Reviewer #1 (Public review):

The study by Luden et al. seeks to elucidate the molecular functions of AHL15, a member of the AT-HOOK MOTIF NUCLEAR LOCALIZED (AHL) protein family, whose overexpression has been shown to extend plant longevity in Arabidopsis. To address this question, the authors conducted genome-wide ChIP-sequencing analyses to identify AHL15 binding sites. They further integrated these data with RNA-sequencing and ATAC-sequencing analyses to compare directly bound AHL15 targets with genes exhibiting altered expression and chromatin accessibility upon ectopic AHL15 overexpression.

The analyses indicate that AHL15 preferentially associates with regions near transcription start sites (TSS) and transcription end sites (TES). Notably, no clear consensus DNA-binding motif was identified, suggesting that AHL15 binding may be mediated through interactions with other regulatory factors rather than through direct sequence recognition. The authors further show that AHL15 predominantly represses its direct target genes; however, this repression appears to be largely independent of detectable changes in chromatin accessibility.

In addition to the AHL protein family, the globular H1 domain-containing high-mobility group A (GH1-HMGA) protein family also harbors AT-hook DNA-binding domains. Recent studies have shown that GH1-HMGA proteins repress FLC, a key regulator of flowering time, by interfering with gene-loop formation. The observed enrichment of AHL15 at both TSS and TES regions, therefore, raises the intriguing possibility that AHL15 may also participate in regulating gene-loop architecture. Consistent with this idea, the authors report that several direct AHL15 target genes are known to form gene loops.

Overall, the conclusions of this study are well supported by the presented data and provide new mechanistic insights into how AHL family proteins may regulate gene expression.

Reviewer #2 (Public review):

Summary:

The manuscript by Luden et al. investigates the molecular function and DNA-binding modes of AHL15, a transcription factor with pleiotropic effects on plant development. The results contribute to our understanding of AHL15 function in development specifically and transcriptional regulation in plants more broadly.

Strengths:

The authors developed a set of genetic tools for high-resolution profiling of AHL15 DNA binding and provide exploratory analyses of chromatin accessibility changes upon AHL15 overexpression. The generated data (CHiP-Seq, ATAC-Seq and RNA-Seq is a valuable resource for further studies. The data suggest that AHL15 does not operate as a pioneer TF, but is likely involved in gene looping.

Weaknesses:

The authors have extended the motif analysis to the top 1,000 shared peaks, addressing part of my previous concern. It did not erase my worries about overclaiming completely, but I think it can be considered as a terminological issue, rather than technical one. Therefore, it could be addressed through minor revision, without further analyses.

Specifically, the absence of a predominant enriched motif does not establish that AHL15 binds non-specifically or lacks sequence preferences. Low motif prevalence limits the proportion of peaks it could explain but does not exclude a genuine binding preference; a binding motif need not be rare in the genomic background (binding can be supported by other factors). Please revise the interpretation in lines 188-194, and the conclusion in lines 204-206 to state that the present analysis did not identify a strongly enriched motif accounting for a substantial proportion of AHL15-associated regions. Any equivalent claims of non-specific binding elsewhere in the manuscript should be toned down.

Additional minor points:

(1) Please provide the exact HOMER background-selection procedure, and definition of the 50-bp search windows.

(2) Figures 2B-C and the related supplementary figures, add the x axis label.

Reviewer #3 (Public review):

Summary:

This study investigated the role of AHL15 in regulation of gene expression using AHL15 overexpression lines. Their results do show that more gene are downregulated when AHL15 is upregulated and its binding is not affecting the chromatin accessibility. Further, they investigated AHL15 binds in regions depleted in histone modifications and other epigenetic signatures. Subsequently, they investigated the presence of AHL15 in the gene chromatin loops. They found overlaps with both upregulated and downregulated genes. The methods are appropriately described, but could be improved to include the analysis of self-looping gene boundaries.

Strengths:

Their study clearly showed lack of any specific sequence enrichment in the AHL15 binding sites, other than these being AT-rich, suggesting that AHL proteins do not recognize a specific DNA sequence but are recruited to their AT-rich target sites in another way. The study does suggest significant enrichment of AHL15 binding sites at TSS and TES, and AHL15 sites are depleted of any histone marks. They also identified that AHL15 binding sites overlap with self-looping gene boundaries. The authors have addressed the comments raised in the revised manuscript.

Comments on revised version.

The authors have addressed the comments raised, in the revised manuscript.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

The study by Luden et al. seeks to elucidate the molecular functions of AHL15, a member of the AT-HOOK MOTIF NUCLEAR LOCALIZED (AHL) protein family, whose overexpression has been shown to extend plant longevity in Arabidopsis. To address this question, the authors conducted genome-wide ChIP-sequencing analyses to identify AHL15 binding sites. They further integrated these data with RNA-sequencing and ATAC-sequencing analyses to compare directly bound AHL15 targets with genes exhibiting altered expression and chromatin accessibility upon ectopic AHL15 overexpression.

The analyses indicate that AHL15 preferentially associates with regions near transcription start sites (TSS) and transcription end sites (TES). Notably, no clear consensus DNA-binding motif was identified, suggesting that AHL15 binding may be mediated through interactions with other regulatory factors rather than through direct sequence recognition. The authors further show that AHL15 predominantly represses its direct target genes; however, this repression appears to be largely independent of detectable changes in chromatin accessibility.

In addition to the AHL protein family, the globular H1 domain-containing high-mobility group A (GH1-HMGA) protein family also harbors AT-hook DNA-binding domains. Recent studies have shown that GH1-HMGA proteins repress FLC, a key regulator of flowering time, by interfering with gene-loop formation. The observed enrichment of AHL15 at both TSS and TES regions, therefore, raises the intriguing possibility that AHL15 may also participate in regulating gene-loop architecture. Consistent with this idea, the authors report that several direct AHL15 target genes are known to form gene loops.

Overall, the conclusions of this study are well supported by the presented data and provide new mechanistic insights into how AHL family proteins may regulate gene expression.

However, it is important to note that the genome-wide analyses in this study rely predominantly on ectopic overexpression of AHL15 at developmental stages when the gene is not usually expressed. Moreover, loss-of-function phenotypes for AHL15 have not been reported, leaving unresolved whether AHL15 plays a physiological role in regulating plant longevity under native conditions. It therefore remains possible that longevity control is mediated by other AHL family members rather than by AHL15 itself. In this regard, the manuscript's title would benefit from more accurately reflecting this broader implication.

The ahl15 loss-of-function phenotype has previously been described in Karami et al., 2020 (Nat. Plants), Rahimi et al., 2022a (New Phyt.), and Rahimi et al., 2022b (Curr. Biol.), showing that ahl15 loss-of-function among others results in accelerated vegetative phase change and flowering, a reduced number of leaves produced by axillary meristems in short day grown plants and reduced secondary growth in the inflorescence stem. The dominant-negative ahl15 delta-G allele, expressing a mutant protein lacking the conserved G motif in the PPC domain, shows these phenotypes more clearly in the heterozygous ahl15 +/- background, and is embryo lethal in the homozygous ahl15 background (Karami et al., 2021, Nature Comm.). In addition, we recently show that leaf senescence is significantly accelerated in the ahl15 loss-of-function mutant (Luden et al., 2025, BioRxiv). These results show that AHL15 is involved in several aspects of ageing in Arabidopsis, and we have adjusted the introduction to discuss these previous findings more explicitlyWe agree with reviewer 1 on the possibility that multiple AHLs could have an effect on longevity, which is partially supported by the delayed flowering time observed in the AHL20, AHL27, or AHL29 overexpression lines (Karami et al., 2020, Street et al., 2008). However, the induction of the AHL15-GR fusion alone by DEX shows a clear delay of developmental phase transitions and the aging process in general, indicating that AHL15 by itself is able to extend longevity as other AHLs are not affected by DEX treatment (proven by the fact that their expression is not significantly changed in our RNA-seq analysis of DEX-treated 35S:AHL15-GR seedlings).

Reviewer #2 (Public review):

Summary:

The manuscript by Luden et al. investigates the molecular function and DNA-binding modes of AHL15, a transcription factor with pleiotropic effects on plant development. The results contribute to our understanding of AHL15 function in development, specifically, and transcriptional regulation in plants, more broadly.

Strengths:

The authors developed a set of genetic tools for high-resolution profiling of AHL15 DNA binding and provided exploratory analyses of chromatin accessibility changes upon AHL15 overexpression. The generated data (CHiP-Seq, ATAC-Seq and RNA-Seq is a valuable resource for further studies. The data suggest that AHL15 does not operate as a pioneer TF, but is likely involved in gene looping.

Weaknesses:

While the overall message is conveyed clearly and convincingly, I see one major issue concerning motif discovery and interpretation. The authors state that because HOMER detected highly enriched motifs at frequencies below 1%, they conclude that "a true DNA binding motif would be present in a large portion of the AHL15 peaks (targets) and would be rare in other regions of the genome (background)."

I agree that the frequency below 1% is unexpectedly low; however, this more likely reflects problems in data preprocessing or motif discovery rather than intrinsic biological properties of the transcriptional factor that possesses a DNA-binding domain and is known to bind AT_rich motifs. As it is, Figure 2 cannot serve as a main figure in the manuscript: it rather suggests that the generated CHiP-Seq peakset is dominated by noise (or motif discovery was done improperly) than that AHL15 binds nonspecifically.

Since key methodological details on the HOMER workflow are missing in the M&M section, it is not possible to determine what went wrong. Looking at other results, i.e. the reasonably structured peak distribution around TSS/TTS and consistent overlap of the peaks between the replicas, I assume that the motif discovery step was done improperly.

Therefore, I recommend redoing the motif analysis, for example, by restricting the search to the top-ranked peaks (e.g. TOP1000) and by using an appropriate background set (HOMER can generate good backgrounds, but it was not documented in the manuscript how the authors did it). If HOMER remains unsuccessful, the authors should consider complementary methods such as STREME or MEME, similar to the approach used for GH1-HMGA (https://pmc.ncbi.nlm.nih.gov/). If the peakset is of good quality, I would expect the analysis to identify an AT-rich motif with a frequency substantially higher than 1%-more likely in the range of at least 30%. If such a motif is detected, it should be reported clearly, ideally with positional enrichment information relative to TSS or TTS. It would also be informative to compare the recovered motif with known GH1-HMGA motifs.

If de novo motif discovery remains inconclusive, the authors should, at a minimum, assess enrichment of known AHL binding motifs using available PWMs (e.g. from JASPAR). As it stands, the claim that "our ChIP-seq data show that AHL15 binds to AT-rich DNA throughout the Arabidopsis genome with limited sequence specificity (Figure 2A, Figure S2-S4)" is not convincingly supported.

Another point concerns the authors' hypothesis regarding the role of AHL15 in gene looping. While I like this hypothesis and it is good to discuss it in the discussion section, the data presented are not sufficient to support the claim, stated in the abstract, that AHL15 "regulates 3D genome organization," as such a conclusion would require additional, dedicated experiments.

The motifs discovered by HOMER are ranked by their enrichment over background, of which the highest-scoring motifs are very rare in the AHL15-bound targets, but even rarer in the background, which is why they score highly on the percent enrichment score. As expected by reviewer 2, we identified AT-rich motifs that were present in a larger percentage of AHL15 targets (found in 3-18% of targets, depending on the motif, see for example motif #5 in figure S4A), which can be seen at the right tail of the histograms shown in figures 2B-C and figures S2-S4 B-C. However, these motifs were also common in the background and were therefore not considered as significantly enriched in the AHL15-bound regions, with a target:background ratio of <2. As most of these motifs were flagged by HOMER as possible false-positives, and to limit the size of the (supplemental) figures, we did not show each of the motifs identified by HOMER in table form, but the full tables of de novo motifs identified by HOMER, including possible false-positive results are included in Additional file 3.

Although the identification of AT-rich motifs shows that AHL15 (and very likely most other AHL proteins as well) binds AT-rich regions, it does not sufficiently explain the binding of AHL15 to its target genes, as these motifs are found at almost equal frequencies in non-AHL15-bound regions. In addition, a sequence found at this frequency in the genomic background is, in our view, too unspecific to be considered as a transcription factor binding site. Based on this, we concluded that AHL15 lacks a specific binding motif that can define the genes it binds.

We have updated the methods section to include more details on the HOMER analysis and have also run the analysis in the top1000 shared peaks as suggested by reviewer 2 for both AHL15 and AHL29 ChIP-seq peaks, which showed that unlike in AHL29, a clear AT-rich motif cannot be found for AHL15 (Additional file 1: Figure S5).

Reviewer #3 (Public review):

Summary:

This study investigated the role of AHL15 in the regulation of gene expression using AHL15 overexpression lines. Their results do show that more genes are downregulated when AHL15 is upregulated, and its binding does not affect the chromatin accessibility. Further, they investigated AHL15 binds in regions depleted in histone modifications and other epigenetic signatures. Subsequently, they investigated the presence of AHL15 in the gene chromatin loops. They found overlaps with both upregulated and downregulated genes. The methods are appropriately described, but could be improved to include the analysis of self-looping gene boundaries.

Strengths:

Their study clearly showed a lack of any specific sequence enrichment in the AHL15 binding sites, other than these being AT-rich, suggesting that AHL proteins do not recognize a specific DNA sequence but are recruited to their AT-rich target sites in another way. The study does suggest significant enrichment of AHL15 binding sites at TSS and TES, and AHL15 sites are depleted of any histone marks. They also identified that AHL15 binding sites overlap with self-looping gene boundaries.

Weaknesses:

The claim that AHL15 acts as a repressor and genes regulated by it are downregulated needs to be investigated based on AHL15 binding sites, to show enrichment/ depletion of AHL15 binding sites in overexpressing genes and repressed genes. The authors should provide data to support plant longevity with AHL15 overexpression using the DEX-induced system to support the claims in the title. Calculation of the enrichment score of AHL15 peaks in the self-looping genes that are upregulated or downregulated, and discussion about the different effects of AHL15 binding on self-looping regions to regulate gene expression may be helpful to understand the significance of the study. Motif enrichment in upregulated and downregulated genes separately to identify binding sequence preferences may be useful. It is not clear how the overlap of AHL15 peaks with self-looping genes has been carried out.

A metagenome plot of AHL15 binding around genes that are differentially expressed upon DEX treatment can be found in Figure 3F. This analysis shows that AHL15 binding near differentially expressed genes is more pronounced compared to all AHL15-bound genes, and that AHL15 binding near the TSS is especially enriched for upregulated genes.

As also suggested by reviewer 2, we ran a motif enrichment analysis on the differentially expressed genes that are bound by AHL15 to see if any motifs are enriched compared to the background and overrepresented in the AHL15-bound genes. Again, this did not reveal an AT-rich motif nor a motif that was conserved between up- and downregulated AHL15-bound genes (Additional file 1: Figure S6).

Plant longevity in 35S:AHL15-GR Arabidopsis plants treated with DEX has been reported previously.. DEX treatment extended vegetative development after flowering resulting in polycarpy (Karami et al., 2020, Nature Plants), enhanced secondary growth resulting in woody stems (Rahimi et al., 2022, Current Biol.) and recently we showed that it delays leaf senescence in Arabidopsis (Luden et al., 2025, bioRxiv). All these observations have now been incorporated in the results section where the p35S::AHL15-GR plants are first presented. In addition, we show that 35S:AHL15-GR plants treated a single time with DEX at 10 days after germination show a significantly delayed flowering time in figure 4C-D of this manuscript.

The enrichment of AHL15 ChIP-seq peaks in self-looping genes will be analyzed as suggested and compared to a random set of genes as a control, and the methods section will be updated to clarify how the analyses on self-looping genes were carried out.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors need to correct Line 28 on page 10:

By comparing the AHL15 ChIP-seq data with 1766 previously identified self-looping genes -> By comparing the AHL15 ChIP-seq data with 1792 previously identified self-looping genes (Liu et al., 2016)

Note: 1792 genes with self-loops were first reported by Liu et al. (2016)

Liu, C., Wang, C.M., Wang, G., Becker, C., Zaidem, M., and Weigel, D. (2016). Genome-wide analysis of chromatin packing in at single-gene resolution. Genome Res 26, 1057-1068.

These numbers will be corrected in the text.

Reviewer #2 (Recommendations for the authors):

(1) The newly generated datasets have been deposited only as raw sequencing reads. For reusability and reproducibility, the authors should also provide processed data accompanied by detailed metadata.

We will upload the processed data and corresponding metadata to GEO.

(2) Figures 4B and 5E are of low quality; can they be improved?

We have submitted the original high-quality images to the publisher, which should resolve the issue.

(3) Supplementary Table 5 lacks description (columns do not have names).

This has been fixed.

Reviewer #3 (Recommendations for the authors):

Suggestions:

(1) Motif enrichment in upregulated and downregulated genes separately to identify binding sequence preferences may be useful.

This analysis will be performed and included in the revised manuscript as Additional file 1: Figure S6.

(2) Investigate AHL15 binding sites to show enrichment/ depletion of AHL15 binding sites in overexpressing genes than repressed genes.

This analysis has been done, please see figure 3F.

(3) Provide data to support plant longevity with AHL15 overexpression using the DEX-induced system to support the claims in the title.

For the effect of AHL15-GR induction by DEX on vegetative phase change and flowering time, please see figure 4C-D and Rahimi et al., (2022, New Phytologist). For other phenotypic changes induced by DEX treatment of 35S:AHL15-GR plants, please see Karami et al. (2020; Nature Plants), Rahimi et al., (2022, Current Biology) and Luden et al., (2025; BioRxiv). Text has been added to the results section where the 35S:AHL15-GR line is first introduced to refer to these previous publications.

(4) Calculation of the enrichment score of AHL15 peaks in the self-looping genes that are upregulated or downregulated, and discussion about the different effects of AHL15 binding on self-looping regions to regulate gene expression, may be helpful to understand the significance of the study.

This analysis has been done and included in the revised manuscript as Additional file 1: Table S1.

(5) Describe how the overlap of AHL15 peaks with self-looping genes has been carried out.

The methods section has been updated with detailed information on this analysis.

eLife Assessment

This study provides important findings on the composition of glutamate receptor (GluR) subunits across diverse Drosophila neuromuscular junctions, spanning larval and adult stages and multiple muscle types. Most previous work has focused on larval body wall muscles, and this study demonstrates that this model does not capture the full diversity of GluR composition across development and tissues. The revised manuscript provides a convincing account of this diversity and will be of broad interest to researchers across neuroscience.

Reviewer #1 (Public review):

Summary:

The manuscript by Sustar et al. takes a methodical approach to document the types of glutamate receptor subunits that reside in Drosophila muscles, examining developmental stages spanning from larvae to adults. Prior work thoroughly documented the subunits operating in Drosophila larval body wall muscles. Most subsequent research focused on the glutamate receptor heterotetramers found in the body wall, composed of GluRIIA/C/D/E or GluRIIB/C/D/E subunits, along with auxiliary subunits like isoforms of Neto.

For the current work, the authors report that the larval muscle glutamate receptor composition is not universal for all Drosophila muscles. They examine the following muscle systems: larval body wall, adult abdomen, adult leg coxa, and adult indirect flight. They also briefly examine adult muscle structures associated with the proboscis, neck, and haltere. The authors find that the receptor subunits in the adult abdomen (mostly) match those in the larval body wall. This makes sense given that the adult abdominal muscles are derived from the larval body wall. Yet not much else matches the larval body wall. For example, all (or most) of the GluRII-type subunits are missing from the adult indirect flight muscles. Leg muscles have GluRII-type subunits, but they do not have all of them expressed prominently, and they are missing GluRIIB. Additionally, leg muscles express a glutamate-gated chloride channel, which could be a source of inhibitory glutamatergic transmission. Interestingly, when it comes to non-abdominal adult muscles, one general theme seems to be an active promoter (GAL4 driver) for the kainate-type glutamate receptor called Clumsy. The authors propose that Clumsy could be key to understanding how functional GluR complexes are assembled in adult insects.

Strengths:

(1) Documenting the types of glutamate receptors that operate in diverse insect muscle systems is important because it uncovers fundamental information.

(2) Much of the prior research focus has been on how the body wall muscle tetramers assemble and operate. It is a strength to demonstrate the other receptor solutions used by adult NMJs.

(3) The work uses GAL4 drivers and immunohistochemistry (when possible) in combination to draw conclusions.

(4) The muscle anatomical analyses are high quality. This allows the research group to reach refined conclusions.

(5) The confocal-level images of synaptic active zones and their apposed glutamate receptor clusters are high quality.

(6) The dataset adds specific detail and complementary context to bulk transcript analysis collections like FlyAtlas.

(7) The Discussion section is insightful. It is not simply a recap of the data in the paper. It is also an integration of that data with prior work, and it suggests direct experiments that the research team or others could attempt downstream.

Weaknesses:

One can draw expression-level conclusions from these data. But genetic tests (e.g., would clumsy losses of function impair leg muscles?) could help the authors and the field draw stronger conclusions about the roles of some of these glutamate receptor gene products.

Overall Assessment and Discussion:

The data in this study are high quality, and the results support the main conclusion: adult muscle glutamate receptor clusters do not recapitulate the "canonical" larval body wall clusters.

Comments on revised version.

The authors have done a serious revision of their manuscript, and they have directly addressed context/interpretation-level concerns that I had from the first round.

Reviewer #3 (Public review):

The Sustar et al. manuscript catalogs glutamate receptor composition across distinct Drosophila NMJs: larval and adult abdominal NMJs, as well as NMJs on adult leg and flight muscles. This work is important and probably overdue. The larval NMJ is the exemplar NMJ in this system, and the identity of "essential" and "alternative" subunits at this stage is assumed by many to hold across developmental stages and NMJ types. Here, the authors show that there is surprising diversification among NMJ types and that the notion of essential/alternative subunits only holds true at larval NMJs.

The study will generate interest in the Clumsy GluR subunit, which has not been well-characterized at all, but is widely expressed at adult NMJs. They also find striking extrasynaptic expression of glutamate-gated chloride channel GluRClalpha in adult leg and flight muscles, raising questions about its role. The study is interesting, logical, and well-written. The figures are clear, and the discussion was particularly thoughtful.

Comments on revised version.

This is a nicely revised manuscript that went a long way toward addressing the concerns in the first round. The response to the reviewers is clear and thoughtful. I think the question is framed very well and the authors do a much better job throughout making clear where the heterologous approaches agree and differ. I also think the Limitations section in the Discussion does a great job putting the work in context.

Author response:

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

eLife Assessment:

This study provides important findings on the expression of glutamate receptor (GluR) subunits across developmental stages and muscle types in Drosophila. It shows that adult muscle differs in GluR composition from larval body wall muscles, which have been the focus of most past studies. The study, while convincing, could be strengthened by acknowledging that it relies on heterogeneous methods and the absence of positive signals to infer receptor loss, which limits confidence in some of its claims. The findings illuminate how Drosophila excites muscles in diverse tissue types at different life stages, and are of interest to researchers across neuroscience.

A note on the eLife assessment

We are grateful for the assessment and for the reviewers' engagement. The assessment notes that the study "could be strengthened by acknowledging that it relies on heterogeneous methods and the absence of positive signals to infer receptor loss." We have taken this seriously and have addressed it in three ways in the revised manuscript:

(i) We have replaced claims of absence with "not detected" throughout;

(ii) We have added a paragraph describing the discrepancies between methods and the specific false-negative risks of each; and

(ii) We have made explicit the internal positive controls that constrain our negative results, including the reciprocal GluRIIB/GluRIIC labeling within a single femur and the detection of Brp, Neto-β, and GluClα in the same flight muscle preparations in which GluRII subunits were not detected.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The manuscript by Sustar et al. takes a methodical approach to document the types of glutamate receptor subunits that reside in Drosophila muscles, examining developmental stages spanning from larvae to adults. Prior work thoroughly documented the subunits operating in Drosophila larval body wall muscles. Most subsequent research focused on the glutamate receptor heterotetramers found in the body wall, composed of GluRIIA/C/D/E or GluRIIB/C/D/E subunits, along with auxiliary subunits like isoforms of Neto.

For the current work, the authors report that the larval muscle glutamate receptor composition is not universal for all Drosophila muscles. They examine the following muscle systems: larval body wall, adult abdomen, adult leg coxa, and adult indirect flight. They also briefly examine adult muscle structures associated with the proboscis, neck, and haltere. The authors find that the receptor subunits in the adult abdomen (mostly) match those in the larval body wall. This makes sense given that the adult abdominal muscles are derived from the larval body wall. Yet not much else matches the larval body wall. For example, all (or most) of the GluRII-type subunits are missing from the adult indirect flight muscles. Leg muscles have GluRII-type subunits, but they do not have all of them expressed prominently, and they are missing GluRIIB. Additionally, leg muscles express a glutamate-gated chloride channel, which could be a source of inhibitory glutamatergic transmission. Interestingly, when it comes to non-abdominal adult muscles, one general theme seems to be an active promoter (GAL4 driver) for the kainate-type glutamate receptor called Clumsy. The authors propose that Clumsy could be key to understanding how functional GluR complexes are assembled in adult insects.

Strengths:

(1) Documenting the types of glutamate receptors that operate in diverse insect muscle systems is important because it uncovers fundamental information.

(2) Much of the prior research focus has been on how the body wall muscle tetramers assemble and operate. It is a strength to demonstrate the other receptor solutions used by adult NMJs.

(3) The work uses GAL4 drivers and immunohistochemistry (when possible) in combination to draw conclusions.

(4) The muscle anatomical analyses are of high quality. This allows the research group to reach refined conclusions.

(5) The confocal-level images of synaptic active zones and their apposed glutamate receptor clusters are of high quality.

Weaknesses:

(1) There is a strawman argument that is used repeatedly to highlight the significance of the work. The argument implies that the field broadly assumes (or “tacitly” assumes) that the larval body wall glutamate receptor composition extrapolates to all muscles of the fly, including the adult. This reviewer cannot find evidence that this assumption or argument has been explicitly promulgated by others. More likely, others have not examined these muscles directly, and thus, they have not speculated one way or the other.

The reviewer is correct that we could not find a paper stating explicitly that "the adult NMJ is molecularly identical to the larval NMJ," and we have revised the text to avoid implying that such an explicit claim exists. However, we do argue that larval body-wall findings are routinely presented as properties of "the Drosophila NMJ," "the fly NMJ," or "Drosophila muscle". That unqualified generalization is what has led readers (ourselves included) to extrapolate the canonical larval architecture to the adult.

Many concrete examples can be found in the literature. He and Dickman (2025, Curr Opin Neurobiol) state that "two subtypes of ionotropic glutamate receptors (GluRs) mediate postsynaptic currents in Drosophila muscle, GluRIIA- and GluRIIB-containing," and describe their regulation by Neto as a general feature of "the fly NMJ". The word "adult" does not appear in the review. Chou et al. (2020, Neural Development) similarly assert that "at the Drosophila NMJ, iGluRs are heterometric tetramers composed of three invariant subunits, GluRIII/GluRIIC, GluRIID, and GluRIIE, as well as one of either GluRIIA or GluRIIB". A highly cited review of these receptors is titled "Glutamate receptors at the Drosophila neuromuscular junction" (DiAntonio, 2006) yet describes only the larval body-wall system, and Harris and Littleton (2015, Genetics) introduce the larval NMJ as "a well-established model glutamatergic synapse" before discussing "the fly NMJ" throughout. Notably, we could not find a review paper about Drosophila neuromuscular control that discussed differences in receptor composition between larval and adult muscles.

This assumption is related to the genesis of this project, which came about due to the failure of pharmacological tools used in the larva (e.g., philanthotoxin) to block synaptic transmission at adult fly muscles. We (the Tuthill Lab) contacted several principal investigators studying adult fly motor control and within the larval NMJ field (including now co-author Dion Dickman) and asked for advice about why these drugs were not effective in paralyzing leg muscles. Nobody suggested that this could be because adult muscles use different glutamate receptors than the larvae. Indeed, it was only years later when we noticed a high level of GluCl expression in the FlyCellAtlas data that we realized it could be due to differences in receptor expression.

We agree with the reviewer that adult muscle has rarely been examined directly (Rivlin et al., 2004 being the principal exception, which we cite and now discuss at greater length). Our argument is that this gap has been filled by an untested extrapolation from larvae rather than by data. Of the ~50 papers citing Rivlin et al. (2004), we could not find any that compare glutamate‑receptor subunit expression between larval and adult muscle. Follow‑up work pursued NMJ morphology, remodeling, adhesion molecules, and transporters, leaving the receptor question open.

Overall, we respectfully disagree with the reviewer that this argument is a strawman, because it reflects our lived experiences as active investigators of adult and larval fly motor control. However, we take the reviewer’s point. We have removed language implying that an explicit model was being overturned, and we now frame the assumption as implicit and not universally held. We note only that the assumption was operative in practice: this project began when pharmacological tools that reliably block transmission at the larval NMJ (e.g., philanthotoxin) failed to paralyze adult leg muscles, and when we consulted colleagues who work on the larval NMJ and adult fly motor control, differences in receptor composition were not among the explanations offered. We recognize this is an anecdote rather than evidence, and we have kept it out of the manuscript.

(2) Related - to the extent that there has been any tacit assumption about GluRIIC/D/E-anchored receptors being ubiquitous among adult muscles, tacit doubt was raised by Rivilin et al., 2004 (cited by the authors but not as a source of doubt) and by RNAseq datasets like FlyAtlas from 2022 (replicated in Figures s11 and s12). To be clear, the current analysis is better than a bulk transcript analysis from adult tissues. But rather than “overturning” a field or being paradigm-shifting, the current data seem confirmatory of FlyAtlas - and confirmatory of Rivlin et al., 2004, which explicitly concluded that larval and adult NMJs were different

Rivlin et al. did not examine GluRIIC, D and E, or most of the other glutamate receptor subunits. Nevertheless, we revised the beginning of our Discussion (pg 8) to position our work in the context of their important findings:

In 2004, Rivlin and colleagues conducted a careful survey of NMJs in seven muscles in the adult Drosophila thorax. They established that adult NMJs are morphologically distinct from larval NMJs, and that GluRIIA and GluRIIB are expressed in muscle-specific subsets, with some muscles mysteriously lacking both. Importantly, they speculated that some adult muscles must be using different glutamate receptor subunits (which were unknown at the time) to build synapses. This problem has remained unexplored for the last two decades.

As the reviewer requested, we have removed "overturning"/"paradigm-shifting" language throughout. But we respectfully disagree that our analysis is “confirmatory” of the Fly Cell Atlas. The Fly Cell Atlas (Li et al., 2022) does not mention glutamate receptors, or the NMJ, anywhere in its analysis. It is a general single-nucleus transcriptomic resource whose adult-muscle glutamate-receptor content was never extracted, curated, or interpreted. Extracting meaning from the dataset required posing the question, curating the relevant cells and genes, and analyzing them, which is itself a meaningful scientific contribution.

(3) One can draw expression-level conclusions from these data. But genetic tests (e.g., would clumsy losses of function impair leg muscles?) could help the authors and the field draw stronger conclusions about the roles of some of these glutamate receptor gene products. The current dataset falls short of definitively establishing the function of alternate glutamate receptor modules.

We intend to perform functional and behavioral experiments with clumsy loss-of-function flies. However, this work will require creation of new genetic reagents and behavioral experiments that make it beyond the scope of this manuscript. We intend to address this important topic in a future paper.

(4) The confocal synaptic images are of high quality. They are good enough that one could analyze how well Brp directly apposes a specific glutamate receptor subunit for all the associated imaging data underlying Figures S1-S8. No such analysis is done, but understanding what components seem to directly oppose the site of release could lead to better conclusions.

In all tissues where IIA-E are expressed at the NMJ, the protein localization is directly adjacent to Brp (see representative images in Figure 2B and s5-8). This localization is often clear in single z-slices. We attempted to perform more detailed analyses, like measure the distance between Brp and GluR puncta, but found it very challenging due to the 3D orientation of the NMJ structure. We added a sentence to page 4 of the manuscript describing what we see and the overall similarity of IIA-E localization.

Overall Assessment and Discussion:

The data in this study are of high quality, and the results support the main conclusion: adult muscle glutamate receptor clusters do not recapitulate the “canonical” larval body wall clusters. This is important, and the data stand on their own. That is the most important part. This reviewer does have suggestions on how to put the current work in proper context; the current draft appears to overstate the novelty of the findings. Additionally, some sentences need editing for accuracy. None of those concerns impeach the excellent foundational data.

Reviewer #2 (Public review):

Summary:

This manuscript presents a broad survey of glutamate receptor composition at the neuromuscular junction in Drosophila across developmental stages and muscle types. The topic is clearly important, and the central observation-that adult muscles differ substantially from the canonical larval NMJ-is interesting and potentially impactful. The dataset is extensive and will likely be of value to the community. However, in my view, there are significant limitations in how the data are generated and interpreted, which at present reduce the strength of the conclusions.

Strengths:

The study addresses a relevant and timely question and provides a large and systematic dataset. The finding that adult muscles diverge from larval NMJ organization is compelling and challenges a widely held assumption in the field. The breadth of approaches, including genetic reporters, immunohistochemistry, endogenous tagging, and transcriptomic data, is, in principle, a strong aspect of the work and allows for a broad overview of receptor expression across tissues and developmental stages. Even in its current form, the manuscript provides useful descriptive information that will be of interest to the community.

Weaknesses:

A major concern is the reliance on a heterogeneous combination of detection methods (GAL4 reporters, antibody staining, endogenous tagging, and RNA), which are treated largely as equivalent lines of evidence. These approaches differ substantially in what they measure and in their sensitivity and specificity. While convergence across methods can in principle be convincing, here this convergence is often inferred from the shared absence of signal. This is problematic because all methods used are susceptible to false negatives for different reasons. As a result, the repeated conclusion that specific GluR subunits are “absent” from adult muscles, including those previously considered essential, is not fully justified by the data presented.

This issue is not only theoretical. The manuscript itself seemingly contains examples where methods disagree, demonstrating that detection is incomplete and method-dependent. These discrepancies could be better integrated into the interpretation. Instead, negative results across methods are often taken as strong evidence for absence, which overstates the certainty of the findings.

In addition, antibody validation appears to rely largely on prior work in larval tissue. Given the structural and biochemical differences in adult muscles, it is not clear that staining performance is equivalent, particularly in cases where the signal is weak or undetected. This further complicates the interpretation of negative results.

More generally, the manuscript moves in several places from descriptive observations to functional or mechanistic implications that are not directly supported. The suggestion that adult muscles operate with fundamentally different receptor assemblies is intriguing, but remains speculative without functional validation. At a minimum, the distinction between observation and interpretation should be made more explicit.

I thus think that the current conclusions need to be more carefully constrained. Ideally, the study would be strengthened by at least one functional experiment, such as electrophysiological recordings from adult NMJs or perturbation of candidate receptors like GluClα or Clumsy. This would help to anchor the expression data in synaptic function.

We thank the reviewer for a careful and constructive critique. We agree that inference from the absence of signal requires caution, and we have revised both the wording and the framing of the manuscript substantially in response. We would also like to draw attention to a feature of our dataset that we did not previously make explicit, and which we believe speaks directly to the core concern: a number of our negative results are internally controlled by positive signal from the same reagent, in the same tissue, in the same preparation.

(i) In the adult femur, anti-GluRIIB labels NMJs on tibia extensor fibers but not on accessory tibia flexor fibers within the same bisected femur, processed, stained, and imaged together (Figure 3C-D).

(ii) Anti-GluRIIC shows the reciprocal pattern in the same preparations (Figure 3E-F). The failure to detect GluRIIC in the tibia extensor therefore cannot be attributed to a general failure of that antibody in adult tissue, to fixation, or to reagent penetration, because the same antibody labels NMJs tens of microns away in the same section.

(iii) In indirect flight muscle, where we detected none of the five GluRII subunits, we reliably detected Brp, Neto-β::sfGFP, and GluClα:V5 at and around NMJs in the same preparations (Figures 2B, 2D, 4C). Reagent access, epitope preservation, and NMJ identification are therefore all demonstrated in the same tissue where our negative results are strongest.

These controls do not exclude the possibility that receptors are present below our detection threshold, and we have accordingly replaced "absent" with "not detected" throughout the manuscript. They do, however, argue that the muscle-specific differences we report reflect genuine biological variation rather than method failure. We have added a paragraph to the Discussion making this argument explicitly, alongside a new paragraph describing the discrepancies between methods, and we have added a description of antibody validation to the Methods.

In summary, this is an interesting and potentially important study, but the current manuscript somewhat overinterprets heterogeneous and partly indirect evidence. It will already be useful in its present form, but could be more convincing if the authors more rigorously account for methodological limitations and moderate their claims accordingly.

Reviewer #3 (Public review):

The Sustar et al. manuscript catalogs glutamate receptor composition across distinct Drosophila NMJs: larval and adult abdominal NMJs, as well as NMJs on adult leg and flight muscles. This work is important and probably overdue. The larval NMJ is the exemplar NMJ in this system, and the identity of “essential” and “alternative” subunits at this stage is assumed by many to hold across developmental stages and NMJ types. Here, the authors show that there is surprising diversification among NMJ types and that the notion of essential/alternative subunits only holds true at larval NMJs.

The study will generate interest in the Clumsy GluR subunit, which has not been well-characterized at all, but is widely expressed at adult NMJs. They also find striking extrasynaptic expression of glutamate-gated chloride channel GluRClalpha in adult leg and flight muscles, raising questions about its role. The study is interesting, logical, and well-written. The figures are clear, and the discussion was particularly thoughtful. I have a couple of comments that the authors could consider.

(1) They cite Rivlin et al., (2004) in the Introduction as the sole previous study to investigate the molecular composition of adult NMJs, but do not mention this work again. In the Discussion, it would be helpful to compare/contrast their finding with those of the earlier work.

Thank you for the suggestion. We have revised the beginning of our Discussion (pg. 8) to position our work in the context of Rivlin et al.’s important findings.

(2) Were these analyses done in adults of consistent ages? It seems possible that the GluR subunit composition could be different in very young adults or in aged flies. The age of the animals should be mentioned in the Methods.

Thank you for noticing this gap. We added age of flies to the Methods section, including the important detail that in cases where we failed to detect any GAL4 signal (e.g., GluRIID-GAL4), we additionally imaged very young and very old flies (0-2 hours old and 20-day-old). It did not change the results.

(3) The broad expression of GluCl:V5 in adult leg and flight muscles is surprisingly robust and appears to light up the edges of all muscle fibers. Would the authors comment on the controls that were done to ensure that this staining is real and specific to animals carrying that V5 endogenous tag?

We added a sentence to the results section (pg 8) to highlight the V5 negative staining controls that are shown in Figure s15.

(4) The snRNAseq data in Figure S12 differ a bit from the IHC/GAL4 data summarized in the table in Figure 2. In particular, the data suggests that Ukar and Grik are widely expressed in adult muscles. Is there a reason not to include an “snRNA seq” column in Figure 2 alongside the data from GAL4 lines and IHC? To my mind, it is about as reliable as GAL4 lines that often capture only a subset of the full expression pattern. In this case, the snRNAseq data suggest that Ukar/Grik are likely at adult flight muscle NMJs, which might be important since NMJ was negative for everything except Neto-beta by IHC.

We liked your suggestion to put these data together in one figure, and we tried to incorporate this during our revisions. However, because of the difficulty of combining multiple types of data into one table, we ultimately decided to keep them separate to avoid any confusion. The GAL4 analysis is qualitative (no expression, weak expression, strong expression) in percent of muscles. The RNA-seq data is quantitative and measured in fraction of muscle cells. Figure s13 now shows RNA-seq results in a table format that is parallel to the table with GAL4 results in Figure 2.

We also added a paragraph to the end of the discussion to mull several discrepancies in results (e.g. Grik and Ukar) when using different methods.

We did observe some discrepancies across the different experimental approaches. For GAL4 reporter lines, we used T2A gene trap lines where possible (for 15 of the 16 GluR genes) to determine receptor expression. However, some of these reporters were extremely weak and may have resulted in false negatives. For example, we did not detect Grik-GAL4 or Ukar-GAL4 expression in any tissue (Figure 2C), despite RNA-seq evidence that these are expressed robustly in adult muscles (Figures s11, s12). We do not have antibodies or protein reporters for these genes to help resolve this. Another discrepancy was with GluRIIE. In this case, antibody staining and RNA-seq did not detect GluRIIE in flight muscles (Figures s8, s11), while the GAL4>GFP reporter showed extremely faint signal in the flight muscles. Because of the marginal signal and the discrepancy with the other methods, we believe this could likely be a false positive. The table in Figure 2 does not effectively capture the nuance of this otherwise confusing result. Overall, however, we found that results from different approaches generally agreed and revealed intriguing differences between different muscle types.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Most of these recommendations are for text edits. Where experiments are noted (#8 and #9 below), they could be helpful, but they are not essential because the study has value as is.

(1) It would be appropriate to scrub the entire manuscript of statements that say that the work is overturning an incorrect model about larval GluRII receptor tetramers working the same way in adult muscles. First, it is not necessary. But more importantly, by this reviewer’s reading, there is not an explicit model promoted by others that the larval body wall findings extrapolate to other muscles. The better way to frame the work is to state that it clearly shows the field has a lot of work to do to properly characterize glutamate receptor composition and function in Drosophila adults. Places in the text that the authors should edit include:

- “...challenging assumptions about the uniformity of neuromuscular function” (Abstract)

We deleted this clause.

- “...it is often tacitly assumed...This extrapolation overlooks...during metamorphosis.” (Introduction)

New wording: … “…it has commonly been assumed…” (Abstract) and “…we and others assumed…” (Intro)

- “(With one notable exception, Rivlin et al., 2004)” (Introduction). This reference deserves more than an obscure parenthetical because it explicitly concluded that larval and adult NMJs differ.

As described above, we revised the beginning of our Discussion (pg 8) to position our work in the context of Rivlin et al.’s important findings.

In 2004, Rivlin and colleagues conducted a careful survey of NMJs in seven muscles in the adult Drosophila thorax. They established that adult NMJs are morphologically distinct from larval NMJs, and that GluRIIA and GluRIIB are expressed in muscle-specific subsets, with some muscles mysteriously lacking both. Importantly, they speculated that some adult muscles must be using different glutamate receptor subunits (which were unknown at the time) to build synapses. This problem has remained unexplored for the last two decades.

- “Collectively, these results overturn the assumption of NMJ uniformity...” (Introduction)

New wording: Collectively, these results reveal a diversity in NMJ composition”

- “Our findings challenge the assumption...” (Conclusions)

We deleted this clause.

(2) (Related) The authors quibble in a couple of places that the GluRIIC/D/E subunits have been “previously considered essential for viability and NMJ function.” This reviewer’s understanding of those subunits has always been that they are essential for life, and indeed, they are essential because null mutants arrest as embryos. The places where the text seems to combine viability and NMJ function (including the Abstract) as incorrectly assigned roles for these subunits, should be more carefully edited. This reviewer agrees with the “NMJ function” conclusion since the authors are considering so many NMJs. Viability still holds.

We agree with the reviewer, and we thank them for catching an imprecision that recurred throughout the manuscript. GluRIIC, GluRIID, and GluRIIE are essential for viability, and nothing in our data contradicts that conclusion.

We think the point we were trying to make is narrower and sharper when stated precisely. Null mutants for these subunits arrest as embryos — that is, they die before the adult leg and flight muscles are formed. Those experiments therefore established a requirement for viability and for larval NMJ function, but they could not, in principle, have tested whether the same subunits are required at NMJs that arise only during pupal development. Our data do not revise the viability conclusion. They show that the subunit requirement established at the larval body-wall NMJ does not generalize to every NMJ in the animal.

We have decoupled "viability" from "NMJ function" throughout the manuscript (Abstract, Introduction, Discussion) and have added a sentence to the Discussion making the developmental logic explicit:

Importantly, because these mutants die before metamorphosis, these experiments established a requirement for viability and for larval NMJ function, but could not test whether the same subunits are required at adult NMJs, which are formed during pupal development.

(3) “...the physiology and molecular architecture of adult fly NMJs remain largely unexplored...” The authors cite the Rivilin paper that examined the prothorax. But physiology has certainly been examined at DLMs as well as proboscis NMJs.

As the manuscript says on page 2, the topic is largely unexplored compared to the larva. The Rivlin paper is an excellent contribution but was conducted over 20 years ago with more limited genetic reagents. There were also no follow-up studies. In the same amount of time, over 1000 papers have been published regarding the Drosophila larval NMJ.

The reviewer is correct that physiology has been performed in adult DLMs and proboscis muscles. These studies, however, have focused on other biological questions and did not investigate the makeup of the NMJ or manipulate glutamate receptors with pharmacology or genetic tools. Our study reveals the need for such experiments.

(4) “Surprisingly, we found that none of the primary GluRII subunits was strongly expressed in adult indirect flight muscles...” This sentence was difficult to parse when simultaneously examining the large dot for GluRIIE-Gal4 in the IFMs (Figure 2C), until the realization that the blank IHC result was driving the conclusion (no expression). The authors may want to delineate Gal4 vs. IHC for each dataset to avoid confusion for readers.

We agree with the reviewer that this result is confusing. GluRIIE-GAL4 expression was a case in which a dot in the table didn’t capture the subtlety of the result. The GluRIIE-GAL4 was expressed very faintly in the IFM, to a degree that we almost called it negative.

We added a paragraph to the Discussion in which we reflect on some data discrepancies:

We did observe some discrepancies across the different experimental approaches. For GAL4 reporter lines, we used T2A gene trap lines where possible (for 15 of the 16 GluR genes) to determine receptor expression. However, some of these reporters were extremely weak and may have resulted in false negatives. For example, we did not detect Grik-GAL4 or Ukar-GAL4 expression in any tissue (Figure 2C), despite RNA-seq evidence that these are expressed robustly in adult muscles (Figures s11, s12). We do not have antibodies or protein reporters for these genes to help resolve this. Another discrepancy was with GluRIIE. In this case, antibody staining and RNA-seq did not detect GluRIIE in flight muscles (Figures s8, s11), while the GAL4>GFP reporter showed extremely faint signal in the flight muscles. Because of the marginal signal and the discrepancy with the other methods, we believe this could likely be a false positive. The table in Figure 2 does not effectively capture the nuance of this otherwise confusing result. Overall, however, we found that results from different approaches generally agreed and revealed intriguing differences between different muscle types.

(5) “GluClalpha in adult muscles establishes the molecular identity of inhibitory glutamate responses described decades ago in other insects...” This reviewer really likes this idea. But the current data fall far short of the conclusion in this sentence.

You are correct. We tempered this statement to “The identification of extrasynaptic GluClα in adult muscles establishes a possible mechanism for inhibitory glutamate responses described decades ago […]”

(6) “One past study (Han et al., 2015) explored many combinations....” Nothing in this sentence is untrue. This reviewer just wanted to point out that one interesting observation from the Han paper was that an A/E combination alone yielded significant function in the heterologous system. To the extent that A and B have been described as competitive for the same C/D/E core, it is not a stretch to imagine that a B/E combination would have significant function, just like A/E. Or B/D/E as well.

We thank the reviewer for this observation, which we think materially strengthens the plausibility of our interpretation, and we have incorporated it into the Discussion. Han et al. (2015) found that GluRIIA and GluRIIE together were sufficient to reconstitute functional receptors in a heterologous system, without GluRIIC or GluRIID. Because GluRIIA and GluRIIB are thought to compete for the same position within the tetramer, there is no obvious reason a GluRIIB/IIE or GluRIIB/IID/IIE complex should not also be functional. This provides a concrete precedent for exactly the kind of non-canonical combinations our expression data imply — for example, GluRIIB in the absence of detectable GluRIIC in tibia extensor fibers. We have added the following to the Discussion (p. 9):

Notably, Han et al. (2015) found that GluRIIA and GluRIIE alone were sufficient to reconstitute functional receptors, without GluRIIC or GluRIID. Because GluRIIA and GluRIIB are thought to occupy the same position within the tetramer, this raises the possibility that GluRIIB-containing complexes lacking GluRIIC — such as the GluRIIB/IID/IIE combination implied by our data in the tibia extensor — could likewise be functional. Neto-β, which is required for receptor gating and synaptic clustering (Han et al., 2024; Kim et al., 2012), is expressed at all adult NMJs we examined (Figures 2D, 3B), so the auxiliary subunit requirement for such complexes would be satisfied. Direct tests of these subunit combinations by heterologous reconstitution are an important next step.

(7) GluClalpha roles: The idea of a negative feedback controller is a good one. An alternative idea can be gleaned from the NMJ anatomy of circuits like the Mauthner Cell Escape Circuit in zebrafish. In that circuit, the fish have excitatory connections on some muscles and simultaneous control of inhibitory connections wired for other muscles to enable fast changes of direction.

We thank the reviewer for this interesting comparison. We think the Mauthner arrangement is unlikely to apply here, for two reasons. First, GluClα appears to be expressed broadly across the leg and flight muscles we examined, rather than in a subset complementary to the excitatory receptors. Second, and more importantly, GluClα is extrasynaptic: it is distributed along the periphery of the muscle fiber and is not apposed to Brp-positive active zones (Figure 4C-D). Target-specific inhibitory transmission of the kind used in the Mauthner circuit requires inhibitory receptors positioned at synapses, whereas the localization we observe is better suited to tonic or slowly varying modulation of muscle excitability. We have added a sentence to the Discussion making this distinction, since the reviewer's question is one that readers will also have. And add to the manuscript, at the end of the GluClα hypothesis paragraph in the Discussion:

We note that this arrangement differs from circuits in which excitatory and inhibitory transmission are targeted to different muscles to produce rapid directional control, as in the Mauthner cell escape circuit of larval zebrafish. While most arthropods possess GABAergic motor neurons that directly inhibit leg muscles, holometabolous insects such as Drosophila do not (Witten and Truman, 1998). And because GluClα is extrasynaptic rather than apposed to active zones, it is unlikely to support fast, target-specific inhibitory transmission.

Two optional experimental suggestions:

(8) The authors’ findings with Clumsy expression along with Clumsy message expression in the FlyAtlas RNAseq datasets - and finally, the unpublished work on Clumsy - all collectively suggest that it is a great target for adult knockdown. It is not required, but the authors’ conclusions would be bolstered if they were to test RNAi against Clumsy in chosen adult NMJs and check behavior (e.g., walking?) for defects.

We intend to perform functional and behavioral experiments with clumsy loss-of-function flies. However, this work will require creation of new genetic reagents and behavioral experiments that make it beyond the scope of this manuscript. We intend to address this in a future paper.

(9) The confocal synaptic images are of high quality. They are good enough that one could analyze how well Brp directly apposes a specific glutamate receptor subunit for all the associated imaging data underlying Figures S1-S8. No such analysis is done, but understanding what components seem to directly oppose the site of release could lead to better conclusions.

In all tissues where IIA-E are expressed at the NMJ, the protein localization is directly adjacent to Brp (see representative images in Figure 2B and s5-8). This localization is often clear in single z-slices. We attempted to perform more detailed analyses, like measure the distance between Brp and GluR puncta, but found it very challenging due to the 3D orientation of the NMJ structure. We added a sentence to page 4 of the manuscript describing what we see and the overall similarity of IIA-E localization.

Reviewer #2 (Recommendations for the authors):

The authors should revise the wording throughout to more clearly distinguish between “absence” and “not detected,” in particular for statements regarding GluRII subunits in adult muscles. In the current form, some claims appear stronger than supported by the methods.

Thank you for this important suggestion. We replaced “absence” with “not detected” throughout the manuscript. We also note this distinction explicitly in the Discussion.

It would also improve clarity if the different experimental approaches (GAL4, antibody staining, tagging, RNA-seq) were presented more explicitly separated, rather than combined into a single readout. This would allow a better assessment of the evidence.

We have kept the Results organized by finding rather than by technique, because the majority of our results were concordant across approaches and a technique-by-technique presentation would fragment each biological conclusion across four sections. However, we agree that the evidence should be separable by the reader, and it now is: Figure 2C reports GAL4 and IHC in separate columns, Figure s13 presents the RNA-seq results in a parallel table format, and the new Discussion paragraph identifies each case in which the methods disagreed and states which result we consider likely to be a false positive or false negative. Where a single method underlies a conclusion, we now say so in the text.

The discrepancies between methods (e.g., RNA-seq vs GAL4 expression) should be discussed more directly, and the possibility of false negatives, especially for antibody staining in adult tissue, should be acknowledged more clearly.

Thank you. Other reviewers also noticed this weakness of our manuscript, and as noted above, we added a paragraph in the discussion to highlight several important discrepancies in methods and possibilities of false positives.

A functional experiment is not strictly required, but would clearly strengthen the manuscript. For example, electrophysiology at adult NMJs or perturbation of candidate receptors (e.g., GluClα or Clumsy) would help to link expression to function.

We intend to perform functional and behavioral experiments with clumsy loss-of-function flies. However, this work will require creation of new genetic reagents and behavioral experiments that make it beyond the scope of this manuscript. These experiments and the accompanying behavioral analysis will form a separate study, which will be the foundation of a future paper.

eLife Assessment

Overall, this is an important manuscript that delivers an invaluable community resource. The execution is relatively simple, but the evidence of this resource is solid. The effort invested in generating the knockout lines that for validation experiments is a clear strength of the study, but it doesn't substitute for a careful evaluation of the same reagents in the end-users' specific protocols before making any biological statement.

Reviewer #1 (Public review):

Summary:

The authors address the lack of validated tools for detection and quantification of proteins associated with amyotrophic lateral sclerosis (ALS) through an extensive screening of 303 commercially available antibodies to 33 protein targets. Their ALS-Reproducible Antibody Platform (ALS-RAP) delivers a validated antibody toolbox for ALS research, which will provide an advantageous starting point for researchers in this field. Ayoubi R. et al. showcase the characterization workflow, presenting as an example the characterization of antibodies targeting Galectin-1, encoded by the LGALS1 gene. A selection of these antibodies was also used to profile protein levels across human induced pluripotent stem cell (iPSC)-derived and primary neurological cell types, and the fundings support that ALS disease mechanism involves both neuronal and glial cells.

Strengths:

The knockout (KO)-based approach is definitively the major strength of this study, providing a high level of confidence in the data collected in human induced pluripotent stem cell (iPSC)-derived and primary neurological cell types. Important is also the focus on renewable reagents (monoclonal and recombinant antibodies). The extensive characterization of this set of antibodies will benefit any scientist interested in any of the 33 targets proteins, even in fields other than neuroscience.

The authors perform an interesting protein profiling study assessing 27 proteins, comparing RNA and protein expression data, and using two independent WB preparations of the same cell types. The conclusions that can be drawn from this first assessment might not be final, but data are compelling, because they have been collected with reliable and validated antibodies.

Another strength of this work is the data dissemination strategy, which includes the Only Good Antibodies (OGA) platform, where YCharOS data are curated and presented in an easy and intuitive manner that facilitates antibody selection by the end user for WB, IP and IF applications.

The authors mentioned the development of single-chain variable fragment (scFv) recombinant antibodies raised by the SGC against the six proteins (ANXA11, OPTN, MATR3, PFN1, UBQLN2 and VCP) that had limited renewable antibodies that are commercially available. The development was optimized to generate antibodies particularly suitable for IP, and the clone selection process was carried out using IP coupled to mass spectrometry. They provide details on the screening process for the SGC-generated scFv antibodies, plus share that scFv sequences.

Weakness:

The protein profiling study is limited to WB data, and the authors did not provide any explanation on why there was no integration with IP and IF data, not even for those targets that have validated antibodies. Also, not all the cell types have been screened by chemiluminescence-based detection and by fluorescence-based WB, and the authors do not elaborate on the reason for such choice. Technical and practical considerations for such decisions could have been briefly described.

Reviewer #2 (Public review):

Overall, this is a solid manuscript that delivers an important community resource. The execution is relatively simple, but the value is real, the work is rigorously performed, and the open dissemination through Zenodo, the F1000Research YCharOS Gateway and OGA is well executed. The effort invested in generating the knockout lines for validation experiments is a clear strength of the study.

Comments on revised version.

I thank the authors for their responses. A number of the smaller points I raised are now resolved. However, I am disappointed to see that the more substantial concerns, which relate to the cell-type expression claims running through the Results and the Discussion, remain unaddressed. My original point was that these claims are not quantitatively supported and that the identity of the iPSC-derived cell types used to make them has not been documented, and I do not think this revision changes that. Most of what I asked for was quantification of experiments the authors have already performed, or quality control on the cell types themselves, and this has been answered with scope arguments rather than with data. The other points I originally raised remain.

I give further details on my two main remaining concerns below:

(1) The cell-type expression claims across the manuscript are still supported by qualitative Western blot images only. These include statements such as "higher signal in glial populations," "enriched in neuronal lineages," "predominantly detected in microglial populations," and the "convergence on multicellular disease mechanisms" narrative in the Discussion. I understand the authors' decision to keep ALS-RAP as a tool and resource paper rather than expand the experimental work. However, if that is the framing, the biological interpretations of these expression data need to be removed. In their response, the authors themselves acknowledge that "quantification across multiple biological replicates would be required to establish definitive differences in protein abundance between neuronal and glial cell types." As long as this quantification is not provided, every claim of cell-type-specific expression should be removed from the Abstract, Results and Discussion, and the data presented as a descriptive survey.

(2) Related to the previous point, I do not think that quality control of the non-microglia iPSC lineages is beyond the scope of the study, as argued in the response. For ALS-RAP to be adopted as a resource, other laboratories need to trust that the authors' iPSC-derived neurons, astrocytes and oligodendrocytes are really neurons, astrocytes and oligodendrocytes. The fact that the differentiation protocols have been previously published does not confirm that they have been correctly implemented here, and this is precisely the kind of quality control that should be documented in the paper. In their response, the authors list the single markers already shown in Figure S3 (ISL1, TH, MBP, GFAP, CD44) as the answer to my concern, but a single positive marker per lineage does not establish purity.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

(1) The authors mentioned the development of single-chain variable fragment (scFv) recombinant antibodies raised by the SGC against the six proteins (ANXA11, OPTN, MATR3, PFN1, UBQLN2 and VCP) that had limited renewable antibodies that are commercially available. The development was optimized to generate antibodies particularly suitable for IP, and the clone selection process was carried out using IP coupled to mass spectrometry. Even though the generation of these novel reagents is not the focus of this work, the authors do not provide any data on this aspect.

The scFv reagents represent an important component of this resource and warranted additional description. In the revised manuscript, we expanded the section describing their origin, selection strategy, and intended use. We also added an updated reference describing the scFv discovery methodology, together with a brief summary of the workflow. In addition, the sequences of all six scFvs (ANXA11, OPTN, MATR3, PFN1, UBQLN2, and VCP) are now provided in Supplementary Table 2. During the revision process, we also identified that two scFv plasmids were missing from Add gene; these have now been deposited, making all six reagents and their sequences publicly available.

(2) The protein profiling study is limited to WB data, and the authors did not provide any explanation on why there was no integration with IP and IF data, not even for those targets that have validated antibodies. Also, not all the cell types have been screened by chemiluminescence-based detection and by fluorescence-based WB, and the authors do not elaborate on the reason for such a choice.

ALS-RAP was conceived as an open science resource for the ALS community. Given the breadth of the project (33 ALS-associated proteins), it is unrealistic for a single laboratory to investigate the biochemical and cellular biology of every target. We therefore generated and openly disseminated antibody characterization data across three complementary applications—western blot (WB), immunoprecipitation (IP), and immunofluorescence (IF)—to provide the community with validated tools that can support diverse downstream studies, including protein abundance, protein interactions, and subcellular localization.

The primary objective of the protein profiling study presented in this manuscript, however, was to compare relative protein abundance across multiple neuronal and glial cell types. Western blotting was selected because it provides a robust and semi-quantitative measurement of protein abundance across biological samples, making it well suited for systematic comparisons between cell types. In contrast, IP and IF were primarily included as antibody validation assays and as community resources for future mechanistic studies rather than for quantitative expression profiling.

Generating the large quantities of iPSC-derived neuronal and glial cells required to profile 33 ALS-associated proteins is technically demanding and resource-intensive. Consequently, a limited number of protein-cell type combinations are absent from one of the two detection modalities because insufficient lysate remained for repeat analyses. Importantly, every protein was evaluated across the complete panel of neurological cell types in at least one western blot detection modality. In most cases, the omitted samples corresponded to cell types in which the target protein was undetectable or expressed at very low levels in the initial experiment.

Reviewer #2 (Public review):

(1) The rationale for the selection of these 33 genes is insufficient. The authors lean on the Nijs & VanDamme classification and on PubMed entry counts, but the number of PubMed entries is not a meaningful criterion for what constitutes an important ALS protein - some of the most disease-relevant genes are precisely those with fewer publications, while heavily cited genes such as CAV1 carry weak ALS-specific evidence. The authors should provide a more transparent and biologically motivated rationale for inclusion and exclusion (ClinGen evidence tier, replicated GWAS signals, large meta-analyses, ALSoD) and explain why specific risk genes outside this list were not part of ALS-RAP.

We thank the reviewer for this comment and apologize if our rationale for target selection was not sufficiently clear. We agree that the number of PubMed entries should not be interpreted as a criterion for inclusion. Rather, we included this metric as a descriptive measure of how extensively each gene has been studied in the context of ALS. Specifically, comparing the number of publications for Gene versus Gene + ALS provides an indication of the relative attention a target has received within the ALS field, but it was not used to prioritize genes for inclusion.

The selection of the 33 ALS-RAP targets was instead based on established genetic evidence for disease association. Specifically, we prioritized ALS-associated genes supported by replicated human genetic studies, including rare variants with high, intermediate, or modest effect sizes, following the classification framework proposed by Nijs and Van Damme. As described in the manuscript, 25 of the 33 targets have also been independently curated by the Clinical Genome Resource (ClinGen) ALS Gene Curation Expert Panel and classified as having evidence supporting an association with ALS (Table 1). The remaining genes were selected based on published human genetic studies and emerging evidence supporting their relevance to ALS biology.

(2) "107 of 231 (46%) demonstrated specific target staining in IF." The criteria used to define "specific target staining" at the IF level are not stated. From the Galectin-1 example, the mosaic WT/KO strategy provides a binary readout, but for proteins with low expression, weak punctate staining or unusual subcellular distributions, a single threshold is unlikely to capture specificity uniformly across 231 antibodies.

We thank the reviewer for highlighting this omission. We agree that the criteria used to classify antibodies in each application should be explicitly stated. In the revised manuscript, we now define the classification criteria for Western blot (WB), immunoprecipitation (IP), and immunofluorescence (IF) in the Methods section. Briefly, WB antibodies were considered target-selective when the predominant immunoreactive band at the expected molecular weight was substantially reduced or absent in the corresponding knockout (KO) lysate. IP antibodies were considered successful when they specifically enriched the target protein from wild-type lysates, as assessed by immunoblotting of the immunoprecipitated material. For IF, antibodies were considered specific when the mean fluorescence intensity in wild-type cells was at least 1.5-fold higher than that measured in KO cells using the mosaic WT/KO assay. A minimum of 250 WT and 250 KO cells were quantified for each antibody. These criteria were applied uniformly across all antibodies to provide a standardized and objective benchmarking framework. We have also added references to the detailed YCharOS characterization workflows previously described in Ayoubi et al., Nature Protocols (2025).

(3) Several claims in the manuscript depend on differential protein abundance across cell types. As presented, these claims are supported by qualitative Western blot images only. They should be substantiated by quantification across multiple biological replicates.

The expression patterns observed were reproducible across two independent batches of iPSC-derived neuronal and glial cell types generated using the same differentiation protocols. In addition, several proteins enriched in iPSC-derived microglia also showed enrichment in primary human microglia and monocyte-derived macrophages, providing independent support for these observations.

We agree that quantification across multiple biological replicates would be required to establish definitive differences in protein abundance between neuronal and glial cell types. However, this was not the objective of the present study. Rather, our goal was to perform an initial survey of ALS-associated protein expression using rigorously validated antibodies and to identify expression patterns that may warrant further investigation.

ALS-RAP was conceived as an open science resource for the ALS community. Given the breadth of the project (33 ALS-associated proteins), we do not envision that a single laboratory can comprehensively define the expression, localization, and function of every target across all relevant cell types, tissues, and disease states. Instead, we provide validated reagents together with an initial characterization of protein expression in well-defined iPSC-derived neuronal and glial cell models to enable and accelerate future studies by the broader research community.

(4) This manuscript represents a unique opportunity to address antibody recognition of splicing variants, which is something of considerable value to the community. For each target, the predicted isoforms in Ensembl could be cross-referenced against the observed bands, and the pattern of bands compared across cell types could be informative about which isoforms each antibody captures. This would convert ambiguous "extra bands" into useful biological information and would substantially increase the value of the resource. I strongly encourage the authors to include this analysis.

We agree that defining which protein isoforms are recognized by individual antibodies would be valuable to the research community. However, we believe that such an analysis would be difficult to interpret and potentially misleading based on the data generated in the present study.

All antibodies were initially characterized in a common cancer cell line, and the best-performing reagents were subsequently used to profile ALS-associated proteins in iPSC-derived neuronal and glial cell types. Additional bands observed in neurological cells, but not in the original characterization cell line, may reflect several nonmutually exclusive possibilities, including cross-reactivity with proteins specifically expressed in neurological cells, recognition of cell type-specific splice isoforms, or post-translationally modified forms of the target protein.

Without knockout validation in each neurological cell type, these possibilities cannot be distinguished confidently.

In addition, protein migration on SDS-PAGE frequently differs from the theoretical molecular weight predicted from amino acid sequence alone. Consequently, assigning individual immunoreactive bands to Ensembl-predicted isoforms based solely on apparent molecular weight would be speculative and could lead to incorrect conclusions. We therefore believe that a rigorous isoform analysis would require complementary experimental approaches beyond the scope of the present resource study.

(5) The iPSC-derived microglia receive a comprehensive QC panel (IBA1/PU.1 IF, CD45/CD11b flow, qRT-PCR for nine canonical markers; Figure S4), which allows the reader to assess culture purity. The other iPSC-derived lineages - motor neurons, dopaminergic neurons, oligodendrocytes and astrocytes- are validated by a single marker each in WB (Figure S3) without purity quantification. Given that several conclusions of the manuscript rest on the cell-type-specific detection of ALS-associated proteins, equivalent quality control should be performed for the other lineages so that the reader can evaluate the purity of each preparation.

We thank the reviewer for this important comment and agree that documenting the identity of iPSC-derived cell populations is essential given their inherent heterogeneity. The differentiation protocols used in this study follow well-established, published methods that have been extensively validated by their developers and the broader stem cell community. We confirmed the identity of each differentiated lineage using established lineage-specific markers, including ISL1 for motor neurons, TH for dopaminergic neurons, SATB2 and CTIP2 for cortical neurons, MBP for oligodendrocytes, GFAP and CD44 for astrocytes, and CD11b and Iba1 for microglia.

We agree that comprehensive quantitative purity analyses for every differentiated lineage would further strengthen the study. However, we believe that these experiments fall beyond the scope of the present work, whose primary objective was to establish a validated antibody resource rather than to optimize or benchmark differentiation protocols. We also note that our conclusions are intentionally limited to broad protein expression patterns rather than definitive quantitative comparisons between cell types.

Finally, the inclusion of primary human microglia, fetal astrocytes, and monocyte-derived macrophages provides an independent layer of biological validation. The concordance of expression patterns observed between these primary cells and the corresponding iPSC-derived populations supports the robustness of our principal observations.

(6) The robustness of the resource would be substantially increased by validating at least a subset of the targets in a second iPSC background, in at least some of the cell types analysed.

We agree that validating antibody performance and protein expression across multiple iPSC genetic backgrounds would further strengthen the resource. However, we believe that this objective falls beyond the scope of the present study, whose primary aim was to establish a rigorously validated antibody toolbox for ALS-associated proteins and to provide an initial survey of their expression in representative neuronal and glial cell types.

We envision ALS-RAP as the foundation of a broader community effort. Rather than comprehensively evaluating all 33 proteins across multiple genetic backgrounds and tissues, our goal is to provide validated, renewable reagents that will enable such studies by the broader ALS research community.

(7) The newly developed SGC scFv antibodies are arguably the most novel reagent contribution of this manuscript, yet they receive a single sentence in the body of the paper. A more thorough description is warranted.

We agree that the scFv reagents represent an important component of this resource and warranted additional description. In the revised manuscript, we expanded the section describing their origin, selection strategy, and intended use. We also added an updated reference describing the scFv discovery methodology, together with a brief summary of the workflow. In addition, the sequences of all six scFvs (ANXA11, OPTN, MATR3, PFN1, UBQLN2, and VCP) are now provided in Supplementary Table 2. During the revision process, we also identified that two scFv plasmids were missing from Addgene; these have now been deposited, making all six reagents and their sequences publicly available.

(8) Accessibility of the resource through Zenodo is not straightforward - the reader currently has to navigate to individual antibody characterization reports one by one to extract recommendations for a given target. While the use of an established public repository is important for permanence, a dedicated ALS-RAP website with an interactive, searchable interface - filterable by target, application, host species and clonality - would meaningfully improve uptake. The relationship between such a portal and the existing OGA platform should also be clarified.

We agree that navigating individual antibody characterization reports on Zenodo can be cumbersome for end users. This challenge was one of the motivations behind the development of the Only Good Antibodies (OGA) platform, which curates YCharOS antibody characterization data, including the ALS-RAP dataset, into an interactive and searchable interface. OGA allows users to identify antibodies by target, application, host species, clonality, and other relevant attributes, while providing direct links to the complete characterization reports archived on Zenodo. In this way, Zenodo serves as the permanent open repository for the complete datasets, whereas OGA provides a user-friendly interface for data exploration and antibody selection.

eLife Assessment

This study used several approaches (computational modeling, neuronal cultures, rodent epilepsy model, and human intracranial recordings) to address a significant question in epilepsy research, with additional relevance to EEG studies more broadly: Are high frequency oscillations (or "fast ripples", defined as >200 Hz by the authors) distinct from randomly occurring clustering of spikes? The results suggest fast ripples can occur by chance and how this may occur. The significance was considered important and the strength of evidence convincing, with minor revisions suggested to temper conclusions related to stochastic vs. oscillatory fast ripples.

Reviewer #1 (Public review):

Summary:

This is a study utilizing several types of analyses (computational modeling, neuronal cultures, rodent epilepsy model, and human intracranial multi-scale recordings) to address a highly relevant conceptual question: Are fast ripples (FRs) distinct pathological entities or largely emergent products of stochastic spike clustering? The results can potentially reshape current approaches to incorporating fast ripples into the epilepsy surgery evaluation.

Strengths:

The conceptualization of fast ripples as potentially arising by chance is highly novel and builds effectively on questions raised in prior studies that have never been satisfactorily resolved. Integration across biological scales and models provides a rigorous approach, now improved by addressing theoretical concerns regarding validity of the shuffling approach and state dependence. The discussion has been updated to provide a more nuanced interpretation of the study's findings.

Weaknesses:

The authors have satisfactorily and thoughtfully addressed the critiques provided in the first review. However, there remain two points that I would like authors to address prior to publication:

(1) Synchronized burst firing is a key feature of an epileptic site generating interictal discharges, and one that could generate either oscillatory or stochastic FRs as documented in multiple prior publications cited in the manuscript and/or in the prior review. Paroxysmal depolarization, for example, has been very well described, and consists of strong, disorganized burst firing (resulting in summated postsynaptic potentials strong enough to generate high gamma signal) in a neuronal population coinciding with a large low-frequency deflection. I would like to see the results described in this context, and to avoid blanket dismissal of stochastic FRs without a clear oscillatory component.

(2) It would be highly useful to add a conclusion paragraph that spells out implications of the study for use of FRs as epileptic biomarkers in clinical invasive EEG recordings.

Comments on revised version.

The author's additions to the discussion are appreciated.

Reviewer #2 (Public review):

Summary:

This paper asks an important question that has not been discussed much in the extensive literature on the High Frequency Oscillations (HFOs) that have been extensively studied in patients with epilepsy and experimental models of epilepsy. The question is whether the Fast Ripples (FRs), the HFOs in the 250-500 Hz frequency band, represent a pathological phenomenon or represent a physiological phenomenon that occurs in the healthy brain but happens to be more frequent in epileptic tissue. It is an important question that has not been systematically addressed until now. The authors conclude, from very extensive simulations, from extensive experimental animal studies (the systemic kianate model of epilepsy in rats), and from a modest amount of human data, that FRs occur in healthy brains as a result of the chance occurrence of bursts of action potentials, and that in epileptic tissue, their frequency of occurrence is approximately 30% higher than what is expected by chance. They conclude that FRs are not a separate phenomenon of epileptic tissue. This finding is reinforced by the recent findings of FRs in experimental models of Alzheimer's disease.

