line 475).

The correlation analyses between visual acuity and MRS/EEG measures were only performed in the congenital cataract reversal group since the sighed control group comprised of individuals with vision in the normal range; thus this analyses would not make sense. Table 1 with the individual visual acuities for all participants, including the normally sighted controls, shows the low variance in the latter group.  

For variables in which no apiori group differences in variance were predicted, we performed the correlation analyses across groups (see Supplementary Material S12, S15).

We have now highlighted these motivations more clearly in the Methods of the revised manuscript (Page 16, Lines 405-410).

(9 3.4) Interpretation of Aperiodic Signal

Relying on previous studies to interpret the aperiodic slope as a proxy for excitation/inhibition (E/I) does not make the interpretation more robust.

How to interpret aperiodic EEG activity has been subject of extensive investigation. We cite studies which provide evidence from multiple species (monkeys, humans) and measurements (EEG, MEG, ECoG), including studies which pharmacologically manipulated E/I balance.

Whether our findings are robust, in fact, requires a replication study. Importantly, we analyzed the intercept of the aperiodic activity fit as well, and discuss results related to the intercept.

Quote:

“(3.4) Interpretation of aperiodic signal:

- Several recent papers demonstrated that the aperiodic signal measured in EEG or ECoG is related to various important aspects such as age, skull thickness, electrode impedance, as well as cognition. Thus, currently, very little is known about the underlying effects which influence the aperiodic intercept and slope. The entire interpretation of the aperiodic slope as a proxy for E/I is based on a computational model and simulation (as described in the Gao et al. paper).

Apart from the modeling work from Gao et al., multiple papers which have also been cited which used ECoG, EEG and MEG and showed concomitant changes in aperiodic activity with pharmacological manipulation of the E/I ratio (Colombo et al., 2019; Molina et al., 2020; Muthukumaraswamy & Liley, 2018). Further, several prior studies have interpreted changes in the aperiodic slope as reflective of changes in the E/I ratio, including studies of developmental groups (Favaro et al., 2023; Hill et al., 2022; McSweeney et al., 2023; Schaworonkow & Voytek, 2021) as well as patient groups (Molina et al., 2020; Ostlund et al., 2021).

- The authors further wrote: We used the slope of the aperiodic (1/f) component of the EEG spectrum as an estimate of E/I ratio (Gao et al., 2017; Medel et al., 2020; Muthukumaraswamy & Liley, 2018). This is a highly speculative interpretation with very little empirical evidence. These papers were conducted with ECoG data (mostly in animals) and mostly under anesthesia. Thus, these studies only allow an indirect interpretation by what the 1/f slope in EEG measurements is actually influenced.

Note that Muthukumaraswamy et al. (2018) used different types of pharmacological manipulations and analyzed periodic and aperiodic MEG activity in humans, in addition to monkey ECoG (Muthukumaraswamy & Liley, 2018). Further, Medel et al. (now published as Medel et al., 2023) compared EEG activity in addition to ECoG data after propofol administration. The interpretation of our results are in line with a number of recent studies in developing (Hill et al., 2022; Schaworonkow & Voytek, 2021) and special populations using EEG. As mentioned above, several prior studies have used the slope of the 1/f component/aperiodic activity as an indirect measure of the E/I ratio (Favaro et al., 2023; Hill et al., 2022; McSweeney et al., 2023; Molina et al., 2020; Ostlund et al., 2021; Schaworonkow & Voytek, 2021), including studies using scalp-recorded EEG from humans.

In the introduction of the revised manuscript, we have made more explicit that this metric is indirect (Page 3, Line 91), (additionally see Discussion, Page 24, Lines 644-645, Page 25, Lines 650-657).

While a full understanding of aperiodic activity needs to be provided, some convergent ideas have emerged. We think that our results contribute to this enterprise, since our study is, to the best of our knowledge, the first which assessed MRS measured neurotransmitter levels and EEG aperiodic activity. “

(10) Additionally, the authors state:

"We cannot think of how any of the exploratory correlations between neurophysiological measures and MRS measures could be accounted for by a difference e.g. in skull thickness."

(11) This could be addressed directly by including skull thickness as a covariate or visualizing it in scatterplots, for instance, by representing skull thickness as the size of the dots.

We are not aware of any study that would justify such an analysis.

Our analyses were based on previous findings in the literature.

Since to the best of our knowledge, no evidence exists that congenital cataracts go together with changes in skull thickness, and that skull thickness might selectively modulate visual cortex Glx/GABA+ but not NAA measures, we decided against following this suggestion.

Notably, the neurotransmitter concentration reported here is after tissue segmentation of the voxel region. The tissue fraction was shown to not differ between groups in the MRS voxels (Supplementary Material S4). The EEG electrode impedance was lowered to <10 kOhm in every participant (Methods, Page 13, Line 344), and preparation was identical across groups.

(12 3.5) Problems with EEG Preprocessing and Analysis

Downsampling: The decision to downsample the data to 60 Hz "to match the stimulation rate" is problematic. This choice conflates subsequent spectral analyses due to aliasing issues, as explained by the Nyquist theorem. While the authors cite prior studies (Schwenk et al., 2020; VanRullen & MacDonald, 2012) to justify this decision, these studies focused on alpha (8-12 Hz), where aliasing is less of a concern compared of analyzing aperiodic signal. Furthermore, in contrast, the current study analyzes the frequency range from 1-20 Hz, which is too narrow for interpreting the aperiodic signal as E/I. Typically, this analysis should include higher frequencies, spanning at least 1-30 Hz or even 1-45 Hz (not 20-40 Hz).

As previously mentied in the Methods (Page 15 Line 376) and the previous response, the pop_resample function used by EEGLAB applies an anti-aliasing filter, at half the resampling frequency (as per the Nyquist theorem

https://eeglab.org/tutorials/05_Preprocess/resampling.html). The upper cut off of the low pass filter set by EEGlab prior to down sampling (30 Hz) is still far above the frequency of interest in the current study  (1-20 Hz), thus allowing us to derive valid results.

Quote:

“- The authors downsampled the data to 60Hz to "to match the stimulation rate". What is the intention of this? Because the subsequent spectral analyses are conflated by this choice (see Nyquist theorem).

This data were collected as part of a study designed to evoke alpha activity with visual white-noise, which ranged in luminance with equal power at all frequencies from 1-60 Hz, restricted by the refresh rate of the monitor on which stimuli were presented (Pant et al., 2023). This paradigm and method was developed by VanRullen and colleagues (Schwenk et al., 2020; Vanrullen & MacDonald, 2012), wherein the analysis requires the same sampling rate between the presented frequencies and the EEG data. The downsampling function used here automatically applies an anti-aliasing filter (EEGLAB 2019) .”

Moreover, the resting-state data were not resampled to 60 Hz. We have made this clearer in the Methods of the second revision (Page 15, Line 367).

Our consistent results of group differences across all three EEG conditions, thus, exclude any possibility that they were driven by aliasing artifacts.

The expected effects of this anti-aliasing filter can be seen in the attached Author response image 1, showing an example participant’s spectrum in the 1-30 Hz range (as opposed to the 1-20 Hz plotted in the manuscript), clearly showing a 30-40 dB drop at 30 Hz. Any aliasing due to, for example, remaining line noise, would additionally be visible in this figure (as well as Figure 3) as a peak.

Author response image 1.

Power spectral density of one congenital cataract-reversal (CC) participant in the visual stimulation condition across all channels. The reduced power at 30 Hz shows the effects of the anti-aliasing filter applied by EEGLAB’s pop_resample function.

As we stated in the manuscript, and in previous reviews, so far there has been no consensus on the exact range of measuring aperiodic activity. We made a principled decision based on the literature (showing a knee in aperiodic fits of this dataset at 20 Hz) (Medel et al., 2023; Ossandón et al., 2023), data quality (possible contamination by line noise at higher frequencies) and the purpose of the visual stimulation experiment (to look at the lower frequency range by stimulating up to 60 Hz, thereby limiting us to quantifying below 30 Hz), that 1-20 Hz would be the fit range in this dataset.

Quote:

“(3) What's the underlying idea of analyzing two separate aperiodic slopes (20-40Hz and 1-19Hz). This is very unusual to compute the slope between 20-40 Hz, where the SNR is rather low.

"Ossandón et al. (2023), however, observed that in addition to the flatter slope of the aperiodic power spectrum in the high frequency range (20-40 Hz), the slope of the low frequency range (1-19 Hz) was steeper in both, congenital cataract-reversal individuals, as well as in permanently congenitally blind humans."

The present manuscript computed the slope between 1-20 Hz. Ossandón et al. as well as Medel et al. (2023) found a “knee” of the 1/f distribution at 20 Hz and describe further the motivations for computing both slope ranges. For example, Ossandón et al. used a data driven approach and compared single vs. dual fits and found that the latter fitted the data better. Additionally, they found the best fit if a knee at 20 Hz was used. We would like to point out that no standard range exists for the fitting of the 1/f component across the literature and, in fact, very different ranges have been used (Gao et al., 2017; Medel et al., 2023; Muthukumaraswamy & Liley, 2018). “

(13) Baseline Removal: Subtracting the mean activity across an epoch as a baseline removal step is inappropriate for resting-state EEG data. This preprocessing step undermines the validity of the analysis. The EEG dataset has fundamental flaws, many of which were pointed out in the previous review round but remain unaddressed. In its current form, the manuscript falls short of standards for robust EEG analysis. If I were reviewing for another journal, I would recommend rejection based on these flaws.

The baseline removal step from each epoch serves to remove the DC component of the recording and detrend the data. This is a standard preprocessing step (included as an option in preprocessing pipelines recommended by the EEGLAB toolbox, FieldTrip toolbox and MNE toolbox), additionally necessary to improve the efficacy of ICA decomposition (Groppe et al., 2009).

In the previous review round, a clarification of the baseline timing was requested, which we added. Beyond this request, there was no mention of the appropriateness of the baseline removal and/or a request to provide reasons for why it might not undermine the validity of the analysis.

Quote:

“- "Subsequently, baseline removal was conducted by subtracting the mean activity across the length of an epoch from every data point." The actual baseline time segment should be specified.

The time segment was the length of the epoch, that is, 1 second for the resting state conditions and 6.25 seconds for the visual stimulation conditions. This has been explicitly stated in the revised manuscript (Page 13, Line 354).”

Prior work in the time (not frequency) domain on event-related potential (ERP) analysis has suggested that the baselining step might cause spurious effects (Delorme, 2023) (although see (Tanner et al., 2016)). We did not perform ERP analysis at any stage. One recent study suggests spurious group differences in the 1/f signal might be driven by an inappropriate dB division baselining method (Gyurkovics et al., 2021), which we did not perform.

Any effect of our baselining procedure on the FFT spectrum would be below the 1 Hz range, which we did not analyze.  

Each of the preprocessing steps in the manuscript match pipelines described and published in extensive prior work. We document how multiple aspects of our EEG results replicate prior findings (Supplementary Material S15, S18, S19), reports of other experimenters, groups and locations, validating that our results are robust.

We therefore reject the claim of methodological flaws in our EEG analyses in the strongest possible terms.

Quote:

“(3.5) Problems with EEG preprocessing and analysis:

- It seems that the authors did not identify bad channels nor address the line noise issue (even a problem if a low pass filter of below-the-line noise was applied).

As pointed out in the methods and Figure 1, we only analyzed data from two occipital channels, O1 and O2 neither of which were rejected for any participant. Channel rejection was performed for the larger dataset, published elsewhere (Ossandón et al., 2023; Pant et al., 2023). As control sites we added the frontal channels FP1 and Fp2 (see Supplementary Material S14)

Neither Ossandón et al. (2023) nor Pant et al. (2023) considered frequency ranges above 40 Hz to avoid any possible contamination with line noise. Here, we focused on activity between 0 and 20 Hz, definitely excluding line noise contaminations (Methods, Page 14, Lines 365-367). The low pass filter (FIR, 1-45 Hz) guaranteed that any spill-over effects of line noise would be restricted to frequencies just below the upper cutoff frequency.

Additionally, a prior version of the analysis used spectrum interpolation to remove line noise; the group differences remained stable (Ossandón et al., 2023). We have reported this analysis in the revised manuscript (Page 14, Lines 364-357).

Further, both groups were measured in the same lab, making line noise (~ 50 Hz) as an account for the observed group effects in the 1-20 Hz frequency range highly unlikely. Finally, any of the exploratory MRS-EEG correlations would be hard to explain if the EEG parameters would be contaminated with line noise.

- What was the percentage of segments that needed to be rejected due to the 120μV criteria? This should be reported specifically for EO & EC and controls and patients.

The mean percentage of 1 second segments rejected for each resting state condition and the percentage of 6.25 long segments rejected in each group for the visual stimulation condition have been added to the revised manuscript (Supplementary Material S10), and referred to in the Methods on Page 14, Lines 372-373).

- The authors downsampled the data to 60Hz to "to match the stimulation rate". What is the intention of this? Because the subsequent spectral analyses are conflated by this choice (see Nyquist theorem).

This data were collected as part of a study designed to evoke alpha activity with visual white-noise, which changed in luminance with equal power at all frequencies from 1-60 Hz, restricted by the refresh rate of the monitor on which stimuli were presented (Pant et al., 2023). This paradigm and method was developed by VanRullen and colleagues (Schwenk et al., 2020; VanRullen & MacDonald, 2012), wherein the analysis requires the same sampling rate between the presented frequencies and the EEG data. The downsampling function used here automatically applies an anti-aliasing filter (EEGLAB 2019) .

- "Subsequently, baseline removal was conducted by subtracting the mean activity across the length of an epoch from every data point." The actual baseline time segment should be specified.

The time segment was the length of the epoch, that is, 1 second for the resting state conditions and 6.25 seconds for the visual stimulation conditions. This has now been explicitly stated in the revised manuscript (Page 14, Lines 379-380).

- "We excluded the alpha range (8-14 Hz) for this fit to avoid biasing the results due to documented differences in alpha activity between CC and SC individuals (Bottari et al., 2016; Ossandón et al., 2023; Pant et al., 2023)." This does not really make sense, as the FOOOF algorithm first fits the 1/f slope, for which the alpha activity is not relevant.

We did not use the FOOOF algorithm/toolbox in this manuscript. As stated in the Methods, we used a 1/f fit to the 1-20 Hz spectrum in the log-log space, and subtracted this fit from the original spectrum to obtain the corrected spectrum. Given the pronounced difference in alpha power between groups (Bottari et al., 2016; Ossandón et al., 2023; Pant et al., 2023), we were concerned it might drive differences in the exponent values. Our analysis pipeline had been adapted from previous publications of our group and other labs (Ossandón et al., 2023; Voytek et al., 2015; Waschke et al., 2017).

We have conducted the analysis with and without the exclusion of the alpha range, as well as using the FOOOF toolbox both in the 1-20 Hz and 20-40 Hz ranges (Ossandón et al., 2023). The findings of a steeper slope in the 1-20 Hz range as well as lower alpha power in CC vs SC individuals remained stable. In Ossandón et al., the comparison between the piecewise fits and FOOOF fits led the authors to use the former, as it outperformed the FOOOF algorithm for their data.

- The model fits of the 1/f fitting for EO, EC, and both participant groups should be reported.

In Figure 3 of the manuscript, we depicted the mean spectra and 1/f fits for each group.

In the revised manuscript, we added the fit quality metrics (average R² values > 0.91 for each group and condition) (Methods Page 15, Lines 395-396; Supplementary Material S11) and additionally show individual subjects’ fits (Supplementary Material S11). “

(14) The authors mention:

"The EEG data sets reported here were part of data published earlier (Ossandón et al., 2023; Pant et al., 2023)." Thus, the statement "The group differences for the EEG assessments corresponded to those of a larger sample of CC individuals (n=38) " is a circular argument and should be avoided."

The authors addressed this comment and adjusted the statement. However, I do not understand, why not the full sample published earlier (Ossandón et al., 2023) was used in the current study?

The recording of EEG resting state data stated in 2013, while MRS testing could only be set up by the second half of 2019. Moreover, not all subjects who qualify for EEG recording qualify for being scanned (e.g. due to MRI safety, claustrophobia)

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Author response:

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

eLife assessment

This useful manuscript challenges the utility of current paradigms for estimating brain-age with magnetic resonance imaging measures, but presents inadequate evidence to support the suggestion that an alternative approach focused on predicting cognition is more useful. The paper would benefit from a clearer explication of the methods and a more critical evaluation of the conceptual basis of the different models. This work will be of interest to researchers working on brain-age and related models.

Thank you so much for providing high-quality reviews on our manuscript. We revised the manuscript to address all of the reviewers’ comments and provided full responses to each of the comments below. Importantly, in this revision, we clarified that we did not intend to use Brain Cognition as an alternative approach as mentioned by the editor. This is because, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Here we made this point more explicit and further stated that the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. By examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. And such quantification is the third aim of this study.

Reviewer #1 (Public Review):

In this paper, the authors evaluate the utility of brain age derived metrics for predicting cognitive decline by performing a 'commonality' analysis in a downstream regression that enables the different contribution of different predictors to be assessed. The main conclusion is that brain age derived metrics do not explain much additional variation in cognition over and above what is already explained by age. The authors propose to use a regression model trained to predict cognition ('brain cognition') as an alternative suited to applications of cognitive decline. While this is less accurate overall than brain age, it explains more unique variance in the downstream regression.

Importantly, in this revision, we clarified that we did not intend to use Brain Cognition as an alternative approach. This is because, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Here we made this point more explicit and further stated that the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. By examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age.

REVISED VERSION: while the authors have partially addressed my concerns, I do not feel they have addressed them all. I do not feel they have addressed the weight instability and concerns about the stacked regression models satisfactorily.

Please see our responses to #3 below

I also must say that I agree with Reviewer 3 about the limitations of the brain age and brain cognition methods conceptually. In particular that the regression model used to predict fluid cognition will by construction explain more variance in cognition than a brain age model that is trained to predict age. This suffers from the same problem the authors raise with brain age and would indeed disappear if the authors had a separate measure of cognition against which to validate and were then to regress this out as they do for age correction. I am aware that these conceptual problems are more widespread than this paper alone (in fact throughout the brain age literature), so I do not believe the authors should be penalised for that. However, I do think they can make these concerns more explicit and further tone down the comments they make about the utility of brain cognition. I have indicated the main considerations about these points in the recommendations section below.

Thank you so much for raising this point. We now have the following statement in the introduction and discussion to address this concern (see below).

Briefly, we made it explicit that, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. That is, the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. More importantly, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. And this is the third goal of this present study.

From Introduction:

“Third and finally, certain variation in fluid cognition is related to brain MRI, but to what extent does Brain Age not capture this variation? To estimate the variation in fluid cognition that is related to the brain MRI, we could build prediction models that directly predict fluid cognition (i.e., as opposed to chronological age) from brain MRI data. Previous studies found reasonable predictive performances of these cognition-prediction models, built from certain MRI modalities (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). Analogous to Brain Age, we called the predicted values from these cognition-prediction models, Brain Cognition. The strength of an out-of-sample relationship between Brain Cognition and fluid cognition reflects variation in fluid cognition that is related to the brain MRI and, therefore, indicates the upper limit of Brain Age’s capability in capturing fluid cognition. This is, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Consequently, if we included Brain Cognition, Brain Age and chronological age in the same model to explain fluid cognition, we would be able to examine the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age. These unique effects of Brain Cognition, in turn, would indicate the amount of co-variation between brain MRI and fluid cognition that is missed by Brain Age.”

From Discussion:

“Third, by introducing Brain Cognition, we showed the extent to which Brain Age indices were not able to capture the variation in fluid cognition that is related to brain MRI. More specifically, using Brain Cognition allowed us to gauge the variation in fluid cognition that is related to the brain MRI, and thereby, to estimate the upper limit of what Brain Age can do. Moreover, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age.

From our results, Brain Cognition, especially from certain cognition-prediction models such as the stacked models, has relatively good predictive performance, consistent with previous studies (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). We then examined Brain Cognition using commonality analyses (Nimon et al., 2008) in multiple regression models having a Brain Age index, chronological age and Brain Cognition as regressors to explain fluid cognition. Similar to Brain Age indices, Brain Cognition exhibited large common effects with chronological age. But more importantly, unlike Brain Age indices, Brain Cognition showed large unique effects, up to around 11%. As explained above, the unique effects of Brain Cognition indicated the amount of co-variation between brain MRI and fluid cognition that was missed by a Brain Age index and chronological age. This missing amount was relatively high, considering that Brain Age and chronological age together explained around 32% of the total variation in fluid cognition. Accordingly, if a Brain Age index was used as a biomarker along with chronological age, we would have missed an opportunity to improve the performance of the model by around one-third of the variation explained.”

This is a reasonably good paper and the use of a commonality analysis is a nice contribution to understanding variance partitioning across different covariates. I have some comments that I believe the authors ought to address, which mostly relate to clarity and interpretation

Reviewer #1 Public Review #1

First, from a conceptual point of view, the authors focus exclusively on cognition as a downstream outcome. I would suggest the authors nuance their discussion to provide broader considerations of the utility of their method and on the limits of interpretation of brain age models more generally.

Thank you for your comments on this issue.

We now discussed the broader consideration in detail:

(1) the consistency between our findings on fluid cognition and other recent works on brain disorders,

(2) the difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021)

and

(3) suggested solutions we and others made to optimise the utility of Brain Age for both cognitive functioning and brain disorders.

From Discussion:

“This discrepancy between the predictive performance of age-prediction models and the utility of Brain Age indices as a biomarker is consistent with recent findings (for review, see Jirsaraie, Gorelik, et al., 2023), both in the context of cognitive functioning (Jirsaraie, Kaufmann, et al., 2023) and neurological/psychological disorders (Bashyam et al., 2020; Rokicki et al., 2021). For instance, combining different MRI modalities into the prediction models, similar to our stacked models, often leads to the highest performance of age-prediction models, but does not likely explain the highest variance across different phenotypes, including cognitive functioning and beyond (Jirsaraie, Gorelik, et al., 2023).”

“There is a notable difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021). We consider the former as a normative type of study and the latter as a case-control type of study (Insel et al., 2010; Marquand et al., 2016). Those case-control Brain Age studies focusing on neurological/psychological disorders often build age-prediction models from MRI data of largely healthy participants (e.g., controls in a case-control design or large samples in a population-based design), apply the built age-prediction models to participants without vs. with neurological/psychological disorders and compare Brain Age indices between the two groups. On the one hand, this means that case-control studies treat Brain Age as a method to detect anomalies in the neurological/psychological group (Hahn et al., 2021). On the other hand, this also means that case-control studies have to ignore under-fitted models when applied prediction models built from largely healthy participants to participants with neurological/psychological disorders (i.e., Brain Age may predict chronological age well for the controls, but not for those with a disorder). On the contrary, our study and other normative studies focusing on cognitive functioning often build age-prediction models from MRI data of largely healthy participants and apply the built age-prediction models to participants who are also largely healthy. Accordingly, the age-prediction models for explaining cognitive functioning in normative studies, while not allowing us to detect group-level anomalies, do not suffer from being under-fitted. This unfortunately might limit the generalisability of our study into just the normative type of study. Future work is still needed to test the utility of brain age in the case-control case.”

“Next, researchers should not select age-prediction models based solely on age-prediction performance. Instead, researchers could select age-prediction models that explained phenotypes of interest the best. Here we selected age-prediction models based on a set of features (i.e., modalities) of brain MRI. This strategy was found effective not only for fluid cognition as we demonstrated here, but also for neurological and psychological disorders as shown elsewhere (Jirsaraie, Gorelik, et al., 2023; Rokicki et al., 2021). Rokicki and colleagues (2021), for instance, found that, while integrating across MRI modalities led to age-prediction models with the highest age-prediction performance, using only T1 structural MRI gave age-prediction models that were better at classifying Alzheimer’s disease. Similarly, using only cerebral blood flow gave age-prediction models that were better at classifying mild/subjective cognitive impairment, schizophrenia and bipolar disorder.

As opposed to selecting age-prediction models based on a set of features, researchers could also select age-prediction models based on modelling methods. For instance, Jirsaraie and colleagues (2023) compared gradient tree boosting (GTB) and deep-learning brain network (DBN) algorithms in building age-prediction models. They found GTB to have higher age-prediction performance but DBN to have better utility in explaining cognitive functioning. In this case, an algorithm with better utility (e.g., DBN) should be used for explaining a phenotype of interest. Similarly, Bashyam and colleagues (2020) built different DBN-based age-prediction models, varying in age-prediction performance. The DBN models with a higher number of epochs corresponded to higher age-prediction performance. However, DBN-based age-prediction models with a moderate (as opposed to higher or lower) number of epochs were better at classifying Alzheimer’s disease, mild cognitive impairment and schizophrenia. In this case, a model from the same algorithm with better utility (e.g., those DBN with a moderate epoch number) should be used for explaining a phenotype of interest. Accordingly, this calls for a change in research practice, as recently pointed out by Jirasarie and colleagues (2023, p7), “Despite mounting evidence, there is a persisting assumption across several studies that the most accurate brain age models will have the most potential for detecting differences in a given phenotype of interest”. Future neuroimaging research should aim to build age-prediction models that are not necessarily good at predicting age, but at capturing phenotypes of interest.”

Reviewer #1 Public Review #2

Second, from a methods perspective, there is not a sufficient explanation of the methodological procedures in the current manuscript to fully understand how the stacked regression models were constructed. I would request that the authors provide more information to enable the reader to better understand the stacked regression models used to ensure that these models are not overfit.

Thank you for allowing us an opportunity to clarify our stacked model. We made additional clarification to make this clearer (see below). We wanted to confirm that we did not use test sets to build a stacked model in both lower and higher levels of the Elastic Net models. Test sets were there just for testing the performance of the models.

From Methods: “We used nested cross-validation (CV) to build these prediction models (see Figure 7). We first split the data into five outer folds, leaving each outer fold with around 100 participants. This number of participants in each fold is to ensure the stability of the test performance across folds. In each outer-fold CV loop, one of the outer folds was treated as an outer-fold test set, and the rest was treated as an outer-fold training set. Ultimately, looping through the nested CV resulted in a) prediction models from each of the 18 sets of features as well as b) prediction models that drew information across different combinations of the 18 separate sets, known as “stacked models.” We specified eight stacked models: “All” (i.e., including all 18 sets of features), “All excluding Task FC”, “All excluding Task Contrast”, “Non-Task” (i.e., including only Rest FC and sMRI), “Resting and Task FC”, “Task Contrast and FC”, “Task Contrast” and “Task FC”. Accordingly, there were 26 prediction models in total for both Brain Age and Brain Cognition.

To create these 26 prediction models, we applied three steps for each outer-fold loop. The first step aimed at tuning prediction models for each of 18 sets of features. This step only involved the outer-fold training set and did not involve the outer-fold test set. Here, we divided the outer-fold training set into five inner folds and applied inner-fold CV to tune hyperparameters with grid search. Specifically, in each inner-fold CV, one of the inner folds was treated as an inner-fold validation set, and the rest was treated as an inner-fold training set. Within each inner-fold CV loop, we used the inner-fold training set to estimate parameters of the prediction model with a particular set of hyperparameters and applied the estimated model to the inner-fold validation set. After looping through the inner-fold CV, we, then, chose the prediction models that led to the highest performance, reflected by coefficient of determination (R2), on average across the inner-fold validation sets. This led to 18 tuned models, one for each of the 18 sets of features, for each outer fold.

The second step aimed at tuning stacked models. Same as the first step, the second step only involved the outer-fold training set and did not involve the outer-fold test set. Here, using the same outer-fold training set as the first step, we applied tuned models, created from the first step, one from each of the 18 sets of features, resulting in 18 predicted values for each participant. We, then, re-divided this outer-fold training set into new five inner folds. In each inner fold, we treated different combinations of the 18 predicted values from separate sets of features as features to predict the targets in separate “stacked” models. Same as the first step, in each inner-fold CV loop, we treated one out of five inner folds as an inner-fold validation set, and the rest as an inner-fold training set. Also as in the first step, we used the inner-fold training set to estimate parameters of the prediction model with a particular set of hyperparameters from our grid. We tuned the hyperparameters of stacked models using grid search by selecting the models with the highest R2 on average across the inner-fold validation sets. This led to eight tuned stacked models.

The third step aimed at testing the predictive performance of the 18 tuned prediction models from each of the set of features, built from the first step, and eight tuned stacked models, built from the second step. Unlike the first two steps, here we applied the already tuned models to the outer-fold test set. We started by applying the 18 tuned prediction models from each of the sets of features to each observation in the outer-fold test set, resulting in 18 predicted values. We then applied the tuned stacked models to these predicted values from separate sets of features, resulting in eight predicted values.

To demonstrate the predictive performance, we assessed the similarity between the observed values and the predicted values of each model across outer-fold test sets, using Pearson’s r, coefficient of determination (R2) and mean absolute error (MAE). Note that for R2, we used the sum of squares definition (i.e., R2 = 1 – (sum of squares residuals/total sum of squares)) per a previous recommendation (Poldrack et al., 2020). We considered the predicted values from the outer-fold test sets of models predicting age or fluid cognition, as Brain Age and Brain Cognition, respectively.”

Note some previous research, including ours (Tetereva et al., 2022), splits the observations in the outer-fold training set into layer 1 and layer 2 and applies the first and second steps to layers 1 and 2, respectively. Here we decided against this approach and used the same outer-fold training set for both first and second steps in order to avoid potential bias toward the stacked models. This is because, when the data are split into two layers, predictive models built for each separate set of features only use the data from layer 1, while the stacked models use the data from both layers 1 and 2. In practice with large enough data, these two approaches might not differ much, as we demonstrated previously (Tetereva et al., 2022).

Reviewer #1 Public Review #3

Please also provide an indication of the different regression strengths that were estimated across the different models and cross-validation splits. Also, how stable were the weights across splits?

The focus of this article is on the predictions. Still, it is informative for readers to understand how stable the feature importance (i.e., Elastic Net coefficients) is. To demonstrate the stability of feature importance, we now examined the rank stability of feature importance using Spearman’s ρ (see Figure 4). Specifically, we correlated the feature importance between two prediction models of the same features, used in two different outer-fold test sets. Given that there were five outer-fold test sets, we computed 10 Spearman’s ρ for each prediction model of the same features. We found Spearman’s ρ to be varied dramatically in both age-prediction (range=.31-.94) and fluid cognition-prediction (range=.16-.84) models. This means that some prediction models were much more stable in their feature importance than others. This is probably due to various factors such as a) the collinearity of features in the model, b) the number of features (e.g., 71,631 features in functional connectivity, which were further reduced to 75 PCAs, as compared to 19 features in subcortical volume based on the ASEG atlas), c) the penalisation of coefficients either with ‘Ridge’ or ‘Lasso’ methods, which resulted in reduction as a group of features or selection of a feature among correlated features, respectively, and d) the predictive performance of the models. Understanding the stability of feature importance is beyond the scope of the current article. As mentioned by Reviewer 1, “The predictions can be stable when the coefficients are not,” and we chose to focus on the prediction in the current article.

Reviewer #1 Public Review #4

Please provide more details about the task designs, MRI processing procedures that were employed on this sample in addition to the regression methods and bias correction methods used. For example, there are several different parameterisations of the elastic net, please provide equations to describe the method used here so that readers can easily determine how the regularisation parameters should be interpreted.

Thank you for the opportunity for us to provide more methodical details.

First, for the task design, we included the following statements:

From Methods:

“HCP-A collected fMRI data from three tasks: Face Name (Sperling et al., 2001), Conditioned Approach Response Inhibition Task (CARIT) (Somerville et al., 2018) and VISual MOTOR (VISMOTOR) (Ances et al., 2009).

First, the Face Name task (Sperling et al., 2001) taps into episodic memory. The task had three blocks. In the encoding block [Encoding], participants were asked to memorise the names of faces shown. These faces were then shown again in the recall block [Recall] when the participants were asked if they could remember the names of the previously shown faces. There was also the distractor block [Distractor] occurring between the encoding and recall blocks. Here participants were distracted by a Go/NoGo task. We computed six contrasts for this Face Name task: [Encode], [Recall], [Distractor], [Encode vs. Distractor], [Recall vs. Distractor] and [Encode vs. Recall].

Second, the CARIT task (Somerville et al., 2018) was adapted from the classic Go/NoGo task and taps into inhibitory control. Participants were asked to press a button to all [Go] but not to two [NoGo] shapes. We computed three contrasts for the CARIT task: [NoGo], [Go] and [NoGo vs. Go].

Third, the VISMOTOR task (Ances et al., 2009) was designed to test simple activation of the motor and visual cortices. Participants saw a checkerboard with a red square either on the left or right. They needed to press a corresponding key to indicate the location of the red square. We computed just one contrast for the VISMOTOR task: [Vismotor], which indicates the presence of the checkerboard vs. baseline.”

Second, for MRI processing procedures, we included the following statements.

From Methods: “HCP-A provides details of parameters for brain MRI elsewhere (Bookheimer et al., 2019; Harms et al., 2018). Here we used MRI data that were pre-processed by the HCP-A with recommended methods, including the MSMALL alignment (Glasser et al., 2016; Robinson et al., 2018) and ICA-FIX (Glasser et al., 2016) for functional MRI. We used multiple brain MRI modalities, covering task functional MRI (task fMRI), resting-state functional MRI (rsfMRI) and structural MRI (sMRI), and organised them into 19 sets of features.”

“ Sets of Features 1-10: Task fMRI contrast (Task Contrast) Task contrasts reflect fMRI activation relevant to events in each task. Bookheimer and colleagues (2019) provided detailed information about the fMRI in HCP-A. Here we focused on the pre-processed task fMRI Connectivity Informatics Technology Initiative (CIFTI) files with a suffix, “_PA_Atlas_MSMAll_hp0_clean.dtseries.nii.” These CIFTI files encompassed both the cortical mesh surface and subcortical volume (Glasser et al., 2013). Collected using the posterior-to-anterior (PA) phase, these files were aligned using MSMALL (Glasser et al., 2016; Robinson et al., 2018), linear detrended (see https://groups.google.com/a/humanconnectome.org/g/hcp-users/c/ZLJc092h980/m/GiihzQAUAwAJ) and cleaned from potential artifacts using ICA-FIX (Glasser et al., 2016).

To extract Task Contrasts, we regressed the fMRI time series on the convolved task events using a double-gamma canonical hemodynamic response function via FMRIB Software Library (FSL)’s FMRI Expert Analysis Tool (FEAT) (Woolrich et al., 2001). We kept FSL’s default high pass cutoff at 200s (i.e., .005 Hz). We then parcellated the contrast ‘cope’ files, using the Glasser atlas (Gordon et al., 2016) for cortical surface regions and the Freesurfer’s automatic segmentation (aseg) (Fischl et al., 2002) for subcortical regions. This resulted in 379 regions, whose number was, in turn, the number of features for each Task Contrast set of features. “

“ Sets of Features 11-13: Task fMRI functional connectivity (Task FC) Task FC reflects functional connectivity (FC ) among the brain regions during each task, which is considered an important source of individual differences (Elliott et al., 2019; Fair et al., 2007; Gratton et al., 2018). We used the same CIFTI file “_PA_Atlas_MSMAll_hp0_clean.dtseries.nii.” as the task contrasts. Unlike Task Contrasts, here we treated the double-gamma, convolved task events as regressors of no interest and focused on the residuals of the regression from each task (Fair et al., 2007). We computed these regressors on FSL, and regressed them in nilearn (Abraham et al., 2014). Following previous work on task FC (Elliott et al., 2019), we applied a highpass at .008 Hz. For parcellation, we used the same atlases as Task Contrast (Fischl et al., 2002; Glasser et al., 2016). We computed Pearson’s correlations of each pair of 379 regions, resulting in a table of 71,631 non-overlapping FC indices for each task. We then applied r-to-z transformation and principal component analysis (PCA) of 75 components (Rasero et al., 2021; Sripada et al., 2019, 2020). Note to avoid data leakage, we conducted the PCA on each training set and applied its definition to the corresponding test set. Accordingly, there were three sets of 75 features for Task FC, one for each task.

Set of Features 14: Resting-state functional MRI functional connectivity (Rest FC) Similar to Task FC, Rest FC reflects functional connectivity (FC ) among the brain regions, except that Rest FC occurred during the resting (as opposed to task-performing) period. HCP-A collected Rest FC from four 6.42-min (488 frames) runs across two days, leading to 26-min long data (Harms et al., 2018). On each day, the study scanned two runs of Rest FC, starting with anterior-to-posterior (AP) and then with posterior-to-anterior (PA) phase encoding polarity. We used the “rfMRI_REST_Atlas_MSMAll_hp0_clean.dscalar.nii” file that was pre-processed and concatenated across the four runs. We applied the same computations (i.e., highpass filter, parcellation, Pearson’s correlations, r-to-z transformation and PCA) with the Task FC.

Sets of Features 15-18: Structural MRI (sMRI)

sMRI reflects individual differences in brain anatomy. The HCP-A used an established pre-processing pipeline for sMRI (Glasser et al., 2013). We focused on four sets of features: cortical thickness, cortical surface area, subcortical volume and total brain volume. For cortical thickness and cortical surface area, we used Destrieux’s atlas (Destrieux et al., 2010; Fischl, 2012) from FreeSurfer’s “aparc.stats” file, resulting in 148 regions for each set of features. For subcortical volume, we used the aseg atlas (Fischl et al., 2002) from FreeSurfer’s “aseg.stats” file, resulting in 19 regions. For total brain volume, we had five FreeSurfer-based features: “FS_IntraCranial_Vol” or estimated intra-cranial volume, “FS_TotCort_GM_Vol” or total cortical grey matter volume, “FS_Tot_WM_Vol” or total cortical white matter volume, “FS_SubCort_GM_Vol” or total subcortical grey matter volume and “FS_BrainSegVol_eTIV_Ratio” or ratio of brain segmentation volume to estimated total intracranial volume.”

Third, for regression methods and bias correction methods used, we included the following statements:

From Methods:

“For the machine learning algorithm, we used Elastic Net (Zou & Hastie, 2005). Elastic Net is a general form of penalised regressions (including Lasso and Ridge regression), allowing us to simultaneously draw information across different brain indices to predict one target variable. Penalised regressions are commonly used for building age-prediction models (Jirsaraie, Gorelik, et al., 2023). Previously we showed that the performance of Elastic Net in predicting cognitive abilities is on par, if not better than, many non-linear and more-complicated algorithms (Pat, Wang, Bartonicek, et al., 2022; Tetereva et al., 2022). Moreover, Elastic Net coefficients are readily explainable, allowing us the ability to explain how our age-prediction and cognition-prediction models made the prediction from each brain feature (Molnar, 2019; Pat, Wang, Bartonicek, et al., 2022) (see below).

Elastic Net simultaneously minimises the weighted sum of the features’ coefficients. The degree of penalty to the sum of the feature’s coefficients is determined by a shrinkage hyperparameter ‘α’: the greater the α, the more the coefficients shrink, and the more regularised the model becomes. Elastic Net also includes another hyperparameter, ‘l1 ratio’, which determines the degree to which the sum of either the squared (known as ‘Ridge’; l1 ratio=0) or absolute (known as ‘Lasso’; l1 ratio=1) coefficients is penalised (Zou & Hastie, 2005). The objective function of Elastic Net as implemented by sklearn (Pedregosa et al., 2011) is defined as:

where X is the features, y is the target, and β is the coefficient. In our grid search, we tuned two Elastic Net hyperparameters: α using 70 numbers in log space, ranging from .1 and 100, and l_1-ratio using 25 numbers in linear space, ranging from 0 and 1.

To understand how Elastic Net made a prediction based on different brain features, we examined the coefficients of the tuned model. Elastic Net coefficients can be considered as feature importance, such that more positive Elastic Net coefficients lead to more positive predicted values and, similarly, more negative Elastic Net coefficients lead to more negative predicted values (Molnar, 2019; Pat, Wang, Bartonicek, et al., 2022). While the magnitude of Elastic Net coefficients is regularised (thus making it difficult for us to interpret the magnitude itself directly), we could still indicate that a brain feature with a higher magnitude weights relatively stronger in making a prediction. Another benefit of Elastic Net as a penalised regression is that the coefficients are less susceptible to collinearity among features as they have already been regularised (Dormann et al., 2013; Pat, Wang, Bartonicek, et al., 2022).

Given that we used five-fold nested cross validation, different outer folds may have different degrees of ‘α’ and ‘l1 ratio’, making the final coefficients from different folds to be different. For instance, for certain sets of features, penalisation may not play a big part (i.e., higher or lower ‘α’ leads to similar predictive performance), resulting in different ‘α’ for different folds. To remedy this in the visualisation of Elastic Net feature importance, we refitted the Elastic Net model to the full dataset without splitting them into five folds and visualised the coefficients on brain images using Brainspace (Vos De Wael et al., 2020) and Nilern (Abraham et al., 2014) packages. Note, unlike other sets of features, Task FC and Rest FC were modelled after data reduction via PCA. Thus, for Task FC and Rest FC, we, first, multiplied the absolute PCA scores (extracted from the ‘components_’ attribute of ‘sklearn.decomposition.PCA’) with Elastic Net coefficients and, then, summed the multiplied values across the 75 components, leaving 71,631 ROI-pair indices. “

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

eLife assessment

This useful manuscript challenges the utility of current paradigms for estimating brain-age with magnetic resonance imaging measures, but presents inadequate evidence to support the suggestion that an alternative approach focused on predicting cognition is more useful. The paper would benefit from a clearer explication of the methods and a more critical evaluation of the conceptual basis of the different models. This work will be of interest to researchers working on brain-age and related models.

Thank you so much for providing high-quality reviews on our manuscript. We revised the manuscript to address all of the reviewers’ comments and provided full responses to each of the comments below. Importantly, in this revision, we clarified that we did not intend to use Brain Cognition as an alternative approach. This is because, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Here we made this point more explicit and further stated that the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. By examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. And such quantification is the third aim of this study.

Public Reviews:

Reviewer 1 (Public Review):

In this paper, the authors evaluate the utility of brain-age-derived metrics for predicting cognitive decline by performing a 'commonality' analysis in a downstream regression that enables the different contribution of different predictors to be assessed. The main conclusion is that brain-age-derived metrics do not explain much additional variation in cognition over and above what is already explained by age. The authors propose to use a regression model trained to predict cognition ("brain-cognition") as an alternative suited to applications of cognitive decline. While this is less accurate overall than brain age, it explains more unique variance in the downstream regression.

(1) I thank the authors for addressing many of my concerns with this revision. However, I do not feel they have addressed them all. In particular I think the authors could do more to address the concern I raised about the instability of the regression coefficients and about providing enough detail to determine that the stacked regression models do not overfit.

Thank you Reviewer 1 for the comment. We addressed them in our response to Reviewer 1 Recommendations For The Authors #1 and #2 (see below).

(2) In considering my responses to the authors revision, I also must say that I agree with Reviewer 3 about the limitations of the brain age and brain cognition methods conceptually. In particular that the regression model used to predict fluid cognition will by construction explain more variance in cognition than a brain age model that is trained to predict age. To be fair, these conceptual problems are more widespread than this paper alone, so I do not believe the authors should be penalised for that. However, I would recommend to make these concerns more explicit in the manuscript

Thank you Reviewer 1 for the comment. We addressed them in our response to Reviewer 1 Recommendations For The Authors #3 (see below).

Reviewer 2 (Public Review):

In this study, the authors aimed to evaluate the contribution of brain-age indices in capturing variance in cognitive decline and proposed an alternative index, brain-cognition, for consideration.

The study employs suitable methods and data to address the research questions, and the methods and results sections are generally clear and easy to follow.

I appreciate the authors' efforts in significantly improving the paper, including some considerable changes, from the original submission. While not all reviewer points were tackled, the majority of them were adequately addressed. These include additional analyses, more clarity in the methods and a much richer and nuanced discussion. While recognising the merits of the revised paper, I have a few additional comments.

(1) Perhaps it would help the reader to note that it might be expected for brain-cognition to account for a significantly larger variance (11%) in fluid cognition, in contrast to brain-age. This stems from the fact that the authors specifically trained brain-cognition to predict fluid cognition, the very variable under consideration. In line with this, the authors later recommend that researchers considering the use of brain-age should evaluate its utility using a regression approach. The latter involves including a brain index (e.g. brain-cognition) previously trained to predict the regression's target variable (e.g. fluid cognition) alongside a brain-age index (e.g., corrected brain-age gap). If the target-trained brain index outperforms the brain-age metric, it suggests that relying solely on brain-age might not be the optimal choice. Although not necessarily the case, is it surprising for the target-trained brain index to demonstrate better performance than brain-age? This harks back to the broader point raised in the initial review: while brain-age may prove useful (though sometimes with modest effect sizes) across diverse outcomes as a generally applicable metric, a brain index tailored for predicting a specific outcome, such as brain-cognition in this case, might capture a considerably larger share of variance in that specific context but could lack broader applicability. The latter aspect needs to be empirically assessed.

Thank you so much for raising this point. Reviewer 1 (Public Review #2/Recommendations For The Authors #3) and Reviewer 3 (Recommendations for the Authors #1) made a similar observation. We now made changes to the introduction and discussion to address this concern (please see our responses to Reviewer 1 Recommendations For The Authors #3 below).

Briefly, as in our 2nd revision, we did not intend to compare Brain Age with Brain Cognition since, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Here we made this point more explicit and further stated that the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. By examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. And such quantification is the third aim of this study.

(2) Furthermore, the discussion pertaining to training brain-age models on healthy populations for subsequent testing on individuals with neurological or psychological disorders seems somewhat one-sided within the broader debate. This one-sidedness might potentially confuse readers. It is worth noting that the choice to employ healthy participants in the training model is likely deliberate, serving as a norm against which atypical populations are compared. To provide a more comprehensive understanding, referencing Tim Hans's counterargument to Bashyam's perspective could offer a more complete view (https://academic.oup.com/brain/article/144/3/e31/6214475?login=false).

Thank you Reviewer 2 for bringing up this issue. We have now revised the paragraph in question and added nuances on the usage of Brain Age for normative vs. case-control studies. We also cited Tim Hahn’s article that explained the conceptual foundation of the use of Brain Age in case-control studies. Please see below. Additionally, we also made a statement about our study not being able to address issues about the case-control studies directly in the newly written conclusion (see Reviewer 3 Recommendations for the Authors #3).

Discussion:

“There is a notable difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021). We consider the former as a normative type of study and the latter as a case-control type of study (Insel et al., 2010; Marquand et al., 2016). Those case-control Brain Age studies focusing on neurological/psychological disorders often build age-prediction models from MRI data of largely healthy participants (e.g., controls in a case-control design or large samples in a population-based design), apply the built age-prediction models to participants without vs. with neurological/psychological disorders and compare Brain Age indices between the two groups. On the one hand, this means that case-control studies treat Brain Age as a method to detect anomalies in the neurological/psychological group (Hahn et al., 2021). On the other hand, this also means that case-control studies have to ignore under-fitted models when applied prediction models built from largely healthy participants to participants with neurological/psychological disorders (i.e., Brain Age may predict chronological age well for the controls, but not for those with a disorder). On the contrary, our study and other normative studies focusing on cognitive functioning often build age-prediction models from MRI data of largely healthy participants and apply the built age-prediction models to participants who are also largely healthy. Accordingly, the age-prediction models for explaining cognitive functioning in normative studies, while not allowing us to detect group-level anomalies, do not suffer from being under-fitted. This unfortunately might limit the generalisability of our study into just the normative type of study. Future work is still needed to test the utility of brain age in the case-control case.”

(3) Overall, this paper makes a significant contribution to the field of brain-age and related brain indices and their utility.

Thank you for the encouragement.

Reviewer 3 (Public Review):

The main question of this article is as follows: "To what extent does having information on brain-age improve our ability to capture declines in fluid cognition beyond knowing a person's chronological age?" This question is worthwhile, considering that there is considerable confusion in the field about the nature of brain-age.

(1) Thank you to the authors for addressing so many of my concerns with this revision. There are a few points that I feel still need addressing/clarifying related to 1) calculating brain cognition, 2) the inevitability of their results, and 3) their continued recommendation to use brain-age metrics.

Thank you Reviewer 3 for the comment. We addressed them in our response to Reviewer 3 Recommendations For The Authors #1-3 (see below).

Recommendations for the authors:

Reviewer 1 (Recommendations For The Authors):

(1) I do not feel the authors have fully addressed the concern I raised about the stacked regression models. Despite the new figure, it is still not entirely clear what the authors are using as the training set in the final step. To be clear, the problem occurs because of the parameters, not the hyperparameters (which the authors now state that they are optimising via nested grid search). in other words, given a regression model y = X*beta, if the X are taken to be predictions from a lower level regression model, then they contain information that is derived from both the training set at the test set for the model that this was trained on. If the split is the same (i.e. the predictions are derived on the same test set as is being used at the second level), then this can lead to overfitting. It is not clear to me whether the authors have done this or not. Please provide additional detail to clarify this point.

Thank you for allowing us an opportunity to clarify our stacked model. We wanted to confirm that we did not use test sets to build a stacked model in both lower and higher levels of the Elastic Net models. Test sets were there just for testing the performance of the models. We made additional clarification to make this clearer (see below). Let us explain what we did and provide the rationales below.

From Methods:

“We used nested cross-validation (CV) to build these prediction models (see Figure 7). We first split the data into five outer folds, leaving each outer fold with around 100 participants. This number of participants in each fold is to ensure the stability of the test performance across folds. In each outer-fold CV loop, one of the outer folds was treated as an outer-fold test set, and the rest was treated as an outer-fold training set. Ultimately, looping through the nested CV resulted in a) prediction models from each of the 18 sets of features as well as b) prediction models that drew information across different combinations of the 18 separate sets, known as “stacked models.” We specified eight stacked models: “All” (i.e., including all 18 sets of features), “All excluding Task FC”, “All excluding Task Contrast”, “Non-Task” (i.e., including only Rest FC and sMRI), “Resting and Task FC”, “Task Contrast and FC”, “Task Contrast” and “Task FC”. Accordingly, there were 26 prediction models in total for both Brain Age and Brain Cognition.

To create these 26 prediction models, we applied three steps for each outer-fold loop. The first step aimed at tuning prediction models for each of 18 sets of features. This step only involved the outer-fold training set and did not involve the outer-fold test set. Here, we divided the outer-fold training set into five inner folds and applied inner-fold CV to tune hyperparameters with grid search. Specifically, in each inner-fold CV, one of the inner folds was treated as an inner-fold validation set, and the rest was treated as an inner-fold training set. Within each inner-fold CV loop, we used the inner-fold training set to estimate parameters of the prediction model with a particular set of hyperparameters and applied the estimated model to the inner-fold validation set. After looping through the inner-fold CV, we, then, chose the prediction models that led to the highest performance, reflected by coefficient of determination (R2), on average across the inner-fold validation sets. This led to 18 tuned models, one for each of the 18 sets of features, for each outer fold.

The second step aimed at tuning stacked models. Same as the first step, the second step only involved the outer-fold training set and did not involve the outer-fold test set. Here, using the same outer-fold training set as the first step, we applied tuned models, created from the first step, one from each of the 18 sets of features, resulting in 18 predicted values for each participant. We, then, re-divided this outer-fold training set into new five inner folds. In each inner fold, we treated different combinations of the 18 predicted values from separate sets of features as features to predict the targets in separate “stacked” models. Same as the first step, in each inner-fold CV loop, we treated one out of five inner folds as an inner-fold validation set, and the rest as an inner-fold training set. Also as in the first step, we used the inner-fold training set to estimate parameters of the prediction model with a particular set of hyperparameters from our grid. We tuned the hyperparameters of stacked models using grid search by selecting the models with the highest R2 on average across the inner-fold validation sets. This led to eight tuned stacked models.

The third step aimed at testing the predictive performance of the 18 tuned prediction models from each of the set of features, built from the first step, and eight tuned stacked models, built from the second step. Unlike the first two steps, here we applied the already tuned models to the outer-fold test set. We started by applying the 18 tuned prediction models from each of the sets of features to each observation in the outer-fold test set, resulting in 18 predicted values. We then applied the tuned stacked models to these predicted values from separate sets of features, resulting in eight predicted values.

To demonstrate the predictive performance, we assessed the similarity between the observed values and the predicted values of each model across outer-fold test sets, using Pearson’s r, coefficient of determination (R2) and mean absolute error (MAE). Note that for R2, we used the sum of squares definition (i.e., R2 = 1 – (sum of squares residuals/total sum of squares)) per a previous recommendation (Poldrack et al., 2020). We considered the predicted values from the outer-fold test sets of models predicting age or fluid cognition, as Brain Age and Brain Cognition, respectively.”

Author response image 1.

Diagram of the nested cross-validation used for creating predictions for models of each set of features as well as predictions for stacked models.

Note some previous research, including ours (Tetereva et al., 2022), splits the observations in the outer-fold training set into layer 1 and layer 2 and applies the first and second steps to layers 1 and 2, respectively. Here we decided against this approach and used the same outer-fold training set for both first and second steps in order to avoid potential bias toward the stacked models. This is because, when the data are split into two layers, predictive models built for each separate set of features only use the data from layer 1, while the stacked models use the data from both layers 1 and 2. In practice with large enough data, these two approaches might not differ much, as we demonstrated previously (Tetereva et al., 2022).

(2) I also do not feel the authors have fully addressed the concern I raised about stability of the regression coefficients over splits of the data. I wanted to see the regression coefficients, not the predictions. The predictions can be stable when the coefficients are not.

The focus of this article is on the predictions. Still, as pointed out by reviewer 1, it is informative for readers to understand how stable the feature importance (i.e., Elastic Net coefficients) is. To demonstrate the stability of feature importance, we now examined the rank stability of feature importance using Spearman’s ρ (see Figure 4). Specifically, we correlated the feature importance between two prediction models of the same features, used in two different outer-fold test sets. Given that there were five outer-fold test sets, we computed 10 Spearman’s ρ for each prediction model of the same features. We found Spearman’s ρ to be varied dramatically in both age-prediction (range=.31-.94) and fluid cognition-prediction (range=.16-.84) models. This means that some prediction models were much more stable in their feature importance than others. This is probably due to various factors such as a) the collinearity of features in the model, b) the number of features (e.g., 71,631 features in functional connectivity, which were further reduced to 75 PCAs, as compared to 19 features in subcortical volume based on the ASEG atlas), c) the penalisation of coefficients either with ‘Ridge’ or ‘Lasso’ methods, which resulted in reduction as a group of features or selection of a feature among correlated features, respectively, and d) the predictive performance of the models. Understanding the stability of feature importance is beyond the scope of the current article. As mentioned by Reviewer 1, “The predictions can be stable when the coefficients are not,” and we chose to focus on the prediction in the current article.

Author response image 2.

Stability of feature importance (i.e., Elastic Net Coefficients) of prediction models. Each dot represents rank stability (reflected by Spearman’s ρ) in the feature importance between two prediction models of the same features, used in two different outer-fold test sets. Given that there were five outer-fold test sets, there were 10 Spearman’s ρs for each prediction model. The numbers to the right of the plots indicate the mean of Spearman’s ρ for each prediction model.

(3) I also must say that I agree with Reviewer 3 about the limitations of the brain-age and brain-cognition methods conceptually. In particular that the regression model used to predict fluid cognition will by construction explain more variance in cognition than a brain-age model that is trained to predict age. This suffers from the same problem the authors raise with brain-age and I agree that this would probably disappear if the authors had a separate measure of cognition against which to validate and were then to regress this out as they do for age correction. I am aware that these conceptual problems are more widespread than this paper alone (in fact throughout the brain-age literature), so I do not believe the authors should be penalised for that. However, I do think they can make these concerns more explicit and further tone down the comments they make about the utility of brain-cognition.

Thank you so much for raising this point. Reviewer 2 (Public Review #1) and Reviewer 3 (Recommendations for the Authors #1) made a similar observation. We now made changes to the introduction and discussion to address this concern (see below).

Briefly, we made it explicit that, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. That is, the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. More importantly, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. And this is the third goal of this present study.

From Introduction:

“Third and finally, certain variation in fluid cognition is related to brain MRI, but to what extent does Brain Age not capture this variation? To estimate the variation in fluid cognition that is related to the brain MRI, we could build prediction models that directly predict fluid cognition (i.e., as opposed to chronological age) from brain MRI data. Previous studies found reasonable predictive performances of these cognition-prediction models, built from certain MRI modalities (Dubois et al., 2018; Pat et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). Analogous to Brain Age, we called the predicted values from these cognition-prediction models, Brain Cognition. The strength of an out-of-sample relationship between Brain Cognition and fluid cognition reflects variation in fluid cognition that is related to the brain MRI and, therefore, indicates the upper limit of Brain Age’s capability in capturing fluid cognition. This is, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Consequently, if we included Brain Cognition, Brain Age and chronological age in the same model to explain fluid cognition, we would be able to examine the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age. These unique effects of Brain Cognition, in turn, would indicate the amount of co-variation between brain MRI and fluid cognition that is missed by Brain Age.”

From Discussion:

“Third, by introducing Brain Cognition, we showed the extent to which Brain Age indices were not able to capture the variation in fluid cognition that is related to brain MRI. More specifically, using Brain Cognition allowed us to gauge the variation in fluid cognition that is related to the brain MRI, and thereby, to estimate the upper limit of what Brain Age can do. Moreover, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age.

From our results, Brain Cognition, especially from certain cognition-prediction models such as the stacked models, has relatively good predictive performance, consistent with previous studies (Dubois et al., 2018; Pat et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). We then examined Brain Cognition using commonality analyses (Nimon et al., 2008) in multiple regression models having a Brain Age index, chronological age and Brain Cognition as regressors to explain fluid cognition. Similar to Brain Age indices, Brain Cognition exhibited large common effects with chronological age. But more importantly, unlike Brain Age indices, Brain Cognition showed large unique effects, up to around 11%. As explained above, the unique effects of Brain Cognition indicated the amount of co-variation between brain MRI and fluid cognition that was missed by a Brain Age index and chronological age. This missing amount was relatively high, considering that Brain Age and chronological age together explained around 32% of the total variation in fluid cognition. Accordingly, if a Brain Age index was used as a biomarker along with chronological age, we would have missed an opportunity to improve the performance of the model by around one-third of the variation explained.”

Reviewer #3 (Recommendations For The Authors):

Thank you to the authors for addressing so many of my concerns with this revision. There are a few points that I feel still need addressing/clarifying related to: 1) calculating brain cognition, 2) the inevitability of their results, and 3) their continued recommendation to use brain age metrics.

(1) I understand your point here. I think the distinction is that it is fine to build predictive models, but then there is no need to go through this intermediate step of "brain-cognition". Just say that brain features can predict cognition XX well, and brain-age (or some related metric) can predict cognition YY well. It creates a confusing framework for the reader that can lead them to believe that "brain-cognition" is not just a predicted value of fluid cognition from a model using brain features to predict cognition. While you clearly state that that is in fact what it is in the text, which is a huge improvement, I do not see what is added by going through brain-cognition instead of simply just obtaining a change in R2 where the first model uses brain features alone to predict cognition, and the second adds on brain-age (or related metrics), or visa versa, depending on the question. Please do this analysis, and either compare and contrast it with going through "brain-cognition" in your paper, or switch to this analysis, as it more directly addresses the question of the incremental predictive utility of brain-age above and beyond brain features.

Thank you so much for raising this point. Reviewer 1 (Public Review #2/Recommendations For The Authors #3) and Reviewer 2 (Public Review #1) made a similar observation. We now made changes to the introduction and discussion to address this concern (see our responses to Reviewer 1 Recommendations For The Authors #3 above).

Briefly, as in our 2nd revision, we made it explicitly clear that we did not intend to compare Brain Age with Brain Cognition since, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. And, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age.

We have thought about changing the name Brain Cognition into something along the lines of “predicted values of prediction models predicting fluid cognition based on brain MRI.” However, this made the manuscript hard to follow, especially with the commonality analyses. For instance, the sentence, “Here, we tested Brain Cognition’s unique effects in multiple regression models with a Brain Age index, chronological age and Brain Cognition as regressors to explain fluid cognition” would become “Here, we tested predicted values of prediction models predicting fluid cognition based on brain MRI unique effects in multiple regression models with a Brain Age index, chronological age and predicted values of prediction models predicting fluid cognition based on brain MRI as regressors to explain fluid cognition.” We believe, given our additional explanation (see our responses to Reviewer 1 Recommendations For The Authors #3 above), readers should understand what Brain Cognition is, and that we did not intend to compare Brain Age and Brain Cognition directly.

As for the suggested analysis, “obtaining a change in R2 where the first model uses brain features alone to predict cognition, and the second adds on brain-age (or related metrics), or visa versa,” we have already done this in the form of commonality analysis (Nimon et al., 2008) (see Figure 7 below). That is, to obtain unique and common effects of the regressors, we need to look at all of the possible changes in R2 when all possible subsets of regressors were excluded or included, see equations 12 and 13 below.

From Methods:

“Similar to the above multiple regression model, we had chronological age, each Brain Age index and Brain Cognition as the regressors for fluid cognition:

Fluid Cognitioni = β0 + β1 Chronological Agei + β2 Brain Age Indexi,j + β3 Brain Cognitioni + εi, (12)

Applying the commonality analysis here allowed us, first, to investigate the addictive, unique effects of Brain Cognition, over and above chronological age and Brain Age indices. More importantly, the commonality analysis also enabled us to test the common, shared effects that Brain Cognition had with chronological age and Brain Age indices in explaining fluid cognition. We calculated the commonality analysis as follows (Nimon et al., 2017):

Unique Effectchronological age = ΔR2chronological age = R2chronological age, Brain Age index, Brain Cognition – R2 Brain Age index, Brain Cognition

Unique EffectBrain Age index = ΔR2Brain Age index = R2chronological age, Brain Age index, Brain Cognition – R2 chronological age, Brain Cognition

Unique EffectBrain Cognition = ΔR2Brain Cognition = R2chronological age, Brain Age index, Brain Cognition – R2 chronological age, Brain Age Index

Common Effectchronological age, Brain Age index = R2chronological age, Brain Cognition + R2 Brain Age index, Brain Cognition – R2 Brain Cognition – R2chronological age, Brain Age index, Brain Cognition

Common Effectchronological age, Brain Cognition = R2chronological age, Brain Age Index + R2 Brain Age index, Brain Cognition – R2 Brain Age Index – R2chronological age, Brain Age index, Brain Cognition

Common Effect Brain Age index, Brain Cognition = R2chronological age, Brain Age Index + R2 chronological age, Brain Cognition – R2 chronological age – R2chronological age, Brain Age index, Brain Cognition

Common Effect chronological age, Brain Age index, Brain Cognition = R2 chronological age + R2 Brain Age Index + R2 Brain Cognition – R2chronological age, Brain Age Index – R2 chronological age, Brain Cognition – R2 Brain Age Index, Brain Cognition – R2chronological age, Brain Age index, Brain Cognition , (13)”

(2) I agree that the solution is not to exclude age as a covariate, and that there is a big difference between inevitable and obvious. I simply think a further discussion of the inevitability of the results would be clarifying for the readers. There is a big opportunity in the brain-age literature to be as direct as possible about why you are finding what you are finding. People need to know not only what you found, but why you found what you found.

Thank you. We agreed that we need to make this point more explicit and direct. In the revised manuscript, we had the statements in both Introduction and Discussion (see below) about the tight relationship between Brain Age and chronological age by design, making the small unique effects of Brain Age inevitable.

Introduction:

“Accordingly, by design, Brain Age is tightly close to chronological age. Because chronological age usually has a strong relationship with fluid cognition, to begin with, it is unclear how much Brain Age adds to what is already captured by chronological age.“

Discussion:

“First, Brain Age itself did not add much more information to help us capture fluid cognition than what we had already known from a person’s chronological age. This can clearly be seen from the small unique effects of Brain Age indices in the multiple regression models having Brain Age and chronological age as the regressors. While the unique effects of some Brain Age indices from certain age-prediction models were statistically significant, there were all relatively small. Without Brain Age indices, chronological age by itself already explained around 32% of the variation in fluid cognition. Including Brain Age indices only added around 1.6% at best. We believe the small unique effects of Brain Age were inevitable because, by design, Brain Age is tightly close to chronological age. Therefore, chronological age and Brain Age captured mostly a similar variation in fluid cognition.

Investigating the simple regression models and the commonality analysis between each Brain Age index and chronological age provided additional insights….”

(3) I believe it is very important to critically examine the use of brain-age and related metrics. As part of this process, I think we should be asking ourselves the following questions (among others): Why go through age prediction? Wouldn't the predictions of cognition (or another variable) using the same set of brain features always be as good or better? You still have not justified the use of brain-age. As I said before, if you are going to continue to recommend the use of brain-age, you need a very strong argument for why you are recommending this. What does it truly add? Otherwise, temper your statements to indicate possible better paths forward.

Thank you Reviewer 3 for making an argument against the use of Brain Age. We largely agree with you. However, our work only focuses on one phenotype, fluid cognition, and on the normative situation (i.e., not having a case vs control group). As Reviewer 2 pointed out, Brain Age might still have utility in other cases, not studied here. Still, future studies that focus on other phenotypes may consider using our approach as a template to test the utility of Brain Age in other situations. We added the conclusion statement to reflect this.

From Discussion:

“Altogether, we examined the utility of Brain Age as a biomarker for fluid cognition. Here are the three conclusions. First, Brain Age failed to add substantially more information over and above chronological age. Second, a higher ability to predict chronological age did not correspond to a higher utility to capture fluid cognition. Third, Brain Age missed up to around one-third of the variation in fluid cognition that could have been explained by brain MRI. Yet, given our focus on fluid cognition, future empirical research is needed to test the utility of Brain Age on other phenotypes, especially when Brain Age is used for anomaly detection in case-control studies (e.g., Bashyam et al., 2020; Rokicki et al., 2021). We hope that future studies may consider applying our approach (i.e., using the commonality analysis that includes predicted values from a model that directly predicts the phenotype of interest) to test the utility of Brain Age as a biomarker for other phenotypes.”

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Author response:

The following is the authors’ response to the previous reviews

Reviewer #1:

Comment:

The authors quantified information in gesture and speech, and investigated the neural processing of speech and gestures in pMTG and LIFG, depending on their informational content, in 8 different time-windows, and using three different methods (EEG, HD-tDCS and TMS). They found that there is a time-sensitive and staged progression of neural engagement that is correlated with the informational content of the signal (speech/gesture).

Strengths:

A strength of the paper is that the authors attempted to combine three different methods to investigate speech-gesture processing.

We sincerely appreciate the reviewer’s recognition of our efforts in employing a multi-method approach, which integrates three complementary experimental paradigms, each leveraging distinct neurophysiological techniques to provide converging evidence.

In Experiment 1, we found that the degree of inhibition in the pMTG and LIFG was strongly associated with the overlap in gesture-speech representations, as quantified by mutual information. Experiment 2 revealed the time-sensitive dynamics of the pMTG-LIFG circuit in processing both unisensory (gesture or speech) and multisensory information. Experiment 3, utilizing high-temporal-resolution EEG, independently replicated the temporal dynamics of gesture-speech integration observed in Experiment 2, further validating our findings.