Strengths:

This is a valuable study because it asks an important and original question and because it evaluates it from several angles (simulation, tissue culture, experimental animals, and human patients). The simulations and the analyses of real data are performed very carefully and with original and solidly documented approaches, using extensive simulations and extensive data sets in the cultured cell data and in the in vivo experiments. The paper is clearly written and well-illustrated.

Comments on revised version.

The authors have appropriately addressed the questions I raised in the first review

Reviewer #3 (Public review):

Summary:

An outstanding question in the field of high frequency oscillations (HFOs) in the context of epilepsy is how these oscillations emerge, considering that they occur at such high frequencies i.e., 250Hz well above the firing ability of single neurons. One hypothesis that has been suggested in the past is that neurons that fire in an out of phase fashion or rather at random intervals may contribute to a spectrum of HFOs ranging from 250-500Hz that observed in epilepsy. However, how possible it is that random action potentials could aggregate to the extent that they could give rise to HFOs in the so-called fast ripple (FRs) frequency range (>200 according to the authors) remains unclear. To test this hypothesis, they used computational modeling to randomly insert action potentials in a signal, and they found that this approach is sufficient to generate FRs. Some of the predictors of whether FRs could occur were neuronal count, firing rate and synchronization. Besides computational modeling, they used different model systems to test whether that would be possible to be observed in neuronal cultures, in epileptic rats (intrahippocampal kainic acid model), and human data. Neuronal cultures treated with picrotoxin did not show evidence that FRs could be generated more than chance aggregation of action potentials. They then asked whether synchronization and firing rate could play a role in the emergence of FRs. They found that changes in neural firing and synchronization, such as those occurring during differences phase of the sleep-wake cycle could affect the number of FRs occurring by chance aggregation, with more FRs seen during periods of wakefulness, a result that they replicated in human data.

The authors largely achieve their proposed aims of demonstrating that random neuronal firing can, in principle, generate FRs. Results from this study could influence current thinking around mechanisms generating FRs in epilepsy. The use of different computational approaches and model systems could offer new analytical methodologies for the study of FRs in the context of brain disease.

Strengths:

(1) The authors used a multi-level approach combining computational modeling with experimental datasets, including neuronal cultures, a rat model of temporal lobe epilepsy and human data.

(2) Identification of key parameters such as neuronal count, firing rate, synchronization and brain state in observed incidence of FRs generated through random aggregation of neural firing.

(3) Cross-species validation increases the likelihood of generalizability of the findings.

Comments on revised version.

The authors have addressed my comments and have no further suggestions or any changes in my assessment.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This is a study utilizing several types of analyses (computational modeling, neuronal cultures, rodent epilepsy model, and human intracranial multi-scale recordings) to address a highly relevant conceptual question: Are fast ripples (FRs) distinct pathological entities or largely emergent products of stochastic spike clustering? The results can potentially reshape current approaches to incorporating fast ripples into the epilepsy surgery evaluation.

Strengths:

The conceptualization of fast ripples as potentially arising by chance is highly novel and builds effectively on questions raised in prior studies that have never been satisfactorily resolved. Integration across biological scales and models provides a rigorous approach, now improved by addressing theoretical concerns regarding validity of the shuffling approach and state dependence. The discussion has been updated to provide a more nuanced interpretation of the study's findings.

Weaknesses:

The authors have satisfactorily and thoughtfully addressed the critiques provided in the first review. However, there remain two points that I would like authors to address:

(1) Synchronized burst firing is a key feature of an epileptic site generating interictal discharges, and one that could generate either oscillatory or stochastic FRs as documented in multiple prior publications cited in the manuscript and/or in the prior review. Paroxysmal depolarization, for example, has been very well described, and consists of strong, disorganized burst firing (resulting in summated postsynaptic potentials strong enough to generate high gamma signal) in a neuronal population coinciding with a large low-frequency deflection. I would like to see the results described in this context, and to avoid blanket dismissal of stochastic FRs without a clear oscillatory component.

To describe the results in this context, we have updated the Discussion. It reads:

“Depolarizations that promote burst firing should also increase the likelihood of FRs. Paroxysmal depolarization shifts, which are the cellular events underlying epileptiform abnormalities, would therefore be expected to co-occur with FRs. Accordingly, epileptiform abnormalities should be associated with increased gamma/high-gamma (> 80 Hz) activity at their source as has been observed in epileptogenic parenchyma (Ren et al., 2015; Sheybani et al., 2021; Weiss et al., 2015).”

(2) It would be highly useful to add a conclusion paragraph that spells out implications of the study for use of FRs as epileptic biomarkers in clinical invasive EEG recordings.

We fully agree that the main message should be further clarified. We have added this paragraph to this end:

“Clinically, our findings do not argue for or against the use of FRs as epilepsy biomarkers, as we did not assess their relationship with the epileptogenic zone. However, they do indicate that FRs are not highly specific to epileptic tissue. We would, however, recommend selecting FRs with particularly long duration, which may offer greater specificity and potentially better reliability as a biomarker. The clinical value of FRs as distinct entities or as emergent oscillations remains to be clarified.”

Please address the above critiques in Discussion, or elsewhere as deemed necessary by the authors.

Reviewer #2 (Public review):

Summary:

This paper asks an important question that has not been discussed much in the extensive literature on the High Frequency Oscillations (HFOs) that have been extensively studied in patients with epilepsy and experimental models of epilepsy. The question is whether the Fast Ripples (FRs), the HFOs in the 250-500 Hz frequency band, represent a pathological phenomenon or represent a physiological phenomenon that occurs in the healthy brain but happens to be more frequent in epileptic tissue. It is an important question that has not been systematically addressed until now. The authors conclude, from very extensive simulations, from extensive experimental animal studies (the systemic kianate model of epilepsy in rats), and from a modest amount of human data, that FRs occur in healthy brains as a result of the chance occurrence of bursts of action potentials, and that in epileptic tissue, their frequency of occurrence is approximately 30% higher than what is expected by chance. They conclude that FRs are not a separate phenomenon of epileptic tissue. This finding is reinforced by the recent findings of FRs in experimental models of Alzheimer's disease.

Strengths:

This is a valuable study because it asks an important and original question and because it evaluates it from several angles (simulation, tissue culture, experimental animals, and human patients). The simulations and the analyses of real data are performed very carefully and with original and solidly documented approaches, using extensive simulations and extensive data sets in the cultured cell data and in the in vivo experiments. The paper is clearly written and well-illustrated.

Comments on revised version.

The authors have appropriately addressed the questions I raised in the first review.

Reviewer #3 (Public review):

Summary:

An outstanding question in the field of high-frequency oscillations (HFOs) in the context of epilepsy is how these oscillations emerge, considering that they occur at such high frequencies i.e., 250Hz well above the firing ability of single neurons. One hypothesis that has been suggested in the past is that neurons that fire in an out-of-phase fashion or rather at random intervals may contribute to a spectrum of HFOs ranging from 250-500Hz that observed in epilepsy. However, how possible it is that random action potentials could aggregate to the extent that they could give rise to HFOs in the so-called fast ripple (FRs) frequency range (>200 according to the authors) remains unclear. To test this hypothesis, they used computational modeling to randomly insert action potentials in a signal, and they found that this approach is sufficient to generate FRs. Some of the predictors of whether FRs could occur were neuronal count, firing rate and synchronization. Besides computational modeling, they used different model systems to test whether that would be possible to be observed in neuronal cultures, in epileptic rats (intrahippocampal kainic acid model), and human data. Neuronal cultures treated with picrotoxin did not show evidence that FRs could be generated more than chance aggregation of action potentials. They then asked whether synchronization and firing rate could play a role in the emergence of FRs. They found that changes in neural firing and synchronization, such as those occurring during different phases of the sleep-wake cycle could affect the number of FRs occurring by chance aggregation, with more FRs seen during periods of wakefulness, a result that they replicated in human data.

The authors largely achieve their proposed aims of demonstrating that random neuronal firing can, in principle, generate FRs. Results from this study could influence current thinking around mechanisms generating FRs in epilepsy. The use of different computational approaches and model systems could offer new analytical methodologies for the study of FRs in the context of brain disease.

Strengths:

(1) The authors used a multi-level approach combining computational modeling with experimental datasets, including neuronal cultures, a rat model of temporal lobe epilepsy and human data.

(2) Identification of key parameters such as neuronal count, firing rate, synchronization and brain state in observed incidence of FRs generated through random aggregation of neural firing.

(3) Cross-species validation increases the likelihood of generalizability of the findings.

Minor weakness:

(1) The analyses conducted in human data lack direct comparison with sleep data due to no available data, but would encourage future investigations directly comparing HFOs during wakefulness and nocturnal sleep.

Comments on revised version.

The authors have addressed my comments and I have no further suggestions.

eLife Assessment

This landmark study is part of an impressive large-scale effort to assess the consistency of published findings in the field of Drosophila immunity. In this article, the authors report an analysis of claims made in approximately 400 research papers from the Drosophila immunity literature. The authors perform validation experiments to test a subset of the claims that are most inconsistent with current understanding in the field. These experiments do not necessarily aim to reproduce the original experiments, but instead to test the repeatability of the result using updated tools and methods. In some cases, the original claim is validated and in others it is not. The conclusions on the consistency of the claims, as presented in this paper, are based on mostly convincing evidence.

Reviewer #1 (Public Review):

This work revisits a substantial part of the published literature in the field of Drosophila innate immunity from 1959 to 2011. The strategy has been to restrain the analysis to some 400 articles and then to extract a main claim, two to four major claims and up to four minor claims totaling some 2000 claims overall. The consistency of these claims with the current state-of-the-art has been evaluated and reported on a dedicated Web site known as Reprosci and also in the text as well as in the 28 Supplements that report experimental verification, direct or indirect, e.g., using novel null mutants unavailable at the time, of a selected set of claims made in several articles. Of note, this review is mostly limited to the manuscript and its associated supplements and does not integrally cover the Reprosci website.

Strengths:<br /> One major strength of this article is that it tackles the issue of reproducibility/consistency on a large-scale. Indeed, while many investigators have some serious doubts on some results found in the literature, few have the courage, or the means and time, to seriously challenge studies, especially if published by leaders in the field. The Discussion adequately states the major limitations of the Reprosci approach, which should be kept in mind by the reader to form its own opinion.

This study also allows investigators not familiar with the field to have a clearer understanding of the questions at stake and to derive a more coherent global picture that allows them to better frame their own scientific questions. Besides a thorough and up-to-date knowledge of the literature used to assess the consistency of the claims with our current knowledge, a merit of this study is the undertaking of independent experiments to address some puzzling findings and the evidence presented is often convincing, albeit one should keep in mind the inherent limitations as several parameters are difficult to control, especially in the field of infections, as underlined by the authors themselves. Importantly, some work of the lead author has also been re-evaluated (e.g., Supplements S2-S4). Thus, while utmost caution should be exerted, and often is, in challenging claims, even if the challenge eventually proves to be not grounded, it is valuable to point out potential controversial issues to the scientific community.

While this is not a point of this review, it should be acknowledged that the possibility to post comments on the ReproSci website will allow further readjustments by the community in the appreciation of the literature and also of the Reprosci assessments themselves and of its complementary additional experiments. As science is evolving continuously, this site allows the current state of knowledge to be updated as needed, not necessarily by the authors themselves.

Comments on revised version:

The major weaknesses identified in the original version of the manuscript have been adequately addressed by the authors. In a few cases, additional KO mutants have been generated and analyzed thus further strengthening the manuscript.

Reviewer #2 (Public review):

Summary:

The authors present an ambitious and large-scale reproducibility analysis of 400 articles on Drosophila immunity published before 2011. They extract major and minor claims from each article, assess their verifiability through literature comparison and, when possible, through targeted experimental re-testing, and synthesize their findings in an openly accessible online database. The goal is to provide clarity to the community regarding claims that have been contradicted, incompletely supported, or insufficiently followed up in the literature, and to foster broader community participation in evaluating historical findings. The manuscript summarizes the major insights emerging from this systematic effort.

Strengths:

(1) Novelty and community value: This work represents a rare example of a systematic, transparent, and community-facing reproducibility project in a specific research domain. The creation of a dedicated public platform for disseminating and discussing these assessments is particularly innovative.

(2) Breadth and depth: The authors analyze an impressive number of publications spanning multiple decades, and they couple literature-based assessments with new experimental data where follow-up is missing.

(3) Clarity of purpose: The manuscript carefully distinguishes between assessing evidential support for claims and judging the scientific merit of historical work. This helps frame the project as constructive rather than punitive.

(4) Metascientific relevance: The analysis identifies methodological and contextual factors that commonly underlie irreproducible claims, providing a useful guide for future study design and interpretation.

(5) Transparency: Supplementary datasets and the public website provide an exceptional degree of openness, which should facilitate community engagement and further refinement.

Comments on revised version:

In the revised manuscript the authors addressed in a satisfactory manner the weaknesses I previously highlighted in my initial review.

Reviewer #3 (Public review):

Summary:

In this ambitious study the authors set out to analyse the validity of a number of claims, both minor and major from 400 published articles within the field of Drosophila immunity that were published before 2011. The authors were able to determine initially if claims were supported by comparing to other published literature in the field and if required by experimentally testing 'unchallenged' claims that had not been followed up in subsequent published literature. Using this approach the authors identified a number of claims that had contradictory evidence using new methods or taking into account developments within the field post initial publication. They publish their findings on a publicly available website designed to enable the research community to assess published work within the field with greater clarity.

Strengths:

The work presented is rigorous and methodical, the data presentation is high quality and importantly the data presented support the conclusions. The discussion is balanced and the study is written considerately and respectfully highlighting that the aim of the study is not to assign merit to individual scientists or publications but rather to improve clarity for scientists across the field. The approach carried out by the researchers focuses on testing the validity of the claims made in the original papers rather than testing whether the original experimental methods produced reproducible results. This is an important point since there are many reasons why the original interpretation of data may have understandably led to the claims made. These potential explanations for irreproducible data or conclusions are discussed in detail by the authors for each claim investigated.

The authors have generated an accompanying website which provides a valuable tool for the Drosophila Immunity research community that can be used to fact check key claims and encourages community engagement. This will achieve one important goal of this study - to prevent time loss for scientists who base their research on claims that are irreproducible. The authors rightly point out that it is impossible (and indeed undesirable) to avoid publication of irreproducible results within a field since science is 'an exploratory process where progress is made by constant course correction'. This study is however an important piece of work that will make that course correction more efficient.

Comments on revised version:

I'm impressed with the revisions carried out by the authors. No further comments.

Reviewer #4 (Public review):

Westlake, Lemaitre and colleagues have revised their manuscript regarding the reproducibility of studies on the Drosophila immune system. As was emphasized by all reviewers at the original submission of this manuscript, this paper captures a tremendous effort and makes a valuable contribution to the community.

One strong conclusion to be drawn from the overall effort is that the scientific literature is, for the most part, very good. The vast majority of claims made in the 400 papers assembled for this project were substantiated, either with previously published follow-up work or with new experimentation presented here. Although the authors have chosen not to quantify the overall validation rate of scientific claims in the present study, that information is available on the ReproSci website and in the companion paper.

In the revised manuscript, the authors make the distinction between repeatability/direct reproducibility and what they term "conceptual replication" and "indirect reproducibility", emphasizing that this study falls in the latter category because in many cases the present authors are not attempting to reproduce or replicate the original study. Instead, they are often using new tools to reinvestigate original claims and determine the accuracy of those claims, and whether they stand up to additional data. The authors have replaced the word "irreproducible" with "irreplicable" in the revised manuscript. I continue to believe the present work can be considered "validation" of the original studies and that the present work is accurately considered a "validation project". The clarification of terminology has strengthened the revised manuscript.

As with any study, the strength and breadth of conclusions that can be drawn from the present work are a function of the strength and resolution of the experiments performed. This may vary across the supplements so readers should interpret the presented results accordingly. In my opinion, all of the supplements in the revised article are sufficiently convincing to warrant inclusion in the final manuscript.

There are several instances where the authors have declined to do additional experiments in response to review. I am comfortable with these decisions, recognizing that the extra work required would be prohibitively much. Instead, the authors have adequately revised their presentation of findings. In some instances where the authors have declined to perform additional experiments, they have provided a compelling logic for their decision in the response to reviews, which unfortunately does not appear in the main manuscript. For example, in response to a comment by Reviewer 1, the authors wrote "In response to the suggestion of scanning multiple blots for quantification, we note that no clear enhancement of ModSP autoactivation was observed across different incubation times. We also explored alternative incubation conditions, but none resulted in a detectable increase in activation. Thus, additional quantification would not change the overall conclusion." This is convincing, but no readers will see it unless it appears in the manuscript or the public response to review. At the same time, I recognize the practical limitations in available space in the main article and supplement. There are a handful of instances where reviewers have made suggestions of additional/alternative experiments that would be more rigorous, accurate, or convincing than what is currently presented but the authors have declined to take up those recommendations. In some instances, I strongly agree with the authors' rationale and in other cases it is less so. However, I did not find any instance where the absence of the suggested additional experiment substantially undermined the conclusions being put forward in this manuscript. Therefore, I believe these decisions can be left to the discretion of the authors in accordance with the eLife publication model and interpretations can be left to the discretion of the readers.

Reviewer 1 and Reviewer 4 both commented on a lack of demonstration of RNAi efficacy in the knockdown experiments and suggested that negative conclusions drawn from RNAi experiments should include controls showing that the RNAi was effective. The authors have declined to include such controls, and I recognize they may be impossible to add now without redoing the entire associated experiment. Instead, the authors point to prior use of the RNA constructs by other authors in the literature. That should be recognized as less than ideal, although it is probably substantially adequate. The authors have added statements to the Discussion that RNAi knockdowns are not equivalent to null mutations and negative results may appear because of hypomorphic effects. This is a positive addition.

The replacement of the sphinx RNAi with a deletion of Sphinx 1 and Sphinx 2 as part of a general strengthening of the section on sphinx and spheroid is an extremely strong addition to the paper. I could not expect that level of effort for each of the validations and I acknowledge and appreciate that they have made that effort here.

Reviewer 1 and Reviewer 4 both commented that some figures in the original submission were ambiguous with respect to sample size and distribution of data points, including undefined error bars and inappropriate graphical representation of experiments with low sample size. These concerns have been largely addressed in the revised manuscript, including with addition of statistical analyses in several cases. The authors note that the figures were generated by multiple individuals across several research teams so it would be a large effort unify their style. I agree that this would be an unreasonable effort at this stage, for minimal return that is primarily aesthetic. The authors have now added illustration of all data points in most figures and have defined the error bars. One response to Reviewer 1 "Data points should be shown in the figure" with respect to a figure in S16 was "Unfortunately, we could not address this point to the difficulty to reach the collaborator who provided the data." That response certainly would not be acceptable in the publication of a typical scientific paper. However, I sense a different standard is being applied to the present work and the lack of these data points in this particular figure does not decrease my confidence in the authors' overall conclusion.

Overall, this is a unique piece of research that is impressive in its scope. Scientific finding is never complete; the process is eternally iterative. Inclusion of the present study in the scientific literature is a testament to collective willingness to engage in that iteration. The authors of this paper are making an exemplar contribution to accuracy in scientific research and should be commended for their effort, dedication, and fairness in what can be a delicate topic.

Author response:

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

eLife Assessment

This fundamental study is part of an impressive, large-scale effort to assess the reproducibility of published findings in the field of Drosophila immunity. In a companion article, the authors analyze 400 papers published between 1959 and 2011, and assess how many of the claims in these papers have been tested in subsequent publications. In this article, the authors report the results of validation experiments to assess a subset of the claims that, according to the literature, have not been corroborated. While the evidence reported for some of these validation studies is convincing, it remains incomplete for others.

We thank the reviewers for their careful assessment of our manuscript. We are fully aware that this review process required a substantial investment of time and effort, and we are deeply grateful for their engagement. We also thank the eLife editors for enabling an open and constructive evaluation process of the highest standard.

We fully agree with the eLife assessment, including the concluding statement highlighting the limitations of our analysis. We also concur with most of the reviewers’ comments, which we have addressed in detail in the revised manuscript. Addressing these comments required extensive additional work, which explains the duration of the revision. This period was also valuable in allowing colleagues from the Drosophila community to provide feedback on our study, including identifying potential issues—for instance regarding SR-C1—that we have carefully re-examined.

Major revisions include the addition of new experimental data in the sections on Hemese, SR-C1, Sphinx1/2, and Caspar. These results largely confirm our initial conclusions, with the exception of SR-C1. We have therefore revised our interpretation of SR-C1, confirming earlier findings that it promotes bacterial binding, while maintaining that it does not function as a major phagocytic receptor. A table with new list of new reagents has been added at the end of the supplement (Table Supplement S4). We also add a comment on the fact that mutation in the serine protease MP1 (work from B.L.) does not affect wound melanization as initially proposed (Tang et al., 2006).

One final point: our study assesses replicability using alternative experimental approaches, and we cannot exclude the possibility that our conclusions may be inaccurate. This limitation is inherent to all reproducibility studies. Nonetheless, our work should encourage the community to exercise caution when interpreting certain previous claims, some of which have become widely accepted.

We thank the reviewers and editors for their constructive input, which has significantly improved the manuscript. At this stage, we are ready to proceed toward a version of record together with the eLife assessment (which may still evolve). We continue to believe that our reproducibility project is unique in its scope and depth. It not only provides quantitative insight into replicability (See companion article)—suggesting that replication rates may be higher in certain fields, consistent with the maturation of knowledge over recent decades—but also contributes to clarifying and refining a number of statements within the field. Although aware of the cost of assessing reproducibility (hard work for articles that are not quoted and statements that are not taking in account), I consider it as one of my most important and original works.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This work revisits a substantial part of the published literature in the field of Drosophila innate immunity from 1959 to 2011. The strategy has been to restrain the analysis to some 400 articles and then to extract a main claim, two to four major claims and up to four minor claims totaling some 2000 claims overall. The consistency of these claims with the current state-of the-art has been evaluated and reported on a dedicated Web site known as ReproSci and also in the text as well as in the 28 Supplements that report experimental verification, direct or indirect, e.g., using novel null mutants unavailable at the time, of a selected set of claims made in several articles. Of note, this review is mostly limited to the manuscript and its associated supplements and does not integrally cover the ReproSci website.

Strengths:

One major strength of this article is that it tackles the issue of reproducibility/consistency on a large scale. Indeed, while many investigators have some serious doubts about some results found in the literature, few have the courage, or the means and time, to seriously challenge studies, especially if published by leaders in the field. The Discussion adequately states the major limitations of the ReproSci approach, which should be kept in mind by the reader to form their own opinion.

This study also allows investigators not familiar with the field to have a clearer understanding of the questions at stake and to derive a more coherent global picture that allows them to better frame their own scientific questions. Besides a thorough and up-to-date knowledge of the literature used to assess the consistency of the claims with our current knowledge, a merit of this study is the undertaking of independent experiments to address some puzzling findings and the evidence presented is often convincing, albeit one should keep in mind the inherent limitations as several parameters are difficult to control, especially in the field of infections, as underlined by the authors themselves. Importantly, some work of the lead author has also been re-evaluated (Supplements S2-S4). Thus, while utmost caution should be exerted, and often is, in challenging claims, even if the challenge eventually proves to be not grounded, it is valuable to point out potential controversial issues to the scientific community.

While this is not a point of this review, it should be acknowledged that the possibility to post comments on the ReproSci website will allow further readjustments by the community in the appreciation of the literature and also of the ReproSci assessments themselves and of its complementary additional experiments.

We praise the reviewer for this assessment of our project

Weaknesses:

Challenging the results from articles is, by its very nature, a highly sensitive issue, and utmost care should be taken when challenging claims. While the authors generally acknowledge the limitations of their approach in the main text and Supplements, there are a few instances where their challenges remain questionable and should be reassessed. This is certainly the case for Supplement S18, for which the ReproSci authors make a claim for a point that was not made in the publication under scrutiny. The authors of that study (Ramet et al., Immunity, 2001) never claimed that scavenger receptor SR-CI is a phagocytosis receptor, but that it is required for optimal binding of S2 cells to bacteria. Westlake et al. here have tested for a role of this scavenger receptor in phagocytosis, which had not been tested by Ramet et al. Thus, even though the ReproSci study brings additional knowledge to our understanding of the function of SR-CI by directly testing its involvement in phagocytosis by larval hemocytes, it did not address the major point of the Ramet et al. study, SR-CI binding to bacteria, and thus inappropriately concludes in Supplement S18 that "Contrary to (Ramet et al., 2001, Saleh et al., 2006), we find that SR-CI is unlikely to be a major Drosophila phagocytic receptor for bacteria in vivo." It follows that the results of Ramet et al. cannot be challenged by ReproSci as it did not address this program. Of note, Saleh et al. (2006) also mistakenly stated that SR-CI impaired phagocytosis in S2 cells and could be used as a positive control to monitor phagocytosis in S2 cells. Their assay appears to have actually not monitored phagocytosis but the association of FITC-labeled bacteria to S2 cells by FACS, as they did not mention quenching the fluorescence of bacteria associated with the surface with Trypan blue.

We have revised our evaluation of Sr-C1, as we acknowledge that we did not initially read Rämet et al. carefully. We incorrectly assumed that this study demonstrated a role for SR-C1 in phagocytosis, whereas it actually reports a defect in binding only. We have updated our assessment of SR-C1, validating the results from Rämet et al., 2001. We still mention our results on phagocytosis (See below for more information).

The inference method to assess the consistency of results with current knowledge also has limitations that should be better acknowledged. At times, the argument is made that the gene under scrutiny may not be expressed at the right time according to large-scale data or that the gene product was not detected in the hemolymph by a mass-spectrometry approach. While being in theory strong arguments, some genes, for instance, those encoding proteases at the apex of proteolytic activation cascades, need not necessarily be strongly expressed and might be released by a few cells. In addition, we are often lacking relevant information on the expression of genes of interest upon specific immune challenges such as infections with such and such pathogens.

The pattern of expression is always used as an element supporting our assessment but never as the central point of decision (See below for more information).

As regards mass spectrometry, there is always the issue of sensitivity that limits the force of the argument. Our understanding of melanization remains currently limited, and methods are lacking to accurately measure the killing activity associated with the triggering of the proPO activation cascade. In this study, the authors monitor only the blackening reaction of the wound site based on a semi-quantitative measurement. They are not attempting to use other assays, such as monitoring the cleavage of proPOs into active POs or measuring PO enzymatic activity. These techniques are sometimes difficult to implement, and they suffer at times from variability. Thus, caution should be exerted when drawing conclusions from just monitoring the melanization of wounds.

We employed approaches similar to those used in the original studies under evaluation. However, we acknowledge that our analysis primarily relied on cuticular melanization, which is more straightforward to monitor. We have revised the manuscript to clarify this limitation, particularly in the case of PGRP-LE.

Likewise, the study of phagocytosis is limited by several factors. As most studies in the field focus on adults, the potential role of phagocytosis in controlling Gram-negative bacterial infections is often masked by the efficiency of the strong IMD-mediated systemic immune response mediated by AMPs (Hanson et al, eLife, 2019). This problem can be bypassed in rare instances of intestinal infections by Gram-negative bacteria such as Serratia marcescens (Nehme et al., PLoS Pathogens, 2007) or Pseudomonas aeruginosa (Limmer et al. PNAS, 2011), which escape from the digestive tract into the hemocoel without triggering, at least initially, the systemic immune response. It is technically feasible to monitor bacterial uptake in adults by injecting fluorescently labeled bacteria and subsequently quenching the signal from noningested bacteria. Nonetheless, many investigators prefer to resort to ex vivo assays starting from hemocytes collected from third-instar wandering larvae as they are easier to collect and then to analyze, e.g., by FACS. However, it should be pointed out that these hemocytes have been strongly exposed to a peak of ecdysone, which may alter their properties. Like for S2 cells, it is thus not clear whether third-instar larval hemocytes faithfully reproduce the situation in adults. The phagocytic assays are often performed with killed bacteria. Evidence with live microorganisms is better, especially with pathogens. Assays with live bacteria require however, an antibody used in a differential permeabilization protocol. Furthermore, the killing method alters the surface of the microorganisms, a key property for phagocytic uptake. Bacterial surface changes are minimal when microorganisms are killed by X-ray or UV light. These limitations should be kept in mind when proceeding to inference analysis of the consistency of claims. Eater illustrates this point well. Westlake et al. state that:" [...] subsequent studies showed that a null mutation of eater does not impact phagocytosis". The authors refer here to Bretscher et al., Biology Open, 2015, in which binding to heat-killed E. coli was assessed in an ex vivo assay in third instar larvae. In contrast, Chung and Kocks (JBC, 2011) tested whether the recombinant extracellular N-terminal ligand-binding domain was able to bind to bacteria. They found that this domain binds to live Gram-positive bacteria but not to live Gram-negative bacteria. For the latter, killing bacteria with ethanol or heating, but not by formaldehyde treatment, allowed binding. More importantly, Chung and Kocks documented a complex picture in which AMPs may be needed to permeabilize the Gram-negative bacterial cell wall that would then allow access of at least the recombinant secreted Eater extracellular domain to peptidoglycan or peptidoglycan-associated molecules. Thus, the systemic Imd-dependent immune response would be required in vivo to allow Eater-dependent uptake of Gram-negative bacteria by adult hemocytes. In ex vivo assays, any AMPs may be diluted too much to effectively attack the bacterial membrane. A prediction is then that there should be an altered phagocytosis of Gramnegative bacteria in IMD-pathway mutants, e.g., an imd null mutant but not the hypomorphic imd[1] allele. This could easily be tested by ReproSci using the adult phagocytosis assay used by Kocks et al, Cell, 2005. At the very least, the part on the role of Eater in phagocytosis should take the Chung &Kocks study into account, and the conclusions modulated.

We agree that experimental conditions can always influence the outcome and may partly explain discrepancies in reproducibility. However, our approach is based on conceptual replication, with the aim of testing the generalizability of the original findings rather than reproducing them under identical conditions. We often used approaches quite similar to the initial statements.

In the case of Eater, our results challenge the conclusion from Kocks et al. that phagocytosis of Gram-negative bacteria is impaired in the absence of Eater, as this was not confirmed when using null eater mutants. Nevertheless, our data support the idea that Eater contributes to the phagocytosis of Gram-negative bacteria, likely in cooperation with NimC1.

Importantly, our findings are fully consistent with those of Chung and Knocks, who showed that the extracellular domain of Eater binds Gram-positive but not Gram-negative bacteria. Therefore, our work refines a specific aspect of the original conclusion, without questioning the overall significance of the initial Eater studies.

Another point is that some mutant phenotypes may be highly sensitive to the genetic background, for instance, even after isogenization in two different backgrounds. In the framework of a Reproducibility project, there might be no other option for such cases than direct reproduction of the experiment as relying solely on inference may not be reliable enough.

With respect to the experimental part, some minor weaknesses have been noted. The authors rely on survival to infection experiments, but often do not show any control experiments with mock-challenged or noninfected mutant fly lines. In some cases, monitoring the microbial burden would have strengthened the evidence. For long survival experiments, a check on the health status of the lines (viral microbiota, Wolbachia) would have been welcome. Also, the experimental validation of reagents, RNAi lines, or KO lines is not documented in all cases.

We thank the reviewer for their careful and constructive assessment. We agree with most of the points raised and have revised the manuscript accordingly. In particular, we have softened the wording throughout to make our evaluation less abrupt. We have also added a dedicated section on limitations at the end of the manuscript, highlighting potential sources of bias and the inherent constraints of our reproducibility approach.

In addition, we have expanded the description of the tools used and the validation of the RNAi experiments (see below). We consider it unlikely that factors such as Wolbachia or Nora virus significantly affect our conclusions, as our assays rely on short-term survival experiments, whereas these variables are more likely to influence ageing-related phenotypes. That said, we fully acknowledge that unrecognized parameters—such as environmental conditions (e.g., humidity), which we did not systematically control—could contribute to discrepancies. This limitation, however, applies broadly to most attempts at experimental reproduction.

More generally, many of the claims we challenge have not been revisited for over a decade. Our inability to validate some of them suggests that the underlying biology may be more complex than initially proposed. We recognize that some of our conclusions may be incorrect, and it would be surprising if all were entirely accurate. At the same time, reproducibility studies often face an asymmetry in standards of evidence, whereby contradicting a published claim requires a higher burden of proof than establishing it. We believe it is important to document and share such discrepancies. We also explicitly acknowledge in the revised manuscript that the ReproSci framework itself may contain errors. Even if a significant proportion of our assessments are not correct, we believe this work contributes meaningfully to clarifying ongoing debates in the field for most of them.

Finally, since the launch of the website, we have received three comments from the community—one addressing a major claim (Sr-C1) and two addressing more minor points— which have led us to refine our conclusions. The limited feedback we received suggest a broad agreement of the community with our assessment. It illustrates the value of maintaining an open, community-driven resource. The public and evolving nature of the project is, in our view, a key strength.

Reviewer #2 (Public review):

Summary:

The authors present an ambitious and large-scale reproducibility analysis of 400 articles on Drosophila immunity published before 2011. They extract major and minor claims from each article, assess their verifiability through literature comparison and, when possible, through targeted experimental re-testing, and synthesize their findings in an openly accessible online database. The goal is to provide clarity to the community regarding claims that have been contradicted, incompletely supported, or insufficiently followed up in the literature, and to foster broader community participation in evaluating historical findings. The manuscript summarizes the major insights emerging from this systematic effort.

Strengths:

(1) Novelty and community value: This work represents a rare example of a systematic, transparent, and community-facing reproducibility project in a specific research domain. The creation of a dedicated public platform for disseminating and discussing these assessments is particularly innovative.

(2) Breadth and depth: The authors analyze an impressive number of publications spanning multiple decades, and they couple literature-based assessments with new experimental data where follow-up is missing.

(3) Clarity of purpose: The manuscript carefully distinguishes between assessing evidential support for claims and judging the scientific merit of historical work. This helps frame the project as constructive rather than punitive.

(4) Metascientific relevance: The analysis identifies methodological and contextual factors that commonly underlie irreproducible claims, providing a useful guide for future study design and interpretation.

(5) Transparency: Supplementary datasets and the public website provide an exceptional degree of openness, which should facilitate community engagement and further refinement.

We praise the reviewer for this assessment of our project.

Weaknesses:

(1) Subjectivity in selection: Despite the authors' efforts, the choice of which papers and claims to highlight cannot be entirely objective. This is an inherent limitation of any retrospective curation effort, but it remains important to acknowledge explicitly.

We have added a section at the end of the discussion to discuss the limitation of our study.

(2) Emphasis on irreproducible claims: The manuscript focuses primarily on claims that are challenged or found to be weakly supported. While understandable from the perspective of novelty, this emphasis may risk overshadowing the value of claims that are well supported and reproducible.

We have added two sentences at the end of the introduction and at the beginning of the discussion that most claims are reproducible.

(3) Framing and language: Certain passages could benefit from more neutral phrasing and avoidance of binary terms such as "correct" or "incorrect," in keeping with the open-ended and iterative nature of scientific progress.

We have carefully checked the phrasing of our article to be more nuanced and avoid black-and-white assessments.

(4) Community interaction with the dataset: While the website is an excellent resource, the manuscript could further clarify how the community is expected to contribute, challenge, or refine the annotations, especially given the large volume of supplementary data.

This point is already addressed in the revised sentence: “We hope that the community accessible website will encourage researchers to share their perspectives and contribute data from diverse sources, thereby improving objectivity.” In addition, we have proactively engaged with principal investigators to motivate them to contribute to this effort by sharing unpublished results and information. However, it remains unclear to what extent scientists are genuinely interested in reproducibility, as has been noted in other studies on the topic. For example, articles that challenge previous findings are often under-cited, and the presence of contradictory evidence does not necessarily prevent researchers from continuing to cite the original claims. This is clearly a challenge of reproducibility study. Comments, evidence and corrections will not be integrated in the ReproSci website. We have already updated this database when revising this article and will continue to do it.

(5) Minor inconsistency: The manuscript states that papers from 1959-2011 were included, but the Methods section mentions a range beginning in 1940.

This should be aligned for clarity.

We have solved this discrepancy by correcting the method section. This should be 1959-2011. Thank you for spotting this mistake.

Impact and significance:

This contribution is likely to have a meaningful impact on both the Drosophila immunity community and the broader scientific ecosystem. It highlights methodological pitfalls, encourages transparent post-publication evaluation, and offers a reusable framework that other fields could adopt. The work also has pedagogical value for early-career researchers entering the field, who often struggle to navigate contradictory or outdated claims. By centralizing and contextualizing these discussions, the manuscript should help accelerate more robust and reproducible research.

Reviewer #3 (Public review):

Summary:

In this ambitious study, the authors set out to analyse the validity of a number of claims, both minor and major, from 400 published articles within the field of Drosophila immunity that were published before 2011. The authors were able to determine initially if claims were supported by comparing them to other published literature in the field and, if required, by experimentally testing 'unchallenged' claims that had not been followed up in subsequent published literature. Using this approach, the authors identified a number of claims that had contradictory evidence using new methods or taking into account developments within the field post-initial publication. They put their findings on a publicly available website designed to enable the research community to assess published work within the field with greater clarity.

Strengths:

The work presented is rigorous and methodical, the data presentation is high quality, and importantly, the data presented support the conclusions. The discussion is balanced, and the study is written considerately and respectfully, highlighting that the aim of the study is not to assign merit to individual scientists or publications but rather to improve clarity for scientists across the field. The approach carried out by the researchers focuses on testing the validity of the claims made in the original papers rather than testing whether the original experimental methods produced reproducible results. This is an important point since there are many reasons why the original interpretation of data may have understandably led to the claims made. These potential explanations for irreproducible data or conclusions are discussed in detail by the authors for each claim investigated.

The authors have generated an accompanying website, which provides a valuable tool for the Drosophila Immunity research community that can be used to fact-check key claims and encourages community engagement. This will achieve one important goal of this study - to prevent time loss for scientists who base their research on claims that are irreproducible. The authors rightly point out that it is impossible (and indeed undesirable) to avoid publication of irreproducible results within a field since science is 'an exploratory process where progress is made by constant course correction'. This study is, however, an important piece of work that will make that course correction more efficient.

Weaknesses:

I have little to recommend for the improvement of this manuscript. As outlined in my comments above, I am very supportive of this manuscript and think it is a bold and ambitious body of work that is important for the Drosophila immunity field and beyond.

We thank the reviewer for this positive assessment. This was indeed a huge amount of work with the hope this would be useful.

Reviewer #4 (Public review):

This is an important paper that can do much to set an example for thoughtful and rigorous evaluation of a discipline-wide body of literature. The compiled website of publications in Drosophila immunity is by itself a valuable contribution to the field. There is much to praise in this work, especially including the extensive and careful evaluation of the published literature.

However, there are also cautions.

We praise the reviewer for this assessment of our project.

One notable concern is that the validation experiments are generally done at low sample sizes and low replication rates, and often lack statistical analysis. This is slippery ground for declaring a published study to be untrue. Since the conclusions reported here are nearly all negative, it is essential that the experiments be performed with adequate power to detect the originally described effects. At a minimum, they should be performed with the same sample size and replication structure as the originally reported studies.

Many of the original claims we are assessing were obtained with lower sample size than our replicability experiments. Furthermore, we are often complementing our data with alternative approaches that are more robust (survival with additional bacterial strains, AMP kinetics with several time points, etc.). Although we can never claim for a total absence of an effect, our experimental designs are largely sufficient to demonstrate that we cannot report the major effects reported in the initial publications.

The first section of Results should be an overview of the general accuracy of the literature.

Of all claims made in the 400 evaluated papers, what proportion fell into each category of "verified", "unchallenged", "challenged", "mixed", or "partially verified"? This summary overview would provide a valuable assessment of the field as a whole. A detailed dispute of individual highlighted claims could follow the summary overview.

We have described the statistic of our analysis on claim validity in a companion article that will be published back-to-back with this article. We have preferred to divide assessment of claims and statistics on replicability in two articles. The present one is to provide an overview of the main claims that we considered to be fragile. Following the reviewer’s comment, we have added at the start of the manuscript a sentence stating that most of the claims were found to be validated, highlighting the solidity of the field with a link to the other article.

Section headings are phrased as declarative statements, "Gene X is not involved in process Y", which is more definitive phrasing than we typically use in scientific research. It implies proving a negative, which is difficult and rare, and the evidence provided in the present manuscript generally does not reach that threshold. A more common phrasing would be "We find no evidence that gene X contributes to process Y". A good model for this more qualified phrasing is the "We conclude that while Caspar might affect the Imd pathway in certain tissue-specific contexts, it is unlikely to act as a generic negative regulator of the Imd pathway," concluding the section on the role of Caspar. I am sure the authors feel that the softer, more qualified phrasing would undermine their article's goal of cleansing the literature of inaccuracies, but the hard declarative 'never' statements are difficult to justify unless every validation experiment is done with a high degree of rigor under a variety of experimental conditions. This caveat is acknowledged in the 3rd paragraph of the Discussion, but it is not reflected in the writing of the Results. The caveat should also appear in the Introduction.

We fully agree with the reviewer and we have softened the way we discuss all the claims in the result section.

The article is clear that "Claims were assessed as verified, unchallenged, challenged, mixed, or partially verified," but the project is called "reproducibility project" in the 7th line of the abstract, and the website is "ReproSci". The fourth line of the abstract and the introduction call some published research "irreproducible". Most of the present manuscript does not describe reproduction or replication. It describes validation, or independent experimental tests for consistency. Published work is considered validated if subsequent studies using distinct approaches yielded consistent results. For work that the authors consider suspicious, or that has not been subsequently tested, the new experiments provided here do not necessarily recreate the published experiment. Instead, the published result is evaluated with experiments that use different tools or methods, again testing for consistency of results. This is an important form of validation, but it is not reproduction, and it should not be referred to as such. I strongly suggest that variations of the words "reproducible" or "replication" be removed from the manuscript and replaced with "validation". This will be more scientifically accurate and will have the additional benefit of reducing the emotional charge that can be associated with declaring published research to be irreproducible.

We agree on this point. In response to the reviewer’s comment, we have clarified our terminology. Specifically, we now use the term “conceptual replicability” in the abstract and consistently refer to “replicability” and “irreplicability” throughout the manuscript. We hope this revised terminology improves clarity.

The manuscript includes an explanatory passage in the Results section, "Our project focuses on assessing the strength of the claims themselves (inferential/indirect reproducibility) rather than testing whether the original methods produce repeatable results (results/direct reproducibility). Thus, our conclusions do not directly challenge the initial results leading to a claim, but rather the general applicability of the claim itself." Rather than first appearing in Results, this statement should appear prominently in the abstract and introduction because it is a core element of the premise of the study. This can be combined with the content of the present Disclaimer section into a single paragraph in the Introduction instead of appearing in two redundant passages. I would again encourage the authors to substitute the word validation for reproduction, which would eliminate the need for the invented distinction between indirect versus direct reproduction. It is notable that the authors have chosen to title the relevant Methods section "Experimental Validation" and not "Replication".

The disclaimer has been moved at the end of the introduction and one sentence has been added in the abstract.

Experimental data "from various laboratories" in the last paragraph of the Introduction and the first paragraph of the Results are ambiguous. Since these new experiments are part of the central core of the manuscript, the specific laboratories contributing them should be named in the two paragraphs. If experiments are being contributed by all authors on the manuscript, it would suffice to say "the authors' laboratories". The attribution to "various labs" appears to be contradicted by the Discussion paragraph 2, which states "the host laboratory has expertise in" antibacterial and antifungal defense, implying a single lab. The claim of expertise by the lead author's laboratory is unnecessary and can be deleted if the Lemaitre lab is the ultimate source of all validation experiments.

The authors and laboratories that did the experiments are listed in the author list and are easy to identify for experts. At the same time, we did not want to highlight the specific authors to avoid a negative impact on their career. We were very happy that a small number of labs helped in our project. Since all the supplement were reviewed by Hannah Westlake (who has left the lab and the project) and myself (BL), our expertise was important as we did not want to test articles far from what we are doing in the lab. I rephrase the sentence to make it clear.

The passage on the controversial role of Duox in the gut is balanced and scholarly, and stands out for its discussion of multiple alternative lines of evidence in the published literature and supplement. This passage may benefit from research by multiple groups following up on the original claims that are not available for other claims, but the tone of the Duox section can be a model for the other sections.

Comments on other sections and supplements:

I understand the desire to explain how original results may have been obtained when they are not substantiated by subsequent experiments. However, statements such as "The initial results may have been obtained due to residual impurities in preparations of recombinant GNBP1" and "Non-replicable results on the roles of Spirit, Sphinx and Spheroide in Toll pathway activation may be due to off-target effects common to first-generation RNAi tools" are speculation. No experimental data are presented to support these assertions, so these statements and others like them (currently at the end of most "insights" sections) should not appear in Results. I recognize that the authors are trying to soften their criticism of prior studies by providing explanations for how errors may have occurred innocently. If they wish to do so, the speculative hypotheses should appear in the Discussion.

The statement in Results that "The initial claim concerning wntD may be explained by a genetic background effect independent of wntD" similarly appears to be a speculation based on the reading of the main text Results. However, the Discussion clarifies that "Here, we obtained the same results as the authors of the claim when using the same mutant lines, but the result does not stand when using an independent mutant of the same gene, indicating the result was likely due to genetic background." That additional explanation in the Discussion greatly increases reader confidence in the Result and should be explained with reference to S5 in the Results. Such complete explanations should be provided everywhere possible without requiring the reader to check the Supplement in each instance.

In some cases, such as "The results of the initial papers are likely due to the use of ubiquitous overexpression of PGRP-LE, resulting in melanization due to overactivation of the Imd pathway and resulting tissue damage", the claim to explain the original finding would be easy to test. The authors should perform those tests where they can, if they wish to retain the statements in the manuscript. Similarly, the claim "The published data are most consistent with a scenario in which RNAi generated off-target knockdown of a protein related to retinophilin/undertaker, while Undertaker itself is unlikely to have a role in phagocytosis" would be stronger if the authors searched the Drosophila genome for a plausible homolog that might have been impacted by the RNAi construct, and then put forth an argument as to why the off-target gene is more likely to have generated the original phenotype than the nominally targeted gene. There is a brief mention in S19 that junctophilin is the authors' preferred off-target candidate, but no evidence or rationale is presented to support that assertion. If the original RNAi line is still available, it would be easy enough to test whether junctophilin is knocked down as an offtarget, and ideally then to use an independent knockdown of junctophilin to recapitulate the original phenotype. Otherwise, the off-target knockdown hypothesis is idle speculation.

A good model is the passage on extracellular DNA, which states, "experiments performed for ReproSci using the original DNAse IIlo hypomorph show that elevated Diptericin expression in the hypomorph is eliminated by outcrossing of chromosome II, and does not occur in an independent DNAse II null mutant, indicating that this effect is due to genetic background (Supplementary S11)." In this case, the authors have performed a clear experiment that explains the original finding, and inclusion of that explanation is warranted. Similar background replacement experiments in other validations are equally compelling.

We believe that offering possible explanations for discrepancies between results is valuable for readers. For this reason, we have generally retained these elements in the Results section, with the exception of PGRP-SD. In that specific case, we removed the sentence stating that we could not identify the expected mutation in the original PGRP-SD mutants (see below). Although these points could have been moved to the Discussion, doing so would have made it difficult to directly associate each explanation with the corresponding claim. We therefore consider that keeping them in the Results section provides greater clarity. Our hypotheses are grounded in well-established considerations. It is known, for example, that early generations of RNAi constructs often exhibited off-target effects, that commercially available LPS preparations (e.g., from Sigma) were sometimes contaminated, and that genetic background can significantly influence immunological outcomes. It is therefore essential to consider and discuss such confounding factors, particularly those that were not fully appreciated at the time the field emerged.

Identifying motivated collaborators and coordinating experimental validation proved to be extremely time-consuming, making it impractical to systematically provide experimental verification for every discrepancy. As a result, most of our explanations remain speculative, except for the cases of WntD and DNase II, where the observed differences can be attributed to genetic background effects.

The statement "Analysis of several fly stocks expected to carry the PGRP-SDdS3 mutation used in the initial study revealed the presence of a wild-type copy PGRP-SD, suggesting that either the stock used in this study did not carry the expected mutation, or that the mutation was lost by contamination prior to sharing the stock with other labs" provides a documentable explanation of a potential error in the original two manuscripts, but the subsequent "analysis of several fly stocks" needs citations to published literature or explanation in the supplement. It is unclear from this passage how the wildtype allele in the purportedly mutant stocks could have led to the misattribution of function to PGRP-SD, so that should be explained more clearly in the manuscript.

We have removed this statement in the revised version from the result section

The originally claimed anorexia of the Gr28b mutation is explained as having been "likely obtained due to comparison to a wild-type line with unusually high feeding rates". This claim would be stronger if the wildtype line in question were named and data showing a high rate of feeding were presented in the supplement or cited from published literature. Otherwise, this appears to be speculation.

The wild-type fly stocks we used are named in the supplement.

In the section "The Toll immune pathway is not negatively regulated by wntD", FlyAtlas is cited as evidence that wntD is not expressed in adult flies. However, the FlyAtlas data is not adequately sensitive to make this claim conclusively. If the present authors wish to state that wntD is not expressed in adults, they should do a thorough test themselves and report it in the Supplement.

Alternatively, the statement "data from FlyAtlas show that wntD is only expressed at the embryonic stage and not at the adult stage at which the experiments were performed by (Gordon et al., 2005a)" could be rephrased to something like "data from FlyAtlas show strong expression of wntD in the embryo but not the adult" and it should be followed by a direct statement that adult expression was also found to be near-undetectable by qPCR in supplement S5. That data is currently "not shown" in the supplement, but it should be shown because this is a central result that is being used to refute the original claim. This manuscript passage should also describe the expression data described in Gordon et al. (2005), for contrast, which was an experimental demonstration of expression in the embryo and a claim "RT-PCR was used to confirm expression of endogenous wntD RNA in adults (data not shown)."

We agree on this but the expression pattern provided from fly atlas and other genomic resource is an additional element that reinforce our conclusion. For instance, the observation that the expression pattern of WntD is limited to early embryo is consistent with a role in the regulation of Toll pathway in D/V patterning but not immunity. The use of the expression pattern is not the key element of our assessments that rely on the use of loss-of-function mutation. We have rephrased the text in the manuscript according to Reviewer’s suggestion.

Inclusion of the section on croquemort is curious because it seems to be focused exclusively on clearance of apoptotic cells in the embryo, not on anything related to immunity. The subsection is titled "Croquemort is not a phagocytic engulfment receptor for apoptotic cells or bacteria", but the text passage contains no mention of phagocytosis of bacteria, and phagocytosis of bacteria is not tested in the S17 supplement. I would suggest deleting this passage entirely if there is not going to be any discussion of the immune-related phenotypes.

The reviewer is correct and we have in the revised version removed ‘bacteria’ from the title. We have kept the section S17 because this statement ‘Crq recognize and uptake apoptotic cells’ (Science, Immunity)’ is still a source of confusion while the role of crq is more downstream. We agree that efferocytosis might not considered as part of innate immunity but we consider these articles were important in the Drosophila immunity community at that time.

The claim "Toll is not activated by overexpression of GNBP3 or Grass: Experiments performed for ReproSci find that contrary to previous reports, overexpression of GNBP3 (Goear et al., 2006) or Grass (El Chamy et al., 2008) in the absence of immune challenge does not effectively activate Toll signaling (Supplementaries S6, S7)" is overly strongly stated unless the authors can directly repeat the original published studies with identical experimental conditions. In the absence of that, the claim in the present manuscript needs to be softened to "we find no evidence that..." or something similar. The definitive claim "does not" presumes that the current experiments are more accurate or correct than the published ones, but no explanation is provided as to why that should be the case. In the absence of a clear and compelling argument as to why the current experiment is more accurate, it appears that there is one study (the original) that obtained a certain result and a second study (the present one) that did not. This can be reported as an inconsistency, but the second experiment does not prove that the first was an error.

We have softened our statement and revised the supplement document. The title of the section is now ‘Toll is not strongly activated by overexpression of GNBP3 or Grass’. However we want to keep these supplements. The comment of the reviewer applies to all our assessment as we could be wrong. We are using experimental validation and not replication, although in this present case, we are using very similar approach to the described in the original study. Of note, the fact that over-expression of GNBP3 does not consistently activate Drs was already stated in Buchon et al 2019 and we spend quite sometimes in attempts to repeat this experiment. Finally, the Ferrandon team that produce this claim can easily repeat the experiment. This does not affect the main conclusion of their landmark article on GNBP3.

The same comment applies to the refutation of the roles for Edin and IRC. Even though the current experiments are done in the context of a broader validation study, this does not automatically make them more correct. The present work should adhere to the same standards of reporting that we expect in any other piece of science.

We fully agree with the reviewer but the comments he/she raised apply to all the assessments made in our article and nearly all the reproducibility experiments. Our assessment does not state that we are right but that we fail to conceptually reproduce the claim. This is clearly mentioned in our article. We hope to see clarification in the future. It may be one day shown that i) IRC indeed regulates intestinal immunity, ii) PGRP-LE will be shown to have an extracellular form, iii) 18W could indeed be a PRR for LPS (maybe in a specific tissues), iv) PGRPSD will be shown to function upstream of Toll, v) that Crq indeed binds apoptotic cell to internalize them… Our study highlights statements that are source of debate, but this is far from being clear. The authors of these challenged claims have the opportunity to contradict us.

The statement "Furthermore, evidence from multiple papers suggests that this result, and other instances where mutations have been found to specifically eliminate Defensin expression, is likely due to segregating polymorphisms within Defensin that disrupt primer binding in some genetic backgrounds and lead to a false negative result (Supplementary S20)" should include citations to the multiple papers being referenced. This passage would benefit from a brief summary of the logic presented in S20 regarding the various means of quantifying Defensin expression.

We appreciate the value of citing some of the papers underlying this claim. Key papers in question are discussed at length in Supplement S20, and the original papers do not realize the issue we are reporting. We therefore modified the text as follows: "Furthermore, this result, and other instances where mutations have been found to specifically eliminate Defensin expression, is likely due to segregating polymorphisms within Defensin that disrupt primer binding in some genetic backgrounds, leading to false negative results (Brennan 2007,Neyen 2014 and see Supplementary S20)”. The hypothesis we raise, namely that defensin function may involve specific polymorphisms that are absent from the reference Drosophila genome, is an important consideration that should be communicated to the community.

In S22 Results, the statement "For general characterization of the IrcMB11278 mutant, including developmental and motor defects and survival to septic injury, see additional information on the ReproSci website" is not acceptable. All necessary information associated with the paper needs to be included in the Supplement. There cannot be supporting data relegated to an independent website with no guaranteed stability or version control. The same comment applies to "Our results show that eiger flies do not have reduced feeding compared to appropriate controls (See ReproSci website)" in S25.

The ReproSci website contains additional data that we could not display in the supplement but may be useful to scientists. We believe that it is worth to mention them. We have however changed the writing stating ‘Experiments reported in the ReproSci website’ rather than ‘See ReproSci website’ to make it clear that the data are not part of the supplement.

For IRC: We have added a new section that addresses the general characterization of the IrcMB11278 mutant in the revised version (Supplement 22 Figure 2 and 3 with associated text). We do not refer to the ReproSci website anymore.

Supplement S21 appears to show a difference between the wildtype and hemese mutants in parasitoid encapsulation, which would support the original finding. However, the validation experiment is performed at a small sample size and is not replicated, so there can be no statistical analysis. There is no reported quantification of lamellocytes or total hemocytes. The validation experiment does not support the conclusion that the original study should be refuted. The S21 evaluation of hemese must either be performed rigorously or removed from the Supplement and the main text.

To address reviewers’ comment, we generated two new Hemese null mutants, Hemese^JP187 and Hemese^JP828, carrying deletions in the central region of the gene. Using these lines, we show that wild-type and Hemese mutant larvae display comparable levels of lamellocytes and similar numbers of melanized capsules following wasp infestation. We further quantified lamellocyte differentiation and included appropriate statistical analyses. We have removed the previous results obtained with the Hemese^SK2 mutant, which yielded similar observations. By reproducing our previous findings with independent mutant lines and by providing quantitative analyses, we strengthen our conclusion that Hemese does not act as a negative regulator of lamellocyte differentiation upon wasp infestation.

In S22, the second sentence of the passage "Due to the fact that IrcMB11278 flies always survived at least 24h prior to death after becoming stuck to the substrate by their wings, we do not attribute the increased mortality in Ecc15-fed IrcMB11278 flies primarily to pathogen ingestion, but rather to locomotor defects. The difference in survival between sucrose-fed and Ecc15-fed IrcMB11278 flies may be explained by the increased viscosity of the Ecc15-containing substrate compared to the sucrose-containing substrate" is quite strange. The first sentence is plausible and a reasonable interpretation of the observations. But to then conclude that the difference between the bacterial treatment versus the control is more plausibly due to substrate viscosity than direct action of the bacteria on the fly is surprising. If the authors wish to put forward that interpretation, they need to test substrate viscosity and demonstrate that fly mortality correlates with viscosity. Otherwise, they must conclude that the validation experiment is consistent with the original study.

The viscosity of a vial can easily be assessed by direct observation. Here, we provide an information that may guide further research but this is by no way a strong point of our article. Thus, we did not do any change to address this comment. We agree that the function of IRC should be entirely re-visited. We have however changed the name viscosity for stickiness to be more neutral.

In S27, the visualization of eiger expression using a GFP reporter is very non-standard as a quantitative assay. The correct assay is qPCR, as is performed in other validation experiments, and which can easily be done on dissected fat body for a tissue-specific analysis. S27 Figure 1 should be replaced with a proper experiment and quantitative analysis. In S27 Figure 2, the authors should add a panel showing that eiger is successfully knocked down with each driver>construct combination. This is important because the data being reported show no effect of knockdown; it is therefore imperative to show that the knockdown is actually occurring. The same comment applies everywhere there is an RNAi to demonstrate a lack of effect.

Eiger expression: Previous RNA-seq (Flyseq, Troha et al., 2018) or Affymetrix array using poly (A)- RNA (De Gregorio et al., 2001) have never identified eiger as an immune-induced gene. We have used a previously characterized GFP reporter gene using the same approach done by the author to attempt to see an induction in the fat body without success. Our conclusions have been nuanced.

Eiger RNAi KD: The two RNAi lines we are using have already been used in many studies assessing the function of eiger ((#108814, reference here, #45253 reference here)

The Drosomycin expression data in S3 Figure 2A look extremely noisy and are presented without error bars or statistical analysis. The S4 claim that sphinx and spheroid are not regulators of the Toll pathway because quantitative expression levels of these genes do not correlate with Toll target expression levels is an extremely weak inference. The RNAi did not work in S4, so no conclusion should be inferred from those experiments. Although the original claims in dispute may be errors in both cases, the validation data used to refute the original claims must be rigorous and of an acceptable scientific standard.

S3: The inducibility of antimicrobial peptide genes is high, albeit very variable. Importantly, we do not observe any inhibition of Drs expression at the two time points (24 and 48 h) following infection with two distinct bacteria, M. luteus and E. faecalis. Although each experiment was performed once, this corresponds to four independent tests challenging the claim from my lab that “Spheroide is required for activation of the Toll pathway.” Furthermore, if Spheroide played a significant role in Toll pathway activation, increased susceptibility to E. faecalis, B. subtilis, and B. bassiana would be expected. However, both survival data (three independent experiments) and Drs expression profiles (four conditions) consistently indicate that Spheroide is not required for Toll pathway activation. For clarity, we have removed the data related to S. aureus.

S4: To address the reviewer’s comments and reinforce our conclusion, we generated a deletion removing both sphinx 1 and sphinx 2 and analyzed Toll pathway activity in the absence of these two serine proteases. We find that flies lacking sphinx 1 and sphinx 2 exhibit wild-type induction of Drosomycin following M. luteus infection, as well as normal survival upon E. faecalis challenge. These new data provide strong evidence supporting our claim that, in contrast to our previous report (Kambris et al., 2006), Sphinx 1 and Sphinx 2 do not regulate the Toll pathway. Accordingly, we have replaced the earlier RNAi-based results with data obtained from loss-of-function mutants.

In S6 Figure 1, it is inappropriate to plot n=2 data points as a histogram with mean and standard errors. If there are fewer than four independent points, all points should be plotted as a dot plot. This comment applies to many qPCR figures throughout the supplement. In S7 Figure 1, "one representative experiment" out of two performed is shown. This strongly suggests that the two replicates are noisy, and a cynical reader might suspect that the authors are trying to hide the variance. This also applies to S5 Fig 3. Particularly in the context of a validation study, it is imperative to present all data clearly and objectively, especially when these are the specific data that are being used to refute the claim.

S6: The figure 1 of S6 shows all the points. Collectively, this represents 6 replications using 3 drivers of the claim ‘over-expression of GNBP3 efficiently activate the Toll pathway’. The observation, we are now reporting in S6, was already mentioned in Buchon et al 2009 (PNAS). To address reviewer’s concern, we have removed the standard deviation. Finally, our conclusion is rather soft ‘Overexpression of GNBP3 either ubiquitously or in the fat body does not effectively activate the Toll pathway’. At most, we find similar to (El Chamy et al., 2008) that overexpression may produce ‘weak but detectable’ activation of Toll’.

S7: We could not address this point. The point stands, there is no condition where overexpression of native Grass corresponds with higher Drosomycin expression

Other comments:

In S26, the authors suggest that much of the observed melanization arises from excessive tissue damage associated with abdominal injection contrasted to the lesser damage associated with thoracic injection. I believe there may be a methodological difference here. The Methods of S27 are not entirely clear, but it appears that the validation experiment was done with a pinprick, whereas the original Mabary and Schneider study was done with injection via a pulled capillary. My lab group (and I personally) have extensive experience with both techniques. In our hands, pinpricks to the abdomen do indeed cause substantial injury, and the physically less pliable thorax is more robust to pinpricks. However, capillary injections to the abdomen do virtually no tissue damage - very probably less than thoracic injections - and result in substantially higher survivals of infection even than thoracic injections. Thus, the present manuscript may infer substantial tissue damage in the original study because they are employing a different technique.

The reviewer is correct that injection and pinprick injury do not induce the same type of injury and there are differences across labs. We still believe that our approach is valuable. The point is that we confirmed a role of eiger in melanization but not due to its expression in the fat body. It is important to underline that our ReproSci is a conceptual replication project and that we never directly challenge the original observation but rather the robustness of the claim. Injection with a pulled capillary was attempted — in our hands, this caused extensive trauma and killed over 80% of flies it was attempted on. The pinprick on the other hand caused very little trauma. The first sentence of the Results/discussion section states this point.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

It is questionable whether all the studies relevant to the field of assessment have been identified, starting with the own publications from the lead authors. Indeed, Buchon et al, Genes & Development, 2009, Buchon et al., Cell Host&Microbe, 2009, Buchon et al., BMC Biology, 2010 have not been included in the 400 articles, even though one of them is cited when discussing the role of Duox in the intestinal host defense. Other missing articles that fulfill the criteria set by the authors include, but may not be limited to, Chung et al. JBC, 2011, Nehme et al., PLoS One, 2011, Cronin et al., Science, 2009, Limmer et al. 2011.

In our selection, we did not choose articles dealing with intestinal homeostasis and stem cells as well as microbiota/symbionts (Buchon 2009a,b and 2010 Cronin 2009). We also did not analyze articles centered on virulence factor (Limmer 2011). I agree that we missed Chung et al. JBC, 2011 and Nehme et al., PLoS One, 2011 that were published in 2011. Table S1 provide all the information on the article we selected and the ones we removed from the first search.

One area of the field that would have benefited from further insights of ReproSci is that of innate immunity memory or priming (Pham et al., PLoS Pathogens, 2007, has been included in the 400 articles). That being said, the scope of this article is already considerable, and this is just a suggestion for future scrutiny.

The reviewer should recognize that this study (Pham et al.) is inherently complex to reproduce. The field of innate immune priming has also matured considerably since the first publications. Importantly, the set of articles containing “non-validated claims” does not fully overlap with the category of studies that might be considered as weak or problematic.

A major issue in science is the exaggeration of claims, which our approach does not capture. As a result, some articles that are strongly promoted yet make relatively trivial claims— often a source of frustration within the community—may still be classified as valid under our framework. This represents an important limitation of our approach.

For the Supplements, it would be better to show all the data points, especially with respect to RTqPCR data. The nature of the error bars (SD, SE) is never indicated except for one exception (Figure 5, S28). When introducing or using novel lines affecting gene expression, such as RNAi lines or KO mutants, there are often no indications as to how these lines have been validated.

This is especially critical for negative results.

Errors bars: The errors bars were standard deviation. Sorry for this lacks of clarity. This is now indicated in the supplement. Experiments were done in multiple laboratories requiring complex coordination. For this reason, changing all the graphs was too complicated and could not be done for all the figures in the revised version. However data points are shown in many figures of the original draft and all the new figures of the revised version.

For RNAi validation: Concerning the RNAi validation:

(a) Sphinx ½: We have extended our work on Sphinx using a newly generated double

mutant that remove both Sphinx1 and 2. Thus our conclusion does not rely anymore only the use of RNAi.

(b) S12: Hep RNAi : We are using standard Hep-RNAi and BskDN fly tools that have been validated in many studies.

Articles validating the HepRNAi (BDSC35210) can be found on this link. This line has also been validated in Figure 1 of the revised version of Supplement S12.

Articles validating the BskDN (BDSC6409) can be found on this link.

Of note, the Bloomington number of Hep RNAi was miss-annotated and has been corrected in the revised version.

(a) S16. Dscam: The Trip RNAi lines has been used in other articles (ex. Bui et al., “Adjacent neuronal fascicle guides motoneuron dendritic branching 2024 (eNeuro)).

(b) S23. Duox. We are using two RNAi lines including the original RNAi construct used in the article we assessed (Ha et al., 2005).

(c) Eiger: we are using two distinct UAS-RNAi constructs that have been validated (#108814, reference here, #45253 reference here).

Loss-of-function mutations:

For previously described mutants: we used some previously described mutants available in stock centers or from other labs. These include Spheroide^D104, wntD mutants Irc^MB11278, NOS^Δall and Gr28b. See references in the supplement. We have always checked the genotypes of these mutants.

For newly generated mutants

spirit^DR32 see Figure 1 in S2

edin^KO: we have added a new figure describing the mutant in S14 D

ΔSphinx1/2 we have added a figure describing the mutant in S4

DNaseII^sk4: the exact frameshift mutation is indicated in S11

SR-CI^SK6 and Δ(Sr-CI,Sr-CIII): we have added a figure describing the mutant in S18

Hemese^JP187 and HemeseJP⁸²⁸ we have added a figure describing the mutant in S21

Listericin^Δ1 and Listericin^Δ2 mutation are described in Figure 1 in S15

We have now included in the revised supplement a table with all the new tools generated in the framework of the ReproSci project (Supplementary Table 4).

The only uncharacterized mutant is PGRP-LE^Δ53, a gift from François Rouyer (Gif-sur-Yvette). But we also did our experiments with an established mutant: PGRP-LE¹¹².

Is the repeated use of "in vitro" to refer to cell culture studies appropriate? In vitro usually refers to experiments performed in the absence of any living organism or cell, e.g., biochemical reactions in a test tube.

Accordingly, we have replaced in vitro by in cell culture when appropriate

(A) MAIN TEXT

(1) Introduction:

PGRP-LC: Ramet et al, Nature 2002 reference is missing.

"[...]epithelial repair through stem cell proliferation" is a typical disease tolerance mechanism and therefore unlikely to "[...]contribute to DETERRING ingested pathogens". In addition, is "detterring" really the appropriate word?

The changes have been made.

(2) Results:

GNBP1: "and find no evidence" would read better as "and found no evidence". In addition, for GNBP3, the authors may also want to cite Mishima et al. (JBC, 2009) and possibly one on silkworm ßGRP (Takehasi et al., PNAS, 2009).

The changes have been made.

Wnt D: "Dif" and not "dif"=diffuse irregular facets

The changes have been made.

cGLR-STING pathway (Cai et al., 2022): subsequent studies indicated that cGLR ligands are RNA molecules, not DNA. Thus, whether such receptors would be able to detect naked DNA remains a remote possibility.

We agree and have amended the text accordingly

DSCAM1: the statement "not amenable to genetic studies" might be modulated into "not easily amenable to genetic studies" as exemplified by Dong et al. PLoS Biol, 2025 (which the authors may now add to their reference list as this article was published after submission of the current work) and all the literature on DSCAM and the Drosophila nervous system.

We agree and have amended the text accordingly

Psidin: "multiple papers suggest...". References are not given.

We have amended the text and reported to the supplement. Some references have been added.

NOS: "this study reports" should be "this study reported"; otherwise, the reader falsely believes that the authors refer to the Reprosci article. NOS expression: what about data from subsequent RNAseq studies and data from FlyCell Atlas?

We agree with the reviewer and used the past time. For simplicity, we did not discuss Nos expression pattern.

Eiger: the Kodra et al. reference appears to be missing in the reference list.

The Kodra reference has been added.

(3) Discussion:

Third source of irreproducible claims: besides off-target effects, a limitation of the RNAi approach is that one can never be sure that a null phenotype is obtained. Thus, when obtaining negative results, it may be caused by a hypomorphic effect.

This additional point has been added with an example that illustrates the point “Besides off-target effects, a limitation of the RNAi approach is that one can never be sure that it mimics a full null phenotype. As an example, the partial silencing of the serine protease gene Grass may explain why its role in the antifungal response was not detected using in vivo RNAi, but was revealed through the use of a null mutation (El Chamy et al., 2008; Kambris et al., 2006b)”.

(4) Reference list:

Cuttell et al, Gordon et al, 2005, and Melcarne et al, 2019 are duplicated.

Thank you for noticing it. Change has been made.

(5) Supplementary materials:

Table S2 and S3 appear to have been interchanged.

This has been corrected.

Ouyang et al: BioRXiv should be indicated.

This has been corrected.

(B) INDIVIDUAL SUPPLEMENTS:

(1) S1: enzymatic activity of GNBP1.

The number of independent experiments does not appear to be mentioned. With respect to the western blot shown in Figure 2A, it seems that the intensity of the band corresponding to activated ModSP is lower in lane 1 than in other lanes. The suggestion is to scan multiple blots to quantify the activation of this protein in different conditions. Do the authors know the nature of the high mobility band that appears solely when S. aureus peptidoglycan is added?

Regarding the lower intensity of the activated ModSP band in lane 1, a similar phenomenon has been reported in An evolutionarily conserved serine protease network mediates melanization and Toll activation in Drosophila (Fig. S2), where ModSP autoactivation was observed following incubation with PGRP-SA, GNBP1, and peptidoglycans. In current experimental design, the primary objective was to determine whether preincubation of peptidoglycans with GNBP1 further enhances ModSP activation. Therefore, our analysis focused on comparisons across different incubation time points rather than direct comparison with lane 1. Within this context, the lower intensity of the activated ModSP band in lane 1 is expected and does not affect the interpretation of the results

In response to the suggestion of scanning multiple blots for quantification, we note that no clear enhancement of ModSP autoactivation was observed across different incubation times. We also explored alternative incubation conditions, but none resulted in a detectable increase in activation. Thus, additional quantification would not change the overall conclusion.

(2) S2: Spirit

It would have been nice to display the spirit mRNA levels in the KO and KD mutants. Is the catalytic domain removed by the deletion and can the authors exclude a potential expression of a truncated Spirit from a cryptic translation initiation site upon leaky Gal4 expression of the transgene, hence the need for RTqPCR data using primers that map 3' to the transposon insertion?

We are using a deletion that remove all the Spirit isoforms that all start with the same ATG which was removed in the mutant, so it's very unlikely. There is an HSP70T = Terminator after the Gal4, which should exclude an initiation of translation after Gal4. However, we have verified the expected mutation by PCR.

Figure 2: Crystal cells appear to be present in spirit larvae. They, however, appear to be smaller, which may be difficult to measure. Quantification of the number of crystal cells is necessary.

We have removed this part in the revised version (Figure 2C and associated text) because it does not concern the assessed claims in Kambris et al et., 2006 that Spirit regulates the Toll pathway.

Figure 3: It is not clear if pooled data are presented for survival experiments.

Yes survivals show pooled data. We have updated figure legend to make this clearer.