The striking convergence across these methodologically independent approaches significantly bolsters the robustness and generalizability of our conclusions regarding the neural mechanisms underlying multisensory integration.

Comment 1: I thank the authors for their careful responses to my comments. However, I remain not convinced by their argumentation regarding the specificity of their spatial targeting and the time-windows that they used.

The authors write that since they included a sham TMS condition, that the TMS selectively disrupted the IFG-pMTG interaction during specific time windows of the task related to gesture-speech semantic congruency. This to me does not show anything about the specificity of the time-windows itself, nor the selectivity of targeting in the TMS condition.

(1) Selection of brain regions (IFG/pMTG)

We thank the reviewer for their thoughtful consideration. The choice of the left IFG and pMTG as regions of interest (ROIs) was informed by a meta-analysis of fMRI studies on gesture-speech integration, which consistently identified these regions as critical hubs (see Author response table 1 for detailed studies and coordinates).

Author response table 1.

Meta-analysis of previous studies on gesture-speech integration.

Based on the meta-analysis of previous studies, we selected the IFG and pMTG as ROIs for gesture-speech integration. The rationale for selecting these brain regions is outlined in the introduction in Lines 63-66: “Empirical studies have investigated the semantic integration between gesture and speech by manipulating their semantic relationship[15-18] and revealed a mutual interaction between them19-21 as reflected by the N400 latency and amplitude14 as well as common neural underpinnings in the left inferior frontal gyrus (IFG) and posterior middle temporal gyrus (pMTG)[15,22,23].”

And further described in Lines 77-78: “Experiment 1 employed high-definition transcranial direct current stimulation (HD-tDCS) to administer Anodal, Cathodal and Sham stimulation to either the IFG or the pMTG”. And Lines 85-88: ‘Given the differential involvement of the IFG and pMTG in gesture-speech integration, shaped by top-down gesture predictions and bottom-up speech processing [23], Experiment 2 was designed to assess whether the activity of these regions was associated with relevant informational matrices”.

In the Methods section, we clarified the selection of coordinates in Lines 194-200: “Building on a meta-analysis of prior fMRI studies examining gesture-speech integration[22], we targeted Montreal Neurological Institute (MNI) coordinates for the left IFG at (-62, 16, 22) and the pMTG at (-50, -56, 10). In the stimulation protocol for HD-tDCS, the IFG was targeted using electrode F7 as the optimal cortical projection site[36], with four return electrodes placed at AF7, FC5, F9, and FT9. For the pMTG, TP7 was selected as the cortical projection site[36], with return electrodes positioned at C5, P5, T9, and P9.”

The selection of IFG or pMTG as integration hubs for gesture and speech has also been validated in our previous studies. Specifically, Zhao et al. (2018, J. Neurosci) applied TMS to both areas. Results demonstrated that disrupting neural activity in the IFG or pMTG via TMS selectively impaired the semantic congruency effect (reaction time costs due to semantic incongruence), while leaving the gender congruency effect unaffected.

These findings identified the IFG and pMTG as crucial hubs for gesture-speech integration, guiding the selection of brain regions for our subsequent studies.

(2) Selection of time windows

The five key time windows (TWs) analyzed in this study were derived from our previous TMS work (Zhao et al., 2021, J. Neurosci), where we segmented the gesture-speech integration period (0–320 ms post-speech onset) into eight 40-ms windows. This interval aligns with established literature on gesture-speech integration, particularly the 200–300 ms window noted by the reviewer. As detailed in Lines (776-779): “Procedure of Experiment 2. Eight time windows (TWs, duration = 40 ms) were segmented in relative to the speech IP. Among the eight TWs, five (TW1, TW2, TW3, TW6, and TW7) were chosen based on the significant results in our prior study[23]. Double-pulse TMS was delivered over each of the TW of either the pMTG or the IFG”.

In our prior work (Zhao et al., 2021, J. Neurosci), we employed a carefully controlled experimental design incorporating two key factors: (1) gesture-speech semantic congruency (serving as our primary measure of integration) and (2) gesture-speech gender congruency (implemented as a matched control factor). Using a time-locked, double-pulse TMS protocol, we systematically targeted each of the eight predefined time windows (TWs) within the left IFG, left pMTG, or vertex (serving as a sham control condition). Our results demonstrated that a TW-selective disruption of gesture-speech integration, indexed by the semantic congruency effect (i.e., a cost of reaction time because of semantic conflict), when stimulating the left pMTG in TW1, TW2, and TW7 but when stimulating the left IFG in TW3 and TW6. Crucially, no significant effects were observed during either sham stimulation or the controlled gender congruency factor (Figure 3 from Zhao et al., 2021, J. Neurosci).

This triple dissociation - showing effects only for semantic integration, only in active stimulation, and only at specific time points - provides compelling causal evidence that IFG-pMTG connectivity plays a temporally precise role in gesture-speech integration.

Noted that this work has undergone rigorous peer review by two independent experts who both endorsed our methodological approach. Their original evaluations, provided below:

Reviewer 1: “significance: Using chronometric TMS-stimulation the data of this experiment suggests a feedforward information flow from left pMTG to left IFG followed by an information flow from left IFG back to the left pMTG.  The study is the first to provide causal evidence for the temporal dynamics of the left pMTG and left IFG found during gesture-speech integration.”

Reviewer 2: “Beyond the new results the manuscript provides regarding the chronometrical interaction of the left inferior frontal gyrus and middle temporal gyrus in gesture-speech interaction, the study more basically shows the possibility of unfolding temporal stages of cognitive processing within domain-specific cortical networks using short-time interval double-pulse TMS. Although this method also has its limitations, a careful study planning as shown here and an appropiate discussion of the results can provide unique insights into cognitive processing.”

References:

Willems, R.M., Ozyurek, A., and Hagoort, P. (2009). Differential roles for left inferior frontal and superior temporal cortex in multimodal integration of action and language. Neuroimage 47, 1992-2004. 10.1016/j.neuroimage.2009.05.066.

Drijvers, L., Jensen, O., and Spaak, E. (2021). Rapid invisible frequency tagging reveals nonlinear integration of auditory and visual information. Human Brain Mapping 42, 1138-1152. 10.1002/hbm.25282.

Drijvers, L., and Ozyurek, A. (2018). Native language status of the listener modulates the neural integration of speech and iconic gestures in clear and adverse listening conditions. Brain and Language 177, 7-17. 10.1016/j.bandl.2018.01.003.

Drijvers, L., van der Plas, M., Ozyurek, A., and Jensen, O. (2019). Native and non-native listeners show similar yet distinct oscillatory dynamics when using gestures to access speech in noise. Neuroimage 194, 55-67. 10.1016/j.neuroimage.2019.03.032.

Holle, H., and Gunter, T.C. (2007). The role of iconic gestures in speech disambiguation: ERP evidence. J Cognitive Neurosci 19, 1175-1192. 10.1162/jocn.2007.19.7.1175.

Kita, S., and Ozyurek, A. (2003). What does cross-linguistic variation in semantic coordination of speech and gesture reveal?: Evidence for an interface representation of spatial thinking and speaking. J Mem Lang 48, 16-32. 10.1016/S0749-596x(02)00505-3.

Bernardis, P., and Gentilucci, M. (2006). Speech and gesture share the same communication system. Neuropsychologia 44, 178-190. 10.1016/j.neuropsychologia.2005.05.007.

Zhao, W.Y., Riggs, K., Schindler, I., and Holle, H. (2018). Transcranial magnetic stimulation over left inferior frontal and posterior temporal cortex disrupts gesture-speech integration. Journal of Neuroscience 38, 1891-1900. 10.1523/Jneurosci.1748-17.2017.

Zhao, W., Li, Y., and Du, Y. (2021). TMS reveals dynamic interaction between inferior frontal gyrus and posterior middle temporal gyrus in gesture-speech semantic integration. The Journal of Neuroscience, 10356-10364. 10.1523/jneurosci.1355-21.2021.

Hartwigsen, G., Bzdok, D., Klein, M., Wawrzyniak, M., Stockert, A., Wrede, K., Classen, J., and Saur, D. (2017). Rapid short-term reorganization in the language network. Elife 6. 10.7554/eLife.25964.

Jackson, R.L., Hoffman, P., Pobric, G., and Ralph, M.A.L. (2016). The semantic network at work and rest: Differential connectivity of anterior temporal lobe subregions. Journal of Neuroscience 36, 1490-1501. 10.1523/JNEUROSCI.2999-15.2016.

Humphreys, G. F., Lambon Ralph, M. A., & Simons, J. S. (2021). A Unifying Account of Angular Gyrus Contributions to Episodic and Semantic Cognition. Trends in neurosciences, 44(6), 452–463. https://doi.org/10.1016/j.tins.2021.01.006

Bonner, M. F., & Price, A. R. (2013). Where is the anterior temporal lobe and what does it do?. The Journal of neuroscience : the official journal of the Society for Neuroscience, 33(10), 4213–4215. https://doi.org/10.1523/JNEUROSCI.0041-13.2013

Comment 2: It could still equally well be the case that other regions or networks relevant for gesture-speech integration are targeted, and it can still be the case that these timewindows are not specific, and effects bleed into other time periods. There seems to be no experimental evidence here that this is not the case.

The selection of IFG and pMTG as regions of interest was rigorously justified through multiple lines of evidence. First, a comprehensive meta-analysis of fMRI studies on gesture-speech integration consistently identified these regions as central nodes (see response to comment 1). Second, our own previous work (Zhao et al., 2018, JN; 2021, JN) provided direct empirical validation of their involvement. Third, by employing the same experimental paradigm, we minimized the likelihood of engaging alternative networks. Fourth, even if other regions connected to IFG or pMTG might be affected by TMS, the distinct engagement of specific time windows of IFG and pMTG minimizes the likelihood of consistent influence from other regions.

Regarding temporal specificity, our 2021 study (Zhao et al., 2021, JN, see details in response to comment 1) systematically examined the entire 0-320ms integration window and found that only select time windows showed significant effects for gesture-speech semantic congruency, while remaining unaffected during gender congruency processing. This double dissociation (significant effects for semantic integration but not gender processing in specific windows) rules out broad temporal spillover.

Comment 3: To be more specific, the authors write that double-pulse TMS has been widely used in previous studies (as found in their table). However, the studies cited in the table do not necessarily demonstrate the level of spatial and temporal specificity required to disentangle the contributions of tightly-coupled brain regions like the IFG and pMTG during the speech-gesture integration process. pMTG and IFG are located in very close proximity, and are known to be functionally and structurally interconnected, something that is not necessarily the case for the relatively large and/or anatomically distinct areas that the authors mention in their table.

Our methodological approach is strongly supported by an established body of research employing double-pulse TMS (dpTMS) to investigate neural dynamics across both primary motor and higher-order cognitive regions. As documented in Author response table 1, multiple studies have successfully applied this technique to: (1) primary motor areas (tongue and lip representations in M1), and (2) semantic processing regions (including pMTG, PFC, and ATL). Particularly relevant precedents include:

(1) Teige et al. (2018, Cortex): Demonstrated precise spatial and temporal specificity by applying 40ms-interval dpTMS to ATL, pMTG, and mid-MTG across multiple time windows (0-40ms, 125-165ms, 250-290ms, 450-490ms), revealing distinct functional contributions from ATL versus pMTG.

(2) Vernet et al. (2015, Cortex): Successfully dissociated functional contributions of right IPS and DLPFC using 40ms-interval dpTMS, despite their anatomical proximity and functional connectivity.

These studies confirm double-pulse TMS can discriminate interconnected nodes at short timescales. Our 2021 study further validated this for IFG-pMTG.

Author response table 2.

Double-pulse TMS studies on brain regions over 3-60 ms time interval

References:

Teige, C., Mollo, G., Millman, R., Savill, N., Smallwood, J., Cornelissen, P. L., & Jefferies, E. (2018). Dynamic semantic cognition: Characterising coherent and controlled conceptual retrieval through time using magnetoencephalography and chronometric transcranial magnetic stimulation. Cortex, 103, 329-349.

Vernet, M., Brem, A. K., Farzan, F., & Pascual-Leone, A. (2015). Synchronous and opposite roles of the parietal and prefrontal cortices in bistable perception: a double-coil TMS–EEG study. Cortex, 64, 78-88.

Comment 4: But also more in general: The mere fact that these methods have been used in other contexts does not necessarily mean they are appropriate or sufficient for investigating the current research question. Likewise, the cognitive processes involved in these studies are quite different from the complex, multimodal integration of gesture and speech. The authors have not provided a strong theoretical justification for why the temporal dynamics observed in these previous studies should generalize to the specific mechanisms of gesture-speech integration..

The neurophysiological mechanisms underlying double-pulse TMS (dpTMS) are well-characterized. While it is established that single-pulse TMS can produce brief artifacts (typically within 0–10 ms) due to transient cortical depolarization (Romero et al., 2019, NC), the dynamics of double-pulse TMS (dpTMS) involve more intricate inhibitory interactions. Specifically, the first pulse increases membrane conductance via GABAergic shunting inhibition, effectively lowering membrane resistance and attenuating the excitatory impact of the second pulse. This results in a measurable reduction in cortical excitability at the paired-pulse interval, as evidenced by suppressed motor evoked potentials (MEPs) (Paulus & Rothwell, 2016, J Physiol). Importantly, this neurophysiological mechanism is independent of cognitive domain and has been robustly demonstrated across multiple functional paradigms.

In our study, we did not rely on previously reported timing parameters but instead employed a dpTMS protocol using a 40-ms inter-pulse interval. Based on the inhibitory dynamics of this protocol, we designed a sliding temporal window sufficiently broad to encompass the integration period of interest. This approach enabled us to capture and localize the critical temporal window associated with ongoing integrative processing in the targeted brain region.

We acknowledge that the previous phrasing may have been ambiguous, a clearer and more detailed description of the dpTMS protocol has now been provided in Lines 88-92: “To this end, we employed chronometric double-pulse transcranial magnetic stimulation, which is known to transiently reduce cortical excitability at the inter-pulse interval]27]. Within a temporal period broad enough to capture the full duration of gesture–speech integration[28], we targeted specific timepoints previously implicated in integrative processing within IFG and pMTG [23].”

References:

Romero, M.C., Davare, M., Armendariz, M. et al. Neural effects of transcranial magnetic stimulation at the single-cell level. Nat Commun 10, 2642 (2019). https://doi.org/10.1038/s41467-019-10638-7

Paulus W, Rothwell JC. Membrane resistance and shunting inhibition: where biophysics meets state-dependent human neurophysiology. J Physiol. 2016 May 15;594(10):2719-28. doi: 10.1113/JP271452. PMID: 26940751; PMCID: PMC4865581.

Obermeier, C., & Gunter, T. C. (2015). Multisensory Integration: The Case of a Time Window of Gesture-Speech Integration. Journal of Cognitive Neuroscience, 27(2), 292-307. https://doi.org/10.1162/jocn_a_00688

Comment 5: Moreover, the studies cited in the table provided by the authors have used a wide range of interpulse intervals, from 20 ms to 100 ms, suggesting that the temporal precision required to capture the dynamics of gesture-speech integration (which is believed to occur within 200-300 ms; Obermeier & Gunter, 2015) may not even be achievable with their 40 ms time windows.

Double-pulse TMS has been empirically validated across neurocognitive studies as an effective method for establishing causal temporal relationships in cortical networks, with demonstrated sensitivity at timescales spanning 3-60 m. Our selection of a 40-ms interpulse interval represents an optimal compromise between temporal precision and physiological feasibility, as evidenced by its successful application in dissociating functional contributions of interconnected regions including ATL/pMTG (Teige et al., 2018) and IPS/DLPFC (Vernet et al., 2015). This methodological approach combines established experimental rigor with demonstrated empirical validity for investigating the precisely timed IFG-pMTG dynamics underlying gesture-speech integration, as shown in our current findings and prior work (Zhao et al., 2021).

Our experimental design comprehensively sampled the 0-320 ms post-stimulus period, fully encompassing the critical 200-300 ms window associated with gesture-speech integration, as raised by the reviewer. Notably, our results revealed temporally distinct causal dynamics within this period: the significantly reduced semantic congruency effect emerged at IFG at 200-240ms, followed by feedback projections from IFG to pMTG at 240-280ms. This precisely timed interaction provides direct neurophysiological evidence for the proposed architecture of gesture-speech integration, demonstrating how these interconnected regions sequentially contribute to multisensory semantic integration.

Comment 6: I do appreciate the extra analyses that the authors mention. However, my 5th comment is still unanswered: why not use entropy scores as a continous measure?

Analysis with MI and entropy as continuous variables were conducted employing Representational Similarity Analysis (RSA) (Popal et.al, 2019). This analysis aimed to build a model to predict neural responses based on these feature metrics.

To capture dynamic temporal features indicative of different stages of multisensory integration, we segmented the EEG data into overlapping time windows (40 ms in duration with a 10 ms step size). The 40 ms window was chosen based on the TMS protocol used in Experiment 2, which also employed a 40 ms time window. The 10 ms step size (equivalent to 5 time points) was used to detect subtle shifts in neural responses that might not be captured by larger time windows, allowing for a more granular analysis of the temporal dynamics of neural activity.

Following segmentation, the EEG data were reshaped into a four-dimensional matrix (42 channels × 20 time points × 97 time windows × 20 features). To construct a neural similarity matrix, we averaged the EEG data across time points within each channel and each time window. The resulting matrix was then processed using the pdist function to compute pairwise distances between adjacent data points. This allowed us to calculate correlations between the neural matrix and three feature similarity matrices, which were constructed in a similar manner. These three matrices corresponded to (1) gesture entropy, (2) speech entropy, and (3) mutual information (MI). This approach enabled us to quantify how well the neural responses corresponded to the semantic dimensions of gesture and speech stimuli at each time window.

To determine the significance of the correlations between neural activity and feature matrices, we conducted 1000 permutation tests. In this procedure, we randomized the data or feature matrices and recalculated the correlations repeatedly, generating a null distribution against which the observed correlation values were compared. Statistical significance was determined if the observed correlation exceeded the null distribution threshold (p < 0.05). This permutation approach helps mitigate the risk of spurious correlations, ensuring that the relationships between the neural data and feature matrices are both robust and meaningful.

Finally, significant correlations were subjected to clustering analysis, which grouped similar neural response patterns across time windows and channels. This clustering allowed us to identify temporal and spatial patterns in the neural data that consistently aligned with the semantic features of gesture and speech stimuli, thus revealing the dynamic integration of these multisensory modalities across time. Results are as follows:

(1)  Two significant clusters were identified for gesture entropy (Figure 1 left). The first cluster was observed between 60-110 ms (channels F1 and F3), with correlation coefficients (r) ranging from 0.207 to 0.236 (p < 0.001). The second cluster was found between 210-280 ms (channel O1), with r-values ranging from 0.244 to 0.313 (p < 0.001).

(2)  For speech entropy (Figure 1 middle), significant clusters were detected in both early and late time windows. In the early time windows, the largest significant cluster was found between 10-170 ms (channels F2, F4, F6, FC2, FC4, FC6, C4, C6, CP4, and CP6), with r-values ranging from 0.151 to 0.340 (p = 0.013), corresponding to the P1 component (0-100 ms). In the late time windows, the largest significant cluster was observed between 560-920 ms (across the whole brain, all channels), with r-values ranging from 0.152 to 0.619 (p = 0.013).

(3)  For mutual information (MI) (Figure 1 right), a significant cluster was found between 270-380 ms (channels FC1, FC2, FC3, FC5, C1, C2, C3, C5, CP1, CP2, CP3, CP5, FCz, Cz, and CPz), with r-values ranging from 0.198 to 0.372 (p = 0.001).

Author response image 1.

Results of RSA analysis.

These additional findings suggest that even using a different modeling approach, neural responses, as indexed by feature metrics of entropy and mutual information, are temporally aligned with distinct ERP components and ERP clusters, as reported in the current manuscript. This alignment serves to further consolidate the results, reinforcing the conclusion we draw. Considering the length of the manuscript, we did not include these results in the current manuscript.

Reference:

Popal, H., Wang, Y., & Olson, I. R. (2019). A guide to representational similarity analysis for social neuroscience. Social cognitive and affective neuroscience, 14(11), 1243-1253.

Comment 7: In light of these concerns, I do not believe the authors have adequately demonstrated the spatial and temporal specificity required to disentangle the contributions of the IFG and pMTG during the gesture-speech integration process. While the authors have made a sincere effort to address the concerns raised by the reviewers, and have done so with a lot of new analyses, I remain doubtful that the current methodological approach is sufficient to draw conclusions about the causal roles of the IFG and pMTG in gesture-speech integration.

To sum up:

(1) Empirical validation from our prior work (Zhao et al., 2018,2021,JN): The selection of IFG and pMTG as target regions was informed by both: (1) a comprehensive meta-analysis of fMRI studies on gesture-speech integration, and (2) our own prior causal evidence from Zhao et al. (2018, J Neurosci), with detailed stereotactic coordinates provided in the attached Response to Editors and Reviewers letter. The temporal parameters were similarly grounded in empirical data from Zhao et al. (2021, J Neurosci), where we systematically examined eight consecutive 40-ms windows spanning the full integration period (0-320 ms). This study revealed a triple dissociation of effects - occurring exclusively during: (i)semantic integration (but not control tasks), (ii) active stimulation (but not sham), and (iii) specific time windows (but not all time windows)- providing robust causal evidence for the spatiotemporal specificity of IFG-pMTG interactions in gesture-speech processing. Notably, all reviewers recognized the methodological strength of this dpTMS approach in their evaluations (see attached JN assessment for details).

(2) Convergent evidence from Experiment 3: Our study employed a multi-method approach incorporating three complementary experimental paradigms, each utilizing distinct neurophysiological techniques to provide converging evidence. Specifically, Experiment 3 implemented high-temporal-resolution EEG, which independently replicated the time-sensitive dynamics of gesture-speech integration observed in our double-pulse TMS experiments. The remarkable convergence between these methodologically independent approaches -demonstrating consistent temporal staging of IFG-pMTG interactions across both causal (TMS) and correlational (EEG) measures - significantly strengthens the validity and generalizability of our conclusions regarding the neural mechanisms underlying multisensory integration.

(3) Established precedents in double-pulse TMS literature: The double-pulse TMS methodology employed in our study is firmly grounded in established neuroscience research. As documented in our detailed Response to Editors and Reviewers letter (citing 11 representative studies), dpTMS has been extensively validated for investigating causal temporal dynamics in cortical networks, with demonstrated sensitivity at timescales ranging from 3-60 ms. Particularly relevant precedents include: 1. Teige et al. (2018, Cortex) successfully dissociated functional contributions of anatomically proximal regions (ATL vs. pMTG vs.mid-MTG) using 40-ms-interval double-pulse TMS; 2. Vernet et al. (2015, Cortex) effectively distinguished neural processing in interconnected frontoparietal regions (right IPS vs. DLPFC) using 40-ms double-pulse TMS parameters. Both parameters are identical to those employed in our current study.

(4) Neurophysiological Plausibility: The neurophysiological basis for the transient double-pulse TMS effects is well-established through mechanistic studies of TMS-induced cortical inhibition (Romero et al.,2019; Paulus & Rothwell, 2016).

Taking together, we respectfully submit that our methodology provides robust support for our conclusions.

Author response:

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

Public Reviews:

Reviewer #1:

Summary:

The work by Combrisson and colleagues investigates the degree to which reward and punishment learning signals overlap in the human brain using intracranial EEG recordings. The authors used information theory approaches to show that local field potential signals in the anterior insula and the three sub regions of the prefrontal cortex encode both reward and punishment prediction errors, albeit to different degrees. Specifically, the authors found that all four regions have electrodes that can selectively encode either the reward or the punishment prediction errors. Additionally, the authors analyzed the neural dynamics across pairs of brain regions and found that the anterior insula to dorsolateral prefrontal cortex neural interactions were specific for punishment prediction errors whereas the ventromedial prefrontal cortex to lateral orbitofrontal cortex interactions were specific to reward prediction errors. This work contributes to the ongoing efforts in both systems neuroscience and learning theory by demonstrating how two differing behavioral signals can be differentiated to a greater extent by analyzing neural interactions between regions as opposed to studying neural signals within one region.

Strengths:

The experimental paradigm incorporates both a reward and punishment component that enables investigating both types of learning in the same group of subjects allowing direct comparisons.

The use of intracranial EEG signals provides much needed insight into the timing of when reward and punishment prediction errors signals emerge in the studied brain regions.

Information theory methods provide important insight into the interregional dynamics associated with reward and punishment learning and allows the authors to assess that reward versus punishment learning can be better dissociated based on interregional dynamics over local activity alone.

We thank the reviewer for this accurate summary. Please find below our answers to the weaknesses raised by the reviewer.

Weaknesses:

The analysis presented in the manuscript focuses solely on gamma band activity. The presence and potential relevance of other frequency bands is not discussed. It is possible that slow oscillations, which are thought to be important for coordinating neural activity across brain regions could provide additional insight.

We thank the reviewer for pointing us to this missing discussion in the first version of the manuscript. We now made this point clearer in the Methods sections entitled “iEEG data analysis” and “Estimate of single-trial gamma-band activity”:

“Here, we focused solely on broadband gamma for three main reasons. First, it has been shown that the gamma band activity correlates with both spiking activity and the BOLD fMRI signals (Lachaux et al., 2007; Mukamel et al., 2004; Niessing et al., 2005; Nir et al., 2007), and it is commonly used in MEG and iEEG studies to map task-related brain regions (Brovelli et al., 2005; Crone et al., 2006; Vidal et al., 2006; Ball et al., 2008; Jerbi et al., 2009; Darvas et al., 2010; Lachaux et al., 2012; Cheyne and Ferrari, 2013; Ko et al., 2013). Therefore, focusing on the gamma band facilitates linking our results with the fMRI and spiking literatures on probabilistic learning. Second, single-trial and time-resolved high-gamma activity can be exploited for the analysis of cortico-cortical interactions in humans using MEG and iEEG techniques (Brovelli et al., 2015; 2017; Combrisson et al., 2022). Finally, while previous analyses of the current dataset (Gueguen et al., 2021) reported an encoding of PE signals at different frequency bands, the power in lower frequency bands were shown to carry redundant information compared to the gamma band power.”

The data is averaged across all electrodes which could introduce biases if some subjects had many more electrodes than others. Controlling for this variation in electrode number across subjects would ensure that the results are not driven by a small subset of subjects with more electrodes.

We thank the reviewer for raising this important issue. We would like to point out that the gamma activity was not averaged across bipolar recordings within an area, nor measures of connectivity. Instead, we used a statistical approach proposed in a previous paper that combines non-parametric permutations with measures of information (Combrisson et al., 2022). As we explain in the “Statistical analysis” section, mutual information (MI) is estimated between PE signals and single-trial modulations in gamma activity separately for each contact (or for each pair of contacts). Then, a one-sample t-test is computed across all of the recordings of all subjects to form the effect size at the group-level. We will address the point of the electrode number in our answer below.

The potential variation in reward versus punishment learning across subjects is not included in the manuscript. While the time course of reward versus punishment prediction errors is symmetrical at the group level, it is possible that some subjects show faster learning for one versus the other type which can bias the group average. Subject level behavioral data along with subject level electrode numbers would provide more convincing evidence that the observed effects are not arising from these potential confounds.

We thank the reviewer for the two points raised. We performed additional analyses at the single-participant level to address the issues raised by the reviewer. We should note, however, that these results are descriptive and cannot be generalized to account for population-level effects. As suggested by the reviewer, we prepared two new figures. The first supplementary figure summarizes the number of participants that had iEEG contacts per brain region and pair of brain regions (Fig. S1A in the Appendix). It can be seen that the number of participants sampled in different brain regions is relatively constant (left panel) and the number of participants with pairs of contacts across brain regions is relatively homogeneous, ranging from 7 to 11 (right panel). Fig. S1B shows the number of bipolar derivations per subject and per brain region.

Author response image 1.

Single subject anatomical repartition. (A) Number of unique subject per brain region and per pair of brain regions (B) Number of bipolar derivations per subject and per brain region

The second supplementary figure describes the estimated prediction error for rewarding and punishing trials for each subject (Fig. S2). The single-subject error bars represent the 95th percentile confidence interval estimated using a bootstrap approach across the different pairs of stimuli presented during the three to six sessions. As the reviewer anticipated, there are indeed variations across subjects, but we observe that RPE and PPE are relatively symmetrical, even at the subject level, and tend toward zero around trial number 10. These results therefore corroborate the patterns observed at the group-level.

Author response image 2.

Single-subject estimation of predictions errors. Single-subject trial-wise reward PE (RPE - blue) and punishment PE (PPE - red), ± 95% confidence interval.

Finally, to assess the variability of local encoding of prediction errors across participants, we quantified the proportion of subjects having at least one significant bipolar derivation encoding either the RPE or PPE (Fig. S4). As expected, we found various proportions of unique subjects with significant R/PPE encoding per region. The lowest proportion was achieved in the ventromedial prefrontal cortex (vmPFC) and lateral orbitofrontal cortex (lOFC) for encoding PPE and RPE, respectively, with approximately 30% of the subjects having the effect. Conversely, we found highly reproducible encodings in the anterior insula (aINS) and dorsolateral prefrontal cortex (dlPFC) with a maximum of 100% of the 9 subjects having at least one bipolar derivation encoding PPE in the dlPFC.

Author response image 3.

Taken together, we acknowledge a certain variability per region and per condition. Nevertheless, the results presented in the supplementary figures suggest that the main results do not arise from a minority of subjects.

We would like to point out that in order to assess across-subject variability, a much larger number of participants would have been needed, given the low signal-to-noise ratios observed at the single-participant level. We thus prefer to add these results as supplementary material in the Appendix, rather than in the main text.

It is unclear if the findings in Figures 3 and 4 truly reflect the differential interregional dynamics in reward versus punishment learning or if these results arise as a statistical byproduct of the reward vs punishment bias observed within each region. For instance, the authors show that information transfer from anterior insula to dorsolateral prefrontal cortex is specific to punishment prediction error. However, both anterior insula and dorsolateral prefrontal cortex have higher prevalence of punishment prediction error selective electrodes to begin with. Therefore the findings in Fig 3 may simply be reflecting the prevalence of punishment specificity in these two regions above and beyond a punishment specific neural interaction between the two regions. Either mathematical or analytical evidence that assesses if the interaction effect is simply reflecting the local dynamics would be important to make this result convincing.

This is an important point that we partly addressed in the manuscript. More precisely, we investigated whether the synergistic effects observed between the dlPFC and vmPFC encoding global PEs (Fig. 5) could be explained by their respective local specificity. Indeed, since we reported larger proportions of recordings encoding the PPE in the dlPFC and the RPE in the vmPFC (Fig. 2B), we checked whether the synergy between dlPFC and vmPFC could be mainly due to complementary roles where the dlPFC brings information about the PPE only and the vmPFC brings information to the RPE only. To address this point, we selected PPE-specific bipolar derivations from the dlPFC and RPE-specific from the vmPFC and, as the reviewer predicted, we found synergistic II between the two regions probably mainly because of their respective specificity. In addition, we included the II estimated between non-selective bipolar derivations (i.e. recordings with significant encoding for both RPE and PPE) and we observed synergistic interactions (Fig. 5C and Fig. S9). Taken together, the local specificity certainly plays a role, but this is not the only factor in defining the type of interactions.

Concerning the interaction information results (II, Fig. 3), several lines of evidence suggest that local specificity cannot account alone for the II effects. For example, the local specificity for PPE is observed across all four areas (Fig. 2A) and the percentage of bipolar derivations displaying an effect is large (equal or above 10%) for three brain regions (aINS, dlPLF and lOFC). If the local specificity were the main driving cause, we would have observed significant redundancy between all pairs of brain regions. On the other hand, the interaction between the aINS and lOFC displayed no significant redundant effect (Fig. 3B). Another example is the result observed in lOFC: approximately 30% of bipolar derivations display a selectivity for PPE (Fig. 2B, third panel from the left), but do not show clear signs of redundant encoding at the level of within-area interactions (Fig. 3A, bottom-left panel). Similarly, the local encoding for RPE is observed across all four brain regions (Fig. 2A) and the percentage of bipolar derivations displaying an effect is large (equal or above 10%) for three brain regions (aINS, dlPLF and vmPFC). Nevertheless, significant between-regions interactions have been observed only between the lOFC and vmPFC (Fig. 3B bottom right panel).

To further support the reasoning, we performed a simulation to show that it is possible to observe synergistic interactions between two regions with the same specificity. As an example, we may consider one region locally encoding early trials of RPE and a second region encoding the late trials of the RPE. Combining the two with the II would lead to synergistic interactions, because each one of them carries information that is not carried by the other. To illustrate this point, we simulated the data of two regions (x and y). To simulate redundant interactions (first row), each region receives a copy of the prediction (one-to-all) and for the synergy (second row), x and y receive early and late PE trials, respectively (all-to-one). This toy example illustrates that the local specificity is not the only factor determining the type of their interactions. We added the following result to the Appendix.

Author response image 4.

Local specificity does not fully determine the type of interactions. Within-area local encoding of PE using the mutual information (MI, in bits) for regions X and Y and between-area interaction information (II, in bits) leading to (A) redundant interactions and (B) synergistic interactions about the PE

Regarding the information transfer results (Fig. 4), similar arguments hold and suggest that the prevalence is not the main factor explaining the arising transfer entropy between the anterior insula (aINS) and dorsolateral prefrontal cortex (dlPFC). Indeed, the lOFC has a strong local specificity for PPE, but the transfer entropy between the lOFC and aINS (or dlPFC) is shown in Fig. S7 does not show significant differences in encoding between PPE and RPE.