(3) S4: Sphinx 1/2

In the absence of testing null mutant flies, the conclusion may be too strong. Can the authors totally exclude the expression of these proteases in a few cells? If they function as apical proteases, a minimal expression may be sufficient to trigger a proteolytic cascade.

To address the reviewer’s comments, we generated a deletion removing both sphinx 1 and sphinx 2 and analyzed Toll pathway activity in the absence of these two serine proteases. We find that flies lacking sphinx 1 and sphinx 2 exhibit wild-type induction of Drosomycin following M. luteus infection, as well as normal survival upon E. faecalis challenge. These new data provide strong evidence supporting our claim that, in contrast to our previous report (Kambris et al., 2006), Sphinx 1 and Sphinx 2 do not regulate the Toll pathway. Accordingly, we have replaced the earlier RNAi-based results with data obtained from loss-of-function mutants.

(4) S5: wntD

Figure 1, if any, appears to be missing.

Thank you for noticing this. This is now corrected Figure 2=>Figure 1 and Figure 3=> Figure

Fig. 3C-C': please, homogenize the color code with other panels (yw in blue and not suddenly in orange)

We have homogenized the color code in the revised version.

(5) S6-S7: Activation of Toll by overexpression of GNBP3 or protease genes The point is not framed appropriately: the overexpression studies were not intended to determine whether the overexpression of these genes activates the Toll pathway to levels of activation encountered during infection, but as tools for epistatic analysis, and in the case of S8, to identify novel protease genes that might be involved in Toll pathway activation. The results of the epistatic analysis are not disputed and, in some cases, have been validated by independent approaches (e.g., by hemolymph transfer experiments), and the hits of the protease screen have been validated by other laboratories, namely grass and SPE. In Figure S5B of Gottar et al, Cell, 2006, a level of only 30% of immunized was achieved, whereas it was about 70% in Figure 3A. Thus, the level of induction by overexpression of GNBP3 is variable but nevertheless sufficient for epistatic analysis both for Gottar et al. and for El Chamy et al., Nat. Immunol, 2008. Furthermore, levels of activation sufficient for epistatic analysis of Toll pathway activation or stimulation of the melanization proteolytic activation cascade upon the overexpression of either GNBP3 or GNBP1 together with PGRP-SA have been reached (Gobert et al., 2003; Gottar et al. 2006; El Chamy et al, 2008; Matskevich et al., Eur. J. Immunol., 2010). Thus, the overexpression of GNBP3 functions for genetic analysis purposes in two independent teams, that however, are working in the same research Unit. While one cannot exclude that enough peptidoglycan metabolites, e.g., TCT, are provided by the microbiota, it cannot be excluded that ß-(1-3)glucans might originate from the food or mycobiota, which may be distinct from that in the Reprosci laboratory. This illustrates the difficulty of controlling all parameters.

We fully agree that the notion that GNBP3 functions upstream of serine protease is validated. The point is that we cannot reproduce the observation that overexpression of GNBP3 trigger a strong Toll activation sufficient for epistatic analysis as shown in Gottar et al., 2006. The point is that ReproSci does not challenged any of the major claims of Gottar et al. 2006 but only a minor claim. The magnitude of gene induction relative to the unchallenged condition is an important consideration in the field of Drosophila immunity and can be misleading. For example, a gene described as being induced fivefold may appear significant, whereas the same gene can be induced up to 1,000-fold following infection. Therefore, absolute expression level compared to challenged level, rather than fold changes alone, should be carefully considered when interpreting immune gene activation.

We have done our studies with two different constructs. The observation that overexpression of a gene activate an immune pathway is by itself a result suggesting a concentration-dependent mode of activation. For instance, overexpression of ModSP is sufficient to activate the Toll pathway (Buchon 2009). This was not the case for GNBP3, even at low level. We cannot exclude that this could be the case in a specific background but at least not all background. Over-expression of GNBP3 is used in 3 panels of Gottar 2006 and this was a significant piece of data. On my side, my lab has lost significant amount of time to reproduce this without success.

Now we could be wrong in our assessment but we let the author of this study to show it.

To take in consideration Reviewer’s comment, we are softened our conclusions : ‘Overexpression of GNBP3 either ubiquitously or in the fat body does not effectively activate the Toll pathway’. At most, we find similar to (El Chamy et al., 2008) that overexpression may produce ‘weak but detectable’ activation of Toll’.

References:

Alphabetical order is not respected (Matskevich before Kim), and the Mishima reference is not optimal: it should be the JBC article in the same year that documents also the biochemistry of binding to ß-glucans.

We have done the changes in the revised version

(6) S8: PGRP-LE not in hemolymph

Fink et al., Mucosal Immunol. 2016 used the NP1-Gal4, which is not expressed in enteroendocrine cells, as stated in the text, but in enterocytes (and possibly the nervous system).

For controls, is the wild-type control the w[iso] Drosdel background?

Please provide the supplier of the GFP antibody.

We have addressed all the points in the revised version.

(7) S9: PGRP-LE and melanization

Figure 1D-E: A quantification would bolster the claim.

We agree that quantification of Figure 1D-E would reinforce the claims but we believe that our data are sufficient to state that PGRP-LE does not block the cuticular melanization upon septic injury (which is also consistent with an intracellular role). We have softened our conclusion.

(8) S10: PGRP-LE and bacillus

Please provide a description of the Bacillus subtilis strain.

This is a strain that derived from the Jean Lambert collection of Strasbourg and used in Lemaitre B PNAS 1997 (J.Millet and A. Klier, Pasteur Institute of Paris). We have checked the strain and confirm that it was indeed a B. subtilis strain that we name B subtillis FS.

It is not clear from the Mat & Meth whether the 2-3 independent replicates per genotype represent biological replicates in one experiment or correspond to several independent experiments. Are the pooled data displayed?

This information was on the methods. It has been copied to the figure caption.

(9) S11: DNAse II and regulation of AMP genes

The exact larval stage is not provided in S11, nor in the original study.

The experiment was done on wandering third-instar larvae as indicated in the material and methods

The number of flies for survival experiments is rather low, but this is not a major issue given the outcome of the experiment.

We agree with the reviewer.

What is the concentration of the injected DNA? As the solution was likely viscous, was the DNA sheared?

We have used a concentration of DNA of: 200 ng/ul, which is now indicated in the revised version of the Supplement. DNA was no sheared.

Figure 1A&D: A positive control of immunization would have been nice. 1D: At which time point was Diptericin expression measured by RTqPCR?

Unchallenged flies were used in Figure 1A while in Figure 1D Diptericin was measured 6 h after challenged. We agree that a bacterial challenge control would have been nice, but clearly the level of Diptericin in 1A corresponds to levels observed in unchallenged flies. Of note, we have tried several different concentrations, of more or less long "sizes" of DNA (short or very long fragments), and also different DNA sources (E. coli or Drosophila) but we did not see any effect on the activation of the Imd pathway.

DNAseII-deficient larvae have wild-type hemocyte numbers. His sub-title is not accurate as Figure 3 actually reports an INCREASED number of hemocytes in the DNase II mutant.

The reviewer is correct and we have adjusted the text.

(10) S12: JNK pathway and AMP gene expression

Hep RNAi lines and possibly also the Bsk-DN line should be validated by monitoring puckered mRNA levels after a stress that activates the JNK pathway. The absence of this control weakens the Reprosci conclusions.

As stated above, we are using standard Hep-RNAi and BskDN fly tools that have been validated in many studies.

Articles validating the HepRNAi (BDSC35210) can be found on this link. We have also validated the RNAi in new Figure 1 of Supplement S12.

Articles validating the BskDN (BDSC6409) can be found on this link

The Bloomington number of Hep RNAi was miss-annotated and has been corrected in the revised version

(11) S13: Caspar

There is clearly a trend for improved survival of the Caspar mutant in Figure 1A. Please, show the pooled data and appropriate statistical analysis. The legend to 1A mentions one overexpression strain that is not displayed and has likely not been performed because loft experiments were performed at 25{degree sign}C, whereas OE experiments should be performed at 29{degree sign}C, hence in separate experiments.

There was a mistake in the original figure legend when we mentioned the impact of overexpression of caspar on survival without showing the data (no effect was observed). The text has been removed in the revised version because it is not related to the claims we assessed from the Caspar article (Kim et al.,2006). To addressed reviewer’s comments, we now present the pooled data in Figure 1 of the revised Supplement S13. The conclusion is that we do not observe any increase host survival in caspar mutant related to wild-type consistent with our observation that the Imd pathway is not strikingly over-activated in absence of infection in caspar loss-of-function mutants.

Why was the c729-Gal4 driver chosen? Has it been validated as a bona fide fat body driver?

The use of c729-Gal4 was suggested by, and borrowed from, the laboratory of Prof. Gaiti Hasan, who had characterized and used it in adult fat body experiments (Subramanian M et al., 2013, Dis. Mod. & Mech). The BDSC number for the corresponding stock is BDSC_6983. Based on Flybase data, it is also expressed in somatic cells of male/female reproductive systems in the adult.

The RTqPCR experiments are not overwhelmingly convincing for a lack of data points: pooled data should be shown, inasmuch as there is a significant difference upon Caspar OE 6h after Ecc15 challenge.

We now show in the revised version of the Supplement S13 the pooled data from different experiments with individual points shown.

In conclusion and although our results are variable, they do not reproduce the results produced in the original article by (Kim et al., 2006) According to our results, we observe:

(1) no increase Dpt expression in absence of challenge both in caspar deficient larvae and adults.

(2) A possible inhibition of Dpt upon over-expression caspar at 6h in adult.

- A possible increased Dpt expression in caspar loss of function mutant larvae upon challenge.

The later may suggest an inhibition role upon overexpression of caspar that required further analysis. The text of the supplement has been amended to take all those points in consideration.

(12) S15: listericin

Introduction: The LLO (also referred to as hly) L. monocytogenes mutant does not prevent the entry of Listeria inside cells. The pore-forming toxin listeriolysin is required for pathogen escape from the phagosome.

There is no reference to LLO in the introduction of the S15 listericin section.

Has the STAT-92E RNAi line been validated? It is difficult to draw a definitive conclusion on the absence of the role of the JAK-STAT pathway in adults using an RNAi transgene because it may only imperfectly silence the expression of the target gene. "Contrary to Goto et al.2010, in our hands reduction of JAK-STAT activity through RNAi [...] in adult flies": Goto et al. apparently tested the JAK-STAT pathway only in S2 cells. This statement should therefore be modulated accordingly.

We have validated the STAT92 RNA in the revised version by confirming that Turandot gene expression is reduced in this mutant (Supplement 15 Figure 2 C-D). We have also validated the PGRP-LE¹¹² null mutant (Supplement 15 Figure 1C).

We have adjusted the conclusion: “Contrary to (Goto et al., 2010), we find that Listericin expression is not specifically dependent on PGRP-LE, and is not dependent on JAK-STAT signaling in flies. Of note, this could be the case in S2 cells where the initial experiments were done.

Antibacterial effects of listericin: It would be cautious not to rely solely on survival experiments, but also to monitor the bacterial titer to draw a definitive conclusion (assay used by Goto et al.). A control overexpressing GFP or a non-relevant peptide would have been welcome to control for potential metabolic effects that would decrease the effect of the overexpression. More importantly, Goto et al. used a Cg-Gal4 driver that is also expressed in hemocytes, which is likely not the case for the Lpp driver. Is it known if the c564 driver is also expressed in hemocytes and to the same level as the Cg-Gal4 driver?

We have used two fat body drivers to overexpress Listerin, Lpp and C564, the latter being expressed in hemocytes indeed. We agree that bacterial counting would provide a sensitive assay but in absence of any protective effect of Listericin overexpression, we do not expect any major titer change in L. monocytogenes growth. To reinforce our conclusion, we have generated Listericin null mutations (Fig 4C) and we have shown that they are not more susceptible than the wild-type to L. monocytogenes.

(13) S16: DSCAM1

The authors use an RNAi construct to knock down DSCAM1 expression. Which part of the transcripts is targeted? Did the authors verify that silencing was effective and would affect all DSCAM transcripts?

The DScam RNAI (BDSC #38945) that we are using has been used in other articles (link) and is validated in Kamiyama et al., Dev cell (Figure S4).

Data points should be shown in the figure.

Unfortunately, we could not address this point to the difficulty to reach the collaborator who provided the data.

Their conclusions would be strengthened by directly testing opsonization using the assay developed by Haller et al., EMBO Reports, 2018. Also, to derive the phagocytic index, the authors must have counted the number of hemocytes retrieved from bled larvae? Was there a decrease when DSCAM1 was silenced in hemocytes? The use of a hml-Gal4-Gal80ts driver would have allowed to bypass the issue of developmental effects.

We expect an opsonin to be abundant in the hemolymph but we did not find any secreted form of dScam in our proteomics analyses (Rommelaere 2024). 20 years after the publication of this landmark article in Science, the absence of any confirmation is puzzling and we are reluctant to do any additional experiment taking into consideration that phagocytosis assays are often variable.

(14) S18: SR-CI

The major issue with this supplement has been dealt with in the Public Review: no phagocytic receptor function was claimed in the Ramet et al, 2001 study.

We fully agree with the reviewer and with Mika Rämet and Monty Krieger (personal communication), and we apologize for this misunderstanding. In fact, Rämet et al. (2001) did not present data demonstrating a role for Sr-CI in phagocytosis per se in his article, but rather showed that this receptor is involved in bacterial binding. Our confusion arose from a subtitle in the Results section of their article (“SR-CI Binds Both Gram-Positive and Gram-Negative Bacteria and Is Necessary for Optimal Phagocytosis by S2 Cells”) and the article title that claim that Sr-CI is a pattern recognition receptor, which does not reflect the content of the article.

To clarify this point, we have revisited the original claim. Consistent with Rämet et al. (2001), we now observe a defect in hemocyte binding to bacteria in Sr-CI mutants. Thus, we validate the claim. Because Sr-CI is often assumed to function as a phagocytic receptor, we have also retained the experiments showing that it is not essential for the phagocytosis of E. coli or S. aureus. All experiments have been repeated during the revision process using a null single mutation and a double mutant removing both Sr-CI and Sr-CIII.

Introduction: Is it really adequate to mention a phagocytic receptor for a ligand, dsRNA, that gets endocytosed?

In the introduction, we summarized what is known on the Sr-CI, including its implication in the uptake of dsRNA. As suggested by the reviewer, we used the term endocytosis to refer to the ability to uptake dsRNA.

Methods: Have the authors excluded the potential off-target effect of CRISPR-Cas9 in other scavenger receptor genes? Monitoring their expression levels would also allow the detection of any compensatory effect in the null mutant by overexpression of other scavenger receptors.

We are now using two mutant lines: one carrying a frameshift mutation (SK6) that specifically affects Sr-CI, and another with a deletion removing both Sr-CI and Sr-CIII. We have carefully validated both mutations by genomic sequencing. As our results are now consistent with the original findings of Rämet et al. (2001), we believe that the analyses presented in the Supplementary Information are genetically well supported.

Results: Figure 1 is really confusing with so much variability in the data, which raises doubts about the reliability of the method. The reduction of the phagocytic index in B is not "mild". Again, one would like to see the individual data points and to know what the error bars are. For 1G, has any statistical analysis been performed? Finally, Panels A to G lack homogeneity in their presentation. Also, why are the absolute values of the y-axis varying so much from panel to panel (A-B vs C-D; E vs. F)?

We have repeated our experiments using a new set of mutants, both generated in the isogenic DrosDel background. In the revised version, we include additional experiments assessing the contribution of Sr-CI to hemocyte binding to bacteria. Consistent with the original report by Rämet et al. (2001), we observe similar results. We have revised the text accordingly and moderated our claims. In addition, we performed further biological replicates and now provide appropriate statistical analyses.

(15) S19: Undertaker

Undertaker has been identified through a deficiency screen that restricted the genomic zone of interest to eight genes. RNAi was then used to identify the candidate gene as being Undertaker. While an off-target effect of RNAi cannot be excluded, it cannot account for the results of the deficiency screen (junctophilin is on the second chromosome, whereas undertaker is on the third). The deficiency phenotype could be rescued by an Undertaker transgene. While overexpression can indeed provide a rescuing activity due to high levels of ectopic expression, why would it do so in the context of an 82F deficiency, unless this deficiency carries a second site mutation, which is a rather remote possibility.

Given that the deficiency line deletes at least 14 genes in a cluster, several of which are involved in growth and development, we assume that another gene(s) within the span of this deficiency is responsible for the effect on efferocytosis, or that some other mutation in the uncontrolled genetic background is responsible. The impact of Df(3R)3-4 on efferocytosis remains to be investigated.

The authors claim that Undertaker is not expressed at the right embryonic stage and hardly in S2 cells, which is correct according to large-scale data. However, Cuttell et al. successfully stained S2 cells with an antibody raised against retinophilin/undertaker by the investigators who studied the role of this gene in the eye (Mecklenburg et al., 2007). Should we trust more largescale datasets based on transcriptomics or a specially developed tool? (Both junctophilin and undertaker are at the limit of detection of the proteomic data available on FlyBase; equivalent signals in hemocytes were measured in FlyCellAtlas). Thus, the argument of the absence of expression is not definitive.

We agree on this but the expression pattern is an additional element that reinforce our conclusion. This is not the key element that relies on the use of loss-of-function mutation. Another element is the absence of follow-up study in the last 18 years.

The new phagocytosis data set generated by Reprosci shows an absence of impact of the undertaker loft mutation in larval hemocytes. Whether these data can be extrapolated to S2 cells, embryonic or adult hemocytes, remains debatable, as are the explanations put forth by Reprosci in their conclusion to explain by a possible off-target effect of RNAi on junctophilin. It would be interesting to determine the phenotype of junctophilin mutants in the ex vivo larval hemocyte assay.

We have analyzed the role of Undertaker using third instar larvae in an ex vivo assay and did not find any role in efferocytosis. I think that all our data and analysis of the literature is consistent with our statement that’ that undertaker is unlikely to have a role in phagocytosis’. Now, we can never exclude that Undertake may play a subtle role in this process. The role of Draper has been observed in larval hemocyte that represent macrophage of flies. We are using a null mutation in undertaker preventing the existence of off-targets. We have nuanced our conclusion in the article and add a sentence in the conclusion of the supplement: ‘We cannot however exclude that Undertaker play a role at a specific stage of development that we did not assess.’

(16) S20: Psidin

This supplement is duplicated

The duplicated supplement has been removed.

Phagocytosis assay: the authors use E. coli-GFP. How can they discriminate between internalization and simple binding at the surface of hemocytes? It would have been more appropriate to use a phalloidin, stained to another color rather than green. The suggestion here is to first use FITC-labeled bacteria, followed by Trypan blue treatment to quench the fluorescence of noninternalized bacteria. Second, pHrodo bacteria could be used to monitor the acidification of the phagosome in wt and psidin hemocytes.

We agree with the reviewer that this would be better. Because our observations are consistent with the data reported in this original article, we did not feel inclined to extend our analysis.

(17) S21: Hemese

The pie charts in Figure 1 would benefit from a statistical analysis. Why do the encapsulated eggs appear to be much larger in the hemese mutant? Could it be that more lamellocytes are recruited and make a thicker capsule? Should Figure 1C be imperatively quantified?

To extent our analysis, we generated two new Hemese null mutants, Hemese^JP187 and Hemese^JP828, carrying deletions in the central region of the gene. Using these lines, we show that wild-type and ^Hemese mutant larvae display comparable levels of lamellocytes and similar numbers of melanized capsules following wasp infestation. We further quantified lamellocyte differentiation and included appropriate statistical analyses. We have removed the previous results obtained with the Hemese^SK2 mutant, which yielded similar observations. By reproducing our previous findings with independent mutant lines and by providing quantitative analyses, we strengthen our conclusion that Hemese does not act as a negative regulator of lamellocyte differentiation upon wasp infestation.

(18) S22 IRC

IRC is actually not a catalase but a heme peroxidase. For the experiments on C. albicans, can the authors exclude that the IRC flies succumb because they are more sensitive to ethanol than wt or spz flies (sucrose is fermented by C. albicans): a control would be to use glycerol (nonfermentable) instead of sucrose solution.

We thank the reviewer and Carolina Barillas (personal communication) to inform us that IRC is not a catalase but an heme peroxidase. This is now included in the article and the supplement. It is clear that the name IRC for immune regulated catalase is misleading. We cannot exclude that the IRC flies succumb because they are more sensitive to ethanol than wt or spz flies but we did not test this interesting idea during the revision.

Do IRC mutants succumb to the ingestion of killed bacteria?

No, they get stuck in fly food and die.

(19) S23 DUOX

Introduction: When citing Kumar et al., the authors might also want to cite Bai et al. on the Bactrocera dorsalis peritrophic matrix.

This reference has been added

Results:

Figure 1: any statistical analysis? Data points are not shown for the lef panel, and error bars are not defined.

We have added in the revised version ‘When using the Mann-Whitney U test, we still observed a statistically significant difference in CFU counts at 6 hpi in Figure 2B, as well as at both 6 hpi and 24 hpi in Figure 2F. However, the magnitude of these differences is relatively small’. Error bars have been defined in the general revision of the supplements (see above).

Figure 2A shows only a limited reduction in Duox expression at the transcriptional level. "successfully" might be a bit of an overstatement.

We have removed the term ‘successfully’.

Figure 2E is too small.

We have increased the size of Figure 2E.

The authors might want to discuss the role of Duox in enterocytes destined to die as described by Amchelavsky et al., Cell Reports, 2020.

Good point, we have discussed this reference in the revised version.

The Sajjadian reference is incomplete.

The reference has been completed

(20) S24: NOS

Maybe the work from the Royet laboratory could be cited along with that of Neyen et al. and Zaidmann-Remy et al. in the Introduction.

Good points. We have added two references related to the work of the Royet lab (Bosco-Drayon et al., 2012; Charroux et al., 2017).

It is not clear from Rabinovich et al. (2016) which line should be the relevant wild-type control. Why use w[1118] in Figure 1 and Ore-R in Figure 2? A more definitive conclusion could be reached upon isogenization or testing a second null mutant in homozygous and transheterozygous conditions?

We agree that ideally, we should have used isogenic wild-type control but in absence of any effect of NOS mutants, we consider that the use of w[1118] and Oregon wild-type control is acceptable, considering that they behave similarly in the assay we have used.

(21) S25 eiger survival

Survival experiments: Are pooled data shown? Have the authors monitored the health status of their fly lines? In some of the survivals with late phenotypes, e.g., egr mutants and E. faecalis, this may be an issue, inasmuch as noninfected or mock-infected controls are not shown (have they been performed?).

The survival analysis showed the pooled of 40 flies and were often done with two sexes. They also include many controls. We cannot never exclude minor effects at late time points, but the critical message is that we cannot reproduced the previously published results.

The survival graphs are difficult to analyze: the authors should definitely avoid light colors such as yellow that do not show up well in a white background.

As stated above, these experiments were done by many scientists in different lab and it was difficult to homogenize the data. Therefore, we did not modify our graphs although we agree with the reviewers. We believe that line patterns and contrast differences between groups guarantee that the readers can still assess the data.

(22) S27: eiger humoral response

Introduction: Have the authors also checked the Flysickseq data from the Buchon lab?

There is no induction of eiger in Flysick. This information along with the reference Troha et al., have been added to S27.

Methods: Have the RNAi lines been validated, and how? Is one more efficient at silencing than the other? This set of data would complement Figure 1 with RTqPCR experiments.

The two RNAi lines we are using have already been used in many studies assessing the function of eiger ((#108814, reference here, #45253 reference here)

Figure 3 colors in survival graphs: see S25.

We did not modify our graphs although we agree with the reviewers. By increasing the magnification, the readers can still assess the data. As stated above, these experiments were done by many scientists in different labs and it was difficult to homogenize the data.

Would it have been worth to also test the transheterozygous Gr28b mutants to avoid any issue of second-site mutations?

We could have extended the genetics approach but, given that both us and another group (Sang) found no effect on feeding in an independent mutant, and extremely high feeding in the claimed 'anorexic' mutant, this would not be relevant to the claim. Future study may tell us if Gr28b has clearly a feeding phenotype.

Reviewer #2 (Recommendations for the authors):

(1) Adjust the discussion to better contextualize subjectivity: Because the choice of claims and papers inevitably involves subjective decisions, consider expanding the discussion to acknowledge this limitation more explicitly and explain how the companion metascience manuscript complements this work.

We have added a section at the end of the discussion to discuss the limitation of our study and we establish more link to the companion article.

(2) Refine language and avoid binary judgments: Terms such as "correct," "incorrect," or similar definitive formulations should be softened. Emphasizing uncertainty and openness to future revision will better reflect the iterative nature of scientific inquiry.

We are softening our language in several of our assessment to avoid binary judgement.

(3) Highlight reproducible findings as well: While the focus on irreproducible or challenged claims is understandable, it may be helpful to balance this by more clearly acknowledging wellsupported claims or areas of strong reproducibility to reinforce the positive impact of robust findings.

We have added two sentences at the end of the introduction and at the beginning of the discussion that most claims are reproducible and that we have focused here on nonreproducible claim.

(4) Clarify how the community can engage with the dataset: Because you provide extensive supplementary material and a large online resource, consider adding more explicit guidance on how researchers can contribute comments, evidence, or corrections, and how these contributions will be integrated.

This point is already addressed in the revised sentence: “We hope that the community-accessible website will encourage researchers to share their perspectives and contribute data from diverse sources, thereby improving objectivity.” In addition, we have proactively engaged with principal investigators to motivate them to contribute to this effort by sharing unpublished results and information. However, it remains unclear to what extent scientists are genuinely interested in reproducibility, as has been noted in other studies on the topic. For example, articles that challenge previous findings are often under-cited, and the presence of contradictory evidence does not necessarily prevent researchers from continuing to cite the original claims. This is clearly a challenge of reproducibility study. Comments, evidence and corrections will be integrated in the ReproSci website. We have already updated this database when revising this article and will continue to do it.

(5) Resolve the date-range inconsistency: The Introduction mentions analysis of papers from 1959-2011, whereas the Methods section cites 1940-2011. This discrepancy should be corrected for consistency.

We have solved this discrepancy by correcting the method section. This should be 1959-2011. Thank you for spotting this mistake.

Reviewer #4 (Recommendations for the authors):

(1) The "disclaimer" subsection should be incorporated into the Introduction, as it is central to the premise of the study.

The disclaimer has been moved at the end of the introduction and one sentence has been added in the abstract.

(2) The inconsistency of graphical representation and statistical analysis of survival and gene expression data across different supplements is distracting and makes the project feel cobbled together. A consistent and unified framework for analysis and presentation would feel more cohesive and rigorous.

The experiments were conducted across multiple laboratories and required substantial coordination. As a result, modifying the graphs at this stage would be technically complex and would require monumental effort for a tiny return. Therefore, we regret that we were unable to implement this change. The most important is that data and analyses are presented transparently, allowing readers to evaluate and interpret the results independently.

(3) The purported roles of eiger and Gr28b in immunity have nothing to do with each other, aside from both having been published by David Schneider's group. I would suggest not combining them into a single section unless there is to be a 'miscellaneous' section that contains work by multiple groups.

We have done two separate sections.

(4) It would be easier to comment on specific passages in the manuscript if line numbers had been included.

Sorry for this. We have included number of lines in the revised version.

(5) The use of the word "elegant" to describe melanization reactions on page 3 is a bit odd and feels out of place.

It has been removed

(6) The sentence "We conclude that PGRP-LE is an exclusively intracellular sensor, with a prominent role regulating the gut immune response (Bosco-Drayon et al., 2012; Neyen et al., 2012)" should be edited to read "as reported in (citations)".

We have edited the sentence.

(7) The sentence "Experiments performed for ReproSci and review of the literature suggest that JNK is unlikely to have a strong direct or systematic role in the regulation of Drosophila AMPs in vivo, and is not required in the adult fat body for AMP expression in response to infection (Supplementary S12)" lacks detail. I realize that the experiments are described in S12, but I would suggest a brief summary in the main text of the article as well.

We have provided more information in the article.

(8) The phrasing of "While many of the challenged claims discussed in this paper are known to be controversial by experts, or have fallen quietly out of current research interests, some are still a source of confusion. This is particularly true for young scientists new to the field of Drosophila immunity or scientists with primary interests outside of Drosophila immunity that use the field as a reference." could be edited for clarity. A more direct phrasing could help, such as "Even in the absence of published refutation, many of the challenged claims were already considered controversial by experts in the field. Others have quietly fallen out of the general current research interest. These may nevertheless still be a source of confusion for young scientists new to the field of Drosophila immunity or scientists with primary interests outside of Drosophila immunity that use the field as a reference."

We have changed the sentence accordingly.

(9) On Discussion page 15, the comma should be removed from "In this article we have not discussed a number of claims, that had no clear follow-up studies and remain unchallenged."

The coma has been removed.

(10) In Methods, the authors "acknowledge that our verification experiments could also be erroneous". It would be appropriate to also include such a disclaimer in the Introduction and/or Discussion.

The disclaimer has been moved at the end of the introduction and one sentence has been added in the abstract.

eLife Assessment

This important study presents an impressive large-scale effort to assess the reproducibility of published findings in the field of Drosophila immunity. The authors analyse 400 papers published between 1959 and 2011 and assess how many of the claims in these papers have been tested in subsequent publications. In a companion article they report the results of experiments to test a subset of the claims that, according to the literature, have not been tested. The evidence presented is convincing, and the limitations inherent to evaluating reproducibility primarily on the basis of the published literature - as opposed to repeating experiments - are acknowledged. The authors also explore if various factors related to authors, institutions and journals influence reproducibility in this field: in general, most correlations between these factors and reproducibility are weak, and some are dependent on analysis choices.

Reviewer #1 (Public review):

Summary:

The authors set out on the ambitious task of establishing the reproducibility of claims from the Drosophila immunity literature. Starting out from a corpus of 400 articles from 1959 and 2011, the authors sought to determine whether their claims were confirmed or contradicted by previous or subsequent publications. Additionally, they actively sought to replicate a subset of the claims for which no previous replications were available (although this set was not necessarily representative of the whole sample, as the authors focused on suspicious and/or easily testable claims). The focus of the article is on inferential reproducibility; thus, methods don't necessarily map exactly to the original ones.

The article is a large-scale analysis of the individual replication findings, which are presented in a companion article (Westlake et al. doi.org/10.1101/2025.07.07.663442). In their retrospective analysis, the authors find that 61% of the original claims were verified by the literature, 7.5% were partially verified, and only 6.8% was challenged, with 23.8% having no replication available. This is in stark contrast with the result of their prospective replications, in which only 16% of claims were successfully reproduced.

The authors proceed to investigate correlates of replicability, with the most consistent finding being that findings stemming from higher-ranked universities were more likely to be challenged - a finding that is observed in a multivariable model and multiple sensitivity analyses. Other trends observed in the initial descriptive analysis, such as less replicability in findings from "trophy" journals and duration of engagement with the field, seem less consistent and fail to reach significance in the multivariable model, and should thus be considered tentative.

Although this is a major contribution to the field, it is important to note that the high replication rates are mostly based on a retrospective survey of the literature, while prospective replication rates in the subset of articles directly replicated by the authors were much lower. Thus, the possibility of biases relating both to the field's decisions about what to replicate (and what to publish) and to the authors' criteria in evaluating claims should be considered when comparing these results with prospective replicability estimates obtained in other fields of science.

Strengths:

The work presents a large-scale, in-depth analysis of a particular field of science that includes authors with deep domain expertise of the field. This is a rare endeavour to establish the reproducibility of a particular subfield of science, and I'd argue that we need many more of these in different areas.

The project was built on a collaborative basis (https://ReproSci.epfl.ch/), using an online database (https://ReproSci.epfl.ch/), which was used to organize the annotations and comments of the community about the claims. The website remains online and can be a valuable resource to the Drosophila immunity community. A companion article details the individual replication findings (Westlake et al. doi.org/10.1101/2025.07.07.663442).

The revised version of the preprint includes a number of sensitivity analyses as supplementary material, which help to evaluate how the main findings change according to analytical decisions.

Main concerns:

(1) Although a number sensitivity analyses have now been conducted in order to address reviewer comments, these have been relegated to the supplementary material. Their existence is acknowledged in the multivariable model section, but the actual results of the main analysis are not mentioned at all in the main text and not taken into account in the discussion. Thus, the casual reader is not made aware of how particular results are dependent on analysis choices.<br /> Although the main finding of the correlation between replicability and university ranking holds over nearly all the analyses conducted, others are not as consistent. The association of irreplicability with trophy journals, for instance, is not statistically significant in the multivariate model (suggesting that it may have been partially due to confounding of journal tier with institutional ranking). It becomes even weaker when unchallenged claims are removed from the analysis (see point 2 below). Similarly, the association of irreplicability with "exploratory" career style is already weak in the univariate analysis and becomes even more marginal in the multivariable model. The effect of the lead author having been a first author in the field, on the other hand, is stronger than that of journal impact factor or that of the continuity/exploratory style (even though it fails to reach formal significance), but seems to receive less attention in the discussion.<br /> These differences in strength of evidence could be made more clear both in the abstract and in the discussion, which seem to prioritize some trends over others when discussing results. Once more, presenting a brief description of how results are affected by the sensitivity analyses in the results would be important to make these nuances clearer to the reader.

(2) I still do not understand the authors' choice of including unchallenged claims along with verified ones in the multivariate model used to investigate predictors of replicability. In particular, the justification given for this choice in the supplementary material (i.e. the fact that a finding remaining unchallenged is not a random event and might be influenced by variables such as journal tier and institutional ranking) actually seems like an additional reason for not including unchallenged claims along with verified ones: if findings from low-tier journals or less prestigious institutions are more likely to remain unchallenged, this could lead to a spurious claim of "less irreplicability" in these journals and institutions, which could be purely due to receiving less attention. Predictably, both associations are reduced when unchallenged claims are removed (although the reduction is much more marked in the journal case) in the sensitivity analysis (whose results, again, are only mentioned in the supplementary material).<br /> Moreover, multiple other statements by the authors themselves concerning unchallenged claims seem to contradict their own decision. In multiple points in the text, they reiterate that remaining unchallenged is associated with less replicability (as suggested by the fact that replicability rates were lower in prospective replications than in the literature, even for non-suspicious claims). The decision to include unchallenged claims along with verified ones thus seems unjustified - if anything, I'd have expected the opposite approach after reading the discussion. That said, I'd argue that the best decision would be to exclude them from the analysis, as done in Figure S4, and presenting this model as the main one.

Reviewer #3 (Public review):

Summary:

The authors of this paper were trying to identify how reproducible, or not, their subfield (Drosophila immunity) was since its inception over 50 years ago. This required identifying not only the papers, but the specific claims made in the paper, assessing if these claims were followed up in the literature, and if so whether they supported or refuted the original claim. In addition to this large manually curated effort, the authors further investigated some claims that were left unchallenged in the literature by conducting replications themselves. This provided a rich corpus of the subfield that could be investigated into what characteristics influence reproducibility.

A major strength of this study is the focus on a subfield, the detailing of identifying the main, major, and minor claims - which is a very challenging manual task - and then cataloging not only their assessment of if these claims were followed up in the literature, but also what characteristics might be contributing to reproducibility, which also included more manual effort to supplement the data that they were able to extract from the published papers. While this provides a rich dataset for analysis, there is a major weakness with this approach, which is not unique to this study.

The main weakness is relying heavily on the published literature as the source of whether a claim was determined to be verified or not. Nonetheless it is understandable why the authors took this approach - it is the only way to get at a breadth of the literature. However, there are many documented issues with this stemming from every field of research - such as publication bias, selective reporting, all the way to fraud. Importantly, this limitation is highlighted throughout the paper. At the same time, it is not reasonable to expect this study to have conducted independent experimental replications for all 400 papers identified as this would have been a laborious and costly effort. To overcome this weakness, the authors leveraged their own expertise, and crowdsourcing within the Drosophila immunity community, to assess the validity of the claims. While this helps mitigate some of this weakness, it does introduce new challenges in interpretation, which is acknowledged in the limitations section of the discussion. Overall, this situates this study more as an expert assessment of the replicability of the published literature opposed to an assessment of independent experimental replications.

The authors should be applauded for the monumental effort they put into this project, which does a wonderful job of having experts within a subfield engage their community to understand the connectiveness of the literature and attempt to understand how reliable specific results are and what factors might contribute to them. This project provides a nice blueprint for others to build from as well as leverage the data generated from this subfield and thus should have an impact in the broader discussion on reproducibility and reliability of research evidence.

Author response:

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

eLife Assessment:

This important study presents an impressive large-scale effort to assess the reproducibility of published findings in the field of Drosophila immunity. The authors analyse 400 papers published between 1959 and 2011, and assess how many of the claims in these papers have been tested in subsequent publications. In a companion article they report the results of experiments to test a subset of the claims that, according to the literature, have not been tested. The present article also explores if various factors related to authors, institutions and journals influence reproducibility in this field. The evidence supporting the claims is solid, but there is considerable scope for strengthening and extending the analysis. The limitations inherent to evaluating reproducibility based on the published literature should also be acknowledged.

We have included in the abstract the limitation of evaluating replicability based on the published literature

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors set out on the ambitious task of establishing the reproducibility of claims from the Drosophila immunity literature. Starting out from a corpus of 400 articles from 1959 and 2011, the authors sought to determine whether their claims were confirmed or contradicted by previous or subsequent publications. Additionally, they actively sought to replicate a subset of the claims for which no previous replications were available (although this set was not representative of the whole sample, as the authors focused on suspicious and/or easily testable claims). The focus of the article is on inferential reproducibility; thus, methods don't necessarily map exactly to the original ones.

The authors present a large-scale analysis of the individual replication findings, which are presented in a companion article (Westlake et al., 2025. DOI 10.1101/2025.07.07.663442). In their retrospective analysis of reproducibility, the authors find that 61% of the original claims were verified by the literature, 7.5% were partialy verified, and only 6.8% were challenged, with 23.8% having no replication available. This is in stark contrast with the result of their prospective replications, in which only 16% of claims were successfully reproduced. The authors proceed to investigate correlates of replicability, with the most consistent finding being that findings stemming from higher-ranked universities (and possibly from very high impact journals) were more likely to be challenged.

Strengths:

(1) The work presents a large-scale, in-depth analysis of a particular field of science that includes authors with deep domain expertise of the field. This is a rare endeavour to establish the reproducibility of a particular subfield of science, and I'd argue that we need many more of these in different areas.

(2) The project was built on a collaborative basis (https://ReproSci.epfl.ch/), using an online database (https://ReproSci.epfl.ch/), which was used to organize the annotations and comments of the community about the claims. The website remains online and can be a valuable resource to the Drosophila immunity community.

(3) Data and code are shared in the authors' GitHub repository, with a Jupyter notebook available to reproduce the results.

We thank the reviewer for their positive comments.

Main concerns:

(1) Although the authors claim that "Drosophila immunity claims are mostly replicable", this conclusion is strictly based on the retrospective analysis - in which around 84% of the claims for which a published verification attempt was found. This is in very stark contrast with the findings that the authors replicate prospectively, of which only 16% are verified. Although this large discrepancy may be explained by the fact that the authors focused on unchallenged and suspicious claims (which seems to be their preferred explanation), an alternative hypothesis is that there is a large amount of confirmation bias in the Drosophila immunity literature, either because attempts to replicate previous findings tend to reach similar results due to researcher bias, or because results that validate previous findings are more likely to be published.

Both explanations are plausible (and, not being an expert in the field, I'd have a hard time estimating their relative probability), and in the absence of prospective replication of a systematic sample of claims - which could determine whether the replication rate for a random sample of claims is as high as that observed in the literature -, both should be considered in the manuscript.

I still believe that most of ‘verified’ claims are indeed solid, consistent with the feeling of increased knowledge in the Drosophila immunity. Of note, when I started in the field in the early 90, nearly all the articles in Drosophila developmental biology, the dominant field at that time, were solid. I agree that this may represent a past period. Still, perceived irreproducibility is high because affecting claims published in high-impact articles. To address the reviewer’s comments, we have included the possibility of confirmation bias in the discussion of the article.

(2) The fact that the analysis of factors correlating with reproducibility includes both prospective and retrospective replications also leads to the possibility of confusion bias in this analysis. If most of the challenged claims come from the authors' prospective replications, while most of the verified ones come from those that were replicated by the literature, it becomes unclear whether the identified factors are correlated with actual reproducibility of the claims or with the likelihood that a given claim will be tested by other authors and that this replication will be published.

We agree that the ReproSci is a human biased endeavor and may be subjected to bias, notably the one mentioned. Some verified claims might be considered as challenged and some challenged claims as verified. But this is likely not affecting most of our results. Our papers have been posted on a public archive and that the community could scrutinize our data (most authors have checked their claims!). Based on community feedback, we have had to change the status of three claims only: one verified claim became challenged, one challenged claim became unchallenged and one unchallenged became verified. We therefore did not expect major changes in our conclusions. We have provided an estimation of irreproducibility ranging from 10-20% and we believe this is a rather safe interval. This is still significant. The fact that the ReproSci project is a human endeavor, and therefore subject to inherent limitations, is already emphasized in the last section of the discussion.

(3) The methods are very brief for a project of this size, and many of the aspects in determining whether claims were conceptually replicated and how replications were set up are missing.

Some of these - such as the PubMed search string for the publications and a better description of the annotation process - are described in the companion article, but this could be more explicitly stated. Others, however, remain obscure. Statements such as "Claims were cross-checked with evidence from previous, contemporary and subsequent publications and assigned a verification category" summarize a very complex process for which more detail should be given - in particular because what constitutes inferential reproducibility is not a self-evident concept. And although I appreciate that what constitutes a replication is ultimately a case-by-case decision, a general description of the guidelines used by the authors to determine this should be provided. As these processes were done by one author and reviewed by another, it would also be useful to know the agreement rates between them to have a general sense of how reproducible the annotation process might be.

The same gap in methods descriptions holds for the prospective replications. How were labs selected, how were experimental protocols developed, and how was the validity of the experiments as a conceptual replication assessed? I understand that providing the methods for each individual replication is beyond the scope of the article, but a general description of how they were developed would be important.

We have extended the first section of the Result to mention that an extended Material and Methods can be found in the complementary article Westlake et al., eLife 2026 and on the ReproSci website indicated the resources described in the companion articles. Disagreement between the two authors were limited and mostly dealt with textual interpretation (the definition of the major claims, which can affect if they are verified or not). As mentioned above, our articles are now public since more 6 months and we got little request to change the status of a claim (only 3 over more than 1000). Of note many claims from some ancient articles are part of the common knowledge, are verified routinely by many labs in the field, and therefore were easy to categorize.

We also added a sentence to also underline that the scientific value of an article does not fully correlate with its status. A number of problematic articles filled with exaggeration or confused claims were still categorized as verified. Thus, we screen for replicability but they are many other publication issues we could not capture in our study. This point is now mentioned in the discussion.

(4) As far as I could tell, the large-scale analysis of the replication results was not preregistered, and many decisions seem somewhat ad hoc. In particular, the categorization of journals (e.g. low impact, high impact, "trophy") and universities (e.g. top 50, 51-100, 101+) relies on arbitrary thresholds, and it is unclear how much the results are dependent on these decisions, as no sensitivity analyses are provided.

Particularly, for analyses that correlate reproducibility with continuous variable (such as year of publication, impact factor or university ranking, I'd strongly favor using these variables as continuous variables in the analysis (e.g. using logistic regression) rather than performing pairwise comparisons between categories determined by arbitrary cutoffs. This would not only reduce the impact of arbitrary thresholds in the analysis, but would also increase statistical power in the univariate analyses (as the whole sample can be used in at once) and reduce the number of parameters in the multivariate model (as they will be included as a single variable rather than multiple dummy variables when there are more than two categories).

We did not pre-registered our study, which is quite different from other reproducibility projects. We did not know at the start how the project would unfold. Of note, I believe that ‘cleaning’ an extensive field by experts was by itself an achievement and represent another way to assess replicability, with its own limitation.

We agree that the cut-off can be seen as arbitrary. However, publication year has been modeled as a continuous variable through a spline (to allow for non-linearity) in the multivariate analysis. For journal and institutional ranking, we would like to defend and keep the categorical specifications in the main text for two reasons:

- Institution ranking: For institutional ranking, the largest institutional category is “Not Ranked” which we cannot assign a rank and ranks institutions individually only through the top 100. Below that it publishes bands (101-150, 151-200, 201-300, 301400, 401-500) of variable width, which are not straightforward to use continuously without making strong assumptions (e.g midpoint) unsupported by the data.

- Prestige: As mentioned by another reviewer there are career consequences attached to Nature, Science and Cell that are different from other journal, and the effect of moving from a journal from an IF 3 to 8 is different than from 30 to 35. We provide a sensitivity analysis in the supplementary information where we refit the multivariate model with log-transformed impact factor continuous predictor. We obtain very similar results than these in the main text, with the exception that the impact factor of the journal becomes significant. We describe and discuss this results in the supplementary information (section S5), while justifying why we keep the categorical model in the main text.

We are grateful to the reviewer for prompting these additions, which we agree strengthen the paper.

The text added in the SI states:

“As a sensitivity analysis, we refitted the multivariable hierarchical logistic model by replacing journal-impact-factor categories with log₂-transformed continuous impact factor, while retaining all other covariates and random intercepts from the primary analysis. University ranking was retained as a categorical variable because the 2010 Shanghai Academic Ranking reports individual ranks only for institutions ranked 1– 100 and otherwise reports rank bands (101–150, 151–200, 201–300, 301–400, and 401–500); moreover, 441 of 1,006 claims (43.8%) were from unranked institutions, which constitute a distinct group.

Each doubling of journal impact factor was associated with 1.51-fold higher odds that a claim was challenged (OR 1.51, 94% HDI 1.13–2.08). At the mean impact factors of the low-impact and trophy-journal tiers (4.4 and 61, respectively; approximately 3.8 doublings), the continuous model implies a trophy-versus-low-impact odds ratio of approximately 4.8. By contrast, the primary model directly estimated the trophy-versus-low-impact odds ratio as 1.75 (94% HDI 0.59–4.91). Although this wide interval includes 4.8, the point estimates differ between the two models. We interpret the larger implied trophy-journal effect in the continuous model cautiously because it assumes that the log-linear slope estimated predominantly from the many journals with lower impact factors (around 2–12) applies unchanged to the sparsely represented trophy journals (62 claims across Science, Nature, and Cell). We therefore retained the categorical journal analysis as the primary analysis because it directly estimates the trophy-journal comparison using claims published in those journals. Estimates for all other covariates were broadly similar to those in the primary model. In particular, the association with Top 50 university affiliation remained evident (OR 4.04, 94% HDI 1.57–10.08, compared with OR 3.68, 94% HDI 1.50–9.28 in the primary model)”.

[This response is referred later as “Response to categorical variable encoding”]

(5) The multivariate model used to investigate predictors of replicability includes unchallenged claims along with verified ones in the outcome, which seems like an odd decision. If the intention is to analyze which factors are correlated with reproducibility, it would make more sense to remove the unchallenged findings, as these are likely uninformative in this sense. In fact, based on the authors' own replications of unchallenged findings, they may be more likely to belong the "challenged" category than to the "unchallenged" one if they were to be verified.

We thank the reviewer for raising this comment, we agree that the classification of the unchallenged claims as not challenged is difficult given their nature. We refitted the multivariable analysis excluding unchallenged claims, with a classification of Challenged and Unchallenged (Verified, Partially Verified, Mixed). The results are shown in the supplementary section S4 and are extremely similar to the main model.

The text added in the SI states:

“We fit the multivariate model from the main text while excluding unchallenged claims from the analysis. The methods are similar and the convergence and diagnosis checks are good and not reported here for brevity. The model simultaneously adjusts for author demographics, laboratory attributes and journal or institutional prestige and predict a binary outcome for each claim: challenged or not challenged (including Verified, Partially Verified, Mixed). The re-analysis included 659 claims, of which 60 (9.1%) were challenged. The non-challenged reference group comprised of Verified (n=525), Partially Verified (n=64), Mixed (n=10). The Adjusted odds ratios and 94% highest-density intervals are reported in Figure S4. The results are very similar to the analysis with the unchallenged claims in the main text, with only university ranking (Top 50) being a significant predictor (OR 3.34 (1.28–9.01) vs the main text OR 3.68 (94% HDI 1.50– 9.28). The other variable with the biggest changes shows only modest differences:

- High-impact journal OR 1.12 (vs 1.31)

- Trophy journal OR 1.47 (vs 1.75)

- Post-doc OR 1.44 (vs 1.16) and their intervals still include 1. Note that the excluding unchallenged decision condition on follow-up, which is not random and might be influenced by our key variable (journal tier, institutional ranking) and bias results for this model.”

However, we did not replace the main model of the article by this particular model because when you chose only claim that are either verified or challenged (so you exclude unchallenged), the condition that made these claims included in this analysis could be influenced by a cofactor, so our odds ratios might be wrong.

[This response is referred later as “Response to unchallenged exclusion”]

Reviewer #2 (Public review):

Summary:

Lemaitre et al. conducted an analysis of 400 publications in the Drosophila immunity field (1959-2011), performing both univariable and multivariable analyses to identify factors that correlate with or influence the irreproducibility of scientific claims. Some of the findings are unexpected, for instance, neither the career stage of the PI nor that of the first author appears to matter that much, while others, such as the influence of institutional prestige or publication in "trophy journals," are more predictable. The results provide valuable insight into patterns of irreproducibility in academia and may help inform policies to improve research reproducibility in the field.

Strengths:

This study is based on a large, manually curated dataset, complemented by a companion paper (Westlake et al., 2025. DOI 10.1101/2025.07.07.663442) that provides additional details on experimentally documented cases. The statistical methods are appropriate, and the findings are both important and informative. The results are clearly presented and supported by accessible documentation through the ReproSci project.

We thank the reviewer for their assessment.

Weaknesses:

The analysis is limited to a specific field (immunity) and model system (Drosophila). Since biological context may influence reproducibility -- for example, depending on whether mechanisms are more hardwired or variable -- and the model system itself may contribute to these effects (as the authors note), it remains unclear to what extent these findings generalize to other fields or organisms. The authors could expand the discussion to address the potential scope and limitations of the study's generalizability.

We have added a limitation section at the end of the manuscript to discuss these points. We wrote:

“Finally, the findings we report may be specific to a particular field, model organism, and time period, and may be strongly influenced by factors idiosyncratic to their development. Because this analysis is limited to a single field (immunity) and model system (Drosophila), it remains unclear to what extent these findings generalize to other fields, organisms, or more recent studies.”

However, we believe that our study adds on the discussion on reproducibility by providing another approach. Our study also aligns with the feeling that knowledge of Drosophila innate immunity has increased so much in the last decades, and that science is still quite robust in many fields.

Reviewer #3 (Public review):

Summary:

The authors of this paper were trying to identify how reproducible, or not, their subfield (Drosophila immunity) was since its inception over 50 years ago. This required identifying not only the papers, but the specific claims made in the paper, assessing if these claims were followed up in the literature, and if so whether the subsequent papers supported or refuted the original claim. In addition to this large manually curated effort, the authors further investigated some claims that were left unchallenged in the literature by conducting replications themselves. This provided a rich corpus of the subfield that could be investigated into what characteristics influence reproducibility.

Strengths:

A major strength of this study is the focus on a subfield, the detailing of identifying the main, major, and minor claims - which is a very challenging manual task - and then cataloging not only their assessment of if these claims were followed up in the literature, but also what characteristics might be contributing to reproducibility, which also included more manual effort to supplement the data that they were able to extract from the published papers. While this provides a rich dataset for analysis, there is a major weakness with this approach, which is not unique to this study.

Weaknesses:

The main weakness is relying heavily on the published literature as the source for if a claim was determined to be verified or not. There are many documented issues with this stemming from every field of research - such as publication bias, selective reporting, all the way to fraud. It's understandable why the authors took this approach - it is the only way to get at a breadth of the literature - however the flaw with this approach is it takes the literature as a solid ground truth, which it is not. At the same time, it is not reasonable to expect the authors to have conducted independent replications for all of the 400 papers they identified.

However, there is a big difference trying to assess the reproducibility of the literature by using the literature as the 'ground truth' vs doing this independently like other large-scale replication projects have attempted to do. This means the interpretation of the data is a bit challenging.

We acknowledge that our analysis necessarily relies on the published literature; however, two important points should be considered. First, we assessed replicability more than a decade after the original studies, allowing us to evaluate whether their claims have withstood subsequent scrutiny. Second, the evaluation draws on the authors’ strong expertise in the field. Accordingly, the validity of published claims was not accepted uncritically but subjected to informed expert assessment. This is exemplified by the case of the proposed microbicidal role of Duox, which we classified as challenged despite the original article accumulating more than 600 citations.

Overall, our replicability analysis, like similar efforts, relies not only on literature but also on expert judgment. Of course it has inherent limitations, which are now more clearly articulated in the discussion.

Below are suggestions for the authors and readers to consider:

(1) I understand why the authors prefer to mention claims as their primary means of reporting what they found, but it is nested within paper, and that makes it very hard to understand how to interpret these results at times. I also cannot understand at the high-level the relationship between claims and papers. The methods suggest there are 3-4 major claims per paper, but at 400 papers and 1,006 claims, this averages to ~2.5 claims per paper. Can the authors consider describing this relationship better (e.g., distribution of claims and papers) and/or considering presenting the data two ways (primary figures as claims and complimentary supplementary figures with papers as the unit). This will help the reader interpret the data both ways without confusion. I am also curious how the results look when presented both ways (e.g., does shifting to the paper as the unit of analysis shift the figures and interpretation?). This is especially true since the first and last author analysis shows there is varying distribution of papers and claims by authors (and thus the relationship between these is important for the reader).

Articles can contain claims that we found replicable and other that we did not. Thus, we believe than an evaluation by claim is more precise. The extraction of the different claims relies on the reading of the article, but is a human enterprise. There are clearly some unavoidable biases at this step. Of note, the articles analyzed in this study are very different one from another (size, novelty, amount of data…).

However, we agree that the analysis at the article level is interesting, and we followed the reviewer suggestion and provided in Supplementary Section S6 a sensitivity analysis of using article-level effects for the multivariate analysis. We note that because only 43 articles (12.5%) contained at least one challenged claim, this analysis is less robust than the claim analysis. The text added in the SI states:

“Two claims in the same paper might not be independent, so we might want to incorporate an article random effect to the primary Bayesian formulation. However, due to the low number of claim per article (mostly one to four) and only 43 articles (12.5%) contained at least one challenged claim (and most articles contains only one to four claims), we could not manage to fit this model properly (we observe MCMC divergences). As a work-around sensitivity analysis, we repeated the analysis with the article as the unit. Each of 345 articles with complete covariate data (representing 869 major claims, 60 of the 69 challenged claims in the full dataset; the remaining 9 fell in articles excluded for missing covariates) contributed as outcome the proportion of its major claims classified as challenged. The model was a (frequentist) binomial-link fractional-response generalized linear model with HC3 standard errors (the intervals reported here are 94% confidence intervals rather than posterior credible intervals).

Each article contributed equally regardless of its number of claims. The Top-50 institutional effect remained significant under both analysis (OR 5.15, 94% CI 2.18– 12.15; versus a claim-level OR 3.68, 94% HDI 1.50–9.28). In this new model Trophy journals also showed had higher odds of challenged claims than low-impact journals (OR 2.90, 94% CI 1.24–6.78 vs a claim-level OR 1.75, 94% HDI 0.59–4.91). This impact was not significant in the primary model but became significant at using article-level analysis. Other estimates are consistent in direction and magnitude with the primary claim-level model. Model diagnostics were satisfactory.”

Moreover, we added Figure S6 which display visually the relationship between the claims and the article.

[This response is referred later as “Response to claim vs article level analysis”]

(2) As mentioned above, I think the biggest weakness is that the authors are taking the literature at face value when assigning if a claim was validated or challenged vs gathering new independent evidence. This means the paper leans more on papers, making it more like a citation analysis vs an independent effort like other large-scale replication projects. I highly recommend the authors state this in their limitations section.

We have now explicitly acknowledged this limitation in a dedicated section at the end of the revised manuscript. However, as noted above, we do not take the literature at face value. Notably, some of the claims we identify as challenged originate from highly cited articles, which could lead a naïve reader to assume their validity.

Ultimately, this replicabilty project remains a human, expert-driven effort aimed at determining which claims withstand scrutiny within a field. The broader community was invited to engage with and respond to these assessments and we did get some feedbacks. Importantly, claims were not evaluated in isolation but in the context of the entire body of knowledge, and all evaluations were made transparent and explicitly justified in the ReproSci database.

On top of that, I have questions that I could not figure out (though I acknowledge I did not dig super deep into the data to try). The main comment I have is How was verified (and challenged) determined? It seems from the methods it was determined by "Claims were cross-checked with evidence from previous, contemporary and subsequent publications and assigned a verification category". If this is true, and all claims were done this way - are verified claims double counted then? (e.g., an original claim is found by a future claim to be verified - and thus that future claim is also considered to be verified because of the original claim).

When two articles reported the same main claim and this claim was judged as “verified,” each instance was counted in the analysis. However, when validation came from studies published after 2011, the claim was counted only once. Thus, our study specifically evaluates the replicability of claims originating from a defined period (pre-2011).

We note that, in principle, repeated publication of the same finding across many articles could artificially inflate estimates of replicability. However, such cases appeared to be rare in practice, and studies reporting similar claims typically provided complementary evidence—for example, elucidating gene function through either genetic or biochemical approaches.

Related, did the authors look at the strength of validation or challenged claims? That is, if there is a relationship mapping the authors did for original claims and follow-up claims, I would imagine some claims have deeper (i.e., more) claims that followed up on them vs others. This might be interested to look at as well.

We did not perform a systematic mapping between original claims and subsequent follow-up studies. While this is an important and interesting aspect, it was considered beyond the scope of the present work. The current study already represents a substantial investment of time and effort, and the resulting database provides a valuable resource for future analyses. In particular, it could support a dedicated bibliometric study at a later stage.

(3) I recommend the authors add sample sizes when not present (e.g., Fig 4C).

The cited panel appears to correspond to Figure 5C in the revised numbering, as the current Figure 4 contains only panels A and B. We systematically checked the denominators of all figures and revised the captions to report the numbers of claims, authors or laboratories represented, together with the reasons for exclusions. We also added the numbers of authors and claims directly within the author-level scatter plots, with the observational unit explicitly identified.

I also find that the sample sizes are a bit confusing, and I recommend the authors check them and add more explanation when not complete, like they did for Fig 4A. For example, Fig 7B equals to 178 labs (how did more than 156 labs get determined here?), and yet the total number of claims is 996 (opposed to 1,006).

There are 156 labs total, 23 labs contributed publications during both junior and senior stages, and 11 claims lacked a junior/senior classification. This has been explicited in the caption.

Another example, is why does Fig 8B not have all 156 labs accounted for?

The panel does not include all 156 laboratories because we could obtain information about first author training for only 146 PI and laboratories while prior first-author status was unavailable or indeterminate for ten PI. This has been added to the caption.

(Related to Fig 8B, I caution on reporting a p value and drawing strong conclusions from this very small sample size - 22 authors).

The 22 authors are not the total sample size; they constitute the subgroup of PIs who had previously published a first-author paper on Drosophila immunity in another laboratory. In the submitted panel, they were compared with 117 PIs without this training history, giving 139 classified laboratories and 774 claims.

As a last example, Fig 8C has al 156 labs and 1,006 claims - is that expected? I guess it means authors who published before 1995 (as shown in Figure 8A continued to publish after 1995?) in that case, it's all authors? But the text says when they 'set up their lab' after 1995, but how can that be?

Thank you for identifying this inconsistency. Figure 8C intentionally includes the full cohort of 156 PIs and all 1,006 claims. Panel C compares research styles and does not impose a restriction based on year of entry into the field or year of claim publication. Thus, PIs who entered the field before 1995 are included together with all claims attributed to them; the panel is not restricted to claims published after 1995.

The statement that only PIs who established their laboratories after 1995 were included was an erroneous carryover from an earlier version of the analysis. We removed this restriction from the Results and revised the caption to state that exploratory PIs (n = 91) contributed 366 claims, whereas continuity PIs (n = 65) contributed 640 claims.

We also replaced references to the date when PIs “established their laboratory” with “year of entry into the field,” defined as the year of their first Drosophila-immunity publication as either first or last author. During the same check, we revised Panel B to include all 146 PIs eligible for the pre-PI training comparison, contributing 793 claims.

(4) Finally, I think it would help if the authors expanded on the limitations generally and potential alternative explanations and/or driving factors. For example, the line "though likely underestimated' is indicated in the discussion about the low rate of challenged claims, it might be useful to call out how publication bias is likely the driver here and thus it needs to be carefully considered in the interpretation of this. Related, I caution the authors on overinterpreting their suggestive evidence. The abstract for example, states claims of what was found in their analysis, when these are suggestive at best, which the authors acknowledge in the paper. But since most people start with the abstract, I worry this is indicating stronger evidence than what the authors actually have.

We have added a dedicated section on limitations at the end of the Discussion to explicitly acknowledge key constraints, and we also address these points throughout the Discussion where relevant. In addition, these limitations are now in the abstract.

The authors should be applauded for the monumental effort they put into this project, which does a wonderful job of having experts within a subfield engage their community to understand the connectiveness of the literature and attempt to understand how reliable specific results are and what factors might contribute to them. This project provides a nice blueprint for others to build from as well as leverage the data generated from this subfield, and thus should have an impact in the broader discussion on reproducibility and reliability of research evidence.

Thank you for this positive assessment!

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Comments and recommendations are provided in the order that they appear in the manuscript.

Introduction:

- In the second paragraph of the introduction, I don't think all the references refer to "molecular life sciences" (e.g. one of them is from ecology and evolution, for example). I'd also argue that Macleod et al. 2014 refers to risk of bias rather than to reproducibility per se.

We have corrected this in the revised version.

- The author use both "reproducibility" and "replicability", apparently as synonyms, but as definitions for these words vary across sources (e.g. https://arxiv.org/abs/1802.03311, https://www.nationalacademies.org/our-work/reproducibility-and-replicability-in-science, https://osf.io/br9sp/) it may be worth stating their definitions upfront.

Thank you for the references. We agree that the literature contains multiple, sometimes conflicting definitions of these terms, which can lead to confusion. In response to the reviewer’s comment, we have clarified our terminology. Specifically, we now use the term “conceptual replicability” in the abstract and consistently refer to “replicability” and “irreplicability” throughout the manuscript. We hope this revised terminology improves clarity.

- Why are analysis described as "exploratory" and "multivariate"? If it has not been preregistered, shouldn't the multivariate analysis be considered exploratory as well?

Thanks, we agree. The word “exploratory” is confusing as we use it for its structural meaning and not its epistemological meaning. We have replaced it throughout by “descriptive”, as to not imply that the multivariate analysis is preregistered by contrast.

Results:

Methodology and claim assessment

- The methods for the selection, annotation and classification of studies are described very cursorily here, and the Methods section doesn't add that much, but I'll keep these observations to the methods. Still, it's worth mentioning that it's hard to know how reproducible the annotation and classification process is from the information provided.

We have provided more information on the method section on the way to annotate and class claims. Of note, there is more information on the methods on the associated publication Westlake et al., 2025 and on the ReproSci website.

- "Then, experimental work was performed in several laboratories...". Once again, a much better description of how replications were set up and performed is needed.

We have provided information on the number of laboratories (nine) involved in the reproduction of 45 major claims. The laboratories involved in replication are listed in the author list. All the files associated with experimental replication can be found in the supplementary materials of Westlake et al 2025 or the ReproSci website.

- "These claims subjected to experimental validation were selected according to criteria such as appearing suspicious due to the absence of direct follow up or being straightforward to test experimentally". This is rather vague, but if no explicit criteria were set upfront this may be inevitable. Still, it would be useful to know who made this decision.

A first list of claims to be replicated was made by Hannah Westlake and Bruno Lemaitre. The claims that were selected to be replicated were tested by the labs and experimental workers that had the expertise required to test them. The choice of the claims to be tested was not random. Claims that were suspicious are claims that were already tested in the host laboratory without success, claims whose validity are debated at meeting, claims from highranked journal with no follow-up. This is now indicated in the method of the revised version.

Drosophila immunity claims are mostly reproducible

- The percentages given in the initial description of the results pool the results of the retrospective analysis of the literature and the prospective replications performed. As mentioned in the Public Review, I think these are rather distinct ways to assess reproducibility, and would recommend that these two analyses are described separately.

We agree with the reviewer but we believe that we have already well separated the results before and after experimental work in the revised version. This is clearly shown in Table 1. Our text says ‘Importantly, 6.8% of claims (69 out of 1006) were challenged. Among these, 44.9% (31 out of 69) were contested by published articles including 7.2% by the same authors, and 55.1% (38 out of 69) were challenged experimentally as part of the ReproSci project.’

- "These results may reflect the robust scientific standards and methodological rigor of Drosophila research...". Once again, as mentioned in the Public Review, I think publication bias is a plausible explanation, so this should be mentioned as an alternative.

We have mentioned publication bias in the revised version in the section on limitation. But an important point to underline is that this analysis did not take publication results as face fact. This is a critical analysis by experts in the field. As already mentioned, some claims like ‘Duox produces microbicidal ROS” ‘NO is a signaling molecule…’that have been mentioned in multiple articles were considered as challenged.

A second point is that it is likely that publications in some fields are more replicable than in other. Actually, we did not discuss ‘reproducibility issues’ when I started in the field 30 year ago because this was not perceived as an issue. It is normal that reproducibility rate varies according to fields. Nevertheless, we do find important claims with high visibility that are not replicable in our sample. Thus, our findings nuance the ‘reproducibility crisis narrative’ but we still believe that there is concern with reproducibility in life science. Last point, the criterium we have used in our study did not map all the problematic papers, notably some claims might be fundamentally verified but exaggerated in the original paper.

- It would be useful to break down the "partially verified" category somewhere. Illustrative examples of what is meant by "insightful data were accompanied by incomplete interpretations" or "incomplete data were paired with insightful interpretations" would be useful as well.

All the claims are listed in the public database with an explanation as to why they got affected to a category. The categories mixed and partially verified refer to claims that are more complex to categorize.

Here are are two examples from the ReproSci website:

Claim: Relish Rel mutants are very susceptible to bacterial and fungal infection. Partially verified

Assessment: Relish mutants are primarily susceptible to Gram-negative bacterial infections, and do not typically have increased susceptibility to Gram-positive bacteria and fungi which are primarily rebuffed by the Toll pathway, although Imd signaling may provide a minor contribution to defense against these. The high susceptibility of Relish mutant to fungi observed in this article is likely due to the presence of the ebony marker (Lemaitre et al., 1996) [here only one part of the statement has been verified]

Claim: PGRP-SC1a is required for Lys-type peptidoglycan recognition and Toll activation. Mixed

Assessment: A possible role for PGRP-SCs in Toll activity has been strongly debated. Challenged by (Bischoff et al., 2006) who found no effect of PGRP-SC RNAi on activation of Toll (Drs expression) in adult flies (although note that their data show a minor reduction of Drs expression in flies in response to E. faecalis). Supported by (Costechareyre et al., 2016) who used single -SC1 and -SC2 mutants to show that Toll activation (Drs expression) was reduced in -SC1 but particularly -SC2 mutants (~50%) in response to E. faecalis (although survival was not affected). The supplementary data of (Paredes et al., 2011) similarly show that Drs expression was reduced (50%) in response to M. luteus septic infection in PGRP-SCdelta flies (PGRP-SC1A/B -SC2 triple mutant), but concluded that this was due to a secondary effect of Imd overactivation. Note that the phenotype found by (Garver et al., 2006) was much stronger (complete ablation of Drs expression), which is not consistent with any subsequent results and argues for a secondary mutation in this line, although this is not consistent with the successful rescue of Drs expression by transgenic replacement of PGRP-SC1a. Downregulation of Toll in these mutants could be explained if the Toll pathway requires amidase activity of PGRP-SC for immunogenicity (e.g. the sugar backbone without stem peptides is a stronger elicitor than whole peptidoglycan), whereas similar cleavage reduces recognition by the Imd pathway (consistent with the demonstrated requirement of stem peptides for full stimulation of the Imd pathway (Chang et al., 2005; Stenbak et al., 2004)). See annotation for (Mellroth et al., 2003). [here the claim is mostly challenged but there are observations that go in the same directions]

As shown by these examples, category assessment was complex process and relied on human expertise. However, there was very little contestation from the community after the submission of our articles and the opening of the ReproSci website.

A significant fraction of unchallenged claims is non-reproducible

- Excluding the 45 unchallenged major claims that were experimentally tested, we categorized the remaining 240 unchallenged claims into three groups". No information is provided on that classification process (either here or in the methods). Who made these assessments (which seem quite subjective and dependent on field expertise), and how do you know if such judgments are reproducible across different evaluators?

This categorization was done by Hannah Westlake and reviewed by Bruno Lemaitre with few disagreements. This is now indicated in the revised version. The category ‘unchallenged logically consistent” and ‘‘unchallenged logically consistent’ refer to claims that although not directly verified are corroborated or in with current literature. See ReproSci for justifications.

Example from ReproSci website:

Claim: The minimal structure needed to activate the Toll pathway is a muropeptide dimer.

Assesment: Unchallenged logically consistent This is consistent with (Park et al., 2007) who show that on a linearized strand of peptidoglycan, the minimal motif is at least 3 dimers. But it is expected that a non-linearized dimer linked by the peptide bridge could serve as the minimal motif by clustering peptidoglycan.

Claim: eater null flies are susceptible to oral infection with Serratia marcescens Unchallenged logically consistent Inconsistent with the observation that Eater mutants successfully phagocytose Serratia marcescens (Bretscher et al., 2015). This may indicate that another factor affected by eater mutation is required for defense against S. marcescens, such as formation of lamellopodia and filopodia or adhesion of hemocytes to the body wall, or that Eater contributes to binding of Gram-negative bacteria but does not trigger phagocytosis in response to them as it does for Gram-positive bacteria.

Higher representation of challenged claims in trophy journals and from top universities

- Both impact factor and the Shanghai university ranking are continuous variables, but the authors opt to use them as categorical variables in the analysis (i.e. "low-impact", "highimpact", "trophy"; "Top 50", "51-100", "101+"). While there may be legitimate reasons to do this if they feel that these categories are a better descriptor of the underlying reality (e.g. perhaps Cell, Science and Nature are indeed in a category by themselves), it is an unusual decision that leads the comparison to ignore the distinctions between journals/universities within a category. Moreover, it also opens up the opportunity to analysis bias as categories can be set up in many different ways. Thus, if the analysis was not preregistered, I'd recommend that analyses using impact factor and ranking as quantitative variables are added as sensitivity analyses, as these seem to me to be the most natural/less ad hoc way to look at the issue.

See “Response to categorical variable encoding” above.

- As mentioned in the Public Review, the analysis here pools the results from the retrospective analysis based on the literature and the prospective one based on the performed replications. Although this may be justified from a sample size perspective (as the number of challenged claims is not that high), it would be useful to perform this analysis separately on the two sets of results as well, as different trends may be noticed. There are many biases that might come into play here (e.g. results from top institutions being more or less likely to have challenged/unchallenged claims published) and looking at the results separately could help in tearing apart these hypotheses.

The ReproSci project analyzes all the papers of a community during a period of time. As such, the total number of claims is limited and we believe that pooling the data was justified. We provide as sensitivity analysis in Supplement S7, a multivariate model with claims in their pre-experimental classification state:

“As a sensitivity analysis, we refitted the multivariable hierarchical logistic model using only the claim classifications available before experimental validation by the ReproSci project, as the choice of which claims to further validate could have been influenced by covariate (impact factor, university status). The 45 claims tested prospectively were therefore restored to their original “Unchallenged” classification, while all covariates and author-level random intercepts were retained from the primary analysis. The complete-case analysis included 869 claims, of which 28 (3.2%) were challenged. No predictor had a 94% highest-density interval excluding 1, including publication in trophy journals (OR 1.11, 94% HDI 0.33–3.77) and affiliation with a Top50 institution (OR 1.44, 94% HDI 0.48–3.94). Thus, the associations observed in the pooled analysis were not evident when using classifications based exclusively on the retrospective literature review, although estimates were imprecise because of the small number of challenged claims”

The irreproducibility rate has increased over time as the field has grown in popularity

- Again, why not use year as a continuous variable rather than using 5-year windows (as this would effectively include more information)? I think the categorization here is less ad hoc than in the journal/university case, but it is still an unusual decision. More important than this, however, is the fact that pairwise comparisons between periods is probably not an appropriate strategy to look for a time trend, as it excludes all information not related to the pair in each analysis. I'd strongly suggest substituting this for a straightforward regression with publication year as a continuous variable.

We thank the reviewer for this important suggestion. We agree that categorizing publication year into five-year periods may obscure temporal trends.

We therefore modelled publication year continuously using a spline in the multivariable analysis, thereby retaining the full temporal information while allowing for non-linearity. A straightforward linear regression would impose a linear trend, which may not adequately capture changes over time. We retained the five-year groupings solely for visualization.

- "The subsequent increase in unchallenged claims may reflect the rapid conceptual expansion of the field, which likely outpaced the growth in the number of researchers". Do we have data on the growth in the number of researchers in the field? If so, it might be interesting to cite this.

We do not have the number of researchers to assess the growth of the field, however we can see in Figure 8A an increase in the number of laboratories (as identified by last author name) after 1995. This together with the increase in the number of articles (Figure 3A) clearly show the expansion on of the field.

- Isn't a "rise in unchallenged claims" over time expected by chance, as older findings will have more time to have been verified by someone else? I understand that the 14-year window probably mitigates this effect, but it still probably exists in some degree and should be mentioned.

The reviewer is correct that the % unchallenged claims should increase over time, but this does not explain the very low number of unchallenged claims between 1992-2001.

First-author patterns of irreproducibility

- With 69 challenged claims and 289 first authors, it would be impossible to achieve "perfect equality" (e.g. a Gini index of 0.88). To verify how far the observed coefficient deviates from chance, it would be useful to obtain (perhaps via simulations) the Gini coefficient expected by chance given the number of challenged claims/authors, and perhaps derive a p value as well (e.g. the proportion of random permutations in which the index exceeds the observed value).

Very good observation, thank you, we provide this analysis for both first and last author, in the main text and in a supplementary table.

Added first author text:

“The distribution of challenged claims among first authors was highly unequal with a Gini coefficient of 0.881 (inequality index ranging from 0 -perfect equality- to 1 extreme inequality-, Figure 4B): the top 10% of first authors accounted for 73.9% of challenged claims, and the top 20% accounted for all challenged claims. This inequality exceeded that expected by chance (reassigning randomly the 69 challenged labels across individual claims, while preserving each author’s number of claims, p = 0.000001). It also remained greater than expected when claims from the same paper were kept together (p = 0.015; Supplementary Table Sx). The concentration of challenged claims among first authors cannot be explained solely by differences in the number of claims or by clustering within papers.”

Added last author text:

“Challenged claims were also unevenly distributed among leading authors (Gini coefficient = 0.856): the top 10% accounted for 71.0% of challenged claims and the top 20% accounted for 94.2%. The observed inequality exceeded that expected when challenged labels were reassigned across individual claims (p = 0.00081), but not when claims from the same paper were kept together (p = 0.127; Supplementary Table S9). The apparent concentration among leading authors could be explained by multiple challenged claims arising from the same papers.”

Added method text:

“We compared the observed Gini coefficients with two permutation analyses, each based on 1,000,000 permutations. First, we randomly reassigned the challenged labels across individual claims while keeping every claim attached to its original author. This preserved the number of claims contributed by each author. Second, we kept the challenged-claim pattern of each paper together and reassigned these patterns among papers containing the same number of claims. This additionally accounted for the possibility that claims from the same paper were challenged because of a shared problem. For each permutation, we recalculated the Gini coefficient across authors and calculated the p-value as the proportion of simulated coefficients that equalled or exceeded the observed coefficient. Full results are reported in Supplementary.”

- Claims in a single paper may not be fully independent from each other (as both could be irreproducible due to the same error), so it could be worth adding the article as a random variable here.

See answer above: [“Response to claim vs article level analysis”]

- In Fig. 4B, what defines the order of the dots between 0 and 250 (i.e. authors that have no challenged claims)? Is this merely arbitrary? This should be stated more clearly.

Thank you, the order was arbitrary, it has now been fixed by using a secondary sorting (verified claim proportion), and Authors tied on challenged-claim proportion are ordered by verified-claim proportion has been added the legend.

- In Fig. 5C, there are clearly less dots than there are authors. This is likely due to superposition (i.e. there are probably multiple circles with 1 article and 0% verified claims). Nevertheless, it means that the graph conveys an erroneous message. As the x axis is a discrete variable, it may be worth turning it into five categories (e.g. 1 to 5) and adding some jitter to each of them in order to let the reader know how many dots are in each category/%.

Thank you, this was indeed due to superposition. After trying to add a jitter, the graph was still confusing, so we changed the representation to show circle whose size depends on the number of authors. The graph now conveys the size of each block properly.

Lead-author patterns of irreproducibility

- The same comment concerning the Gini index made for the first authors also holds here.

We added a text, see answer above.

- In Fig. 6B, the same comment made for figure 4B also holds.

Thank you, the order was arbitrary, it has now been fixed by using a secondary sorting (verified claim proportion), and Authors tied on challenged-claim proportion are ordered by verified-claim proportion has been added the legend.

- The division between "senior" and "junior" PIs is rather ad hoc here. Once more, why not use "years from first last-author publication" as a continuous variable as a more neutral way to analyze this (as done in Fig. 8)? Also note that it is not clear whether "published a lastauthor article at least five years prior to the considered publication" means any article or one about Drosophila immunity (as in Fig. 8A), and which database was used to examine this (PubMed? Other?).

Senior and junior researchers were classified based on whether they had published a last-author article five years or more using Pubmed (for seniors). We did not specify articles in Drosophila immunity when considering seniority but only having a last author article five year before the publication.

- In Fig. 7C, the same comment made for Fig. 5C also holds, although the solution here is less obvious as there are more possible numbers for "number of articles".

Thank you. As in Fig. 5C, superposition obscured multiple authors occupying the same coordinates. We therefore revised Fig. 7C so that authors with the same number of articles and proportion of challenged claims are represented by a single circle. Circle size and the number shown inside indicate how many authors are represented.

- As far as I could tell, the data on Fig. 8A refers to when authors published their first first/last author papers on Drosophila immunity (which makes it different from Fig. 7, which refers to any article, but I could be mistaken). If this is the case, I'm not sure it's correct to talk about "the period when principal investigators established their laboratories" as mentioned in the text, as (a) they could have published a first author paper in somebody else's lab or (b) they could have started a lab and only later published a paper on Drosophila immunity. "Year of entry in the field" as in the figure legend seems more appropriate.

We have changed for ‘year of entry in the field’ as suggested by the reviewer

- In the same figure, the 1995 cutoff seems completely arbitrary. Why not analyze this as a regression with year of entry as a continuous variable?

The 1995 boundary is historical as it marks the expansion of Drosophila immunity from a marginal subject into a popular field. The expansion of the field at this specific time was probably driven by a combination of factors: major advances in Drosophila genetics and genomic resources and growing knowledge of antimicrobial peptides in the early 1990, a strong interest on innate immunity that drew attention on the power of Drosophila to answer key questions in this new area. These developments attracted new researchers to insect immunity, and the later discoveries of the IMD and Toll pathways in 1995 and 1996 gave the field an additional (and probably even stronger) boost. Our corpus holds 29 articles for 1959– 1994 (0.8 per year) against 371 for 1995–2011 (21.8 per year), and only 13 of the 156 PIs entered before 1995. The comparison is therefore a cohort contrast more than a contrast or search for a cutting point. Moreover, a regression would impose a linear relationship between the different years, which we believe is too constrained on regard of the observed data.

- "We hypothesized that these authors, having gained prior hands-on experience on Drosophila immunity, would be less prone to publishing irreproducible claims.". This is a possibility, but given that most of the sample is retrospective, it's also possible that the field is more prone to publicly challenging findings from newcomers.

Since we do not observe major difference in replicability between senior and junior PI, we still believe that training as first author in a traditional immunity laboratory compared to no training is significant.

Irreproducibility according to research styles

- The objective definition of "continuity" and "exploratory" PIs should be stated here for this to be interpretable (note that this is not clear in the Methods either).

We have better defined how we separate "continuity" and "exploratory" PIs in the methods and in the result section.

Multivariable analysis of predictors of claim irreproducibility

- As mentioned in the Public Review, does it make sense to include "unchallenged" along with "verified" in the outcome? If the objective is to reduce the analysis to a "verified/not verified" claim, wouldn't it make more sense to remove the unchallenged findings (as these are likely uninformative, and based on the authors' own replications may be more related to the "challenged" category than to the "unchallenged" one?

See above, “Response to unchallenged exclusion”

- As stated previously, why not include journal impact factor, university ranking, year of first paper and year of first Drosophila immunity paper, as continuous variables rather than categorical ones (which would effectively lead to a model with less parameters when there are more than 2 categories). Particularly, there is more information to be gained from adding a single variable than from performing individual comparisons between categories when these have a natural order.

See above, “Response to categorical variable encoding”

Discussion:

- As "conceptual reproducibility" is somewhat of a vague concept, it seems important to discuss (both in the Methods and Discussion) how this was operationalized. Although it's obvious some decisions of what constitutes a direct replication will vary on a case-by-case basis, general guidelines on how these criteria were set are needed.

We have defined in the methods used to categorize article claims as well as the link with the other companion article. In the ReproSci database, all the assessment are justified allowing to see how we classified claims.

- "Contrary to the more dramatic narratives...". Here, it is important to emphasize the key differences between this and the cited references: (a) the fact that the majority of the replicability of the sample was found on the basis of a retrospective sample and (b) the fact that the study is dealing with conceptual rather than direct replications. Also, the possibility of confirmation bias should be mentioned as an alternative hypothesis in the last sentence of this paragraph.

This is a good point and we have highlighted that methodological differences between our study and other studies could explain differences in replicability rates.

- "findings that, despite being published, have never been independently tested". A more accurate description may be "have never been independently confirmed or refuted in the published literature", as many (and perhaps most - see Baker 2016) replication attempts may go unpublished, as the following sentences themselves indicate.

We have changed the text according to the reviewer’s suggestion.

- The description of how findings came to be regarded as "suspicious" here is interesting - and an important part of how the sample was determined. In this sense, I'd consider this as part of the methods. Even though defining what makes something "suspicious" may not be completely systematic, a general description of the method that led the researchers to arrive at this list (e.g. the process that seems to be hinted at in this paragraph) deserves a thorough description.

The description of how findings came to be regarded as "suspicious" is now detailed in the methods.

- "Our results suggest the status of a claim being "unchallenged" is not a reliable proxy for its validity". I agree, but this is statement is in direct contradiction with the authors' decision to include unchallenged claims along with validated ones in the binary outcome of the multivariate model.

See above, “Response to unchallenged exclusion”

- "Trophy journals are more likely to publish articles with challenged claims than high or lowimpact, although the difference was not significant." Again, a single analysis using a continuous measure of impact should provide more statistical evidence than the pairwise comparisons.

See above, “Response to categorical variable encoding”

- "However, this higher rate of follow-up work cannot fully explain by itself the higher proportion of challenged claims in trophy journals." Why not, exactly? I don't remember seeing an objective analysis of it.

If we remove the unchallenged claims, we still observe higher rate of irreplicability in trophy journal: 15.85% in trophy journal versus 9% in high-impact and 8.1% in low-impact. So we believe that the higher rate of irreplicability in trophy journals cannot be explained by a lower level of unchallenged.

- The very large paragraph on pages 21-22 could be split into two, one about journals and the other about universities.

This has been done.

- "Our data align with the broader narrative of increasing rates of non-reproducible science.". Does it? The time trend did not seem very clear to me (and I would argue that it was not analyzed properly).

As indicated in the text, we observed an increase in the rate of irreplicable claims over time; however, this trend did not reach statistical significance. We are confident in the robustness of our analysis and therefore did not pursue this question further. While our findings align with concerns about non-replicable science, they also offer a more nuanced perspective, showing that in some fields, replicability remains significantly high.

- "A similar but more acute pattern was observed during the SARS-CoV-2 pandemic." References should be provided here.

We have added this reference to suggest that articles published on SARS-CoV-2 pandemic are overall less reliable than others: An alarming retraction rate for scientific publications on Coronavirus Disease 2019 (COVID-19) Nicole Shu Ling Yeo-The https://doi.org/10.1080/08989621.2020.1782203

- Some of the trends discussed here (e.g. time, continuity vs. exploratory style are not supported (even as a trend) by the multivariate model, and this caveat should be mentioned. An odds ratio of 0.89 with a very wide confidence interval may be too weak in terms of evidence strength to merit a whole paragraph in the introduction discussing it.

We did not mention the question of time horizon or the distinction between continuity and exploratory research styles in the Introduction; however, we believe these issues merit consideration in the Discussion. In particular, the contrast between continuity-driven and exploratory approaches is noteworthy. Although we found no significant difference in the rate of challenged claims between these approaches, there was a significant difference in the rate of unchallenged claims, which are subsequently more likely to be challenged. This finding is important in the current funding landscape, where many agencies prioritize short-term, exploratory projects. Such incentives may inadvertently contribute to issues of irreproducibility.

- There are many other limitations beyond those mentioned, in particular the fact that much of the analysis is retrospective and based on a potentially biased literature. The fact that the analysis does not seem to be preregistered and is dependent on a lot of ad hoc decisions also merits discussion. This should definitely be explored in more detail in the Limitations section.

These limitations are now discussed in the limitation section at the end of the discussion. We agree on the fact that our analysis was not preregistered and that some of our conclusions are raised after analyzing the data. This article is part of a more global project including the databases with all the information. However, full objectivity when analyzing literature is not unachievable, and these critics are inherent to all reproducibility projects.

Methods:

Selected articles, annotation and experimental validation:

- "In brief, a list of 400 publications published before 2011 was generated using a curated search string on the publicly available PubMed database.". Please state that the search string is available in the companion article (e.g. https://doi.org/10.1101/2025.07.07.663442) or include it here.

This is now stated.

- "Selected primary articles were annotated by a single researcher".

By "annotation", do the authors mean the extraction of claims? This is not self-evident. Also, what does the "review" process entails? Do the authors have any data on agreement?

We do not have data on agreement but overall, there were few discrepancies. We agree that the way to section article in separate claims could affect the conclusion in a number of cases. All the data are public and we did not have any request from the community. The fact that this project depends from arbitrage from the two annotators is mentioned in the limitations.

- "Claims were cross-checked with evidence from previous, contemporary and subsequent publications and assigned a verification category."

How was this process performed? This seems to be quite complex and there's hardly any information about it. And once again, do the authors have any data on how reproducible this process would be when performed by different people?

All the data, notably claim assessment and justifications, are available on the website. Findings cross-checking the claim could be identified by knowledge of the authors, checking articles that quotes the articles. This was an enormous amount of work with human arbitrage. We expected more feedback from the community. The reaction of the community will be described in a companion article later.

- The authors mentioned that annotations and verifications were made available for comments on the community, but how were these comments incorporated if different opinions were voiced? Can the authors provide data on how frequent these comments were, and how often they were incorporated?

All data is available on the website, where members of the community can publicly comment on our assessments. The authors can see these comments on the ReproSci website

Table 1:

- Again, the three "partially verified" categories in Table 1 seem to refer to very different situations and it would be interesting to break these down somewhere.

We agree that categories ‘mixed’ and ‘partially verified’ are complex. They represent situations where a decision was not easy. We prefer not to break down those categories in multiple sub-categories.

First and last author classification:

- What does "status of first author" mean?

Status means their position: technician, PhD student, Post-doc, PI….

- "PIs were manually classified as..." - there seems to be something missing in this sentence (e.g. "as senior or junior on the basis of whether they have...")

We have added PIs: PIs were manually classified as senior or junior PIs on the basis on having published an article in Pubmed as last author more than five year ago.

- The distinction between continuity and exploratory is not explained in objective terms. Is there any objective definition of what it means to "continue to work in the field". Publishing a paper in the last X years? And what counts as a "transient" incursion?

We have better explained in the methods this distinction.

Statistical analysis:

- Can the authors define exactly what they mean by "weakly informative priors"?

Weakly informative prior are Bayesian prior distribution that are meant to be vague as to let the data dominate the results (vs the prior belief of the scientist). They can be seen as very close to flat priors, which are not used here because they cause numerical convergence issues.

- The authors mention a lot of variables included in the multivariable analysis, but little information is provided on the categorization. What are "low, high and trophy journals"? What university rankings are used?

We used Shanghai Ranking’s 2010 Academic Ranking of World Universities as our ranking of university. Our binning of ranking in categories make the analysis less susceptible to changes in ranking system. We selected the Shanghai ranking as it primarily evaluates research output and awards (where Times also evaluate teaching, and QS also employer reputation), which we believe represent better the variable than may affect irreplaceability. For the categorization, please see answer above: “Response to categorical variable encoding”

- "Exact formulas (...) are available in the public repository". What repository do authors mean? The project website? The GitHub repository? Please specify and provide a direct link if possible.

We added a link to the main text (it was only in the supplementary document). The Supplementary document contains information on how to reproduce the results.

Reviewer #2 (Recommendations for the authors):

Specific comments:

Some methodological details related to the main conclusions of the paper are missing.

We have extended the methodological section and also better link this article to the companion article.

- Impact factor: It is unclear which year(s) of journal impact factors were used. Trophy journals are defined as those with an impact factor >50 (Science, Nature, and Cell), but according to Figure 2B, there are only three such journals. Are "trophy journals" limited to these three, or are others included that meet the >50 impact factor threshold?

These are the 2022 impact factor, we made that clear in the main text. Moreover, only 3 journals in our datasets had an impact factor >50: Nature, Cell, and Science (so the Trophy Journal category is limited to these 3, but not by definition). This is explicit in Table S1: List of journals with impact factor and claim assessment.

- University ranking: Similarly, please clarify which year(s) of university ranking data were used. Since rankings vary depending on the system (e.g., QS, Times, Shanghai), were the conclusions consistent across multiple ranking sources?

We used Shanghai Ranking’s 2010 Academic Ranking of World Universities as our ranking of university. Our binning of ranking in categories make the analysis less susceptible to changes in ranking system. We selected the Shanghai ranking as it primarily evaluate research output and awards (where Times also evaluate teaching, and QS also employer reputation), which we believe represent better the variable than may affect irreplaceability.

Reviewer #3 (Recommendations for the authors):

Table S4 - for leading author there is a variable of 'historical lab after 1998 continuity' - should that be 1995?

Correct, we changed this label to Trained in Historical laboratory (Comparison restricted to claims published after 1995) to make it more explicit.

eLife Assessment

This useful study shows that neural activity before a conversational response contains information about the duration and timing of the subsequent turn. The evidence that this information originates from speech-production planning is incomplete. Because the analyzed EEG is recorded during processing of the partner's speech, and because that speech causally determines the subsequent response, production planning and comprehension/context are confounded in the current analyses. It would strengthen the production interpretation considerably if the authors could show that the relationship with forthcoming duration survives richer controls for the preceding turn, or ideally after accounting for EEG variance driven by the incoming speech.

Reviewer #1 (Public review):

This manuscript examines EEG activity during face-to-face Diapix conversations and asks whether neural activity preceding a participant's next speaking turn predicts the latency and duration of that turn. The authors report sustained ERP and alpha/beta effects, particularly associated with upcoming response duration, together with temporal-generalization decoding beginning approximately 1-1.3 s before speech onset. They interpret these results as evidence for two stages of conversational speech planning: an early process that activates and maintains the forthcoming response, and a later process related to commitment and motor execution. The naturalistic dyadic EEG setting, relatively large number of conversational turns, trial-level analyses, and convergence across ERP, oscillatory, and multivariate approaches are important strengths.

I nevertheless have substantial concerns about the interpretation. Most importantly, the EEG analyzed during this period is recorded while participants are processing their partner's speech. Therefore, neural activity necessarily includes auditory, linguistic, semantic, pragmatic, and turn-boundary processing, in addition to any potential response-planning activity. Because properties of the incoming utterance are themselves strongly related to what the listener subsequently says, predicting subsequent response duration or latency does not by itself isolate production planning. The authors acknowledge some of these limitations, but the current title, theoretical framing, Figure 8, and conclusions remain considerably stronger than the evidence allows. Indeed, the Discussion itself acknowledges that the signals cannot be determined to reflect linguistic content, general planning demands, or motor preparation.

I therefore think the study could become valuable, but substantial additional analyses and conceptual reframing are required.

Major concerns:

(1) The central problem is dissociating speech planning from listening/comprehension

This is my main concern with the manuscript and also with the claims in the Discussion. The authors repeatedly infer that because EEG during the partner's turn predicts the duration or latency of the participant's subsequent response, this activity reflects speech planning. For example, the manuscript states that examining the period before self-speech onset "isolat[es] preparatory neural activity before articulation." I do not think this inference is justified.

During precisely this interval, the participant is also listening to and comprehending the partner. The incoming utterance is not independent of the forthcoming response; it is what determines the response. A complex statement, several questions, a request for clarification, or an information-rich description will produce different auditory/linguistic/comprehension activity and may also systematically change the length and timing of the subsequent response. Consequently, both partner speech → listening/comprehension EEG and partner speech → subsequent response properties can generate an EEG-response relationship without requiring that the measured EEG activity itself reflect production planning.

The authors control partner-turn duration, which is useful, and they show that self-duration, self-latency, and partner duration are behaviorally related. However, partner duration is only a very coarse property of the input and cannot control for what participants are actually processing. The analysis should consider, at minimum, partner word count/speech rate, acoustic properties, information density or lexical/syntactic complexity, dialogue act, question versus statement, and preferably semantic/discourse content. For example, the number of questions or propositions in the partner's turn may directly determine both comprehension demands and how much the listener subsequently needs to say.

Given that transcripts and word-level timing are already available, the authors should be able to substantially improve this analysis. One particularly useful approach would be to construct an encoding model of the EEG driven by acoustic and linguistic features of the partner's speech and then test whether the residual neural activity continues to predict subsequent response properties. At minimum, richer input-related covariates are necessary.

Without such analyses, I think the main conclusion should be reframed from "neural signatures of speech planning" to something closer to "pre-response neural activity during conversational listening predicts properties of the subsequent turn." The latter is supported by the data; the former requires stronger dissociation.

(2) It is not clear that the analyzed period is actually a "listening interval".

Relatedly, the definition of the analyzed interval needs careful reconsideration. Epochs are aligned to the participant's own speech onset and extend back 2.2 s, whereas a turn transition is accepted whenever self-onset falls between −1 and +1 s relative to partner offset.

Therefore, the interval from −2 to 0 s relative to self-onset is not necessarily an interval during which the partner is continuously speaking. For positive response latencies, part of this interval contains silence following partner offset. If the preceding partner IPU is relatively short, earlier portions of the epoch could potentially contain a different conversational state altogether. Yet the manuscript describes the whole pre-onset period as being "while they are listening to their partner."

This matters particularly for the comparison between the early and late periods. Different response-latency conditions will necessarily place the partner offset at systematically different positions within an epoch aligned to self-onset. The authors already demonstrate this problem for the anterior latency ERP, where its inflection tracks the distribution of partner offsets. This is an important observation, but I do not think the problem is restricted to that single component.

The authors should quantify, separately for TW1 and TW2, how much time is occupied by: active partner speech, silence after partner offset, overlapping speech, and potentially other conversational states.

I would strongly recommend repeating the critical analyses for periods/trials during which the partner is actually speaking, and/or explicitly modeling partner-speech presence and the temporal distance to partner offset. Analyses aligned with both partner offset and self-onset would also help separate responses to the conversational boundary from activity specifically preceding self-production.

(3) The Early-versus-Late Planning hypotheses are not sufficiently differentiated

I was confused by the theoretical contrast (e.g., Lines 53-62). The Early Planning account is described as proposing that response preparation begins once sufficient information is available, whereas the Late Planning account explicitly allows "some aspects of conceptual preparation" during listening but proposes that full articulatory planning is delayed until near the turn boundary.

Under these definitions, both hypotheses allow for early planning. They differ mainly in the level of production planning that occurs early, that is, conceptual/content preparation versus articulatory/motor preparation. This is quite different from a simple early-versus-late timing hypothesis.

This is problematic because the current EEG measures do not determine whether the early activity reflects conceptual planning, lexical formulation, articulatory planning, comprehension, or general cognitive demands. Indeed, the authors explicitly acknowledge this later. Consequently, observing EEG-behavior relationships 1 s before speech cannot adjudicate between the two hypotheses as currently formulated.

The theoretical framework should therefore distinguish explicitly among at least: conceptual/message planning → linguistic formulation → articulatory/motor preparation → initiation.

If the "Late Planning" hypothesis specifically concerns late articulatory planning, then the authors need evidence that distinguishes articulatory planning from earlier conceptual processes. Otherwise, I would describe the findings more conservatively as showing early behavior-related neural activity followed by stronger onset-proximal sensorimotor activity, rather than claiming that Early and Late Planning accounts have been reconciled.

(4) Response duration is not equivalent to the amount or content of a response that has already been planned

The strongest empirical finding concerns upcoming speaking duration. I agree that this is interesting. However, throughout the Discussion, duration is gradually interpreted as the "extent," "scale," or even the amount of content already prepared. For example, the authors argue that longer responses involve maintaining a larger set of propositions, lexical items, or planned sequences. Figure 8 goes even further and explicitly contrasts "High Content" and "Low Content," although no measure of speech content has been analyzed.

I do not think response duration alone supports this inference.

A 2-s utterance is not necessarily twice as much planned content as a 1-s utterance. Duration can vary because of speech rate, hesitations, lexical retrieval, syntactic formulation, repetitions, interactive feedback, or decisions made after speech has already begun. An eventual IPU duration is therefore not necessarily specified before articulation.

This issue is especially important because the manuscript explicitly acknowledges that the analyses cannot establish whether the signals encode lexical or semantic content. It is then inconsistent to conclude later that early activity supports "what and how much to say."

Since transcripts are available, the authors could directly test several alternatives: word count, content-word count, number of propositions, speech rate, syntactic complexity, semantic similarity between partner and self turns, and possibly dialogue-act categories. If the early signal predicts eventual linguistic content/amount rather than merely duration, the claim of maintained response specification would become considerably stronger. If not, the interpretation should remain at the level of response duration.

(5) The ROI/time-window linear mixed-model (LMM) analysis appears circular

I have a methodological concern about the relationship between the cluster analyses and subsequent LMMs. The authors first identify electrodes and time ranges showing significant differences between long versus short responses or fast versus slow responses. They then use those same data-driven clusters to define anterior/posterior ROIs and TW1/TW2 and extract EEG values from the same trials, after which the extracted EEG measures are tested as predictors of the same behavioral variables.

This creates a potentially serious double-dipping/selection bias problem. The continuous LMM outcome is not statistically independent of the median-split outcome used to select the neural features. FDR correction at the LMM stage does not correct for this feature-selection procedure.

I think the confirmatory analyses need independent feature definition, for example, predefined electrodes/time windows from previous literature, split-half analysis, leave-one-participant-out feature selection, or another cross-validated procedure in which the data used to identify the ROI/window are independent from those used to estimate and test the EEG-behavior relationship.

This is particularly important because the LMM results are used as evidence that the effect survives behavioral covariates. That conclusion should come from statistically independent tests.

(6) Several statistical and validation issues need additional attention

There are several related concerns here. First, the trial-level LMMs include only (1 | participant), despite the fact that the observations come from dyadic interactions, multiple 4-min conversations, and temporally adjacent conversational turns. Participants within the same dyad do not generate independent observations because the speech of one participant directly determines the context for the other participant. I would expect the hierarchy to include at least a dyad/conversation block, and random slopes for critical within-participant predictors should be considered. Robustness to conversational autocorrelation should also be examined.

Second, the authors describe response duration as approximately log-normal, but the model description indicates only centering/scaling rather than transformation. The authors should report residual diagnostics and consider modeling log-duration or using an appropriate non-Gaussian mixed model.

Third, the decoding uses stratified 10-fold cross-validation, but it is unclear how conversational dependence is handled. Randomly assigning turns from the same 4-min conversation to training and testing sets may permit classifiers to exploit slow neural states, discourse context, or block-specific characteristics shared by temporally adjacent turns. A more convincing analysis would use blocked cross-validation, such as leave-one-conversation/run-out. The authors should also clarify whether decoding is performed independently within participants and whether median thresholds are participant-specific or global.

These analyses are particularly important because temporal generalisation establishes stable predictive information, but not the functional identity of that information. A stable partner-speech/context signal could also produce a broad temporal-generalisation pattern.

(7) ERP baseline correction and potential speech/muscle contamination require clarification

The ERP preprocessing raises another concern. ERPs were baseline corrected using the entire −2200 to +500 ms epoch. This interval includes the first 500 ms after self-speech onset, the period most vulnerable to speech-related muscular activity. Because the main grouping variable is upcoming response duration, post-onset activity may itself systematically differ between long and short responses. Subtracting a baseline that includes this activity could introduce condition-dependent shifts in the pre-speech ERP.

I therefore think the critical ERP results should be demonstrated without using post-speech activity in baseline estimation, for example, by using an appropriate pre-speech/regression-based baseline strategy, or by analyses demonstrating that the result is insensitive to baseline choice.

There is also an intriguing inconsistency concerning EMG. The participant section states that facial hair was an exclusion criterion to ensure electrode contact for EMG recordings, whereas the Limitations section suggests that combining EEG with EMG would be useful in future work. If EMG was in fact recorded, it should be described and, ideally, analyzed to establish when peripheral speech preparation begins and whether the onset-proximal alpha/beta results remain significant after controlling for muscle activity. This would be particularly valuable for the proposed late "motor commitment" interpretation.

Reviewer #2 (Public review):

This is an excellent paper, well researched, correctly referenced and very well presented. The main addition to the existing literature, apart from supporting earlier results (see also Roberts et al. 2015), is the ability to detect the length of the upcoming conversational contribution from the neural signal. This is interesting because it shows very early and sustained planning of response during listening to the incoming turn from the interlocutor. Why is that interesting? Because this simultaneous listening and response planning is utilising the very same mental machinery - a kind of dual-tasking that humans generally find very hard, given extreme capacity constraints on short-term and working memory. This then talks to the issue of whether speech production and comprehension are more independent than current theory holds. Clearly, human language is one of the elite skills of the species, but this dual-task ability in just this domain may be a specialization evolved over deep evolutionary time. I would like to see this background sketched more clearly in the introduction - it would make the paper of more interest to the general reader.

The other main contribution is methodological, namely the ability to extract meaningful EEG out of unconstrained verbal interaction, using, e.g. machine learning to filter out movement artefacts. Earlier work was held back by scepticism that this was possible, but this paper points clearly to one way to do this. A further contribution is the suggestion that Beta modulation is associated with the duration of the turn under planning, while Alpha modulation was in addition associated with preparation for execution. This needs to be tested in further studies, but could be a valuable addition to the analytical armoury.

In the final discussion, a conceptual model is outlined in Figure 8. This looks very similar to that given in Levinson & Torreira 2015 and Levinson 2016 - at least if there is a difference, it would be good to see it clarified. Note that in that model we hypothesized that preparation of the upcoming turn was continued right up to completion and then held if necessary for ending cues from the interlocutor. Note that quite late delivery preparations have been noted both in Torreira et al. 2015 (breathing signal) and in Bögels & Levinson 2023; in the latter, there is evidence of tongue preparation sometimes occurring not tied time-wise to delivery (suggesting inhibition till incoming turn is ending). So our model already had an early and late component - the news here is that the early component can be robustly discerned in naturalistic verbal interaction.

Also, in the discussion, the Pickering & Garrod IAM model is favourably discussed, even though that model imagines the production machinery is used to predict the unfolding comprehension of the incoming turn: in that case, the production machinery would have to be doing two things at once - doing comprehension and planning one's own turn. In a way, the main lesson of the findings of the submission is precisely that this is implausible.

In general, I have no hesitation recommending publication of an important contribution to the neuroscience of human performance in ecologically more valid settings.

References:

Bögels S, Levinson SC. Ultrasound measurements of interactive turn-taking in question-answer sequences: Articulatory preparation is delayed but not tied to the response. PLoS One. 2023 Jul 5;18(7):e0276470. doi: 10.1371/journal.pone.0276470. PMID: 37405982; PMCID: PMC10321606.

Griffin, Z.M. and Bock, K. (2000) What the eyes say about speaking. Psychol. Sci. 4, 274-279.

Levinson SC. Turn-taking in Human Communication--Origins and Implications for Language Processing. Trends Cogn Sci. 2016 Jan;20(1):6-14. doi: 10.1016/j.tics.2015.10.010. Epub 2015 Dec 1. PMID: 26651245.

Levinson SC, Torreira F. Timing in turn-taking and its implications for processing models of language. Front Psychol. 2015 Jun 12;6:731. doi: 10.3389/fpsyg.2015.00731. PMID: 26124727; PMCID: PMC4464110.

Roberts SG, Torreira F, Levinson SC. The effects of processing and sequence organization on the timing of turn taking: a corpus study. Front Psychol. 2015 May 13;6:509. doi: 10.3389/fpsyg.2015.00509. PMID: 26029125; PMCID: PMC4429583.

eLife Assessment

This important study provides theoretical and experimental evidence that aliphatic-to-threonine substitutions in transmembrane domains improve the translocation properties of mitochondrial proteins from the cytosol to mitochondria. The authors provide convincing evidence that substitutions within hydrophobic transmembrane regions of mitochondrial proteins may have contributed to their evolutionary adaptation following the transfer of their genes from the mitochondria to the nucleus. This study will be of interest to biologists and biochemists working on mitochondrial protein import and mitochondrial evolution.

Reviewer #1 (Public review):

In this manuscript, Yadav and coworkers investigate hydrophobicity governing membrane insertion of mitochondria-encoded polypeptides. The basis of their considerations is the question of why mitochondria maintain a co-translational insertion mechanism and what rules allow allotopic expression. The issue if mitochondrial-encoded proteins can be expressed in the cytoplasm and imported into mitochondria is a long-standing topic in the field with broad implications for the treatment of mitochondrial disorders. In the manuscript, Yadav et al. propose that aliphatic-to-threonine substitution (ATS) are a recurrent and convergent adaptation in the transmembrane helices (TMH) of the inner mitochondrial membrane (MIM) proteins, solving the conflict between hydrophobicity required for membrane insertion and the need for soluble cytosolic transit. The study combines structural comparative genomics, MD simulations, and cellular experiments.

This is a well-written and highly interesting study that provides a solid basis for considerations regarding mitochondrial protein insertion. I am sure that the study will represent an important asset for future studies on allotopic protein expression and potentially the development of genetic tools. The study provides solid evidence, from evolutionary correlation to experimental manipulation and molecular-level explanation. The study provides abundant and well-thought-out controls.

Specific points

(1) There are multiple comparisons throughout the manuscript, and not all of them appear to have been explicitly corrected. Numerous Wilcoxon tests, t-tests, and ANOVAs are reported (Figures 2, 3, 4), without a systematic correction for multiple testing or clear mention of FDR/Bonferroni corrections, except for the directional analysis of substitutions, for which the Benjamini-Hochberg procedure was applied. Given the large number of pairwise comparisons in Figures 3 A-C; and Figure 3 Supplement 1, Supplement 2, Supplement 4, and Supplement 5, with dozens of p-values per panel, it would be relevant to clarify whether a multiple-testing correction was also applied in these analyses. If not, the authors should explain the rationale for not applying one.

(2) The authors used experimental structures as one criterion but, in other cases, AlphaFold2 to compare evolutionarily distant pairs. Using non-experimental structures as a base for structural alignment among very divergent proteins is understandable but also prone to errors, especially for membrane proteins. It might wrongly identify which helices are considered "related". To address this, the authors need to clearly indicate which data are based on experimental or computational data - this is not always the case.

(3) The Kyte-Doolittle hydrophobicity scale is standard but relatively raw in comparison with scales based on experimental insertion energy (like Hessa et al., cited in the text or Bothelo et al.). It might be useful to explain why the authors preferred K-D over an experimental membrane insertion scale for the analysis. Particularly, since the Hessa et al. scale was later used in Figure 8G for the thermodynamic analysis.

(4) The phylogenetic tree of ATP6 (Figure 5A) presents low bootstrap values in some internal nodes (43, 40, 55) on which the interpretation of "independent events" of genetic transfer relies. This must be discussed, since a bootstrap of 40-50% provides not too much confidence in the deep topology of the tree, even though the point that the nuclear sequences don't form a monophyletic group with the mitochondrion seems robust (supported by distinct MTS in each clade).

(5) Definition of "core" vs "peripheric" in TMH (11 central positions) seems arbitrary; it would be worth clarifying why that cut was chosen and whether the results are robust when they vary.

(6) There is a notable gap in the literature when describing some of the findings in the Results and Discussion section:

Biophysics of threonine/serine in TMH:<br /> Senes et al., 2004, Dawson et al., 2002. The result described in Figure 8 (Threonine rotamers) is essentially a biophysical refinement of a body of work already established by the Engelman and DeGrado labs about how Ser-Thr, in comparison with other polar residues, promotes specifically the packing and stability of TMH through intra-inter helical hydrogen bonds, without compromising the membrane insertion. Chamberlain & Bowie, 2002 was included (C-H bonds), and Hessa et al. 2005 (energy of insertion), but no reference was included about why Ser/Thr are polar amino acids "tolerated" at the hydrophobic core of TMH, which is the state the authors describe.

In the argument about why TMH hydrophobicity matters for targeting (not only for membrane insertion), there is much more direct and recent mechanistic work that should be included: Botelho et al., 2011 established experimentally the hydrophobicity threshold for the "stop-transfer" pathway of TIM23 with quantitative data in an analogous way as reported in this work. Lee et al., 2020 and Yang et al., 2025 described structurally how hydrophobicity of the substrate modulates the Mgr2-Tim17 interaction to allow precursors to be embedded within the membrane.

It may be helpful to consider previous published work as an important precedent for the discussion of TMH hydrophobicity and TIM23 in allotopic expression. The final observations of incomplete mitochondrial localization despite reduced TMH hydrophobicity could also be discussed in light of previous published studies. These studies suggest that hydrophobicity is an important factor, but not the only determinant of efficient mitochondrial targeting. The role of TMH hydrophobicity in mitochondrial import had already been explored in this context. This would help clarify how the current findings build upon the existing literature.

Reviewer #2 (Public review):

Summary:

The paper by Yadav et al. provides compelling theoretical and experimental evidence for an aliphatic-to-threonine substitution (ATS) in the transmembrane helices (TMs) of membrane proteins residing in the inner mitochondrial membrane (IMM) across several species. Furthermore, using ATS, they designed variants of the human Atp6 subunit and of Atp6 subunits from other species that seem to be internalized into mitochondria.

Strengths:

In general, the results support the conclusions. The findings are particularly relevant to the field of allotopic expression and could have significant implications for the future development of gene therapies for mitochondrial disorders.

Weaknesses:

The manuscript could be substantially strengthened by the addition of further experimental evidence and by some minor revisions and adjustments to the interpretation and presentation of the results.

Major Points

(1) The protein product of atp6 is an essential component of the proton channel of ATP synthase, and more than a dozen pathogenic mutations in this gene have been associated with mitochondrial diseases. Accordingly, several studies have reported attempts to achieve allotopic expression of Atp6 in human cells. I would dedicate a pair of paragraphs in the Discussion to acknowledging the most relevant of these previous efforts. Here, in the work of Yadav et al., several Atp6 constructs were detected within mitochondria by fluorescence microscopy. However, no direct evidence was provided that the allotopically expressed Atp6 protein was incorporated into complex V. Localization within mitochondria, by itself, does not demonstrate successful allotopic expression in the functional sense, as the protein could remain unassembled, inserted in an incorrect topology, or in a process of degradation. In my view, this is the main weakness of the present study. A convincing demonstration of allotopic ATP6 expression should ideally be supported by biochemical evidence showing that the imported subunit is stably incorporated into ATP synthase and, most importantly, contributes to its function. This would require demonstrating at least partial restoration of the respiratory or OXPHOS defect.

I therefore encourage the authors to test their different constructs in cybrid cells carrying a pathogenic mutation in the mitochondrial atp6 gene and determine whether they can restore OXPHOS function or, at a minimum, respiratory capacity. Such an experiment would provide substantially stronger evidence that the imported Atp6 protein is not merely localized to mitochondria but is functionally incorporated into ATP synthase. Alternatively, Blue Native PAGE of mitochondria isolated after allotopic expression of the different constructs, followed by second-dimensional SDS-PAGE, could provide direct evidence that a tagged Atp6 subunit has been incorporated into the ATP synthase complex. Furthermore, this experiment could provide a valuable functional comparison of the three ATS constructs (T1, T2, and T3) and identify which one is most effective in restoring function. Importantly, the T3 construct, despite carrying the highest level of ATS, may not necessarily be the most effective in increasing the levels of assembled ATP synthase or in restoring ATP synthase activity.

(2) I do not agree with the interpretation of the results presented in Figure 7 - Figure Supplement 3, "Targeting tracks with hydrophobicity, not expression." I am concerned that the experimental design may be biased. The two most highly hydrophobic proteins (WT and T1), which are expected to have greater difficulty being imported into mitochondria, were selected for low-level expression. In contrast, the two constructs with extensive ATS (T2 and T3) were expressed at high levels. The hydrophobicity effect and the expression levels are confounded in this experiment, making it difficult to determine whether the observed targeting differences are attributable to one of these parameters. To disentangle these effects, this experiment should be repeated using both low and high expression levels for all four constructs, resulting in eight experimental conditions (four constructs x two expression levels).

Reviewer #3 (Public review):

Yadav et al. revisit the old conundrum of why certain genes encoding inner mitochondrial membrane (IMM) proteins are retained in the mitochondrial genome (mtIMMs; 13 genes in humans) while genes encoding other IMM proteins (nuIMMs) have been relocated to the nuclear genome during evolution. It was noted already in 1986 that nuIMMs have transmembrane helices (TMHs) of lower hydrophobicity than mtIMMs (FEBS Lett 198:1). A number of subsequent studies have shown that some mtIMMs can be converted to nuIMMs by appending a mitochondrial targeting sequence (MTS) and, in most cases, reducing the hydrophobicity of one or more of the TMHs (reviewed in Genes & Dis 7:578). Conversely, increasing the hydrophobicity of a TMH in a nuIMM protein can prevent its import into mitochondria (e.g., PNAS 99:10510). Whether the reduction in TMH hydrophobicity in nuIMMs is mainly driven by the need to bypass cotranslational targeting of the protein to the ER and trafficking along the secretory pathway, or to prevent the protein from being prematurely stuck in the IMM during mitochondrial import, is still, to some extent and open question, and experimental support for both possibilities exists (e.g., FEBS Lett 591:65).

Yadav et al. present an extensive bioinformatics study which nicely confirms the reduced hydrophobicity of nuIMM TMHs compared to mtIMM TMHs (and also compared to TMHs in proteins that traffic along the secretory pathway). The study is based on a lot more sequence data and many more kinds of comparisons than previous publications, and leaves little doubt that the reduction in hydrophobicity in nuIMM TMHs is real.

Based on their bioinformatics analysis, the authors also propose that aliphatic -> Thr substitutions (ATS) are the main driver of hydrophobicity reduction in nuIMMs, TMHs, and that Thr has been enriched also in mtIMMs. TMHs in organisms that depend only on Oxa1-type IMM insertases, possibly in order to reduce the aggregation propensity of these proteins when produced in the mitochondrial matrix. This is a novel hypothesis that has not been proposed in earlier work.

The authors additionally show that a mitochondrially encoded ATP6 protein can be converted into a nuclearly encoded, import-competent protein using ATS to reduce the hydrophobicity of its TMHs and, conversely, that import of a nuclearly encoded ATP6 protein is blocked when Thr residues in its TMHs are mutated to aliphatic residues. Similar findings have been published before; what is new is the use of aliphatic -> Thr substitutions (rather than other aliphatic -> polar substitutions).

Detailed comments:

While previous bioinformatics studies of how gene relocation from the mitochondrial to the nuclear genome impacts protein sequence have focused on TMH hydrophobicity, Yadav et al. expand this to include individual amino acid frequencies. The authors present four types of analyses:

(1) The authors identify E. coli homologs of the 13 genes retained in human mitochondrial DNA, do structure-based sequence alignments of the homologous pairs, and then compare the individual aligned TMH pairs in terms of hydrophobicity and Thr content. The authors also calculate an amino acid substitution matrix from the aligned TMH pairs. These data are presented in Figure 2 (and supplements).

Hydrophobicity is calculated based using the GRAVY algorithm and the Kyte-Doolittle scale, and by calculating the fraction of ALIVF residues. Both nuIMM and mtIMM TMHs are found to be significantly less hydrophobic than the E. coli TMHs (p ≈ 0.002). Thr is reported to be enriched in nuIMM and mtIMM TMHs relative to E. coli TMHs (as are Asn and Pro, while Val and Phe are reduced relative to E. coli TMHs, panel C). Panels F and G show an enrichment of Thr residues in nuIMMs of marginal significance (p = 0.02), and an enrichment in mtIMMs of higher significance (but the statistics are skewed by one mtIMM TMH that apparently contains almost 40% Thr residues). The substitution matrix in panel H indicates that aliphatic I, L, A, and G residues in the E. coli TMHs are often substituted by Thr and Val in the mitochondrial proteins. F does not show this substitution pattern, questioning the use of ALIVF counts in the analysis.

(2) The authors calculate hydrophobicities and amino acid frequencies for all human TMHs found in AlphaFold2 structures and grouped according to their cellular location: ER, Golgi, plasma membrane, nucleus, outer mitochondrial membrane (OMM), nuclearly encoded proteins in the inner mitochondrial membrane (nuIMM), and mitochondrially encoded proteins in the inner mitochondrial membrane (mtIMM). These data are presented in Figure 3 (and supplements).

OMM and nuIMM TMHs are significantly less hydrophobic than the secretory pathway TMHs, whereas mtIMM TMHs seem to have similar hydrophobicities as the secretory ones. nuIMM TMHs may have a slightly increased Thr content compared to secretory pathway proteins, but only one p-value is significant (Golgi vs nuIMM). mtIMM TMHs appear to have a higher Thr content than nuIMM proteins, but the statistics is skewed by a single point at a Thr fraction of 0.25. The Thr enrichment is less pronounced than for the E. coli comparison in Figure 2, Figure 3 Supplement. Fig. 8 shows that TMHs in chloroplast and mitochondrial plant proteins both have reduced hydrophobicity compared to ER-targeted proteins.

(3) Starting from the 66 mitochondrially encoded proteins in Jakobids, the authors identify homologous proteins that have become nuclearly encoded and carry an N-terminal mitochondrial targeting sequence (MTS) in organisms with smaller mitochondrial genomes. As in 1, the authors then do structure-based sequence alignments of the 63 homologous nuIMM and mtIMM TMH pairs found, and compare the individual aligned TMH pairs in terms of hydrophobicity and Thr content. These data are presented in Figure 4 (and supplements).

The reduction in hydrophobicity in nuIMM vs mtIMM TMHs upon relocation to the nucleus is robust and confirms earlier publications (panel C). The increase in Thr content in nuIMM vs mtIMM TMHs is less convincing (p = 0.012, panel G) and is opposite to what is seen in Figure 3C.

(4) By phylogenetic analysis, the authors identify three independent relocations of the ATP6 gene to the nuclear genome, do structure-based sequence alignments of nuIMM and mtIMM pairs representing these three events, and illustrate the reduced hydrophobicity of the TMHs in the nuclearly encoded proteins by hydrophobicity plots. These data are presented in Figure 5 (and supplements).

In panel C, it is not only aliphatic-to-Thr substitutions that reduce the hydrophobicity of the nuATP6 TMHs. How much is the hydrophobicity reduced if the Thr mutations are reversed (i.e., how much does the hydrophobicity reduction depend on ATS specifically and not on other kinds of substitutions)?

In a short experimental section, the authors go on to show that a mitochondrially encoded ATP6 protein can be converted into a nuclearly encoded, import-competent protein using ATS to reduce the hydrophobicity of its TMHs (but functionality is not tested) and, conversely, that import of a nuclearly encoded ATP6 protein is blocked when Thr residues in its TMHs are mutated to aliphatic residues (Figures 6, 7).

Finally, the authors carry out all-atom MD simulations to study the energetics of H-bond formation between Thr side chains and TMH backbone atoms.

In summary, the reduction in TMH hydrophobicity in nuIMMs compared to mtIMMs (and to secretory pathway membrane proteins) is robust and nicely confirms earlier studies. The purported enrichment in Thr content in both nuIMMs and mtIMMs has weaker statistical support in the data: p-values are typically > 0.01 (or may be skewed by an outlier) and appear not to have been corrected for multiple testing in all cases. As is clear from the ATP6 data in Figure 5, aliphatic -> Thr substitutions explain only a fraction of the overall hydrophobicity reduction in nuIMM TMHs, and the role of other hydrophobicity-reducing mutations in gene relocation could be better defined.

Author response:

We thank the reviewers for their careful reading of the manuscript and for their insightful comments. Several suggestions relate to a lack of clarity in our presentation, and others propose analyses that will strengthen the impact and robustness of the work. We outline our planned revisions below.

Reviewer 1:

We are grateful to the reviewer for appreciating the significance of our work for the treatment of mitochondrial disorders and its future implications in the development of genetic tools and protein design.

(1) Multiple testing

Figure 3A–C, Figure 3—figure supplements 1, 2, 4 and 5, Figure 6G and Figure 7F used one-way ANOVA with Tukey's post-hoc test, in which correction is intrinsic; the p-values shown are already adjusted. Our legends did not state this, and we will include this information in the revised manuscript.

We will apply Benjamini-Hochberg correction across all 400 comparisons, and as individual cells are likely underpowered, will also test aliphatic-to-threonine substitution at the level of residue classes, analogous to the directional analysis in Figure 4.

(2) Experimental versus predicted structures

We thank the reviewer for pointing this out. Our description here was not adequately clear. All structural alignments and compositional analyses used AlphaFold2 models; experimental structure availability was used only as an inclusion criterion for the compartment comparisons. We chose predicted models because experimental structures are frequently incomplete, which would bias residue composition. We will state this more prominently and add the source of the structure to the relevant legends.

(3) Hydrophobicity scale

We used Kyte-Doolittle for comparability with the prior literature on TMH hydrophobicity in relocated mitochondrial genes, and because it is additive by construction, which the mean-hydrophobicity analyses require. The Hessa scale is defined for insertion of a complete segment and carries substantial position dependence (PMID: 15674282). It is used in Figure 8G because that analysis plots single-residue transfer free energies, which is the scale's intended use and which Kyte-Doolittle, being a hydropathy index does not provide. We will state this rationale in the Methods and in the Figure 8G legend.

(4) Bootstrap support in the ATP6 tree

We agree that the low-support nodes warrant discussion, and we should have addressed it in the original text. These nodes (43, 55, 40) concern relationships among Porifera, Ctenophora and Cnidaria, which remain contested in analyses of far larger datasets (PMID: 41686647). The inference of independent relocation does not depend on them: the apicomplexan, chlorophyte and ctenophore sequences are separated by backbone nodes with 100% support. We thank the reviewer for noting that the distinct MTSs in each clade provide independent support, and we will state this explicitly along with an acknowledgement that values below 70 indicate unresolved relationships.

(5) Core versus peripheral definition

We sincerely thank the reviewer for pointing this out as our text was unclear regarding this. This was set using the ER TMHs, which provide the largest and best-powered set, and applied unchanged to all other groups. The window was chosen to give comparable numbers of positions in each bin, and so that core positions remain membrane-embedded despite helix tilt and uncertainty in the inferred helix midpoint, both of which are greatest near the termini. We will make the rationale explicit and add a robustness analysis at alternative window sizes, as recommended by the reviewer.

(6) Literature

We thank the reviewer for these references and agree they should be discussed. We will incorporate the role of Ser and Thr -containing motifs in TM helix association into the discussion of the biophysical properties of these residues. We will review relevant literature regarding hydrophobicity preferences of the TIM translocon in the context of competition between Sec61 and TIM/TOM insertion, together with the differences between insertion of proteins encoded in the mitochondrial and nuclear genomes. Further, we will also make a version of Figure 8G using the Bothelo and the Kyte-Doolittle scale.

Reviewer 2:

We sincerely appreciate the reviewer for their insightful comments, and for suggesting experiments to further strengthen the manuscript.

(1) Assembly and function of allotopically expressed ATP6

We agree that mitochondrial localization does not establish functional allotopic expression, and will revise the text so this is unambiguous in our manuscript. Our figures 6 and 7 test whether reduced TMH hydrophobicity allows a mitochondrially encoded protein to reach mitochondria when expressed from the nucleus. Assembly into complex V requires further constraints — correct topology, coordinated assembly with the c-ring, and stoichiometry with nuclear-encoded subunits — for which ATS may not be sufficient.

Following the reviewer's thoughtful suggestion, we will perform Blue Native PAGE to test whether the imported subunit is incorporated into ATP synthase and to compare the T1, T2 and T3 constructs. We will also add a Discussion section on topology as a distinct barrier and acknowledge the previous efforts at ATP6 allotopic expression.  As the reviewer anticipates, we expect that it can be challenging for the current constructs to be fully functional, but we will test this experimentally following the BN-PAGE assays. If we do not get successful incorporation, we will discuss this in the text as to what caveats may have caused this.

(2) Expression level confound

We appreciate with the reviewer’s concern regarding this panel. For context, we would like to point out that the conditions originally shown were chosen so that the comparison runs against our conclusion: the most hydrophobic constructs were expressed at low levels and the ATS constructs at high levels, so expression would be expected to work against the observed difference rather than produce it. We recognize that this rationale was not apparent from the figure.

To address this concern further, we have the remaining conditions in hand and will show all four constructs at both expression levels, as requested.

Reviewer 3:

We are very grateful to the reviewer for their thorough review of the manuscript and for providing constructive feedback.

(1) Statistical support for threonine enrichment

We take this point. The strength of statistical support varies across these comparisons, and we will report the p-values with the outliers removed, together with the corrections described under Reviewer 1 point 1. We note that the comparisons are constrained by the number of proteins available there are 13 mtDNA-encoded human IMM proteins, and the E. coli-human comparisons are limited to pairs with detectable homology.

(2) Enrichment of threonine relative to other residues

We will report the absolute residue compositions for the E. coli and human sets in a supplementary figure, and examine the relative enrichment of threonine, asparagine and proline more closely.

(3) Threonine content in Figure 3

The values in Figure 3C are Tukey-adjusted, and all pairwise comparisons are shown in Figure 3—figure supplement 1. The reviewer is correct that only the Golgi comparison reaches significance. Figure 2 compares each human TMH to its aligned E. coli counterpart, so each protein serves as its own control; Figure 3 compares means across unrelated proteins, where between-protein variation is large relative to the compositional difference. We will make this distinction clearer in the text.

(4) Hydrophobicity of mtDNA-encoded TMHs in Figure 3

The reviewer is correct that mtDNA-encoded IMM TMHs do not differ significantly in hydrophobicity from secretory-pathway TMHs. The compartment comparisons test proteins of shared nuclear origin with different destinations; the mtDNA-encoded group is shown for reference, as it differs in both genomic origin and biogenesis route. We will revise the text to specify which mitochondrial class the differences apply to.

(5) Direction of the Figure 3C and Figure 4G comparisons

We thank the reviewer for bringing this up. Our current text did not make it clear that these comparisons involved different organisms. The mtDNA-encoded proteins in Figure 4 are drawn largely from jakobids with large mitochondrial genomes, which retain extensive IMM biogenesis machinery and may face weaker constraints on TMH composition. Those in Figure 3C are the 13 human mitochondrially encoded proteins, which do face these constraints and are correspondingly threonine-rich. The apparent difference in direction reflects this rather than an inconsistency in the underlying trend, and we will make it explicit in the text.

(6) Contribution of ATS to hydrophobicity reduction

We are grateful to the reviewer for their insightful reading of potential evolutionary solutions to the targeting problem. We agree that ATS accounts for part rather than all of the reduction, and that the role of other hydrophobicity-reducing substitutions should be better defined. We will quantify the share attributable to aliphatic-to-threonine substitution, and for the ATP6 examples, report how much of the reduction remains when the threonine substitutions are reverted.

(7) ALIVF grouping

The reviewer is right for noting that phenylalanine does not show substitution towards threonine in the way the other aliphatic residues do in Figure 2H. Phenylalanine is nonetheless depleted in human mitochondrial TMHs alongside isoleucine, valine and alanine (Figure 2C), so the grouping is consistent at the level of composition even though the substitution routes differ. We will also discuss aliphatic-to-valine substitutions, which are largely hydrophobicity-neutral and so do not contribute to the reduction in the same way.

(8) Literature

We thank the reviewer for pointing out early attempts at understanding mitochondrial protein biogenesis and allotopic expression. We will incorporate these references into our discussion, specifically in the context of considering factors which could favor TIM/TOM over Sec61 insertion.

eLife Assessment

This study investigates the temporal dynamics of neural activity preceding self-initiated movements and makes a valuable contribution to this field. To overcome methodological and analytical limitations in previous work the authors introduce a matched control condition in which no response is required to assess when neural activity is predictive of self-initiated movement (using electro- and magnetoencephalography). Applying solid methods and machine-learning analyses, the authors show that a late-stage neural event is most predictive of upcoming movements (~100 ms before the response), whereas earlier neural activity is less informative. This finding contradicts previous work that suggested that earlier build-up of neural activity (e.g., starting 500 ms before the response) reflects the planning and preparation of movement.

Reviewer #2 (Public review):

Summary:

The authors set out to investigate how well the onset of a self-initiated movement could be predicted at different times prior to action onset. To do so, they collected EEG and MEG data across 15 human participants who watched natural landscape images on a screen. These participants performed active self-initiated movements, or observed passive actions, to have a new image appear. By comparing the neural activity prior to active and time-matched passive actions, the authors found that even though a build-up of neural activity is visible close to 1s prior to action, action onset could only be reliably predicted around 100ms prior to action. These results confirm what was already suggested in previous literature: the commitment to action is only clear from the late stages in the visible neural ramp-up to action onset.

Strengths:

(1) The paper presents a well thought out methodology to assess the predictive value of neural activity prior to a self-initiated movement and passively observed action, while keeping all other experimental factors identical. This methodology can be applied outside the specific scope of this paper as well, in efforts to assess the correspondence of a neural signature with an observed behavior.

(2) The results are a strong confirmation of what was suggested less clearly in previous research (Trevena & Miller, 2010, Consciousness & Cognition; Schmidt et al., 2016, Neuroscience & Biobehavioral Reviews; Travers et al., 2020, NeuroImage).

Comments on revised version.

I thank the authors for addressing my concerns in the Introduction and Discussion of their paper. I don't require any further edits at this point.

Author response:

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

Public Reviews:

Reviewer #1:

Summary:

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

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

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

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

We thank the reviewer for this thorough summary and for providing the opportunity to clarify our claims in light of the concerns identified by this review. Our key claim we make is not that there are no early signals. Rather it is that the well-known and reliable signals (e.g. the RP) that could be construed as evidence for early commitments do not have the characteristics of early commitment signals (i.e. they are not predictive). Based on our main results (Figure 3) we can classify the presence of those early signals using traditional approaches rather well (time-based approach), but when we control for autocorrelation in the data (task-based approach), this classification performance goes away – indicating that those particular signals might not contain movement or intention specific information. Further, we do have evidence that our paradigm was sensitive enough to detect small differences between the two conditions as is evidenced in Appendix 1, Figure 12 with above chance AUC right after trial start, a period during which participants likely recall the trial type (Active vs. passive). We have now added individual peak AUC to the figure to illustrate that our approach was sensitive to these differences (See Figure S12).

We do however fully agree that absence of evidence is not evidence of absence. We have therefore effected the following changes to mitigate misinterpretations of our results: Abstract: “…it was not useful in predicting movement.” “ “Our results substantially constrain the interpretation that early EEG antecedents, including the RP, reflect a commitment to act, instead indicating that EEG-detectable evidence consistent with such a commitment emerges closer to movement onset, in line with the timing of conscious intention and the capacity for late movement inhibition.

Introduction:

“We show that, once appropriate controls are introduced, there is little evidence that cortical EEG contains reliable predictive information much earlier than ~100 ms before movement. Those results better align with late-decision accounts, which posit that the final neural commitment to initiate movement arises very close to the time of movement onset, in the context of self-initiated movements that are not pre-planned.”

“[…] and at odds with the presence of predictive early signals indicative of a commitment to move – from the vantage point of cortical activity.”

Discussion:

“Instead, the data better align with the more recent late-decision accounts”

“We show here that the data, once properly controlled for, do not support this early neural commitment.”

“Importantly, the significance of these findings lies not in whether premovement neural activity exists, but in what that activity can legitimately be interpreted to reflect. Our results suggest that although early ramping activity precedes self-initiated movement, this ramping activity may not reflect a true commitment to initiate movement. Instead, they may reflect broader preparatory neural dynamics that bias action likelihood without determining action outcome. Importantly, our findings do not establish whether the relationship between premovement activity, intention, and action is causal or merely correlational. Rather, they constrain interpretations that equate the presence of early neural antecedents with evidence that a specific voluntary decision has already been unconsciously determined one or more seconds before movement onset.”

Figure S12

Added individual peak AUCs post slide appearance

Caption: “Individual peaks after the appearance of the slide are displayed as black circular dots in the figure.”

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

We agree with the reviewer that our data does not support the strong claim that there are no early signals. In particular, we agree that the absence of statistically significant decoding does not demonstrate the absence of any underlying signal, especially for potentially subtle effects. However, our central claim is more specific. We do not argue that no early signals exist, rather, we argue that signals previously taken to be evidence of early commitment to move (like the RP) do not exhibit the characteristics expected of a cortical EEG signature of commitment: namely being predictive.

The slow ramping that we observed, despite its early onset, was not reliably predictive of upcoming movement. It is precisely the contrast between the early presence of ERPs without reliable early decoding that supports our main claim that those signals do not reflect commitment-like processes.

Classifiers specifically designed to pick up the clearly observable slow ramping activity (e.g. basic-slope LDA in Figure 5) or trained on a large search space of features (e.g. Haar-Adaboost) failed to produce strong or reliable early decoding.

Importantly, Haar-AdaBoost was not restricted to slow ramping activity or the RP. Its feature space included spatial, temporal, and time-frequency information, allowing it to detect other potentially informative EEG features beyond slow ramping activity, including changes in spectral power. Our key claim is not that no early neural signals exist. Rather, we found little reliable early predictive information across a broad range of EEG features. Our classifiers were sensitive to slow ramping activity (like the RP), spatial patterns, and changes in spectral power, yet robust discrimination emerged only close to movement onset. Thus, any earlier commitment signal would need either to differ from the RP and the other features accessible to our analyses, or to be largely invisible to scalp EEG and MEG. We have revised the abstract and selected sections to clarify that our findings concern early predictive information detectable by our classifiers in EEG more broadly, including but not limited to the RP. These revisions do not rule out an early neural commitment represented in signals inaccessible to EEG or MEG or to our classifiers.

Abstract:

“Although early ramping activity was present, our classifiers found little reliable predictive information in the EEG until about 100 ms before movement, when classification accuracy rose abruptly.”

“Our results substantially constrain the interpretation that early EEG antecedents, including the RP, reflect a commitment to act, instead indicating that EEG-detectable evidence consistent with such a commitment emerges closer to movement onset, in line with the timing of conscious intention and the capacity for late movement inhibition.”

Introduction:

“Here, we introduce a paradigm that tests whether early antecedents detectable in EEG—including the RP, but not limited to slow ramping activity—distinguish epochs culminating in self-initiated movement from well-matched epochs not culminating in movement, thereby assessing whether early EEG activity contains reliable outcome-specific information consistent with a commitment to act.”

“Thus, the analysis was not restricted to the RP nor to other slow potentials, but could exploit temporal, spatial, and spectral differences throughout the EEG signal.”

Results:

“Our results show that the slow buildup observed in movement-locked averages was not reliably predictive under more carefully controlled conditions (i.e. when classified against a control condition using the task-based approach). More broadly, classifiers sensitive to diverse temporal, spatial, and spectral features found little reliable early predictive information in the EEG.”

Discussion:

“Our results cannot rule out the possibility of an early neural commitment that is undetectable in EEG or MEG. Rather, neither the RP nor slow ramping nor other early EEG/MEG features accessible to our classifiers exhibited reliable commitment-like predictability. Any earlier commitment signal would therefore need to be distinct from the RP and either largely invisible to EEG/MEG or too weak, distributed, or otherwise inaccessible for the present decoding methods to recover.”

Further, we agree that our study may be underpowered to detect extremely small early effects. However, several observations suggest that any such effects are weak and unlikely to reflect a robust commitment. First, the slight early above-chance decoding visible in Figure 3A is primarily driven by a small number of participants and disappears following outlier exclusion (Figure S7). Second, even when present, early decoding remained extremely weak (approximately AUC ≈ 0.52–0.55), far below the level expected from a stable neural commitment to a specific action outcome. Third, when examining the earliest time points at which single trials became consistently and continuously classifiable until movement onset (EDT analysis), decoding emerged only very close to movement onset (~100 ms on average, with the most extreme participant remaining below ~200 ms). This pattern was additionally replicated in the now-expanded Libet dataset (N = 8; Figure S4), despite early onset of low-decoding performance at the group level, single trials EDTs or non-outlier group onsets were also very close to movement onset.

Importantly, these conclusions were robust across multiple classifier architectures, parameter choices, and preprocessing pipelines. We additionally reprocessed the EEG data using a 0.05–80 Hz band-pass filter, a 58–62 Hz notch filter, and down-sampling to 512 Hz, following the reviewer’s recommendations (below). Although this preprocessing marginally increased early above-chance decoding, the effect again depended primarily on a single outlier participant (participant 6), and single-trial EDTs remained below ~200 ms even for the outliers (Figure S14). Excluding this participant eliminated the apparent early decoding.

We therefore agree that early signals may exist. However, our findings suggest that the classical premovement ramping previously interpreted as evidence for an early decision does not behave like a commitment signal. At best, the early decoding observed in outliers could reflect weak biases or task compliance rather than early commitments to a specific course of action. Our conclusions do not depend on proving the complete absence of early information. Rather, they depend on showing that the early signals traditionally invoked in support of early-decision accounts lack the reliability and predictive strength that would be expected if a neural commitment to act were represented by a stable EEG signal.

In addition to the changes presented earlier, we have made the following changes to the manuscript to accommodate the above:

Introduction:

“Although very weak sustained above-chance classification was observed at early time points (Figure 3), these effects were driven by outliers (Figure S7). Crucially, this above-chance classification does not provide evidence for a commitment to initiate movement. Instead, it indicates that upcoming movements can be weakly discriminated from a matched control condition only in a small subset of participants and trials. Moreover, classifiers trained exclusively on slow ramping activity performed comparably—but not better—during the pre-movement period (Figure 5).”

Results:

“…we could decode only slightly better than chance…”

“…could only be classified reliably very close to movement onset…”

“Indeed, once outliers were excluded, classification remained at chance until very close to movement onset (Figure S7).”

“This single-trial EDT suggests that commitment, defined as sticking to a course of action, arises only late in time, close to movement onset.”

“This single-trial EDT suggests that commitment, defined as sticking to a course of action, arises only late in time, close to movement onset.”

“Additionally, while ramping activity is observable in multiple participants (Figure S3) it disappears when a high-pass filter with a 0.1 Hz cutoff is applied (Figure S14). This suggests that the effect may be driven by very slow fluctuations, slower than typical anticipatory signals, and may therefore reflect non-neural or artifactual processes.”

Discussion:

“, when using a classifier based solely on these slow ramping signals (basic slope LDA), performance also hovered around chance levels before movement, indicating that early ramping activity is not predictive of upcoming movements (Figure 5).”

“Some readers may note a slight above-chance performance in early time windows (Fig. 3). However, this effect was driven by outliers (Fig. S7). Even when present, such weak performance (e.g., AUC ≈ 0.53) falls far short of what would be expected from a reliable neural signature of commitment. Moreover, analyses of EDTs derived from correct classifications at the single-trial level show that correct predictions emerge and are sustained only very close to movement onset. This indicates that the underlying predictive signal itself arises only late. Together, these results suggest that the signal supporting early classification is not commitment-like.”

“In our primary analyses, we deliberately avoided filtering to preserve even the slowest fluctuations in the signal. However, this choice may have allowed low-frequency noise to remain, potentially obscuring smaller effects. To address this possibility, we re-analyzed the data using a 0.05–80 Hz band-pass filter, applied a band-stop filter to attenuate line noise, and down-sampled the data to 512 Hz (rather than 500 Hz, to minimize loss of frequency information). The filtered analysis (Fig. S14) revealed broadly similar patterns, with two notable differences: the slow drift in the passive ERP was no longer present, and group-level AUC onsets (both by-eye and 90\% criteria) appeared earlier. However, these early onsets were driven by a single outlier (participant 6; figure S14). When considering mean EDTs at the participant level, or when excluding this outlier, onset estimates remained late (figure S14) and consistent with our main findings (Figure 3).”

New figure in the appendix Figure S14

New figure with filtered data

Caption: “Decoding performance and MRCPs from filtered EEG data. EEG data were sampled at 512 Hz to avoid loss of frequency content during downsampling. Line noise was attenuated using a 58–62 Hz band-stop filter, and signals were further filtered using a 0.05–80 Hz one-pass zero-phase FIR filter (FieldTrip, firws) to reduce artifactual activity. (A) Grand-average movement-related cortical potentials (MRCPs) at electrode C3 for active (blue) and passive (red) trials, aligned to slide transition (t = 0; dotted gray line). Shaded areas indicate the standard error of the mean. MRCP onsets are marked by dashed gray lines. (B) Grand-average time course of validation AUC (10-fold cross-validation) for the task-based decoding approach (blue line). The x-axis reflects the leading edge of the sliding window relative to slide transition (t = 0; dotted gray line). Shaded areas indicate the standard error of the mean. AUC onsets are marked by dashed gray lines. Despite early apparent onsets at the group level (AUC onset-by-eye and 90% method > 1 s before movement), classification performance remains near chance and does not exceed ~0.55 until close to movement onset. At the participant level, both AUC onsets and single-trial EDTs average -0.09 s. Excluding participant 6 shifts group-level AUC onset estimates to -0.44 s (by eye) and -0.32 s (90% onset method), indicating that early onsets are driven by outliers.”

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

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

Strengths:

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

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

Weaknesses:

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

We thank the reviewer for highlighting this important conceptual distinction. When proposing a matched control condition, the primary requirement was that the two conditions differ in the presence versus absence of a commitment to act. We argue that our two conditions (active vs. passive) satisfy this criterion. In the active condition, participants are instructed to execute a self-initiated motor action to advance from one slide to the next. In the passive condition, participants are not preparing or committing to any action during the slideshow.

We agree, however, that the two conditions are not matched in all other respects. Most notably, as pointed out by the reviewer, they also differ in the presence versus absence of movement itself as well as of accompanying movement preparation. As such, any differences observed between the conditions could in principle reflect motor-related processes, intention-related processes, or both. Importantly however, this ambiguity does not weaken our main conclusion. If early commitment-related signals were present and robust, they should still contribute to reliable discrimination between conditions. Yet despite the presence of visible premovement ramping activity in the averaged ERPs, classification remained weak and unreliable until very close to movement onset.

We have made the following changes to the manuscript accordingly:

Introduction:

“While the two conditions differ in the presence or absence of movement, they also differ in the presence or absence of an intention to move. As such, any early differences, if present, could reflect either motor-related or intention-related processes. However, this ambiguity is not a concern here, as we only observe differences at later time points.”

Discussion:

“A recent study (Derchi et al., 2023) contrasted volitional blinks with spontaneous blinks, thereby keeping the occurrence of movement constant while varying the presence of intention. Such an approach would avoid the movement-versus-no-movement contrast inherent to our paradigm. Importantly however, matching motor outcomes across conditions would likely make classification substantially more difficult, since motor-related information could no longer contribute to decoding performance.”

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

See our responses above regarding accepting the null. Also, we included an additional 5 participants to the Libet task (See updated Figure S4) to slightly improve our sample size. Although as previously stated in our manuscript, the number of trials matter more than the number of participants for a decoding study and with 1400 trials representing about 4 hours of data collection, should such early signals exist yet remain undetectable even with extensive trial counts and multiple decoding approaches, our results would suggest that EEG and MEG may have limited utility for studying them.

We have emphasized this point in our revised version of the manuscript:

Discussion:

“Some of our participants contributed up to 1400 trials, totaling up to 4 hours of data collection over 2 to 4 sessions in the EEG or MEG. Should such early signals exist yet remain undetectable even with extensive trial counts and multiple decoding approaches, our results would suggest that EEG and MEG may have limited utility for studying them.”