Indeed, such transfer can only be found when there is a delay between the gamma activity of the two regions. In this example, the transfer entropy quantifies the amount of information shared between the past activity of the aINS and the present activity of the dlPFC conditioned on the past activity of the dlPFC. The conditioning ensures that the present activity of the dlPFC is not only explained by its own past. Consequently, if both regions exhibit various prevalences toward reward and punishment but without delay (i.e. at the same timing), the transfer entropy would be null because of the conditioning. As a fact, between 10 to -20% of bipolar recordings show a selectivity to the reward PE (represented by a proportion of 40-60% of subjects, Fig.S4). However, the transfer entropy estimated from the aINS to the dlPFC across rewarding trials is flat and clearly non-significant. If the transfer entropy was a byproduct of the local specificity then we should observe an increase, which is not the case here.

Reviewer #2:

Summary:

Reward and punishment learning have long been seen as emerging from separate networks of frontal and subcortical areas, often studied separately. Nevertheless, both systems are complimentary and distributed representations of rewards and punishments have been repeatedly observed within multiple areas. This raised the unsolved question of the possible mechanisms by which both systems might interact, which this manuscript went after. The authors skillfully leveraged intracranial recordings in epileptic patients performing a probabilistic learning task combined with model-based information theoretical analyses of gamma activities to reveal that information about reward and punishment was not only distributed across multiple prefrontal and insular regions, but that each system showed specific redundant interactions. The reward subsystem was characterized by redundant interactions between orbitofrontal and ventromedial prefrontal cortex, while the punishment subsystem relied on insular and dorsolateral redundant interactions. Finally, the authors revealed a way by which the two systems might interact, through synergistic interaction between ventromedial and dorsolateral prefrontal cortex.

Strengths:

Here, the authors performed an excellent reanalysis of a unique dataset using innovative approaches, pushing our understanding on the interaction at play between prefrontal and insular cortex regions during learning. Importantly, the description of the methods and results is truly made accessible, making it an excellent resource to the community.

This manuscript goes beyond what is classically performed using intracranial EEG dataset, by not only reporting where a given information, like reward and punishment prediction errors, is represented but also by characterizing the functional interactions that might underlie such representations. The authors highlight the distributed nature of frontal cortex representations and propose new ways by which the information specifically flows between nodes. This work is well placed to unify our understanding of the complementarity and specificity of the reward and punishment learning systems.

We thank the reviewer for the positive feedback. Please find below our answers to the weaknesses raised by the reviewer.

Weaknesses:

The conclusions of this paper are mostly supported by the data, but whether the findings are entirely generalizable would require further information/analyses.

First, the authors found that prediction errors very quickly converge toward 0 (less than 10 trials) while subjects performed the task for sets of 96 trials. Considering all trials, and therefore having a non-uniform distribution of prediction errors, could potentially bias the various estimates the authors are extracting. Separating trials between learning (at the start of a set) and exploiting periods could prove that the observed functional interactions are specific to the learning stages, which would strengthen the results.

We thank the reviewer for this question. We would like to note that the probabilistic nature of the learning task does not allow a strict distinction between the exploration and exploitation phases. Indeed, the probability of obtaining the less rewarding outcome was 25% (i.e., for 0€ gain in the reward learning condition and -1€ loss in the punishment learning condition). Thus, participants tended to explore even during the last set of trials in each session. This is evident from the average learning curves shown in Fig. 1B of (Gueguen et al., 2021). Learning curves show rates of correct choice (75% chance of 1€ gain) in the reward condition (blue curves) and incorrect choice (75% chance of 1€ loss) in the punishment condition (red curves).

For what concerns the evolution of PEs, as reviewer #1 suggested, we added a new figure representing the single-subject estimates of the R/PPE (Fig S2). Here, the confidence interval is obtained across all pairs of stimuli presented during the different sessions. We retrieved the general trend of the R/PPE converging toward zero around 10 trials. Both average reward and punishment prediction errors converge toward zero in approximately 10 trials, single-participant curves display large variability, also at the end of each session. As a reminder, the 96 trials represent the total number of trials for one session for the four pairs and the number of trials for each stimulus was only 24.

Author response image 5.

Single-subject estimation of predictions errors. Single-subject trial-wise reward PE (RPE - blue) and punishment PE (PPE - red), ± 95% confidence interval

However, the convergence of the R/PPE is due to the average across the pairs of stimuli. In the figure below, we superimposed the estimated R/PPE, per pair of stimuli, for each subject. It becomes very clear that high values of PE can be reached, even for late trials. Therefore, we believe that the split into early/late trials because of the convergence of PE is far from being trivial.

Author response image 6.

Single-subject estimation of predictions errors per pair of stimuli. Single-subject trial-wise reward PE (RPE - blue) and punishment PE (PPE - red)

Consequently, nonzero PRE and PPE occur during the whole session and separating trials between learning (at the start of a set) and exploiting periods, as suggested by the reviewer, does not allow a strict dissociation between learning vs no-learning. Nevertheless, we tested the analysis proposed by the reviewer, at the local level. We splitted the 24 trials of each pair of stimuli into early, middle and late trials (8 trials each). We then reproduced Fig. 2 by computing the mutual information between the gamma activity and the R/PPE for subsets of trials: early (first row) and late trials (second row). We retrieved significant encoding of both R/PPE in the aINS, dlPFC and lOFC in both early and late trials. The vmPFC also showed significant encoding of both during early trials. The only difference emerges in the late trials of the vmPFC where we found a strong encoding of the RPE only. It should also be noted that here since we are sub-selecting the trials, the statistical analyses are only performed using a third of the trials.

Taken together, the combination of high values of PE achieved even for late trials and the fact that most of the findings are reproduced even with a third of the trials does not justify the split into early and late trials here. Crucially, this latest analysis confirms that the neural correlates of learning that we observed reflect PE signals rather than early versus late trials in the session.

Author response image 7.

MI between gamma activity and R/PPE using early and late trials. Time courses of MI estimated between the gamma power and both RPE (blue) and PPE (red) using either early or late trials (first and second row, respectively). Horizontal thick lines represent significant clusters of information (p<0.05, cluster-based correction, non-parametric randomization across epochs).

Importantly, it is unclear whether the results described are a common feature observed across subjects or the results of a minority of them. The authors should report and assess the reliability of each result across subjects. For example, the authors found RPE-specific interactions between vmPFC and lOFC, even though less than 10% of sites represent RPE or both RPE/PPE in lOFC. It is questionable whether such a low proportion of sites might come from different subjects, and therefore whether the interactions observed are truly observed in multiple subjects. The nature of the dataset obviously precludes from requiring all subjects to show all effects (given the known limits inherent to intracerebral recording in patients), but it should be proven that the effects were reproducibly seen across multiple subjects.

We thank the reviewer for this remark that has also been raised by the first reviewer. This issue was raised by the first reviewer. Indeed, we added a supplementary figure describing the number of unique subjects per brain region and per pair of brain regions (Fig. S1A) such as the number of bipolar derivations per region and per subject (Fig. S1B).

Author response image 8.

Single subject anatomical repartition. (A) Number of unique subject per brain region and per pair of brain regions (B) Number of bipolar derivations per subject and per brain region

Regarding the reproducibility of the results across subjects for the local analysis (Fig. 2), we also added the instantaneous proportion of subjects having at least one bipolar derivation showing a significant encoding of the RPE and PPE (Fig. S4). We found a minimum proportion of approximately 30% of unique subjects having the effect in the lOFC and vmPFC, respectively with the RPE and PPE. On the other hand, both the aINS and dlPFC showed between 50 to 100% of the subjects having the effect. Therefore, local encoding of RPE and PPE was never represented by a single subject.

Author response image 9.

Similarly, we performed statistical analysis on interaction information at the single-subject level and counted the proportion of unique subjects having at least one pair of recordings with significant redundant and synergistic interactions about the RPE and PPE (Fig. S5). Consistently with the results shown in Fig. 3, the proportions of significant redundant and synergistic interactions are negative and positive, respectively. For the within-regions interactions, approximately 60% of the subjects with redundant interactions are about R/PPE in the aINS and about the PPE in the dlPFC and 40% about the RPE in the vmPFC. For the across-regions interactions, 60% of the subjects have redundant interactions between the aINS-dlPFC and dlPFC-lOFC about the PPE, and 30% have redundant interactions between lOFC-vmPFC about the RPE. Globally, we reproduced the main results shown in Fig. 3.

Author response image 10.

Inter-subjects reproducibility of redundant interactions about PE signals. Time-courses of proportion of subjects having at least one pair of bipolar derivation with a significant interaction information (p<0.05, cluster-based correction, non-parametric randomization across epochs) about the RPE (blue) or PPE (red). Data are aligned to the outcome presentation (vertical line at 0 seconds). Proportion of subjects with redundant (solid) and synergistic (dashed) interactions are respectively going downward and upward.

Finally, the timings of the observed interactions between areas preclude one of the authors' main conclusions. Specifically, the authors repeatedly concluded that the encoding of RPE/PPE signals are "emerging" from redundancy-dominated prefrontal-insular interactions. However, the between-region information and transfer entropy between vmPFC and lOFC for example is observed almost 500ms after the encoding of RPE/PPE in these regions, questioning how it could possibly lead to the encoding of RPE/PPE. It is also noteworthy that the two information measures, interaction information and transfer entropy, between these areas happened at non overlapping time windows, questioning the underlying mechanism of the communication at play (see Figures 3/4). As an aside, when assessing the direction of information flow, the authors also found delays between pairs of signals peaking at 176ms, far beyond what would be expected for direct communication between nodes. Discussing this aspect might also be of importance as it raises the possibility of third-party involvement.

The local encoding of RPE in the vmPFC and lOFC is observed in a time interval ranging from approximately 0.2-0.4s to 1.2-1.4s after outcome presentation (blue bars in Fig. 2A). The encoding of RPE by interaction information covers a time interval from approximately 1.1s to 1.5s (blue bars in Fig. 3B, bottom right panel). Similarly, significant TE modulations between the vmPFC and lOFC specific for PPE occur mainly in the 0.7s-1.1s range. Thus, it seems that the local encoding of PPE precedes the effects observed at the level of the neural interactions (II and TE). On the other hand, the modulations in MI, II and TE related to PPE co-occur in a time window from 0.2s to 0.7s after outcome presentation. Thus, we agree with the reviewer that a generic conclusion about the potential mechanisms relating the three levels of analysis cannot be drawn. We thus replaced the term “emerge from” by “occur with” from the manuscript which may be misinterpreted as hinting at a potential mechanism. We nevertheless concluded that the three levels of analysis (and phenomena) co-occur in time, thus hinting at a potential across-scales interaction that needs further study. Indeed, our study suggests that further work, beyond the scope of the current study, is required to better understand the interaction between scales.

Regarding the delay for the conditioning of the transfer entropy, the value of 176 ms reflects the delay at which we observed a maximum of transfer entropy. However, we did not use a single delay for conditioning, we used every possible delay between [116, 236] ms, as explained in the Method section. We would like to stress that transfer entropy is a directed metric of functional connectivity, and it can only be interpreted as quantifying statistical causality defined in terms of predictacìbility according to the Wiener-Granger principle, as detailed in the methods. Thus, it cannot be interpreted in Pearl’s causal terms and as indexing any type of direct communication between nodes. This is a known limitation of the method, which has been stressed in past literature and that we believe does not need to be addressed here.

To account for this, we revised the discussion to make sure this issue is addressed in the following paragraph:

“Here, we quantified directional relationships between regions using the transfer entropy (Schreiber, 2000), which is a functional connectivity measure based on the Granger-Wiener causality principle. Tract tracing studies in the macaque have revealed strong interconnections between the lOFC and vmPFC in the macaque (Carmichael and Price, 1996; Öngür and Price, 2000). In humans, cortico-cortical anatomical connections have mainly been investigated using diffusion magnetic resonance imaging (dMRI). Several studies found strong probabilities of structural connectivity between the anterior insula with the orbitofrontal cortex and dorsolateral part of the prefrontal cortex (Cloutman et al., 2012; Ghaziri et al., 2017), and between the lOFC and vmPFC (Heather Hsu et al., 2020). In addition, the statistical dependency (e.g. coherence) between the LFP of distant areas could be potentially explained by direct anatomical connections (Schneider et al., 2021; Vinck et al., 2023). Taken together, the existence of an information transfer might rely on both direct or indirect structural connectivity. However, here we also reported differences of TE between rewarding and punishing trials given the same backbone anatomical connectivity (Fig. 4). [...] “

Reviewer #3:

Summary:

The authors investigated that learning processes relied on distinct reward or punishment outcomes in probabilistic instrumental learning tasks were involved in functional interactions of two different cortico-cortical gamma-band modulations, suggesting that learning signals like reward or punishment prediction errors can be processed by two dominated interactions, such as areas lOFC-vmPFC and areas aINS-dlPFC, and later on integrated together in support of switching conditions between reward and punishment learning. By performing the well-known analyses of mutual information, interaction information, and transfer entropy, the conclusion was accomplished by identifying directional task information flow between redundancy-dominated and synergy-dominated interactions. Also, this integral concept provided a unifying view to explain how functional distributed reward and/or punishment information were segregated and integrated across cortical areas.

Strengths:

The dataset used in this manuscript may come from previously published works (Gueguen et al., 2021) or from the same grant project due to the methods. Previous works have shown strong evidence about why gamma-band activities and those 4 areas are important. For further analyses, the current manuscript moved the ideas forward to examine how reward/punishment information transfer between recorded areas corresponding to the task conditions. The standard measurements such mutual information, interaction information, and transfer entropy showed time-series activities in the millisecond level and allowed us to learn the directional information flow during a certain window. In addition, the diagram in Figure 6 summarized the results and proposed an integral concept with functional heterogeneities in cortical areas. These findings in this manuscript will support the ideas from human fMRI studies and add a new insight to electrophysiological studies with the non-human primates.

We thank the reviewer for the summary such as for highlighting the strengths. Please find below our answers regarding the weaknesses of the manuscript.

Weaknesses:

After reading through the manuscript, the term "non-selective" in the abstract confused me and I did not actually know what it meant and how it fits the conclusion. If I learned the methods correctly, the 4 areas were studied in this manuscript because of their selective responses to the RPE and PPE signals (Figure 2). The redundancy- and synergy-dominated subsystems indicated that two areas shared similar and complementary information, respectively, due to the negative and positive value of interaction information (Page 6). For me, it doesn't mean they are "non-selective", especially in redundancy-dominated subsystem. I may miss something about how you calculate the mutual information or interaction information. Could you elaborate this and explain what the "non-selective" means?

In the study performed by Gueguen et al. in 2021, the authors used a general linear model (GLM) to link the gamma activity to both the reward and punishment prediction errors and they looked for differences between the two conditions. Here, we reproduced this analysis except that we used measures from the information theory (mutual information) that were able to capture linear and non-linear relationships (although monotonic) between the gamma activity and the prediction errors. The clusters we reported reflect significant encoding of either the RPE and/or the PPE. From Fig. 2, it can be seen that the four regions have a gamma activity that is modulated according to both reward and punishment PE. We used the term “non-selective”, because the regions did not encode either one or the other, but various proportions of bipolar derivations encoding either one or both of them.

The directional information flows identified in this manuscript were evidenced by the recording contacts of iEEG with levels of concurrent neural activities to the task conditions. However, are the conclusions well supported by the anatomical connections? Is it possible that the information was transferred to the target via another area? These questions may remain to be elucidated by using other approaches or animal models. It would be great to point this out here for further investigation.

We thank the reviewer for this interesting question. We added the following paragraph to the discussion to clarify the current limitations of the transfer entropy and the link with anatomical connections :

“Here, we quantified directional relationships between regions using the transfer entropy (Schreiber, 2000), which is a functional connectivity measure based on the Granger-Wiener causality principle. Tract tracing studies in the macaque have revealed strong interconnections between the lOFC and vmPFC in the macaque (Carmichael and Price, 1996; Öngür and Price, 2000). In humans, cortico-cortical anatomical connections have mainly been investigated using diffusion magnetic resonance imaging (dMRI). Several studies found strong probabilities of structural connectivity between the anterior insula with the orbitofrontal cortex and dorsolateral part of the prefrontal cortex (Cloutman et al., 2012; Ghaziri et al., 2017), and between the lOFC and vmPFC (Heather Hsu et al., 2020). In addition, the statistical dependency (e.g. coherence) between the LFP of distant areas could be potentially explained by direct anatomical connections (Schneider et al., 2021). Taken together, the existence of an information transfer might rely on both direct or indirect structural connectivity. However, here we also reported differences of TE between rewarding and punishing trials given the same backbone anatomical connectivity (Fig. 4). Our results are further supported by a recent study involving drug-resistant epileptic patients with resected insula who showed poorer performance than healthy controls in case of risky loss compared to risky gains (Von Siebenthal et al., 2017).”

References

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Combrisson E, Allegra M, Basanisi R, Ince RAA, Giordano BL, Bastin J, Brovelli A. 2022. Group-level inference of information-based measures for the analyses of cognitive brain networks from neurophysiological data. NeuroImage 258:119347. doi:10.1016/j.neuroimage.2022.119347

Ghaziri J, Tucholka A, Girard G, Houde J-C, Boucher O, Gilbert G, Descoteaux M, Lippé S, Rainville P, Nguyen DK. 2017. The Corticocortical Structural Connectivity of the Human Insula. Cereb Cortex 27:1216–1228. doi:10.1093/cercor/bhv308

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Recommendations for the authors

Reviewer #1

(1) Overall, the writing of the manuscript is dense and makes it hard to follow the scientific logic and appreciate the key findings of the manuscript. I believe the manuscript would be accessible to a broader audience if the authors improved the writing and provided greater detail for their scientific questions, choice of analysis, and an explanation of their results in simpler terms.

We extensively modified the introduction to better describe the rationale and research question.

(2) In the introduction the authors state "we hypothesized that reward and punishment learning arise from complementary neural interactions between frontal cortex regions". This stated hypothesis arrives rather abruptly after a summary of the literature given that the literature summary does not directly inform their stated hypothesis. Put differently, the authors should explicitly state what the contradictions and/or gaps in the literature are, and what specific combinations of findings guide them to their hypothesis. When the authors state their hypothesis the reader is still left asking: why are the authors focusing on the frontal regions? What do the authors mean by complementary interactions? What specific evidence or contradiction in the literature led them to hypothesize that complementary interactions between frontal regions underlie reward and punishment learning?

We extensively modified the introduction and provided a clearer description of the brain circuits involved and the rationale for searching redundant and synergistic interactions between areas.

(3) Related to the above point: when the authors subsequently state "we tested whether redundancy- or synergy dominated interactions allow the emergence of collective brain networks differentially supporting reward and punishment learning", the Introduction (up to the point of this sentence) has not been written to explain the synergy vs. redundancy framework in the literature and how this framework comes into play to inform the authors' hypothesis on reward and punishment learning.

We extensively modified the introduction and provided a clearer description of redundant and synergistic interactions between areas.

(4) The explanation of redundancy vs synergy dominated brain networks itself is written densely and hard to follow. Furthermore, how this framework informs the question on the neural substrates of reward versus punishment learning is unclear. The authors should provide more precise statements on how and why redundancy vs. synergy comes into play in reward and punishment learning. Put differently, this redundancy vs. synergy framework is key for understanding the manuscript and the introduction is not written clearly enough to explain the framework and how it informs the authors' hypothesis and research questions on the neural substrates of reward vs. punishment learning.

Same as above

(5) While the choice of these four brain regions in context of reward and punishment learning does makes sense, the authors do not outline a clear scientific justification as to why these regions were selected in relation to their question.

Same as above

(6) Could the authors explain why they used gamma band power (as opposed to or in addition to the lower frequency bands) to investigate MI. Relatedly, when the authors introduce MI analysis, it would be helpful to briefly explain what this analysis measures and why it is relevant to address the question they are asking.

Please see our answer to the first public comment. We added a paragraph to the discussion section to justify our choice of focusing on the gamma band only. We added the following sentence to the result section to justify our choice for using mutual-information:

The MI allowed us to detect both linear and non-linear relationships between the gamma activity and the PE

An extended explanation justifying our choice for the MI was already present in the method section.

(7) The authors state that "all regions displayed a local "probabilistic" encoding of prediction errors with temporal dynamics peaking around 500 ms after outcome presentation". It would be helpful for the reader if the authors spelled out what they mean by probabilistic in this context as the term can be interpreted in many different ways.

We agree with the reviewer that the term “probabilistic” can be interpreted in different ways. In the revised manuscript we changed “probabilistic” for “mixed”.

(8) The authors should include a brief description of how they compute RPE and PPE in the beginning of the relevant results section.

The explanation of how we estimated the PE is already present in the result section: “We estimated trial-wise prediction errors by fitting a Q-learning model to behavioral data. Fitting the model consisted in adjusting the constant parameters to maximize the likelihood of observed choices etc.”

(9) It is unclear from the Methods whether the authors have taken any measures to address the likely difference in the number of electrodes across subjects. For example, it is likely that some subjects have 10 electrodes in vmPFC while others may have 20. In group analyses, if the data is simply averaged across all electrodes then each subject contributes a different number of data points to the analysis. Hence, a subject with more electrodes can bias the group average. A starting point would be to state the variation in number of electrodes across subjects per brain region. If this variation is rather small, then simple averaging across electrodes might be justified. If the variation is large then one idea would be to average data across electrodes within subjects prior to taking the group average or use a resampling approach where the minimum number of electrodes per brain area is subsampled.

We addressed this point in our public answers. As a reminder, the new version of the manuscript contains a figure showing the number of unique patients per region, the PE at per participant level together with local-encoding at the single participant level.

(10) One thing to consider is whether the reward and punishment in the task is symmetrical in valence. While 1$ increase and 1$ decrease is equivalent in magnitude, the psychological effect of the positive (vs. the negative) outcome may still be asymmetrical and the direction and magnitude of this asymmetry can vary across individuals. For instance, some subjects may be more sensitive to the reward (over punishment) while others are more sensitive to the punishment (over reward). In this scenario, it is possible that the differentiation observed in PPE versus RPE signals may arise from such psychological asymmetry rather than the intrinsic differences in how certain brain regions (and their interactions) may encode for reward vs punishment. Perhaps the authors can comment on this possibility, and/or conduct more in depth behavioral analysis to determine if certain subjects adjust their choice behavior faster in response to reward vs. punishment contexts.

While it could be possible that individuals display different sensitivities vis-à-vis positive and negative prediction errors (and, indeed, a vast body of human reinforcement learning literature seems to point in this direction; Palminteri & Lebreton, 2022), it is unclear to us how such differences would explain into the recruitment of anatomically distinct areas reward and punishment prediction errors. It is important to note here that our design partially orthogonalized positive and reward vs. negative and punishment PEs, because the neutral outcome can generate both positive and negative prediction errors, as a function of the learning context (reward-seeking and punishment avoidance). Back to the main question, for instance, Lefebvre et al (2017) investigated with fMRI the neural correlates of reward prediction errors only and found that inter-individual differences in learning rates for positive and negative prediction errors correlated with differences in the degree of striatal activation and not with the recruitment of different areas. To sum up, while we acknowledge that individuals may display different sensitivity to prediction errors (and reward magnitudes), we believe that such differences should translated in difference in the degree of activation of a given system (the reward systems vs the punishment one) rather than difference in neural system recruitment

(11) As summarized in Fig 6, the authors show that information transfer between aINS to dlPFC was PPE specific whereas the information transfer between vmPFC to lOFC was RPE specific. What is unclear is if these findings arise as an inevitable statistical byproduct of the fact that aINS has high PPE-specificity and that vmPFC has high RPE-specificity. In other words, it is possible that the analysis in Fig 3,4 are sensitive to fact that there is a larger proportion of electrodes with either PPE or RPE sensitivity in aINS and vmPFC respectively - and as such, the II analysis might reflect the dominant local encoding properties above and beyond reflecting the interactions between regions per se. Simply put, could the analysis in Fig 3B turn out in any other way given that there are more PPE specific electrodes in aINS and more RPE specific electrodes in vmPFC? Some options to address this question would be to limit the electrodes included in the analyses (in Fig 3B for example) so that each region has the same number of PPE and RPE specific electrodes included.

Please see the simulation we added to the revised manuscript (Fig. S10) demonstrating that synergistic interactions can emerge between regions with the same specificity.

Regarding the possibility that Fig. 3 and 4 are sensitive to the number of bipolar derivations being R/PPE specific, a counter-example is the vmPFC. The vmPFC has a few recordings specific to punishment (Fig. 2) in almost 30% of the subjects (Fig. S4). However, there is no II about the PPE between recordings of the vmPFC (Fig. 3). The same reasoning also holds for the lOFC. Therefore, the proportion of recordings being RPE or PPE-specific is not sufficient to determine the type of interactions.

(12)  Related to the point above, what would the results presented in Fig 3A (and 3B) look like if the authors ran the analyses on RPE specific and PPE specific electrodes only. Is the vmPFC-vmPFC RPE effect in Fig 3A arising simply due to the high prevalence of RPE specific electrodes in vmPFC (as shown in Fig. 2)?

Please see our answer above.

Reviewer #2:

Regarding Figure 2A, the authors argued that their findings "globally reproduced their previously published findings" (from Gueguen et al, 2021). It is worth noting though that in their original analysis, both aINS and lOFC show differential effects (aINS showing greater punishment compared to reward, and the opposite for lOFC) compared to the current analysis. Although I would be akin to believe that the nonlinear approach used here might explain part of the differences (as the authors discussed), I am very wary of the other argument advanced: "the removal of iEEG sites contaminated with pathological activity". This raised some red flags. Does that mean some of the conclusions observed in Gueguen et al (2021) are only the result of noise contamination, and therefore should be disregarded? The author might want to add a short supplementary figure using the same approach as in Gueguen (2021) but using the subset of contacts used here to comfort potential readers of the validity of their previous manuscript.

We appreciate the reviewer's concerns and understand the request for additional information. However, we would like to point out that the figure suggested by the reviewer is already present in the supplementary files of Gueguen et al. 2021 (see Fig. S2). The results of this study should not be disregarded, as the supplementary figure reproduces the results of the main text after excluding sites with pathological activity. Including or excluding sites contaminated with epileptic activity does not have a significant impact on the results, as analyses are performed at each time-stamp and across trials, and epileptic spikes are never aligned in time across trials.

That being said, there are some methodological differences between the two studies. To extract gamma power, Gueguen et al. filtered and averaged 10 Hz sub-bands, while we used multi-tapers. Additionally, they used a temporal smoothing of 250 ms, while we used less smoothing. However, as explained in the main text, we used information-theoretical approaches to capture the statistical dependencies between gamma power and PE. Despite divergent methodologies, we obtained almost identical results.

The data and code supporting this manuscript should be made available. If raw data cannot be shared for ethical reasons, single-trial gamma activities should at least be provided. Regarding the code used to process the data, sharing it could increase the appeal (and use) of the methods applied.

We thank the reviewer for this suggestion. We added a section entitled “Code and data availability” and gave links to the scripts, notebooks and preprocessed data.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Shen et al. conducted three experiments to study the cortical tracking of the natural rhythms involved in biological motion (BM), and whether these involve audiovisual integration (AVI). They presented participants with visual (dot) motion and/or the sound of a walking person. They found that EEG activity tracks the step rhythm, as well as the gait (2-step cycle) rhythm. The gait rhythm specifically is tracked superadditively (power for A+V condition is higher than the sum of the A-only and V-only condition, Experiments 1a/b), which is independent of the specific step frequency (Experiment 1b). Furthermore, audiovisual integration during tracking of gait was specific to BM, as it was absent (that is, the audiovisual congruency effect) when the walking dot motion was vertically inverted (Experiment 2). Finally, the study shows that an individual's autistic traits are negatively correlated with the BM-AVI congruency effect.

Strengths:

The three experiments are well designed and the various conditions are well controlled. The rationale of the study is clear, and the manuscript is pleasant to read. The analysis choices are easy to follow, and mostly appropriate.

Weaknesses:

There is a concern of double-dipping in one of the tests (Experiment 2, Figure 3: interaction of Upright/Inverted X Congruent/Incongruent). I raised this concern on the original submission, and it has not been resolved properly. The follow-up statistical test (after channel selection using the interaction contrast permutation test) still is geared towards that same contrast, even though the latter is now being tested differently. (Perhaps not explicitly testing the interaction, but in essence still testing the same.) A very simple solution would be to remove the post-hoc statistical tests and simply acknowledge that you're comparing simple means, while the statistical assessment was already taken care of using the permutation test. (In other words: the data appear compelling because of the cluster test, but NOT because of the subsequent t-tests.)

We are sorry that we did not explain this issue clearly before, which might have caused some misunderstanding. When performing the cluster-based permutation test, we only tested whether the audiovisual congruency effect (congruent vs. incongruent) between the upright and inverted conditions was significantly different [i.e., (UprCon – UprInc) vs. (InvCon – InvInc)], without conducting extra statistical analyses on whether the congruency effect was significant in each orientation condition. Such an analysis yielded a cluster with a significant interaction between audiovisual integration and BM orientation for the cortical tracking effect at 1Hz (but not at 2Hz). However, this does not provide valid information about whether the audiovisual congruency effect at this cluster is significant in each orientation condition, given that a significant interaction effect may result from various patterns of data across conditions: such as significant congruency effects in both orientation conditions (Author response image 1a), a significant congruency effect in the upright condition and a non-significant effect in the inverted condition (Author response image 1b), or even non-significant yet opposite effects in the two conditions (Author response image 1c). Here, our results conform to the second pattern, indicating that cortical tracking of the high-order gait cycles involves a domain-specific process exclusively engaged in the AVI of BM. In a similar vein, the non-significant interaction found at 2Hz does not necessarily indicate that the congruency effect is non-significant in each orientation condition (Author response image 1f&e). Indeed, the congruency effect was significant in both the upright and inverted conditions at 2Hz in our study despite the non-significant interaction, suggesting that neural tracking of the lower-order step cycles is associated with a domain-general AVI process mostly driven by temporal correspondence in physical stimuli.

Therefore, we need to perform subsequent t-tests to examine the significance of the simple effects in the two orientation conditions, which do not duplicate the clusterbased permutation test (for interaction only) and cause no double-dipping. Results from interaction and simple effects, put together, provide solid evidence that the cortical tracking of higher-order and lower-order rhythms involves BM-specific and domaingeneral audiovisual processing, respectively.

To avoid ambiguity, we have removed the sentence “We calculated the audiovisual congruency effect for the upright and the inverted conditions” (line 194, which referred to the calculation of the indices rather than any statistical tests) from the manuscript. We have also clarified the meanings of the findings based on the interaction and simple effects together at the two temporal scales, respectively (Lines 205-207; Lines 213-215).

Author response image 1.

Examples of different patterns of data yielding a significant or nonsignificant interaction effect.

Reviewer #2 (Public review):

Summary:

The authors evaluate spectral changes in electroencephalography (EEG) data as a function of the congruency of audio and visual information associated with biological motion (BM) or non-biological motion. The results show supra-additive power gains in the neural response to gait dynamics, with trials in which audio and visual information was presented simultaneously producing higher average amplitude than the combined average power for auditory and visual conditions alone. Further analyses suggest that such supra-additivity is specific to BM and emerges from temporoparietal areas. The authors also find that the BM-specific supra-additivity is negatively correlated with autism traits.

Strengths:

The manuscript is well-written, with a concise and clear writing style. The visual presentation is largely clear. The study involves multiple experiments with different participant groups. Each experiment involves specific considered changes to the experimental paradigm that both replicate the previous experiment's finding yet extend it in a relevant manner.

Weaknesses:

In the revised version of the paper, the manuscript better relays the results and anticipates analyses, and this version adequately resolves some concerns I had about analysis details. Still, it is my view that the findings of the study are basic neural correlate results that do not provide insights into neural mechanisms or the causal relevance of neural effects towards behavior and cognition. The presence of an inversion effect suggests that the supra-additivity is related to cognition, but that leaves open whether any detected neural pattern is actually consequential for multi-sensory integration (i.e., correlation is not causation). In other words, the fact that frequency-specific neural responses to the [audio & visual] condition are stronger than those to [audio] and [visual] combined does not mean this has implications for behavioral performance. While the correlation to autism traits could suggest some relation to behavior and is interesting in its own right, this correlation is a highly indirect way of assessing behavioral relevance. It would be helpful to test the relevance of supra-additive cortical tracking on a behavioral task directly related to the processing of biological motion to justify the claim that inputs are being integrated in the service of behavior. Under either framework, cortical tracking or entrainment, the causal relevance of neural findings toward cognition is lacking.

Overall, I believe this study finds neural correlates of biological motion, and it is possible that such neural correlates relate to behaviorally relevant neural mechanisms, but based on the current task and associated analyses this has not been shown.

Thank you for providing these thoughtful comments regarding the theoretical implications of our neural findings. Previous behavioral evidence highlights the specificity of the audiovisual integration (AVI) of biological motion (BM) and reveals the impairment of such ability in individuals with autism spectrum disorder. However, the neural implementation underlying the AVI of BM, its specificity, and its association with autistic traits remain largely unknown. The current study aimed to address these issues.