“[…] in eight additional participants and we found more or less identical results […]”

Figure S4:

Figure was updated to reflect an additional 5 participants

Caption updated to “AUC and ERP of Libet-task participants. Machine learning and ERP results for eight participants that we ran with a spontaneous movement initiation task based on Libet et al. (1983). (A) Readiness potential at Cz for the eight participants. In blue are the averages of the press trials and in red the averages of the no-press trials. Time 0 is the time of the trial end (dotted black line). Shaded areas are the standard errors of the mean. RP onsets using the 3 methods on press trials are reported and accordingly labeled (dashed grey lines) (B) Validation AUC for the eight participants using the task-based approach. Time 0 is the time of slide transition (dotted gray line). The AUC is aligned to the leading edge of the sliding window. Shaded areas are the standard errors of the AUC. AUC onsets using the three onset detection methods are reported and labeled accordingly (dashed grey lines). Our slideshow paradigm, while providing a more ecologically valid task, is agnostic as to the spontaneity of the participants’ movement decisions. To ensure that our task would generalize to more standard paradigms in the field of self-initiated action, we performed our analyses on data from a spontaneous voluntary movement paradigm based on (Libet et al., 1983). Here we collected eight further participants (4 female, 4 males, age M=24, 1 left-handed, 7 right-handed). They performed 350 trials of a task similar to the task performed by participants at OC except for the fact that there were no pictures, simply a fixation cross. Furthermore, the instructions for the manual trials were for participants to wait for a minimum of 3 seconds then start monitoring inwards for an urge to move. Whenever they detected such urge they were instructed to press as abruptly and spontaneously as possible, ending the trial. In the automatic trials, participants were instructed to do the same (monitor introspectively for an urge), except that they should not act on the urge if/when they felt it, but rather to wait for the next urge passively, and repeat such process until the trial ended automatically. This paradigm is much closer to the seminal studies on self-initiated actions (Libet et al., 1983; Kornhuber & Deecke., 1965). Here movements are performed spontaneously, and the matched condition (automatic) is identical in most regards apart from it not containing or terminating in a movement. All preprocessing and data analysis applied were the same. We found no strong qualitative difference with our main result (Figures 2A and 3A), suggesting that our task would generalize to other types of self-initiated actions.”

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

We did perform common average reference during the data preprocessing (lines 200-204 Slideshow2025/preprocess.m at main · lucasjeaybizot/Slideshow2025 · GitHub). We however clarified this description in the methods to clarify that this was performed offline:

Methods:

“We recorded EEG using a 64-channel BioSemi system keeping electrode offsets below 10 mV.”

The CAR was moved down for clarity.

“Data was re-referenced to the common average offline.”

In addition, the data is downsampled using a non-integer divisor of the original sampling rate (a 2,048 Hz dataset is downsampled to 500 Hz rather than 512 Hz). Downsampling using a non-integer divisor is not recommended and can lead to substantial artefacts in raw data as a result, as personally observed by this Reviewer in Biosemi data.

We had initially downsampled to 500 Hz to keep our analyses consistent from PF to OC. However, this is a very valid point, we have therefore re-analyzed the data using a downsampling to 512 Hz. Results did not change qualitatively nor quantitatively. Descriptions can now be found in the new supplementary Figure S14 and as referenced in the main manuscript (see changes below).

Discussion:

“In our primary analyses, we deliberately avoided filtering to preserve even the slowest fluctuations in the signal. However, this choice may have allowed low-frequency noise to remain, potentially obscuring smaller effects. To address this possibility, we re-analyzed the data using a 0.05–80 Hz band-pass filter, applied a band-stop filter to attenuate line noise, and downsampled the data to 512 Hz (rather than 500 Hz, to minimize loss of frequency information). The filtered analysis (Fig. S14) revealed broadly similar patterns, with two notable differences: the slow drift in the passive ERP was no longer present, and group-level AUC onsets (both by-eye and 90% criteria) appeared earlier. However, these early onsets were driven by a single outlier (participant 6; figure S14). When considering mean EDTs at the participant level, or when excluding this outlier, onset estimates remained late (figure S14) and consistent with our main findings (Figure 3).”

Finally, although a 30 Hz low-pass filter is applied for visualisation purposes of ERPs, no such filter is applied prior to analyses, and no method is used to account for alternating current noise that is likely to be in the data. As noted above, much of the alternating current noise will be retained when an offline reference is not applied, and this is likely to further degrade the quality of the data and reduce one's ability to identify subtle patterns in EEG signals. Changes in data processing to address these issues would likely lead to more precise estimates of EEG signals (and by extension differences across conditions).

In order to assess whether line noise or the absence of filtering in our main analyses could explain the absence of strong early decoding, we re-processed our data with a low pass filter at 80 Hz, a high pass filter at 0.01 Hz and a notch filter from 58 to 62 Hz. We further downsampled our data from 2048 Hz to 512 Hz to maximally retain spectral features. We then ran this preprocessed data through our algorithm. These changes are all comprised in new figure S14 and described above (see response to previous comment).

With regard to possible effects extending hundreds of milliseconds before the response, it would be helpful for the authors to more precisely clarify the time windows associated with 'early' and 'late' theories in this case.

We agree this is a very important clarification for the readers and as it stands is only implied in the literature. We now formalized it as follows, an early signal is a signal that would precede the time participants become aware of their intentions to move. In the case of self-initiated action, a recent meta-analysis suggests the lower bound of the 95% predictability intervals lands at -257 ms (Braun et al., 2021).

We have made the following modifications to the manuscript to reflect this definition:

Introduction:

“According to early-decision accounts, decisions (i.e., commitments to a course of action) occur early at the neural level, before participants typically report becoming aware of them. The lower bound of meta-analytic estimates of awareness, at ~250 ms before movement onset (Braun et al., 2021), can be used as a pragmatic threshold to classify neural signals as “early” (more than 250 ms before movement onset) or “late” (less than 250 ms before movement onset).”

“[…] well in advance, prior to the typical range during which participants report becoming aware of having decided (Braun et al., 2021).”

“[…] in time to movement onset, during the typical range during which participants report becoming aware of having decided (Braun et al., 2021).”

Discussion:

“Early-decision accounts posit that there is an early neural commitment to a decision that occurs prior to the subjective awareness of the decision.”

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

We thank the reviewers for pointing out a set of two very pivotal assumptions in our work: early models predict that there are early commitment signals and that those signals both, (1) precede the subjective experience of the decision and, (2) are highly specific to the decisions’ outcome.

Assumption (1) rests on a set of findings that participants report being first aware of their decision up until very close to movement onset (Libet et al., 1983) which, according to a recent meta-analysis occurs up to around ~250 ms before movement onset (Braun et al., 2021). It is additionally supported by a large corpus of literature on movement inhibition: participants can inhibit their movement up until within ~225 ms from executing them (Vergbruggen et al, 2019). A similar time is also reported specifically for self-paced arbitrary movements (Schultze-Kraft et al., 2016). As such we take it that early-decision accounts, to satisfy (1), predict the early signal to be present more than ~250 ms before movement onset.

Assumption (2) relates to the conceptualization of decisions. Early-decision accounts posit that decisions are made early. A decision can be viewed as an act of settling on a plan of action. That is, unless new information interferes, the plan of action that was settled on by the act of deciding will be carried out. Maintaining this settled plan of action until it is carried out implies that once a decision has occurred, its accompanying plan of action must be maintained somewhere in the brain. In other words, there should be a brain signal that could in theory be used to predict with high accuracy an upcoming action. While ‘high accuracy’ is a vague concept, another prediction is that it should be equally useful over time to predict the decision, in other words, once a trial begins being correctly classified, it should remain so until movement onset.

In our paradigm, evidence for early theories would therefore be EDTs (Figure 3B) that occur more than 250 ms before the slide transition.

We have added the following section to clarify this in our manuscript:

Discussion:

“Evidence for early accounts would require EDTs that occur earlier than the ~250 ms lower boundary of meta-analytic estimates of the subjective awareness of the decision (Braun et al., 2021). In our data, no participants' EDTs (Figure 3B) occurred earlier than 250 ms before slide transition. While AUC onsets computed on the group data did occur earlier than 250 ms (Figure 3A), this was driven by outliers (Figure S7) and not present at the individual level.”

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

The reviewer correctly describes the plotted data. However, it is important to note that because of two reasons (1 and 2 below), the concern of the onset of the AUC of the leading edge of the sliding window not reflecting the onset of the outcome-specific brain activity, can be substantially reduced. (1) The analysis we conducted is a sliding window, which means that an onset detected at -100 ms is above chance performance when classifying data taken from -600 to -100 ms but no such classification for the previous window from -620 to -120 ms. While this could mean that the entire window of activity was necessary for classification, it also suggests that only when incorporating data from the -120 ms to -100 ms window can the classifier perform above chance. (2) We used Haar features of different sub-window length combined with AdaBoost. AdaBoost selects the most informative features given the data, under this circumstance an increase in performance occurring only when including data from -120 ms to 100 ms indicates that data from that window was necessary for this increase in performance.

Additionally, to ensure more precision we now tested window of 250 ms and 100 ms (updated figure S11), the results of which align with what we previously report.

Discussion:

“Another potential concern is that predictive performance observed in wide sliding windows (e.g., -600 to -100 ms) could reflect information present as early as the beginning of the window. However, this interpretation is inconsistent with the temporal profile of decoding performance. For example, if the -620 to -120 ms window is non-predictive whereas the -600 to -100 ms window becomes predictive, the most parsimonious interpretation is that predictive information emerges near the newly included time points close to -100 ms, rather than being present throughout the entire window. This interpretation is further supported by the comparable performance observed across different window widths (figure S11), suggesting that the classifier was able to localize informative features within broader windows.”

Figure S11

Figure was updated to include analysis run with 250 ms window and 100 ms window Figure caption: “Evaluation of the sliding window widths. (A) Average validation AUC of Haar-Adaboost of the three participants of the PF EEG dataset using a sliding window (light blue) or growing window approach (pink) with the task-based approach. Time 0 is the time of slide transition (dotted gray line). The AUC is aligned to the leading edge of the sliding window. Shaded area is the standard error of the mean. A growing window analysis is similar to the sliding window analysis except that at each iteration, instead of sliding the window, the window width is increased by 0.02 s. This means that for an epoch beginning 3 s before movement, the window of analysis for the leading edge aligned to the slide transition would be 3 s wide from -3 s to 0 s (while for the sliding window method it would be 0.5 s wide from -0.5 s to 0 s). While it enables the capture of more patterns, it is a computation heavy analysis. To ensure that we were not missing out on some substantial longer-term patterns with sliding window, we ran a growing window on our PF EEG data. We found no improvement of using growing window over sliding window. (B) Average validation AUC of Haar-AdaBoost on the main OC EEG dataset using sliding windows of 100 ms (light blue), 250 ms (medium blue), and 500 ms (dark blue). Shaded areas represent the standard error of the mean. While clear classification differences emerged following movement onset, no substantial differences were observed prior to movement onset. This indicates that the 500 ms window was not too large to obscure finer temporal patterns. Furthermore, these results suggest that Haar-AdaBoost can identify localized informative features within larger windows, supporting the interpretation that the leading edge of the sliding window approximates the earliest time point at which predictive information becomes available.”

Reviewer #2:

Summary:

The authors set out to investigate how well the onset of a self-initiated movement could be predicted at different times prior to action onset. To do so, they collected EEG and MEG data across 15 human participants who watched natural landscape images on a screen. These participants performed active self-initiated movements or observed passive actions to have a new image appear. By comparing the neural activity prior to active and time-matched passive actions, the authors found that even though a build-up of neural activity is visible close to 1s prior to action, action onset could only be reliably predicted around 100ms prior to action. These results confirm what was already suggested in previous literature: the commitment to action is only clear from the late stages in the visible neural ramp-up to action onset.

Strengths:

(1) The paper presents a well-thought-out methodology to assess the predictive value of neural activity prior to a self-initiated movement and passively observed action, while keeping all other experimental factors identical. This methodology can be applied outside the specific scope of this paper as well, in efforts to assess the correspondence of a neural signature with an observed behavior.

(2) The results are a strong confirmation of what was suggested less clearly in previous research (Trevena & Miller, 2010, Consciousness & Cognition; Schmidt et al., 2016, Neuroscience & Biobehavioral Reviews; Travers et al., 2020, NeuroImage).

Weaknesses:

(1) Although the authors conducted a solid confirmatory study, the importance of this confirmation is less clear to me. How do the current results change our interpretation of the relation between conscious intention and neural preparation for action? Do these results affect our interpretation of free will? Why does it matter at all whether we see neural preparatory activity prior to the report of a conscious intention to act, or prior to action observation? This study does not clarify the relationship between the observed neural phenomenon, the action or the experienced intention. It does not explain whether this relation is causal, correlational or something else.

We thank the reviewer for their review. While it was previously suggested that the commitment to action comes late (Schultze-Kraft et al. 2016) and mechanisms were proposed to explain the early ramp-up in light of this late commitment (Schurger et al., 2012; Schmidt et al., 2016). Our main contribution is not merely confirmatory. Rather, our study introduces a matched control condition together with a classifier-based framework specifically designed to test whether early premovement activity is sufficiently predictive to qualify as a commitment-like signal.

Trevena & Miller 2010 differ largely from our approach, their control condition being matched for ‘decision’ but differing only in motor output. Their results are therefore still consistent with the RP being a decision-following signal. In contrast, our paradigm directly tests whether the early ramping activity reliably distinguishes epochs culminating in self-initiated movement from well-matched epochs not culminating in movement. Travers et al. 2020, while more directly testing the question of the specificity of the RP to self-initiated actions, provided ambiguous and contradictory interpretations, stating both that “[RP-like events] occur to the same degree in control data” and that “these events do not support the hypothesis that Readiness Potentials happen in the absence of action” with results allowing for multiple interpretations. Our study addresses this ambiguity directly by testing whether these early signals contain reliable outcome-specific information predictive of an upcoming action.

More broadly, while our findings are relevant to debates surrounding free will, our primary goal is neuroscientific rather than philosophical. Specifically, we address whether the signals traditionally interpreted as evidence for early decisions actually possess the properties expected of an early commitment signal. Our findings suggest that they do not.

Our data therefore invites a reinterpretation of the signals previously taken to challenge views of free will that require decisions to be made consciously. Specifically, the slow ramping signals traditionally interpreted as markers of decisions occurring very early in the brain do not exhibit the characteristics expected of a commitment-like signal. Rather than reflecting a stable and outcome-specific commitment to act, these early ramping signals may instead reflect broader preparatory dynamics that bias action likelihood without determining action outcome.

Our findings do not establish whether the relationship between premovement neural activity, intention, and action is causal or merely correlational. Addressing that question would require causal interventions beyond the scope of the present study. However, if early premovement activity were causally related to a settled commitment to act, one would expect it to contain strong and reliable predictive information regarding the upcoming action outcome. Our results do not support this account.

To clarify these points further, we have revised the manuscript accordingly and added the following text to the Introduction and Discussion sections.

Intoduction:

“Previous work showed that these early ramping signals were not specific to the outcome of a motor decision (Trevena & Miller, 2010). However, because their analyses remained time-locked to decision outcomes, they could not directly test whether the observed slow buildup specifically reflected a commitment-like process. Related work further suggested that RP-like patterns can emerge elsewhere in ongoing neural activity as features of spontaneous low-frequency fluctuations (Travers et al., 2020). Here, we introduce a paradigm that explicitly tests whether these early ramping signals distinguish epochs culminating in self-initiated movement, where a motor intention is present, from well-matched epochs not culminating in movement, where no motor intentions were present, thereby assessing whether they reliably reflect a commitment to act.”

Discussion:

“Our data therefore invites a reinterpretation of the signals previously taken to challenge views of free will that require decisions to be made consciously. Specifically, the slow ramping signals traditionally interpreted as markers of decisions occurring very early in the brain do not exhibit the characteristics expected of a commitment-like signal. Rather than reflecting a stable and outcome-specific commitment to act, this early antecedent ramp-like buildup may instead reflect broader preparatory dynamics that bias action likelihood without determining action outcome.”

(2) Whereas Derchi et al. (2023, Scientific Reports) were able to keep the entire experimental context similar across intended and unintended conditions, Jeay-Bizot et al. have one big difference between their passive and active conditions: the presence of a movement. Therefore, the present results explain the presence or absence of a movement rather than the presence or absence of an intention to act.

We thank the reviewer for pointing us to this very relevant and elegant paradigm introduced in Derchi et al., 2023. We agree that our active and passive conditions are not matched for movement itself, and therefore that any differences observed between these conditions could in principle reflect motor-related processes, intention-related processes, or both.

However, our primary goal was not to isolate a pure neural correlate of intention independent of movement, but rather to test whether the early premovement signals traditionally interpreted as markers of commitment contain reliable outcome-specific information predictive of an upcoming action. In that respect, the presence of an additional movement-related difference between conditions would be expected to increase, rather than decrease, decodability. Consequently, if reliable early commitment-like signals were present, they should still have contributed to reliable early classification performance in our paradigm.

More closely matching the motor output across conditions, as in Derchi et al. (2023), would likely make classification substantially more difficult by removing movement-related information from the decoding problem altogether. Importantly, despite movement differing between our two conditions, reliable decoding still emerged only very close to movement onset.

In addition to our modifications made with respect to a similar comment by reviewer #1 (see above), we have added the following paragraph:

Discussion:

“Our goal was not to isolate intention, but to test whether the signals traditionally interpreted as commitment signals actually possess commitment-like predictive properties. A recent study (Derchi et al., 2023) contrasted volitional eyeblinks with spontaneous eyeblinks, thereby keeping the occurrence of movement constant while varying the presence of intention. Such an approach would avoid the movement-versus-no-movement contrast inherent to our paradigm. However, matching motor outcomes across conditions would likely make classification substantially more difficult, since motor-related information could no longer contribute to decoding performance. More importantly, our paradigm is focused on the neural antecedents that are specific to whether or not a movement is initiated. This is a fundamentally different question from Derchi et al, which is focused on whether or not an intention is present. The two questions are complementary, however, and taken together, our study and the Derchi study contribute significantly to our understanding of spontaneous voluntary action.”

eLife Assessment

This study introduces a valuable simulation-based inference (SBI) framework to identify degenerate compensatory mechanisms that stabilize network activity despite neuronal hyperexcitability, a feature common to many brain disorders. By estimating posterior distributions of network parameters, the authors highlight factors such as threshold potential and interneuron-to-principal cell connectivity as key compensators for increased intrinsic excitability and interneuron loss. The approach is promising and can become a convincing tool for probing network degeneracy.

Joint Public Review:

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

Summary:

This manuscript couples a 32-parameter model with simulation-based inference (SBI) to identify parameter changes that can compensate for three canonical hyperexcitability perturbations (interneuron loss, recurrent-excitatory sprouting, and intrinsic depolarisation). The study demonstrates a careful implementation of SBI and offers a practical ranking of "compensatory levers" that could, in principle, guide therapeutic strategies for epilepsy and related network disorders.

Strengths:

(1) By analysing three mechanistically distinct hyper-excitable regimes within the same modelling and inference framework, the work reveals how different perturbations require different compensatory interventions.

(2) The authors adopt posterior estimation to systematically rank the efficiency of different mechanisms in balancing hyperexcitability.

(3) Code and data are available.

Author response:

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

Joint Public Reviews:

(1) The manuscript states that simulation-based calibration showed the amortized posterior estimator was unreliable (85-88), but these results are not shown. The manuscript explicitly states that simulation-based calibration demonstrated substantial failures of the amortized posterior estimator, yet the corresponding analyses are not presented. Since these results motivate the transition to sequential NPE and are central to assessing inference reliability, they should be reported quantitatively, either in the main text or supplementary material.

We agree and have therefore added the simulation-based calibration result as a supplementary figure.

(2) The authors present two independently trained estimators and show strong agreement between them. This is a useful robustness analysis. However, the rebuttal occasionally presents this as addressing concerns regarding cross-validation and generalization. The new analysis does not constitute cross-validation in the usual sense and does not directly assess generalization to held-out targets or posterior accuracy.

I recommend that the authors explicitly describe Figure 4 as a reproducibility analysis and avoid presenting it as a substitute for validation.

We are sorry for causing confusion with our response in the rebuttal. But we hope that the manuscript text is clearer than our rebuttal. We refer to the results as a “replication of the posterior estimator”. Regarding cross-validation, Figure 1 D shows additional simulations of posterior parameters that were not part of the training dataset.

(3) Posterior correlations are useful for generating hypotheses about compensatory mechanisms, but they should not be interpreted as direct evidence of compensation. The compensatory interpretation should instead be supported by the perturbation analyses (e.g., Figure 6), which provide mechanistic validation.

The manuscript consistently treats posterior correlations and conditional posterior shifts as direct evidence of compensatory mechanisms. These are consistent with compensatory mechanisms, but they do not by themselves establish that the corresponding biological parameters causally compensate for the perturbation. I recommend clarifying this distinction and emphasizing that the conditional posterior analyses generate hypotheses regarding compensation, which are then partially supported by the perturbation experiments shown later in the manuscript.

The language throughout the manuscript should therefore be softened.

We agree and have added hedging phrases to communicate the caveats of the results. For example, we now refer to “putative compensatory mechanisms” and adjusted the language in many other parts of the manuscript to highlight that our results provide estimates of mechanisms rather than the mechanisms themselves.

(4) The manuscript repeatedly suggests that the inferred conditional distributions may be useful for identifying precise interventions or guiding personalized treatments (examples include lines 24-29, lines 217-223, lines 242-246, lines 277-282, lines 283-286). These claims go beyond what is directly demonstrated.

The study does not evaluate treatment outcomes, patient-specific inference, intervention efficacy, or clinical decision-making. Rather, it demonstrates differences in inferred parameter distributions within a computational model. While these results are valuable and may generate clinically relevant hypotheses, they do not yet establish predictive utility for treatment selection or precision medicine. I therefore recommend substantially softening these translational claims and emphasizing that the current findings generate hypotheses that could be tested experimentally in future work.

You are correct. We are currently working to use our approach on patient data, but the present manuscript does not test the translational potential of the method and therefore some of our previous claims are unsupported. We have therefore deleted references to clinical potential in large parts of the manuscript and add qualifying phrases where we kept discussions of translational potential.

(5) The revised manuscript still mixes presentation of findings with interpretation.

For example, lines 217-226 largely continue to describe findings from Figure 6 and would fit better in the Results section. The Discussion would be strengthened by focusing more exclusively on biological implications, limitations, and future directions.

A similar issue appears later in the discussion comparing posterior correlations and conditional distributions. Much of this section effectively reinterprets Figures 2 and 3 rather than discussing broader implications.

We agree that the main function of the discussion is to put results into a broader context. But we also believe that repeating results at different levels of detail, different wording, and different interpretation can be to the benefit of some readers. We have therefore left the discussion largely intact except for the changes relating to above points 3 & 4.

(6) The discussion around lines 271-282 overstates what can be concluded from the inferred posteriors.

The statement that correlations "discover broadly applicable mechanisms" whereas conditionals "identify specific mechanisms" is stronger than the presented evidence supports. Likewise, the conclusion that conditional distributions are more useful for precision treatments is speculative and not directly demonstrated.

I recommend reformulating these statements as interpretations or hypotheses rather than conclusions.

We have deleted the reference to personalized treatment and refer to the mechanisms as “hypotheses” in other parts of the discussion.

(7) Around line 84, the manuscript introduces q(theta|x) without clearly defining θ, x, or q. Readers unfamiliar with SBI may struggle to follow the notation. All quantities should be defined when first introduced.

We have added definitions of theta and x. We hope that q is sufficiently defined when we call it the “posterior estimate”.

(8) The manuscript equates larger KS distances between conditional posteriors with greater compensatory potential. While KS distance provides a useful measure of posterior redistribution, it is not obvious that it should be interpreted as a measure of biological efficacy.

We hope that the changes described above make it clear that we view the KS distance as an estimate of putative compensatory mechanisms in the simulator, rather than direct measures of biological efficacy.

(9) The manuscript would benefit from a discussion of parameter identifiability. The inference problem maps 32 model parameters to 7 summary statistics, implying substantial nonidentifiability. While complete identifiability analysis is likely beyond the scope of the current work, this limitation should be discussed explicitly.

Non-identifiability is indeed an important aspect of simulation-based inference. We allude to it in the introduction where we mention degeneracy. But since we do not present results directly quantifying non-identifiability, we believe an explicit discussion goes beyond the scope of our manuscript.

All in all, the revised manuscript is significantly improved and addresses several concerns raised in the previous review. However, important issues remain as discussed above.

We thank you for the comments that led to the improved revision and for your constructive feedback on this revised version.

eLife Assessment

This is a very helpful study that presents an easy to use and reliable alternative to conventional and UV-based tetramers for the identification of antigen-specific CD8 T cells. The authors demonstrate that tetramers for a number of HLA alleles can be subjected to specific temperatures that facilitate peptide exchange whilst maintaining structural integrity, thereby generating detection reagents. They provide convincing evidence for this method, and the approach is likely to provide a useful alternative to generating reagents for examining T cell specificities.

Reviewer #1 (Public review):

Summary:

A fundamental technique for the identification of peptide-specific CD8 T cells is the use of fluorophore-conjugated and peptide loaded MHC tetramers. Classically, refolding of specific peptides with MHC monomers can be labour intensive, and not optimal for screening large numbers of different peptides. Hence, UV-exchanged tetramers have been developed to upscale this, however, still has some associated challenges such as UV-mediated damage to peptide complexes. Here, Pothast, C.R. et al demonstrate the efficacy of using temperature exchanged tetramers for the prevalent alleles HLA-A*03:01, A*11:01, B*07:02, and C*07:02. Building upon their previous work with HLA-A*02:01, H-2Kb, and HLA-E. They first demonstrate the complex stability of tetramers with different affinity peptides at high temperature, showing complex destabilisation can be rescued with higher affinity peptides. This is followed by an optimisation of peptide exchange temperatures, tailored for each allele. The authors then demonstrate successful binding to clonal T cell lines, and then a step further with viral peptides against PBMCs from individuals with confirmed infection history. For the latter they compare to conventional tetramers and demonstrate comparable signal.

Due to the prevalence of these 4 alleles, the ease-of-handling, and short time requirements, these tetramers are likely to show high utility.

Strengths:

The manuscript is well-written and results are solid, although more detail may add clarity to some of the results, in particular figure 1 and 2. Other than the points reported below, the study uses accurate controls to demonstrate the specificity of the tetramers, and the data is convincing.

Overall, their interpretation of the results is accurate and the discussion thorough, additional comments may be included to cover potential tetramer batch variability, and differences in the stability of different alleles. Specifically, whether certain alleles require higher affinity peptides to be stable, compared to others.

Comments on revised version.

The authors addressed the weaknesses highlighted in the previous version, specifically addressing that they do not conclude that thermal peptide exchange is not superior to existing technologies, but may be more feasible, as well as including a section on the stability of the different alleles and template peptides. The authors also updated the labelling and description of figures, making them much more interpretable. Addition of the LILRB1 reporter cell line to demonstrate successful peptide exchange and stability adds extra validity to the results.

Reviewer #2 (Public review):

Summary:

This work highlights a new approach to build an array of highly stable peptide MHC-I using temperature exchange, which can be used to identify antigen specific CD8+ T cells.

Strengths:

In this work, the authors have proposed an alternative method to reload the peptide MHC-I molecule. Their temperature-exchange approach is distinct from current reloadable peptide MHC technologies involving photolabile peptide, empty MHC-I (Nat Commun 11, 1314 (2020). https://doi.org/10.1038/s41467-020-14862-4), tapasin/TAPBPR chaperone-assisted (eLife 7:e40126.), enzyme exchangeable (https://pubmed.ncbi.nlm.nih.gov/31201791/) and small alcohol (Curr Res Immunol. 2022 Aug 18;3:167-174. doi: 10.1016/j.crimmu.2022.08.002) approaches

Weaknesses:

The temperature-exchange approach identifies antigen-specific T cells at the same frequency of the photolabile peptide MHC-I molecules. The time saved using temperature-exchange protocol may not be a pull factor as the photolabile peptide MHC-I approach is not unreasonably laborious.

As with other exchange systems, performance can vary by HLA allele and complex stability, so each new allele needs empirical optimization.

In short, temperature-based pMHC exchange is a practical and fast loading strategy with good utility for multimer generation, but its main limitation is dependence on thermal stability and careful template selection.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

A fundamental technique for the identification of peptide-specific CD8 T cells is the use of fluorophore-conjugated and peptide loaded MHC tetramers. Classically, refolding of specific peptides with MHC monomers can be labour intensive, and not optimal for screening large numbers of different peptides. Hence, UV-exchanged tetramers have been developed to upscale this, however, still has some associated challenges such as UV-mediated damage to peptide complexes. Here, Pothast, C.R. et al demonstrate the efficacy of using temperature exchanged tetramers for the prevalent alleles HLA-A*03:01, A*11:01, B*07:02, and C*07:02. Building upon their previous work with HLA-A*02:01, H-2Kb, and HLA-E. They first demonstrate the complex stability of tetramers with different affinity peptides at high temperature, showing complex destabilisation can be rescued with higher affinity peptides. This is followed by an optimisation of peptide exchange temperatures, tailored for each allele. The authors then demonstrate successful binding to clonal T cell lines, and then a step further with viral peptides against PBMCs from individuals with confirmed infection history. For the latter they compare to conventional tetramers and demonstrate comparable signal.

Due to the prevalence of these 4 alleles, the ease-of-handling, and short time requirements, these tetramers are likely to show high utility.

Strengths:

The manuscript is well-written and the results are solid, although more detail may add clarity to some of the results, in particular Figures 1 and 2. Other than the points reported below, the study uses accurate controls to demonstrate the specificity of the tetramers, and the data are convincing.

Overall, the interpretation of the results is accurate, and the discussion is thorough. Additional comments may be included to cover potential tetramer batch variability and differences in the stability of different alleles. Specifically, whether certain alleles require higher-affinity peptides to be stable, compared to others.

Weaknesses:

The authors demonstrate the equivalence of temperature-exchanged tetramers to conventional ones, however, as they are an advancement on UV-exchange, it would be useful to show data on how their stability, exchange efficacy, and binding to T cell lines compare to UV-based tetramers. It would be supportive to show that temperature does not impact fluorophore intensity as well.

Reviewer #2 (Public review):

Summary:

The majority of CD8+ T cell responses rely on the proper presentation of antigens through stable MHC-I (but not requiring a stable immunological synapse). This work highlights a new approach to build an array of stable peptide MHC-I using temperature exchange, which can be used to identify antigen-specific CD8+ T cells.

Strengths:

In this work, the authors have proposed an alternative method to reload the peptide MHC-I molecule. Their temperature-exchange approach is distinct from current reloadable peptide MHC technologies involving photolabile peptide, empty MHC-I (Nat Commun 11, 1314 (2020). https://doi.org/10.1038/s41467-020-14862-4), tapasin/TAPBPR chaperone-assisted (eLife 7:e40126.), enzyme exchangeable (WO2020226570) and small alcohol (Curr Res Immunol. 2022 Aug 18;3:167-174. doi: 10.1016/j.crimmu.2022.08.002) approaches.

Weaknesses:

However, the proposed temperature-exchange approach does not substantially improve the quality of antigen-specific T cells that can be identified using the photolabile peptide MHC-I molecules.

The time saved using the temperature-exchange protocol may not be a pull factor as the photolabile peptide MHC-I approach is not unreasonably laborious.

Reviewer #3 (Public review):

Summary:

The study by Pothast and colleagues outlines an extension of their previously described temperature-based MHC-I peptide exchange method on 4 common HLA alleles, to enable the generation of peptide/MCH-I tetramers for characterization of antigen-specific T cells by flow cytometry.

Strengths:

This work outlines a protocol for generating MHC-I tetramers on 4 common HLA allotypes, which can then be applied to monitor T cell responses by flow cytometry studies. The work provides conditional ligands for exchange on each HLA and demonstrates proof of concept studies using clonotypic T cells and CD8+ PBMCs.

The results support that the temperature-exchanged tetramers can perform similarly to conventional tetramers in some settings.

Weaknesses:

Given that there are several proposed methodologies addressing the same task (including UV-mediated, disulfide-bond based stabilization of empty MHC-I conformers, and chaperone-based methods), the relevance of the proposed temperature-mediated technology is questionable.

More specifically, important limitations of the study include:

(1) A lack of quantification of exchanged molecules relative to molecules that retain the original placeholder peptides, or completely empty molecules present in the same sample.

(2) A lack of validation that peptide exchange has occurred in the absence of a reporter T cell line appears to be a significant limitation of the methodology for antigen / T cell discovery.

(3) The sub-optimal exchange efficiency relative to conventional prepared pMHC-I molecules, shown in Figure 4, is a significant limitation of the approach.

(4) There are no data to support that exchange proceeds through the generation of empty molecules during the temperature cycle, or by peptide binding on empty molecules that are already present in the sample. Understanding the mechanism of exchange is important for the necessary improvements to the methodology.

(5) It is possible that the temperature cycle causes protein aggregation or other irreversible changes to the sample - this should be explicitly quantified and addressed in the paper, since misfolded MHC-I molecules can lead to high levels of background staining.

(6) These potential limitations should limit detection of low-affinity/low-avidity interactions between TCRs and their cognate pMHC antigens - this should be addressed explicitly in a model antigen setting.

(7) The approach appears to be limited to the HLAs showing high thermal stability, which have been explored in this study. However, a large fraction of HLAs show sub-optimal thermal stabilities. It seems that explicit validation of peptide exchange would be required for any new HLA allele introduced into this process.

(8) Whether the approach can be used to load suboptimal peptides with lower thermal stabilities that are emerging immunotherapy targets is not addressed in the present study.

Because of these limitations, the present manuscript does not conclusively support the claim that temperature-based exchange can be used as a robust methodology to generate pMHC-I tetramers with desired peptide specificities.

As a result, the scope of applications using these suboptimal exchanged pHLA tetramers is limited, and should be addressed with further improvements of the methodology, including better characterization of exchange efficiency, demonstration of functionality across a broader range of HLA allotypes with varying thermal stability profiles, and validation with clinically relevant low-affinity peptides that would strengthen the potential utility of this approach in immunotherapy development and basic T cell biology research.

We are submittng a revised version that addresses the major points raised. We believe that the manuscript in its present form clearly communicates the development of a robust and versatile temperature-based peptide exchange platform applicable across multiple HLA class I alleles, with relevance for both fundamental and clinical immunology. While we appreciate the constructive feedback provided, we feel that the core findings and conclusions are already well supported and suitable for publication.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The main recommendation here is to include a stability and staining comparison to UV-exchanged tetramers, as this will directly address why temperature-exchanged tetramers are superior. It could also be discussed that research groups may have better access to temperature-regulating equipment than UV. Other minor corrections may include:

We thank the reviewer for this suggestion. We have previously demonstrated that HLA‑A*02:01 and H‑2Kb remain stable as frozen monomers, and similarly showed the stability of thermal peptide exchange for HLA‑E, both at the monomer stage and after multimerization into thermal‑exchange HLA‑E tetramers. In addition, we have directly compared these reagents with conventional tetramers (see Figure 5). Conventional monomers and tetramers are routinely stored at −80 °C for several months without loss of staining performance, and we applied the same storage conditions to thermal‑exchange HLA‑E tetramers. Consistent with conventional tetramers, thermal‑exchange tetramers maintained their ability to stain TCR‑expressing cells for up to six months, with optimal staining preserved at both −20 °C and −80 °C. These findings have been published previously and are discussed in the current manuscript.

We would like to emphasize that we do not conclude that thermal peptide exchange is superior to existing technologies. Our intention is to demonstrate that this approach is feasible and to present its advantages and limitations, which are discussed in detail in the manuscript.

In the discussion we have included a sentence about the accessibility of heat exchange in relation to the equipment needed for UV exchange.

“Moreover, the broader availability and simplicity of equipment needed for thermal exchange compared to UV sources enables wider adoption of this approach.”

(1) Greater explanation of the different coloured curves in Figures 1 and 2, and whether all curves represent samples that are incubated at 50 degrees Centigrade.

We have now clarified in the figure legends that the different coloured curves represent the distinct peptide–HLA complexes analysed, and we explicitly state which curves correspond to samples incubated at 50 °C.

(2) Addition of X-axis title for Figures 1 and 2.

An X‑axis title was already present in Figures 1 and 2, but it was minimal; we have now revised it to make the labeling clearer and more informative.

(3) Clarify whether the background signal (negative) increases with the addition of more tetramer in Supplementary Figure 3 (non-specific binding).

The background (negative) signal did not appreciably increase with the addition of higher tetramer concentrations, indicating minimal non-specific binding under these conditions. This is consistent with observations in the MHC class I multimer field, where non-specific binding is generally limited under optimized staining conditions, and MHC class I multimers can be reliably used to detect antigen-specific T cells.

(4) Address stability of different alleles, or whether they are similar.

Peptide stability varies for each peptide–HLA combination rather than being strictly allele‑specific. We have therefore clarified this point in the manuscript. In addition, as requested by the reviewer, we have included a dedicated section describing the stability of the thermal‑exchange template peptides.

“The peptides that formed stable complexes at 4°C but unstable complexes at 20–32°C and 50°C showed affinities ranging from 4 to 11 µM. Such low affinities are uncommon for endogenous peptides and are unlikely to have physiological relevance, given that the complexes are highly unstable at 37°C.”.

(5) Measure fluorescence signal of tetramer before and after temperature exchange, compared to UV, to show fluorophore stability.

Fluorescent streptavidin forms a highly stable complex. During UV-mediated peptide exchange, reagents are exposed to heat generated by the UV lamp, which can partially denature MHC-I proteins. For this reason, it is necessary to centrifuge the complexes after UV exchange to remove denatured protein aggregates. Importantly, the fluorescence of streptavidin itself is not affected by this process. In contrast, thermal exchange is performed at substantially lower temperatures than UV-mediated exchange and does not compromise MHC-I protein integrity. Therefore, in our view, it does not pose a significant risk to fluorophore stability. In addition, UV may destroy fluorescence by simple bleaching, which cannot be an issue with temperature-dependent peptide exchange.

(6) Use HPLC to show stability of tetramer following temperature exchange versus UV.

HPLC analysis of tetramers is not possible and this is also not performed by others. The reason is that the tetramers are very heterogeneous (clustering of streptavidin together and the amount of MHCI monomers attached to streptavidin). As discussed above we do not claim to be better or worse compared to UV-exchange. This technology has a some additional benefits compared to UV-exchange, such as the tetramerization can be done before the peptide exchange. Additional it does not need a calibrated UV lamp but just an heatblock is needed for the peptide exchange making the exchange less complicated and in our opinion easier to implement. The UV exposure may oxidize amino acids, which is unlike to occur under temperature dependent conditions.

Reviewer #2 (Recommendations for the authors):

Minor in figure:

The authors should explain what "inputs" are in the figure legend.

We have now clarified in the figure legends that the different coloured curves represent the distinct peptide–HLA complexes analysed, and we explicitly state the nature of the “inputs”.

Minor in text:

The authors should also state two important limitations when designing temperature-sensitive peptide MHC-I, which are peptide binding affinity and subsequent T cell recognition. Poorly designed peptides can result in unexchanged peptide MHC-I complexes that may be recognized by the CD8 T cells, leading to false positives.

We have adjusted this in the text (discussion) although we did not make poorly designed peptides. The peptide presented in this manuscript are only stable at 4°C and unstable from 20°C and higher. As the T cell staining are performed at room temperature, there will be no peptide MHC-I complex of the original thermal-exchange peptide present as this is disintegrated. Only the stable, higher-affinity peptide-exchanged MHC-I is in complex. This does pose a problem for peptide exchange with low-affinity peptides, which is mentioned in the current version. However, this does not differ from the other loading technologies as in each case the mother peptide has to be exchanged for a proper peptide and a low-affinity peptide will be lost in time in each other case as well

The authors should include other recent reloadable peptide MHC technologies, e.g. chaperone-assisted, enzyme-exchangeble, and small alcohol treatment.

We apologize for not including these technologies and in the current manuscript they are included in the introduction. (see text below)

“Several technologies have since been developed to allow the parallel production of multiple MHC-I multimers, facilitating high-throughput analysis. For instance, dipeptides have been used as catalysts for peptide exchange[7-10][FS1] , UV-sensitive conditional MHC ligands have been a widely adopted approach [11, 12], in which a photocleavable peptide is cleaved upon UV exposure. Additional peptide exchange technologies include: chaperone-mediated peptide exchange[13, 14] enzymatic cleavage of low-affinity peptides that are covalently linked [15] and small alcohol peptide exchange [16].”

Major in data:

The authors should show if any T cell was detected using the original unexchanged peptide MHC-I in cytometry, as the interpreted use of an irrelevant peptide also depends on the existence of antigen-specific T cells in circulation.

The unexchanged peptide–MHC‑I complex cannot be used for T‑cell staining under our standard conditions because the template peptide dissociates at room temperature, leading to disintegration of the complex. Since our T‑cell staining protocol is performed at room temperature, unexchanged complexes would not remain intact long enough to allow reliable detection. Performing this experiment would require modifying the standard protocol and carrying out all staining steps strictly at 4°C. We choose not to change the staining protocol to perform this experiment.

In addition, the thermal‑exchanged peptide–MHC‑I complexes do not produce elevated background staining. As shown in Figure 5, background staining would appear as single‑positive events (PE or APC only), which we do not observe. This indicates that the thermal exchange approach does not introduce nonspecific tetramer binding.

Reviewer #3 (Recommendations for the authors):

(1) The proportion of exchanged molecules should be quantified relative to those retaining the original placeholder peptides and completely empty molecules present in the sample, using quantitative mass-spectrometry analysis. This would provide critical information about exchange efficiency and help assess the method's reliability.

We thank the reviewer for this point. We have performed this experiment and quantified the efficiencies. This is in the current version in figure 2b.

(2) Validation studies demonstrating peptide exchange in the absence of reporter T cell lines should be included. This would strengthen the methodology's applicability for antigen/T cell discovery applications where such reporter lines may not be available.

We thank the reviewer for raising this important point. Indeed, incomplete or unstable peptide exchange is a general concern inherent to all MHC-I peptide exchange protocols. To address this, we implemented a T cell–independent validation strategy based on LILRB1 binding. The innate immune receptor LILRB1 selectively recognizes properly folded peptide–MHC-I complexes by interacting with β2-microglobulin (β2M) and the α3 domain of the MHC heavy chain in a peptide-independent manner.

Critically, in our system the conditional template peptides are thermally unstable and dissociate during the exchange step. As a result, only successfully exchanged complexes containing a stabilizing peptide remain intact. Consequently, LILRB1 binding serves as a functional readout of successful peptide exchange and pMHC stability.

To assess this, we used K562 cells retrovirally transduced with LILRB1 and stained them with the corresponding fluorophore-conjugated pMHC multimers. Flow cytometric analysis enables clear discrimination between stable (successfully exchanged) and unstable complexes.

This assay is fully independent of TCR-based reporter systems and can therefore be broadly applied in antigen discovery settings where such reagents are not available. Importantly, it complements our HPLC-based quantification of peptide exchange efficiency (Figure 2B) by providing a scalable quality-control readout of structural integrity (Figure 2C).

We have now included this analysis in the Results section and updated the Discussion and Materials and Methods accordingly.

(3) Optimization strategies to improve exchange efficiency should be explored, along with direct comparisons with established methods.

In the revised manuscript, we have included the quantified exchange efficiencies of the thermal peptide exchange reaction, as determined by HPLC analysis on monomeric complexes. In addition, we now present a novel assay that enables routine quality control of each peptide exchange. This analysis is performed using LILRB1⁺ cells and can be readily applied to any peptide–MHC complex using standard flow cytometry.

Our data demonstrate that the exchange efficiencies obtained with our method are robust, and for the HLA alleles included in this study no further optimization was required. With respect to comparisons with established technologies, we chose to benchmark our approach against conventionally folded tetramers (Fig. 5). As stated above, we do not claim superiority over other peptide-exchange platforms; rather, we aim to present an alternative workflow with distinct practical advantages.

(4) Potential protein aggregation or other irreversible structural changes resulting from temperature cycling should be quantified and addressed. Since misfolded MHC-I molecules can contribute to high background staining, this characterization is essential for assessing the method's reliability. This can be done using DLS studies, which should report on the fraction of misfolded, high MW species present in the sample upon temperature treatment.

We thank the reviewer for raising this important point regarding potential aggregation or irreversible structural changes during temperature cycling. We agree that the presence of misfolded or aggregated MHC-I complexes could contribute to nonspecific staining and affect the reliability of the method.

Although we did not perform dynamic light scattering (DLS), we addressed this concern using complementary biochemical and functional approaches. First, monomeric peptide–MHC complexes were analyzed by size-exclusion HPLC throughout the study. These analyses consistently showed well-defined peaks corresponding to properly folded complexes, without detectable high–molecular weight species that would indicate aggregation (Figures 1 and 2).

Second, and importantly, we assessed the functional consequences of any potential misfolding or aggregation at the multimer level. If aggregated or misfolded MHC-I complexes were present, this would be expected to result in increased nonspecific binding and elevated background staining. However, across all experiments using both clonal T cell lines and primary PBMCs, we consistently observed low background staining and clear antigen-specific populations (Figures 3–5), arguing against the presence of aggregation-prone or sticky multimer species.

Third, we incorporated an additional quality control step based on LILRB1 binding (Figure 2C). Because LILRB1 selectively recognizes properly folded peptide–MHC-I complexes, this assay provides a sensitive readout for structural integrity. Unstable or improperly folded complexes do not bind LILRB1, allowing discrimination between functional and non-functional pMHC complexes.

Taken together, these complementary analyses indicate that temperature-based peptide exchange does not induce detectable aggregation or irreversible structural damage under our experimental conditions, and that the resulting multimer reagents are structurally intact and suitable for downstream applications. We have clarified this in the revised manuscript.

(5) The method's capacity to detect low-affinity/low-avidity TCR-pMHC interactions in a well-characterized model antigen system should be explicitly addressed. This would define the sensitivity limits of the approach compared to established methods.

The reviewer raises a valid and broadly relevant point that applies to all MHC-based technologies. However, we consider a full discussion of this topic to be outside the scope of the current manuscript. We do address this limitation for low-affinity peptides in the Discussion, where we write: “This technology is most likely not optimal for low-affinity peptides, as the template peptide itself must also have low affinity.” However, this problem may be universal since low-affinity peptides will simply release all MHC class I-peptide exchanged complexes during the staining process.

(6) Since the current study focuses on HLAs with high thermal stability, the approach should be tested with HLA alleles exhibiting lower thermal stability profiles. A validation framework could be developed that could be applied when introducing new HLA alleles to this process.

We thank the reviewer for this insightful comment. To our knowledge, there is no established classification of HLA alleles strictly based on “high” versus “low” intrinsic thermal stability; rather, stability is largely determined by the peptide–HLA combination.

Regarding the development of a validation framework for additional HLA alleles, our data indicate that suitable template peptide affinities generally fall within a range of approximately 4–11 µM. We anticipate that this range may vary between alleles, and therefore each HLA allele will require empirical identification of an optimal template peptide to achieve appropriate thermal stability and efficient peptide exchange.

This can be accomplished using the workflow presented in our study: first, assessing complex stability at 50 °C in the absence or presence of a high-affinity peptide (Fig. 1), followed by stepwise temperature reduction to determine optimal exchange conditions and incubation times (Fig. 2). In addition, LILRB1-based quality control can be incorporated to confirm the formation of properly folded and stable peptide–MHC complexes.

(7) It is encouraged that the approach be explored for its ability to effectively load suboptimal peptides with lower thermal stabilities. Demonstrating this capability would significantly enhance the method's clinical relevance.

We agree with the reviewer that evaluating the performance of the approach on suboptimal, low‑affinity peptides would be highly valuable and would further strengthen the clinical relevance of the method. In the current study, however, this falls outside our experimental scope. We are working on this in a follow-up project. We have now acknowledged the limitation of low-affinity peptides in the revised manuscript, noting that low‑affinity peptides are less suitable to this technology because the template peptide itself must also possess low affinity. Future work will be needed to systematically explore template design and exchange conditions optimized for such peptides.

eLife Assessment

This important study reports a novel phenomenon of maternal growth during pregnancy that is independent of growth hormone (GH), adding a new dimension to maternal biology of reproduction. The evidence is convincing and supported by state-of-the-art methodologies conducted in mice and persuasive, interesting and unique observations in humans with hereditary isolated GH deficiency.

Reviewer #1 (Public review):

This work evaluates the impact of reproductive history on growth, body weight and body composition in mammals. In mice, somatic growth is stimulated by the first pregnancy while the second pregnancy increases body weight mainly by increasing adiposity. To probe the role of pituitary growth hormone (GH), the key regulator of somatic growth in these processes, this was addressed by comparing the impact of reproduction on growth in normal ("wild type") and genetically GH-deficient females and by detailed characterization of the profile of fluctuations in circulating GH levels in both types of animals. Additional studies addressed the possible role of other endocrine pathways (ghrelin and estrogen) in the pregnancy-related growth. Surprisingly, reproduction-related growth was independent of GH, ghrelin and estrogen. To determine whether these results may apply ("translate") to human physiology, data on various parameters of somatic growth were collected from women with hereditary GH deficiency. The findings indicate that GH-independent stimulation of growth by reproductive events also occurs in women.

Use of multiple animal models, rigorous characterization of GH levels in normal and GH-deficient females, and inclusion of data derived from a unique and well-characterised population of people with hereditary isolated GH deficiency and no GH replacement therapy are important strengths of these elegant and innovative studies. The results address a broader and clinically significant issue of permanent changes in body size, composition and function that result from pregnancy and lactation. This work also provides important background for further studies aimed at the identification of the mechanism involved and the role of specific reproductive events in the regulation of growth.

Reviewer #2 (Public review):

This manuscript describes the fascinating phenomenon of growth hormone (GH)-independent growth occurring in the mother during pregnancy. This growth was most pronounced in dwarf mice that are lacking the receptor for growth hormone-releasing hormone (GHRH) and therefore showing isolated GH deficiency. However, the pregnancy-induced growth could also be observed in wild-type mice, suggesting that it is a normal part of the maternal adaptation to pregnancy. The study falls short of identifying the mechanism(s) driving this pregnancy-induced growth response, but it certainly reveals a novel insight into maternal physiology. The authors have completed a range of experiments in mice to prove that, as well as being GH independent, the pregnancy-induced growth also did not require GH signaling in the liver (i.e., not another pregnancy-specific ligand operating through the GHR to promote IGF). They also provided complementary data from a population of humans with untreated isolated GH deficiency that are broadly consistent with the hypothesis. While it is important to consider the significant species differences between rodents and humans, both in terms of growth physiology and also in terms of evolution of placental somato-mammotrophic hormones, this unique population is a valuable resource and adds credence to the study. Overall, I find this a compelling research story, but somewhat unfinished. There are some areas where additional information could improve the ability to interpret the data, and some additional concepts that could be considered in the discussion. There are also areas where additional experiments might provide important insights. However, I think that such suggestions can be considered as appropriate for future research, rather than delaying the dissemination of the findings in the current manuscript.

Reviewer #3 (Public review):

Summary:

The study describes an increase in body growth and body composition in both mice and women. In mice, the impact on growth is mainly seen during the first pregnancy, and the changes postpartum on body composition are also different during the first and second pregnancies. The study has used various knockout models in the growth hormone axis to understand these changes as well as some gene expression analysis related to GH, IGF-1 and estrogen signalling pathways.

Strengths:

(1) The inclusion of various knock-out mouse models that allow for exploration of mechanisms related to the above-mentioned changes.

(2) The investigation of gene expression of GHR, IGF-1R and ER pathways.

Author response:

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

eLife Assessment:

This important study reports a novel phenomenon of maternal growth during pregnancy that is independent of growth hormone (GH), adding a new dimension to maternal biology of reproduction. The evidence is convincing and supported by state-of-the-art methodologies conducted in mice and persuasive observations in humans with hereditary isolated GH deficiency. Revised discussion should focus on possible mechanisms, including the role of IGF2, and on directions for future research.

We thank the editors for these valuable suggestions. In response, we assessed hepatic Igf2 mRNA expression. As shown in Author response image 1, hepatic Igf2 mRNA expression was higher in Ghrhr^lit/lit mice but was not significantly affected by pregnancy. However, we recognize that IGF-2 is produced by multiple tissues, particularly at the maternal-fetal interface, as well as by other maternal tissues, exerting endocrine or paracrine effects. Therefore, we believe that hepatic Igf2 expression alone provides only a limited view of the potential contribution of IGF-2 to the maternal adaptations induced by pregnancy. For this reason, we chose not to include these data in the revised manuscript. Instead, we expanded the Discussion to address the potential role of IGF-2 in the observed phenotypes and to highlight important directions for future research, as suggested.

Author response image 1.

Public Reviews:

Reviewer #1 (Public review):

This work evaluates the impact of reproductive history on growth, body weight and body composition in mammals. In mice, somatic growth is stimulated by the first pregnancy while the second pregnancy increases body weight mainly by increasing adiposity. To probe the role of pituitary growth hormone (GH), the key regulator of somatic growth in these processes, was addressed by comparing the impact of reproduction on growth in normal ("wild type") and genetically GH-deficient females and by detailed characterization of the profile of fluctuations in circulating GH levels in both types of animals. Additional studies addressed the possible role of other endocrine pathways (ghrelin and estrogen) in the pregnancy-related growth. Surprisingly, reproduction-related growth was independent of GH, ghrelin and estrogen. To determine whether these results may apply ("translate") to human physiology, data on various parameters of somatic growth were collected from women with hereditary GH deficiency. The findings indicate that GH-independent stimulation of growth by reproductive events also occurs in women.

Use of multiple animal models, rigorous characterization of GH levels in normal and GH-deficient females, and inclusion of data derived from a unique and well-characterised population of people with hereditary isolated GH deficiency and no GH replacement therapy are important strengths of these elegant and innovative studies. The results address a broader and clinically significant issue of permanent changes in body size, composition and function that result from pregnancy and lactation. This work also provides important background for further studies aimed at the identification of the mechanism involved and the role of specific reproductive events in the regulation of growth.

We sincerely thank the reviewer for this thoughtful and highly positive evaluation of our work and for recognizing its novelty, rigor, and potential physiological and clinical significance.

Reviewer #2 (Public review):

This manuscript describes the fascinating phenomenon of growth hormone (GH)-independent growth occurring in the mother during pregnancy. This growth was most pronounced in dwarf mice that are lacking the receptor for growth hormone-releasing hormone (GHRH) and therefore showing isolated GH deficiency. However, the pregnancy-induced growth could also be observed in wild-type mice, suggesting that it is a normal part of the maternal adaptation to pregnancy. The study falls short of identifying the mechanism(s) driving this pregnancy-induced growth response, but it certainly reveals a novel insight into maternal physiology. The authors have completed a range of experiments in mice to prove that, as well as being GH independent, the pregnancy-induced growth also did not require GH signaling in the liver (i.e. not another pregnancy-specific ligand operating through the GHR to promote IGF). They also provided complementary data from a population of humans with untreated isolated GH deficiency that are broadly consistent with the hypothesis. While it is important to consider the significant species differences between rodents and humans, both in terms of growth physiology and also in terms of evolution of placental somato-mammotrophic hormones, this unique population are a valuable resource and adds credence to the study. Overall, I find this a compelling research story, but disappointingly unfinished. There are some areas where additional information could improve the ability to interpret the data, and some additional concepts that could be considered in the discussion. There are also areas where additional experiments might provide important insights. However, I think that such suggestions can be considered as appropriate for future research, rather than delaying consideration of the current manuscript.

Main comments:

(1) Data in Figure 1 are remarkable - not so much the growth in pregnancy in the wildtype mice, because while elevated GH is well known in pregnancy, but growth in the dwarf mice is indicative of GH-independent growth. From these data, it seems that there is good evidence that growth in pregnancy is an adaptive function. However, it is possible that growth is achieved in dwarf mice and that in wildtype mice may have been mediated through different mechanisms. The dwarf mice showed an increase in liver and plasma IGF1, suggestive of an additional ligand driving IGF in pregnancy. One could hypothesize that such an effect could be mediated by an additional pregnancy-specific ligand activating the GH receptor. In humans, placental growth hormone could be such a ligand, but as far as we know, there is no placental GH in mice. In contrast, the wildtype animals showed suppression of liver and circulating IGF1, and low levels of pSTAT5 in the liver during pregnancy. These data (in Figure 5) are very surprising. Given the high circulating GH in pregnancy, as well as high placental lactogen (which would be expected to activate STAT5 in the liver through the Prlr), the low levels of pSTAT5 are unexpected and would seem to indicate some sort of acquired insensitivity to GH. Is this entirely driven by down-regulation of STAT5b protein, or could there be activation of other, negative regulators of STAT signalling, such as SOCS? What is causing such a profound suppression of STAT5? Regardless of the mechanism, this suggests that pregnancy-induced growth in wildtype mice is independent of circulating IGF1 (potentially a different mechanism or in addition to that seen in IGHD mice).

We thank the reviewer for this insightful comment. The mechanisms underlying the reduced hepatic STAT5b protein expression observed during pregnancy remain unknown. Previous studies have also reported desensitization of hepatic JAK2/STAT5 GH signaling during pregnancy, associated with increased expression of negative regulators of STAT signaling, including CIS (Miquet et al., Am J Physiol Endocrinol Metab 289–E607, 2005). In the current manuscript, we also observed increased Cish mRNA expression in the liver of pregnant mice. We have incorporated this information into the revised manuscript. In addition, we expanded the Discussion to acknowledge the possibility that pregnancy-induced growth may occur through distinct mechanisms in wild-type and GH-deficient mice and that, in wild-type mice, this response may involve liver-derived IGF-1-independent mechanisms.

The data shown in Figure 6 are a major strength of the study, showing that the pregnancy-induced changes are not specific to one particular transgenic model, but still occur in a variety of models affecting GH through different approaches. Given the pregnancy-specific nature of the changes, however, it seems an oversight not to have evaluated the role of placental lactogens. Prlr is highly expressed in the liver, but the function of this hormone in the liver is not well established. Could the extremely high levels of PL be mediating this growth response? Given the low expression of STAT5 in the liver and the fact that plasma IGF1 is not markedly elevated, it seems more likely that this growth response may be mediated by locally produced IGF1 in target tissues.

We thank the reviewer for this important suggestion. Although we were not able to investigate the role of prolactin receptor signaling using mouse models in the present study, we agree that prolactin may contribute to pregnancy-induced growth. Accordingly, we revised the Discussion to acknowledge this possibility and to include the potential roles of placental lactogens and locally produced IGF-1 as additional mechanisms that may underlie pregnancy-induced body growth.

I think these possibilities could be addressed by an expanded discussion of species variation in placental hormones, to highlight that humans have expansion of the GH locus, but rodents have expansion of the prolactin axis (see Soares, M. J. The prolactin and growth hormone families: pregnancy-specific hormones/cytokines at the maternal-fetal interface. Reprod Biol Endocrinol 2, 51, 2004). Importantly, placental GH and chorionic somatomammotropins (CSM) in humans are all variants of the GH gene, but CSM have preferential activity at Prlr. This seems to be a fundamental species difference in pregnancy biology, but has been interpreted as an example of convergent evolution, with conservation of prolactin and GH-like functions at the maternal-fetal interface, mediated by different mechanisms, likely contributing to the metabolic adaptations of the mother (see Newbern D, Freemark M. Placental hormones and the control of maternal metabolism and fetal growth. Curr Opin Endocrinol Diabetes Obes. 2011; 18: 409-416). While the preceding function has focused on explaining the evolution of placental lactogens (either prolactin or GH variants), the present data suggest that there are also mechanisms to maintain growth in pregnancy, independent of GH (even in the absence of a placental GH).

Thank you very much for this observation and suggestion. In the Introduction, we succinctly mention species-specific differences in the GH locus (see Introduction). Since our study focused primarily on mice, we believe expanding on this information would detract from the study's focus, especially given that such details are available in other publications. However, we have added a sentence to the discussion noting that, despite significant species-specific differences in the GH locus, there has been evolutionary conservation in the maintenance of pregnancy-induced growth, potentially involving distinct mechanisms in rodents and humans, though both appear to be GH-independent.

“However, important differences are observed between humans and rodents. Humans, but not rodents, possess the GH2 gene, which encodes the placental growth hormone (GH) variant, whose production progressively replaces pituitary GH (derived from the GH1 gene) secretion during pregnancy (Liao et al., 2018). In contrast, rodents maintain pituitary GH secretion throughout gestation (Gatford et al., 2017; Liao et al., 2018). Additionally, human GH, both pituitary and placental variants, as well as chorionic somatomammotropins, can activate both the GH receptor (GHR) and the prolactin receptor (PrlR), explaining their lactogenic effects. In contrast, murine GH activates only the GHR (Bartke and Kopchick, 2015).”

(2) The human data are very interesting, and my initial impression was that it seemed unlikely to be the same phenomenon. Was there any real evidence for "growth" in pregnancy? Pubertal maturation of long bone growth might be expected to prevent further growth in adulthood. However, these issues were appropriately discussed, and it seems well justified to evaluate this unique population of women with IGHD who underwent pregnancy. It would be very interesting to know if these women experienced elevated IGF1 during pregnancy, indicative of placental GH contributing to growth. Mechanistically, this might be more like the dwarf mouse situation of IGHD, that the situation in wildtype mice (associated with liver insensitivity to GH and low IGF1).

We thank the reviewer for this comment. Unfortunately, the pregnancies of the women with IGHD occurred with limited medical assistance, and no additional clinical information is available, particularly regarding changes in circulating IGF-1 levels during pregnancy. Therefore, the evidence presented and discussed in the current manuscript represents the only information currently available on pregnancy-induced growth in this unique population.

(3) It would be useful to include investigations that isolate the effects of pregnancy and the placental hormones. Such studies could include evaluating growth in pseudopregnant mice with IGHD (pregnancy-like changes in hormones but lacking the placental contribution) and in IGHD animals that experience pregnancy but not lactation (pups removed at birth). I accept that this might be too large an additional study to add for the present manuscript.

We thank the reviewer for this valuable suggestion and agree that this experiment could provide valuable information regarding the role of placental hormones in pregnancy-induced growth. Interestingly, previous work has shown that female mice housed with vasectomized males exhibit increased body weight compared with non-reproductive females, although this increase is substantially smaller than that observed in females with successive litters (Garratt et al., Proc Natl Acad Sci U S A 117:15748–15754, 2020). We discuss this study in the current manuscript. However, this study did not provide additional information on whether this increase reflects greater adiposity, enhanced body growth, or both. Unfortunately, we are unable to perform these time-intensive experiments. We appreciate the reviewer's understanding and agree that this important question should be addressed in future studies.

(4) It is an important and translationally relevant observation that pregnancy increased the risk of long-term weight gain, and that after the first pregnancy, the pregnancy-induced growth response was more directed to promoting fat deposition. Does this provide any mechanistic insight? Could a metabolic adaptation result in growth?

We thank the reviewer for this thoughtful comment. At present, we do not have additional data to explain the mechanisms underlying the pregnancy-induced increases in body growth and adiposity or to determine whether these processes are mechanistically linked. In the revised manuscript, we have expanded the Discussion to address potential mechanisms that may contribute to the observed post-pregnancy growth, including hormonal and metabolic factors, while acknowledging that these possibilities remain speculative and require further investigation.

Reviewer #3 (Public review):

Summary:

The study describes an increase in body growth and body composition in both mice and women. In mice, the impact on growth is mainly seen during the first pregnancy, and the changes postpartum on body composition are also different during the first and second pregnancies. The study has used various knock-out models in the growth hormone axis to understand these changes as well as some gene expression analysis related to GH, IGF-1 and estrogen signalling pathways.

Strengths:

(1) The inclusion of various knock-out mouse models that allow for exploration of mechanisms related to the above-mentioned changes.

(2) The investigation of gene expression of GHR, IGF-1R and ER pathways.

Weaknesses:

The human findings are dependent on the patient's recollection of bodily changes after their pregnancies.

Conclusion:

The authors have partly achieved their aim of describing changes in growth and body composition that remain after pregnancy and the mechanisms behind these changes. This study may have importance for a wide variety of research areas as well as in the clinical setting. The study is also unique in its attempt to bridge findings in mice to a unique human model of congenital GH deficiency.

We sincerely thank the reviewer for the thoughtful evaluation of our study, for recognizing its novelty and potential significance, and for highlighting the strengths of our experimental approach. We have revised the manuscript to further acknowledge the limitations of the human data, as suggested.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The findings presented in this study are novel, exciting and important. I believe it would help the readers to include a diagram showing the timing of the various measurements and tissue collection in relation to conception, parturition and weaning. It would also be helpful to expand the discussion to include the author's thoughts on the possible role of various placental hormones, pituitary prolactin, metabolic changes and/or other factors in the observed growth. Finally, humans from whom the data were obtained should probably be referred to as individuals or subjects rather than patients.

We thank the reviewer for these helpful suggestions. We included Figure 7 in the revised manuscript, which summarizes the study's experimental timeline. Additionally, we expanded the Discussion as recommended and replaced the term "patients" with "subjects" throughout the manuscript.

Reviewer #2 (Recommendations for the authors):

In addition to my comment above about addressing the different evolution of placental hormones, the following minor suggestions are provided:

(1) Abstract line 23 "most" could be "some" (because lots of evidence that pregnancy-induced adaptations are long-term - e.g. brain structure, maternal behavior, endocrine changes) - see below.

Done.

(2) Is "reproductive experience" the best term? Or is it "pregnancy"? (likely specifically due to the presence of placental hormones and/or maternal patterns of hormones, rather than other aspects of "reproductive experience) e.g. mating, parturition or lactation?

We appreciate the reviewer's point. However, because we cannot exclude potential contributions of mating, parturition, or lactation to the observed increases in body growth and adiposity, we prefer to retain the term "reproductive experience," as the mice in the present study underwent all of these processes rather than pregnancy alone.

(3) Potentially, the introduction could add references to brain changes in humans in pregnancy (this is a particularly topical area of research where long-term changes have been reported; e.g. Pritschet L, Taylor CM, Cossio D, Faskowitz J, Santander T, Handwerker DA, Grotzinger H, Layher E, Chrastil ER, Jacobs EG. Neuroanatomical changes observed over the course of a human pregnancy. Nat Neurosci. 2024 Nov;27(11):2253-2260; Martínez-García M, Paternina-Die M, Barba-Müller E, Martín de Blas D, Beumala L, Cortizo R, Pozzobon C, Marcos-Vidal L, Fernández-Pena A, Picado M, Belmonte-Padilla E, Massó-Rodriguez A, Ballesteros A, Desco M, Vilarroya Ó, Hoekzema E, Carmona S. Do Pregnancy-Induced Brain Changes Reverse? The Brain of a Mother Six Years after Parturition. Brain Sci. 2021 Jan 28;11(2):168. There is also a significant literature on long-term effects of reproductive experience (Bridges RS. Long-term alterations in neural and endocrine processes induced by motherhood in mammals. Horm Behav. 2016 Jan;77:193-203).

We thank the reviewer for this helpful suggestion. Accordingly, we incorporated these references into the Introduction to further emphasize the long-term effects of reproductive experience.

(4) Figure 1: Why show body weight as a "delta" for primiparous animals, and "absolute "values for multiparous? Similarly, it seems that body length is an informative readout for these experiments, but this is only reported for one model, and most models are only shown as body weight and lean mass.

We thank the reviewer for this comment. For the primiparous mice, we chose to present the change (Δ) in body weight and lean mass because it more directly illustrates the effects of the first reproductive experience relative to each animal's baseline while avoiding redundant presentation of both absolute and Δ values, as both analyses yielded the same statistical conclusions. For the multiparous mice, absolute values were presented to facilitate comparison with the corresponding images and to allow direct comparison of body size between wild-type and Ghrhr^lit/lit mice. Regarding body length, these measurements were collected only in the multiparous cohort and were not obtained after the first reproductive experience. Therefore, we are unable to provide body length data for the primiparous groups.

(5) It seems it would be better to present all of the mouse data first, then the supporting human data.

Done.

(6) The manuscript includes a high-quality investigation of GH secretion - particularly the pulsatile secretion of GH. Is it possible to have matching IGF data (at least multiple time points in pregnancy)?

We agree with the reviewer that serial measurements of circulating IGF-1 during pregnancy would provide valuable additional information. Unfortunately, this analysis is not feasible because the limited blood volume collected during the study did not allow sufficient sample storage for additional measurements.

(7) Line 221 - "GHRH signaling is required for pregnancy-induced increases in GH secretion...". Can you actually make that conclusion, or is it possible that the lack of GHRH developmentally has permanently altered the pituitary gland, so it cannot respond to other GH secretagogues?

We thank the reviewer for this important comment. We agree that the congenital absence of GHRH signaling may cause developmental alterations in the pituitary that impair the response to other GH secretagogues. Therefore, we cannot distinguish whether the lack of pregnancy-induced increases in GH secretion reflects the absence of GHRH signaling per se or the developmental defects resulting from GHRH deficiency. We removed the aforementioned phrase from Results and have revised the Discussion to acknowledge this important limitation and to clarify that the observed phenotype may be secondary to impaired pituitary development.

(8) Line 238 - "GHR signaling stimulates hepatic insulin-like growth factor 1 (IGF-1) secretion, particularly by activating the signal transducer and activator of transcription 5b (STAT5b) pathway" for this point, should probably cite: Davey HW, Xie T, McLachlan MJ, Wilkins RJ, Waxman DJ, Grattan DR. STAT5b is required for GH-induced liver IGF-I gene expression. Endocrinology. 2001 Sep;142(9):3836-41.

Thank you for this suggestion; we added this reference.

(9) Line 240 - "GH action in the liver is not only controlled by the pattern of GH secretion...". should probably cite Waxman's work regarding patterns of GH secretion (e.g reviewed in Waxman DJ, O'Connor C. Growth hormone regulation of sex-dependent liver gene expression. Mol Endocrinol. 2006 Nov;20(11):2613-29.).

This reference was included in this sentence.

(10) Methods: Check statistics - some of the analysis should have been repeated measures?

We thank the reviewer for this comment. We carefully re-evaluated all statistical analyses and did not identify any experiment for which a repeated-measures analysis would have been appropriate. Therefore, no changes to the statistical analyses were necessary.

Reviewer #3 (Recommendations for the authors):

(1) Introduction: The context of the sentence "Furthermore, historically, females have been underrepresented in studies" is unclear.

We thank the reviewer for this observation. Our intention was to emphasize that, because pregnancy is unique to females and females have historically been underrepresented in biomedical research, pregnancy-related physiology has received comparatively less attention. However, we agree that this statement was not essential in this context. Thus, we have removed it from the revised manuscript.

(2) Introduction: Based on the paper, the main aim seems to be to study the lasting effects of pregnancy on the mother and not primarily to study the hormonal changes during pregnancy.

We thank the reviewer for this helpful observation. We agree that our study primarily focuses on the long-term effects of pregnancy on the maternal organism rather than the hormonal changes that occur during pregnancy. Accordingly, we revised this sentence to better reflect the main objective of the study: “Therefore, the goal of this study is to investigate the lasting effects of pregnancy on the maternal organism and the possible involvement of the somatotrophic axis in these changes.”

(3) Other endocrine factors could affect the changes seen after pregnancy in mice and humans, such as the insulin level and activation of the IR.

We thank the reviewer for this valuable suggestion. In the revised manuscript, we expanded the Discussion to acknowledge the potential contribution of several endocrine factors, including insulin signaling, to pregnancy-induced growth.

(4) The receptor activation in tissues other than the liver has not been studied, such as in the growth plate, adipose tissue and muscle.

We thank the reviewer for this important comment. We agree with this point and have addressed this possibility in the revised Discussion.

(5) Information on the age of the patient at the time of pregnancy could be included as well as the patient's height and weight before pregnancy and at follow-up.

This information was added as Table 1.

eLife Assessment

By integrating RelB proximity labeling with targeted CRISPR screening, the authors identify several potential regulators of HIV latency and provide evidence implicating RelB, KAT7, and p300 in AZD5582-mediated HIV reactivation. While the study is important, the current work is incomplete, as it needs to establish physiological relevance. The findings require validation in primary latency models, and the unusually high basal RelB expression in the experimental system raises concerns about whether the observed effects accurately reflect endogenous mechanisms regulating HIV latency.

Reviewer #1 (Public review):

Summary:

Bussey-Sutton, Gray, Wu et al. combine RelB proximity-labeling proteomics (BioID) with a custom, BioID-informed HIV-CRISPR screen to map the chromatin/transcriptional network that links non-canonical NF-κB (RelB/p52) activation by the SMAC mimetic AZD5582 to HIV-1 latency reversal. They identify a broad basal RelB interactome (chromatin remodelers, RNA-binding proteins, transcription machinery) that is partially reshaped, rather than replaced, by AZD5582 treatment. A targeted CRISPR screen against the BioID hit list then functionally separates these interactors into pro-reactivation factors (KAT7/HBO1, NSD2, SIN3A) and restrictive factors (p300, CHD4, USP7, UHRF1, DNMT1).

Pharmacological inhibition of the two acetyltransferase hits (KAT7i and p300i) validates opposing phenotypes predicted by the screen, and a comparative TNF-α (canonical NF-κB) screen argues that at least the p300 and, more selectively, the KAT7 pharmacology are biased toward the ncNF-κB axis. The dataset is a useful resource, and the BioID, CRISPR, pharmacology pipeline is a nice template for functionally triaging proximity-proteomics hits rather than treating them as a static interactome.

Strengths:

This study takes an integrative approach in which proximity proteomics is used to define candidate RelB-associated regulators, a purpose-built targeted CRISPR library tests these candidates directly for a functional phenotype, and pharmacological inhibition cross-validates the two acetyltransferase hits with an orthogonal, catalytic-activity-specific perturbation. This funneling from unbiased proteomic discovery to targeted functional testing to mechanistic pharmacology is an efficient and logical pipeline for converting a large interactome into a smaller set of high-confidence, functionally validated regulators.

The comparison of basal versus AZD5582-stimulated RelB interactomes is conceptually useful, as it shows that RelB engages a largely pre-existing chromatin and transcriptional regulatory scaffold upon ncNF-κB activation, rather than recruiting an entirely new complex. This is a finding with potential implications for non-canonical NF-κB signaling beyond the HIV latency context specifically.

The inclusion of a parallel HIV-CRISPR screen using TNF-α to activate canonical NF-κB signaling is a valuable control, allowing the authors to distinguish regulators that are broadly required for NF-κB-dependent HIV expression from those more selectively linked to AZD5582-driven ncNF-κB signaling. This comparison strengthens the authors' claims of pathway specificity for hits such as KAT7 and p300.

Finally, pharmacological validation of the top acetyltransferase hits was performed across two independent latency models (J-Lat 10.6 and N6), which helps address, at least in part, the concern that phenotypes are specific to a single clonal integration site. Together with the deposited proteomics and screen datasets, this provides a genuinely useful resource for the field.

Weaknesses:

(1) BioID inherently reports both direct and indirect (proximal) interactions, and no individual hits are validated by an orthogonal method (e.g., co-IP, PLA). As a transcription factor, RelB would be expected to reside near transcriptional/chromatin machinery, so this enrichment alone isn't surprising, making it hard to distinguish functionally relevant RelB complexes from bystander proteins in the same active chromatin neighborhood. At least a subset of top hits should be validated independently.

(2) BioID interactome was defined in a single clonal cell line, limiting generalizability across latent cell types. The RelB BioID proteomics, which forms the entire basis for the downstream targeted CRISPR library generation, was performed in one engineered Jurkat N6 clone. Both RelA/RelB pathway dependency and the baseline expression of the chromatin regulators identified as RelB interactors (e.g., DNMT1, UHRF1, SWI/SNF subunits, NSD2) can vary considerably across cell lines, latency clones, and primary CD4+ T cells. Since the CRISPR screen, and thus all functional hits in the paper, is entirely constrained by this single-cell-line interactome, any RelB interactor that is absent or differently regulated elsewhere would never have been tested, regardless of its true biological importance. To support claims of a broadly relevant RelB/ncNF-κB regulatory network, the authors should at least partially validate the basal and AZD5582-induced interactome (e.g., by co-IP/western for key hits) in a second cell line or primary CD4+ T cells, to distinguish clone-specific interactions from generalizable ones.

(3) Is KAT7/HBO1's contribution to reactivation a direct interaction/synergy with AZD5582, or an independent parallel requirement? The data show that KAT7/HBO1 knockout and catalytic inhibition (WM-3835) both reduce AZD5582-induced reactivation, and that KAT7 was detected as AZD5582-enriched in the RelB BioID. However, it remains unclear from the current data whether KAT7/HBO1 acts as a direct downstream effector in the ncNF-κB/RelB signaling axis (i.e., is recruited by or acts together with RelB/p52 at the LTR specifically upon AZD5582 stimulation), or whether it represents a more general/parallel chromatin requirement for HIV reactivation that is simply necessary regardless of the activating stimulus (and happens to also associate with RelB). Distinguishing these possibilities matters for interpretation: the former would support a model in which AZD5582 and KAT7 act synergistically through the same pathway (i.e., acetylation is mechanistically coupled to ncNF-κB activation), whereas the latter would suggest KAT7-mediated acetylation and RelB/p52 signaling are two independent, simultaneously required mechanisms that converge on the same locus without being mechanistically linked. The comparative TNF-α data (Figure 3C), where the genetic screen shows a shared dependency but the pharmacological inhibitor does not phenocopy this for TNF-α, adds to this ambiguity rather than resolving it. Clarifying whether KAT7/HBO1 functions upstream, downstream, or in parallel with RelB/p52 (e.g., via RelB ChIP after KAT7 knockdown, or KAT7 recruitment kinetics relative to RelB/p52 at the LTR) would strengthen the mechanistic claims in this section.

(4) A major limitation of the study is that screen results were validated in only two cell line models, and neither is a primary cell system. Different latency models are known to have distinct dominant transcriptional blocks, not just different genetic backgrounds. J-Lat clones, U1, ACH2, and other transformed lines differ substantially in why the provirus is silent; some are more Tat/P-TEFb-limited, some more chromatin/Polycomb-restricted, some more dependent on transcription factor availability (NF-κB, NFAT, AP-1). A regulator that is rate-limiting in J-Lat 10.6 specifically (a single integration site, clonally selected for a particular chromatin environment around the LTR) may therefore be irrelevant, or could even act in the opposite direction, in a model where the block is elsewhere.

(5) HIV latency and LRA responsiveness are well known to be strongly integration-site and clone-dependent. Pharmacological validation of CRISPR screen hits extends to N6, but the primary screen hits themselves are not confirmed in a second genetic background. This is an important caveat that should be discussed explicitly, and ideally at least the top hits (KAT7, NSD2, SIN3A, p300, CHD4) should be individually knocked out (not just inhibited) in a second model to confirm the genetic phenotype generalizability, not just the pharmacology.

(6) More importantly, no validation was performed in primary CD4+ T cells or ex vivo resting CD4+ T cells from people with HIV, which remain the field's benchmark for confirming that a candidate regulator is relevant to authentic latency rather than to a transformed cell line. Basal chromatin state, NF-κB pathway, and expression of the chromatin regulators identified here (e.g., DNMT1, UHRF1, SWI/SNF subunits) can differ substantially between transformed lines and primary resting T cells. Given this, the current claims of a broadly applicable "chromatin regulator" network should be tempered, and at least the top hits (e.g., KAT7/HBO1, NSD2, SIN3A, p300) should ideally be tested in a primary cell model before being generalized as regulators of HIV latency and reactivation more broadly.

(7) The finding that p300 restricts AZD5582-driven reactivation is framed as consistent with Horvath & Sadowski (ref 36), but p300/CBP is also a well-established Tat/LTR coactivator in many contexts (Kiernan et al., Marzio et al). The Discussion would benefit from a slightly more developed treatment of how these findings can be reconciled rather than citing a single concordant paper.

Reviewer #2 (Public review):

Summary:

Bussey-Sutton et al. investigate the RelB interactome in the presence and absence of the SMAC mimetic AZD5582. They combined RelB BioID with CRISPR screening and highlighted multiple potential transcriptional regulators that may contribute to the maintenance or reversal of HIV latency. However, there are several technical limitations and gaps in validation in the current version of the work.

Strengths:

The overall topic is of clear interest; the RelB interactome and CRISPR screens provide interesting hits.

Weaknesses:

From a technical standpoint, RelB is expressed using a doxycycline-inducible system, yet the fusion protein (Figure S1A) appears to be expressed at high levels even in the absence of doxycycline (and does not seem to respond to doxycycline supplementation). As this is the key model system used in the paper to identify RelB interactors, this limitation should be discussed and potentially addressed.

It would also be important to include some orthogonal validation (e.g., co-immunoprecipitation) of top novel RelB interactors identified by BioID.

In Figure 2C, two non-targeting controls appear among the most highly enriched hits. This raises the question that other top hits might reflect nonspecific effects or assay noise. Consistent with this concern, the effects observed following siRNA-mediated depletion of the top CRISPR-screen candidates in Figure 2D and Figure 3 appear relatively modest.

More broadly, the absence of validation in primary-cell models is a further limitation, as the chromatin environment and transcriptional regulation of HIV latency in the two cell-line models used here are likely to differ substantially from those in primary CD4+ T cells.

Minor point:

Endogenous RelB remains present in the RelB-BioID cells and could compete with the miniTurbo-RelB fusion protein for physiological binding partners. Moreover, the effect of two sources of constitutive RelB expression (see comment above) on the physiologic RelB interactome is not obvious. Controlling for this is not trivial, but this potential confounding factor should be acknowledged (and further reinforces the need for orthogonal targeted validations of interactors in cells with endogenous RelB).

Reviewer #3 (Public review):

The study is built on the premise that the SMAC mimetic AZD5582 can reverse HIV latency via the RelB-mediated non-canonical NF-kB pathway activation; however, its molecular regulators remain undefined. The authors use an inducible BioID RelB reporter system in Jurkat N6 cells containing an integrated HIV-1 provirus and identify both the basal and the AZD5582-activated chromatin and transcriptional regulatory network of the non-canonical NF-kB pathway. To further explore the role of the identified regulators, an HIV-CRISPR latency screening approach was used, and based on enrichment or depletion of guide RNAs in the supernatant, genes that inhibited or activated virus reactivation, respectively, were identified. Genes like LRPPRC (RNA-binding protein), KAT7 (acetyltransferase), NSD2 (H3L36 methyltransferase), SIN3A (part of histone deacetylase complex), and others were identified to be essential for HIV reactivation. Nearly half of the identified factors were found to be negative regulators of reactivation, notably CBP/p300 (acetyltransferase), CHD4, USP7, UHRF1, and DNMT1. The roles of KAT7 and p300 were validated through the use of specific inhibitors. To narrow down regulators that are specific for nc NF-kB HIV reactivation vs NF-kB dependent HIV expression, a parallel CRISPR screen was performed with TNF-alpha, which reconfirmed the role of RelB, KAT7, and p300 in AZD5582-mediated HIV reactivation.

Overall, this is a solid and well-designed study that combines complementary approaches to deliver a valuable resource.

The study's strength lies in integrating two high-throughput approaches of RelB proximity labelling and targeted CSIPR screening to identify molecular regulators of the HIV reactivation pathway. A parallel CSIPR screen with TNF-alpha provides key insights into pathway-specific vs shared regulators of latency reversal.

The limitation of the study, as indicated by the authors, is that the assays are based only on HIV output. Additionally, some of the identified interactors may be indirect or context-dependent and may not represent all HIV reservoirs in vivo.

Author response:

We greatly appreciate the editors and reviewers for their time and careful evaluation of our manuscript. It was clear that the reviewers valued our study that integrated RelB proximity proteomics with targeted HIV-CRISPR screening to identify chromatin and transcriptional regulators of AZD5582-mediated HIV reactivation. We appreciate all of the constructive comments and agree that the manuscript can be further strengthened by clarifying several technical points, correcting text and figure issues, and more clearly defining the scope of the study.

A recurring theme of the reviews is the need to better define which RelB-associated factors are functionally meaningful regulators of HIV reactivation. We agree with the reviewers’ point that BioID/miniTurbo proximity labeling does not by itself establish direct physical interaction. That said, the method provides an in vivo cell measurement of protein proximity and can capture core complex interactions as well as transient, weak, or chromatin-associated interactions. Notably, such transient interactions are often lost during cell lysis and extraction, as well as co-IP. In the revised manuscript, we will clarify this distinction and emphasize that the BioID dataset identifies RelB-proximal candidate regulators rather than exclusively direct binding partners. We will also consider orthogonal validation of key hits using either co-IP or an orthogonal in cell proximity assay like PLA, which would preserve the cellular context of RelB-associated regulatory complexes.

The reviewers also raised a fair concern regarding physiological relevance and the use of transformed latency models. We agree that primary cell validation would be an important next step for determining how broadly these findings apply to HIV regulation. At the same time, the present study was intended to be an initial resource of RelB-associated factors that contribute to HIV transcription in tractable latency models. Nonetheless, we will temper any language that implies broad generalization across all latency contexts and further discuss the limitations of clonal and transformed latency models. Additionally, and as the reviewers suggested, we will also test whether the KAT7/HBO1 and p300 inhibitor phenotypes extend to a primary CD4+ T-cell latency model.

We also appreciate comments regarding the RelB-miniTurbo system; notably concerns with the basal expression of the fusion protein and presence of endogenous RelB. We will revise the manuscript to better describe these limitations and discuss how they may affect interpretation of the BioID data. In particular, we will emphasize that the dataset should be viewed as a resource for candidate RelB-associated regulatory factors that require functional and orthogonal follow-up.

Several reviewers identified figure and text issues that will be addressed in the revised manuscript. Specifically, we will correct the Figure 1 legend and reference errors, the duplicated sentence, and other typos mentioned. We will also clarify the number of biological replicates and statistical thresholds used for the BioID comparisons, improve the Supplementary Table 1 annotation, and expand the discussion of p300/CBP to better reconcile our findings with prior literature.

Overall, the revised manuscript will more clearly separate what this study establishes from what remains to be tested. Our goal for revision will be to enhance the value of the study while more clearly highlighting the limitations and what this resource provides for future directions.

eLife Assessment

This manuscript presents valuable experimental results describing the localisation and regulation of casein kinase CK1δ during the cell cycle. During the G2 phase of the cell cycle, the autophosphorylation of the C-terminal tail stabilises and inhibits the kinase which might protect CK1δ in the subsequent G1 phase. The results may be of interest to researchers working on casein kinase function and regulation but due to lack of some controls remain incomplete.

[Editors' note: this paper was reviewed by Review Commons.]

Reviewer #1 (Public review):

Summary:

Involved in various cellular pathways and processes, Ser/Thr kinase CK1δ is thought to be constitutively active and its tail autophosphorylation is suggested as a putative inhibitory mechanism of CK1δ kinase activity. Here, the authors investigate CK1δ's phosphorylation status, in relation to its location and dynamics throughout the cell cycle. Immunofluorescence and biochemistry studies showed that the subcellular distribution of CK1δ is dynamic and in equilibrium between centrosomal and nuclear pools. The authors argue that CK1δ phosphorylation protects it from degradation. Finally, the authors show differences in CK1δ phosphorylation status and location throughout the cell cycle. Combining their findings with the existing literature, they propose a model of CK1δ phosphorylation status, location and dynamics throughout the cell cycle.

Comments on latest version:

The authors have unfortunately taken a very defensive mode There are two themes that authors resort to: 1) We have published previously with some reagents - therefore these are well-established and we do not need to include controls anymore; 2) Independent biological replicates and statistics are only appropriate in some places, again because certain observations have been previously published (by the same authors) and well-established. In my opinion, this is not how rigorous research should be done. Specially with IF, it is essential in every experiment to have robust negative controls.

Reviewer #2 (Public review):

Summary:

In this study, Serrano et al. employed a combination of cell biological and molecular approaches to investigate the localization and regulation of Casein Kinase CK1 during the cell cycle using U20S cells. They show that CK1 dynamically localizes between the centrosomes and the nucleus but can be sequestered away from the centrosomes upon overexpression of its binding partner PER2. They provide evidence that CK1 WT but not a phospho-null mutant strongly accumulates in a hyperphosphorylated form upon inhibition of phosphatases (using Calyculin and Okadaic Acid) and thus conclude that CK1 tail phosphorylation protects the kinase from degradation. Using synchronized cells, they show that CK1 accumulates unphosphorylated in S-phase (APC/Cdh1 inactive) but phosphorylated at the G2-M transition. Immunostaining shows that CK1 localizes to the centrosomes during mitosis.

Strengths:

The authors reveal that the activity and abundance of dephosphorylated and phosphorylated CK1δ are regulated in a cell cycle-dependent manner. This suggests that these different pools are associated with distinct physiological functions.

Comments on latest version:

Unfortunately, problems with controls remain in the revised manuscript. At the very least, the authors should include all the necessary controls in their study instead of referring to previously published papers. I have asked for a detailed description of the kinase construct in which the phospho-Serine and Threonine of the C-terminal tail are substituted, but I did not see any more information in the revised version.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

We appreciate the authors have provided answers to many of the points we raised, and the changes made to their manuscript, which we think strengthen the overall evidence presented. However, we find that some important controls are still missing across experiments.

Major comments:

(1) Shortcomings in Immunofluorescence experiments:

a. Antibody cross-reactivity was only tested against CK1ɛ, but should also be tested against CK1α, which is abundant in U2OS cells, and is also known to be involved in cell-cycle regulation.

We selected the CK1δ antibody (abcam, ab85320 clone AF12G4) precisely because of its well-established specificity for CK1δ. In many well-cited studies [An et al., Nature Communications, 2022, PMID: 35810166], [Eng et al., PLOS One 2017, PMID: 28545154], some of which involve direct comparison with CK1α and CK1ε [Sinnberg et al., BMC Cancer, 2016, PMID: 27488834], [Beale et al., Journal of Biological Rhythms, 2019, PMID: 30898060], the CK1δ (ab85320) antibody is cited directly as the antibody used to specifically detect CK1δ.

Additionally, through our previous eLife paper, we have confirmed the observation from previous studies that clearly demonstrate that this CK1δ (ab85320) antibody can specifically recognize CK1δ and not even its closest homolog CK1ε. Given the high degree of conservation in the kinase region between CK1δ and CK1ε, this implies that this antibody is likely directed at the divergent C-terminal tail (see sequence alignments in Author response image 1). Given that CK1α C-terminal tail is even more divergent from CK1δ, along with its reliable use in the literature from multiple working groups, it is safe to assume that this antibody can reliably distinguish CK1δ from CK1α.

Author response image 1.

Protein sequence alignments between CK1δ, CK1ε, and CK1α highlighting high sequence conservation in the structured kinase domain and sequence divergence at the C-terminal tail.

b. Fig. 1: Statistical analyses are missing from the analysis.

We have clearly added statistical analysis showing significant differences of CK1δ localization at the centrosome.

c. Fig. 2: No colocalisation analysis shown for figure 2, only some arrowheads pointing to puncta. Appropriate colocalisation statistics are important since for practical reasons, only a few representative images can be shown on the figure.

CK1δ colocalization is already well-established in the literature and additionally demonstrated in this study with the clear colocalization in Figures 1C and 1D. In Figure 2, we have chosen to report representative images which correspond to the typical phenotype we observe and can compare side-by-side which show clear and striking differences in terms of CK1δ localization between a) cells that form foci and lose CK1δ localization at a clear and distinct centrosome and b) cells that do not form foci and CK1δ is clearly localized to the apparent centrosome. By showing several fields-of-view, we demonstrate that this is the prevalent comparative phenotype.

d. Fig. 6: Even if the figure is illustrative, it is important to show centrosome staining to visualise CK1ẟ's recruitment to the centrosome in G2/prophase, especially since this information is used to propose the model in figure 7.

It is well-established that centrosomal duplication is a key hallmark of G2. Combined with our observations from Figure 2 showing that CK1δ to distinct puncta that one can only assume is the centrosome, and now showing in Figure 6, a clear duplication of these puncta. Importantly, this occurs in cells that also exhibit higher DAPI staining consistent with the duplicated and condensed genomic state when compared to other cells in the field of view, another hallmark of G2. Therefore, additional centrosomal staining and colocalization will only confirm what we already know about typical hallmarks of G2 and wider mitosis and the established CK1δ localization to the centrosomes.

e. For all figures: Please mention the number of independent biological replicates in the figure legends (1, 2, 6). For figure 1, if there are 3 independent biological replicates, the quantification should take all of them into account (as opposed to the data points corresponding to 10 cells), and statistics must be done appropriately, taking those independent replicates into account. Same for the colocalisation analysis in figure 2 once you include it.

We have mentioned the number of independent biological replicates where we considered it appropriate in Figures 3, 4, and 5. Figure 1 A and B are representative fields-of-view which show a replicable phenotype and we have quantified 10 cells to show the statistical difference in CKδ colocalization to PCNT. Figure 1 C and D show individual representative cells used for the line plot analysis but as one can already see from Figures 1 and B, these observations are clearly reproducible. Figure 2 A is an additional representative photo from observations we have made in our previous eLife publication. Figure 2 B already shows multiple fields-of-view which show a replicable result. Figure 6, again, shows a representative series of cells which already clearly demonstrate the change in CK1δ localization over the course of mitosis.

(2) Shortcomings in biochemistry experiments:

On CalA control, this is not a matter of confirming that CalA treatment works in principle, but rather to confirm that CalA treatment worked in this specific replicate. Aliquots may lose potency (e.g. with freeze-thaw cycles / exposure to light), hence checking for enrichment of phospho-proteins is essential to confirm the treatment was successful in this particular instance. In the worst-case scenario, the company may have sent the wrong compound altogether! A positive and a negative control is the basis for every experiment to make meaningful interpretation. On a separate note, many experiments have control and siRNA or compound treatments on two different gels - this should be rectified as they are meaningless if different exposures have been selected for different immunoblots.

I find it hard to seriously answer to these points. I do not know what kind of reagents the reviewer is used to work with. On every experiment we show as a sub-figure, we use the same CalA that clearly works as intended since we can clearly see a phosphorylation-induced gel shift of the kinase. This rules out aliquots losing their potency or supplier providing the wrong compound. We also show a clear negative control in showing the absence of the gel shift prior to CalA treatment.

On a separate note, we have no experiments with siRNA so we are unsure what the reviewer is referring to here. Of the 11 immunoblots we report here, each of which are representative of a triple replicate, only 1, Figure 3B, shows a split view on an equal exposure. Even then this was actually run on the same gel and this figure was simply spliced to simplify the message we want to convey. Therefore, we believe we have used the appropriate controls and level of rigor to make our observations and interpret them adequately.

(4) As the authors mention, the kinase is not fully inactive when tail phosphorylated. Recent research has also suggested that tail-phosphorylated CK1ẟ may show increased catalytic activity for a few select, specific substrates, in the co-occurrence of pT220 (Cullati et al., 2022; Cullati et al., 2024). It is thus tricky to directly infer that phosphorylated CK1ẟ is inhibited, when no positive control for CK1ẟ inhibition was shown in the evidence presented. It would be necessary to either nuance your claim or include a positive control for CK1ẟ inhibition. Please revise statements in the manuscript accordingly.

We have clearly demonstrated that CKδ tail phosphorylation leads to kinase inhibition and refer the reviewer to our work in PNAS [Marzoll et al., PNAS, 2021; PMID: 35217617].

(5) It would be important to include statistical analyses for the immunofluorescence data in Fig. 1 and 2.

We have included statistical analysis where we considered it appropriate in Figure 1 A and B. In Figure 1 C and D, statistical analysis is not appropriate to apply to compare single line plots as the individual data are clearly distinct from one another. For Figure 2 A and B, again, we are showing this data to show what is already a clear difference in CK1δ centrosomal localization when we compare cells that either form PER-CRY foci or do not.

(9) The authors mentioned "In the eLife study, we show that inhibition of kinase activity by PF670462 stabilizes CK1δ and that the overexpressed kinase-dead mutant CK1δ-K38R is stable." Unfortunately, the data from biochemical analyses presented in the eLife publication is uninterpretable due to a lack of loading controls.

We respect the reviewer’s opinion on this matter. However, the earlier study was independently peer-reviewed and has already been published. The reviewer was not involved in the assessment of that work, and we therefore feel that a retrospective evaluation of its merits is beyond the scope of the present review. We would respectfully ask that the current manuscript be evaluated on the basis of the questions it addresses and the evidence presented here.

(10) While the data presented in Penas et al. strongly suggests a link between CK1ẟ stabilisation and the APC/C-Cdh1 complex, it is the only study to have shown it. Given that (1) science relies on data reproducibility and (2) your proposed model relies heavily on the relationship between CK1ẟ stabilisation and the APC/CCdh1 complex, it would be appropriate to include the investigations mentioned in our original comment.

We respectfully point out that the purpose of the present review is to assess the manuscript under consideration, not to retrospectively reassess data that have already been published, such as those reported by Penas et al., even if this is the only study we cite in support of this particular point.

After checking the peer review received from Review Commons, we cannot see the “investigations in our original comment” that this reviewer is referring to.

Reviewer #2 (Public review):

In this study, Serrano et al. employed a combination of cell biological and molecular approaches to investigate the localization and regulation of Casein Kinase CK1 during the cell cycle using U20S cells. They show that CK1 dynamically localizes between the centrosomes and the nucleus but can be sequestered away from the centrosomes upon overexpression of its binding partner PER2. They provide evidence that CK1 WT but not a phospho-null mutant strongly accumulates in a hyperphosphorylated form upon inhibition of phosphatases (using Calyculin and Okadaic Acid) and thus conclude that CK1 tail phosphorylation protects the kinase from degradation. Using synchronized cells, they show that CK1 accumulates unphosphorylated in S-phase (APC/Cdh1 inactive) but phosphorylated at the G2-M transition. Immunostaining shows that CK1 localizes to the centrosomes during mitosis.

The manuscript has improved overall, but some sections are still inconclusive and require clarification.

Major comments:

Figure 1 is inconclusive. CK1 nuclear staining is highly similar in untreated cells and in cells treated with CHX + PF670462. The reduction in centrosomal staining in these cells is barely significant. However, the authors draw very strong conclusions from these data sets. In panel B, the cells appear to have been fixed incorrectly, and the anti-PCNT shows a strong background signal. Not convinced that immunofluorescence is the best approach to look at protein dynamics in vivo.

Figures 1 A and B are meant to show how CHX and PF670462 may affect CK1δ localization to the centrosome (stained by PCNT) over several cells whereas Figures 1 C and D are meant to more clearly show this effect in individual cells. This effect is indeed modest in the endogenous situation compared to the overexpressed which shows a clearer redistribution of CK1δ. We show this when we compare the quantification in Figure 1A and the colocalization analysis in Figure 1 C (right panel; showing that some CK1δ still colocalizes to the PCNT-stained centrosome) to their overexpressed counterparts. This however, only emphasizes the strength of our overexpression approach as it has allowed us to observe a more dramatic shift in CK1δ centrosomal localization.  

In Figure 2, panel B, the authors should co-stain the centrosomes of cells that co-express CRY1 and CK1, as some of these dots may represent the centrosomes.

In principle, we indeed cannot exclude the possibility that a CRY-stained foci may actually be a centrosome. However, we refer to our comments to Reviewer #1 and add our observation that these PER-CRY foci are clearly nuclear based on our earlier eLife publication and are therefore unlikely to be centrosomal. (If some of the dots represent centrosomes, this would mean that a fraction of CRY1 is recruited from the nucleus to the centrosome in the cytosol. There is no mechanism for this known.)

Figures 3B, please provide information on the non-phosphorylable CK1a mutant (it is mentioned as a variant in which all serine and threonine residues in the C-terminal tail were replaced by alanine). Specify the number of sites mutated and their exact position. Is this non-phosphorylable CK1a version catalytically active?

As said, all serine and threonine residues in the tail have been changed, and yes, the kinase is of course active.

Treatment of samples with inactivated PPase should be used as a control.

It is unclear what this experiment would control for and how its outcome would affect any of the conclusions of the present study.

Strengths:

The authors reveal that the activity and abundance of dephosphorylated and phosphorylated CK1δ are regulated in a cell cycle-dependent manner. This suggests that these different pools are associated with distinct physiological functions.

Weaknesses:

Unfortunately, some of the data are inconclusive, and there is no data/information linking the cell cycle regulation of CK1δ to its function during the cell cycle.

Although CK1δ continuously undergoes cycles of autophosphorylation and dephosphorylation, the kinase is predominantly found in its dephosphorylated, active state under steady-state conditions. This has obscured the physiological relevance of its well-established inhibitory autophosphorylation. We now identify mitosis as the cellular state in which this equilibrium shifts: autophosphorylated and consequently inhibited CK1δ accumulates. These findings resolve a longstanding question regarding the physiological function of CK1δ autophosphorylation and reveal it as a cell-cycle-regulated mechanism of kinase inhibition.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Most of our minor comments related to editorial issues have been ignored by the authors and the errors persist. Simple corrections will improve the manuscript and make it more readable.

We also found new minor errors as follows:

69-70: 'dependent on its kinase is activity' --> 'its kinase activity'

164: 'sites or targeted by' --> 'sites are targeted by'

179: 'PF670' instead of 'PF670462'

292: 'against higher the steady state levels' --> 'against the higher steady state levels' or 'against higher steady state levels'

We thank Reviewer #1 for their close reading of our text. We have adjusted the text accordingly.

eLife Assessment

This study provides an important insight into how the medial and lateral entorhinal cortices interact through distinct excitatory and inhibitory pathways. Using anatomical tracing, optogenetics, and electrophysiology, the authors show that glutamatergic medial entorhinal neurons provide broad excitatory input to lateral entorhinal, while long-range SST+ interneurons deliver selective inhibition to layer I. These findings reveal a novel layer- and cell-type-specific organization of medial to lateral entorhinal connectivity with implications for spatial and episodic memory. The evidence for the paper's overall conclusions is convincing.

Reviewer #1 (Public review):

The study addresses the organisation of synaptic connections from medial to lateral entorhinal cortex. Classic anatomical work has suggested these connections exist but very little is known about their identity or functional impact. The manuscript argues that these projections are mediated by glutamatergic neurons, providing excitatory input from MEC to all layers of LEC, and by SST+ve interneurons sending inhibitory projections to L1 of LEC. This appears the most likely interpretation of the data. Potential concerns about confounds due to spread of virus/tracer from the injection site are addressed in the supplemental figures. My view is that the weight of evidence favours the authors' interpretation although the evidence isn't quite compelling.

Knowing the configuration of projections from MEC to LEC is important for thinking about circuit mechanisms for spatial cognition and episodic memory. This study adds to an emerging view that MEC and LEC can interact directly, indicating that the cell-type level organisation of these interactions is asymmetric and identifying an intriguing long range inhibitory pathway.

Reviewer #2 (Public review):

Summary:

The manuscript by Nilssen et al. presents a comprehensive study of the circuitry linking the medial and lateral entorhinal cortices (MEC and LEC). Using a combination of anatomical tracing, optogenetics, and in vitro electrophysiology, the authors convincingly demonstrate that the MEC sends both glutamatergic and long-range inhibitory SST+ GABAergic projections to the LEC, with distinct laminar and cell-type-specific targeting. Notably, they reveal that SST+ inhibitory projections selectively suppress the activity of layer IIa neurons, whereas excitatory inputs preferentially engage neurons in layers IIb and III, thereby differentially modulating hippocampal-projecting populations.

Strengths:

The experiments are carefully executed, the results are compelling, and the conclusions are well supported by the data. This work will be of broad interest to researchers studying memory circuits, cortical inhibition, and the organization of long-range connectivity.

Weaknesses:

Although the in vivo relevance of these connections remains to be determined, this is an important and timely contribution to our understanding of entorhinal-hippocampal interactions.

Comments on revised version.

The authors have addressed my comments satisfactorily, and I am satisfied with the changes made in the revised version.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

The study addresses the organisation of synaptic connections from the medial to the lateral entorhinal cortex. Classic anatomical work has suggested these connections exist, but very little is known about their identity or functional impact. The manuscript argues that these projections are mediated by glutamatergic neurons, providing excitatory input from MEC to all layers of LEC, and by SST+ve interneurons sending inhibitory projections to L1 of LEC. This appears to be the most likely interpretation of the data, although in my opinion, more could be done to rule out the possible impact of the spread of the virus/tracer from the injection site.

While this concern might seem overly picky, the importance of this level of detail is nicely shown by the authors' previous work clarifying connectivity from postrhinal to entorhinal cortices through careful analysis of similar types of data (Doan et al. 2019). If additional analyses/data can address the concern here, then I think this will be an important set of fundamental results that will influence thinking about circuit mechanisms for spatial cognition and episodic memory. In particular, it will nicely add to an emerging view that MEC and LEC can interact directly, showing that the organisation of these interactions is asymmetric and identifying a potentially interesting long-range inhibitory pathway.

Reviewer #2 (Public review):

Summary:

The manuscript by Nilssen et al. presents a comprehensive study of the circuitry linking the medial and lateral entorhinal cortices (MEC and LEC). Using a combination of anatomical tracing, optogenetics, and in vitro electrophysiology, the authors convincingly demonstrate that the MEC sends both glutamatergic and long-range inhibitory SST+ GABAergic projections to the LEC, with distinct laminar and cell-type-specific targeting. Notably, they reveal that SST+ inhibitory projections selectively suppress the activity of layer IIa neurons, whereas excitatory inputs preferentially engage neurons in layers IIb and III, thereby differentially modulating hippocampal-projecting populations.

Strengths:

The experiments are carefully executed, the results are compelling, and the conclusions are well supported by the data. This work will be of broad interest to researchers studying memory circuits, cortical inhibition, and the organization of long-range connectivity.

Weaknesses:

Although the in vivo relevance of these connections remains to be determined, this is an important and timely contribution to our understanding of entorhinal-hippocampal interactions.

The request for validation of injection specificity and viral spread, as detailed in the comments and suggestions of the two reviewers has been provided in the revised version. We added supplementary figures 1,2 and 6 as well as an extra insert into the old supplementary figure 5, now supplementary figure 9.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Major Points:

(1) Interpretation of the retrograde labelling experiment in Figure 1A-C is challenging, as the spread of the tracer at the injection site is not shown. It's important to see the full dorsal-ventral extent of the injection site in order to establish that the labelling of neurons in MEC results from projections to LEC and not adjacent areas (including MEC).

As mentioned in our initial reply, we are fully aware of the risks associated with an incomplete assessment of injection sites and viral spread, so we provide a new Supplementary Fig. 1 showing 6 dorsoventral levels of the case shown in Fig. 1A. The injection site in case of FG often shows a core of damaged tissue with a halo of substantial unspecific fluorescence. Outside of the injection side, one only sees retrogradely labeled somata (often recognizable by FG signal clustered in lysosomes) and dendritic elements. As indicated in the legend, we report some tracer leakage along the needle track in temporal and perirhinal cortex, areas that receive only sparse MEC projections, but there is no apparent spread of the injection into MEC.

Numbers are also quite low. E.g., Figure 1A is N=1/2 for retrograde labelling experiments.

The reviewer would be correct if the experiments were meant to analyze MEC projections to LEC in full anatomical detail. This was not our intention (several papers addressed this pathway in detail), we merely aimed to distinguish between glutamatergic and potential GABAergic contributions to this pathway and to establish optimal coordinates in slices to prepare for the electrophysiological recording experiments. Two animals suffice for this purpose and using more would be against the aim of reducing the use of experimental animals as much as possible.

The rationale here for the use of AAV2-CAG-tdTomato as a retrograde tracer is unclear. My understanding is that this is more effective as an anterograde tracer. Some clarification and validation would be important.

The reviewer is correct that AAV2 is generally considered an effective anterograde tracer, but tracing the connectivity of entorhinal cortex with AAVs has been proven to be notoriously difficult, in particular retrograde tracing of inputs to layer II. In a neighboring lab in the centre, headed by Edvard and May-Britt Moser, it was established that AAV2 types show very efficient retrograde transport and that is why we decided to use the virus. Also, in our hands the virus showed excellent retrograde transport that served our purpose

(2) Interpretation of the anterograde experiments in Figure 1D-E would also benefit from showing evidence that the injection sites are restricted to MEC. It should be straightforward to make a supplemental figure showing labelling at all dorsoventral levels.

More careful analysis of the axon labelling in the dentate gyrus could also help make a case for the selectivity of the injection site for eGFP. In this case, only the intermediate portion of the molecular layer of the DG should be labelled. In the image shown, the labelled band is quite wide, but it's hard to tell if this reflects the plane of section or is because it also includes labelling in the outer molecular layer (which would be indicative of LEC expression).

We thank the reviewer for these two suggestions, and we have prepared a new Supplementary Fig. 2 in line with this.

Numbers are also on the low side for these experiments.

See our response above

(3) For optogenetic experiments in Figure 2, the selectivity of targeting of AAV to MEC is assessed through the specificity of labelling in the DG. This is great, but it's important to show that this specificity is maintained at all dorsoventral levels.

Higher resolution images of labelling in LEC could also be helpful. It's hard to tell from the images in 2A if labelling is axonal or is in the soma adjacent to the nuclear NeuN signal (which would indicate a lack of selectivity for MEC).

We thank the reviewer for these two suggestions and provide a new Supplementary Fig. 6, showing both the details of AAV1 being present only in neuropil in MEC not in somata as well as the specific labeling in the middle molecular layer of DG in detail. Including all dorsoventral levels would not provide additional information in view of the very well-established topographical organization of the entorhinal to dentate projection, reaching approximately 20 -25 % of the full long axis of DG (Van Groen et al., 2003)

In addition, we have again carefully screened all tissue from the electrophysiological experiments for possible leakage of virus from MEC to LEC. We decided to exclude recordings from one mouse, which had labelling in MEC that was close to the border with LEC. Neuron counts have therefore been adjusted (pages 7-9) and the example recording showing responses to TTX/4-AP exposure in Figure 2B has been exchanged.

(4) The analysis of excitatory and inhibitory opto-responses in Figure 2 is nice. It may be helpful to report quantification of the rise and decay kinetics of the synaptic currents. They appear much slower for the inhibitory input, which may be functionally important.

This would indeed be nice to add, but it would not significantly impact or change the main message of our study. Since the lab of the senior author (MPW) has been discontinued and the resources for conducting these analyses are not readily available anymore, we have found it difficult to comply with the reviewer’s request

(5) More direct evidence for SST axons projecting from MEC to LEC would strengthen the conclusions made. E.g., in experiments where the SST neurons are labelled, is it possible to follow the axons? Do they project as expected from the MEC to the LEC?

In our view the tracing data provide convincing evidence in support of a direct projection from MEC to LEC by SST neurons, as shown in horizontal brain sections where SST axons labelled in MEC of an SST^Cre mouse projects within Layer I from the site of origin in MEC to Layer I of MEC (Supplementary Figure 3). Similar visualizations were not possible to obtain in our electrophysiological experiments where semicoronal slices were used. This cutting angle has been shown to be optimal to preserve most of the axon and the dendritic tree of LEC neurons (Tahvildari and Alonso, 2005; Canto and Witter 2012), but does not maintain the projection from MEC to LEC.

Minor Points:

(1) "These layers are heavily innervated by medial entorhinal axons (Figure 1F...". I don't see a 1F.

This has been corrected; should have been Figure 1E.

(2) Methods should report series resistance values for patch-clamp experiments (range and mean).

Fully agree and this information has now been added on page 22 of the manuscript:

Under Voltage clamp: ‘Recordings with series resistance ≤ 25 MΩ were accepted, with an average of 16.2 MΩ for voltage clamp recorded neurons (range, 4.9 – 24.9 MΩ).’

Under Current clamp: ‘All recordings (series resistance: 18.9 MΩ, 5.0 – 66.7 MΩ; mean, range) were included for analysis.’

Reviewer #2 (Recommendations for the authors):

(1) Please specify in the figure or, alternatively, in the figure legend which virus was used in each group shown in Figures 2H and 2I. This is somewhat confusing, since Figure 2E illustrates a specific combination of viruses and mouse lines that only corresponds to part of Figure 2H. While this information is provided in the text, including it directly in the figure would help the reader.

We thank the reviewer for this excellent suggestion, and we have implemented this in the new version of figure 2.

(2) In Figure 4, regarding the inputs from PIR, cLEC, and PER to LEC, the inhibitory components recruited by each input were not examined as thoroughly as for the MEC inputs. In fact, some inhibitory interneurons were double-labeled in the GAD67 mice (Figure 4B), which could also influence the responses of LEC neurons, especially for PER inputs. Recordings in Figure 4C appear to have been obtained near the reversal potential for inhibition, which may have prevented the observation of inhibitory effects. The authors could discuss this point in the Results.

The reviewer is correct and this issue is now addressed in the relevant section in the results (page 11):

‘It should be noted, however, that it is possible that inhibitory effects could have been masked in some recordings, due to the resting membrane potential in our recordings being close to the theoretical chloride equilibrium potential. This could be particularly relevant for the inputs from PER, an area where we found LEC-projecting GABAergic neurons (Fig. 4B) and which is known to provide long-distance inhibition to LEC (Pinto et al., 2006; Apergis- Schoute et al., 2007).’

(2) A diagram summarizing the known connections among MEC, LEC, and the hippocampal formation, highlighting the relevant cell types, layers, and the new connections identified in this study, would be a valuable addition, perhaps as a supplementary figure.

We appreciate the suggestion, though find a full summary of known connectivity a bit overdone. Instead, we included a new figure 6 that summarizes the main new findings of the paper in the context of LEC projections to the hippocampal formation.

(3) Although the main focus is on MEC-LEC connectivity, the experiments examining interactions with other cortical areas and converging inputs would benefit from a discussion of how MEC-driven inhibition of LEC might influence those inputs and shape the resulting output to the hippocampus. Including a short paragraph addressing this in the Discussion section would strengthen the manuscript.

Excellent suggestion although we did speculate briefly in the result section on the possible effect. We have added a short paragraph in the discussion (page 15), reiterating the part in the results (page 13, last paragraph of results). We also briefly discussed the potential functional relevance of the suppression of the pathway from layer IIa to DG-CA3/CA2 versus the facilitation of activity in the pathway from layers IIb/III to CA1 and subiculum (last section of the discussion).

(4) Lastly, it would be interesting to know what the main source of activation is for the SST long-range LEC projecting neurons. Are these neurons recruited in a feedback manner by the activity of MEC excitatory cells? I realize this question is beyond the scope of the present study, but if the authors have any data or insights related to this point, including a brief discussion would be valuable.

This is an interesting thought, and we have included a new supplementary figure (supplementary Figure 5) showing data from experiments mapping monosynaptic inputs to MEC SST neurons using rabies virus. Although it was not possible to target only MEC SST neurons that project to LEC, the data show which are the main extrinsic inputs to the population of MEC SST neurons, most likely including those that project to LEC.

eLife Assessment

This important study introduces Hetlearn, a novel learning algorithm that demonstrates that an ensemble of simple sub-learners with varying learning rates can effectively manage inference in complex, unstable environments. While the theoretical framework and its proposed application to parallel memory traces in the insect mushroom body are intriguing, the evidence supporting the core claims is currently incomplete. To fully validate the authors' conclusions, further exploration is needed to rigorously define the boundaries of the model's hyperparameter space, along with a deeper justification and clarification of its biological plausibility.

Reviewer #1 (Public review):

The authors describe a learning algorithm that is meant to deal with the problem of inference in large, complex environments. They argue that simpler but ensemble learning systems with heterogeneous learning rates often perform better than more complex approaches. They also relate the ideas of their model to a circuit implementation in the mushroom body, an associative learning area in insects.

I found the argument about the value of sublearners remaining simple to be thoughtful and intriguing. I also appreciated the connection to biology and, although there remain details to be worked out, it seems that the proposed approach has what I'd call a "biologically plausible" instantiation.

Comments on the major claims:

The paper claims that algorithms that learn stochasticity and volatility "necessarily result in worse short-term performance than Hetlearn." The results with Autocovariance Least Squares and the model of Piray and Daw are consistent with this statement, but the authors seem to be making a more generic claim. Is there a rigorous justification of this? In particular, I found the section "Competing sublearners should stay simple" to straddle a line between opinion and fact, and I wasn't sure where it intended to be regarding that line.

Relatedly, regarding the statement just before that section: "The exponential convergence of Hetlearn weightings stands in contrast to the slow convergence of stochasticity/volatility estimates (Figures 2A and C), which result in poor initial performance of the Kalman learner." Is the claim here that the Kalman learner doesn't converge exponentially, or that it converges more slowly?

The paper would benefit from a comparison to other models of multiple learning systems with different timescales. The classic one would be the complementary learning systems ideas about hippocampus and neocortex (McClelland, McNaughten, O'Reilly 1995), and the many subsequent follow-ups. Two other relevant ones to consider are Roxin & Fusi 2013 and Lindsey & Litwin-Kumar 2024, which also consider multiple memory systems with different plasticity rates.

Comments on clarity:

(1) Page 2: There could be some more unpacking of the relationship between x and z in equations 1a, 1b. If z_t are time-varying, shouldn't theta, if it represents what is learned about "large-world factors," also depend on time?

The description of second-order conditioning on page 6 is confusing. Second-order conditioning tests whether S2 acquires a positive predicted value after pairing with S1, which had previously been paired with reward. The text makes it seem like the goal of second-order conditioning is to learn S2->S1->no reward.

(2) Page 6: "Representations decay on a slower timescale than stimulus presentation. Hence, the representation x2 after experiencing S2 → S1 holds traces of the S2 representation." I couldn't understand this. Maybe an equation would help?

(3) Page 7: The phrase "unconditioned stimulus" is introduced without being described. Is this a reward or punishment? What does it have to do with valence lower-case v, or value upper-case V? The authors seem to mix notations from different subfields, leading to a rather confusing description of the model.

Comments on relationship to biology:

(1) Page 6: It is assumed that Kenyon cells interact recurrently through plastic weights. This is an unconventional assumption for mushroom body models, and it is made without much discussion. The authors cite papers that argue for changes in the calyx during learning (although these effects are generally much weaker than the well-documented plasticity onto MBONs). However, KC-to-KC interactions are largely in the lobes, not the calyx. The authors should provide more discussion of this assumption. What happens if the recurrence is weak or absent? A relevant reference to consider is Manoim et al. Current Biology 2022, which shows that KC-to-KC interactions are inhibitory.

The model seems to imply that each MBON compartment encodes only one memory, or did I misunderstand? Is this necessary? Typically, it is thought that because of the sparse, decorrelated representations in the KCs, an individual MBON could store multiple associations without too much interference.

Reviewer #2 (Public review):

Summary:

The authors propose Hetlearn, a novel learning algorithm for unstable environments: instead of using statistically optimal methods to estimate the variability of the environment, simply have a range of "sub-learners" that learn at different rates, and rely more heavily on the sub-learners with a recent track record of success. This strategy is particularly helpful when the environment has unknown and fluctuating stochasticity (randomness around a constant mean reward) and volatility (the mean itself changes over time). For high stochasticity and low volatility, it's better to learn slowly to smooth out randomness; for low stochasticity and high volatility, it's better to learn quickly to catch onto the new trend. The authors show that existing methods work well when stochasticity and volatility are constant, or when methods can learn them over a long time, but that Hetlearn does better when stochasticity and volatility change over time or an agent has limited time or data to learn from.

They then propose that the fly mushroom body implements a form of Hetlearn, since it has different compartments that form parallel memory traces at different learning and forgetting rates. Here, the conclusions are less clear because their model doesn't appear to implement the key feature of Hetlearn (the differential weighting of sublearners based on recent success), and because their model has features that don't have an obvious biological equivalent in the real mushroom body.

Strengths:

The idea behind Hetlearn is clever and interesting, and it makes sense that a heuristic method like Hetlearn would outperform a theoretically optimal algorithm under conditions of limited data. The model is clearly defined, and they test it across a range of tasks and compare it to a range of different Kalman/particle filter learners. The application to the mushroom body is also an inspiring connection and takes advantage of the discovery of empirically described sublearners. The work will stimulate new ways of understanding how biological systems might implement heuristic tricks that may not be optimal under ideal conditions, but that succeed in "real world" conditions, and it will stimulate new thinking about the computational role of parallel memory traces in the mushroom body.

Weaknesses:

In the tests of Hetlearn vs. Kalman filters, it would be useful to more fully explore the parameter space. Specifically, in Figures 1-2, it would help define the boundaries of when Hetlearn is better or worse than Kalman filters, by systematically changing the parameters of the task (e.g. increasing/decreasing the amount of data available to the learner or the frequency of changing stochasticity/volatility), and changing the parameters of Hetlearn (the learning rates of the sublearners and the recency bias, i.e. how far back to track the recent success of the sublearners when weighting their outputs). For Figure 3, while they do check the performance when varying the recency bias, there are no conditions presented in which the particle filter does better. To define when Hetlearn is better, it is important to show when it is worse.

In the mushroom body model, there are several elements that have no apparent biological equivalent, and it's not clear whether they are incidental (in which case they could be removed to enhance biological realism) or essential to the model's performance (in which case the discrepancy should be discussed; perhaps the model can be reframed as a prediction for as-yet-undiscovered features). In addition, the model seems to lack the defining feature of Hetlearn (up/down-weighting sublearners according to their recent performance). Finally, the authors argue that Hetlearn explains experimental data better than existing models, but existing models could be easily and parsimoniously tweaked to accommodate these data, so the explanatory advantage of Hetlearn is unclear.

eLife Assessment

In this useful study, Millard et al. assessed the effects of nicotine on pain sensitivity and peak alpha frequency (PAF). They propose a solid experimental framework to test the modulatory effects of nicotine on PAF and pain sensitivity, but the evidence is incomplete to support the claims that the chosen experimental intervention may actually play a significant mechanistic role in pain sensitivity given the modest effect sizes observed. The work can be incorporated into the literature investigating the relationship between nicotine and pain and could be of broad interest to pain researchers.

Reviewer #2 (Public review):

Summary:

The study by Millard et al. investigates the effects of nicotine on peak alpha frequency and pain using a highly elaborate experimental design. According to the statistical analysis, the authors found a small covariate-corrected effect for prolonged heat pain and a small effect on global peak alpha frequency in response to nicotine treatment. However, the effect on heat pain was not found for pressure pain, was not mediated by peak alpha frequency, and appears mainly based on a worsening in the placebo condition rather than a clear reduction of pain after nicotine.

Strengths:

I very much like the study design and that the authors followed their research line by aiming to provide a complete picture of the pain-related cortical impact of peak alpha frequency. This is important work, even in the absence of clear statistical or mechanistic support for the main hypothesis. I also appreciate the preregistration of the study, the well-written and balanced introduction, and the additional analyses added during revision.

Weaknesses:

The weakness of the study revolves around two main aspects:

(1) Source separation would still have been more appropriate than electrode regions or global peak alpha frequency to extract the alpha signal. The added ICA analysis is appreciated, but in my view, it does not fully solve the problem. Different alpha sources, such as mu rhythm, occipital alpha, and lateralised alpha activity, are still not clearly disentangled. The main peak alpha frequency effect remains a small global, wide-band, sensor-space effect rather than a clearly source-specific sensorimotor effect.

(2) I still think the choice of nicotine is a major weakness of the study. The rationale for using nicotine as an intervention rests partly on previous reports of nicotine effects on experimental pain, but the most relevant cited meta-analysis already suggested that these effects are small and may be affected by publication bias. It is therefore not a clean way to test whether peak alpha frequency has a causal role in pain. The heat-pain result is also difficult to interpret as analgesia. Statistically, the placebo-controlled contrast may be significant, but in practice, the nicotine condition changed very little, and the effect seems mainly driven by worsening in the placebo group. In a real intervention, one gives the drug, not the difference between drug and placebo.

Impact:

The impact of the study could be to show what did not work to answer the authors' research question. The study is valuable because it provides a careful and largely negative mechanistic test: nicotine produced at most small effects, peak alpha frequency did not mediate pain, and pressure pain was not affected. The study would have more impact with a more direct intervention model and an analysis strategy that more clearly untangles the different alpha sources.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, Millard and colleagues investigated if the analgesic effect of nicotine on pain sensitivity, assessed with two pain models, is mediated by Peak Alpha Frequency (PAF) recorded with resting state EEG. The authors found indeed that nicotine (4 mg, gum) reduced pain ratings during phasic heat pain but not cuff pressor algometry compared to placebo conditions. Nicotine also increased PAF (globally). However, mediation analysis revealed that the reduction in pain ratings elicited by the phasic heat pain after taking nicotine was not mediated by the changes in PAF. Also, the authors only partially replicated the correlation between PAF and pain sensitivity at baseline (before nicotine treatment). At the group-level no correlation was found, but an exploratory analysis showed that the negative correlation (lower PAF, higher pain sensitivity) was present in males but not in females. The authors discuss the lack of correlation.

In general, the study is rigorous, methodology is sound and the paper is well-written. Results are compelling and sufficiently discussed.

Strengths:

Strengths of this study are the pre-registration, proper sample size calculation, and data analysis. But also the presence of the analgesic effect of nicotine and the change in PAF.

Weaknesses:

It would even be more convincing if they had manipulated PAF directly.

We thank Reviewer #1 for their positive and constructive comments regarding our study. We appreciate the view that the study was rigorous and methodologically sound, that the paper was well-written, and that the strengths included our pre-registration, sample size calculation, and data analysis.

In response to the reviewer's comment about more directly manipulating Peak Alpha Frequency (PAF), we agree that such an approach could provide a more direct investigation of the role of PAF in pain processing. We chose nicotine to modulate PAF as the literature suggested it was associated with a reliable increase in PAF speed. As mentioned in our Discussion, there are several alternative methods to manipulate PAF, such as non-invasive brain stimulation techniques (NIBS) like transcranial alternating current stimulation (tACS) or neurofeedback training. These approaches could help clarify whether a causal relationship exists between PAF and pain sensitivity. Although methods such as NIBS still require further investigation as there is little evidence for these approaches changing PAF (Millard et al., 2024).

Reviewer #2 (Public Review):

Summary:

The study by Millard et al. investigates the effect of nicotine on alpha peak frequency and pain in a very elaborate experimental design. According to the statistical analysis, the authors found a factor-corrected significant effect for prolonged heat pain but not for alpha peak frequency in response to the nicotine treatment.

Strengths:

I very much like the study design and that the authors followed their research line by aiming to provide a complete picture of the pain-related cortical impact of alpha peak frequency. This is very important work, even in the absence of any statistical significance. I also appreciate the preregistration of the study and the well-written and balanced introduction. However, it is important to give access to the preregistration beforehand.

Comment on latest version:

I thank the authors for their efforts to respond to my previous concerns. I appreciate the additional analyses and the more cautious wording in several places. However, I still think the manuscript would benefit from a more direct interpretation of the findings.

Reviewer #3 (Public Review):

In this manuscript, Millard et al. investigate the effects of nicotine on pain sensitivity and peak alpha frequency (PAF) in resting state EEG. To this end, they ran a pre-registered, randomized, double-blind, placebo-controlled experiment involving 62 healthy adults who received either 4 mg nicotine gum (n=29) or placebo (n=33). Prolonged heat and pressure were used as pain models. Resting state EEG and pain intensity (assessed with a visual analog scale) were measured before and after the intervention. Additionally, several covariates (sex at birth, depression and anxiety symptoms, stress, sleep quality, among others) were recorded. Data was analyzed using ANCOVAequivalent two-wave latent change score models, as well as repeated measures analysis of variance. Results do not show ‘experimentally relevant’ changes of PAF or pain intensity scores for either of the prolonged pain models due to nicotine intake.

The main strengths of the manuscript are its solid conceptual framework and the thorough experimental design. The researchers make a good case in the introduction and discussion for the need to further investigate the association of PAF and pain sensitivity. Furthermore, they proceed to carefully describe every aspect of the experiment in great detail, which is excellent for reproducibility purposes. Finally, they analyse the data from almost every possible angle and provide an extensive report of their results.

The main weakness of the manuscript is the interpretation of these results. Even though some of the differences are statistically significant (e.g., global PAF, pain intensity ratings during heat pain), these differences are far from being experimentally or clinically relevant. The effect sizes observed are not sufficiently large to consider that pain sensitivity was modulated by the nicotine intake, which puts into question all the answers to the research questions posed in the study.

We would like to express our gratitude to Reviewer #3 for their thoughtful and constructive review, including the positive feedback on the strengths of our study's conceptual framework, experimental design, and thorough methodological descriptions.

We acknowledge the concern regarding the experimental and clinical relevance of some statistically significant results (e.g., global PAF and pain intensity during heat pain) and agree that small effect sizes may limit their practical implications. However, our primary goal was to assess whether nicotine-induced changes in PAF mediate pain changes, rather than to demonstrate large direct effects on pain sensitivity. Nicotine was chosen for its known ability to modulate PAF, and our focus was on the mechanistic role of PAF in pain perception. To clarify this, we have revised the discussion to better differentiate between statistical significance, experimental relevance, and clinical applicability. We emphasize that this study represents a preliminary step towards understanding PAF’s mechanistic role in pain, rather than a direct clinical application.

We appreciate the suggestion to refine our interpretation. We have adjusted our language to ensure it aligns with the effect sizes observed and made recommendations for future research, such as testing different nicotine doses, to potentially uncover stronger or more clinically relevant effects.

Although modest, we believe these findings offer valuable insights into the potential mechanisms by which nicotine affects alpha oscillations and pain. We have also discussed how these small effects could become more pronounced in different populations (e.g., chronic pain patients) and over time, offering guidance for future research on PAF modulation and pain sensitivity.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

I thank the authors for their efforts to respond to my concerns. I very much admire the thoughts and effort that the authors have put into this study. This is a great study design, a fantastic research idea and an important path to study the neurophysiology of pain.

I also understand that some of my suggestions are not compatible with the authors' current line of analysing their data. Since the authors did not change the analysis procedure and obviously could not change their experimental design, I would largely keep my public review.

However, acknowledge the different opinions and have a few remarks and suggestions.

(1) In agreement with reviewer 3, I would not consider the effect of nicotine to be meaningful. The random effect mentioned by the authors could have been addressed with a crossover design. In this case, the placebo and intervention could have been directly compared. Interindividual differences in pain perception are at least partially controlled for by analysing the difference between pre and post-gum. The distribution of the pre-post difference separately for placebo and nicotine would be a valuable addition to the manuscript. I still think the minimal effect of nicotine on pain is not meaningful and not interpretable. The relevance of any explanatory variable like stress could be by chance (PMID: 35296861). Reviewer 3 had a valid point (comment 6) and this is something that should be mentioned as clearly as possible: there was no effect of nicotine. For PHP the comparison with the placebo is irrelevant if there is no pre vs. post-effect.

It is fair to say that some issues could have been resolved using a cross-over design, however, the choice of a parallel design was made, in part, due to the desire to mask the presence of a placebo gum. Having a single session per participant allowed us to produce a deception that all participants were receiving nicotine gum, which was later revealed during a debrief. This aspect is far less feasible in a cross-over design. In future, different approaches could be used. And we appreciated the reviewers recognition that this cannot, of course, be changed at this stage.

Regarding the comments of 1) ’I would not consider the effect of nicotine to be meaningful’, 2) the minimal effect of nicotine on pain is not meaningful and not interpretable’, and 3) ’there was no effect of nicotine’, we discern that the latter differs considerably from the first two points. We would like to address this point by first calling into question what the reviewer(s) mean by meaningful, and highlighting that discerning this varies by context. Edenberg (2021) highlights that meaning can be situated within several contexts: statistical, biological (mechanistic), clinical, and public policy. We show the statistical context, and therefore would like to emphasise that we cannot state number 3) ’there was no effect of nicotine’.

Although the complexity of our analysis is not at the same scale, we appreciate the need for thousands of participants for brain-wide associations, as cited (PMID: 35296861 = Marek et al., 2022). The article referenced states that reproducible brain-wide association studies require thousands of individuals, and thus we would like to highlight that our work indicating the potential relevance of sex/stress greatly differs from this. Though it may be by chance, the potential for that chance is 0.05 from a statistical significance perspective. Certainly, no finding should be taken as truth without replication, but that does not mean we should not report our finding of a statistically significant effect of stress on change in PAF in our model.

Then, the question becomes, are we already at the point where the issue of ’how to go beyond statistical significance’ should be addressed? One could argue no, as this is the first study to assess this question of nicotine’s effect on PAF and pain at the same time. But we would like to argue yes, although only to the mechanistic/biological level, because the question of what is meaningful is dependent on the study goals (Edenberg, 2021). We aimed to gain mechanistic insight into the PAF-pain relationship.

We hoped to achieve some biological/mechanistic meaning in the present study, however, as outlined in the discussion, with small effect sizes for nicotine on PAF and nicotine on heat pain, and lack of a mediating effect, we may not have achieved this. Although, if replicated, even small magnitude effects can shape our understanding of relevant mechanisms underlying pain and aid future clinical perspectives (Edenberg, 2021; Ross & Bassett, 2024). Meaningfulness in clinical or public policy contexts should of course be in mind, but were clearly not the focus of this present work.

We have edited the manuscript to demonstrate the fact that our effect size is small.

We corrected the rounding to 2 decimals, and now also refer the reader to the supplementary materials table:

“Change in pain was reduced by a factor of -0.68 for the nicotine group compared to the placebo group when controlling for confounding variables (Figure 3). See Supplementary Material 3.2, Table 5, for full model output.”

We edited the abstract and the first paragraph of the discussion to make clear to the reader that the effect sizes were small. In our desire to keep the text clear and readable, we did not intend to overstretch our claims, and apologise if the manuscript was unintentionally portraying this overstretch. These are very important sections of the manuscript in which to mention such nuances, as these are the parts viewed most when readers do not wish to read the entire manuscript.

Abstract

“The nicotine group showed a small decrease in heat-pain ratings compared to placebo group when controlling confounders, and a small increase in PAF across the scalp from pre- to post-gum, both with and without confounder adjustment. These effects were most pronounced in the central-parietal and right-frontal electrodes.”

Discussion first paragraph

“Compared to placebo, our data demonstrate three key findings: 1) nicotine increased PAF speed; 2) nicotine reduced prolonged heat pain intensity but only when controlling for confounding and not for the prolonged pressure pain model, and 3) decreases in prolonged heat pain intensity were not mediated by changes in PAF. This suggests that changes in heat pain due to nicotine occur through mechanisms unrelated to change in PAF and require replication as the effects required control for confounding and the reduction was small in magnitude.”

Discussion section on effect of nicotine on PAF:

“In line with previous literature in non-smokers [38,47,48], we contribute additional evidence that chewing 4 mg of nicotine gum produces a statistically significant increase in PAF speed in non-smoking, nicotine-gum-naïve, pain-free, adult participants. An exploratory cluster-based permutation analysis indicated that the change in wide-window PAF (8–12 Hz) produced by nicotine, was most pronounced in a cluster of electrodes in the central-parietal region and a separate cluster of electrodes in the right-frontal region, rather than in the pre-registered sensorimotor ROI (i.e., Cz, C1, C2, C3, C4).”

Discussion section on the effect of nicotine on pain:

“While acknowledging the modest effect size, it’s essential to consider the context of our study’s focus. Assessing the clinical relevance of pain reduction is pertinent in applications involving the use of any intervention for pain management [71]. However, from a mechanistic standpoint, particularly in understanding the implications of and relation to PAF, the specific magnitude of the pain effect becomes less pivotal, as small effects can still have mechanistic or biological meaning without establishing clinical meaning [72]. Nevertheless, future research should examine whether effects on pain increase in magnitude with different nicotine administration regimens (i.e. dose and frequency).” 

Discussion section on relationship between PAF and pain:

“However, as this is the first study attempting to directly manipulate PAF, observing only small effects on pain, we cannot confidently state that a causal relationship between PAF and pain sensitivity does not exist, and future research should explore these relationships with larger sample sizes, larger doses of nicotine, and alternative PAF modulators.”

Discussion final paragraph:

“We have shown that, compared to placebo, nicotine gum produced statistically significant increases global PAF speed and decreases pain ratings during prolonged heat pain. However, the effects of nicotine on heat pain were not mediated by changes in PAF. Therefore, we find no evidence that PAF is causally related to pain. The implication of this is that changing PAF may not be a useful target for pain modulation, because pain sensitivity may not be dependent on state changes in PAF. However, this is the first study to test modulation of PAF as a mechanism for reducing pain intensity. Moreover, while effects on PAF appear small but robust, effects on heat pain required control for confounding to be observed. More randomised experiments on the effects of nicotine that use larger sample sizes, higher nicotine doses, and pharmacokinetic tracking, whilst also reducing mediator measurement error are needed to confirm the present findings and uncover whether these factors account for the lack of mediation effect seen here.”

(2) I still think the authors made a mistake in using nicotine. Their new wording did not convince me, and I doubt that any reader would buy the "mediation by design" phrase.

We addressed the reviewers previous comment (comment 1) on nicotine being a ‘mistake’, and no longer suggest there is a “large body of evidence suggests that nicotine is an ideal choice for manipulating PAF”. We have been clearer about our intention to assess mediation-by-design, with the manipulation of PAF being out primary aim. For example, this edit in the discussion:

“The choice of nicotine was driven by its potential to change PAF, but also, short-term nicotine use is thought to have acute analgesic properties in experimental settings, with a review reporting that nicotine increased pain thresholds and pain tolerance [51].”

In addition, we discussed the ’direct’ manipulation of PAF using non-invasive brain stimulation methods, and have now added further future research directions using methods other than nicotine or NIBS:

“Furthermore, there may have been other mediators that suppress the mediating effects of PAF within our model [66,82,83]. This is plausible, as nicotine is thought to act on pain through multiple pathways [52,54,84], and more direct PAF modulation could more definitively evaluate whether PAF is mechanistically linked to pain sensitivity. Future interventions to modulate PAF could use non-invasive brain stimulation (NIBS), such as transcranial alternating current stimulation (tACS) or repetitive transcranial magnetic stimulation (rTMS), to influence neuronal firing and thereby directly target the brain mechanisms theorised to generate PAF [85–87]. This approach has since been investigated following the initial preprint of

the present manuscript [88,89]. In addition, other approaches to modulating approaches could be considered, such as exercise [32–34], visual stimulation [35,36], cannabis [90,91], and neurofeedback [92,93], while considering their viability in terms of blinding, tolerability, and scalability.”

(3) I acknowledge the work of the authors on SNR, the frequency spectrum looks smooth enough to detect peaks. However, the problem of different alpha sources is not solved. This can be seen in the frequency spectrum, where some participants show two peaks. This is not the first time I have suggested this to the authors; the idea is not new. The fMRI analogue would be to average all GM voxels; instead of global alpha it would be "global brain activity". Some suggestions for a future approach that the authors might consider:

Run a group ICA and select topographies from there. This should simplify the (potentially arbitrary) selection process.

Consider filtering the data before running the ICA, at least >20 Hz to exclude muscle artefacts.

We respectfully note that the reviewer’s comment appears to overlook the substantial revisions we have already made in direct response to this issue. Specifically, we implemented ICA in the revised manuscript, using an automated, objective pipeline to identify components with a clear alpha peak and a topography aligned with a predefined sensorimotor template. This was explicitly done to address concerns about overlapping alpha sources and improve anatomical specificity.

Contrary to the reviewer’s implication, we did not rely solely on global analyses in the original or revised manuscript, as we also included pre-defined ROIs and data-driven ROIs from cluster-based permutation analysis. The additional ICA-based analyses—included in the first revision—produced results that were consistent with the original sensor-space ROI findings, supporting the robustness of the PAF–pain mediation effect regardless of the method used to isolate sensorimotor alpha.

We agree that group ICA could be a valuable complementary approach. However, it is not without limitations, particularly in EEG where inter-individual variability in source topographies is high. Our choice to perform ICA at the individual level and apply an automated selection criterion based on spectral and spatial features was deliberate, data-driven, and avoids the subjectivity involved in manual selection or group-level back-projection.

We have added a discussion of this point and fully acknowledge that future work may benefit from comparing multiple alpha sources (e.g., mu vs. occipital) more explicitly. However, we must emphasise that this is not a missing analysis—it is already included in the revised manuscript. In this second revision, we have added an additional reference to this supplementary analysis within the section previously titled “Exploratory cluster-based permutation anlaysis”, now titled “Exploratory data-driven analysis of alpha”, in case the previous reference to it was in a sub-optimal location:

“Lastly, use of in-house code developed to automatically extract a sensorimotor alpha component using independent component analysis (ICA) showed similar results to the sensorimotor ROI mediation analysis (Supplementary Material 3.11). This supports the robustness of the PAF-pain effect regardless of the method used to isolate sensorimotor alpha.”

We strongly disagree with the suggestion to apply a low-pass filter below 20 Hz prior to ICA. This would remove high-frequency content, including muscle activity—the very signals ICA is designed to isolate and separate from neural activity.

By removing muscle-related frequencies before ICA, the reviewer’s proposed approach would prevent ICA from identifying muscle components in the data. This is methodologically flawed. as ICA works best when it has access to the full spectral range of the signal, allowing it to separate statistically independent sources— including muscle, eye movements, and neural oscillations—based on their spatial and temporal structure (Onton et al., 2006). Thus the desired sensorimotor alpha component would be more distinct if the full spectral range is included. Low-pass filtering the data before ICA designed to identify alpha would severely compromise artifact removal, degrade component separation, and reduce the effectiveness of our preprocessing pipeline.

References for responses to reviewer 2

Edenberg HJ. Perspective on beyond statistical significance: Finding meaningful effects. Complex Psychiatry 2021;7:1–8. https://doi.org/10.1159/000517237.

Marek S, Tervo-Clemmens B, Calabro FJ, Montez DF, Kay BP, Hatoum AS, Donohue MR, Foran W, Miller RL, Hendrickson TJ, Malone SM. Reproducible brain-wide association studies require thousands of individuals. Nature. 2022 Mar 24;603(7902):654-60.

Ross LN, Bassett DS. Causation in neuroscience: keeping mechanism meaningful. Nature Reviews Neuroscience. 2024 Feb;25(2):81-90.

Reviewer #3 (Recommendations for the authors):

I would like to thank the authors for the time and dedication that they clearly put into addressing the reviewer's comments. As researchers, we alternate between both sides (as authors and reviewers) and we are all privy of how difficult these tasks can be.

For me as a reviewer, this is one of the tough times. I wanted to support this manuscript because it is clear that conducting the study had to be a monumental effort, and there were early indications that it was rigorously carried out. Specifically referring to rigor, I value preregistration as a tool to assess the strength of the hypothesis posed before conducting the study, and the severity with which the claims are tested. During my first review, I tried to access the preregistration and even provided my email address as a sign of transparency, but access was not granted. During my second review, the main file in the submission system contained two versions of the same manuscript (the first one corresponding to the old version with the wrong preregistration link). I was not initially aware of this and I apologize for the misunderstanding.

With respect to the rest of my observations, I see that the authors made concessions on small and less relevant issues (e.g. comments #1, #2, #3), but did not satisfactorily address the main ones (#4, #5, #6, #7, #8 and #9). Addressing those comments (which are in line with the issues noted by other reviewers), would probably have lead to a different interpretation of the results compared with what they state in the first paragraph of the discussion.

The main claims (abstract and first paragraph of the discussion) are " 1) nicotine increased PAF speed; 2) nicotine reduced prolonged heat pain intensity but not prolonged pressure pain intensity compared to placebo gum". Just by reading and contrasting the claims with the results, my assessment is that the strength of evidence is inadequate.

I was now able to review the analysis plan, which did not contain an estimation of the effect sizes (only effect directions) and did not have a proper sample size estimation (comment #4) and the main outcome was not, to my understanding, based in terms of the beta coefficients (as you replied to reviewer #1). I also do not think that the possibility of no effect or a false positive (comment #5) is fairly weighed in relation to these main claims in the abstract an first paragraph of the discussion.

I also do not consider the response to comment #6 as satisfactory, first because it is a mistake to consider that we (as reviewers) only interpret the 'mean results'. As we have detailed access to the data, we interpret these results in terms of signal-to-noise ratio, i.e., how large is the effect (signal) compared with the intra and interindividual variance (noise), and it should be clear for anyone working on this fields (pain and EEG) that not only the main effect is not experimentally relevant to support the claims (comments #6 and #7), but in some cases it is likely to have arisen from the unjustified inclusion of covariates (comment #8 and #9). I only raise the final strength of evidence in my assessment from 'inadequate' to 'incomplete', because of the additions to the discussion.

As a final thought, I would have been more than happy to support and recommend the reading of a manuscript that described a carefully designed and preregistered study, but in which the hypothesis were not corroborated by the data. I would have even marked the strength of evidence as compelling. Unfortunately, the preregistered hypothesis cannot be severely tested (at least not in terms of a frequentist framework) because the effects sizes were not predefined and the required sample size was not estimated, and what I see from the manuscript is that there is an effort to maintain claims that are not properly supported by the data and the final analysis. I recognized that I myself can also be in the wrong, so it will be left for eLife readers to make up their own minds.