It is noteworthy that the operation of multisensory integration does not always depend on specific tasks, as our brains tend to integrate signals from different sensory modalities even when there is no explicit task. Hence, many studies have investigated multisensory integration at the neural level without examining its correlation with behavioral performance. For example, the widely known super-additivity mode for multisensory integration proposed by Perrault and colleagues was based on single-cell recording findings without behavioral tasks (Perrault et al., 2003, 2005). As we mentioned in the manuscript, the super-additive and sub-additive modes indicate non-linear interaction processing, either with potentiated neural activation to facilitate the perception or detection of near-threshold signals (super-additive) or a deactivation mechanism to minimize the processing of redundant information cross-modally (subadditive) (Laurienti et al., 2005; Metzger et al., 2020; Stanford et al., 2005; Wright et al., 2003). Meanwhile, the additive integration mode represents a linear combination between two modalities. Distinguishing among these integration modes helps elucidate the neural mechanism underlying AVI in specific contexts, even though sometimes, the neural-level AVI effects do not directly correspond to a significant behavioral-level AVI effect (Ahmed et al., 2023; Metzger et al., 2020). In the current study, we unveiled the dissociation of multisensory integration modes between neural responses at two temporal scales (Exps. 1a & 1b), which may involve the cooperation of a domain-specific and a domain-general AVI processes (Exp. 2). While these findings were not expected to be captured by a single behavioral index, they revealed the multifaceted mechanism whereby hierarchical cortical activity supports audiovisual BM integration. They also advance our understanding of the emerging view that multi-timescale neural dynamics coordinate multisensory integration (Senkowski & Engel, 2024), especially from the perspective of natural stimuli processing.

Meanwhile, our finding that the cortical tracking of higher-order rhythmic structure in audiovisual BM specifically correlated with individual autistic traits extends previous behavioral evidence that ASD children exhibited reduced orienting to audiovisual synchrony in BM (Falck-Ytter et al., 2018), offering new evidence that individual differences in audiovisual BM processing are present at the neural level and associated with autistic traits. This finding opens the possibility of utilizing the cortical tracking of BM as a potential neural maker to assist the diagnosis of autism spectrum disorder (see more details in our Discussion Lines 334-346).

However, despite the main objective of the current study focusing on the neural processing of BM, we agree with the reviewer that it would be helpful to test the relevance of supra-additive cortical tracking on a behavioral task directly related to BM perception, for further justifying that inputs are being integrated in the service of behavior. In the current study, we adopted a color-change detection task entirely unrelated to audiovisual correspondence but only for maintaining participants’ attention. The advantage of this design is that it allows us to investigate whether and how the human brain integrates audiovisual BM information under task-irrelevant settings, as people in daily life can integrate such information even without a relevant task. However, this advantage is accompanied by a limitation: the task does not facilitate the direct examination of the correlation between neural responses and behavioral performance, since the task performance was generally high (mean accuracy >98% in all experiments). Future research could investigate this issue by introducing behavioral tasks more relevant to BM perception (e.g., Shen et al., 2023). They could also apply advanced neuromodulation techniques to elucidate the causal relevance of the cortical tracking effect to behavior (e.g., Ko sem et al., 2018, 2020).

We have discussed the abovementioned points as a separate paragraph in the revised manuscript (Lines 322-333). In addition, since the scope of the current study does not involve a causal correlation with behavioral performance, we have removed or modified the descriptions related to "functional relevance" in the manuscript (Abstract; Introduction, lines 101-103; Results, lines 239; Discussion, line 336; Supplementary Information, line 794、803). Moreover, we have strengthened the descriptions of the theoretical implications of the current findings in the abstract.

We hope these changes adequately address your concern.

References

Ahmed, F., Nidiffer, A. R., O’Sullivan, A. E., Zuk, N. J., & Lalor, E. C. (2023). The integration of continuous audio and visual speech in a cocktail-party environment depends on attention. Neuroimage, 274, 120143. https://doi.org/10.1016/j.neuroimage.2023.120143

Falck-Ytter, T., Nystro m, P., Gredeba ck, G., Gliga, T., Bo lte, S., & the EASE team. (2018). Reduced orienting to audiovisual synchrony in infancy predicts autism diagnosis at 3 years of age. Journal of Child Psychology and Psychiatry, 59(8), 872–880. https://doi.org/10.1111/jcpp.12863

Ko sem, A., Bosker, H., Jensen, O., Hagoort, P., & Riecke, L. (2020). Biasing the Perception of Spoken Words with Transcranial Alternating Current Stimulation. Journal of Cognitive Neuroscience, 32, 1–10. https://doi.org/10.1162/jocn_a_01579

Ko sem, A., Bosker, H. R., Takashima, A., Meyer, A., Jensen, O., & Hagoort, P. (2018). Neural Entrainment Determines the Words We Hear. Current Biology, 28(18), 2867-2875.e3. https://doi.org/10.1016/j.cub.2018.07.023

Laurienti, P. J., Perrault, T. J., Stanford, T. R., Wallace, M. T., & Stein, B. E. (2005). On the use of superadditivity as a metric for characterizing multisensory integration in functional neuroimaging studies. Experimental Brain Research, 166(3), 289–297. https://doi.org/10.1007/s00221-005-2370-2

Metzger, B. A., Magnotti, J. F., Wang, Z., Nesbitt, E., Karas, P. J., Yoshor, D., & Beauchamp, M. S. (2020). Responses to Visual Speech in Human Posterior Superior Temporal Gyrus Examined with iEEG Deconvolution. The Journal of Neuroscience: The Official Journal of the Society for Neuroscience, 40(36), 6938–6948. https://doi.org/10.1523/JNEUROSCI.0279-20.2020

Perrault, T. J., Vaughan, J. W., Stein, B. E., & Wallace, M. T. (2003). Neuron-Specific Response Characteristics Predict the Magnitude of Multisensory Integration. Journal of Neurophysiology, 90(6), 4022–4026. https://doi.org/10.1152/jn.00494.2003

Perrault, T. J., Vaughan, J. W., Stein, B. E., & Wallace, M. T. (2005). Superior Colliculus Neurons Use Distinct Operational Modes in the Integration of Multisensory Stimuli. Journal of Neurophysiology, 93(5), 2575–2586. https://doi.org/10.1152/jn.00926.2004

Senkowski, D., & Engel, A. K. (2024). Multi-timescale neural dynamics for multisensory integration. Nature Reviews Neuroscience, 25(9), 625–642. https://doi.org/10.1038/s41583-024-00845-7

Shen, L., Lu, X., Wang, Y., & Jiang, Y. (2023). Audiovisual correspondence facilitates the visual search for biological motion. Psychonomic Bulletin & Review, 30(6), 2272–2281. https://doi.org/10.3758/s13423-023-02308-z

Stanford, T. R., Quessy, S., & Stein, B. E. (2005). Evaluating the Operations Underlying Multisensory Integration in the Cat Superior Colliculus. Journal of Neuroscience, 25(28), 6499–6508. https://doi.org/10.1523/JNEUROSCI.5095-04.2005

Wright, T. M., Pelphrey, K. A., Allison, T., McKeown, M. J., & McCarthy, G. (2003). Polysensory Interactions along Lateral Temporal Regions Evoked by Audiovisual Speech. Cerebral Cortex, 13(10), 1034–1043. https://doi.org/10.1093/cercor/13.10.1034

Author Response

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

Reviewer #1 (Public Review):

This is an interesting and somewhat unusual paper supporting the idea that creatine is a neurotransmitter in the central nervous system of vertebrates. The idea is not entirely new, and the authors carefully weigh the evidence, both past and newly acquired, to make their case. The strength of the paper lies in the importance of the potential discovery - as the authors point out, creatine ticks more boxes on criteria of neurotransmitters than some of the ones listed in textbooks - and the list of known transmitters (currently 16) certainly is textbook material. A further strength of the manuscript is the careful consideration of a list of criteria for transmitters and newly acquired evidence for four of these criteria: 1. evidence that creatine is stored in synaptic vesicles, 2. mutants for creatine synthesis and a vesicular transporter show reduced storage and release of creatine, 3. functional measurement that creatine release has an excitatory or inhibitory (here inhibitory) effect in vivo, and 4. ATP-dependence. The key weakness of the paper is that there is no single clear 'smoking gun', like a postsynaptic creatine receptor, that would really demonstrate the function as a transmitter. Instead, the evidence is of a cumulative nature, and not all bits of evidence are equally strong. On balance, I found the path to discovery and the evidence assembled in this manuscript to establish a clear possibility, positive evidence, and to provide a foundation for further work in this direction.

it is notable that, historically, no neurotransmitter has ever been established in a single paper. While creatine will not be an exception, data presented in this paper are more than any previous paper in demonstrating the possibility of a new neurotransmitter. However, we added an entire paragraph in the Discussion part about differences between Cr and classic neurotransmitters such as Glu, beginning with the absence of a molecularly defined receptor at this point and the Ca2+ independent component of Cr release induced by extracellular K+.

We appreciate the reviewer for noting that evidence obtained by us now support that creatine satisfies all 4 criteria of transmitters.

We respectively disagree the point about a smoking gun: any of these four is a smoking gun, while the satisfication of all 4 is quite strong, more than a smoking gun.

We find it disagreeable that a receptor “would really demonstrate the function of a transmitter”. Textbook criteria for a transmitter usually require postsynaptic responses, not a molecularly defined receptor. A molecularly defined receptor for many of the known transmitters required many years of work, while they were accepted as transmitters before their receptors were finally molecularly defined. As long as there is a postsynaptic response, there is of course a receptor, though its molecular properties should be further studied. For examples, responses to choline were discovered in 1900 (Hunt, Am J Physiol 3, xviii-xix, 1900), those to acetylcholine in 1906 (Hunt and Taveau, Br Med J 2:1788-1789, 1906), those to supradrenal glands before 1894 (Oliver and Schäfer, J Physiol 18:230-276 1895). Henry Dale was awarded a Nobel prize in 1936 partly for his work on acetylcholine. Receptors for acetylcholine and noradrenaline were not molecularly defined until the 1970s and 1980s. Before then, they were only known by mediating responses to natural transmitters and synthesized chemicals.

There were two previous reports that creatine could be taken into brain slices (Almeida et al., 2006) or synaptosomes (Peral, Vázquez-Carretero and Ilundain, 2010). These were used by the reviewer to argue that the idea of creatine as a neurotransmitter “is not entirely new”. However, no one has followed up these studies for 10 years, thus they would not be considered as good smoking guns. While we have reproduced the synaptosome uptake result (together with our new finding that this uptake was dependent on SLC6A8), it should be noted that uptake of molecules into synaptosomes is not absolutely required for a neurotransmitter because degradation of a transmitter is equally valid. Furthermore, molecules required synaptically but not as a transmitter can also be transported into the synaptic terminal.

Our detection of Cr in the synaptic vesicles provides much stronger evidence supporting its importance. If a smoking gun is important, the detection of creatine in the SVs is the best smoking gun, whose discovery in fact was the reason leading us to study its release, postsynaptic responses as well as repeating the uptake experiment with genetic mutants.

Reviewer #2 (Public Review):

Summary:

Bian et al studied creatine (Cr) in the context of central nervous system (CNS) function. They detected Cr in synaptic vesicles purified from mouse brains with anti-Synaptophysin using capillary electrophoresis-mass spectrometry. Cr levels in the synaptic vesicle fraction were reduced in mice lacking the Cr synthetase AGAT, or the Cr transporter SLC6A8. They provide evidence for Cr release within several minutes after treating brain slices with KCl. This KCl-induced Cr release was partially calcium-dependent and was attenuated in slices obtained from AGAT and SLC6A8 mutant mice. Cr application also decreased the excitability of cortical pyramidal cells in one third of the cells tested. Finally, they provide evidence for SLC6A8-dependent Cr uptake into synaptosomes, and ATP-dependent Cr loading into synaptic vesicles. Based on these data, the authors propose that Cr may act as a neurotransmitter in the CNS.

Strengths:

1) A major strength of the paper is the broad spectrum of tools used to investigate Cr.

2) The study provides strong evidence that Cr is present in/loaded into synaptic vesicles.

Weaknesses:

(in sequential order)

1) Are Cr levels indeed reduced in Agat-/-? The decrease in Cr IgG in Agat-/- (and Agat+/-) is similar to the corresponding decrease in Syp (Fig. 3B). What is the explanation for this? Is the decrease in Cr in Agat-/- significant when considering the drop in IgG? The data should be normalized to the respective IgG control.

We measured the Cr concentration in the whole brain lysates using Creatine Assay Kit (Sigma, MAK079). Cr levels in the brain were reduced in Agat-/- mice. The Cr concentration in AGAT-/- mice was reduced to about 1/10 of AGAT+/+ and AGAT+/- mice (Author response image 1).

Author response image 1.

Cr concentration in brain from AGAT+/+, AGAT+/- and AGAT-/- mice (n=5 male mice for each group). , p<0.05, **, p<0.001, one-way ANOVA with Tukey’s correction.

As pointed by the reviewer, the decrease in Cr IgG in Agat-/- seems similar to the corresponding decrease in Syp (Fig. 3B in the paper). Cr pulled down by IgG was 0.46 ± 0.04, 0.37 ± 0.06 and 0.17 ±0.03 pmol/μg anti-syp antibody for Agat+/+, Agat+/-, and Agat-/- mice respectively. There was a trend of reduction Cr IgG in Agat-/-, however, there were no statistically significant differences between Agat-/- and Agat+/+, or between Agat-/- and Agat+/-, as determined by one-way ANOVA (Fig. 3B in the paper). Due to the fact that Agat-/- reduced Cr concentration in the brain, we speculate that the apparent drop in Cr pulled down by IgG may have partially resulted from the overall reduction of Cr content in the brain.

The absolute content of Cr pulled down by Syp in Agat-/- mice was reduced to 21.6% of Agat+/+ mice and 23.6% of Agat+/- mice (Fig. 3B in the paper). As suggested by the reviewer, we normalized the Cr pulled down by Syp to the respective IgG control (Author response image 2). The normalized Cr content in AGAT-/- mice has a tendency to decrease, but not statistically significant, as compared to Agat+/+ and Agat+/- mice (n=10 for each group, one-way ANOVA).

Author response image 2.

Normalized Cr content in brain from AGAT+/+, AGAT+/- and AGAT-/- mice (n=10 for each group). Cr pulled down by anti-Syp antibody was normalized to that of IgG.

2) The data supporting that depolarization-induced Cr release is SLC6A8 dependent is not convincing because the relative increase in KCl-induced Cr release is similar between SLC6A8-/Y and SLC6A8+/Y (Fig. 5D). The data should be also normalized to the respective controls.

As suggested by the reviewer, we normalized the Cr release during KCl stimulation to the baseline (Author response image 3). The ratio of Cr release evoked by high KCl stimulation to the baseline was similar in WT and Slc6a8 knockouts. This suggests that Cr is not released through SLC6A8 transporter.

Author response image 3.

Normalized Cr release from slices from Slc6a8+/Y and Slc6a8-/Y mice (n=7 slices for each group). Cr released evoked by high KCl stimulation was normalized to baseline.

However, without Slc6a8, KCl-induced release of Cr was significantly reduced (Figure 5D in the paper). This is because Slc6a8 is a transporter to Cr uptake into synaptic terminals (Figure 5D and 8C in the paper). Therefore, Cr content in SVs (Figure 2C in the paper) indirectly reduced Cr release.

3) The majority (almost 3/4) of depolarization-induced Cr release is Ca2+ independent (Fig. 5G). Furthermore, KCl-induced, Ca2+-independent release persists in SLC6A8-/Y (Fig. 5G). What is the model for Ca2+-independent Cr release? Why is there Ca2+-independent Cr release from SLC6A8 KO neurons? How does this relate to the prominent decrease in Ca2+-dependent Cr release in SLC6A8-/Y (Fig. 5G)? They show a prominent decrease in Cr control levels in SLC6A8-/Y in Fig. 5D. Were the data shown in Fig. 5D obtained in the presence or absence of Ca2+? Could the decrease in Ca2+-dependent Cr release in SLC6A8-/Y (Fig. 5G) be due to decreased Cr baseline levels in the presence of Ca2+ (Fig. 5D)?

These are interesting questions that, at this point, could only be answered by references to literature. For example, one possibility was that Ca2+-independent Cr release might occurs in glia, since as pointed by the reviewer in Point 6, high GAMT levels were reported for astrocytes and oligodendrites (Schmidt et al. 2004; Rosko et al. 2023). As reported, other neuromodulators such as taurine can be released from astrocytes (Philibert, Rogers, and Dutton 1989) or slices (Saransaari and Oja 2006) in Ca2+ independent manner. In addition, in the absence of potassium stimulation, Ca2+ depletion lead to increased release of taurine in cultured astrocytes (Takuma et al. 1996) or in striatum in vivo (Molchanova, Oja, and Saransaari 2005). Similarly, in SLC6A8 KO slices, Ca2+ depletion (Figure 5G) also increased creatine baseline levels as compared to that in normal ACSF (Figure 5D). Another possibility was that Ca2+-independent Cr release might occurs in neurons lacking SLC6a8 expression.

As mentioned in the paper, data shown in Figure 5D was obtained in the presence Ca2+. Reduction of Ca2+-dependent Cr release evoked by potassium in SLC6A8-/Y (Figure 5G) may be due to decreased Cr baseline levels in the presence of Ca2+ and reduced Cr in synaptic vesicles (Figure 5D).

4) Cr levels are strongly reduced in Agat-/- (Figure 6B). However, KCl-induced Cr release persists after loss of AGAT (Figure 6B). These data do not support that Cr release is Agat dependent.

Although KCl-induced Cr release persisted in AGAT-/- mutants, it was dropped to 11.6% of WT mice (Figure 6B). AGAT is not directly involved in the release, but required for providing sufficient Cr.

5) The authors show that Cr application decreases excitability in ~1/3 of the tested neurons (Figure 7). How were responders and non-responders defined? What justifies this classification? The data for all Cr-treated cells should be pooled. Are there indeed two distributions (responders/non-responders)? Running statistics on pre-selected groups (Figure 7H-J) is meaningless. Given that the effects could be seen 2-8 minutes after Cr application - at what time points were the data shown in Figure 7E-J collected? Is the Cr group shown in Figure 7F significantly different from the control group/wash?

The responders were defined by three criteria: (1) When Cr was applied, the rheobase was increased as compared to both control and wash conditions. (2) The number of total evoked spikes was decreased during Cr application than both control and wash. (3) The number of total evoked spikes was decreased at least by 10% than control or wash.

For all the individual responders, when Cr was applied, the rheobase was increased (Figure 7E and 7F). While in individual non-responders, the rheobase was either identical to both control and wash (n=19/35), identical to either control or wash (n=11/35), between control and wash (n=2/35) or smaller than both control and wash (n=3/35) following Cr application. Thus, the responders and non-responders were separatable. When the rheobase data were pulled together, many points were overlapped, so we did not pull the data here.

As suggested, we pulled the data of the ratio of spike changes in response to 100 μM Cr application for all neurons together (Author response image 4). Evoked spikes of non-responders were typically (34/35) changed in the range of -10% to 10%.

Author response image 4.

Relative changes of total evoked spikes in response to 100 μM Cr. Responders are represented by red dots and non-responders by black dots. Dashed black line indicates 10%. Relative change = (Cr-(Control +wash)/2)/((Control +wash)/2)*100%.

In Figure 7E-J, we collected data at time points when the maximal response was reached. The Cr group shown in Figure 7F was indeed significantly different from the control group/wash (p<0.05, paired t test, for data points collected under 75-500 pA current injection).

6) Indirect effects: The phenotypes could be partially caused by indirect effects of perturbing the Cr/PCr/CK system, which is known to play essential roles in ATP regeneration, Ca2+ homeostasis, neurotransmission, intracellular signaling systems, axonal and dendritic transport... Similarly, high GAMT levels were reported for astrocytes (e.g., Schmidt et al. 2004; doi: 10.1093/hmg/ddh112), and changes in astrocytic Cr may underlie the phenotypes. Cr has been also reported to be an osmolyte: a hyperosmotic shock of astrocytes induced an increase in Cr uptake, suggesting that Cr can work as a compensatory osmolyte (Alfieri et al. 2006; doi: 10.1113/jphysiol.2006.115006). Potential indirect effects are also consistent with a trend towards decreased KCl-induced GABA (and Glutamate) release in SLC6A8-/Y (Figure 5C). These indirect effects may in part explain the phenotypes seen after perturbing Agat, SLC6A8, and should be thoroughly discussed.

We discussed the possibility of creatine/phosphocreatine as non-transmitters in discussion part. We added the possibility of astrocytic Cr in discussion part. KCl-induced GABA (and Glutamate) release in SLC6A8-/Y (Figure 5C) was not significant.

7) As stated by the authors, there is some evidence that Cr may act as a co-transmitter for GABAA receptors (although only at high concentrations). Would a GABAA blocker decrease the fraction of cells with decreased excitability after Cr exposure?

We performed another experiment in CA1 pyramidal neurons in hippocampus showing that Cr at 100 μM did not change GABAergic neurotransmission (n=8, Author response image 5). Inhibitory postsynaptic currents (IPSCs) recorded in the presence of glutamate receptor blockers (10 μM APV and 10 μM CNQX) were not changed by 100 μM creatine in hippocampal CA1 pyramidal neurons (Bgroup data of IPSC frequency (B) and amplitude (C) averaged in 1 min duration). These did not support Cr activation of GABAA receptors.

Author response image 5.

IPSCs recorded in in hippocampal CA1 pyramidal neurons. (A) representative raw traces before (Control), during (Creatine) and after (Wash) the application of 100 μM creatine. (B&C) group data of IPSC frequency (B) and amplitude (C) averaged in 1 min duration.

8) The statement "Our results have also satisfied the criteria of Purves et al. 67,68, because the presence of postsynaptic receptors can be inferred by postsynaptic responses." (l.568) is not supported by the data and should be removed.

We have deleted this sentence, though what could mediate postsynaptic responses other than receptors?

Reviewer #3 (Public Review):

SUMMARY:

The manuscript by Bian et al. promotes the idea that creatine is a new neurotransmitter. The authors conduct an impressive combination of mass spectrometry (Fig. 1), genetics (Figs. 2, 3, 6), biochemistry (Figs. 2, 3, 8), immunostaining (Fig. 4), electrophysiology (Figs. 5, 6, 7), and EM (Fig. 8) in order to offer support for the hypothesis that creatine is a CNS neurotransmitter.

We thank the reviewer for the summary.

STRENGTHS:

There are many strengths to this study.

• The combinatorial approach is a strength. There is no shortage of data in this study.

• The careful consideration of specific criteria that creatine would need to meet in order to be considered a neurotransmitter is a strength.

• The comparison studies that the authors have done in parallel with classical neurotransmitters are helpful.

• Demonstration that creatine has inhibitory effects is another strength.

• The new genetic mutations for Slc6a8 and AGAT are strengths and potentially incredibly helpful for downstream work.

WEAKNESSES:

• Some data are indirect. Even though Slc6a8 and AGAT are helpful sentinels for the presence of creatine, they are not creatine themselves. Therefore, the conclusions that are drawn should be circumspect.

SLC6A8 and AGAT mutants are not essential for Cr’s role as a neurotransmitter.

• Regarding Slc6a8, it seems to work only as a reuptake transporter - not as a transporter into SVs. Therefore, we do not know what the transporter is.

Indeed, SLC6A8 is only a transporter on the cytoplasmic membrane, not a transporter on synaptic vesicles. We have shown biochemistry here, and we have unpublished data that showed other SLCs on SVs, which did not include SLC6A8.

• Puzzlingly, Slc6a8 and AGAT are in different cells, setting up the complicated model that creatine is created in one cell type and then processed as a neurotransmitter in another.

• No candidate receptor for creatine has been identified postsynaptically.

• Because no candidate receptor has been identified, is it possible that creatine is exerting its effects indirectly through other inhibitory receptors (e.g., GABAergic Rs)?

As shown in our response to Question 7 of Reviewer 2, Cr did not exert its effects through inhibitory GABAA receptors.

• More broadly, what are the other possibilities for roles of creatine that would explain these observations other than it being a neurotransmitter? Could it simply be a modifier that exists in the SVs (lots of molecules exist in SVs)?

We discussed the possibility of a non-transmitter role for creatine/phosphocreatine in discussion part.

• The biochemical studies are helpful in terms of comparing relevant molecules (e.g., Figs. 8 and S1), but the images of the westerns are all so fuzzy that there are questions about processing and the accuracy of the quantification.

Multiple members (>4) have carried out SV purifications repeatedly over the last decade in our group, we are highly confident of SV purifications presented in Figs. 8 and S1.

There are several criteria that define a neurotransmitter. The authors nicely delineated many criteria in their discussion, but it is worth it for readers to do the same with their own understanding of the data.

By this reviewer's understanding (and the Purves' textbook definition) a neurotransmitter: 1) must be present within the presynaptic neuron and stored in vesicles; 2) must be released by depolarization of the presynaptic terminal; 3) must require Ca2+ influx upon depolarization prior to release; 4) must bind specific receptors present on the postsynaptic cell; 5) exogenous transmitter can mimic presynaptic release; 6) there exists a mechanism of removal of the neurotransmitter from the synaptic cleft.

6 criteria seem to be only required by the reviewer. As discussed in our Discussion part, Purves’ textbook did not list 6 criteria but only three criteria, “the substance must be present within the presynaptic neuron; the substance must be released in response to presynaptic depolarization, and the release must be Ca2+ dependent; specific receptors for the substance be present on the postsynaptic cell” (Purves et al., 2001, 2016).

Kandel et al. (2013, 2021) listed 4 criteria for a neurotransmitter: “it is synthesized in the presynaptic neuron; it is present within vesicles and is released in amounts sufficient to exert a defined action on the postsynaptic neuron or effector organ; when administered exogenously in reasonable concentrations it mimics the action of the endogenous transmitter; a specific mechanism usually exists for removing the substance from the synaptic cleft”.

While we agree that any neuroscientist can have his/her own criteria, it is more reasonable to accept the textbooks that have been widely read for decades.

For a paper to claim that the work has identified a new neurotransmitter, several of these criteria would be met - and the paper would acknowledge in the discussion which ones have not been met. For this particular paper, this reviewer finds that condition 1 is clearly met.

Conditions 2 and 3 seem to be met by electrophysiology, but there are caveats here. High KCl stimulation is a blunt instrument that will depolarize absolutely everything in the prep all at once and could result in any number of non-specific biological reactions as a result of K+ rushing into all neurons in the prep. Moreover, the results in 0 Ca2+ are puzzling. For creatine (and for the other neurotransmitters), why is there such a massive uptick in release, even when the extracellular saline is devoid of calcium?

To avoid the disadvantage of high KCl stimulation, we performed optogenetic experiments recently, with encouraging preliminary data. We do not know the source of Ca2+-independent release of Cr and neurotransmitters, though astrocytes are a possibility.

Condition 4 is not discussed in detail at all. In the discussion, the authors elide the criterion of receptors specified by Purves by inferring that the existence of postsynaptic responses implies the existence of receptors. True, but does it specifically imply the existence of creatinergic receptors? This reviewer does not think that is necessarily the case. The authors should be appropriately circumspect and consider other modes of inhibition that are induced by activation or potentiation of other receptors (e.g., GABAergic or glycinergic).

Our results did not support Cr stimulation of inhibitory GABAA receptors (see our answer to Point 7 in of Reviewer 2).

Condition 5 may be met, because the authors applied exogenous creatine and observed inhibition (Fig. 7). However, this is tough to know without understanding the effects of endogenous release of creatine. if they were to test if the absence of creatine caused excess excitation (at putative creatinergic synapses), then that would be supportive of the same.

After the submission of our manuscript, we found a recent paper showing that slc6a8 knockout led to increased excitation in pyramidal neurons in the prefrontal cortex (PFC), with increased firing frequency (Ghirardini et al., 2023). Because we have shown that slc6a8 knockout would cause decrease of Cr in SVs (Figure 2 in our paper), this result provide the evidence described as Condition 5 of this reviewer: that decrease of Cr in SVs led to excess excitation.

For condition 6, the authors made a great effort with Slc6a8. This is a very tough criterion to understand for many synapses and neurotransmitters.

In terms of fundamental neuroscience, the story would be impactful if proven correct. There are certainly more neurotransmitters out there than currently identified.

The impact as framed by the authors in the abstract and introduction for intellectual disability is uncertain (forming a "new basis for ID pathogenesis") and it seems quite speculative beyond the data in this paper.

We deleted this sentence.

Reviewer #1 (Recommendations For The Authors):

To strengthen the manuscript, I suggest the following considerations:

1) The key missing evidence to my mind is a receptor - but this is clearly outside the scope of this paper. Yet, I am surprised that in the list of criteria for neurotransmitters in general there is no mention of a receptor. Furthermore, many receptors have been identified through receptor agonists or antagonists, like neurotoxins or drugs. The authors do not talk about putative receptors except for a sentence in the discussion where they speculate on a GPCR. There are numerous GPCR agonists and antagonists, which may be a long-shot, or something even a bit more designed based on knowledge about creatine? I do not think the publication of this manuscript should have been made dependent on finding an agonist or antagonist of this specific unknown receptor (if it exists), but it would be good to have at least some leads on this from the authors what has been tried or what could be done? How about a manipulation of G-protein-coupled signal transduction to support the idea that there IS such a GPCR? There may be a real opportunity here to test existing compounds in wild type, the slc6a8 and agat mutants.

We will keep trying, but accept the reality that Rome was not built in a single day and that no transmitter was proven by one single paper.

A key new puzzle piece of evidence is the identification of creatine in synaptic vesicles. The experiment relies heavily on the purity of the SV fraction using the anti-synaptophysin antibody. I am quite sure that these preparations contain many other compartments - and of course a big mix of synaptic (and other) vesicles. Would it be possible to purify with an anti slc6a8 antibody?

Sl6a8 is expressed in on the plasma membrane of neurons7-9, instead of synaptic vesicles. Consistent with this, we could not detect obvious Slc6a8-HA signal in our starting material (Lane S in Author response image 6) that was used for SV purification. We have tried to purify SVs by HA antibody in Slc6a8 mice and SV markers could not be detected.

Author response image 6.

Lack of Slc6a8-HA in our starting material. In Slc6a8-HA knock-in mice, the HA signal was present in whole brain homogenate (H), but not obvious in supernatants (S) following 35000 × centrifugation. In contrast, SV marker Syp was present in supernatants.

The K stimulation protocol in slices is relatively crude, as all neurons in the slice get simultaneously overactivated - and some of the effects on Ca-dependent release are not very strong (e.g. the 35 neurons that were not responsive to creatine at all). A primary neuronal culture of neurons that respond to creatine would strengthen this section.

To avoid the disadvantage of K stimulation, we also performed optogenetic experiments recently and obtained encouraging preliminary results.

Reviewer #2 (Recommendations For The Authors):

1) The different sections of the manuscript are not separated by headers.

2) The beginning of the results section either does not reference the underlying literature or refers to unpublished data.

We have kept a bit background in the beginning of the Results section.

3) The text contains many opinions and historical information that are not required (e.g., "It has never been easy to discover a new neurotransmitter, especially one in the central nervous system (CNS). We have been searching for new neurotransmitters for 12 years."; l. 17).

This is a field that has been dormant for decades and such background introductions are helpful for at least some readers.

4) Almeida et al. (2008; doi: 10.1002/syn.20280) provided evidence for electrical activity-, and Ca2+-dependent Cr release from rat brain slices. This paper should be introduced in the introduction.

Those were stand-alone papers which have not been reproduced or paid attention to. Our introduction part did not mention them because our research did not begin with those papers. We had no idea that those papers existed when we began. We started with SV purification and only read those papers afterwards. Thus, they were not necessary background to our paper but can be discussed after we discovered Cr in SVs.

5) Fig. 7: A Y-scale for the stimulation protocol is missing.

Revised.

Reviewer #3 (Recommendations For The Authors):

The main suggestion by this reviewer (beyond the details in the public review) is to consider the full spectrum of biology that is consistent with these results. By my reading, creatine could be a neurotransmitter, but other possibilities also exist, and the authors need to highlight those too.

We have discussed non-transmitter role in the discussion.

References

Ghirardini, E., G. Sagona, A. Marquez-Galera, F. Calugi, C. M. Navarron, F. Cacciante, S. Chen, F. Di Vetta, L. Dada, R. Mazziotti, L. Lupori, E. Putignano, P. Baldi, J. P. Lopez-Atalaya, T. Pizzorusso, and L. Baroncelli. 2023. Cell-specific vulnerability to metabolic failure: the crucial role of parvalbumin expressing neurons in creatine transporter deficiency. Acta Neuropathol Commun, 11: 34. doi: 10.1186/s40478-023-01533-w.

Lowe, M. T., Faull, R. L., Christie, D. L. & Waldvogel, H. J. Distribution of the creatine transporter throughout the human brain reveals a spectrum of creatine transporter immunoreactivity. J Comp Neurol 523, 699-725 (2015). https://doi.org:10.1002/cne.23667

Mak, C. S. et al. Immunohistochemical localisation of the creatine transporter in the rat brain. Neuroscience 163, 571-585 (2009). https://doi.org:10.1016/j.neuroscience.2009.06.065.

Molchanova, S. M., Oja, S. S. & Saransaari, P. Mechanisms of enhanced taurine release under Ca2+ depletion. Neurochem Int 47, 343-349 (2005). https://doi.org:10.1016/j.neuint.2005.04.027

Philibert, R. A., Rogers, K. L. & Dutton, G. R. K+-evoked taurine efflux from cerebellar astrocytes: on the roles of Ca2+ and Na+. Neurochem Res 14, 43-48 (1989). https://doi.org:10.1007/BF00969756

Rosko, L. M. et al. Cerebral Creatine Deficiency Affects the Timing of Oligodendrocyte Myelination. J Neurosci 43, 1143-1153 (2023). https://doi.org:10.1523/JNEUROSCI.2120-21.2022

Saransaari, P. & Oja, S. S. Characteristics of taurine release in slices from adult and developing mouse brain stem. Amino Acids 31, 35-43 (2006). https://doi.org:10.1007/s00726-006-0290-5

Schmidt, A. et al. Severely altered guanidino compound levels, disturbed body weight homeostasis and impaired fertility in a mouse model of guanidinoacetate N-methyltransferase (GAMT) deficiency. Hum Mol Genet 13, 905-921 (2004). https://doi.org:10.1093/hmg/ddh112

Speer, O. et al. Creatine transporters: a reappraisal. Mol Cell Biochem 256-257, 407-424 (2004). https://doi.org:10.1023/b:mcbi.0000009886.98508.e7

Takuma, K. et al. Ca2+ depletion facilitates taurine release in cultured rat astrocytes. Jpn J Pharmacol 72, 75-78 (1996). https://doi.org:10.1254/jjp.72.75

Author response:

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

Public Review:

Reviewer #2 (Public Review): 

Regarding reviewer #2 public review, we update here our answers to this public review with new analysis and modification done in the manuscript. 

This manuscript is missing a direct phenotypic comparison of control cells to complement that of cells expressing RhoGEF2-DHPH at "low levels" (the cells that would respond to optogenetic stimulation by retracting); and cells expressing RhoGEF2-DHPH at "high levels" (the cells that would respond to optogenetic stimulation by protruding). In other words, the authors should examine cell area, the distribution of actin and myosin, etc in all three groups of cells (akin to the time zero data from figures 3 and 5, with a negative control). For example, does the basal expression meaningfully affect the PRG low-expressing cells before activation e.g. ectopic stress fibers? This need not be an optogenetic experiment, the authors could express RhoGEF2DHPH without SspB (as in Fig 4G). 

Updated answer: We thank reviewer #2 for this suggestion. PRG-DHPH overexpression is known to affect the phenotype of the cell as shown in Valon et al., 2017. In our experiments, we could not identify any evidence of a particular phenotype before optogenetic activation apart from the area and spontaneous membrane speed that were already reported in our manuscript (Fig 2E and SuppFig 2). Regarding the distribution of actin and myosin, we did not observe an obvious pattern that will be predictive of the protruding/retracting phenotype. Trying to be more quantitative, we have classified (by eye, without knowing the expression level of PRG nor the future phenotype) the presence of stress fibers, the amount of cortical actin, the strength of focal adhesions, and the circularity of cells. As shown below, when these classes are binned by levels of expression of PRG (two levels below the threshold and two above) there is no clear determinant. Thus, we concluded that the main driver of the phenotype was the PRG basal expression rather than any particularity of the actin cytoskeleton/cell shape.

Author response image 1.

Author response image 2.

Relatedly, the authors seem to assume ("recruitment of the same DH-PH domain of PRG at the membrane, in the same cell line, which means in the same biochemical environment." supplement) that the only difference between the high and low expressors are the level of expression. Given the chronic overexpression and the fact that the capacity for this phenotypic shift is not recruitmentdependent, this is not necessarily a safe assumption. The expression of this GEF could well induce e.g. gene expression changes. 

Updated answer: We agree with reviewer #2 that there could be changes in gene expression. In the next point of this supplementary note, we had specified it, by saying « that overexpression has an influence on cell state, defined as protein basal activity or concentration before activation. »  We are sorry if it was not clear, and we changed this sentence in the revised manuscript (in red in the supp note). 

One of the interests of the model is that it does not require any change in absolute concentrations, beside the GEF. The model is thought to be minimal and fits well and explains the data with very few parameters. We do not show that there is no change in concentration, but we show that it is not required to invoke it. We revised a sentence in the new version of the manuscript to include this point.

Additional answer: During the revision process, we have been looking for an experimental demonstration of the independence of the phenotypic switch to any change in global gene expression pattern due to the chronic overexpression of PRG. Our idea was to be in a condition of high PRG overexpression such that cells protrude upon optogenetic activation, and then acutely deplete PRG to see if cells where then retracting. To deplete PRG in a timescale that prevent any change of gene expression, we considered the recently developed CATCHFIRE (PMID: 37640938) chemical dimerizer. We designed an experiment in which the PRG DH-PH domain was expressed in fusion with a FIRE-tag and co-expressing the FIRE-mate fused to TOM20 together with the optoPRG tool. Upon incubation with the MATCH small molecule, we should be able to recruit the overexpressed PRG to the mitochondria within minutes, hereby preventing it to form a complex with active RhoA in the vicinity of the plasma membrane. Unfortunately, despite of numerous trials we never achieved the required conditions: we could not have cells with high enough expression of PRGFIRE-tag (for protrusive response) and low enough expression of optoPRG (for retraction upon PRGFIRE-tag depletion). We still think this would be a nice experiment to perform, but it will require the establishment of a stable cell line with finely tuned expression levels of the CATCHFIRE system that goes beyond the timeline of our present work.      

Concerning the overall model summarizing the authors' observations, they "hypothesized that the activity of RhoA was in competition with the activity of Cdc42"; "At low concentration of the GEF, both RhoA and Cdc42 are activated by optogenetic recruitment of optoPRG, but RhoA takes over. At high GEF concentration, recruitment of optoPRG lead to both activation of Cdc42 and inhibition of already present activated RhoA, which pushes the balance towards Cdc42."

These descriptions are not precise. What is the nature of the competition between RhoA and Cdc42? Is this competition for activation by the GEFs? Is it a competition between the phenotypic output resulting from the effectors of the GEFs? Is it competition from the optogenetic probe and Rho effectors and the Rho biosensors? In all likelihood, all of these effects are involved, but the authors should more precisely explain the underlying nature of this phenotypic switch. Some of these points are clarified in the supplement, but should also be explicit in the main text. 

Updated answer: We consider the competition between RhoA and Cdc42 as a competition between retraction due to the protein network triggered by RhoA (through ROCK-Myosin and mDia-bundled actin) and the protrusion triggered by Cdc42 (through PAK-Rac-ARP2/3-branched Actin). We made this point explicit in the main text.  

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):  

Major 

- why this is only possible for such few cells. Can the authors comment on this in the discussion? Does the model provide any hints? 

As said in our answer to the public comment or reviewer #1, we think that the low number of cells being able to switch can be explained by two different reasons: 

(1) First, we were looking for clear inversions of the phenotype, where we could see clear ruffles in the case of the protrusion, and clear retractions in the other case. Thus, we discarded cells that would show in-between phenotypes, because we had no quantitative parameter to compare how protrusive or retractile they were. This reduced the number of switching cells 

(2) Second, we had a limitation due to the dynamic of the optogenetic dimer used here. Indeed, the control of the frequency was limited by the dynamic of unbinding of the optogenetic dimer. This dynamic of recruitment (~20s) is comparable to the dynamics of the deactivation of RhoA and Cdc42. Thus, the differences in frequency are smoothed and we could not vary enough the frequency to increase the number of switches. Thanks to the model, we can predict that increasing the unbinding rate of the optogenetic tool (shorter dimer lifetime) should allow us to increase the number of switching cells. 

We have added a sentence in the discussion to make this second point explicit.

- I would encourage the authors to discuss this molecular signaling switch in the context of general design principles of switches. How generalizable is this network/mechanism? Is it exclusive to activating signaling proteins or would it work with inhibiting mechanisms? Is the competition for the same binding site between activators and effectors a common mechanism in other switches? 

The most common design principle for molecular switches is the bistable switch that relies on a nonlinear activation (for example through cooperativity) with a linear deactivation. Such a design allows the switch between low and high levels. In our case, there is no need for a non-linearity since the core mechanism is a competition for the same binding site on active RhoA of the activator and the effectors. Thus, the design principle would be closer to the notion of a minimal “paradoxical component” (PMID: 23352242) that both activate and limit signal propagation, which in our case can be thought as a self-limiting mechanism to prevent uncontrolled RhoA activation by the positive feedback. Yet, as we show in our work, this core mechanism is not enough for the phenotypic switch to happen since the dual activation of RhoA and Cdc42 is ultimately required for the protrusion phenotype to take over the retracting one. Given the particularity of the switch we observed here, we do not feel comfortable to speculate on any general design principles in the main text, but we thank reviewer #1 for his/her suggestion.

- Supplementary figures - there is a discrepancy between the figures called in the text and the supplementary files, which only include SF1-4. 

We apologize for this error and we made the correction. 

- In the text, the authors use Supp Figure 7 to show that the phenotype could not be switched by varying the fold increase of recruitment through changing the intensity/duration of the light pulse. Aside from providing the figure, could you give an explanation or speculation of why? Does the model give any prediction as to why this could be difficult to achieve experimentally (is the range of experimentally feasible fold change of 1.1-3 too small? Also, could you clarify why the range is different than the 3 to 10-fold mentioned at the beginning of the results section? 

We thank the reviewer for this question, and this difference between frequency and intensity can be indeed understood in a simple manner through the model. 

All the reactions in our model were modeled as linear reactions. Thus, at any timepoint, changing the intensity of the pulse will only change proportionally the amount of the different components (amount of active RhoA, amount of sequestered RhoA, and amount of active Cdc42). This explains why we cannot change the balance between RhoA activity and Cdc42 activity only through the pulse strength. We observed the same experimentally: when we changed the intensity of the pulses, the phenotype would be smaller/stronger, but would never switch, supporting our hypothesis on the linearity of all biochemical reactions. 

On the contrary, changing the frequency has an effect, for a simple reason: the dynamics of RhoA and Cdc42 activation are not the same as the dynamics of inhibition of RhoA by the PH domain (see

Figure 4). The inhibition of RhoA by the PH is almost instantaneous while the activation of RhoGTPases has a delay (sets by the deactivation parameter k_2). Intuitively, increasing the frequency will lead to sustained inhibition of RhoA, promoting the protrusion phenotype. Decreasing the frequency – with a stronger pulse to keep the same amount of recruited PRG – restricts this inhibition of RhoA to the first seconds following the activation. The delayed activation of RhoA will then take over. 

We added two sentences in the manuscript to explain in greater details the difference between intensity and frequency.  

Regarding the difference between the 1.3-3 fold and the 3 to 10 fold, the explanation is the following: the 3 to 10 fold referred to the cumulative amount of proteins being recruited after multiple activations (steady state amount reached after 5 minutes with one activation every 30s); while the 1.3-3 fold is what can be obtained after only one single pulse of activation.  

- The transient expression achieves a large range of concentration levels which is a strength in this case. To solve the experimental difficulties associated with this, i.e. finding transfected cells at low cell density, the authors developed a software solution (Cell finder). Since this approach will be of interest for a wide range of applications, I think it would deserve a mention in the discussion part. 

We thank the reviewer for his/her interest in this small software solution.

We developed the description of the tool in the Method section. The Cell finder is also available with comments on github (https://github.com/jdeseze/cellfinder) and usable for anyone using Metamorph or Micromanager imaging software. 

Minor 

- Can the authors describe what they mean with "cell state"? It is used multiple times in the manuscript and can be interpreted as various things. 

We now explain what we mean by ‘cell state’ in the main text :

“protein basal activities and/or concentrations - which we called the cell state”

- “(from 0% to 45%, Figure 2D)", maybe add here: "compare also with Fig. 2A". 

We completed the sentence as suggested, which clarifies the data for the readers.

- The sentence "Given that the phenotype switch appeared to be controlled by the amount of overexpressed optoPRG, we hypothesized that the corresponding leakiness of activity could influence the cell state prior to any activation." might be hard to understand for readers unfamiliar with optogenetic systems. I suggest adding a short sentence explaining dark-state activity/leakiness before putting the hypothesis forward. 

We changed this whole beginning of the paragraph to clarify.

- Figure 2E and SF2A. I would suggest swapping these two panels as the quantification of the membrane displacement before activation seems more relevant in this context. 

We thank reviewer #1 for this suggestion and we agree with it (we swapped the two panels)

- Fig. 2B is missing the white frames in the mixed panels. 

We are sorry for this mistake, we changed it in the new version.  

- In the text describing the experiment of Fig. 4G, it would again be helpful to define what the authors mean by cell state, or to state the expected outcome for both hypotheses before revealing the result.

We added precisions above on what we meant by cell state, which is the basal protein activities and/or concentrations prior to optogenetic activation. We added the expectation as follow: 

To discriminate between these two hypotheses, we overexpressed the DH-PH domain alone in another fluorescent channel (iRFP) and recruited the mutated PH at the membrane. “If the binding to RhoA-GTP was only required to change the cell state, we would expect the same statistics than in Figure 2D, with a majority of protruding cells due to DH-PH overexpression. On the contrary, we observed a large majority of retracting phenotype even in highly expressing cells (Figure 4G), showing that the PH binding to RhoA-GTP during recruitment is a key component of the protruding phenotype.”

- Figure 4H,I: "of cells that overexpress PRG, where we only recruit the PH domain" doesn't match with the figure caption. Are these two constructs in the same cell? If not please clarify the main text. 

We agree that it was not clear. Both constructs are in the same cell, and we changed the figure caption accordingly.  

- "since RhoA dominates Cdc42" is this concluded from experiments (if yes, please refer to the figure) or is this known from the literature (if yes, please cite). 

The assumption that RhoA dominates Cdc42 comes from the fact that we see retraction at low PRG concentration. We assumed that RhoA is responsible for the retraction phenotype. Our assumption is based on the literature (Burridge 2004 as an example of a review, confirmed by many experiments, such as the direct recruitment of RhoA to the membrane, see Berlew 2021) and is supported by our observations of immediate increase of RhoA activity at low PRG. We modified the text to clarify it is an assumption.

- Fig. 6G  o left: is not intuitive, why are the number of molecules different to start with? 

The number of molecules is different because they represent the active molecules: increasing the amount of PRG increases the amount of active RhoA and active Cdc42. We updated the figure to clarify this point.

o right: the y-axis label says "phenotype", maybe change it to "activity" or add a second y-axis on the right with "phenotype"? 

We updated the figure following reviewer #1 suggestion.

- Discussion: "or a retraction in the same region" sounds like in the same cell. Perhaps rephrase to state retraction in a similar region? 

Sorry for the confusion, we change it to be really clear: “a protrusion in the activation region when highly expressed, or a retraction in the activation region when expressed at low concentrations.”

Typos: 

- "between 3 and 10 fold" without s. 

- Fig. 1H, y-axis label. 

- "whose spectrum overlaps" with s. 

- "it first decays, and then rises" with s. 

- Fig 4B and Fig 6B. Is the time in sec or min? (Maybe double-check all figures). 

- "This result suggests that one could switch the phenotype in a single cell by selecting it for an intermediate expression level of the optoPRG.". 

- "GEF-H1 PH domain has almost the same inhibition ability as PRG PH domain". 

We corrected all these mistakes and thank the reviewer for his careful reading of the manuscript.

Reviewer #2 (Recommendations For The Authors): 

Likewise, the model assumes that at high PRG GEF expression, the "reaction is happening far from saturation ..." and that "GTPases activated with strong stimuli -giving rise to strong phenotypic changes- lead to only 5% of the proteins in a GTP-state, both for RhoA and Cdc42". Given the high levels of expression (the absolute value of which is not known) this assumption is not necessarily safe to assume. The shift to Cdc42 could indeed result from the quantitative conversion of RhoA into its active state. 

We agree with the reviewer that the hypothesis that RhoA is fully converted into its active state cannot be completely ruled out. However, we think that the two following points can justify our choice.

- First, we see that even in the protruding phenotype, RhoA activity is increasing upon optoPRG recruitment (Figure 3). This means that RhoA is not completely turned into its active GTP-loaded state. The biosensor intensity is rising by a factor 1.5 after 5 minutes (and continue to increase, even if not shown here). For sure, it could be explained by the relocation of RhoA to the place of activation, but it still shows that cells with high PRG expression are not completely saturated in RhoA-GTP. 

- We agree that linearity (no saturation) is still an hypothesis and very difficult to rule out, because it is not only a question of absolute concentrations of GEFs and RhoA, but also a question of their reaction kinetics, which are unknow parameters in vivo. Yet, adding a saturation parameter would mean adding 3 unknown parameters (absolute concentrations of RhoA, as well as two reaction constants). The fact that there are not needed to fit the complex curves of RhoA as we do with only one parameter tends to show that the minimal ingredients representing the interaction are captured here.  

The observed "inhibition of RhoA by the PH domain of the GEF at high concentrations" could result from the ability of the probe to, upon membrane recruitment, bind to active RhoA (via its PH domain) thereby outcompeting the RhoA biosensor (Figure 4A-C). This reaction is explicitly stated in the supplemental materials ("PH domain binding to RhoA-GTP is required for protruding phenotype but not sufficient, and it is acting as an inhibitor of RhoA activity."), but should be more explicit in the main text. Indeed, even when PRG DHPH is expressed at high concentrations, it does activate RhoA upon recruitment (figure 3GH). Not only might overexpression of this active RhoA-binding probe inhibit the cortical recruitment of the RhoA biosensor, but it may also inhibit the ability of active RhoA to activate its downstream effectors, such as ROCK, which could explain the decrease in myosin accumulation (figure 3D-F). It is not clear that there is a way to clearly rule this out, but it may impact the interpretation. 

This hypothesis is actually what we claim in the manuscript. We think that the inhibition of RhoA by the PH domain is explained by its direct binding. We may have missed what Reviewer #2 wanted to say, but we think that we state it explicitly in the main text :

“Knowing that the PH domain of PRG triggers a positive feedback loop thanks to its binding to active RhoA 18, we hypothesized that this binding could sequester active RhoA at high optoPRG levels, thus being responsible for its inhibition.”

And also in the Discussion:

“However, this feedback loop can turn into a negative one for high levels of GEF: the direct interaction between the PH domain and RhoA-GTP prevents RhoA-GTP binding to effectors through a competition for the same binding site.”

We may have not been clear, but we think that this is what is happening: the PH domain prevents the binding to effectors and decreases RhoA activity (as was shown in Chen et al. 2010).  

The X-axis in Figure 4C time is in seconds not minutes. The Y-axis in Figure 4H is unlabeled. 

We are sorry for the mistake of Figure 4C. We changed the Y-axis in the Figure 4h.  

Although this publication cites some of the relevant prior literature, it fails to cite some particularly relevant works. For example, the authors state, "The LARG DH domain was already used with the iLid system" and refers to a 2018 paper (ref 19), whereas that domain was first used in 2016 (PMID 27298323). Indeed, the authors used the plasmid from this 2016 paper to build their construct. 

We thank the reviewer for pointing out this error, we have corrected the citation and put the seminal one in the revised version.

An analogous situation pertains to previous work that showed that an optogenetic probe containing the DH and PH domains in RhoGEF2 is somewhat toxic in vivo (table 6; PMID 33200987). Furthermore, it has previously been shown that mutation of the equivalent of F1044A and I1046E eliminates this toxicity (table 6; PMID 33200987) in vivo. This is particularly important because the Rho probe expressing RhoGEF2-DHPH is in widespread usage (76 citations in PubMed). The ability of this probe to activate Cdc42 may explain some of the phenotypic differences described resulting from the recruitment of RhoGEF2-DHPH and LARG-DH in a developmental context (PMID 29915285, 33200987). 

We thank reviewer #2 for these comments, and added a small section in the discussion, for optogenetic users: 

This underlines the attention that needs to be paid to the choice of specific GEF domains when using optogenetic tools. Tools using DH-PH domains of PRG have been widely used, both in mammalian cells and in Drosophila (with the orthologous gene RhoGEF2), and have been shown to be toxic in some contexts in vivo 28. Our study confirms the complex behavior of this domain which cannot be reduced to a simple RhoA activator.   

Concerning the experiment shown in 4D, it would be informative to repeat this experiment in which a non-recruitable DH-PH domain of PRG is overexpressed at high levels and the DH domain of LARG is recruited. This would enable the authors to distinguish whether the protrusion response is entirely dependent on the cell state prior to activation or the combination of the cell state prior to activation and the ability of PRG DHPH to also activate Cdc42. 

We thank the reviewer for his suggestion. Yet, we think that we have enough direct evidence that the protruding phenotype is due to both the cell state prior to activation and the ability of PRG DHPH to also activate Cdc42. First, we see a direct increase in Cdc42 activity following optoPRG recruitment (see Figure 6). This increase is sustained in the protruding phenotype and precedes Rac1 and RhoA activity, which shows that it is the first of these three GTPases to be activated. Moreover, we showed that inhibition of PAK by the very specific drug IPA3 is completely abolishing only the protruding phenotype, which shows that PAK, a direct effector of Cdc42 and Rac1, is required for the protruding phenotype to happen. We know also that the cell state prior to activation is defining the phenotype, thanks to the data presented in Figure 2. 

We further showed in Figure 1 that LARG DH-PH domain was not able to promote protrusion. The proposed experiment would be interesting to confirm that LARG does not have the ability to activate another GTPase, even in a different cell state with overexpressed PRG. However, we are not sure it would bring any substantial findings to understand the mechanism we describe here, given the facts provided above.  

Similarly, as PRG activates both Cdc42 and Rho at high levels, it would be important to determine the extent to which the acute Rho activation contributes to the observed phenotype (e.g. with Rho kinase inhibitor). 

We agree with the reviewer that it would be interesting to know whether RhoA activation contributes to the observed phenotype, and we have tried such experiments. 

For Rho kinase inhibitor, we tried with Y-27632 and we could never prevent the protruding phenotype to happen. However, we could not completely abolish the retracting phenotype either (even when the effect on the cells was quite strong and visible), which could be due to other effectors compensating for this inhibition. As RhoA has many other effectors, it does not tell us that RhoA is not required for protrusion. 

We also tried with C3, which is a direct inhibitor of RhoA. However, it had too much impact on the basal state of the cells, making it impossible to recruit (cells were becoming round and clearly dying. As both the basal state and optogenetic activation require the activation of RhoA, it is hard to conclude out of experiments where no cell is responding. 

The ability of PRG to activate Cdc42 in vivo is striking given the strong preference for RhoA over Cdc42 in vitro (2400X) (PMID 23255595). Is it possible that at these high expression levels, much of the RhoA in the cell is already activated, so that the sole effect that recruited PRG can induce is activation of Cdc42? This is related to the previous point pertaining to absolute expression levels.  

As discussed before, we think that it is not only a question of absolute expression levels, but also of the affinities between the different partners. But Reviewer #2 is right, there is a competition between the activation of RhoA and Cdc42 by optoPRG, and activation of Cdc42 probably happens at higher concentration because of smaller effective affinity.

Still, we know that activation of the Cdc42 by PRG DH-PH domain is possible in vivo, as it was very clearly shown in Castillo-Kauil et al., 2020 (PMID 33023908). They show that this activation requires the linker between DH and PH domain of PRG, as well as Gαs activation, which requires a change in PRG DH-PH conformation. This conformational switch does not happen in vitro, which might explain why the affinity against Cdc42 was found to be very low. 

Minor points 

In both the abstract and the introduction the authors state, "we show that a single protein can trigger either protrusion or retraction when recruited to the plasma membrane, polarizing the cell in two opposite directions." However, the cells do not polarize in opposite directions, ie the cells that retract do not protrude in the direction opposite the retraction (or at least that is not shown). Rather a single protein can trigger either protrusion or retraction when recruited to the plasma membrane, depending upon expression levels. 

We thank the reviewer for this remark, and we agree that we had not shown any data supporting a change in polarization. We solved this issue, by showing now in Supplementary Figure 1 the change in areas in both the activated and in the not activated region. The data clearly show that when a protrusion is happening, the cell retracts in the non-activated region. On the other hand, when the cell retracts, a protrusion happens in the other part of the cell, while the total area is staying approximately constant. 

We added the following sentence to describe our new figure:

Quantification of the changes in membrane area in both the activated and non-activated part of the cell (Supp Figure 1B-C) reveals that the whole cell is moving, polarizing in one direction or the other upon optogenetic activation.

While the authors provide extensive quantitative data in this manuscript and quantify the relative differences in expression levels that result in the different phenotypes, it would be helpful to quantify the absolute levels of expression of these GEFs relative to e.g. an endogenously expressed GEF. 

We agree with the reviewer comment, and we also wanted to have an idea of the absolute level of expression of GEFs present in these cells to be able to relate fluorescent intensities with absolute concentrations. We tried different methods, especially with the purified fluorescent protein, but having exact numbers is a hard task.

We ended up quantifying the amount of fluorescent protein within a stable cell line thanks to ELISA and comparing it with the mean fluorescence seen under the microscope. 

We estimated that the switch concentration was around 200nM, which is 8 times more than the mean endogenous concentration according to https://opencell.czbiohub.org/, but should be reachable locally in wild type cell, or globally in mutated cancer cells. 

Given the numerical data (mostly) in hand, it would be interesting to determine whether RhoGEF2 levels, cell area, the pattern of actin assembly, or some other property is most predictive of the response to PRG DHPH recruitment. 

We think that the manuscript made it clear that the concentration of PRG DHPH is almost 100% predictive of the response to PRG DHPH. We believe that other phenotypes such as the cell area or the pattern of actin assembly would only be consequences of this. Interestingly, as experimentators we were absolutely not able to predict the behavior by only seeing the shape of the cell, event after hundreds of activation experiments, and we tried to find characteristics that would distinguish both populations with the data in our hands and could not find any.

There is some room for general improvement/editing of the text. 

We tried our best to improve the text, following reviewers suggestions.

Author Response

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

We would like to thank the reviewers for their insightful comments and recommendations. We have extensively revised the manuscript in response to the valuable feedback. We believe the results is a more rigorous and thoughtful analysis of the data. Furthermore, our interpretation and discussion of the findings is more focused and highlights the importance of the circuit and its role in the response to stress. Thank you for helping to improve the presented science.

Key changes made in response to the reviewers comments include:

• Revision of statistical analyses for nearly all figures, with the addition of a new table of summary statistics to include F and/or t values alongside p-values.

• Addition of statistical analyses for all fiber photometry data.

• Examination of data for possible sex dependent effects.

• Clarification of breeding strategies and genotype differences, with added details to methods to improve clarity.

• Addressing concerns about the specificity of virus injections and the spread, with additional details added to methods.

• Modification of terminology related to goal-directed behavior based on reviewer feedback, including removal of the term from the manuscript.

• Clarification and additional data on the use of photostimulation and its effects, including efforts to inactivate neurons for further insight, despite technical challenges.

• Correction of grammatical errors throughout the manuscript.

Reviewer 1:

Despite the manuscript being generally well-written and easy to follow, there are several grammatical errors throughout that need to be addressed.

Thank you for highlighting this issue. Grammatical errors have been fixed in the revised version of the manuscript.

Only p values are given in the text to support statistical differences. This is not sufficient. F and/or t values should be given as well.

In response to this critique and similar comments from Reviewer 2, we re-evaluated our approach to statistical analyses and extensively revised analyses for nearly all figures. We also added a new table of summary statistics (Supplemental Table 1) containing the type of analysis, statistic, comparison, multiple comparisons, and p value(s). For Figures 4C-E, 5C, 6C-E, 7H-I, and 8H we analyzed these data using two-way repeated measures (RM) ANOVA that examined the main effect of time (either number of sessions or stimulation period) in the same animal and compared that to the main effect of genotype of the animal (Cre+ vs Cre-), and if there was an interaction. For Supplemental Figure 7A we also conducted a two-way RM ANOVA with time as a factor and activity state (number of port activations in active vs inactive nose port) as the other in Cre+ mice. For Figures 5D-E we conducted a two-way mixed model ANOVA that accounted and corrected for missing data. In figures that only compared two groups of data (Figures 5F-L, 6F, 8C-D, 8I, and Supp 6F-G) we used two-tailed t-test for the analysis. If our question and/or hypothesis required us to conduct multiple comparisons between or within treatments, we conducted Bonferroni’s multiple comparisons test for post hoc analysis (we note which groups we compared in Supplemental Table 1). For figures that did or did not show a change in calcium activity (Figure 3G, 3I-K, 7B, 7D-E, 8E-F), we compared waveform confidence intervals (Jean-Richard-Dit-Bressel, Clifford, McNally, 2020). The time windows we used as comparison are noted in Supplemental Table 1, and if the comparisons were significant at 95%, 99%, and 99.9% thresholds.

None of prior comparisons in prior analyses that were significant were found to have fallen below thresh holds for significance. Of those found to be not significantly different, only one change was noted. In Figure 6E there was now a significant baseline difference between Cre+ and Cre- mice with Cre- mice taking longer to first engage the port compared to Cre+ mice (p=0.045). Although the more rigorous approach the statistical analyses did not change our interpretations we feel the enhanced the paper and thank the reviewer for pushing this improvement.

Moreover, the fibre photometry data does not appear to have any statistical analyses reported - only confidence intervals represented in the figures without any mention of whether the null hypothesis that the elevations in activity observed are different from the baseline.

This is particularly important where there is ambiguity, such as in Figure 3K, where the spontaneous activity of the animal appears to correlate with a spike in activity but the text mentions that there is no such difference. Without statistics, this is difficult to judge.

Thank you for highlighting this critical point and providing an opportunity to strengthen our manuscript. We added statistical analyses of all fiber photometry data using a recently described approach based on waveform confidence intervals (Jean-Richard-Dit-Bressel, Clifford, McNally, 2020). In the statistical summary (Supplemental Table 1) we note the time window that we used for comparison in each analysis and if the comparisons were significant at 95%, 99%, and 99.9% thresholds. Thank you from highlighting this and helping make the manuscript stronger.

With respect to Figure 3K, we are not certain we understood the spike in activity the reviewer referred to. Figure 3J and K include both velocity data (gold) and Ca2+ dependent signal (blue). We used episodes of velocity that were comparable to the avoidance respond during the ambush test and no significant differences in the Ca2+ signal when gating around changes in velocity in the absence of stressor (Supplemental Table1). This is in contrast to the significant change in Ca2+ signal following a mock predator ambush (Figure 3J). We interpret these data together to indicate that locomotion does not correlate with an increase in calcium activity in SuMVGLUT2+::POA neurons, but that coping to a stressor does. This conclusion is further examined in supplemental Figure 5, including examining cross-correlation to test for temporally offset relationship between velocity and Ca2+ signal in SUMVGLUT2+::POA neurons.

The use of photostimulation only is unfortunate, it would have been really nice to see some inactivation of these neurons as well. This is because of the well-documented issues with being able to determine whether photostimulation is occurring in a physiological manner, and therefore makes certain data difficult to interpret. For instance, with regards to the 'active coping' behaviours - is this really the correct characterisation of what's going on? I wonder if the mice simply had developed immobile responding as a coping strategy but when they experience stimulation of these neurons that they find aversive, immobility is not sufficient to deal with the summative effects of the aversion from the swimming task as well as from the neuronal activation? An inactivation study would be more convincing.

We agree with the point of the reviewer, experiments demonstrating necessity of SUMVGLUT2+::POA neurons would have added to the story here. We carried out multiple experiments aimed at addressing questions about necessity of SuMVGLUT2+::POA neurons in stress coping behaviors, specifically the forced swim assay. Efforts included employing chemogenetic, optogenetic, and tetanus toxin-based methods. We observed no effects on locomotor activity or stress coping. These experiments are both technically difficult and challenging to interpret. Interpretation of negative results, as we obtained, is particularly difficult because of potential technical confounds. Selective targeting of SuMVGLUT2+::POA neurons for inhibition requires a process requiring three viral injections and two recombination steps, increasing variability and reducing the number of neurons impacted. Alternatively, photoinhibition targeting SuMVGLUT2+::POA cells can be done using Retro-AAV injected into POA and a fiber implant over SuM. We tried both approaches. Data obtained were difficult to interpret because of questions about adequate coverage of SuMVGLUT2+::POA population by virally expressed constructs and/or light spread arose. The challenge of adequate coverage to effectively prevent output from the targeted population is further confounded by challenges inherent in neural inhibition, specifically determining if the inhibition created at the cellular level is adequate to block output in the context of excitatory inputs or if neurons must be first engaged in a particular manner for inhibition to be effective. Baseline neural activity, release probability, and post-synaptic effects could all be relevant, which photo-inhibition will potentially not resolve. So, while the trend is to always show “necessary and sufficient” effects, we’ve tried nearly everything, and we simply cannot conclude much from our mixed results. There are also wellestablished problems with existing photo-inhibition methods, which while people use them and tout them, are often ignored. We have a lot of expertise in photo-inhibition optogenetics, and indeed have used it with some success, developed new methods, yet in this particular case we are unable to draw conclusions related to inhibition. People have experienced similar challenges in locus coeruleus neurons, which have very low basal activity, and inhibition with chemogenetics is very hard, as well as with optogenetic pump-based approaches, because the neurons fire robust rebound APs. We have spent almost 2.5 years trying to get this to work in this circuit because reviews have been insistent on this result for the paper to be conclusive. Unfortunately, it simply isn’t possible in our view until we know more about the cell types involved. This is all in spite of experience using the approach in many other publications.

We also employed less selective approaches, such as injecting AAV-DIO-tetanus toxin light chain (Tettox) constructs directly into SuM VGLUT2-Cre mice but found off target effects impacting animal wellbeing and impeding behavioral testing due viral spread to surrounding areas.

While we are disappointed for being unable to directly address questions about necessity of SuMVGLUT2+::POA neurons in active coping with experimental data, we were unable to obtain results allowing for clear interpretation across numerous other domains the reviewers requested. We also feel strongly that until we have a clear picture of the molecular cell type architecture in the SuM, and Cre-drivers to target subsets of neurons, this question will be difficult to resolve for any group. We are working now on RNAseq and related spatial transcriptomics efforts in the SuM and examining additional behavioral paradigm to resolve these issues, so stay tuned for future publications.