We respectfully disagree with the assertion that our preregistered hypotheses "cannot be severely tested" due to the absence of predefined effect sizes and sample size estimation. First, the primary purpose of preregistration is to increase transparency and reduce analytical flexibility—not necessarily to formalize power calculations, especially when reliable effect size estimates are unavailable, as is the case in emerging areas of research such as this one (Nosek et al., 2018). Predefining effect sizes based on speculative or contextually irrelevant prior studies would have introduced unjustified assumptions and potentially distorted interpretation. In this case, we made the scientifically responsible choice to avoid anchoring our design on uncertain estimates. 

Second, our sample size is comparable to or larger than those used in prior published studies addressing similar questions, and our analytic pipeline followed the preregistered plan. The reviewer suggests that we are attempting to maintain unsupported claims; however, our discussion is careful to reflect the limitations of the findings, including their statistical uncertainty, and we do not overstate conclusions. Where effects were weak or absent, we reported this transparently and interpreted them cautiously.

Finally, while formal power calculations are useful under certain conditions, they are not a prerequisite for a study to be considered a "severe test" of a hypothesis—especially when the statistical approach is preregistered, data are handled transparently, and null results are acknowledged rather than hidden. The sample size was informed by resource and feasibility constraints (Lakens, 2022) and aligns with or exceeds that of comparable studies in the field (Bowers et al., 2015). We have now made this rationale explicit in the manuscript.

“The sample size was informed by resource and feasibility constraints [98] and aligns with or exceeds that of comparable studies in the field [38], covering 60 participants in total, with two extra in case of incomplete data identified during later data analysis.”

We therefore maintain that the study is a valid and informative contribution, regardless of whether the observed results confirm or disconfirm the hypotheses.

Nonetheless, below we have revisited previous comments (#4, #5, #6, #7, #8 and #9) that reviewer 3 stated were not satisfactorily addressed.

Previous comment 4) Availability of the pre-registration

We consider this point now addressed, as access to the OSF pre-registration was resolved. Moreover, we can assure the reviewer that their identity was not revealed, as the request for access was not received/seen.

Previous comment 5) Magnitude of pain change – possibility of a type 1 error.

Previous comment 5) To be perfectly clear, I trust the results of this study more than some of the cited studies regarding nicotine and pain because it was preregistered, the sample size is considerably larger, and it seems carefully controlled. I just do not agree with the interpretation of the results, stated in the first paragraph of the Discussion. Quoting J. Cohen, "The primary product of a research inquiry is one or more measures of effect size, not P values" (Cohen, 1990). As I am sure the authors are aware of, even tiny differences between conditions, treatments or groups will eventually be statistically significant given arbitrarily large sample sizes. What really matters then is the magnitude of these differences. In general, the authors hypothesize on why there were no differences on the pressure pain model, and why decreases in heat pain were not mediated by PAF, but do not seem to consider the possibility that the intervention just did not cause the intended effect on the nociceptive system, which would be a much more straightforward explanations for all observations.

Our previous response included the fact that N=62 is not an arbitrarily large sample size and our consideration of the possibility of a false positive. In addition, we agree that conclusions should not be made based on p-values alone. Therefore, we have added more careful descriptions to highlight the nuances of our findings to the reader.

We edited the abstract and the first paragraph of the discussion to make clear to the reader that the effect sizes were small. In our desire to keep the text clear and readable, we did not intend to overstretch our claims, and apologise if the manuscript was unintentionally portraying this overstretch. These are very important sections of the manuscript in which to mention such nuances, as these are the parts viewed most when readers do not wish to read the entire manuscript.

Abstract

“The nicotine group showed a small decrease in heat-pain ratings compared to placebo group when controlling confounders, and a small increase in PAF across the scalp from pre- to post-gum, both with and without confounder adjustment. These effects were most pronounced in the central-parietal and right-frontal electrodes.”

Discussion first paragraph

“Compared to placebo, our data demonstrate three key findings: 1) nicotine increased PAF speed; 2) nicotine reduced prolonged heat pain intensity but only when controlling for confounding and not for the prolonged pressure pain model, and 3) decreases in prolonged heat pain intensity were not mediated by changes in PAF. This suggests that changes in heat pain due to nicotine occur through mechanisms unrelated to change in PAF and require replication as the effects required control for confounding and the reduction was small in magnitude.”

Discussion section on effect of nicotine on PAF:

“In line with previous literature in non-smokers [38,47,48], we contribute additional evidence that chewing 4 mg of nicotine gum produces a statistically significant increase in PAF speed in non-smoking, nicotine-gum-naïve, pain-free, adult participants. An exploratory cluster-based permutation analysis indicated that the change in wide-window PAF (8–12 Hz) produced by nicotine, was most pronounced in a cluster of electrodes in the central-parietal region and a separate cluster of electrodes in the right-frontal region, rather than in the pre-registered sensorimotor ROI (i.e., Cz, C1, C2, C3, C4).”

Discussion section on the effect of nicotine on pain:

“While acknowledging the modest effect size, it’s essential to consider the context of our study’s focus. Assessing the clinical relevance of pain reduction is pertinent in applications involving the use of any intervention for pain management [71]. However, from a mechanistic standpoint, particularly in understanding the implications of and relation to PAF, the specific magnitude of the pain effect becomes less pivotal, as small effects can still have mechanistic or biological meaning without establishing clinical meaning [72]. Nevertheless, future research should examine whether effects on pain increase in magnitude with different nicotine administration regimens (i.e. dose and frequency).”

Discussion section on relationship between PAF and pain:

“However, as this is the first study attempting to directly manipulate PAF, observing only small effects on pain, we cannot confidently state that a causal relationship between PAF and pain sensitivity does not exist, and future research should explore these relationships with larger sample sizes, larger doses of nicotine, and alternative PAF modulators.”

Discussion final paragraph:

“We have shown that, compared to placebo, nicotine gum produced statistically significant increases global PAF speed and decreases pain ratings during prolonged heat pain. However, the effects of nicotine on heat pain were not mediated by changes in PAF. Therefore, we find no evidence that PAF is causally related to pain. The implication of this is that changing PAF may not be a useful target for pain modulation, because pain sensitivity may not be dependent on state changes in PAF. However, this is the first study to test modulation of PAF as a mechanism for reducing pain intensity. Moreover, while effects on PAF appear small but robust, effects on heat pain required control for confounding to be observed. More randomised experiments on the effects of nicotine that use larger sample sizes, higher nicotine doses, and pharmacokinetic tracking, whilst also reducing mediator measurement error are needed to confirm the present findings and uncover whether these factors account for the lack of mediation effect seen here.”

Previous comment 6) Magnitude of pain change

Previous comment (6) In this regard, I do not believe that an average *increase* of 0.05 / 10 (Nicotine post pre) can be considered a "reduction of pain ratings", regardless of the contrast with placebo (average increase of 0.24 / 10). This tiny effect size is more relevant in the context of the considerable inter-individual variation, in which subjects scored the same heat pain model anywhere from 1 to 10, and the same pressure pain model anywhere from 1 to 8.5. In this regard, the minimum clinically or experimentally important differences (MID) in pain ratings varies from study to study and across painful conditions but is rarely below 1 / 10 in a VAS or NRS scale, see f. ex. (Olsen et al., 2017). It is not my intention to question whether nicotine can function as an acute analgesic in general (as stated in the Discussion), but instead, if it worked as such under these very specific experimental conditions. I also acknowledge that the authors note this issue in two lines in the Discussion, but I believe that this is not weighed properly.

Our previous response included discussion of interpreting mean values, a correction to a table that showed the ”increase” erroneously displayed previously due to list-wise deletion in the analysis. We have further attempted to weigh this issue more thoroughly and to always highlight the nuances of our results, as seen in our response to your previous comment 5 above. In further consideration of the effect size, note that the bootstrapped 95% CI for the effect of gum on change in pain was [-1.28, -0.16], which indicates that the overall difference falls within this range when controlling for other factors in the model. Of course this means the difference may be as small as -0.16, but also may be as large as -1.28. Such an effect might have be considered clinically relevant. Replication of the results is therefore warranted.

Also, as outlined in our response to reviewer 2 comment 1, our intention was not to establish a clinical utility at this stage. We hoped to achieve some biological/mechanistic meaning in the present study, and if our present findings are replicated in future, even these small-magnitude effects can shape our understanding of relevant mechanisms underlying pain and aid the direction of future clinical perspectives (Edenberg, 2021; Ross & Bassett, 2024). Meaningfulness in clinical (e.g., MID) or public policy contexts should of course be in mind, but were not the focus of this present work.

Several additional changes were made to the manuscript to emphasise these points to the reader, which are also outlined in the second round of response to your first comment 5 above, as both this comment 6 and 5 focus on magnitude of pain change. We hope this point is now considered to be weighed properly.

Previous comment 7) Magnitude of PAF change

Previous comment (7) In line with the topic of effect sizes, average effect sizes for PAF in the study cited in the manuscript range from around 1 Hz (Boord et al., 2008; Wydenkeller et al., 2009; Lim et al., 2016), to 2 Hz (Foulds et al., 1994), compared with changes of 0.06 Hz (Nicotine post - pre) or -0.01 Hz (Placebo post - pre). MIDs are not so clearly established for peak frequencies in EEG bands, but they should be certainly larger than some fractions of a Hertz (which is considerably below the reliability of the measurement).

In our first response to this comment, we acknowledged this difference in magnitude, agreed that MIDs for PAF are not established, discussed the potential impact of bin size, and highlighted this issue in the revised manuscript text. Although, note that we have now slightly reduced the emphasis on the bin size:

“The ability to detect changes in PAF could be considerably impacted by the frequency resolution used during Fourier Transformations, an element that is overlooked in recent methodological studies on PAF calculation [16,95].”

In addition, we would now like to highlight some more details regarding the prior studies.

We aimed to determine whether nicotine gum could increase PAF in healthy, pain-free, non-smokers. In line with previous literature in non-smokers (Foulds et al., 1994; Harkrider and Champlin, 2001; Bowers et al., 2015), we contribute additional evidence that chewing 4 mg of nicotine gum produces small increases in PAF speed in non-smoking, nicotine-gum-naïve, pain-free, adult participants. The other three papers mentioned by the reviewer are not cited in our manuscript and compare healthy individuals to chronic pain patients (Boord et al., 2008; Wydenkeller et al., 2009; Lim et al., 2016), and are thus not relevant to this discussion on the effect of nicotine on PAF.

A cluster-based permutation analysis indicated that the change in wide window PAF (8-12 Hz) produced by nicotine, was most pronounced in a cluster of electrodes in the central-parietal region and a separate cluster of electrodes in the right-frontal region, rather than in the pre-registered sensorimotor ROI (i.e., Cz, C1, C2, C3, C4). The mediation analysis results showed minimal differences when these clusters of electrodes were used compared to global results (global: b = 0.085, p < .018), except for the expected stronger effect of nicotine on change in PAF alongside greater confidence in this effect (bs = 0.11-0.14, ps < .003). See Supplementary Material 3.8-3.10.

Previous work examining nicotine-induced changes in PAF in healthy non-smokers have used small samples (i.e. <= 20) with nicotine injections or patches (Foulds et al., 1994; Harkrider and Champlin, 2001), while a later investigation used 62 male participants and nicotine gum (Bowers et al., 2015). Therefore, the present study is the largest study to date on nicotine and PAF including non-smoking male and female participants. Bowers didn’t see effects as large as 1 or 2 Hz (approx. 10 or 20% increases) seen in studies with fewer participants, such as n=4 (Foulds et al., 1994) and n=20 (Harkrider & Champlin, 2001), and the magnitude and location of effect depended on the COMT (Bowers et al., 2015).

Bowers et al (2015) showed that the Met allele was related to nicotine-induced increases in PAF, whereas Val/Val homozygotes did not demonstrate PAF changes. In addition, the distribution of PAF increases varied depending on whether Met allele carriers were heterozygotes (i.e. Val/Met: frontal, central, and occipital electrodes) or homozygotes (i.e. Met/Met: parietal electrode). The largest difference between placebo and nicotine gum was 0.51 Hz (a 5.8% increase) at the Fz electrode for the Val/Met group and the smallest significant difference was 0.34 Hz (a 3.5% increase) at the Pz electrode for the Met/Met group.

This study from Bowers used 6mg of nicotine gum, whereas we used 4mg, which may contribute to the lower effect size seen in our study. Dose-dependent effects have not been assessed in non-smokers, but given the dose-dependent changes seen in smokers who abstained from cigarettes prior to EEG recording (Pickworth et al., 1989; Pickworth et al., 1988; Pickworth et al., 1986), the smaller effect sizes seen in the present study may be in line with Bowers study.

Though genetic analysis was not included in the present work, the use of a lower nicotine dose, inclusion of male and female participants, use of more electrodes (64 rather than 8), and unmeasured genetic variations in PAF’s response to nicotine could explain the smaller effect sizes compared to (Bowers et al., 2015).

We have written a condensed summary of this to include in the manuscript discussion:

”Research on nicotine-induced changes in PAF in healthy non-smokers has largely relied on small samples (≤20) using injections or patches [47,48], with Bowers and colleagues [38] providing the only larger study (n= 62 males) using 6 mg nicotine gum. Their results showed modest PAF increases (~0.34–0.51 Hz; 3.5– 5.8%) compared to the larger effects (1–2 Hz; ~10–20%) reported in earlier small-sample studies, with magnitude and scalp distribution influenced by COMT genotype: Met allele carriers exhibited nicotineinduced increases (Val/Met: frontal, central, occipital; Met/Met: parietal), while Val/Val homozygotes showed no change. The present study now the largest to include both male and female non-smokers found smaller effects, likely due to the lower nicotine dose (4 mg), consistent with dose-dependent PAF modulation reported in abstinent smokers [69]. Broader EEG coverage (64 vs. 8 electrodes), sex inclusion, and unmeasured genetic variation may also account for differences between the present study and Bowers and colleagues [38]. Interestingly, beyond nicotine’s main effect on PAF, our 2W-LCS mediation model indicated a significant influence of sex, with females showing greater PAF increases than males. Given that female participants were significantly lighter than males (Supplementary Material 3.4) and the model did not test the interaction between sex at birth and gum group, these finding should be interpreted cautiously and warrant further investigation.”

Previous comment 8) removing confounders calls to question robustness of the findings. Simmons paper

Previous comment (8) The authors also ran alternative statistical models to analyze the data and did not find consistent results in terms of PHP ratings (PAF modulation was still statistically significantly different). The authors attribute this to the necessity of controlling for covariates. Now, considering the effects sizes, aren't these statistically significant differences just artifacts stemming from the inclusion of too many covariates (Simmons et al., 2011)? How much influence should be attributable to depression and anxiety symptoms, stress, sleep quality and past pain, considering that these are healthy volunteers? Should these contrasting differences call the authors to question the robustness of the findings (i.e., whether the same data subjected to different analysis provides the same results), particularly when the results do not align with the preregistered hypothesis (PAF modulation should occur on sensorimotor ROIs)?

In addition to our previous response, we would like to add the following: Although we were previously unaware of the author recommendations from Simmons et al (2011) during initial preparation of this manuscript, we find we cover all points and have added a few improvements to ensure our adherence to this guideline is clear.

We cover all six recommendations for authors suggested in Simmons et al (2011):

(1) We decided to collect 62 participants prior to commencing data collection, this covered 60 participants in total, with two extra in case of incomplete data identified during data analysis.

(2) We had more than 20 participants per group. We have now outlined this decision in the methods section:

“The sample size was informed by resource and feasibility constraints [98] and aligns with or exceeds that of comparable studies in the field [38], covering 60 participants in total, with two extra in case of incomplete data identified during later data analysis.”

(3) We provide detailed methods, which outlines all the variables collected.

(4) We report all experimental conditions, and had no failed manipulations to report. We have now slightly adjusted the wording of our experimental protocol within the methods section to make this clear:

“Participants were randomly assigned to one of only two conditions, thus after the second resting-state EEG, either nicotine or placebo gum was administered with the chew procedure. Following completion of the chew procedure, the third resting state, the second pain assessments, and the fouth resting state were conducted.”

Regarding recommendation (5), listwise deletion was used, as already stated in the manuscript (see Methods, Statistical analysis, Mediation analysis, Assumptions), to exclude participants for whom only one timepoint was available in either the pain or PAF measures, and thus it is not possible to conduct analysis on participants with this missing data. Otherwise, no participants were removed for other reasons. 6) As we conducted analyses using pre-registered covariates determined based on a DAG, we repeated analyses without including these covariates in the form of RM-ANOVAs. The effect on PAF remains, however, as Simmons et al (2011) suggests, the fact we no longer observed a significant effect of gum on heat pain ratings may indicate that the finding is reliant on the presence of a covariate, which does not necessarily mean that the finding is not relevant. However, as reviewer 3 suggests, this should also cause us to question the robustness of the findings and the possibility of type 1 error. Therefore, we have adjusted text in the discussion as follows:

“This underscores the necessity of controlling for confounding variables, as nicotine may only produce pain reduction for those with higher stress, and calls for further investigation into the robustness of the effect of nicotine on heat pain ratings.”

Lastly, regarding the influence that should be attributable to our confounding health-related measures, given the healthy population, we still observe variation in several of these confounders. ’Healthy’ populations still score across a range on these scales, with cut-offs acting as suggestions for problematic symptomology. Assumptions testing confirmed the normality of these covariates, and lack of collinearity so that they could be included in our analyses. We have added a sentence to the Sample Characteristics in Results to outline the ranges reported for the confounding variables:

“Depressive symptoms ranged from 0-4 (out of a maximum of 6), anxiety from 0-6 (out of a maximum of 6), perceived stress from 2-18 (out of a maximum of 40), and sleep quality from 2-10 (out of a maximum of 10; i.e. “excellent sleep quality”).”

Previous comment 9) Exploratory sex analysis?

(9) Beyond that, I believe in some cases that the authors overreach in an attempt to provide explanations for their results. While I agree that sex might be a relevant covariate, I cannot say whether the authors are confirming a pre-registered hypothesis regarding the gender-specific correlation of PAF and pain, or if this is just a post hoc subgroup analysis. Given the large number of analyses performed (considering the main document and the supplementary files), caution should be exercised on the selective interpretation of those that align with the researchers' hypotheses.

To reiterate our previous response to this comment, we stated that sex was an exploratory analysis in the results and was chosen based on other PAF-pain literature, and had also adjusted part of the discussion to align with this. However, we have now seen the first paragraph of the discussion was not adjusted. Therefore, we hope the below edit has now adequately address the previous reviewer 3 comment 9:

“In addition, when assessing the whole sample, we found inconclusive evidence for 4) slower PAF speed at baseline being associated with higher pain ratings for both the heat and pressure pain models. However, during exploratory analysis we found moderate evidence that slower PAF speed at baseline is associated with higher heat pain ratings at baseline in males but not females. In contrast PAF was not associated with pressure pain ratings for males or females.”

References for response to reviewer 3

Boord P, Siddall PJ, Tran Y, Herbert D, Middleton J, Craig A. Electroencephalographic slowing and reduced reactivity in neuropathic pain following spinal cord injury. Spinal cord. 2008 Feb;46(2):118-23.

Bowers H, Smith D, De La Salle S, Choueiry J, Impey D, Philippe T, et al. COMT polymorphism modulates the resting-state EEG alpha oscillatory response to acute nicotine in male non-smokers. Genes, Brain and Behavior 2015;14:466–76.

Edenberg HJ. Perspective on beyond statistical significance: Finding meaningful effects. Complex Psychiatry 2021;7:1–8. https://doi.org/10.1159/000517237.

Foulds J, McSorley K, Sneddon J, Feyerabend C, Jarvis MJ, Russell MA. Effect of subcutaneous nicotine injections on EEG alpha frequency in non-smokers: A placebo-controlled pilot study. Psychopharmacology 1994;115:163–6.

Harkrider AW, Champlin CA. Acute effect of nicotine on non-smokers: III. LLRs and EEGs. Hearing Research 2001;160:99–110.

Lakens D. Sample size justification. Collabra: psychology. 2022 Mar 22;8(1):33267.

Lim M, Kim JS, Kim DJ, Chung CK. Increased low-and high-frequency oscillatory activity in the prefrontal cortex of fibromyalgia patients. Frontiers in human neuroscience. 2016 Mar 14;10:111.

Nosek BA, Ebersole CR, DeHaven AC, Mellor DT. The preregistration revolution. Proceedings of the National Academy of Sciences. 2018 Mar 13;115(11):2600-6.

Pickworth WB, Herning RI, Henningfield JE. Electroencephalographic effects of nicotine chewing gum in humans. Pharmacology Biochemistry and Behavior 1986;25:879–82.

Pickworth WB, Herning RI, Henningfield JE. Mecamylamine reduces some EEG effects of nicotine chewing gum in humans. Pharmacology, Biochemistry, and Behavior 1988;30:149–53.

Pickworth WB, Herning RI, Henningfield JE. Spontaneous EEG changes during tobacco abstinence and nicotine substitution in human volunteers. Journal of Pharmacology and Experimental Therapeutics 1989;251:976–82.

Ross LN, Bassett DS. Causation in neuroscience: keeping mechanism meaningful. Nature Reviews Neuroscience. 2024 Feb;25(2):81-90.

Simmons JP, Nelson LD, Simonsohn U. False-positive psychology: Undisclosed flexibility in data collection and analysis allows presenting anything as significant. Psychological science. 2011 Nov;22(11):1359-66.

Wydenkeller S, Maurizio S, Dietz V, Halder P. Neuropathic pain in spinal cord injury: significance of clinical and electrophysiological measures. European Journal of Neuroscience. 2009 Jul;30(1):91-9.

eLife Assessment

The identification of a pleiotropic EPAS1 enhancer that influences adipocyte responses to hypoxia and thermogenic stimulation provides a valuable contribution to our understanding of high-altitude adaptation in Tibetans. The data are solid, although additional experiments would strengthen the link between ENH5 activity and the mechanisms underlying high-altitude adaptation.

Reviewer #1 (Public review):

In the article, the authors set out to characterize in adipocytes an enhancer, ENH5, of the gene EPAS1, a gene that was found to show strong selection in Tibetan populations. They investigate whether this enhancer contributes to adipocyte response to environmental stress. The authors show that ENH5 is active in preadipocytes and that the Tibetan high-altitude allele confers reduced activity. They then use a mouse ENH5 knockout model to show a hypoxia/thermogenesis responsive phenotype of stronger transcriptional downregulation of aerobic respiration, electron transport chain, and adipogenesis pathways. The authors interpret these findings as evidence that ENH5 conditionally regulates adipocyte energetics and thermogenic response, potentially favoring energy conservation in Tibetans exposed to the demands of high-altitude hypoxia and cold. Overall, the paper presents an interesting potential connection between EPAS1-mediated high-altitude tolerance and energy metabolism; however, more work needs to be done to establish this connection.

Major comments:

(1) The authors use mouse ENH5 enhancer knockout (ENH5-KO) as the model of the Tibetan EPAS1 locus because the high-altitude allele of human ENH5 has lower transcriptional activity than the low-altitude allele (Figure 1A) and mouse ENH5 (musENH5) has enhancer activity (Figure 1D) in mouse preadipocytes. However, it is an overstatement to claim the functional role of Tibetan ENH5 haplotype only based on these data because musENH5 is neither identical to human ENH5 nor the murine high-altitude haplotype. The title should also be revised to better reflect the function of ENH5, like "An EPAS1 enhancer mediates hypoxic and cold response in mouse adipocytes". The authors should consider in some way to actually show that the Tibetan haplotype in ENH5-KO leads to expression changes. This could be done by inserting the haplotype into preadipocytes via CRISPR (realize this is a tough one) or if they have available cells from Tibetans or some eQTL or other similar datasets. The more closely they can connect this haplotype to EPAS1 expression, the more beneficial it would be for the article. As it stands, they currently have episomal luciferase assays showing reduction of enhancer activity in mouse preadipocytes of a human allele and a complete knockout of the mouse enhancer that doesn't recapitulate the Tibetan haplotype. A bit more work is needed to connect all of these to the Tibetan adaptation. As it stands now, this is all very circumstantial.

(2) In Figure 2A, the body weight of ENH5-KO normal diet is significantly lower until four weeks in male, and until 11 weeks and 18 and 19 weeks in female than that of WT. These are slight but significant differences between ENH5-KO and WT; therefore, the authors should describe and discuss this and how it could affect their results.

(3) For the mouse work, it is not clear why the authors did not do cold-exposure or some type of hypoxia experiment for the mice themselves. This will be helpful to support their claim, and if not done, or done without significant differences in the results, the authors should add and mention this. The RNA-seq work, while substantial, again provides circumstantial support.

(4) The authors used CL316243 as a β3-AR selective agonist to mimic thermogenesis in vitro. In humans, it is not β3-AR but β2-AR that mainly drives thermogenesis (Blondin et al., Cell Metabolism, 32, 287-300. e7). Therefore, the authors should describe the limitation due to the difference in mechanisms of action of thermogenesis between humans and mice, as they use the mouse cells as a human model.

(5) The authors note in the discussion that Figure 3's CL316243 stimulation intended to simulate a thermogenic reaction to cold temperatures also generated a change in OXPHOS pathways associated with hypoxia, thus making it difficult to separate the contribution of β3-adrenergic/thermogenic effect from an indirect local hypoxia response. The authors could further interrogate this effect by measuring canonical hypoxia-responsive genes, oxygen consumption, or performing an in vivo cold challenge.

(6) Figure 4: The authors mention that reduced aerobic respiration pathways are evidence for reduced thermogenesis, but it does not directly demonstrate altered thermogenesis correlates. They do not measure heat synthesis, oxygen consumption/respiration, uncoupled respiration, UCP1 protein levels or activity, mitochondrial changes, etc. Their evidence for changed thermogenesis stems from transcriptional changes in energy consumption pathways shared with hypoxia changes. They should tone down their findings.

(7) In the Discussion, the authors should interpret and discuss their data carefully. For example, in the GSEA analysis, the authors identified enriched gene sets in ENH5-KO. Therefore, the authors should discuss which genes might contribute to each pathway, since some genes show large logFC changes. In the current discussion, there is little mention of their results, and it mostly focuses on prospects.

Reviewer #2 (Public review):

Summary:

This study extends previous work on the adaptive EPAS1 locus by examining the pleiotropic activity of the ENH5 enhancer in adipocytes and its potential role in metabolic and thermogenic responses. The authors progress from demonstrating enhancer activity and evolutionary conservation to in vivo phenotyping and environmentally dependent transcriptional responses in primary adipocytes. The work provides an interesting example of how pleiotropic regulatory effects can contribute to the complexity of adaptation, with a single adaptive regulatory locus influencing multiple biological processes in an environmentally dependent manner.

Strengths:

The study is well executed and is clearly presented, with a logical experimental progression. A particular strength is the genotype-by-treatment interaction analysis demonstrating that ENH5 loss alters metabolic and adipocyte-associated transcriptional programs following both hypoxia and beta-3-adrenergic stimulation. The convergence of these responses is particularly interesting in the context of regulatory pleiotropy and suggests that selection at the EPAS1 locus may have consequences extending beyond the canonical hypoxia response. The inclusion of negative findings, including the absence of an overt baseline metabolic phenotype and the lack of an additive response to combined stimulation, also provides a balanced presentation of the results.

Weaknesses:

The principal conclusions are generally supported by the data, and the weaknesses are relatively minor and primarily relate to the scope of interpretation. The study assesses transcriptional programs associated with thermogenic signaling using CL316243 rather than directly measuring physiological thermogenesis. Nonetheless, CL316243 is a rational and well-established approach for experimentally inducting beta-3-adrenergic thermogenic signaling. In addition, the murine ENH5 knockout is a useful model of reduced enhancer activity that phenocopies the Tibetan ENH5 haplotype, but it is not genetically equivalent to the naturally occurring Tibetan ENH5 haplotype. The authors generally recognize these limitations, and they do not substantially detract from the central findings.

eLife Assessment

This study provides important insights into the regulation of neuroblast lifespan and proliferation in the Drosophila mushroom body, identifying Krüppel (Kr) as a key transcription factor promoting timely termination of these neuroblasts by regulating Imp/Syp transition and E93 expression. This study proposes that Kr acts antagonistic to Krüppel homolog 1 (Kr-h1), whose overexpression leads to prolonged mushroom body neuroblast proliferation and tumor-like expansion. The findings are impactful for researchers interested in temporal patterning and neural development. The methods and data analysis are solid.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors investigated factors required for neural progenitors to exit cell cycle before the adult stage. They first show that Kr is expressed in pupal stage MBNBs, and depletion of Kr from pupal stage NBs leads to retention of MBNBs into the adult stage. Then they demonstrate that these retained NBs maintain the expression of Imp, and co-depletion of Imp abolishes the extended neurogenesis. Further, they show that co-depletion of kr-h1 significantly reduces the retained MBNBs caused by loss of kr, suggesting antagonistic genetic interactions between these two. In addition, they demonstrate that over-expressing Kr-h1 leads to the striking phenotype of tumor-like neuroblast overgrowth in adult brains. In the revised manuscript, they provide evidence suggesting that Kr does not regulate Kr-h1 expression, but rather Kr and Kr-h1 may regulate the late temporal gene E93 expression in parallel.

Strengths:

(1) The authors leveraged well-controlled powerful genetic tools (including temporal control of RNAi knock down using the Gal80ts system), and provided strong evidence that Kr is required for the Imp to Syp transition and to promote the end of neurogenesis through E93 in mushroom body neuroblasts. Similarly, the experimental result of co-depleting Kr-h1 and Kr, and the striking phenotype upon Kr-h1 mis-expression, support the antagonistic roles played by Kr-h1 and Kr in this process.

(2) The sample sizes, quantification methods and p-values are well documented for all experiments. In most parts, the data presented strongly support their conclusions.

(3) Identification of two transcription factors with opposite roles in controlling cell cycle exit, and their possible interactions with the Imp/Syp axis, is highly significant for the study on how the proliferation of neural progenitors is regulated and limited before the adult stage.

Weaknesses:

(1) In the revised manuscript, Kr immunostaining was done in KrIf-1 mutant brains using tyramide signal amplification (TSA) to enhance the weak endogenous Kr signal, and they conclude that Kr is ectopically detected in MBNBs and their progeny. However, a wildtype control with TSA amplified Kr immunostaining was not provided, so it is not known whether the elevated signal comes from TSA amplification or the mutant condition. If Kr is indeed mis-expressed in MBNBs in the KrIf-1 mutant, the authors should provide a hypothesis to explain why both loss of Kr and mis-expression of Kr in MBNBs lead to the same NB retention phenotype.

Reviewer #2 (Public review):

In this paper, the authors study the role of Krüppel in regulating the termination and survival of mushroom body neuroblasts. They first confirm that adult wild-type brains have no proliferation and report that Kr mutants and Kr RNAi specifically in neuroblasts prolong MBNB lifespan, enabling continued neurogenesis in the adult brain. They further show that Kr acts during pupal stages to regulate the elimination to the mushroom body neuroblasts, as its depletion leads to neuroblast retention, revealing a previously unrecognised postembryonic function of Kr distinct from its established role in embryonic neurogenesis. Mechanistically, this is achieved by the regulation of the Imp/Syp transition and E93 expression. Finally, they show that Kr acts antagonistically to Kr-h1, which is expressed predominantly in larval stages. Together, these results identify Kr as a mushroom body neuroblast regulator coordinating intrinsic and extrinsic signal to regulate neuroblast termination.

Strengths:

The main strength of this paper is that it identified a novel regulator of Imp expression in the mushroom body neuroblasts. Imp is a conserved RNA binding protein that has been shown to regulate neural stem cell proliferation and survival in different animals.

Moreover, the authors provide a series of evidence that this regulator, Kruppel, acts by integrating extrinsic signals (ecdysone) with intrinsic timers (Imp-Syp transition) to regulate neuroblast termination.

Weaknesses:

No significant weaknesses were identified.

Reviewer #3 (Public review):

Summary:

Drosophila neuroblasts (NBs) serve as a well-established model for studying neural stem cell biology. The intrinsic genetic programs that control their mitotic potential throughout development have been described in remarkable detail, highlighting a series of sequentially expressed transcription factors and RNA-binding proteins that together constitute the temporal patterning system.

However, the mechanisms that limit the number of NB divisions remain largely unknown in a specific subset of NBs known as mushroom body neuroblasts (MB NBs). Unlike other NBs, which terminate proliferation before or shortly after the onset of metamorphosis, MB NBs continue dividing until the end of metamorphosis, ceasing only just before adulthood.<br /> In this study, the authors identify the transcription factor Krüppel (Kr), a member of the conserved Krüppel-like family, as temporally regulated in MB NBs. They demonstrate that Kr knockdown during pupal stages maintains expression of the RNA-binding protein Imp and results in prolonged MB NB proliferation into adulthood. Their data suggest that Kr contributes to the timely silencing of Imp during metamorphosis. The authors further identify Kr-h1, a related transcription factor, as a potential antagonist. While Kr-h1 appears dispensable for the timely termination of MB NBs under normal conditions, its overexpression leads to their continued proliferation and tumor-like expansion in adults.

This work provides the first evidence for a transcription factor-driven temporal regulation mechanism in MB NBs, offering new insight into the control of neural stem cell self-renewal. Given the evolutionary conservation of Krüppel-like factors, this study may have broader implications for the neural stem cell field.

Strengths:

(1)The study possibly identifies a new series of temporal transcription factors that are specific for mushroom body neuroblasts.

(2) The mechanism could be conserved in vertebrates.

Comment on revised version.

The authors have clarified the expression status of Kr in the KrIf-1 mutant, as well as the regulatory interactions among Kr, Kr-h1, and E93. My other concerns have also been satisfactorily addressed. I congratulate the authors on this excellent work and on discovering a novel mechanism that regulates temporal progression and the termination of division in mushroom body neuroblasts.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors investigated factors required for neural progenitors to exit the cell cycle before the adult stage. They first show that Kr is turned on in pupal stage MBNBs, and depletion of Kr from pupal stage NBs leads to retention of MBNBs into the adult stage. Then they demonstrate that these retained NBs maintain the expression of Imp, and co-depletion of Imp abolishes the extended neurogenesis. Further, they show that co-depletion of kr-h1 significantly reduces the retained MBNBs caused by loss of kr, suggesting antagonistic genetic interactions between these two. In addition, they demonstrate that over-expressing Kr-h1 leads to the striking phenotype of tumor-like neuroblast overgrowth in adult brains.

Strengths:

(1) The authors leveraged well-controlled, powerful genetic tools (including temporal control of RNAi knockdown using the Gal80ts system), and provided strong evidence that Kr expression in pupal stage MBNBs is required to repress Imp and promote the end of neurogenesis. Similarly, the experimental result of co-depleting Kr-h1 and Kr, and the striking phenotype upon Kr-h1 mis-expression, support the antagonistic roles played by Kr-h1 and Kr in this process.

(2) The sample sizes, quantification methods, and p-values are well documented for all experiments. In most parts, the data presented strongly support their conclusions.

(3) Identification of two transcription factors with opposite roles in controlling cell cycle exit, and their possible interactions with the Imp/Syp axis, is highly significant for the study on how the proliferation of neural progenitors is regulated and limited before the adult stage.

We thank Reviewer #1 for their thoughtful and constructive assessment of our manuscript. We are grateful that the reviewer recognised the strength of our genetic approaches, the significance of identifying Kr and Kr-h1 as opposing regulators of MBNB termination, and the value of linking these factors to the Imp/Syp axis. We have revised the manuscript substantially in response to the reviewer’s comments. In particular, we have further characterised Kr expression in the KrIf-1 mutant background, examined the relationship between Kr, Kr-h1 and E93, analysed Kr-h1 expression in MBNBs using a Kr-h1::GFP BAC reporter, revised the proposed model, improved figure presentation and corrected typographical errors throughout the manuscript.

Weaknesses:

(1) The nature of the KrIf-1 allele is not clear. It is mentioned that this allele leads to misexpression of Kr in various tissues. However, it is not clear if Kr is mis-expressed or lost in MBNBs in the KrIf-1 mutant. If Kr is mis-expressed in MBNBs in the KrIf-1 mutant, then it would be difficult to explain why both loss of Kr and mis-expression of Kr in MBNBs lead to the same NB retention phenotype. The authors should examine Kr expression in MBNBs in the KrIf-1 mutant.

We agree that clarifying the nature of Kr expression in the KrIf-1 mutant background is important. We have therefore performed additional Kr immunostaining in KrIf-1 mutant brains using tyramide signal amplification (TSA) to enhance the weak endogenous Kr signal. These new data show that Kr is ectopically detected in MBNBs and their progeny in KrIf-1 mutant late pupal and adult brains (Fig. S3G, H), and quantification of TSA-enhanced Kr signals further supports Kr misexpression in MBNBs during late pupal stages (Fig. S3I). We have added these data to the revised manuscript. These results indicate that the KrIf-1 phenotype is associated with aberrant Kr expression in MBNBs rather than a simple loss of Kr expression. We agree with the reviewer that it may appear counterintuitive that both Kr depletion and Kr misexpression can lead to MBNB retention. We now discuss this point more explicitly. Our interpretation is that MBNB termination requires tight control of Kr activity during a narrow developmental window. Loss of Kr prevents the normal progression of the Imp-to-Syp transition and E93 activation, whereas ectopic or mistimed Kr expression in KrIf-1 mutants may also interfere with the same termination programme. Thus, both reduced Kr activity and inappropriate Kr expression can disrupt the precisely regulated Kr-dependent transition required for timely MBNB cell-cycle exit and elimination.

We have revised the Results and Discussion to make this interpretation clearer and to avoid describing KrIf-1 simply as equivalent to Kr loss of function.

(2) Some parts of the regulations and interactions between Kr, Kr-h1, Imp, Syp, and E93 are not well-defined. For example, the data suggest that Kr is turned on in the pupal stage MBNBs, and is required to end neurogenesis through repressing Imp and Kr-h1. To further support this conclusion, the authors can examine if Kr-h1 expression is up-regulated in kr-RNAi.

The authors suggested that Kr-h1 may act upstream or in parallel to Imp/Syp, but also suggested that Kr-h1 may repress E93. The expression of Imp, Syp, and E93 can be examined in brains with Kr-h1 mis-expression to determine where Kr-h1 acts. If Imp expression is elevated when Kr-h1 is mis-expressed, then Kr-h1 may act upstream of Imp. If Imp/Syp expression does not change, then Kr-h1 may act on the E93 level.

We thank the reviewer for this helpful suggestion. We agree that the regulatory relationships between Kr, Kr-h1, Imp/Syp and E93 were not sufficiently defined in the original manuscript. In the revised manuscript, we have therefore clarified which relationships are supported by our data and which remain unresolved.

During revision, we placed particular emphasis on the relationship between Kr, Kr-h1 and E93, because our genetic interaction data showed that co-depletion of Kr-h1 partially suppresses MBNB retention caused by Kr depletion (Fig. 5A). This indicated that Kr and Kr-h1 functionally oppose each other during MBNB termination. We therefore asked whether this functional antagonism could be explained by a simple linear pathway in which Kr promotes termination by suppressing Kr-h1, which in turn antagonises E93.

We first tested whether Kr-h1 regulates E93 in the MBNB lineage. Kr-h1 depletion increased E93 expression in the MBNB lineage, whereas Kr-h1 overexpression strongly reduced E93 expression (Fig. S5B). These data support the conclusion that Kr-h1 antagonises E93 expression in this lineage, consistent with the established antagonistic relationship between Kr-h1 and E93 in other developmental contexts.

We next examined whether Kr regulates this Kr-h1–E93 axis by suppressing Kr-h1 expression. To address this, we used a functional Kr-h1::GFP BAC reporter. Kr-h1::GFP was readily detected in larval MBNBs but was strongly downregulated during pupal development, consistent with the MBNB-lineage-specific RNA-seq dataset of Liu et al. (2015). However, Kr depletion did not significantly increase Kr-h1::GFP levels in late pupal MBNBs (Fig. 5B and Fig. S5C). Moreover, despite the absence of detectable Kr-h1::GFP upregulation, Kr depletion strongly reduced E93 expression in the progeny region of the MBNB lineage, while the weak E93 signal detectable in MBNBs themselves was not substantially altered (Fig. 5B).

These results argue against a simple linear pathway in which Kr promotes MBNB termination by directly repressing Kr-h1 expression. Instead, they suggest that Kr supports E93 expression within the MBNB lineage through a mechanism that does not require detectable upregulation of Kr-h1. Thus, Kr and Kr-h1 functionally oppose each other during MBNB termination, but they are unlikely to act through a simple linear Kr–Kr-h1–E93 pathway. We have revised the model accordingly, proposing that Kr and Kr-h1 act through convergent or parallel mechanisms to regulate the MBNB termination programme.

Regarding the Imp/Syp axis, the original manuscript had already shown that Kr depletion causes persistent Imp expression in adult MBNB lineages and that co-depletion of Imp suppresses MBNB retention caused by Kr depletion. These data supported the conclusion that persistent Imp expression is required for MBNB retention following Kr depletion. In the revised manuscript, we strengthened this conclusion by analysing Imp and Syp expression during late pupal development, when MBNBs normally undergo cell-cycle exit and elimination. We found that Kr-depleted MBNBs maintain higher Imp expression and show reduced Syp expression compared with controls (Fig. 4A, B), supporting the idea that Kr promotes MBNB termination by facilitating the normal Imp-to-Syp transition.

We also considered whether Kr-h1 acts upstream of the Imp/Syp transition. Kr-h1 overexpression caused persistent Imp expression in proliferating adult NBs (Fig. 5E). However, this manipulation produced a severe tumour-like overgrowth phenotype and likely represents a strongly non-physiological state. We therefore do not conclude that Kr-h1 normally acts upstream of Imp/Syp during MBNB termination. Rather, our revised interpretation is that Kr promotes MBNB termination through the Imp-to-Syp transition and by supporting E93 expression, whereas Kr-h1 counteracts termination at least in part by repressing E93. How the Imp/Syp and E93-associated pathways converge during MBNB termination remains an important question for future work.

We have revised the Results, Discussion and Fig. 6D model accordingly, distinguishing experimentally supported relationships from more speculative connections.

Reviewer #2 (Public review):

Summary:

In this paper, the authors study the role of Kruppel in regulating the survival of mushroom body neuroblasts. They first confirm that adult wild-type brains have no proliferation and report that Kruppel mutants and Kruppel RNAi in neuroblasts show a few proliferative clones; they show that these proliferative clones are localized in the mushroom body. They then show that Kruppel is expressed mostly during pupal stages and acts by downregulating the expression of Imp, which has been shown to positively regulate neuroblast proliferation and survival. Expectedly, this also affects neuronal diversity in the mushroom body, which is enriched in gamma neurons that are born during the Imp-expression window. Finally, they show that Kr acts antagonistically to Kr-h1, which is expressed predominantly in larval stages.

Strengths:

The main strength of this paper is that it identified a novel regulator of Imp expression in the mushroom body neuroblasts. Imp is a conserved RNA-binding protein that has been shown to regulate neural stem cell proliferation and survival in different animals.

We thank Reviewer #2 for their critical assessment of our manuscript and for the specific suggestions regarding manuscript framing, figure clarity, public dataset analysis and textual accuracy. We have revised the manuscript extensively in response to these comments. In particular, we have clarified that our study does not aim to describe physiological adult neurogenesis in Drosophila, but rather investigates how normally terminating neural progenitors can retain or regain neurogenic potential when the developmental termination programme is disrupted. We have also revised the text to avoid overstatement about functional integration of adult-born neurons, improved figure presentation, removed the incomplete targeted-screen framing, added analysis of public MBNB-lineage transcriptomic data, and corrected multiple textual and citation issues.

Weaknesses:

(1) The main weakness of the paper is that the authors want to test adult neurogenesis in a system where no adult neurogenesis exists. To achieve this, they force neuroblasts to survive in adulthood by altering the genetic program that prevents them from terminating their proliferation. If this was reminiscing about "adult neurogenesis", the authors should at least show how adult neurons incorporate into the mushroom body even if they are born much later. On the contrary, this more likely resembles a tumorigenic phenotype, when stem cells divide way past their appropriate timing.

We appreciate this important point and agree that Drosophila does not normally show substantial physiological neurogenesis in the adult central brain under standard conditions. We have therefore revised the manuscript to clarify the framing of our study. Our aim is not to claim that Kr depletion reveals a normal physiological adult neurogenesis programme, but rather to identify developmental mechanisms that normally terminate MBNB proliferation and restrict latent neurogenic potential in the adult brain.

We note, however, that the original manuscript already provided evidence that the persistent proliferative cells induced by Kr depletion or the KrIf-1 mutation are associated with the MB lineage and generate neuronal progeny in young adult brains. EdU-positive clones were detected predominantly in the dorsoposterior MB cell body region (Fig. 2A, B). These clones generally contained a single Mira- and insc>GFP-positive NB-like cell, including mitotic cells with cortical Mira localisation (Fig. 2C, D), together with surrounding Elav-positive neuronal progeny (Fig. 2E). In addition, persistent mitotic cells in KrIf-1 mutant brains were found in the MB cell body region marked by mb247>GFP and OK107>GFP, and showed Mira localisation consistent with dividing MBNBs (Fig. 2F-H). Thus, although we have not directly demonstrated mature circuit integration, the original data support the conclusion that Kr depletion and the KrIf-1 mutation allow MBNBs to persist beyond their normal termination window and generate neuronal progeny within the MB region.

At the same time, our data do not establish the precise neuronal identity, connectivity or functional incorporation of the newly generated progeny into mature MB circuits, nor do they determine the long-term behaviour of these progeny in older adult brains. We have therefore revised the text and Discussion to avoid overinterpreting these cells as fully integrated adult-born MB neurons, and now state that these issues remain important questions for future work.

We also agree that prolonged progenitor proliferation can become pathological in some contexts. However, we do not think that the Kr-depletion and KrIf-1 phenotypes are equivalent to tumour-like overgrowth, at least under the conditions analysed here. In young adult brains, retained MBNBs remained spatially restricted to the MB cell body region, and each EdU-positive clone generally contained only a single NB-like cell with asymmetric Mira localisation, surrounded by Elav-positive neuronal progeny (Fig. 2C-E, G, H). This pattern is more consistent with persistent asymmetric MBNB divisions than with tumour-like expansion. This contrasts with Kr-h1 overexpression, which caused extensive tumour-like NB overproliferation with impaired neuronal differentiation; we now describe this latter phenotype as tumour-like NB overgrowth (Fig. 5C-E). We have revised the manuscript to distinguish these phenotypes more clearly.

(2) Moreover, the figures are, in many cases, hard to understand, and the interpretation of the figures doesn't always match what one sees. The manuscript would benefit from better figures; for example, in Figure 2C, Miranda expression in insc>GFP in Kr-IF-1 is not visible.

We thank the reviewer for pointing out the need to improve figure clarity. We have revised the figure presentation throughout the manuscript to improve readability, including increasing label size, improving panel labelling and ensuring that the interpretation in the Results is consistent with the corresponding figure panels and legends.

Regarding the specific concern about Fig. 2C, we agree that the Mira signal was not sufficiently clear in the merged image. We have therefore added a Mira-only single-channel panel to Fig. 2C to allow the relevant signal to be evaluated more directly. We have also revised the text to clarify that retained MBNBs were identified based on combined positional, morphological and marker criteria, rather than by Mira signal alone.

(3) The authors describe a targeted genetic screen, but they don't describe which genes were tested, how they were chosen, and why Kruppel was finally selected.

We agree that the original description of a targeted genetic screen was insufficient. Because the screen was preliminary and incomplete, we concluded that presenting partial screening information would not be sufficiently informative and could overstate the scope of the present study. We have therefore removed the screen-based framing from the revised manuscript. Instead, the revised manuscript presents Kr as a candidate selected for focused functional analysis based on its known role in neuroblast temporal regulation and the strong MBNB retention phenotype observed upon Kr depletion and in the KrIf-1 mutant background.

(4) The authors argue that Kr does not behave as a typical tTF in MBNBs. However, they show no expression in the embryo, limited expression in the larva and early pupa, and a peak around P24-P48. This sounds like a temporally regulated expression of a transcription factor. Importantly, they mentioned that they tested their observations against different datasets (FlyAtlas2, modENCODE, and MBNB-lineage-specific RNA-seq data), but they don't provide the data.

We thank the reviewer for this helpful comment. We agree that our original wording could have been clearer. Our intention was not to argue that Kr cannot have a temporally restricted function in MBNBs, but rather that Kr does not behave like a canonical temporal transcription factor whose expression undergoes a strong stage-specific switch in this lineage.

We have revised both the text and the corresponding quantification. In the original version, Kr signal levels in pupal MBNBs appeared to vary modestly across pupal stages. However, after reanalysing cytoplasmic and nuclear Kr signals separately using Welch’s ANOVA followed by Dunnett T3 multiple-comparison correction, no pairwise comparisons reached statistical significance (Fig. 3E, F). Thus, the revised quantification does not support a significant temporal change in Kr protein levels during the pupal stages analysed, and we have avoided describing Kr as showing a clear pupal expression peak.

As requested, we have also included the public MBNB-lineage RNA-seq analysis in the revised manuscript as Fig. S5A. This analysis shows that Kr transcript levels remain low across the analysed developmental stages, in contrast to the stronger temporal changes observed for other regulators, including larval Kr-h1 expression followed by pupal downregulation, reciprocal induction of E93, and marked increases in Syp expression. Because FlyAtlas2 and modENCODE have limited spatial resolution for MBNB-specific expression, we now focus this comparison on the MBNB-lineage-specific RNA-seq dataset.

We have therefore revised the manuscript to describe Kr as a postembryonic regulator required for pupal MBNB termination, rather than as a conventional temporally induced tTF in this lineage. In our revised interpretation, Kr expression is low and not detectably strongly temporally induced in MBNBs, whereas Kr function is temporally required during pupal MBNB termination, as supported by the Gal80ts knockdown experiments.

(5) Finally, the contribution of Kr to the neuronal composition of the mushroom body is expected (since Imp is known to regulate neuronal diversity in the MB), but the presentation in the paper is very incomplete.

We agree that, given the known role of Imp/Syp in MB neuronal temporal identity, altered MB neuronal composition is a plausible consequence of disrupted Kr function. However, we also agree that our study does not directly determine the precise neuronal identities, connectivity or functional properties of the progeny produced by persistent MBNBs. We have therefore revised the manuscript to present this aspect more cautiously.

In the original manuscript, we had shown that Kr depletion and the KrIf-1 mutation affect MB morphology. In the revised manuscript, we have clarified the presentation of these data and added new analysis of the severe MB defects caused by Kr-h1 overexpression (Fig. 6C). We now describe these phenotypes as changes in MB morphology and lineage progression, rather than as direct evidence for altered neuronal composition.

In the Discussion, we state that persistent Imp expression in Kr-depleted MBNBs could bias neuronal progeny toward earlier identities or delay their transition to later identities, but we explicitly note that neuronal identity and connectivity were not directly analysed. We also state that future studies will be required to determine whether prolonged MB neurogenesis alters MB circuit function, learning, plasticity or ageing. Thus, we have revised the manuscript to avoid overstating the contribution of Kr to MB neuronal composition.

Unfortunately, based on the above, I am not convinced that the authors can use this framework to infer anything about adult neurogenesis. Therefore, the impact of this work is limited to the role of Kruppel in regulating Imp, which has already been shown to regulate the extent of neuroblast division, as well as the neuronal types that are born at different temporal windows.

We understand the reviewer’s concern and have revised the manuscript to avoid implying that our data establish physiological adult neurogenesis in Drosophila. Instead, we now frame the study as identifying mechanisms that normally terminate MBNB proliferation and restrict latent neurogenic potential in the adult brain.

We respectfully note, however, that the impact of this study is not limited to showing that Kr regulates Imp. First, we identify Kr as a postembryonic regulator required for timely MBNB termination during pupal development. Second, we show that both Kr depletion and the KrIf-1 mutation allow MBNBs to persist beyond their normal termination window and generate neuronal progeny in the adult MB region. Third, we show that Kr promotes not only the Imp-to-Syp transition but also proper E93 expression within the MBNB lineage. Finally, we identify Kr-h1 as a functionally opposing KLF-family factor that represses E93 and can drive tumour-like NB overgrowth when misexpressed. We have revised the manuscript to present these conclusions more clearly and cautiously.

Reviewer #3 (Public review):

Summary:

Drosophila neuroblasts (NBs) serve as a well-established model for studying neural stem cell biology. The intrinsic genetic programs that control their mitotic potential throughout development have been described in remarkable detail, highlighting a series of sequentially expressed transcription factors and RNA-binding proteins that together constitute the temporal patterning system.

However, the mechanisms that limit the number of NB divisions remain largely unknown in a specific subset of NBs known as mushroom body neuroblasts (MB NBs). Unlike other NBs, which terminate proliferation before or shortly after the onset of metamorphosis, MB NBs continue dividing until the end of metamorphosis, ceasing only just before adulthood.

In this study, the authors identify the transcription factor Krüppel (Kr), a member of the conserved Krüppel-like family, as temporally regulated in MB NBs. They demonstrate that Kr knockdown during pupal stages maintains expression of the RNA-binding protein Imp and results in prolonged MB NB proliferation into adulthood. Their data suggest that Kr contributes to the timely silencing of Imp during metamorphosis. The authors further identify Kr-h1, a related transcription factor, as a potential antagonist. While Kr-h1 appears dispensable for the timely termination of MBNBs under normal conditions, its overexpression leads to their continued proliferation and tumor-like expansion in adults.

This work provides the first evidence for a transcription factor-driven temporal regulation mechanism in MB NBs, offering new insight into the control of neural stem cell self-renewal. Given the evolutionary conservation of Krüppel-like factors, this study may have broader implications for the neural stem cell field.

Strengths:

(1) The study possibly identifies a new series of temporal transcription factors that are specific for mushroom body neuroblasts.

(2) The mechanism could be conserved in vertebrates.

We thank Reviewer #3 for their positive and constructive assessment of our study. We are grateful that the reviewer recognised the significance of identifying Kr as a regulator of mushroom body neuroblast termination, and the potential broader relevance of KLF-family transcription factors to neural stem cell regulation.

In response to the reviewer’s comments, we have substantially revised the manuscript. In particular, we have added new data on Kr expression in the KrIf-1 mutant background, Kr-h1 expression in MBNBs, and the regulation of E93 by Kr and Kr-h1. We have also incorporated public MBNB-lineage transcriptomic data to place Kr, Kr-h1, E93, Imp and Syp within the known temporal progression of the MB lineage. Finally, we have revised the proposed model to distinguish experimentally supported interactions from open mechanistic questions.

Weaknesses:

Some proposed regulatory interactions, particularly between Kr, Kr-h1, and other temporal factors like Imp, Chinmo, and E93, have not been thoroughly investigated, which weakens the support for the proposed model. Additional experimental validation is needed to confirm these relationships and strengthen the mechanistic framework.

We agree with the reviewer that some regulatory relationships in the original model required further experimental support. In response, we have added new data and revised the model substantially to distinguish experimentally supported interactions from unresolved mechanistic links.

In the revised manuscript, we provide additional analysis of the Imp/Syp axis after Kr depletion, direct evidence for Kr-h1 expression in MBNBs, and new data showing that Kr-h1 antagonises E93 expression in the MBNB lineage. We also found that Kr depletion reduces E93 expression in the progeny region of the MBNB lineage without significantly increasing Kr-h1::GFP levels in MBNBs, arguing against a simple linear pathway in which Kr promotes termination by directly repressing Kr-h1. Together, these results support a revised model in which Kr promotes MBNB termination by facilitating the Imp-to-Syp transition and supporting E93 expression, whereas Kr-h1 functionally opposes termination at least in part through E93 repression.

Recommendations for the authors:

Reviewing Editor Comments:

The majority of the reviewers agreed that a few major important points should be addressed, in particular:

(1) Better characterization of the nature of the KrIf-1 allele.

(2) Better define the regulations and interactions between Kr, Kr-h1, Imp, Syp, chinmo, and E93.

(3) More information about the genetic screen performed.

(4) The timings of expression of Kr in pupal MBNBs and of KrIf-1.

The reviewers also found that a general proofreading of the manuscript would greatly benefit its readability and comprehension and suggested several small corrections and more detailed explanations.

We thank the Reviewing Editor and Senior Editor for their careful assessment of our manuscript and for summarising the major points that required revision. We have addressed these points as follows.

(1) Better characterisation of the nature of the KrIf-1 allele

We agree that clarifying the nature of the KrIf-1 allele was important. We have now examined Kr expression in KrIf-1 mutant brains using TSA-enhanced Kr immunostaining. These new data show ectopic Kr signal in MBNBs and their progeny in KrIf-1 mutant late pupal and adult brains (Fig. S3G–I), supporting the conclusion that the KrIf-1 phenotype is associated with Kr misexpression rather than simple loss of Kr expression. We have revised the Results and Discussion to explain that MBNB termination requires precise control of Kr activity, and that both Kr depletion and inappropriate Kr expression can disrupt this termination programme.

(2) Better definition of the regulatory relationships between Kr, Kr-h1, Imp, Syp, Chinmo and E93

We have strengthened this part of the manuscript by combining the genetic evidence already present in the original manuscript with new expression analyses of temporal and hormone-responsive regulators. The original manuscript already showed that co-depletion of Imp suppresses MBNB retention caused by Kr depletion, supporting Imp as a key downstream effector of Kr. In the revised manuscript, we further show that Kr depletion causes persistent Imp expression and reduced Syp expression in late pupal MBNBs (Fig. 4), supporting the conclusion that Kr promotes MBNB termination by facilitating the Imp-to-Syp transition.

We have also added new data on Kr-h1 and E93. Kr-h1 depletion increases E93 expression in the MBNB lineage, whereas Kr-h1 overexpression reduces E93 expression (Fig. S5B), supporting an antagonistic relationship between Kr-h1 and E93 in this lineage. In addition, Kr depletion reduces E93 expression in the surrounding progeny of the MBNB lineage without detectably increasing Kr-h1::GFP levels in late pupal MBNBs (Fig. 5B). These data argue against a simple linear Kr-Kr-h1-E93 pathway and instead support a model in which Kr and Kr-h1 function through convergent or parallel mechanisms to regulate MBNB termination.

Regarding Chinmo, we agree that it is an important temporal factor. However, Chinmo is best characterised in this context as an early temporal fate regulator acting downstream of the Imp/Syp programme in MB lineages, where Imp and Syp regulate Chinmo translation post-transcriptionally (Liu et al., 2015). Because our study focuses primarily on late pupal MBNB termination, and because we were unable to obtain reliable Chinmo antibodies or reporter lines within the timeframe of this revision, we did not directly analyse Chinmo expression. We have therefore removed Chinmo from the main model and revised the Discussion to focus on the experimentally supported Imp/Syp and Kr-h1/E93 axes.

(3) More information about the genetic screen

We agree that the original screen-based description was not sufficiently informative. Because the targeted screen was preliminary and incomplete, we have removed the screen-based framing from the revised manuscript. Instead, we now present Kr as a candidate selected for focused functional analysis based on its known role in neuroblast temporal regulation and the strong MBNB retention phenotype observed upon Kr depletion and in the KrIf-1 mutant background.

(4) Timing of Kr expression in pupal MBNBs and in KrIf-1

We have clarified the timing of Kr expression in MBNBs. In wild-type brains, weak Kr signals were detected in MBNBs during pupal development using two Kr antibodies and a Kr::GFP BAC reporter, and these signals were reduced by Kr RNAi (Fig. 3E, F and Fig. S3F). We also analysed MBNB-lineage RNA-seq data, which show relatively low but persistent Kr transcript levels during postembryonic development (Fig. S5A). In the KrIf-1 background, TSA-enhanced Kr staining revealed ectopic Kr expression in MBNBs and their progeny during late pupal and adult stages (Fig. S3G–I). We have revised the manuscript to describe these expression patterns more clearly and to avoid overinterpreting weak embryonic or larval Kr signals.

We have also proofread the manuscript, corrected typographical errors, standardised figure references and nomenclature, improved figure legends and revised several figures for clarity.

Reviewer #1 (Recommendations for the authors):

(1) The authors identified Kr from a targeted genetic screen. Information about how many factors and what factors they have screened will also be very helpful to readers.

We thank the reviewer for this suggestion. In the original manuscript, we briefly referred to a targeted genetic screen that led us to focus on Kr. However, because this screen was preliminary and incomplete, we agree that including partial screening information would not be sufficiently informative and might overstate the scope of the present study. We have therefore revised the manuscript to remove the screen-based framing and instead present Kr as a candidate selected for focused functional analysis based on its known role in neuroblast temporal regulation and the strong MBNB retention phenotype observed upon Kr depletion and in the KrIf-1 mutant background.

(2) In Figure 2C wild type brains, what are the Mira+ cells and insc>GFP+ cells? There seems to be one cell that expresses both. Could it be a dormant NB?

We thank the reviewer for pointing this out. We agree that a small number of weakly Mira-positive and insc>GFP-positive cells can occasionally be observed in adult control brains, as well as in KrIf-1 mutant brains. These cells were few in number, were generally located outside the stereotyped MBNB region, and showed much weaker marker signals than the retained MBNBs observed after Kr depletion or in KrIf-1 mutants. Because they did not appear to express other NB markers examined in this study, such as wor>GFP, we did not investigate them further. Their identity therefore remains unclear, and we cannot exclude the possibility that they represent rare dormant or NB-like cells in the adult brain.

We have revised the text and figure legend to clarify that the retained MBNBs analysed in this study were identified based on their stereotyped MB-region position and strong NB-marker expression.

(3) Kr is normally expressed in stage 10 embryonic NBs. Have stage 10 embryos been examined to make sure that there is no Kr expression in MBNBs?

We thank the reviewer for this important point. We agree that Kr expression in early embryonic neuroblasts is well established. Early embryonic MBNBs can in principle be identified using a detailed positional and combinatorial marker map, as shown by Kunz et al. (2012), who traced individual MBNBs from late embryonic stages back to stage 9 using combinations of Dac, Ey, Svp-lacZ and Rx, together with morphological and positional criteria. However, reliable identification of MBNBs at such early stages is technically challenging in our assay, because our analysis depended on simultaneous detection of OK107>GFP, Mira and Kr, and OK107>GFP/Mira-based identification of the MB lineage was more robust at later embryonic stages. We therefore focused our embryonic Kr analysis on stages at which MBNBs could be confidently identified by their position and marker expression.

In these embryos, Kr was broadly detected in surrounding embryonic CNS cells, including thoracic NBs, but was not robustly detected in OK107>GFP- and Mira-positive MBNBs (Fig. S3A, B). We cannot fully exclude the possibility that MBNBs transiently express very low levels of Kr at earlier embryonic stages before they can be reliably identified in our assay. However, our temporally controlled Gal80ts experiments show that Kr depletion during the pupal stage, but not during earlier embryonic or larval stages, is sufficient to cause MBNB retention in adult brains (Fig. 3C, D). Thus, any transient embryonic Kr expression, if present, is unlikely to be the main cause of the adult MBNB retention phenotype described here.

We have revised the text to avoid overinterpreting the absence of embryonic Kr expression and to emphasise that the critical requirement for Kr in this study occurs during pupal MBNB termination.

(4) In Figure S3C, Kr expression seems to be cytoplasmic. Also in S3D, the expression of KrGFP in NBs is not obvious. Overall, Kr expression in pupal MBNBs is much more convincing than the larval expression.

We agree with the reviewer. Kr expression in larval MBNBs is weak and less convincing than the pupal signal. We have therefore revised the manuscript to describe larval Kr expression more cautiously. In the revised text, we state that Kr was weakly detected in larval MBNBs by antibody staining and that the Kr::GFP BAC reporter showed stronger signals in cells adjacent to MBNBs, likely corresponding to GMCs or immature neurons that may have inherited Kr::GFP from MBNBs.

We now base our main conclusion primarily on the pupal-stage data. At this stage, weak Kr signals were detected in MBNBs using two independent Kr antibodies and the Kr::GFP BAC reporter, and Kr depletion reduced the antibody signal (Fig. 3E, F and Fig. S3F). Importantly, this expression pattern is consistent with our functional data showing that pupal-stage-specific Kr depletion is sufficient to induce MBNB retention in adult brains, whereas earlier embryonic or larval depletion did not produce the same phenotype (Fig. 3C, D). Thus, both the expression and temporal knockdown data support a critical role for Kr during pupal MBNB termination.

We also discuss the observation that Kr signals in pupal MBNBs appear partly cytoplasmic, raising the possibility that Kr may not act solely as a canonical nuclear transcription factor in this context, or that its localisation may be dynamically regulated during MBNB termination. Thus, we agree that the pupal expression data provide the strongest support for Kr expression in MBNBs, and we have revised the text accordingly.

(5) A thorough proofreading is needed to correct the typos.

We apologise for the typographical and formatting errors in the original manuscript. We have thoroughly proofread the revised manuscript, corrected typographical errors, standardised figure references and gene/protein nomenclature, and revised multiple sections for clarity and readability. We have also revised the figure legends and improved figure presentation where possible.

Reviewer #2 (Recommendations for the authors):

(1) The authors should proofread for typos; there are quite a few ("survivial", "fount", "mitoic", "persistenc").

We apologise for these typographical errors. We have thoroughly proofread the revised manuscript, corrected typographical errors and formatting problems, and revised multiple sections for clarity and readability.

(2) In line 59, "adult eclosion" is incorrect. MBNBs also cease dividing before adult eclosion.

We thank the reviewer for pointing this out. We have revised the wording to avoid the incorrect phrase “adult eclosion” and now state that MBNBs normally terminate during late pupal development, before adulthood.

(3) In line 70, this progression of transcription factors is seen in the mammalian retina, not the brain.

We thank the reviewer for this correction. We have revised the relevant sentence to more accurately describe temporal patterning in mammalian neural progenitors, including the well-characterised example of retinal progenitor temporal progression and broader examples of temporal competence changes in cortical development.

(4) In lines 73-75, I don't think that any of the cited papers show that Cas triggers cell cycle exit. Ref 11 shows that, in UAS-Cas, NBs persist (as the authors also say in lines 79-81).

We agree that the original wording was too strong and potentially misleading. We have revised this section to state more generally that temporal transcription factors can influence NB proliferation and NB lifespan, rather than claiming that Cas directly triggers cell-cycle exit. We have also adjusted the discussion of Cas and Svp to better reflect the cited literature.

(5) In lines 133-134, it should be Figure 2A, B instead of Figure 3A, B.

We thank the reviewer for identifying this error. We have corrected the figure reference.

(6) Figures 1B and 1C are impossible to read. The x-axis should be reorganized and grouped into positive and negative CCRs to make a better argument. Moreover, the purpose of this figure is unclear. We already knew that neurons are postmitotic and all adult clusters are neurons. IF there were any NBs in the adult, they would be so few that they would be invisible with this resolution.

We thank the reviewer for this comment. We agree that the dot plots are dense, because they summarise the expression of 112 selected cell-cycle regulator (CCR) genes across multiple adult and larval brain cell clusters. In preparing the revised manuscript, we have ensured that the figure legends explain the meaning of colour intensity and dot size, and that the submitted PDF preserves sufficient resolution for the gene and cluster labels to be read upon enlargement.

In the original figures, CCR genes were arranged according to broad functional categories. We have not forced all CCR genes into a simple positive-versus-negative classification, because the function of many CCRs is context-dependent. For example, APC/C components can contribute to either mitotic progression or G1 maintenance depending on co-activator context, and mitotic regulators such as Polo and Aurora kinases regulate multiple aspects of mitosis rather than acting simply as positive cell-cycle drivers. We therefore present the genes according to broad functional categories and discuss representative examples of positive and inhibitory regulators in the Results and figure legends, rather than implying that every CCR can be assigned unambiguously to one of two categories.

Regarding the purpose of these analyses, our aim was not simply to restate that adult neurons are postmitotic, nor to claim that scRNA-seq can definitively exclude extremely rare adult progenitors. Rather, we used published scRNA-seq datasets to compare CCR expression programmes across adult and larval brain cell populations in an unbiased manner. The analysis shows that no adult brain cluster displays a coordinated larval NB-like positive CCR expression programme, whereas such a programme is readily observed in larval NB clusters. We have clarified this point in the text and acknowledge the limitation that very rare or non-canonical progenitor-like cells may not be detected by this approach.

(7) The survival assays are confusing. Do the authors believe that the presence or absence of 2-3 clones in the adult brain of a few cells would lead to such a limited survival?

We thank the reviewer for raising this point. We agree that the survival assay required clearer explanation and should be interpreted cautiously. In this experiment, E2F1-Dp and Cdk2-CycE were expressed using TH-Gal4 to test whether forced activation of positive cell-cycle regulators can drive postmitotic neurons into aberrant cell-cycle re-entry. Although only a small number of pH3-positive cells may be detected at any single time point, this represents only a snapshot of an ongoing process and may underestimate the cumulative number of affected cells over time.

TH-Gal4-positive dopaminergic neurons are relatively limited in number, but they include functionally important neuronal populations involved in motor behaviour, arousal, sleep/wake regulation and ageing-associated behavioural decline. Therefore, broad induction of aberrant cell-cycle re-entry and apoptosis within these neurons could plausibly affect organismal survival. However, we agree that the survival phenotype should not be overinterpreted. We cannot exclude the possibility that TH-Gal4 expression outside dopaminergic neurons, developmental effects of the manipulation, or other indirect consequences contribute to the reduced survival. Moreover, the precise cause of death was not determined in this study. We have therefore revised the manuscript to present the survival assay as supporting evidence that inappropriate activation of positive cell-cycle regulators is deleterious in postmitotic neurons, rather than as a direct mechanistic explanation for organismal lethality.

(8) In Figure 2, how many of the proliferative clones are found in the mushroom body. Is it all of them?

We thank the reviewer for this question. In Fig. 2, EdU-positive proliferative clones were scored based on their stereotyped position in the dorsoposterior MB cell body region. Under the conditions analysed, the scored clones were consistently detected within this MB region, and their number did not exceed four per brain hemisphere, consistent with the expected number of MBNBs (Fig. 2A, B). In addition, the identity of these clones as retained MBNB lineages was supported by NB marker expression, Mira localisation, insc>GFP expression where applicable, and their association with MB lineage markers such as mb247>GFP and OK107>GFP in KrIf-1 mutant brains (Fig. 2C-H). We have clarified this point in the revised text and figure legend.

(9) In Figure 2C, why are there so many Miranda-positive cells?

We thank the reviewer for this question. We agree that several Mira-positive cells can be observed in Fig. 2C, including in control brains. The identity of these additional Mira-positive cells remains unclear. They did not consistently co-express the canonical NB markers examined in this study, such as insc>GFP or wor>GFP, and therefore do not appear to represent canonical proliferative NBs. However, we cannot exclude the possibility that some weak Mira-positive cells represent rare dormant or NB-like cells in the adult brain. We have revised the text and figure legend to clarify this point.

(10) In Figure 3C, the authors argue that Kr has an opposing function in NB regulation during larval stages, however, the Kr mutant (which is in both larval and pupal stages) has the highest number of EdU-positive clones. Moreover, conditions 2 and 9 have a comparable (low) number of EdU positive clones, although condition 2 has Kruppel downregulated in all stages.

We thank the reviewer for this comment. We agree that this part of the temporal knockdown experiment required more careful interpretation, and we have revised the manuscript to avoid overinterpreting small quantitative differences among individual temperature-shift conditions.

First, Fig. 3C does not include a Kr mutant condition. We assume that the reviewer is referring to the constitutive insc>KrIR condition grown at 29°C throughout development (condition 1). This condition does not contain tub-Gal80ts and may therefore produce stronger and more continuous Kr RNAi induction than the Gal80ts-based temporal knockdown conditions. In addition, for practical reasons, flies in all conditions were initially kept at 25°C during egg laying to obtain sufficient embryos before being shifted to the indicated temperature regime, including condition 2. These differences may explain why condition 1 produced the highest number of EdU-positive clones. For this reason, we do not interpret condition 1 as a temporal-control condition and do not use it for direct quantitative comparison with the Gal80ts-based conditions.

Second, regarding the comparison between conditions 2 and 9, we agree that these conditions should not be used to infer a simple relationship between the total duration of Kr knockdown and the number of retained MBNBs. We therefore avoid using these differences to infer an additional larval function of Kr. Instead, we now interpret this temporal knockdown experiment more conservatively: Kr depletion during the pupal period is sufficient to induce MBNB retention in adult brains, whereas depletion restricted to earlier embryonic/larval stages or later adult stages has little or no effect.