Accordingly, we avoid making statements relating to necessity in the manuscript. In spite of having several lines of physiological data with strong robust correlations behavior related to the SuMVGLUT2+::POA circuit.

Nose poke is only nominally instrumental as it cannot be shown to have a unique relationship with the outcome that is independent of the stimuli-outcome relationships (in the same way that a lever press can, for example). Moreover, there is nothing here to show that the behaviours are goal-directed.

Thank you for highlighting this point. Regarding goal-direct terminology, we removed this terminology from the manuscript. Since the mice perform highly selective (active vs inactive) port activation robustly across multiple days of training the behavior likely transitions to habitual behavior. We only tested the valuation of stimuli termination of the final day of training with time limited progressive ratio test. With respect to lever press versus active port activation, we are unclear how using a lever in this context would offer a different interpretation. Lever pressing may be more sensitive to changes in valuation when compared to nose poke port activation (Atalayer and Rowland 2008); however, in this study the focus of the operant behavior is separating innate behaviors for learned action–outcome instrumental learned behaviors for threat response (LeDoux and Daw 2018). The robust highly selective activation of the active port illustrated in Figure 6 fits as an action–outcome instrumental behavior wherein mice learn to engage the active but not inactive port to terminate photostimulation. The first activation of the port occurs through exploration of the arena but as demonstrated by the number of active port activations and the decline in time of the first active port engagement, mice expressing ChR2eYFP learn to engage the port to terminate the stimulation. To aid in illustrating this point we have added Supplemental Figure 7 showing active and inactive port activations for both Cre+ and Cre- mice. This adds clarity to high rate of selective port activation driven my stimulation of SUMVGLUT2+::POA neurons compared to controls. The elimination of goal directed and providing additional data narrows and supports one of the key points of the operant experiment.

With regards to Figure 1: This is a nice figure, but I wonder if some quantification of the pathways and their density might be helpful, perhaps by measuring the intensity of fluorescence in image J (as these are processes, not cell bodies that can be counted)? Mind you, they all look pretty dense so perhaps this is not necessary! However, because the authors are looking at projections in so-called 'stress-engaged regions', the amygdala seems conspicuous by its absence. Did the authors look in the amygdala and find no projections? If so it seems that this would be worth noting.

This is an interesting question but has proven to be a very technically challenging question. We consulted with several leaders who routinely use complimentary viral tracing methods in the field. We were unable to devise a method to provide a satisfactorily meaningful quantitative (as opposed to qualitative) approach to compare SUMVGLUT2+::POA to SuMVGLUT2+ projections. A few limitations are present that hinder a meaningful quantitative approach. One limitation was the need for different viral strategies to label the two populations. Labeling SuMVGLUT2+::POA neurons requires using VGLUT2-Flp mice with two injections into the POA and one into SuM. Two recombinase steps were required, reducing efficiency of overlap. This combination of viral injections, particularly the injections of RetroAAVs in the POA, can induce significant quantitative variability due to tropism, efficacy, and variability of retro-viral methods, and viral infection generally. These issues are often totally ignored in similar studies across the “neural circuit” landscape, but it doesn’t make them less relevant here.

Although people do this in the field, and show quantification, we actually believe that it can be a quite misleading read-out of functionally relevant circuitry, given that neurotransmitter release ultimately is amplified by receptors post-synaptically, and many examples of robust behavioral effects have been observed with low fiber tracing complimentary methods (McCall, Siuda et al. 2017). In contrast, the broader SuMVGLUT2+ population was labeled using a single injection into the SuM. This means there like more efficient expression of the fluorophore. Additionally, in areas that contain terminals and passing fibers understanding and interpreting fluorescent signal is challenging. Together, these factors limit a meaningful quantitative comparison and make an interpretation difficult to make. In this context, we focused on a conservative qualitative presentation to demonstrate two central points. That 1) SuMVGLUT2+::POA neurons are subset of SuMVGLUT2+ neurons that project to specific areas and that exclude dentate gyrus, and they 2) arborize extensively to multiple areas which have be linked to threat responses. We agree that there is much to be learned about how different populations in SuM connect to targets in different regions of the brain and to continue to examine this question with different techniques. A meaningful quantitative study comparing projections is technically complex and, we feel, beyond our ability for this study.

Also, for the reasons above we do not believe that quantification provides exceptional clarity with respect to the putative function of the circuit, glutamate released, or other cotransmitters given known amplification at the post-synaptic side of the circuit.

With regard to the amygdala, other studies on SuM projections have found efferent projections to amygdala (Ottersen, 1980; Vertes, 1992). In our study we were unable to definitively determine projections from SuMVGLUT2+::POA neurons to amygdala, which if present are not particularly dense. For this reason we were conservative and do not comment on this particular structure.

I would suggest removing the term goal-directed from the manuscript and just focusing on the active vs. passive distinction.

We removed the use of goal-directed. Thank you for helping us clarify our terminology.

The effect observed in Figure 7I is interesting, and I'm wondering if a rebound effect is the most likely explanation for this. Did the authors inhibit the VGAT neurons in this region at any other times and observe a similar rebound? If such a rebound was not observed it would suggest that it is something specific about this task that is producing the behaviour. I would like it if the authors could comment on this.

We agree that results showing the change in coping strategy (passive to active) in forced swim after but not during stimulation of SuMVGAT+ neurons is quite interesting (Figure 7I). This experiment activated SuMVGAT+ neurons during a section of the forced swim assay and mice showed a robust shift to mobility after the stimulation of SuMVGAT+ neurons stopped. We did not carry out inhibition of SuMVGAT+ neurons in this manuscript. As the reviewer suggested, strong inhibition of local SuM neurons, including SUMVGLUT2+::POA neurons, could lead to rebound activity that may shift coping behaviors in confusing ways. We agree this is an interesting idea but do not have data to support the hypothesis further at this time.

Reviewer 2

(1) These are very difficult, small brain regions to hit, and it is commendable to take on the circuit under investigation here. However, there is no evidence throughout the manuscript that the authors are reliably hitting the targets and the spread is comparable across experiments, groups, etc., decreasing the significance of the current findings. There are no hit/virus spread maps presented for any data, and the representative images are cropped to avoid showing the brain regions lateral and dorsal to the target regions. In images where you can see the adjacent regions, there appears expression of cell bodies (such as Supp 6B), suggesting a lack of SuM specificity to the injections.

We agree with the reviewer that the areas studied are small and technically challenging to hit. This was one of driving motivations for using multiple tools in tandem to restrict the area targeted for stimulation. Approaches included using a retrograde AAVs to express ChR2eFYP in SUMVGLUT2+::POA neurons; thereby, restricting expression to VGLUT2+ neurons that project to the POA. Targeting was further limited by placement of the optic fiber over cell bodies on SuM. Thus, only neurons that are VGLUT2+, project to the POA, and were close enough to the fiber were active by photostimulation. Regrettably, we were not able to compile images from mice where the fiber was misplaced leading to loss of behavioral effects. We would have liked to provide that here to address this comment. Unfortunately, generating heat maps for injections is not possible for anatomic studies that use unlabeled recombinase as part of an intersectional approach. Also determining the point of injection of a retroAAV can be difficult to accurately determine its location because neurons remote to injection site and their processes are labeled.

Experiments described in Supplemental Figure 6B on VGAT neurons in SuM were designed and interpreted to support the point that SUMVGLUT2+::POA neurons are a distinct population that does not overlap with GABAergic neurons. For this point it is important that we targeted SuM, but highly confined targeting is not needed to support the central interpretation of the data. We do see labeling in SuM in VGAT-Cre mice but photo stimulation of SuMVGAT+ neurons does not generate the behavioral changes seen with activation of SUMVGLUT2+::POA neurons. As the reviewer points out, SuM is small target and viral injection is likely to spread beyond the anatomic boundaries to other VGAT+ neurons in the region, which are not the focus here. The activation would be restricted by the spread of light from the fiber over SuM (estimated to be about a 200um sphere in all directions). We did not further examine projections or localization of VGAT+ neurons in this study but focused on the differential behavioral effects of SUMVGLUT2+::POA neurons.

(2) In addition, the whole brain tracing is very valuable, but there is very little quantification of the tracing. As the tracing is the first several figures and supp figure and the basis for the interpretation of the behavior results, it is important to understand things including how robust the POA projection is compared to the collateral regions, etc. Just a rep image for each of the first two figures is insufficient, especially given the above issue raised. The combination of validation of the restricted expression of viruses, rep images, and quantified tracing would add rigor that made the behavioral effects have more significance.

For example, in Fig 2, how can one be sure that the nature of the difference between the nonspecific anterograde glutamate neuron tracing and the Sum-POA glutamate neuron tracing is real when there is no quantification or validation of the hits and expression, nor any quantification showing the effects replicate across mice? It could be due to many factors, such as the spread up the tract of the injection in the nonspecific experiment resulting in the labeling of additional regions, etc.

Relatedly, in Supp 4, why isn’t C normalized to DAPI, which they show, or area? Similar for G what is the mcherry coverage/expression, and why isn’t Fos normalized to that?

Thank you for highlighting the importance of anatomy and the value of anatomy. Two points based on the anatomic studies are central to our interpretation of the experimental data. First, SUMVGLUT2+::POA are a distinct population within the SuM. We show this by demonstrating they are not GABAergic and that they do not project to dentate gyrus. Projections from SuM to dentate gyrus have been described in multiple studies (Boulland et al., 2009; Haglund et al., 1987; Hashimotodani et al., 2018; Vertes, 1992) and we demonstrate them here for SuMVGLUT2+ cells. Using an intersectional approach in VGLUT2-Flp mice we show SUMVGLUT2+::POA neurons do not project to dentate gyrus. We show cell bodies of SUMVGLUT2+::POA neurons located in SuM across multiple figures including clear brain images. Thus, SUMVGLUT2+::POA neurons are SuM neurons that do not project to dentate gyrus, are not GABAergic, send projections to a distinct subset of targets, most notably excluding dentate gyrus. Second, SUMVGLUT2+::POA neurons arborize sending projections to multiple regions. We show this using a combinatorial genetic and viral approach to restrict expression of eYFP to only neurons that are in SuM (based on viral injection), project to the POA (based on retrograde AAV injection in POA), and VGLUT2+ (VGLUT2-Flp mice). Thus, any eYFP labeled projection comes from SUMVGLUT2+::POA neurons. We further confirmed projections using retroAAV injection into areas identified using anterograde approaches (Supplemental Figure 2). As discussed above in replies to Reviewer 1, we feel limitations are present that preclude meaningful quantitative analysis. We thus opted for a conservative interpretation as outlined.

Prior studies have shown efferent projections from SuM to many areas, and projections to dentate gyrus have received substantial attention (Bouland et al., 2009; Haglund, Swanson, and Kohler, 1984; Hashimotodani et al., 2018; Soussi et al., 2010; Vertes, 1992; Pan and McNaugton, 2004). We saw many of the same projections from SuMVGLUT2+ neurons. We found no projections from SUMVGLUT2+::POA neurons to dentate gyrus (Figure 2). Our description of SuM projection to dentate gyrus is not new but finding a population of neurons in SuM that does not project to dentate gyrus but does project to other regions in hippocampus is new. This finding cannot be explained by spread of the virus in the tract or non-selective labeling.

(3) The authors state that they use male and female mice, but they do not describe the n’s for each experiment or address sex as a biological variable in the design here. As there are baseline sex differences in locomotion, stress responses, etc., these could easily factor into behavioral effects observed here.

Sex specific effects are possible; however, the studies presented here were not designed or powered to directly examine them. A point about experimental design that helps mitigate against strong sex dependent effect is that often the paradigm we used examined baseline (pre-stimulation) behavior, how behavior changed during stimulation, and how behavior returned (or not) to baseline after stimulation. Thus, we test changes in individual behaviors. Although we had limited statistical power, we conducted analyses to examine the effects of sex as variable in the experiments and found no differences among males and females.

(4) In a similar vein as the above, the authors appear to use mice of different genotypes (however the exact genotypes and breeding strategy are not described) for their circuit manipulation studies without first validating that baseline behavioral expression, habituation, stress responses are not different. Therefore, it is unclear how to interpret the behavioral effects of circuit manipulation. For example in 7H, what would the VGLUT2-Cre mouse with control virus look like over time? Time is a confound for these behaviors, as mice often habituate to the task, and this varies from genotype to genotype. In Fig 8H, it looks like there may be some baseline differences between genotypes- what is normal food consumption like in these mice compared to each other? Do Cre+ mice just locomote and/or eat less? This issue exists across the figures and is related to issues of statistics, potential genotype differences, and other experimental design issues as described, as well as the question about the possibility of a general locomotor difference (vs only stress-induced). In addition, the authors use a control virus for the control groups in VGAT-Cre manipulation studies but do not explain the reasoning for the difference in approach.

Thank you for highlighting the need for greater clarity about the breeding strategies used and for these related questions. We address the breeding strategy and then move to address the additional concerns raised. We have added details to the methods section to address this point. For VGLUT2-Cre mice we use litter mates controls from Cre/WT x WT/WT cross. The VGLUT2-Cre line (RRID:IMSR_JAX:028863) (Vong L , et al. 2011) used here been used in many other reports. We are not aware of any reports indicating a phenotype associated with the addition of the IRES-Cre to the Slc17a6 loci and there is no expected impact of expression of VGLUT2. Also, we see in many of the experiments here that the baseline (Figures 4, 5, and 7) behaviors are not different between the Cre+ and Cre- mice. For VGAT-Cre mice we used a different breeding strategy that allowed us to achieve greater control of the composition of litters and more efficient cohorts cohort. A Cre/Cre x WT/WT cross yielded all Cre/WT litters. The AAV injected, ChR2eYFP or eYFP, allowed us to balance the cohort.

Regarding Figure 7H, which shows time immobile on the second day of a swim test, data from the Cre- mice demonstrate the natural course of progression during the second day of the test. The control mice in the VGAT-Cre cohort (Figure 7I) have similar trend. The change in behavior during the stimulation period in the Cre+ mice is caused by the activation of SUMVGLUT2+::POA neurons. The behavioral shift largely, but not completely, returns to baseline when the photostimulation stops. We have no reason to believe a VGLUT2-Cre+ mouse injected with control AAV to express eYFP would be different from WT littermate injected with AVV expressing ChR2eYFP in a Cre dependent manner.

Turning to concerns related to 8H, which shows data from fasted mice quantify time spent interacting with food pellet immediately after presentation of a chow pellet, we found no significant difference between the control and Cre+ mice. We unaware of any evidence indicating that the two groups should have a different baseline since the Cre insertion is not expected to alter gene expression and we are unaware of reports of a phenotype relating to feeding and the presence of the transgene in this mouse line. Even if there were a small baseline shift this would not explain the large abrupt shift induced by the photostimulation. As noted above, we saw shifts in behavior abruptly induced by the initiation of photostimulation when compared to baseline in multiple experiments. This shift would not be explained by a hypothetical difference in the baseline behaviors of litter mates.

(5) The statistics used throughout are inappropriate. The authors use serial Mann-Whitney U tests without a description of data distributions within and across groups. Further, they do not use any overall F tests even though most of the data are presented with more than two bars on the same graph. Stats should be employed according to how the data are presented together on a graph. For example, stats for pre-stim, stim, and post-stim behavior X between Cre+ and Cre- groups should employ something like a two-way repeated measures ANOVA, with post-hoc comparisons following up on those effects and interactions. There are many instances in which one group changes over time or there could be overall main effects of genotype. Not only is serially using Mann-Whitney tests within the same panel misleading and statistically inaccurate, but it cherry-picks the comparisons to be made to avoid more complex results. It is difficult to comprehend the effects of the manipulations presented without more careful consideration of the appropriate options for statistical analysis.

We thank the reviewer for pointing this out and suggesting alterative analyses, we agree with the assessment on this topic. Therefore, we have extensively revised the statical approach to our data using the suggested approach. Reviewer 1 also made a similar comment, and we would like to point to our reply to reviewer 1’s second point in regard to what we changed and added to the new statistical analyses. Further, we have added a full table detailing the statical values for each figure to the paper.

Conceptual:

(6) What does the signal look like at the terminals in the POA? Any suggestion from the data that the projection to the POA is important?

This is an interesting question that we will pursue in future investigations into the roles of the POA. We used the projection to the POA from SuM to identify a subpopulation in SuM and we were surprised to find the extensive arborization of these neurons to many areas associated with threat responses. We focused on the cell bodies as “hubs” with many “spokes”. Extensive studies are needed to understand the roles of individual projections and their targets. There is also the hypothetical technical challenge of manipulating one projection without activating retrograde propagation of action potentials to the soma. At the current time we have no specific insights into the roles of the isolated projection to POA. Interpretation of experiments activating only “spoke” of the hub would be challenging. Simple terminal stimulation experiments are challenged by the need to separate POA projections from activation of passing fibers targeting more anterior structures of the accumbens and septum.

(7) Is this distinguishing active coping behavior without a locomotor phenotype? For example, Fig. 5I and other figure panels show a distance effect of stimulation (but see issues raised about the genotype of comparison groups). In addition, locomotor behavior is not included for many behaviors, so it is hard to completely buy the interpretation presented.

We agree with the reviewer and thank them for highlighting this fundamental challenge in studies examining active coping behaviors in rodents, which requires movement. Additionally, actively responding to threatening stressors would include increased locomotor activity. Separation of movement alone from active coping can be challenging. Because of these concerns we undertook experiments using diverse behavioral paradigms to examine the elicited behaviors and the recruitment of SuMVGLUT2+::POA neurons to stressors. We conducted experiments to directly examine behaviors evoked by photoactivation of SuMVGLUT2+::POA. In these experiments we observed a diversity of behaviors including increased locomotion and jumping but also treading/digging (Figure 4). These are behaviors elicited in mice by threatening and noxious stimuli. An Increase of running or only jumping could signify a specific locomotor effect, but this is not what was observed. Based on these behaviors, we expected to find evidence of increase movement in open field (Figure 5G-I) and light dark choice (Figure 5J-L) assays. For many of the assays, reporting distance traveled is not practical. An important set of experiments that argues against a generic increase in locomotion is the operant behavior experiments, which require the animal to engage in a learned behavior while receiving photostimulation of SuMVGLUT2+::POA neurons (Figure 6). This is particularly true for testing using a progressive ratio when the time of ongoing photostimulation is longer, yet animals actively and selectively engage the active port (Figure 6G-H). Further, we saw a shift in behavioral strategy induce by photoactivation in forced swim test (Figure 7H). Thus, activation of SUMVGLUT2+::POA neurons elicited a range of behaviors that included swimming, jumping, treading, and learned response, not just increased movement. Together these data strongly argue that SuMVGLUT2+::POA neurons do not only promote increased locomotor behavior. We interpret these data together with the data from fiber photometry studies to show SuMVGLUT2+::POA neurons are recruited during acute stressors, contribute to aversive affective component of stress, and promote active behaviors without constraining the behavioral pattern.

Regarding genotype, we address this in comments above as well but believe that clarifying the use of litter mates, the extensive use of the VGLUT2-Cre line by multiple groups, and experimental design allowing for comparison to baseline, stimulation evoked, and post stimulation behaviors within and across genotypes mitigate possible concerns relating to the genotype.

(8) What is the role of GABA neurons in the SuM and how does this relate to their function and interaction with glutamate neurons? In Supp 8, GABA neuron activation also modulates locomotion and in Fig 7 there is an effect on immobility, so this seems pretty important for the overall interpretation and should probably be mentioned in the abstract.

Thank you for noting these interesting findings. We added text to highlight these findings to the abstract. Possible roles of GABAergic neurons in SuM extend beyond the scope of the current study particularly since SuM neurons have been shown to release both GABA and glutamate (Li Y, Bao H, Luo Y, et al. 2020, Root DH, Zhang S, Barker DJ et al. 2018). GABAergic neurons regulate dentate gyrus (Ajibola MI, Wu JW, Abdulmajeed WI, Lien CC 2021), REM sleep (Billwiller F, Renouard L, Clement O, Fort P, Luppi PH 2017), and novelty processing Chen S, He L, Huang AJY, Boehringer R et al. 2020). The population of exclusively GABAergic vs dual neurotransmitter neurons in SuM requires further dissection to be understood. How they may relate to SUMVGLUT2+::POA neurons require further investigation.

Questions about figure presentation:

(9) In Fig 3, why are heat maps shown as a single animal for the first couple and a group average for the others?

Thank you for highlighting this point for further clarification. We modified the labels in the figure to help make clear which figures are from one animal across multiple trials and those that are from multiple animals. In the ambush assay each animal one had one trial, to avoid habituation to the mock predator. Accordingly, we do not have multiple trials for each animal in this test. In contrast, the dunk assay (10 trial/animal) and the shock (5 trials/animal) had multiple trials for each animal. We present data from a representative animal when there are multiple trials per animal and the aggerate data.

Why is the temporal resolution for J and K different even though the time scale shown is the same?

Thank you for noticing this error carried forward from a prior draft of the figure so we could correct it. We replaced the image in 3J with a more correctly scaled heatmap.

What is the evidence that these signal changes are not due to movement per se?

Thank you for the question. There are two points of evidence. First, all the 465 nm excitation (Ca2+ dependent) data was collected in interleaved fashion with 415 nm (isosbestic) excitation data. The isosbestic signal is derived from GCaMP emission but is independent of Ca2+ binding (Martianova E, Aronson S, Proulx CD. 2019). This approach, time-division multiplexing, can correct calcium-dependent for changes in signal most often due to mechanical change. The second piece of evidence is experimental. Using multiple cohorts of mice, we examined if the change in Ca2+ signal was correlated with movement. We used the threshold of velocity of movement seen following the ambush. We found no correlation between high velocity movements and Ca2+ signal (Figure 3K) including cross correlational analysis (Supplemental figure 5). Based on these points together we conclude the change in the Ca2+ signal in SUMVGLUT2+::POA neurons is not due to movement induced mechanical changes and we find no correlation to movement unless a stressor is present, i.e. mock predator ambush or forced swim. Further, the stressors evoke very different locomotor responses fleeing, jumping, or swimming.

(10) In Fig 4, the authors carefully code various behaviors in mice. While they pick a few and show them as bars, they do not show the distribution of behaviors in Cre- vs Cre+ mice before manipulation (to show they have similar behaviors) or how these behaviors shift categories in each group with stimulation. Which behaviors in each group are shifting to others across the stim and post-stim periods compared to pre-stim?

This is an important point. We selected behaviors to highlight in Figure4 C-E because these behaviors are exhibited in response to stress (De Boer & Koolhaas, 2003; van Erp et al., 1994). For the highlighted behaviors, jumping, treading/digging, grooming, we show baseline (pre photostimulation), stimulation, and post stimulation for Cre+ and Cre- mice with the values for each animal plotted. We show all nine behaviors as a heat map in Figure 4B. The panels show changes that may occur as a function of time and show changes induced by photostimulation.

The heatmaps demonstrate that photostimulation of SUMVGLUT2+::POA neurons causes a suppression of walking, grooming, and immobile behaviors with an increase in jumping, digging/treading, and rapid locomotion. After stimulation stops, there is an increase in grooming and time immobile. The control mice show a range of behaviors with no shifts noted with the onset or termination of photostimulation.

Of note, issues of statistics, genotype, and SABV are important here. For example, the hint that treading/digging may have a slightly different pre-stim basal expression, it seems important to first evaluate strain and sex differences before interpreting these data.

We examined the effects of sex as a biological variable in the experiments reported in the manuscript and found no differences among males and females in any of the experiments where we had enough animals in each sex (minimum of 5 mice) for meaningful comparisons. We did this by comparing means and SEM of males and females within each group (e.g. Cre+ males vs Cre+ female, Cre- males vs Cre- females) and then conducted a t-test to see if there was a difference. For figures that show time as a variable (e.g Figure 6C-E), we compared males and females with time x sex as main factors and compared them (including multiple comparisons if needed). We found no significant main effects or interactions between males and females. Because of this, and to maximize statistical power, we decided to move forward to keep males and females together in all the analyses presented in the manuscript. It is worth noting also that the core of the experimental design employed is a change in behavior caused by photostimulation. The mice are also the same strain with only difference being the modification to add an IRES and sequence for Cre behind the coding sequence of the Slc17A6 (VGLUT2) gene.

(11) Why do the authors use 10 Hz stimulation primarily? is this a physiologically relevant stim frequency? They show that they get effects with 1 Hz, which can be quite different in terms of plasticity compared to 10 Hz.

Thank you for the raising this important question. Because tests like open field and forced swim are subject to habituation and cannot be run multiple times per animal a test frequency was needed to use across multiple experiments for consistency. The frequency of 10Hz was selected because it falls within the rate of reported firing rates for SuM neurons (Farrel et al., 2021; Pedersen et al., 2017) and based on the robust but sub maximal effects seen in the real-time place preference assays. Identification of the native firing rates during stress response would be ideal but gathering this data for the identified population remains a dauting task.

(12) In Fig 5A-F, it is unclear whether locomotion differences are playing a role. Entrances (which are low for both groups) are shown but distance traveled or velocity are not.

In B, there is no color in the lower left panel. where are these mice spending their time? How is the entirety of the upper left panel brighter than the lower left? If the heat map is based on time distribution during the session, there should be more color in between blue and red in the lower left when you start to lose the red hot spots in the upper left, for example. That is, the mice have to be somewhere in apparatus. If the heat map is based on distance, it would seem the Cre- mice move less during the stim.

We appreciate the opportunity to address this question, and the attention to detail the reviewer applied to our paper. In the real time place preference test (RTPP) stimulation would only be provided while the animal was on the stimulation side. Mice quickly leave the stimulation side of the arena, as seen in the supplemental video, particularly at the higher frequencies. Thus, the time stimulation is applied is quite low. The mice often retreat to a corner from entering the stimulation side during trials using higher frequency stimulation. Changing locomotor activity along could drive changes in the number entrances but we did not find this. In regard to the heat map, the color scale is dynamically set for each of the paired examples that are pulled from a single trial. To maximize the visibility between the paired examples the color scale does not transfer between the trials. As a result, in the example for 10 Hz the mouse spent a larger amount of time in the in the area corresponding to the lower right corner of the image and the maximum value of the color scale is assigned to that region. As seen in the supplemental video, mice often retreated to the corner of the non-stimulation side after entering the stimulation side. The control animal did not spend a concentrated amount of time in any one region, thus there is a lack of warmer colors. In contrast the baseline condition both Cre+ and Cre- mice spent time in areas disturbed on both sides of arena, as expected. As a result, the maximum value in the heat map is lower and more area are coded in warmer colors allowing for easier visual comparison between the pair. Using the scale for the 10 Hz pair across all leads to mostly dark images. We considered ways to optimized visualization across and within pairs and focused on the within pair comparison for visualization.

(13) By starting with 1 hz, are the experimenters inducing LTD in the circuit? what would happen if you stop stimming after the first epoch? Would the behavioral effect continue? What does the heat map for the 1 hz stim look like?

Relatedly, it is a lot of consistent stimulation over time and you likely would get glutamate depletion without a break in the stim for that long.

Thank you for the opportunity to add clarity around this point regarding the trials in RTPP testing. Importantly, the trials were not carried out in order of increasing frequency of stimulation, as plotted. Rather, the order of trials was, to the extent possible with the number of mice, counterbalanced across the five conditions. Thus, possible contribution of effects of one trial on the next were minimized by altering the order of the trials.

We have added a heat map for the 1 Hz condition to figure 5B.

For experiments on RTPP the average stimulation time at 10Hz was less than 10 seconds per event. As a result, the data are unlikely to be affected by possible depletion of synaptic glutamate. For experiments using sustained stimulation (open field or light dark choice assays) we have no clear data to address if this might be a factor where 10Hz stimulation was applied for the entire trial.

(14) In Fig 6, the authors show that the Cre- mice just don't do the task, so it is unclear what the utility of the rest of the figure is (such as the PR part). Relatedly, the pause is dependent on the activation, so isn't C just the same as D? In G and H, why ids a subset of Cre+ mice shown?

Why not all mice, including Cre- mice?

Thank you for the opportunity to improve the clarity of this section. A central aspect of the experiments in Figure 6 is the aversiveness of SUMVGLUT2+::POA neuron photostimulation, as shown in Figure 5B-F. The aversion to photostimulation drives task performance in the negative reinforcer paradigm. The mice perform a task (active port activation) to terminate the negative reinforcer (photostimulation of SuMVGLUT2+::POA neurons). Accordingly, control mice are not expected to perform the task because SuMVGLUT2+::POA neurons are not activated and, thus the mice are not motivated to perform the task.

A central point we aim to covey in this figure is that while SuMVGLUT2+::POA neurons are being stimulated, mice perform the operant task. They selectively activated the active port (Supplemental Figure 7). As expected, control mice activate the active port at a low level in the process of exploring the arena. This diminishes on subsequent trials as mice habituate to the arena (Figure 6D). The data in Figures 6 C and D are related but can be divergent. Each pause in stimulation requires a port activation of a FR1 test but the number of port activations can exceed the pauses, which are 10 seconds long, if the animal continues to activate the port. Comparing data in Figures 6 C and D revels that mice generally activated the port two to three times for each pause earned with a trend towards greater efficiency on day 4 with more rewards and fewer activations.

The purpose of the progressive ratio test is to examine if photostimulation of SuMVGLUT2+::POA continues to drive behavior as the effort required to terminate the negative stimuli increases. As seen in Figures 6 G and H, the stimulation of SuMVGLUT2+::POA neurons remains highly motivating. In the 20-minute trial we did not find a break point even as the number of port activations required to pause the stimulation exceed 50. We do not show the Cre- mice is Figure 6G and H because they did not perform the task, as seen in Figure 6F. For technical reasons in early trials, we have fully timely time stamped data for rewards and port activations from a subset of the Cre+ mice. Of note, this contains both the highest and lowest performing mice from the entire data set.

Taken together, we interpret the results of the operant behavioral testing as demonstrating that SuMVGLUT2+::POA neuron activation is aversive, can drive performance of an operant tasks (as opposed to fixed escape behaviors), and is highly motivating.

(15) In Fig 7, what does the GCaMP signal look like if aligned to the onset of immobility? It looks like since the hindpaw swimming is short and seems to precede immobility, and the increase in the signal is ramping up at the onset of hindpaw swimming, it may be that the calcium signal is aligned with the onset of immobility.

What does it look like for swimming onset?

In I, what is the temporal resolution for the decrease in immobility? Does it start prior to the termination of the stim, or does it require some elapsed time after the termination, etc?

Thank for the opportunity to addresses these points and improve that clarity of our interpretation of the data. Regarding aligning the Ca2+ signal from fiber photometry recordings to swimming onset and offset, it is important to note that the swimming bouts are not the same length. As a result, in the time prior to alignment to offset of behaviors animals will have been swimming for different lengths of time. In Figure 7 C, we use the behavioral heat map to convey the behavioral average. Below we show the Ca2+ dependent signal aligned at the offset of hindpaw swim for an individual mouse (A) and for the total cohort (B). This alignment shows that the Ca2+ dependent signal declines corresponding to the termination of hindpaw swimming. Because these bouts last less than the total the widow shown, the data is largely included in Figure 7 C and D, which is aligned to onset. Due to the nuance of the difference is the alignment and the partial redundancy, we elected to include the requested alignment to swimming offset in the reply rather in primary figure.

Author response image 1.

Turning to the question regarding swimming onset, the animals started swimming immediately when placed in the water and maintained swimming and climbing behaviors until shifting behaviors as illustrated in Figure 7A and B. During this time the Ca2+-dependent signal was elevated but there is only one trial per animal. This question can perhaps be better addressed in the dunk assay presented in Figure 3C, F and G and Supplemental Figure 4 H and I. Here swimming started with each dunk and the Ca2+ signal increased.

Regarding the question for about figure 7I. We scored for entire periods (2 mins) in aggerate. We noted in videos of the behavior test that there was an abrupt decrease in immobility tightly corresponding to the end of stimulation. In a few animals this shift occurred approximately 15-20s before the end of stimulation. This may relate to the depletion of neurotransmitter as suggested by the reviewer.

Reviewer 3

Major points

(1) Results in Figure 1 suggested that SuM-Vglu2::POA projected not only POA but also to the diverse brain regions. We can think of two models which account for this. One is that homogeneous populations of neurons in SuM-Vglu2::POA have collaterals and innervated all the efferent targets shown in Figure 1. Another is to think of distinct subpopulations of neurons projecting subsets of efferent targets shown in Figure 1 as well as POA. It is suggested to address this by combining approaches taken in experiments for Figure 1 and Supplemental Figure 2.

Thank you for raising this interesting point. We have attempted combining retroAAV injections into multiple areas that receive projections from SUMVGLUT2+::POA neurons. However, we have found the results unsatisfactory for separating the two models proposed. Using eYFP and tdTomato expressing we saw some overlapping expressing in SuM. We are not able to conclude if this indicates separate populations or partial labeling of a homogenous populations. A third option seems possible as well. There could be a mix of neurons projecting to different combinations of downstream targets. This seems particularly difficult to address using fluorophores. We are preparing to apply additional methodologies to this question, but it extends beyond the scope of this manuscript.

(2) Since the authors drew a hypothetical model in which the diverse brain regions mediate the effect of SuM-Vglu2::POA activation in behavioral alterations at least in part, examination of the concurrent activation of those brain regions upon photoactivation of SuM-Vglu2::POA. This must help the readers to understand which neural circuits act upon the induction of active coping behavior under stress.

Thank you for raising this important point. We agree that activating glutamatergic neurons should lead to activation of post synaptic neurons in the target regions. Delineating this in vivo is less straight forward. Doing so requires much greater knowledge of post synaptic partners of SUMVGLUT2+::POA neurons. There are a number of issues that would need to be accounted for. Undertaking two color photo stimulation plus fiber photometry is possible but not a technical triviality. Further, it is possible that we would measure Ca2+ signals in neurons that have no relevant input or that local circuits in a region may shape the signal. We would also lack temporal resolution to identify mono-postsynaptic vs polysynaptic connections. Thus, we would struggle to know if the change in signal was due to the excitatory input from SuM or from a second region. At present, we remain unclear on how to pursue this question experimentally in a manner that is likely to generate clearly interpretable results.

(3) In Figure 4, "active coping behaviors" must be called "behaviors relevant to the active behaviors" or "active coping-like behaviors", since those behaviors were in the absence of stressors to cope with.

Thank you for the suggestion on how to clarify our terminology. We have adopted the active coping-like term.

(4) For the Dunk test, it is suggested to describe the results and methods more in detail, since the readers would be new to it. In particular, the mice could change their behavior between dunks under this test, although they still showed immobility across trials as in Supplemental Figure 4I. Since neural activity during the test was summarized across trials as in Figure 3, it is critical to examine whether the behavior changes according to time.

Thank you for identifying this opportunity to improve our manuscript. We have expanded and added a detailed description of the dunk test in the methods section.

As for Supplemental Figure 4I, we apologize for the confusion because the purpose of this figure is to show that mice remained mobile for the entire 30-second dunk trial. This did not appreciably change over the 10 trials. We have revised this figure to plot both immobile and mobile time to achieve greater clarity on this point.

Minor points

Typos

In Figure 1, please add a serotype of AAVs to make it compatible with other figures and their legends.

In the main text and Figure 2K, the authors used MHb/LHb and mHb/lHb in a mixed fashion. Please make them unified.

In the figure legend of Figure 6, change "SuMVGLUT2+::POA neurons drive" to "SuMVGLUT2+::POA neurons " in the title.

In line 86, please change "Retro-AAV2-Nuc-flox(mCherry)-eGFP" to "AAV5-Nuc-flox(mCherry)eGFP".

In line 80, please change "Positive controls" to "As positive controls, ".

Thank you for taking the time and making the effort to identify and call these out. We have corrected them.

Author Response

The following is the authors’ response to the previous reviews

The revised manuscript is much improved - many unclear points are now better explained. However, in our opinion, some issues could still be significantly improved.

1. Statistics: none of us are experts in statistics but several things remain questionable in our opinion and if it were our study, we would consult with an expert:

a) while we understand the authors note about N-chasing and p-hacking, we wonder how the number of N's was premeditated before obtaining the results. Why in 4M an N of 3 is sufficient while in 3E the N is >20 (and not mentioned). At the very least, we think it would be wise to be cautious when stating something as not-significant when it is clear (as in 4M) that the likelihood of it actually being statistically significant is quite large.

b) In most analyses, the data is not only normalized by actin or some other measure but also to the first (i.e left side on the graph) condition, resulting in identical data points that equal '1' (in Figure 4 alone - C; I; K; M; and O) - while this might be scientifically sound, it should be mentioned (the specific normalization) and also note that this technique shadows any real variance that exists in the original data in this condition. consider exploring techniques to overcome this issue.

c) In 3C, - if we understand the experiment, you want to convince us that the DIFFERENCE between eB2-FC compared to FC is larger in the control compared to the experiment. We are not absolutely sure that the statistical tools employed here are sufficient - which is why we would consult an expert.

A) We are aware that many studies do not consistently quantify such experiments. For example, there are essentially no published examples of the signalling timelines of EphB2 receptors as in Fig. 5. By striving to quantifying such biochemical effects, an unquantified experiment stands out, and so perhaps we were too strict by trying to quantify as many experiments as possible, resulting in low n’s for some of them. We acknowledge that additional experiments on EPHB1 protein stability may reach significance. We have adjusted our text on line 332-335 to point to this interesting trend, and slightly changed the conclusion to this section. Similarly, we commented on similar trends when describing Figs. 1E and 4G on lines 901 and 952.

B) For the Western blot band intensity normalisation, we believe that our method is scientifically sound. Normally, when the replicate samples are loaded on one gel and blotted on the same membrane, the experimenter only needs to normalise the target band intensity to its cognate loading control band intensity for quantitation. However, we usually have a large number of samples from multiple experiments, carried out on different dates. For example, in Fig. 4B,C there are 7 biological replicates collected from 7 experiments and in Fig. 4D there are 10 protein samples. It is not possible for us to run all samples on the same gel. In addition, due to the combined effects of variance in transfer efficiency, the potency of antibodies, detection efficiency and the developing time for each blot, it is practically impossible to generate similar band intensity for each batch. Thus, we use normalisation of test bands to the loading control for individual experiments, and this analysis method is widely accepted by reputable journals with a focus on biochemical experiments (for example: PMID 37695914: Fig. 3 A,B,C; PMID 36282215: Fig. 3 B,C,D,E; PMID 33843588: Fig. 3 C,D,E,F,G,H). Since the value of the first sample on the plot is 1, which is a hypothetical value and does not meet the parametric test requirement, we performed one-sample t-test for statistics when other samples are compared with the first sample (PMID 35243233 Fig. 6 A,B,C,D; https://www.graphpad.com/quickcalcs/oneSampleT1/, “A one sample t-test compares the mean with a hypothetical value. In most cases, the hypothetical value comes from theory. For example, if you express your data as 'percent of control', you can test whether the average differs significantly from 100.”). Thus, we believe that our normalisation and statistical methods are both correct with a large number of precedents.

C) This comment refers to the cell collapse experiment shown in Fig. 3C for which the data are plotted in Fig. 3D. We stand by the statistical method used. There are two groups of cells (CTRLCRISPR and MYCBP2 CRISPR) and two treatments for each cell group (Fc control and eB2), thus we should use two-way ANOVA. Since we compared the cell retraction effects of Fc and eB2 on the two groups of cells, Sidak post hoc comparison is the right method to avoid errors introduced by multiple comparisons. Here is an example of an eLife article that used the same statistical method for similar comparisons: PMID 37830910, Fig. 1 H,I. To make the comparison easier, we grouped the experiments by cell type (CTRLCRISPR and MYCBP2 CRISPR) as opposed to by treatment. Below, the old version is on the right, and the new version is on the left. The conclusion is that eB2 induces less cell collapse in cells depleted of MYCBP2, when compared to the control cells. However, eB2 is still able to collapse cells lacking MYCBP2.

Author response image 1.

Revisiting these data, we noticed an error introduced when CC compiled the data used to generate Fig. 3D. The data were acquired from nine biological replicates per condition. CC used a mix of two methods for cell collapse rate calculation: the first method involved the sum of collapsed cells and all cells from multiple regions of one coverslip (biological replicate). The second method involved computing a collapse rate in each region which then was used to calculate the average collapse rate for the entire coverslip (technical replicate). Given the small cell numbers due to sparse culture conditions, we believe that the first method is a more conservative approach. We hence re-plotted all replicate data using the first method. This resulted in slightly different % collapse and p values. These were changed accordingly in the text and plot and do not affect the conclusion of this experiment.

2) thanks for the clarification that the interaction between the extracellular domain of EPHB2 and MYCBP2 might not occur directly - however, unless we missed this it was not clearly stated in the text. It is an important point and also a cool direction for the future - to find the elusive co-receptor that actually helps EPHB2 and MYCBP2 form a complex.

We now also refer to this in the results section on line 215.

“Since EPHB2 is a transmembrane protein and MYCBP2 is localised in the cytosol, these experiments suggest that the interaction between the extracellular domain of EPHB2 and MYCBP2 might be indirect and mediated by other unknown transmembrane proteins.”

3) The Hela CRISPR cell line is better explained in the response letter but still not sufficiently explained in the text for a non-expert reader. If the authors want any reader to comprehend this, we would strongly recommend adding a scheme.

We now include a schematic outlining the CRISPR cell generation as Fig. 3A and its description on line 926.

Author response image 2.

4) To clarify some of our previous (and persisting) concerns about Figure 3D/E - it is true that a reduction in 25% of cell size is dramatic. But (if we understand correctly) your claim is that a reduction in 22% (this is a guess, as the actual numbers are not supplies) is significantly less than 25%. Even if it is, statistically speaking, significant, what is the physiological relevance of this very slight effect? In this experiment, the N was quite large, and we wonder if the images in D are representative - it would be nice to label the data points in E to highlight which images you used.

We now mention the average cell area contraction measurements in the legend to Fig. 3F on line 935. We also tracked down the individual cells shown in Fig. 3E and they are now labelled as data points in blue in Fig. 3F. HeLa cell collapse is a simplified model of EPHB2 function and we do not know whether the difference between the behaviour of CTRLCRISPR and MYCBP2 CRISPR cells is physiologically significant and thus we prefer not to speculate on this.

5) Figure 3F and other stripe assays - In the end, it is your choice how to quantify. We believe that quantifying area of overlap is a more informative and objective measurement that might actually benefit your analyses. That said, if you do keep the quantification as it is now, you have to define the threshold of what you mean by "cell/s (or an axon in 7A, where it is even more complicated as are you eluding to primary, secondary, or even smaller branches) are RESIDING within the stripe". Is 1% overlap sufficient or do you need 10 or 50% overlap?

We now added this statement to the methods on line 745: “A cell was considered to be on an ephrin-B2 stripe when more than 50% of its nucleus was located on that stripe”. For chick explant stripe assay, when measuring the length of an axon on a stripe, we only measured the main axons originated from the explants.

For explant/stripe experiments in Fig. 7 AB, we now use the term “GFP-expressing neurite” rather than “branch”. This was already present in the results of the previous version, but the methods and legend needed to be brought up to date (lines 786 and 1008. We think that “branch” was a confusing term that was supposed to mean the same thing as “neurite” but came across as some indication of branching. We do not know whether the GFP+ neurites were primary or secondary extensions of explants, or in fact, whether some of them contained more than one axon. We also adjusted the method to reflect the fact that some stripes were used in conjunction with a single explant and added a reference to a previous study extensively using this method (Poliak et al., 2015) on line 778.

6) We still don't get the link to the lysosomal degradation. Your data suggests that in your cells EPHB2 is primarily degraded by the lysosomal pathway and not proteasome. Any statement about MYCBP2 is not strongly supported by the data, in our opinion - Unless you develop some statistical measurement that shows that the effect of BafA1 is statistically different in MYCBP2 cells than in control cells. Currently, this is not the case and the link is therefore not warranted in our opinion.

We generated a new version of Fig. 4K with average increase in EPHB2 levels in the presence of BafA1 and CoQ, compared to DMSO treated controls (see below). BafA1 and CoQ restored EPHB2 protein levels by 19% and 14% respectively in CtrlCRISPR cells, while the inhibitors restored EPHB2 protein levels by 40% and 35% respectively in MYCBP2 CRISPR cells.

Author response image 3.

For each of the 4 replicates, the increase in EPHB2 levels by BafA1 compared to DMSO is as follows:

Author response table 1.

These values are not significantly different between CtrlCRISPR cells versus MYCBP2 CRISPR cells (p= 0.08, student’s t test). Similarly for the CoQ experiment. We now temper our conclusion for this experiment: Although the difference in percentage increase between CTRLCRISPR cells and MYCBP2CRISPR cells is not significant, this trend raises the possibility that the loss of MYCBP2 promotes EPHB2 receptor degradation through the lysosomal pathway (line 319). We also adjusted the section title (line 306).

7) While the C. elegans part is now MUCH better explained - we are not sure we understand the additional insight. The fact that vab-1 and glo4 double mutants are additive as are vab1 and fsn1, suggest they act in parallel (if the mutants are NULL, and not if they are hypomorphs, if one wants to be accurate) - how this relates to your story is unclear. The vab1/rpm1 double mutant is still uninformative and incomplete. rpm1 phenotype is so severe that nothing would make it more severe. We read the Jin paper that the authors directed to - nothing makes the rpm1 phenotype more severe. Yes, some DOWNSTREAM elements make the rpm1 phenotype LESS severe - this is not something you were testing, to the best of our knowledge. Rather, you wanted to see if rpm1 mutant resulted in stabilization of vab1 and thus suppression of vab1 phenotype - we are just not sure the system is amenable to test (actually reject) your hypothesis that Vab1 is degraded by rpm1. Also, assuming we are talking about NULLs, the fact that the rpm1 phenotype is WAY stronger than the vab1 mutant, suggests that rpm1 functions via multiple routes, adding even more complexity to the system. Given these results, despite the much improved clarity, we are still not sure that the worm data adds new insight, rather than potentially confusing the reader.

We realise that the genetic interactions between vab-1 and the RPM-1/MYCBP2 signalling network are complicated. However, we insist on keeping the data for the sake of its availability for future studies and completeness. We also think it is important for readers and the community to see these data, even if the authors and reviewers are not entirely in agreement about the importance/interpretation of experimental outcomes. It is our hope that the community will examine the results and draw their own conclusions.

A few points of clarification:

The C. elegans experiments were designed to test genetically if the vertebrate interactions between EPHB2 and MYCBP2 and its signalling network are conserved. We studied two kinds of interactions: (1) between vab-1 and RPM-1/MYCBP2 downstream proteins (GLO-4 and FSN-1) and (2) between vab-1 and rpm-1. For these studies, we used null alleles for vab-1, glo-4 and fsn-1 which is now noted on lines 440, 453, 475 and 859. Our findings are consistent with the VAB-1 Ephrin receptor functioning in parallel to known RPM-1 binding proteins. This is further supported by new data: vab-1; fsn-1 double mutants showed enhanced incidence of axon overextension defects using a second transgenic background, zdIs5 (Pmec-4::GFP), to visualize axon termination (Fig. 8F).

This second transgenic background also allowed us to generate new data to address your concerns about phenotypic saturation in rpm-1 mutants. To do this, we used the zdIs5 (Pmec4::GFP) genetic background, in which axon termination defects are not saturated in rpm-1 mutants (Fig. 8F) because they can be enhanced by other mutants such as cdc-42 and unc-33 (Fig. 7C, D, in Borgen et al. Development 144, 4658–4672 (2017), PMID 29084805). In this new background, we found that vab-1 loss of function fails to enhance the incidence of severe “hook” defects in rpm-1 mutants which is an indication that the two genes function in the same pathway. Importantly, prior studies in this background, also showed that mutants in the RPM-1 signalling network (e.g. fsn-1, glo-4 and ppm-2) do not enhance the incidence of severe “hook” defects as double mutants with rpm-1 compared to rpm-1 single mutants (Fig. 7B, ibid.).

To reflect these ideas more clearly, we revised the Results section pertaining to C. elegans genetics (starting on line 418) and tempered our discussion (lines 517). Basically, this section now says that we studied genetic interactions between vab-1 and the RPM-1/MYCBP2 signalling network. From these experiments we conclude that: (1) The enhancement of overextension defects in vab-1; glo-4 and vab-1; fsn-1 double mutants compared to single mutants indicates that VAB-1/EPHR functions in parallel to known RPM-1 binding proteins to facilitate axon termination, and (2) Since the vab-1; rpm-1 double mutants do not display an increased frequency or severity of overextension defects compared to rpm-1 single mutants, VAB-1 /EPHR functions in the same genetic pathway as RPM-1/MYCBP2.

The new genetic data included in this version were generated by Karla J. Opperman who is now included as a co-author.

Further corrections:

Author response image 4.

Because of the errors associated with quantifications in Fig. 3D (see above), we reviewed other quantification methodologies and noticed another discrepancy that required a correction. In the hippocampal neuron growth cone collapse assay shown in the previous version of Fig. 7 D (left), the growth cones were classified into three groups: 1, fully collapsed; 2, hard to tell, but not fully collapsed; 3, fan-shape cones. Two different quantifications were performed as follows: (1), number of fully collapsed cones divided by the numbers of all growth cones; (2), number of fully collapsed cones divided by [number of fully collapsed cones + fan-shape cones]. CC erroneously used the second method to generate Fig. 7D.

We think that the first method is more appropriate. Furthermore, since n=5 for the Fc and eB1-Fc conditions, but n=3 for the eB2-Fc condition, we decided to omit it. The final plot for figure 7D is the following:

Author response image 5.

Our conclusion still stands that exogenous FBD1 WT overexpression impaired the growth cone collapse mediated by EphB.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

Summary:

Liver cancer shows a high incidence in males than females with incompletely understood causes. This study utilized a mouse model that lacks the bile acid feedback mechanisms (FXR/SHP DKO mice) to study how dysregulation of bile acid homeostasis and a high circulating bile acid may underlie the gender-dependent prevalence and prognosis of HCC. By transcriptomics analysis comparing male and female mice, unique sets of gene signatures were identified and correlated with HCC outcomes in human patients. The study showed that ovariectomy procedure increased HCC incidence in female FXR/SHP DKO mice that were otherwise resistant to agedependent HCC development, and that removing bile acids by blocking intestine bile acid absorption reduced HCC progression in FXR/SHP DKO mice. Based on these findings, the authors suggest that gender-dependent bile acid metabolism may play a role in the male-dominant HCC incidence, and that reducing bile acid level and signaling may be beneficial in HCC treatment. 

strengths:

(1) Chronic liver diseases often proceed the development of liver and bile duct cancer. Advanced chronic liver diseases are often associated with dysregulation of bile acid homeostasis and cholestasis. This study takes advantage of a unique FXR/SHP DKO model that develop high organ bile acid exposure and spontaneous age-dependent HCC development in males but not females to identify unique HCC-associated gene signatures. The study showed that the unique gene signature in female DKO mice that had lower HCC incidence also correlated with lower grade HCC and better survival in human HCC patients. 2. The study also suggests that differentially regulated bile acid signaling or gender-dependent response to altered bile acids may contribute to gender-dependent susceptibility to HCC development and/or progression. 3. The sex-dependent differences in bile acidmediated pathology clearly exist but are still not fully understood at the mechanistic level. Female mice have been shown to be more sensitive to bile acid toxicity in a few cholestasis models, while this study showed a male dominance of bile acid promotion of HCC. This study used ovariectomy to demonstrate that female hormones are possible underlying factors. Future studies are needed to understand the interaction of sex hormones, bile acids, and chronic liver diseases and cancer. 

We thank Reviewer 1 for their positive and thorough assessment of our manuscript

Weaknesses:

(1) HCC shows heterogeneity, and it is unclear what tissues (tumor or normal) were used from the DKO mice and human HCC gene expression dataset to obtain the gene signature, and how the authors reconcile these gene signatures with HCC prognosis.

Mice studies: Aged DKO mice develop aggressive tumors (major and minor nodules, See Figure 1), and the entire liver is burdened with multiple tumor nodules. It is technically challenging to demarcate the tumor boundaries as most of the surrounding tissues do not display normal tissue architecture. Therefore, livers from age- and sexmatched wild-type C57/BL6 mice were used as control tissue. All the mice were inbred in our facility. Spatial transcriptomics and longitudinal studies are ongoing to collect tumors at earlier time points wherein we can differentiate tumor and non-tumor tissue. 

Human Studies: We mined five separate clinical data sets. The human HCC gene expression comprised of samples from the (i) National Cancer Institute (NCI) cohort (GEO accession numbers, GSE1898 and GSE4024) and (ii) Korea, (iii) Samsung, (iv) Modena, and (v) Fudan cohorts as previously described (GEO accession numbers, GSE14520, GSE16757, GSE43619, GSE36376, and GSE54236). We have added a new supplemental table 4, giving details of these datasets. Depending on the cohort, they are primarily HCC samples- surgical resections of HCC, control samples, with some tumors and paired non-tumor tissues.

(2) The authors identified a unique set of gene expression signatures that are linked to HCC patient outcomes, but analysis of these gene sets to understand the causes of cancer promotion is still lacking. The studies of urea cycle metabolism and estrogen signaling were preliminary and inconclusive. These mechanistic aspects may be followed up in revision or future studies.

We agree. Experiments to elicit HCC causality and promotion are complex, given the heterogeneous nature of liver cancer. Moreover, the length of time (12 months) needed to spontaneously develop cancer in this DKO mouse model makes it challenging. As mentioned by the reviewer, mechanistic studies are ongoing, and longitudinal time course experiments are actively being pursued to delineate causality. Having said that, we mined the TCGA LIHC (The Cancer Genome Atlas Liver Hepatocellular Carcinoma) database to examine the expression of the individual urea cycle genes and found them suppressed in liver tumorigenesis (new Supplementary Figure 4). We also evaluated if estrogen receptor  (Er) targets altered in DKO females (DKO_Estrogen) correlate with overall survival in HCC (new Supplementary Figure 6). We note that Er expression per se is reduced in males and females upon liver tumorigenesis. Also, DKO_Estrogen signature positively corroborated with better overall survival (new Supplementary Figure 6). These findings further bolster the relevance of urea cycle metabolism and estrogen signaling during HCC. 

(3) While high levels of bile acids are convincingly shown to promote HCC progression, their role in HCC initiation is not established. The DKO model may be limited to conditions of extremely high levels of organ bile acid exposure. The DKO mice do not model the human population of HCC patients with various etiology and shared liver pathology (i.e. cirrhosis). Therefore, high circulating bile acids may not fully explain the male prevalence of HCC incidence.

We agree with this comment that our studies do not show bile acids can initiate HCC and may act as one of the many factors that contribute to the high male prevalence of HCC. This is exactly the reason why throughout the manuscript we do not write about HCC initiation. To clarify further, in the revised discussion of the manuscript, we have added a sentence to highlight this aspect, “while this study demonstrates bile acids promote HCC progression it does not investigate or provide evidence if excess bile acids are sufficient for HCC initiation.”

(4) The authors showed lower circulating bile acids and increased fecal bile acid excretion in female mice and hypothesized that this may be a mechanism underlying the lower bile acid exposure that contributed to lower HCC incidence in female DKO mice. Additional analysis of organ bile acids within the enterohepatic circulation may be performed because a more accurate interpretation of the circulating bile acids and fecal bile acids can be made in reference to organ bile acids and total bile acid pool changes in these mice.

As shown in this manuscript- we provide BA compositional analyses from the liver, serum, urine, and feces (Figures 5 and 6, new Supplementary Figure 8, Supplementary Tables 4 and 5). Unfortunately, we did not collect the intestinal tissue or gallbladders for BA analysis in this study. Separate cohorts of mice are being aged for future BA analyses from different organs within the enterohepatic loop. We thank you for this suggestion. Nevertheless, we have previously measured and reported BA values to be elevated in the intestines and the gall bladder of young DKO mice (PMC3007143).

Reviewer #2 (Public review):

Weaknesses:

(1) The translational value to human HCC is not so strong yet. Authors show that there is a correlation between the female-selective gene signature and low-grade tumors and better survival in HCC patients overall. However, these data do not show whether this signature is more highly correlated with female tumor burden and survival. In other words, whether the mechanisms of female protection may be similar between humans and mice. In that respect, it would also be good to elaborate on whether women have higher fecal BA excretion and lower serum BA concentration.

The reviewer poses an interesting question to test if the DKO female-specific signatures are altered differently in male vs. female HCC samples. As we found the urea cycle and estrogen signaling to be protective and enriched in our mouse model, we tested their expression pattern using the TCGA-LIHC RNA-seq data. We found urea cycle genes and Er transcripts broadly reduced in tumor samples irrespective of the sex (new Supplementary Figure 4 and Supplementary Figure 6), indicating that these pathways are compromised upon tumorigenesis even in the female livers. 

While prior studies have shown (i) a smaller BA pool w synthesis in men than women (PMID: 22003820), we did not find a study that systematically investigated BA excretion between the sexes in HCC context. The reviewer is spot on in suggesting BA analysis from HCC and unaffected human fecal samples from both sexes. Designing and performing such studies in the future will provide concrete proof of whether BA excretion protects female livers from developing liver cancer. We thank you for these suggestions.

(2) The authors should perform a thorough spelling and grammar check.

We apologize for the typos, which have been fixed, and as suggested by the reviewer, we have performed a grammar check.

(3) There are quite some errors and inaccuracies in the result section, figures, and legends. The authors should correct this.

We apologize for the inadvertent errors in the manuscript, and we have clarified these inaccuracies in the revised version. Thank you.

Reviewer#1 (Recommendations for the authors).

(1) Figures 1A-F, This statement of altered liver steatosis needs to be further supported by measurement of liver triglycerides. Lower magnification images of Sirius red stain should be shown for better evaluation of liver fibrosis.

Unfortunately, we did not measure liver triglycerides and sirius red stained samples have faded, and lower magnification is unavailable at this juncture. We have modified our results accordingly.  

We did not take the gross picture of WT female and DKO female livers in the same frame as shown below. Since the manuscript is focused on male and female differences in liver cancer incidence, we provided DKO male and female liver images as Figure 1D in the paper.

Author response image 1.

Gross liver images of a year-old WT and DKO mice which show prominent hepatocarcinogenesis in DKO male mice

(2) Can the authors clarify if the gene transcriptomics was performed with normal or tumor tissues of DKO mice?

Gene transcriptomics were performed with the tumor tissue of DKO mice. We have previously published data from younger non tumor bearing DKO male mice (PMCID: PMC3007143). 

(3) Supplementary Figure 3C. Could the authors confirm if this is F vs M or just DKO female since it does not seem to match the result description in the main text? It is better practice to indicate the sub-panels of the Supplementary Figures in the main text while describing the results.

As the reviewer correctly points out Supplementary Figure 3C is DKO F vs M signature not DKO_female signature and this has been clarified in the text. We have also included DKO_F data now to reduce the confusion.

(4) Figure 3. Legend, the data presented are not well explained in the Legend, especially the labeling and what is being presented and compared.

As suggested by the reviewer, we have modified the legend accordingly.

(5) Supplementary Table 4 does not contain total serum bile acid as described in the main text.

We agree with the reviewer. We provided primary and secondary BA concentrations, Supplementary Table 4 (currently Supplementary Table 5 in the revised version): Rows 20 and 21. but not their added total. We have modified the text accordingly.

(6) Method section: many experiments lack descriptions of details.

We have added details to the animal experimental design, ER ChIP-PCR, schematics of experiments are included within the main and supplemental figures, metabolomics and BA analysis have been expanded. 

Reviewer #2 (Recommendations For The Authors):

General:

(1) The authors are advised to do a thorough grammar and spelling check.

We have performed spelling and grammar check as suggested using an online platform Grammarly. Thank You.

Results:

(1) Figure 1 o The authors should show in Figure 1D female WT and female DKO liver.

See Figure 1 added in our responses to point 1 of reviewer 1’s comment.

In the Figure legend, (A-E) should be replaced by (A+D). 

Thank you. We have modified it accordingly.

The authors do not refer to 1J in the text, please add this reference.

Thank you for pointing it. We have referenced 1J in the text.

The description of 1H does not elaborate on the sex differences in ALT/AST levels, as this is the focus of the manuscript.

We have added a sentence to show that the injury markers are higher in DKO males, which is consistent with an advanced disease. Thanks.

The authors should use the correct nomenclature in Figure 1I/1J (gene vs protein and capitals vs non-capitals).

The Figure 1I and 1J show gene expression of Fxr and Shp and hence we used the non-capital italicized nomenclature. Thanks.

(2) Figure 2:

The x-axis length is different in Figures 2A and 2B. Please correct to visualize the differences between males and females better.

The x axis length has been fixed as suggested. Thanks

(3) Figure 3:

The authors should elaborate on how the patients were assigned to each gene signature. This is not fully clear.

The gene set obtained from the WT and DKO mice were used. The process used is shown as a schematic in Supplemental Fig 2C and the gene list is included  in an excel sheet as Supplemental table 1. 

We are curious how these data (F3A-C) would look when separating male and female human patients.

We performed an overall survival analysis with a subgroup of patients and provide it. We segregated the HCC cohort data on sex and age (>55 yr, since we assumed 55 as an age for menopause) and evaluated the DKO gene signature. Similar to the original figure 3, we find that irrespective of sex, and age, DKO FvsM gene signature corresponds with better overall survival in men and in women. These findings align with the combined analysis in overall survival shown in original Figure 3 of the manuscript, and therefore we did not modify it. If deemed necessary, we are happy to include the figure below to reviewers in the main manuscript.

Author response image 2.

Correlation of gene signatures obtained from WT and DKO mouse model with the survival data of HCC patients segregated by age and sex. The Kaplan Meier Survival graphs were generated based on WT and DKO transcriptome changes using five HCC clinical cohorts. Analysis of OS (Overall Survival) in patients ((A) Men and (B) Women) using the gene signatures representative of either male WT or male DKO, female WT or female DKO, and unique changes observed in female DKO mice but not in male DKO mice.

What was used as the control signature in Figure 3C? Please specify this.

For Figure 3C we compared the DKO_M signature to that of DKOF vs M signature. These genes are listed as an Excel Sheet (Supplementary Table 1).

The authors claim that DKO female mice display chronic cholestasis, similar to their male counterparts. Please refer to previous work or show the data.

Serum BA levels are elevated in DKO females are reported in supplementary table 5 and we find comparable hepatic BA composition in Figure 5 F.

(4) Figure 4: Labels for the x-axis are missing in Figure 4C. Please add legends or labels to the bars.

The x axis label is included in the top Serum BAs in (M)

In Figure 4I, the percentage of input is quite low. An IgG control would show whether recruitment of ERalpha to the shown loci is significant above background levels. Also, ChIP on the OVX liver could serve as a negative control.

We did use IgG as control pull down and the signals above this background were considered. We have not performed this in OVX, which would be an excellent negative control for future studies. Thank You.

The results and legends refer to ChIP-qPCR, while methods only mention ChIP-seq.Please adapt.

We sincerely apologize for the mistake. We used published ChIP-seq to identify putative binding site and then performed ChIP PCR to validate it. We have clarified and rectified this error. Thank You.

Significance indications in the figure legend do not correspond with significance indications in the figure. Please explain the used significance symbols in the figure in the legend.

Thank You. The legends and their significance have been matched.

(5) Figure 5:

Authors claim lowered total serum BA in females compared to males, and reference to Supplementary Table 4. However, these data are not provided, only percentages and ratios are displayed.

In the revised version, this has become Table 5. See response to the same concern noted by Reviewer 1, Point 5 above.

Figure 5D: Are sulphated BA also elevated in WT females? Please provide these data.

There is no significant urinary excretion of BAs in WT control animals. We have previously measured and found none. But under cholestatic conditions BAs are observed in urine. Therefore, sulphated BA levels were found only in the DKO mice. 

Figure 5H: Is the fecal BA excretion in WT females also proportionally higher than in males? Please provide these data.

We were unable to perform the untargeted metabolomics profiling of WT fecal samples. When we measured for BAs in the feces, as expected very low conc were present irrespective of the sex (~0.01 M) and we did not find any sex difference.  Also, prior studies in 129SVJ strain exhibited comparable fecal excretion (PMC150802). We did not find any clinical studies that measured fecal BA between the sexes.

(6) Figure 6:

References in the text of the result section to Figure 6 are wrong. The authors should change this.

Thank You. This has been rectified.

Significance indications in the legend do not correspond with significance indications in the figure. Please explain the used significance symbols in the figure in the legend.

Thank You. The legends and their significance have been matched.

(7) Supplemental Figure 3:

Please adapt the title of this figure; the sentence is incorrect. The description of this figure is very poor.

We have modified the legend and the title of the Supplemental Figure 3 to make it more appropriate. Thanks

Please explain what the blue and red dots represent.

Each dot in blue and yellow indicate the Bayesian probability generated from our BCCP model.

What are the bold horizontal lines representing? Why are there no dots in some box plots? Please elaborate.

The box represents the interquartile range (IQR), encompassing the middle 50% of the data. The bottom and top edges correspond to the 25th and 75th percentiles, respectively, while the bold horizontal line indicates the median value.

The absence of visible dots in certain categories—particularly in higher CLIP and TNM stages—is due to the small number of patients, all of whom had similar Bayesian prediction probabilities. As these values cluster tightly around the median, the individual dots may be overlapped and hidden behind the median line.

The figure is not visually easy to understand, please reconsider the representation.  

We hope the modified figure legends with the explanation of the lines and the points in the graphs increases the clarity and makes them acceptable.

Please add the DKO_female signature plot.

We have added these graph to Supplemental figure 3

(8) Supplemental 4A:

Fold change at Z-score is missing. This should be added.

Thank you we have added this information

(9) Supplemental 5:

The scale bar is missing. This should be included.

The figure is now supplemental figure 8 and the scale bar has been added.

Methods:

(1) Did the authors use ChIP-sequencing or ChIP-qPCR? Please describe the correct method.

We apologize for the error. We have used ChIP-PCR and rectified it in our methods and in our response to a figure 4 query.

(2) It is unclear how the mouse model was generated. Please refer to earlier publications.

The mice were generated in house at UIUC, and we have added this sentence to the Methods section. The original reference has been cited in the text (PMCID: PMC3007143).

Discussion:

(1) The authors claim in the discussion: 'consistently higher recruitment of ER to the classical BA synthetic genes ...' This is not shown in Figure 4I, only ER recruitment to Cyp7a1 is significantly higher in females. Please rephrase.

We agree and we have modified the sentence Cyp7A1 accounts for ~75% of BA synthesis and is a rate-limiting gene in the classical BA synthesis pathway. 

(2) The authors could make their statements stronger if they could elaborate on whether women have more fecal BA excretion, and if there are differences in serum BA concentration in HCC between male and female patients. 

Unfortunately, we were unable to find clinical studies with appropriate controls which examined and reported serum BA in HCC in a sex specific manner.

In addition, to understand whether the female-specific protections in humans are similar to mice, it would be nice to show correlations of the female-specific mouse signature with male and female liver signatures.