Thus, the key conclusion supported by these data is the pupal-stage requirement for Kr in MBNB termination, rather than detailed comparisons among all temperature-shift conditions. We have revised the text accordingly.

Overall, we have revised the manuscript to address the reviewer’s concerns by narrowing the framing of adult neurogenesis, clarifying the distinction between persistent MBNBs and tumour-like overgrowth, improving figure presentation, removing the incomplete screen description, adding public dataset analysis, and correcting textual and citation errors. We believe these revisions make the scope and conclusions of the study more precise.

Reviewer #3 (Recommendations for the authors):

Major Points

(1) Targeted screen: The authors mention performing a targeted genetic screen. Please specify which transcription factors were tested.

We thank the reviewer for this suggestion. In the original manuscript, we briefly referred to a targeted genetic screen. However, this screen was preliminary, incomplete, and included a broader set of candidate regulators rather than a systematically completed transcription-factor collection. We therefore agree that listing a partial set of tested factors would not be sufficiently informative and could overstate the scope of the present study.

We have therefore removed the screen-based framing from the revised manuscript. Instead, the revised manuscript presents Kr as a candidate selected for focused functional analysis based on its established role in neuroblast temporal patterning and the strong MBNB retention phenotype observed upon Kr depletion and in the KrIf-1 mutant background. We also no longer use the preliminary screen as part of the evidence supporting our conclusions.

(2) KrIf-1 allele : The authors report that KrIf-1 mutants retain MB NBs in adults, a phenotype resembling Kr loss of function. They propose that this results from Kr deregulation. However, KrIf-1 is a neomorphic allele known to cause ectopic expression in imaginal discs, raising the possibility that Kr is upregulated, not downregulated, in MB NBs. The authors should present experimental data on Kr expression in MB NBs in the KrIf-1 background to clarify this point.

We agree that clarification of Kr expression in the KrIf-1 background is important. We have therefore performed additional Kr immunostaining in KrIf-1 mutant brains using tyramide signal amplification (TSA) to enhance the weak endogenous Kr signal. These new data show that Kr is ectopically detected in MBNBs and their progeny in KrIf-1 mutant late pupal and adult brains (Fig. S3G, H), and quantification of TSA-enhanced Kr signals further supports Kr misexpression in MBNBs during late pupal stages (Fig. S3I).

These results indicate that KrIf-1 is associated with ectopic or aberrant Kr expression in MBNBs, rather than simple loss or downregulation of Kr expression. We have revised the manuscript to clarify this point and no longer interpret KrIf-1 as a simple Kr loss-of-function condition. Although both Kr depletion and KrIf-1 lead to MBNB retention, our revised interpretation is that MBNB termination requires precise temporal and spatial control of Kr activity. Kr depletion disrupts the normal Imp-to-Syp transition and reduces E93 expression in the MBNB lineage, whereas ectopic or mistimed Kr expression in KrIf-1 mutants may also interfere with the termination programme. Thus, both reduced Kr activity and inappropriate Kr expression can perturb the tightly regulated transition required for timely MBNB cell-cycle exit and elimination.

(3) Line 258 - OK107>GFP subset (Fig. 2G): Please clarify why only a subset of EdU-positive clones co-express OK107>GFP. Is this due to EdU labeling other NB lineages not related to the mushroom body?

We thank the reviewer for raising this point. We do not think that the OK107-negative EdU-positive clones represent unrelated NB lineages. The EdU-positive clones analysed in Fig. 2G were located in the dorsoposterior MB cell body region and were associated with Mira-positive NB-like cells, supporting their identification as persistent MBNB-lineage clones.

The reason that only a subset of EdU-positive clones clearly co-express OK107>GFP is likely that, while OK107-Gal4 strongly labels MB neurons and lineage cells, its activity in MBNBs and very young progeny appears to be weaker or more variable at the stages analysed. Thus, the absence of strong OK107>GFP signal in some EdU-positive cells does not necessarily indicate that these clones belong to non-MB lineages.

We have revised the text and figure legend to clarify this point.

(4) Line 261 - Early adulthood mitotic activity: The statement that NBs retain mitotic activity during early adulthood (citing Technau, 2007; Li and Hidalgo, 2020) is misleading. To my knowledge, this mitotic activity has only been reported in glial cells, not NBs. Please revise accordingly.

We thank the reviewer for pointing this out. We agree that the original wording was misleading, because it could be read as implying that normal NBs retain mitotic activity during early adulthood. We have revised the text accordingly. The revised manuscript now refers more cautiously to the previously described early-adult period during which rare residual cell-cycle or proliferative activity has been reported in the adult Drosophila brain, without attributing this activity to normal persistent NBs.

(5) Line 313 - Public dataset analysis: The manuscript mentions analysis of publicly available data, but no results are presented. Please include these findings.

We agree and have now included the public dataset analysis in the revised manuscript. We analysed a published MBNB-lineage-specific RNA-seq dataset and present the expression profiles of selected temporal regulators in Fig. S5A.

This analysis shows that Imp and chinmo transcripts are high during larval stages and decrease during pupal development, whereas Syp is strongly upregulated during the same period. Kr transcript levels remain relatively low throughout the analysed larval and pupal stages and do not show strong temporal induction. In contrast, Kr-h1 is highly expressed during larval stages and sharply downregulated after the larval-to-pupal transition, whereas E93 is strongly induced during pupal development.

These expression profiles support the idea that MBNBs undergo a major temporal transition during pupal development, including the Imp/Syp transition and reciprocal changes in Kr-h1 and E93 expression. They are also consistent with our experimental finding that Kr-h1 antagonises E93 expression in the MBNB lineage. We have added this analysis to the Results and incorporated it into the revised model.

(6) Figure 3A - Kr localization: Kr is detected predominantly in the cytoplasm, which contrasts with its function as a transcription factor. Is cytoplasmic localization typical for Kr? Please discuss.

We thank the reviewer for this important observation. We agree that the weak Kr signal in pupal MBNBs appears partly enriched in the cytoplasm, which is unexpected for a canonical nuclear transcription factor. We have revised the Discussion to address this point.

Because this signal was reduced upon Kr RNAi, we think that it is likely to represent a Kr-dependent signal rather than nonspecific background. However, we do not yet know whether the apparent cytoplasmic enrichment reflects dynamic regulation of Kr localisation, a non-canonical aspect of Kr function in postembryonic MBNBs, or technical limitations associated with detecting very low endogenous Kr levels. We therefore avoid overinterpreting the cytoplasmic signal, but note that Kr localisation and activity in pupal MBNBs may be more complex than expected for a canonical nuclear transcription factor. Future studies will be required to determine how Kr activity and localisation are regulated in pupal MBNBs.

(7) Temporal Kr knockdown experiment: The result that Kr knockdown during pupal stages - but not earlier - leads to MB NB persistence is interesting but counterintuitive. Given the limitations of RNAi (e.g., leaky expression, incomplete knockdown), MARCM clones for Kr mutants would provide stronger evidence and improve confidence in this conclusion.

We agree that MARCM analysis of Kr mutant MBNB clones would provide a valuable independent test of the temporal RNAi results. We attempted to establish this approach during revision, but it proved technically difficult within the available timeframe.

A major practical limitation is that MBNBs are very few in number, with only four per brain hemisphere. Conventional MARCM or flip-out approaches therefore generate stochastic clones that are inefficient for reliably recovering and analysing MBNB clones. We also explored the possibility of using MB-lineage MARCM reagents reported in a previous study (Rossi & Desplan, 2020), but the available stocks were not directly compatible with the FRT chromosome required for our Kr mutant analysis. Generating the necessary compatible stocks and recovering sufficient MBNB clones would require substantial additional crossing and screening.

For this reason, we were not able to include Kr mutant MARCM data in the revised manuscript. Instead, we base our conclusion on several complementary lines of evidence, including temporal Gal80ts-based Kr RNAi, two independent Kr RNAi lines, the reduction of Kr signal upon Kr RNAi newly added in this revision, and the independent KrIf-1 phenotype, which supports the idea that precise regulation of Kr activity is required for MBNB termination.

(8) OK107-GAL4 activity: Please indicate early in the manuscript that OK107-GAL4 is not active in MB NBs but is active in their progeny. This would clarify the rationale for using the pan-NB driver insc-GAL4 for manipulating MB NBs.

We thank the reviewer for this suggestion. We have revised the manuscript to clarify the use of OK107-Gal4 and insc-Gal4 earlier in the Results and in the relevant figure legends.

Although OK107-Gal4 activity is not completely absent from MBNBs, its activity in MBNBs is stage-dependent and weaker or more variable than in MB neurons and their progeny. We therefore used OK107-Gal4 mainly to visualise MB structures and MB lineage regions, whereas insc-Gal4 was used for robust NB-specific manipulation. This clarification should help explain why insc-Gal4, rather than OK107-Gal4, was used for MBNB-targeted knockdown experiments.

(9) Figure 5A - Mira+ cell numbers: There appears to be an excess of Mira+ cells compared to the expected number of MB NBs. Please explain this observation.

We thank the reviewer for pointing this out. In Fig. 5A, we quantified the number of EdU-positive clones, not the total number of Mira-positive cells. As shown in Fig. 2, proliferative cells retained in Kr-depleted or KrIf-1 mutant adult brains were identified as persistent MBNBs based on combined criteria, including EdU incorporation, NB marker expression such as Mira and insc>GFP, NB-like morphology, and stereotyped location in the dorsoposterior MB region.

We agree that additional Mira-positive cells can be observed in adult brains, including in control and Kr-depleted brains. However, these cells were not associated with EdU-positive proliferative clones and did not consistently express canonical NB markers examined in this study. Their identity therefore remains unclear, and they were not scored as retained MBNBs.

(10) Line 430 - Kr-h1 over-expression phenotype: The amplification phenotype caused by Kr-h1 overexpression is reminiscent of that caused by chinmo overexpression (Narbonne-Reveau et al., 2016), suggesting that Kr-h1 may promote chinmo and Imp expression. Also, what is the expression pattern of Kr in the supernumerary adult MB NBs following Kr-h1 overexpression? Is Kr silenced? Investigating this would help clarify the regulatory links between Kr, Kr-h1, and Imp/chinmo.

We agree that the Kr-h1 overexpression phenotype is reminiscent of NB amplification phenotypes associated with forced or aberrant activation of early temporal growth programmes, including those linked to Chinmo. Narbonne-Reveau et al. showed that Chinmo can promote NB amplification and tumour growth, and that Chinmo, Imp and Lin-28 form a growth-promoting module in neural tumours. Consistent with this idea, our revised manuscript shows that Kr-h1 overexpression causes extensive tumour-like NB overgrowth, impaired neuronal differentiation and persistent Imp expression (Fig. 5C–E).

Although we did not analyse Chinmo expression in this revision, we did examine Imp expression following Kr-h1 overexpression and found persistent Imp expression in tumour-like NB cells (Fig. 5E). These data are consistent with the idea that excessive Kr-h1 activity can reinforce a progenitor-like state. However, we have interpreted this result cautiously, because Kr-h1 overexpression produces a severe tumour-like phenotype with impaired asymmetric division and neuronal differentiation. Thus, persistent Imp expression in this context could reflect either a more direct effect of Kr-h1 on early temporal programmes or an indirect consequence of the strongly perturbed progenitor-like state.

We also did not directly analyse Kr expression in supernumerary NB-like cells following Kr-h1 overexpression. This is an interesting question, but the severe tissue disruption caused by Kr-h1 overexpression would make it difficult to distinguish a physiological regulatory effect on Kr from an indirect consequence of tumour-like overgrowth. In addition, endogenous Kr signals in MBNBs are weak, making it technically challenging to reliably quantify changes in Kr expression in this strongly perturbed condition.

We have therefore revised the Discussion to clarify that the Kr-h1 overexpression phenotype should be interpreted mainly as evidence that excessive Kr-h1 activity can oppose MBNB termination and maintain Imp-positive progenitor-like cells, rather than as evidence for a defined normal regulatory pathway from Kr-h1 to Chinmo, Imp or Kr. In parallel, our revised loss-of-function and expression analyses show that Kr depletion causes persistent Imp and reduced Syp expression, that Kr supports E93 expression in the MBNB lineage (Fig. 5B), and that Kr-h1 antagonises E93 expression (Fig. S5B). Because Kr depletion did not significantly increase Kr-h1::GFP expression (Fig. 5B), we no longer present a simple linear model in which Kr promotes MBNB termination by repressing Kr-h1 expression.

(11) Kr-h1 expression in MB NBs: Please provide direct evidence that Kr-h1 is expressed in MB NBs during development.

We agree that direct evidence for Kr-h1 expression in MBNBs is important. We have therefore analysed Kr-h1 expression using a functional Kr-h1::GFP BAC reporter. Kr-h1::GFP was clearly detected in MBNBs during third-instar larval stages, with nuclear enrichment, but became barely detectable in late pupal MBNBs (Fig. 5B and Fig. S5C).

This developmental downregulation is consistent with the published MBNB-lineage RNA-seq dataset, which shows high Kr-h1 transcript levels during larval stages and strong reduction after the larval-to-pupal transition (Fig. S5A). Together, these data provide direct evidence that Kr-h1 is expressed in MBNBs during development and is downregulated before MBNB termination.

(12) Figure 6D - Model validation: The model in Figure 6D is appealing, but many of the proposed interactions remain untested. For example:

- It is not established that Kr-h1 antagonizes E93 or vice versa in MB NBs.

- The antagonistic relationship between Kr and Kr-h1 has not been experimentally confirmed.

- The temporal expression of Kr-h1 in MB NBs is unknown.

- The repression of E93 by Kr-h1 is unlikely to fully explain the MB NB amplification phenotype.

We thank the reviewer for this helpful critique. We have substantially revised Fig. 6D and the accompanying text to distinguish experimentally supported interactions from unresolved regulatory links.

First, we have now tested the relationship between Kr-h1 and E93 in the MBNB lineage. Kr-h1 depletion increased E93 expression, whereas Kr-h1 overexpression reduced E93 expression (Fig. S5B), supporting the conclusion that Kr-h1 antagonises E93 expression in this lineage. Reciprocal antagonism between Kr-h1 and E93 has been reported in other insect developmental contexts. However, because we did not directly test whether E93 represses Kr-h1 in MBNBs, we now present this possible E93-to-Kr-h1 regulation as an unresolved or putative interaction rather than as an experimentally established relationship in our system.

Second, we have clarified the relationship between Kr and Kr-h1. Our genetic data show that Kr-h1 knockdown partially suppresses MBNB retention caused by Kr depletion (Fig. 5A), indicating that Kr and Kr-h1 have opposing functions during MBNB termination. However, although Kr depletion reduced E93 expression in the MBNB lineage, it did not detectably increase Kr-h1::GFP levels in late pupal MBNBs (Fig. 5B). We therefore no longer present Kr as a direct upstream repressor of Kr-h1. Instead, the revised model proposes that Kr promotes MBNB termination by supporting the Imp-to-Syp transition and E93 expression, whereas Kr-h1 opposes termination at least in part by repressing E93.

Third, we now provide direct evidence for Kr-h1 expression in MBNBs using a functional Kr-h1::GFP BAC reporter. Kr-h1::GFP was detected in larval MBNBs and became strongly reduced during pupal development (Fig. 5B and Fig. S5C). This temporal pattern is also consistent with the published MBNB-lineage RNA-seq dataset, which shows high Kr-h1 transcript levels during larval stages and downregulation after the larval-to-pupal transition (Fig. S5A).

Finally, we agree that repression of E93 by Kr-h1 is unlikely to fully explain the strong tumour-like NB overgrowth caused by Kr-h1 overexpression. In the revised manuscript, we show that supernumerary tumour-like NB cells induced by Kr-h1 overexpression retain high Imp expression (Fig. 5E). This suggests that excessive Kr-h1 activity can oppose MBNB termination and maintain an Imp-positive progenitor-like state.

However, we interpret the Kr-h1 overexpression phenotype cautiously, because this strong gain-of-function condition causes severe tumour-like overgrowth and may not accurately reflect the physiological regulatory relationship between Kr-h1 and the normal MBNB termination programme. We have therefore revised the Discussion to state that Chinmo, an early temporal factor linked to the Imp/Syp programme, may be relevant to the persistent progenitor-like state observed after Kr depletion or Kr-h1 overexpression. However, because we did not directly analyse Chinmo expression in this study, we do not include Chinmo in the main model and leave this question for future work.

Minor Points

(1) OK107-GAL4 activity: Please check and indicate early on in the manuscript that OK107-GAL4 is not active in MB NBs (although being active in their progeny). It would clarify why the authors keep using the pan NB insc-GAL4 to manipulate MB NBs.

As described in our response to Major Point 8, we have clarified earlier in the Results that OK107-Gal4 strongly labels MB neurons and the MB lineage, but is not a robust or consistent driver in MBNBs at the stages relevant to our functional assays. We therefore used OK107-Gal4 primarily for visualising MB structures and MB lineage regions, whereas insc-Gal4 was used for robust NB-specific manipulation.

(2) CCR list: Please clarify how the list of candidate cell cycle regulators (CCRs) was compiled.

We have revised the Materials and Methods to clarify how the list of candidate cell-cycle regulators was compiled. Briefly, the CCR list was manually curated to include core cell-cycle regulators, cyclins and CDKs, DNA replication factors, checkpoint regulators, mitotic regulators, APC/C and ubiquitin-proteasome components, and non-canonical CDKs with known roles in transcriptional regulation.

(3) Line 77-78 - Cas and Svp: The statement that Cas and Svp regulate neurogenesis termination by directly regulating cell cycle regulators needs references. As far as I know, the direct targets of Cas and Svp remain unidentified.

We agree that the original wording was too strong. We have revised the text to state more generally that temporal transcription factors, including Cas and Svp, influence NB proliferation and lifespan, without implying that they directly regulate known cell-cycle target genes.

(4) Line 410: Please add references to support this statement.

We have added the appropriate reference to the original genetic modifier screen by Abrell et al., 2000, in which Kr-h1 mutations were identified as enhancers of the KrIf-1 eye phenotype. We have also revised the wording to state that this finding suggests a functional interaction between Kr and Kr-h1, rather than using it alone as evidence for a direct regulatory relationship.

(5) Typos and minor edits:

- Line 38: "capable" (spelling)

- Line 102: Replace "unexplored" with "explored"

- Line 106: "potential" (spelling)

- Line 243: "mitotic" (spelling)

- Line 260: "KrIf-1" (correct gene formatting)

We have corrected the typographical errors and formatting issues indicated by the reviewer, including spelling errors and KrIf-1 gene formatting. We have also proofread the manuscript throughout.

eLife Assessment

This paper provides a valuable observation that imiquimod, a compound often used to induce a psoriasis-like skin inflammation in mice, has a TLR7-independent effect acting through the unfolded protein response and binding to Gelsolin. These solid findings expand our understanding of imiquimod-mediated inflammation and are of interest to the field of skin immunology.

Reviewer #2 (Public review):

Summary:

This paper shows that imiquimod, a compound often used to induce a psoriasis-like skin inflammation in mice, has a TLR7-independent effects that induce the unfolded protein response and amplify cytokine expression in dendritic cells. Although these effects of imiquimod have been described in the literature before, this study provides more detailed evidence and different contexts to this observation. These findings add to existing literature that imiquimod has a pleotropic mechanism of action involving changes in mitochondrial functions and cellular stress responses. Specifically, the authors show that imiquimod can induce calcium signaling in immune cells and potentiate two branches of the unfolded protein response in a TLR7-independent and MyD88-independent manner. They also show that some of these effects might be partially mediated by direct binding of imiquimod to Gelsolin. These findings expand our understanding of imiquimod-mediated inflammation and are useful for the field of experimental skin immunology and mouse models of psoriasis. However, molecular and cellular mechanisms connecting Gelsolin to the unfolded protein response and skin inflammation presented in this paper requires further investigation in the context of TLR-mediated inflammation.

Strengths:

(1) TLR7-independent effects of imiquimod to the expression of genes and proteins involved into the unfolded protein response are well demonstrated.

(2) Gelsolin is identified as a new imiquimod-binding protein in mouse cells.

Weaknesses:

(1) Effects of imiquimod on mitochondrial Ca signaling are not clear form the presented data.

(2) The mechanism of action connecting imiquimod to Gelsolin on the unfolded protein response and cytokine production remains not fully explained.

(3) It remains unclear if Gelsolin contributes to regulating TLR7 (or other types of TLR-mediated) inflammation in vivo.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study is technically extensive and employs a wide range of experimental approaches, including in vivo analyses, cell-based assays, and transcriptomic data integration. The authors provide a detailed characterization of inflammatory and stress-related pathways activated following IMQ exposure in mouse skin. These datasets may be informative for researchers specifically interested in IMQ-induced dermatitis or in stress responses triggered by chemical skin irritants.

We sincerely thank the reviewer for this positive assessment of our study. We appreciate the recognition of the breadth of our experimental approaches, including the integration of in vivo analyses, cell-based experiments, and transcriptomic analyses, as well as the acknowledgement that our findings provide useful insights into IMQ-induced dermatitis and stress responses triggered by chemical skin irritants. We have carefully considered the reviewer's comments and have substantially revised the manuscript to address the concerns regarding the interpretation and disease relevance of our findings. Detailed responses to the specific points raised are provided below.

Strengths:

The study is technically extensive and employs a wide range of experimental approaches, including in vivo analyses, cell-based assays, and transcriptomic data integration. The authors provide a detailed characterization of inflammatory and stress-related pathways activated following IMQ exposure in mouse skin. These datasets may be informative for researchers specifically interested in IMQ-induced dermatitis or in stress responses triggered by chemical skin irritants.

We sincerely thank the reviewer for this positive assessment and for recognizing the breadth of our experimental approaches and the potential value of our findings for researchers studying IMQ-induced dermatitis and stress responses.

Weaknesses:

A major limitation of the manuscript is its exclusive reliance on the IMQ model, which does not adequately represent the immunological drivers, cellular interactions, or therapeutic responsiveness of human psoriasis, despite the manuscript's framing. IMQ-induced inflammation is dominated by innate immune activation and mouse-specific pathways, whereas human psoriasis is driven primarily by IL-23/IL-17-mediated interactions between keratinocytes and Th17/Tc17 cells. As a result, conclusions drawn entirely from IMQ-based experiments have limited relevance to human disease biology.

Consistent with this issue, the manuscript places strong emphasis on pathways such as TLR signaling, inflammasome activation, and IL-1-associated responses, none of which are established as central drivers of plaque psoriasis in patients. Therapeutic strategies targeting these pathways have failed to achieve clinical efficacy comparable to IL-23 or IL-17 blockade, yet this translational gap is not adequately addressed.

The in vitro keratinocyte experiments further limit interpretability. Stimulation of keratinocytes with IMQ is not an accepted model of psoriasis-relevant keratinocyte activation, and the study does not demonstrate induction of well-established psoriasis signature gene programs. Without this validation, it is difficult to assess the relevance of the observed cellular stress responses to human disease.

The RNA-sequencing analyses raise additional concerns regarding rationale and interpretation. The basis for selecting specific mouse and human datasets is unclear, including the use of unpublished or non-psoriasis inflammatory datasets. Key methodological details related to data processing, normalization, cross-species comparison, and statistical analysis are insufficiently described. In addition, the limited number of differentially expressed genes identified does not align with the extensive psoriasis transcriptomic literature, raising concerns about analytical rigor.

Finally, the manuscript emphasizes a small number of genes described as "psoriasis-associated" while failing to demonstrate regulation of widely accepted psoriasis signature genes known to correlate with disease activity and therapeutic response in patients.

We thank the reviewer for this thoughtful and comprehensive assessment of our study. We carefully considered each of the concerns raised regarding the interpretation and translational relevance of our findings and have substantially revised the manuscript accordingly.

Specifically, we have tempered our interpretation throughout the manuscript to clearly distinguish IMQ-induced dermatitis from human plaque psoriasis and to emphasize that our conclusions should be interpreted primarily within the context of the IMQ-induced inflammation model. To improve the relevance of our findings to psoriasis biology, we performed additional experiments using IL-17A- and TNF-α-stimulated primary keratinocytes and incorporated these data into the revised manuscript. We also expanded the description of our RNA-seq analyses, including dataset selection, analytical procedures, and cross-species comparison, and clarified the rationale for selecting representative UPR-responsive genes for validation. In addition, we revised the Introduction and Discussion to more appropriately position the roles of inflammasome signaling, IL-1-associated pathways, and Gelsolin in the context of IMQ-induced inflammation and human psoriasis.

We believe that these revisions substantially strengthen the manuscript and address the reviewer's major concerns. Detailed responses to each specific point are provided below.

Reviewer #2 (Public review):

Summary:

This paper shows that imiquimod, a compound often used to induce a psoriasis-like skin inflammation in mice, has a TLR7-independent effects that induce the unfolded protein response and amplify cytokine expression in dendritic cells. Although these effects of imiquimod have been described in the literature before, this study provides more detailed evidence and different contexts to this observation. These findings add to existing literature that imiquimod has a pleotropic mechanism of action involving changes in mitochondrial functions and cellular stress responses. Specifically, the authors show that imiquimod can induce calcium signaling in immune cells and potentiate two branches of the unfolded protein response in a TLR7-independent and MyD88-independent manner. They also show that some of these effects might be partially mediated by direct binding of imiquimod to Gelsolin. These findings expand our understanding of imiquimod-mediated inflammation and are useful for the field of experimental skin immunology and mouse models of psoriasis. However, the molecular and cellular mechanisms connecting Gelsolin to the unfolded protein response and skin inflammation presented in this paper require further investigation in the context of TLR-mediated inflammation.

We sincerely thank the reviewer for this thoughtful and balanced assessment of our study. We greatly appreciate the recognition that our work provides additional mechanistic insight into the TLR7-independent actions of IMQ and expands current understanding of IMQ-induced inflammation, mitochondrial dysfunction, and unfolded protein response signaling. We also appreciate the recognition that our findings may be valuable for the fields of experimental skin immunology and mouse models of psoriasis. In response to the reviewer's comments, we have further revised the manuscript to clarify the rationale for investigating Gelsolin, to better distinguish IMQ-induced inflammation from human psoriasis, and to more appropriately discuss the limitations of our mechanistic interpretation. Detailed responses to the specific points raised are provided below.

Strengths:

(1) TLR7-independent effects of imiquimod on the expression of genes and proteins involved in the unfolded protein response are well demonstrated.

(2) Gelsolin is identified as a new imiquimod-binding protein in mouse cells.

We sincerely thank the reviewer for these positive comments. We greatly appreciate the recognition that our study provides clear evidence for the TLR7-independent effects of IMQ on unfolded protein response signaling and identifies Gelsolin as a novel IMQ-binding protein. We are grateful for the reviewer's positive assessment of these findings.

Weaknesses:

(1) Effects of imiquimod on mitochondrial Ca signaling are not clear from the presented data.

(2) The mechanism of action connecting imiquimod to Gelsolin on the unfolded protein response and cytokine production remains not fully explained.

(3) It remains unclear if Gelsolin contributes to regulating TLR7 (or other types of TLR-mediated) inflammation in vivo.

We thank the reviewer for these thoughtful comments. We have carefully considered each of the concerns raised regarding the interpretation of mitochondrial Ca²⁺ signaling, the mechanistic link between Gelsolin and UPR signaling, and the role of Gelsolin in TLR-mediated inflammatory responses. In the revised manuscript, we have clarified the interpretation of our mitochondrial Ca²⁺ data, strengthened the discussion regarding the mechanistic role of Gelsolin based on the additional experiments performed in this revision, and more clearly defined the scope of our conclusions regarding Gelsolin in IMQ-induced inflammation. We believe these revisions substantially strengthen the manuscript while avoiding conclusions that extend beyond the experimental evidence. Detailed responses to each point are provided below.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The following points outline specific issues that would need to be addressed to substantially strengthen the manuscript. Several of these represent fundamental limitations of the current study design and interpretation.

We thank the reviewer for this overall assessment. We have carefully addressed each of the points raised and have revised the manuscript accordingly. Detailed point-by-point responses are provided below.

(1) Model limitations

- The manuscript relies exclusively on imiquimod (IMQ), which does not model the core immune drivers or treatment responsiveness of human psoriasis.

- Claims regarding relevance to human psoriasis should therefore be substantially tempered, or alternative models more reflective of human disease biology should be incorporated.

We thank the reviewer for this important comment. We agree that the IMQ-induced dermatitis model does not fully recapitulate the immunopathology, chronicity, or therapeutic responsiveness of human plaque psoriasis. Accordingly, we have substantially tempered our interpretation throughout the manuscript. In the revised Introduction and Discussion, we explicitly state that our findings should be interpreted primarily in the context of IMQ-induced skin inflammation rather than human psoriasis, and that further validation in human psoriasis-relevant systems will be required. We have also revised statements throughout the manuscript to avoid overgeneralization regarding human psoriasis. In addition, to improve the disease relevance of our mechanistic findings, we have performed additional keratinocyte experiments using IL-17A and TNF-α stimulation, which better reflect the canonical inflammatory pathways implicated in human psoriasis. Together with the revised interpretation throughout the manuscript, we believe these changes appropriately position our findings within the context of the IMQ-induced dermatitis model while improving their relevance to human psoriasis.

Changes made in the manuscript: See Figure S6

- The Introduction and Discussion were revised to clarify the limitations of the IMQ-induced dermatitis model and to distinguish IMQ-driven inflammation from human plaque psoriasis.

- Statements implying direct relevance to human psoriasis were revised to more appropriately reflect the scope of the study.

- Additional experiments using IL-17A and TNF-α-stimulated keratinocytes were incorporated to strengthen the relevance of the findings to established psoriasis biology.

(2) Immune context

- gdT cells should be removed from the Introduction as contributors to IL-17A production in human psoriasis, as this is a feature of mouse models rather than human disease (PMID: 28945199).

- The roles of Th17 and Tc17 cells should be emphasized, with appropriate acknowledgment that IMQ-driven inflammation differs substantially from human psoriasis immunopathology.

We thank the reviewer for this valuable comment. We agree that gdT cells are major IL-17A-producing cells in the IMQ-induced mouse model but are not considered the principal source of IL-17A in human plaque psoriasis. Accordingly, we have revised the Introduction to remove statements implying that gdT cells are major contributors to IL-17A production in human psoriasis and have instead emphasized the established roles of Th17 and Tc17 cells. In addition, we have revised the Discussion to explicitly acknowledge that the immunopathology of the IMQ-induced dermatitis model differs substantially from that of human psoriasis and that our findings should therefore be interpreted within the context of IMQ-induced skin inflammation.

Changes made in the manuscript:

- Statements describing gdT cells as major IL-17A-producing cells in human psoriasis were removed from the Introduction.

- The roles of Th17 and Tc17 cells in human psoriasis were emphasized.

- Additional text was added to the Discussion clarifying the immunological differences between the IMQ-induced dermatitis model and human plaque psoriasis.

(3) Keratinocyte stimulation

- IMQ stimulation of keratinocytes is not an accepted model of psoriasis-relevant keratinocyte activation.

- To support disease relevance, experiments should incorporate stimulation with IL-17A (100 ng/ml) {plus minus} TNF-a (10 ng/ml) and appropriate time points consistent with established psoriasis biology.

We thank the reviewer for this constructive suggestion. We agree that stimulation of keratinocytes with IL-17A and TNF-α more closely reflects cytokine-mediated keratinocyte activation in human psoriasis than stimulation with IMQ alone.

We would like to clarify that our IMQ stimulation experiments were not intended to serve as a model of psoriasis-associated keratinocyte activation. Rather, these experiments were designed to investigate the molecular mechanisms by which IMQ directly induces UPR signaling in keratinocytes, as IMQ is the primary experimental stimulus used throughout this study.

To address the reviewer's concern regarding disease relevance, we performed additional experiments using primary keratinocytes stimulated with IL-17A and TNF-α. As expected, IL-17A and TNF-α robustly induced canonical psoriasis-associated genes, including S100a8, S100a9, and Defb14, thereby providing complementary evidence supporting the relevance of our findings to psoriasis-associated inflammatory signaling. These new data have been incorporated as Figure S6.

We believe that these additional experiments appropriately complement our mechanistic studies by linking the identified pathways to established psoriasis-associated inflammatory signaling while preserving the original objective of the IMQ stimulation experiments.

Changes made in the manuscript: See Figure S6

- New experiments using IL-17A and TNF-a-stimulated primary keratinocytes were performed.

- A time-course analysis was conducted to evaluate cytokine-induced gene expression.

- The new data have been included as Figure S6.

(4) Inflammasome and IL-1-related claims

- The manuscript should acknowledge that IL-1 and inflammasome targeting have failed to demonstrate clinical efficacy in plaque psoriasis.

- Observations in inflammasome-, MyD88-, or TLR-deficient mice should not be interpreted as evidence of underexplored human psoriasis pathways, but rather as reflecting IMQ-specific biology.

We thank the reviewer for this important comment. We agree that the contribution of IL-1 signaling and inflammasome activation to IMQ-induced skin inflammation should not be directly extrapolated to human plaque psoriasis. Accordingly, we have revised the Discussion to acknowledge that clinical studies targeting IL-1 signaling have not demonstrated consistent therapeutic efficacy in plaque psoriasis. We have also tempered our interpretation of findings obtained from inflammasome-, MyD88-, and TLR-deficient mouse models, emphasizing that these observations likely reflect mechanisms specific to the IMQ-induced dermatitis model rather than underexplored pathways in human psoriasis. Throughout the revised manuscript, statements implying direct relevance to human psoriasis have been modified accordingly.

Changes made in the manuscript:

- The Introduction and Discussion now acknowledge the limited clinical efficacy of IL-1-targeted therapies in plaque psoriasis.

- Statements regarding inflammasome-, MyD88-, and TLR-dependent mechanisms have been revised to clarify that they primarily reflect IMQ-specific biology.

- Interpretations linking these pathways directly to human psoriasis have been moderated throughout the manuscript.

(5) Cathelicidin and defensin biology

- Statements suggesting that LL37 or b-defensins "exacerbate psoriasis" should be revised to reflect their contributory roles in disease pathogenesis rather than disease worsening.

- It should be acknowledged that CRAMP- or defensin-deficient mice do not show improvement in IMQ-induced dermatitis, consistent with IMQ bypassing these pathways.

We thank the reviewer for this valuable comment. We agree that LL37 and b-defensins should not be described as factors that directly exacerbate psoriasis, but rather as multifunctional mediators that contribute to disease pathogenesis in a context-dependent manner. Accordingly, we have revised the relevant statements throughout the manuscript to more accurately reflect their proposed roles.

In addition, we have expanded the Discussion to acknowledge previous studies demonstrating that CRAMP- or b-defensin-deficient mice do not exhibit substantial improvement in IMQ-induced dermatitis. We now explicitly state that IMQ-driven inflammation can proceed independently of these pathways, highlighting the distinction between mechanisms contributing to human psoriasis pathogenesis and those operating in the IMQ-induced dermatitis model.

Changes made in the manuscript:

- Statements describing LL37 or b-defensins as exacerbating psoriasis were revised to indicate that they contribute to disease pathogenesis.

- The Discussion was expanded to acknowledge that CRAMP- or b-defensin deficiency does not substantially attenuate IMQ-induced dermatitis, consistent with the IMQ model bypassing these pathways.

- The limitations of extrapolating these observations to human psoriasis were clarified.

(6) Gelsolin and IMQ-binding experiments

- Experiments focused on proteins that bind IMQ have limited translational relevance.

- If gelsolin is to be emphasized, the rationale should be grounded in human psoriasis data demonstrating altered gelsolin levels rather than IMQ binding (PMIDs: 36902587, 32002760).

We thank the reviewer for this important comment. We agree that the translational relevance of proteins identified solely through their ability to bind IMQ is limited. Accordingly, we have revised the manuscript to clarify that our rationale for focusing on Gelsolin is supported not only by its interaction with IMQ but also by independent evidence demonstrating altered Gelsolin expression in patients with psoriasis and psoriatic arthritis. We have incorporated these human studies into the Introduction and Discussion and have revised the relevant text to emphasize the potential clinical relevance of Gelsolin beyond its interaction with IMQ.

Changes made in the manuscript:

- Statements emphasizing IMQ binding as the primary rationale for studying Gelsolin were revised.

- Additional references reporting altered Gelsolin expression in patients with psoriasis and psoriatic arthritis were incorporated.

- The Discussion now clarifies that the rationale for investigating Gelsolin is supported by both its interaction with IMQ and independent observations from human disease.

(7) Vehicle controls

- Appropriate vehicle controls for IMQ treatment (Aldara alone) should be included and clearly described, particularly given the known inflammasome-activating properties of isostearic acid (PMID: 23463003).

- The use of DMSO or ethanol as vehicle controls is not justified in this context.

We thank the reviewer for this important comment. We agree that inclusion of an appropriate vehicle control for Aldara cream would have strengthened the interpretation of the in vivo experiments. Unfortunately, the vehicle formulation of Aldara was not commercially available to us and therefore could not be included in the present study.

Because the in vivo experiment assessing mtDNA accumulation in ear tissue following topical IMQ cream application could not be appropriately controlled, we have removed these data from the revised manuscript. We believe this is the most appropriate approach to avoid overinterpretation of results that may potentially be influenced by the cream formulation.

Importantly, our in vitro experiments were performed using purified IMQ rather than IMQ cream. Thus, our conclusion that IMQ induces mtDNA release is supported by experiments performed with purified IMQ, independent of the topical cream formulation.

Changes made in the manuscript: See Figure 4

- The in vivo experiment assessing mtDNA accumulation in ear tissue following topical IMQ cream application has been removed from the revised manuscript.

- The Results and corresponding figure have been revised accordingly.

- The Discussion has been updated to acknowledge the limitation associated with the absence of an Aldara vehicle control.

(8) RNA-sequencing and bioinformatics

- The rationale for selecting specific mouse and human RNA-sequencing datasets should be clearly articulated.

- All datasets analyzed should be explicitly identified, with clarification of their relevance and publication status.

- Methods describing normalization, differential expression analysis, false-discovery correction, and cross-species gene mapping should be expanded to ensure transparency and reproducibility.

We thank the reviewer for this constructive comment. We have substantially expanded the description of the RNA-sequencing and bioinformatics analyses to improve transparency and reproducibility.

First, we now explicitly describe the rationale for selecting the public RNA-seq datasets. GSE289485 was selected because it contains transcriptomic profiles from an IMQ-induced mouse model of psoriasis-like dermatitis, whereas GSE117405 contains transcriptomic data from human psoriasis lesions and healthy control skin, enabling comparison between the mouse model and human disease. We also clarify that both datasets were publicly available at the time of analysis.

Second, detailed information regarding all GEO datasets analyzed, including accession numbers, sample descriptions, publication status, and the specific samples included in the present study, has been provided in Supplementary Table 14.

Finally, the bioinformatics workflow has been described in substantially greater detail. The revised Methods now include descriptions of raw data retrieval from the SRA, quality trimming, sequence alignment, rRNA read removal, read counting, normalization, differential expression analysis, multiple-testing correction, and the orthology-based cross-species comparison used to identify conserved transcriptional responses between mouse and human datasets.

Changes made in the manuscript: See Table S14

- The rationale for selecting GSE289485 and GSE117405 was added.

- Detailed information for all analyzed datasets was summarized in Supplementary Table 14.

- The RNA-seq Methods were expanded to describe quality control, alignment, read counting, normalization, differential expression analysis, false-discovery correction, and orthology-based cross-species comparison.

(9) Gene selection and validation

- Validation should include canonical psoriasis signature genes known to correlate with disease activity and therapeutic response (e.g., S100A8/A9, IL-17C, IL-36g, IL-23, TNF; see PMID: 21085185).

- The current emphasis on Ccl20, Nr4a3, and Defb14 does not adequately capture established psoriasis biology and should be better justified.

We thank the reviewer for this valuable suggestion. We agree that validation using canonical psoriasis-associated genes strengthens the disease relevance of our findings. Accordingly, we performed additional experiments using primary keratinocytes stimulated with IL-17A and TNF-α and evaluated the expression of established psoriasis signature genes, including S100a8 and S100a9. As expected, both genes were robustly induced by IL-17A and TNF- a stimulation. In addition, Defb14, which was also induced by IMQ stimulation, was similarly upregulated by IL-17A and TNF-α. These results further support the relevance of our findings to psoriasis-associated inflammatory signaling.

We have also clarified the rationale for selecting Ccl20, Nr4a3, and Defb14 for further validation. These genes were not intended to represent canonical psoriasis biomarkers but were selected because our transcriptomic analyses identified them as representative UPR-responsive genes that were strongly induced by IMQ stimulation. Accordingly, they were used to investigate the mechanistic contribution of UPR signaling rather than to represent the overall psoriasis transcriptional signature. This rationale has now been clarified in the revised Results section.

Changes made in the manuscript: See Figure S6, and S7

- Additional validation experiments were performed using IL-17A/TNF-a-stimulated keratinocytes.

- The rationale for selecting Ccl20, Nr4a3, and Defb14 was clarified in the Results section.

(10) Histology and data presentation

- Ear skin sampling procedures should be standardized and clearly described.

- All relevant control groups should be shown histologically.

- Figures require clearer labeling, consistent terminology (e.g., ear skin vs. ear lobe), appropriate white balancing, and improved quantitative presentation (e.g., dot plots where appropriate).

- qRT-PCR data should be presented using clearly defined raw or normalized values rather than scaled or ambiguous controls.

We thank the reviewer for these helpful suggestions. We have revised the manuscript to improve the description of histological procedures and the presentation of histological and quantitative data.

First, the Methods section has been expanded to clearly describe the ear skin sampling procedure. We now specify that approximately the distal 2 mm of the ear was collected and processed for histological analysis, thereby ensuring consistent sampling among all animals.

Second, we carefully reviewed the histological figures and confirmed that the relevant control groups are included in the revised manuscript.

Third, figure labeling and terminology have been standardized throughout the manuscript. In addition, quantitative histological data are now presented with individual data points overlaid on the graphs where appropriate, thereby improving data visualization and transparency. The representative histological images are intended to illustrate epidermal thickening, whereas the conclusions are based on quantitative measurements rather than qualitative assessment of image appearance.

Finally, the presentation of the RT-qPCR data has been clarified. The Y-axis labels now explicitly indicate the reference condition used for normalization, and the Methods section has been expanded to describe the DDCt method, including the reference genes used for normalization.

Changes made in the manuscript: See Figure 4D, and 5C

- The ear skin sampling procedure was described in greater detail in the Methods.

- Histological figures and figure labels were reviewed and terminology was standardized throughout the manuscript.

- Individual data points were added to quantitative graphs where appropriate.

- The RT-qPCR y-axis labels were revised to clearly indicate the normalization reference, and the DDCt analysis was described in the Methods.

Reviewer #2 (Recommendations for the authors):

(1) The effects of IMQ in Figure 1B are very small. I recommend adding an orthogonal approach to support that mitochondrial Ca is involved.

We sincerely thank the reviewer for this thoughtful and constructive comment. We agree that the increase in the Rhod-2 signal observed following IMQ stimulation is quantitatively modest. However, we respectfully believe that the biological significance of this observation should not be judged solely by the magnitude of the fluorescence change. Rather, the increase in mitochondrial Ca²⁺ should be interpreted in the context of the multiple independent functional assays presented throughout Figure 1, all of which consistently support a role for mitochondrial Ca²⁺ in IMQ-induced inflammatory responses.

First, we demonstrated that IMQ stimulation significantly increased intracellular ROS production, as assessed by CellROX staining (Figure 1C), and that this increase was significantly suppressed by pretreatment with 2-APB, suggesting that Ca²⁺ dysregulation functionally contributes to ROS generation. In addition, 2-APB markedly reduced IL-1b secretion (Figure 1D), further supporting a functional link between Ca²⁺ signaling and inflammasome activation.

Second, IMQ stimulation induced mitochondrial dysfunction, as demonstrated by JC-1 staining (Figure 1G), and significantly increased mitochondrial ROS production, as measured by MitoSOX (Figure 1H). These findings indicate that IMQ triggers a cascade of mitochondrial events extending beyond the modest increase in mitochondrial Ca²⁺, ultimately resulting in oxidative stress and mitochondrial damage.

Furthermore, treatment with the mitochondria-targeted antioxidant MitoQ, as well as the antioxidants GSHEE, NAC, and PDTC, significantly suppressed IMQ-induced IL-1b secretion (Figures 1I and 1K), supporting the conclusion that mitochondrial ROS is a critical downstream mediator of IMQ-induced inflammatory signaling.

Taken together, these complementary findings provide multiple independent lines of evidence supporting a role for mitochondrial Ca²⁺-associated signaling in IMQ-induced inflammation. Although the increase in Rhod-2 fluorescence was relatively modest, it was consistently accompanied by mitochondrial ROS generation, mitochondrial dysfunction, and inflammasome activation. We therefore believe that the biological significance of mitochondrial Ca²⁺ is best evaluated in the context of these convergent functional outcomes rather than by the magnitude of the Rhod-2 signal alone.

We agree that an independent approach for measuring mitochondrial Ca²⁺ would further strengthen this conclusion. However, because several complementary functional assays consistently support the involvement of mitochondrial Ca²⁺-associated mitochondrial dysfunction in IMQ-induced inflammatory responses, we believe that the current data collectively provide strong evidence for the proposed mechanism.

(2) Figure 7E-G would benefit from testing effects of IMQ versus RSQ on observed phenotypes to confirm that they are mediated by Gelsolin-IMQ interaction but not an effect of Gelsolin on TLR7-mediated inflammation.

We sincerely thank the reviewer for this valuable suggestion. We agree that it is important to determine whether the observed phenotypes reflect a specific interaction between Gelsolin and IMQ rather than a general role of Gelsolin in TLR7-mediated signaling.

In response to this comment, we performed additional experiments using resiquimod (RSQ), a TLR7/8 agonist. Gelsolin-deficient MEFs were stimulated with RSQ, and the same parameters analyzed in the IMQ experiments were evaluated.

Unlike the phenotypes observed following IMQ stimulation, RSQ stimulation did not reveal significant differences between wild-type and Gelsolin-deficient MEFs. Specifically, the Xbp1s/Xbp1 ratio was comparable between the two genotypes following RSQ stimulation. Similarly, mitochondrial ROS production, assessed by MitoSOX staining, and MAM formation, evaluated by proximity ligation assay (PLA), were not significantly altered by Gelsolin deficiency under RSQ stimulation.

Although the IMQ and RSQ experiments were performed independently and were not intended as a direct side-by-side quantitative comparison, the absence of genotype-dependent effects in the RSQ experiments indicates that Gelsolin deficiency alone does not generally enhance TLR7-mediated responses. Instead, these findings support the interpretation that the enhanced UPR activation, mitochondrial ROS production, and MAM formation observed in Gelsolin-deficient cells are specific to IMQ stimulation, consistent with the interaction between Gelsolin and IMQ.

Accordingly, the Results section has been revised to include these additional experiments, and the corresponding data have been incorporated into the revised Figure S11.

Changes made in the manuscript: See Figure S12

- Additional experiments using RSQ-stimulated wild-type and Gelsolin-deficient MEFs were performed.

- The Xbp1s/Xbp1 ratio, mitochondrial ROS production, and MAM formation were evaluated following RSQ stimulation.

- No significant genotype-dependent differences were observed under RSQ stimulation, supporting the specificity of the phenotypes observed following IMQ stimulation.

eLife Assessment

This important study addresses a discrepancy between population-level growth laws and single-cell correlations. It shows, for flagellar and synthetic genes in E. coli, that while gene expression of certain genes reduces population-average growth, expression levels positively correlate with growth at the single-cell level. The measurements are convincing, and the proposed mechanism - inheritance of growth factors such as ribosomes during asymmetric division - can explain this observation.

Reviewer #1 (Public review):

Summary:

Garcia-Alcala, Kratz and Cluzel investigate to what extent our understanding of bacterial physiology in bulk experiments can be applied to single-cell observations. They find that intrinsic noise may be powerful enough to even inverse the trends found in the bulk. The authors hypothesize that asymmetric distribution of ribosomes to daughter cells during the cell division plays the dominant role in the intrinsic noise and is able to generate the observed phenomenon. They do not show it directly, but the data and its agreement with the model suffice to support this claim.

Strengths:

The experimental part is convincing: the positive correlation between the elongation rate and promoter activity of unnecessary protein is clear, as well as the negative correlation between the mean values while changing the promoter strength. This was demonstrated in both rich and poor media. The causality between the growth rate and the promoter activity was shown using the negative lag time of the cross-correlation function. A simple, reasonable model accounts well for the data. This paper demonstrates an interesting phenomenon and provides a plausible theory for it, advancing our understanding of bacterial physiology on the single-cell level.

Weaknesses:

(1) Mean-reversion timescales were assumed to be longer than the simulation time and much longer than the cell cycle time. It is not clear whether the results robust in case mean-reversion timescales become of the order of cell cycle or smaller. If not, is there an argument for such practically infinite reversion timescales?

(2) It is not easy to understand the simulation part unless one reads Ref. [14]. Is k(t) assumed to follow Eq. (1) from ref. [14]? Is this crucial that the ribosome noise appears only at the division? The ribosome noise strength \sigma_R=0.06 - is it lower or higher than the naively expected binomial division?<br /> Also, more intuitive explanation of the Simpson paradox would help the reader.

(3) It would be useful for the reader to see the raw data and not only the filtered one to appreciate the measurement noise level.

(4) Negative lag time of the cross-correlation function is visible, but consider adding statistical test for it.

(5) Can you make similar cross-correlation plots using the model? Can you infer using it whether the data agrees better with the assumption that ribosomes noise appear only at division or continuous fluctuations during the cell cycle?

Comments on revised version:

The authors addressed the five comments listed above.

Reviewer #2 (Public review):

Summary:

The manuscript by Garcia-Alcala et al. reports an interesting paradox: the cost of gene expression slows the population-average growth rate, whereas at the single-cell level, expression levels from these genes positively correlate with the growth rate. The effect is observed in the expression of flagellar genes and a gene under a synthetic promoter in E. coli. The findings are explained by the inheritance of growth factors, including ribosomes, during asymmetric division.

Strengths:

(1) The manuscript adds strength to an emerging body of literature showing that the population-level bacterial growth laws do not match correlations based on single-cell data. The evidence presented here is more striking than in previous works (such as Pavlou et al., Nat. Commun. 2025), as the trends in population-level data and single-cell data are reversed.

(2) A relatively simple model correctly explains the trends in the data.

The findings raise an interesting question of whether similar effects occur in other bacterial species and, more broadly, in other organisms.

Comment on latest version:

The additional analysis has strengthened the conclusions.

Author response:

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

Public Reviews:

Reviewer #2 (Public review):

(1) The differing behavior of the MG1655 and MC4100 strains remains a lingering question concerning the generality of the conclusions. It appears unlikely that ribosomes or other growth factors partition significantly differently in the MC4100 strain than in the MG1655 strain. Furthermore, based on Fig. S15, it is still unclear to what extent MC4100 exhibits growth-rate fluctuations, as stated in the text, rather than primarily size fluctuations, as shown in the figure. It is also unclear why such very slow fluctuations would lead to qualitatively different behavior, given that the proposed mechanism appears to be rather fundamental. It would be helpful for the authors to discuss these two points.

We thank the reviewer for revisiting this point. Here, we re-examined the MC4100 data in more detail and found that our original analysis was inaccurate; we now clarify this below along with new supporting analyses.

We agree that there is no a priori reason for ribosome or growth-factor partitioning to differ between MC4100 and MG1655, and our expanded analysis now supports this directly in Fig.S15.

Using the Class-1 promoter of the flagellar cascade in MC4100, which behaves under our conditions as a quasi-constitutive promoter, we find a positive correlation between instantaneous elongation rate and promoter activity that is comparable in magnitude to MG1655 (Fig.15C). We further analyzed publicly available data from two independent studies of strains expressing a constitutive fluorescent protein (new Fig.S18): Tanouchi et al. [44, 48], who tracked MC4100 at 25°C and 37°C, and Wang et al. [33], who tracked MG1655 and B/r strains. In these datasets, we found the same positive coupling between instantaneous elongation rate and expression, consistent with what we observe in MG1655. Together, these results indicate that the short-timescale coupling between growth-factor availability and gene expression that underlies our proposed mechanism is not strain-specific and is present in MC4100 for constitutively expressed and Class-1 activity.

On the nature of MC4100's slow fluctuations: We thank the reviewer for pointing out that Fig. S15 did not distinguish growth-rate from size fluctuations. We have now computed the autocorrelation function of elongation rate for both strains and added it to Fig. S15. This analysis shows that MC4100's characteristic oscillation is present in cell size but is absent from the elongation-rate autocorrelation. We have revised the text accordingly to state that MC4100 displays long-timescale oscillations in cell size, rather than describing this as a growth-rate phenomenon.

On why MC4100 does not show coupling between elongation rate and flagellar Class-2 activity despite this coupling being present at Class-1: In MC4100, the positive correlation between elongation rate and promoter activity, comparable to MG1655 at Class-1, is markedly attenuated at Class-2. Since both promoters are measured from the same cells and time series, this rules out our first assumption, a generic masking effect, and instead localizes the discrepancy to the Class-1-to-Class-2 step of the flagellar cascade, the pulse-generating switch we and others have described previously (Sassi et al., 2020, [24]). We do not have data to determine the molecular basis of this attenuation and present it as an open question.

(2) It is unclear what fraction of the total proteome mVenus represents in different measurements. Adding this information would strengthen the conclusions.

We agree that a direct proteomic quantification (e.g., Coomassie staining or mass spectrometry) would be the most direct way to determine the fraction of the proteome occupied by mVenus. However, we are no longer in a position to carry out such experiments.

As in our original response, our elongation-rate reductions (1.3-9.3% across our promoter series; see Table S3) remain far smaller than the 67% reduction associated with ~27% proteome occupancy reported by Scott et al. [6], making it unlikely that mVenus approaches such an extreme fraction in our system.

Now we used a validated quantitative model relating relative growth-rate reduction to unnecessary-protein fraction, built on the same ribosome-allocation theory as Scott et al. and empirically calibrated specifically for a GFP-family fluorescent protein (Bienick et al., 2014, PLoS ONE [59]). This model predicts μ/μ_max = 1 - b·ɸ_U, with b = 2.33 µg dry cell weight (DCW) per µg protein determined for eGFP across multiple growth media. Applying this relationship to our own elongation-rate data, using the growth rate of our non-expressing WT strain as μ_max, we estimate that mVenus constitutes approximately 0.6-4.0% of dry cell weight across our promoter series, reaching ~4.0% in our strongest-expressing strain, P5.

While this remains a model-based estimate rather than a direct proteomic measurement and involves some extrapolation across growth media and strain background relative to the original Bienick et al. study, both independent approaches converge on the same conclusion: mVenus occupies a modest fraction of the proteome in our experiments, well below the f_U = 14.4% upper value explored in our simulations. This supports our original framing of f_U = 14.4% as a conservative exploratory upper bound rather than an underestimate of experimental burden, and we have added this quantitative estimate (Table S3) to the revised manuscript to strengthen this point, as suggested.

eLife Assessment

This valuable study examines how the rodent prelimbic cortex represents learned and generalized threat over time and identifies distinct stable and dynamic neuronal populations that contribute to these representations. The evidence is convincing, supported by longitudinal calcium imaging, appropriate control groups, and sophisticated analyses showing that the relevant neural signals cannot be explained simply by freezing behavior. The work provides a conceptual framework for understanding how stable threat-related representations supporting memory generalization and discrimination can be maintained despite ongoing changes in neuronal ensemble composition.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. We appreciate the care with which the authors have addressed the remaining concerns. The additional analyses and the revisions to the framing and interpretation have strengthened the manuscript and clarified several of the issues raised during the previous round of review. In particular, the added analyses in Figure 4 and the more precise treatment of repeated retrieval, learned threat value, and the relationship between neural activity and freezing have improved the paper substantially.]

Summary:

The authors combine discriminative auditory fear conditioning with longitudinal in vivo calcium imaging to ask how prelimbic (PL) representations of learned and generalized threat evolve across recent and remote memory time points. Using two different CS+ frequencies and a no-shock control group, they report that PL population activity tracks graded behavioral generalization, that population similarity is highest for tones eliciting strong threat responding, and that distinct subnetworks can be identified that appear to encode tone-specific sensory features versus learned threat-related response structure.

To my knowledge, this may be the first study to comprehensively examine neural encoding of fear generalization in prelimbic cortex (PL). The manuscript is ambitious and technically interesting, and several aspects are potentially important. In particular, the suggestion that neurons showing graded, learning-related response patterns become selectively stabilized over time is intriguing. The inclusion of two CS+ training conditions and a no-shock control also strengthens the case that at least some of the reported effects are related to associative learning rather than simple sensory differences.

Reviewer #3 (Public review):

Summary:

Normandin et al. explore the coding of stimuli predicting an aversive event in the prelimbic cortex. Stimuli could either be explicitly paired, explicitly unpaired, or novel but with an inferred association with the aversive event (generalization). Long-term tracking of GCaMP positive neurons allowed them to examine how coding evolves out to a month following training. In general, they found two types of ensemble codes. One was ensembles coding for each stimulus independently, but with enhanced responding to the one eliciting a freezing response. The other was ensembles that responded to all stimuli in proportion to their similarity to the stimulus paired with the aversive event, either increasing or decreasing their activation with the degree of freezing elicited by a stimulus. Importantly, this second set of ensembles was more stable across days, potentially providing a memory trace.

Strengths:

(1) The authors track ensembles in prelimbic cortex over long time scales, providing valuable information on the consolidation of neural codes.

(2) Neural coding of generalization is examined, which is under examined in the field.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors combine discriminative auditory fear conditioning with longitudinal in vivo calcium imaging to ask how prelimbic (PL) representations of learned and generalized threat evolve across recent and remote memory time points. Using two different CS+ frequencies and a noshock control group, they report that PL population activity tracks graded behavioral generalization, that population similarity is highest for tones eliciting strong threat responding, and that distinct subnetworks can be identified that appear to encode tone-specific sensory features versus learned threat-related response structure.

To my knowledge, this may be the first study to comprehensively examine neural encoding of fear generalization in prelimbic cortex (PL). The manuscript is ambitious and technically interesting, and several aspects are potentially important. In particular, the suggestion that neurons showing graded, learning-related response patterns become selectively stabilized over time is intriguing. The inclusion of two CS+ training conditions and a no-shock control also strengthens the case that at least some of the reported effects are related to associative learning rather than simple sensory differences. However, in its current form, the manuscript does not yet fully support the strength of the conceptual claims. Several issues limit confidence in the interpretation, including the possibility that repeated testing itself contributes to changes across days, uncertainty about the relationship between neural activity and freezing behavior, limited quantitative documentation of longitudinal cell registration, and a number of problems in figure clarity and statistical framing. Overall, the study contains promising observations, but the claims should be narrowed, and several analyses or controls would be needed to fully support the proposed framework.

Comments on revised version.

The authors have addressed my previous concerns well, and the revised manuscript is substantially improved. In particular, the additional analyses strengthen the conclusion that prelimbic cortical activity reflects learned threat value rather than simply freezing behavior, while the revised framing and additional controls clarify the interpretation of the longitudinal neural dynamics. This paper represents an important contribution to our understanding of the neural mechanisms supporting aversive learning, memory, and generalization.

We thank Reviewer 1 for his/her constructive comments, which significantly contributed to strengthen our conclusions.

In response to the reviewer’s recommendations, we added two new analyses to Fig. 4, presented in Fig. 4c–g.

Reviewer #2 (Public review):

The authors have substantially revised the paper in response to the original review, which is greatly appreciated. It is clear that it will eventually make a nice contribution to the literature. This being said, the following points are somewhere between major and minor in term of their implications for interpretation of the study results. If they were to be addressed, the paper would be again improved.

We thank Reviewer 2 for the careful second review, which helped us sharpen our arguments and improve the manuscript. The reviewer’s additional comments prompted us to refine the scope and precision of several interpretations. Accordingly, we have removed or clarified potentially confusing language, reframed the longitudinal findings in terms of repeated retrieval rather than the passage of time, and explicitly acknowledged the limitations of relying exclusively on freezing as a behavioral measure. We now also recognize repeated nonreinforced testing as the most direct explanation for the sharpening of the generalization gradients and the responses of newly recruited neurons, while clarifying below how we view this additional learning as contributing to memory updating. We believe these revisions have substantially improved the manuscript, and we are grateful for the reviewer’s thoughtful and detailed feedback.

There are a few remnants of the past language that are not helpful for the interpretation of the study results: 1) "Specifically, the observed population gradients could emerge either from the pooled activity of frequency-selective neurons that respond to individual tones or from neuronal subpopulations that integrate information across tones to encode their learned threat-value."; and 2) "Together, these findings suggest that the PL integrates sensory similarity with learned threat value to generate stable representations that support adaptive generalization and discrimination." Neither of these statement follows what has been shown in the study, even with inclusion of the results from the GLM analysis (see point 4 below).

We directly address this point in response to the reviewer’s point 4

(1) This paragraph in the Discussion is difficult to follow: "Generalization has traditionally been explained by perceptual similarity (Shepard, 1987), whereby stimuli resembling a conditioned cue recruit overlapping sensory representations and evoke similar behavioral responses (Corches et al., 2019; Grosso et al., 2018). Although perceptual similarity clearly influences the extent of generalization, accumulating evidence indicates that it cannot fully account for generalized responding (Verra et al., 2026). More recent frameworks propose that associative learning assigns learned value to novel stimuli by integrating their sensory similarity with previous experience, allowing behavior to scale according to predicted biological significance (Verra et al., 2026; Zaman et al., 2023). Our findings provide a neural framework consistent with these ideas. Sensory similarity promoted consistent neuronal population responses across tones, whereas associative learning organized these responses into graded representations that tracked learned threat value across the stimulus continuum. Thus, sensory similarity appears to define the neuronal substrate upon which associative learning constructs value-based representations that support graded behavioral generalization."

While the revisions have removed the many unnecessary references to inference and integration, this paragraph seems like it is adhering to the original idea of how the authors wished to present their work. If the authors wished to talk about something more than perceptual similarity in the context of generalization, they should have used a task that lends itself to a more-than-perceptual-similarity explanation. Again, the inclusion of the GLM analysis is suggestive for some of what the authors wish to say, but doesn't justify the statements that: "Sensory similarity promoted consistent neuronal population responses across tones, whereas associative learning organized these responses into graded representations that tracked learned threat value across the stimulus continuum." In short, the analysis does not substitute for the design that could have and should have been used to assess learned threat value independently of sensory similarity.

We thank the reviewer for this comment, which helped us identify ambiguity in our terminology. By “learned threat value,” we did not intend to imply that the PL independently infers or computes the value of each novel tone, separate from perceptual similarity. Rather, we used this term to denote the associative significance acquired by the CS+ and CS− during conditioning. Novel cues may then be evaluated according to their perceptual similarity to these learned associations. We have now defined “learned threat value” when it first appears in the manuscript.

Furthermore, we agree that perceptual similarity can account for the graded generalization of responses from the CS+ to neighboring frequencies. We therefore do not consider learned associations and perceptual similarity to be competing explanations. Instead, conditioning determines which stimulus anchors the gradient and its direction according to their acquired “threat value”, whereas perceptual similarity governs how the response extends across intermediate frequencies. This interpretation is supported by our reversed conditioning design: the same frequency continuum produced opposite neural gradients depending on whether 3 or 15 kHz served as the CS+, and no gradients emerged in control animals exposed to the same tones without conditioning. Thus, the physical relationships among the tones shape the graded response, but mnemonic experience determines its organization along the frequency continuum.

The GLM analysis was not intended to demonstrate threat value independently of sensory similarity. Rather, it showed that the learning-dependent gradient remained after accounting for freezing and therefore could not be explained solely by this behavioral response (we address the point of other potential fear responses below).

“Generalization has traditionally been explained in terms of perceptual similarity (Shepard, 1987): stimuli resembling a conditioned cue recruit overlapping sensory representations and therefore evoke similar behavioral responses (Corches et al., 2019; Grosso et al., 2018). More recent frameworks propose that responses to novel stimuli depend not only on sensory similarity but also on mnemonic representations of learned threat value, allowing behavior to scale with the predicted significance of each stimulus (Verra et al., 2026; Zaman et al., 2023). This mnemonic contribution should be especially important when generalization is assessed long after conditioning because responding to a novel cue requires retrieval of the associations formed during learning. Our design did not manipulate sensory similarity and learned threat value independently. However, the reversed conditioning procedure dissociated them in one respect: depending on whether 3 or 15 kHz served as the CS+, the neural gradients ran in opposite directions along the same frequency continuum, with each anchored to the threat-associated tone. A gradient determined by spectral features alone would have run in the same direction in both groups. Thus, the learned associations and their mnemonic representations must have determined the anchor and direction of the neural gradient. By contrast, the contribution of sensory similarity is inferred rather than directly demonstrated: intermediate tones were represented in an order that followed their spectral distance from the CS+. Because discriminative conditioning tends to narrow generalization gradients (Dunsmoor & LaBar, 2013; Herzog et al., 2021; Jenkins & Harrison, 1960; Lommen et al., 2017), tracking neural representations over 30 days allowed us to examine how PL populations evolved as behavioral discrimination became progressively more precise during repeated retrieval. Whereas stable neuronal populations retained consistent response profiles across retrieval sessions, neurons recruited after conditioning exhibited changes that paralleled the behavioral sharpening. These results suggest that memory, new learning, and sensory similarity interact to shape generalization gradients.”

(2) The next paragraph in the Discussion is also confusing. "Such reorganization has been proposed to provide flexibility by allowing new information to be incorporated into existing cortical representations while preserving stable behavioral performance (Mau et al., 2020; Zaki & Cai, 2024). Several mechanisms could contribute to this turnover, including systems consolidation, retrieval-induced reconsolidation or memory updating, and repeated nonreinforced stimulus exposure (Lacagnina et al., 2019; Mau et al., 2020; Sangha, 2015; Zaki & Cai, 2024). Although our experiments cannot distinguish between the first two possibilities, the behavioral data argue against extinction as the primary explanation. Extinction is generally associated with the formation of new CS+-safety associations (Bouton et al., 2021), whereas discrimination ratios increased across retrieval sessions, indicating that animals progressively improved their discrimination between threat-associated and safe stimuli rather than acquiring generalized safety responses. This pattern is consistent with previous work showing that discrimination learning sharpens stimulus representations and narrows behavioral generalization gradients (Dunsmoor & LaBar, 2013; Herzog et al., 2021; Jenkins & Harrison, 1960; Lommen et al., 2017). Importantly, turnover was not uniform across the population. Graded neurons retained remarkably consistent response profiles across retrieval sessions, and their activity remained more strongly associated with learned threat value than with freezing behavior. These observations indicate that stable components of the population code can coexist with extensive reorganization of surrounding neuronal ensembles."

The issue with repeated testing is not caused by extinction per se. The issue is that nonreinforcement across the repeated testing should differentially affect the CS+ and CS-. Specifically, it should extinguish responding to the CS- stimulus at a rate that matches its distance from the CS+, thereby sharpening the CS+ versus CS- discrimination in precisely the ways that have been observed. Ergo, the repeated testing is a problem for inferences that might be drawn about the way that generalization gradients change with; and is a problem for statements regarding "dynamic reorganization of cortical activity patterns over time." There is nothing in the study that allows one to comment on the reorganization of cortical activity patterns over time. The reorganization can and should be attributed to the repeated testing, which is confounded with time. Nonetheless, the reorganization must be due to the repeated testing and NOT time as the present findings are inconsistent with the well-documented broadening of generalization gradients with time.

We agree with the reviewer that discrimination between the CS− and CS+ sharpened across retrieval sessions and that repeated testing may have contributed to this effect. Our discussion of extinction was included specifically to address a concern previously raised by Reviewer 1 and to clarify that the observed sharpening did not reflect a uniform reduction in conditioned responding. We now only left this explanation in the results section.

We also agree that later retrieval sessions are not passive readouts of the original memory. Repeated presentation can provide new opportunities for learning, update reactivated memory traces, and initiate reconsolidation. The intermediate tones illustrate this point particularly well: they are novel during the first retrieval session but become familiar through subsequent exposure, and their representations may therefore change across sessions. Thus, new learning, memory updating, and reconsolidation are not mutually exclusive explanations but interacting processes engaged by repeated retrieval. We have revised the Discussion to acknowledge these contributions more explicitly.

We also agree that our use of phrases such as “over time” was imprecise. We have replaced this language with “across retrieval sessions” to avoid implying that the passage of time alone produced ensemble turnover.

However, we respectfully disagree that cortical reorganization cannot be evaluated across repeated retrieval sessions or that repeated testing alone necessarily accounts for all the observed changes. Multiple studies have documented turnover within cortical ensembles following learning (Lacagnina et al., 2019; Mau et al., 2020; Sangha, 2015; Zaki & Cai, 2024). Importantly, we observed ensemble turnover by test day 1, before repeated testing could have exerted a cumulative effect, and similar early turnover has been reported by other laboratories (Kitamura et al., 2017; DeNardo et al., 2019). These previous studies have also interpreted changes in ensemble composition between conditioning and subsequent retrieval sessions, including remote retrieval, as evidence of cortical reorganization. Our paradigm differs from these studies because we introduced novel tones to examine how representations of the original CS+/CS− associations interact with representations of perceptually similar cues.

In summary, we agree with the reviewer that repeated testing may generate additional learning that contributes to the sharpening of behavioral generalization gradients and the responses of newly recruited neurons. However, we view this learning as inseparable from memory updating and reconsolidation, because information acquired during retrieval must be incorporated into existing memory representations to persist across sessions.

“The ensemble turnover observed here is consistent with previous studies demonstrating dynamic reorganization of cortical activity patterns across temporally separated retrieval sessions (DeNardo et al., 2019; Gallego et al., 2020; Kitamura et al., 2017; Tome et al., 2024). Such reorganization has been proposed to provide flexibility by allowing new information to be incorporated into existing cortical representations while preserving stable behavioral performance (Mau et al., 2020; Zaki & Cai, 2024). Several processes could contribute to this turnover, including additional learning during repeated nonreinforced testing, memory updating, and reconsolidation (Lacagnina et al., 2019; Mau et al., 2020; Sangha, 2015; Zaki & Cai, 2024). In our experiments, turnover was already evident at the first retrieval session, before repeated testing could have exerted a cumulative effect, indicating that this reorganization emerges early after learning. Nevertheless, repeated testing provides a plausible explanation for changes during subsequent sessions. Each retrieval session reactivated the original CS+/CS− associations while presenting the conditioned and intermediate tones without reinforcement, thereby creating opportunities for additional discrimination learning. These experiences may have progressively sharpened differentiation between the CS+ and CS-, modifying the retrieved memory representations and changing which neurons participated in representing the refined associations. Although our data do not establish a mechanistic link between neuronal turnover and additional learning, they raise the possibility that dynamic ensemble membership provides the flexibility needed to incorporate new information.”

(3) In the next paragraph, the authors state: "At the same time, narrower generalization gradients and improved discrimination across retrieval sessions suggests ongoing memory updating. These observations are consistent with contemporary theories proposing that systems consolidation and retrieval-dependent updating are complementary processes through which memories continue to evolve after learning (Mau et al., 2020; Tome et al., 2024; Zaki & Cai, 2024)."

In general, I'm not sure why one would invoke systems consolidation or retrieval-induced reconsolidation as an explanation for any of the present findings: they are not explanations of much at all. In this specific text, the authors seem to be implying an updating process that occurs independently of what is learned across the repeated sessions of testing. Why? The changes that occur in the behaviour and neuronal representations are perfectly explicable in terms of additional learning that occurs - of the sort that I hope to have made clear in my previous comment. Why invoke more than what is needed to explain the observed pattern of results?

We appreciate the reviewer’s clarification. As discussed in our response to the preceding comment, we agree that repeated nonreinforced testing provided additional learning opportunities and offers the most direct explanation for the progressive sharpening of behavioral discrimination and neuronal responses. We recognize that our original wording could have been interpreted as proposing memory updating as a process occurring independently of learning during the test sessions. This was not our intention. By “memory updating,” we meant that new information acquired during repeated retrieval modified the existing representations of the CS+ and CS−, allowing these stimuli to become more clearly differentiated. Thus, the additional learning that occurs through repeated testing provides the experience through which the original associations are refined.

We agree that systems consolidation and retrieval-induced reconsolidation are not required as direct explanations for the observed sharpening and that our design cannot isolate their contributions. However, ensemble turnover was evident by day 1, before repeated testing could have exerted cumulative effects, indicating that repeated testing cannot fully explain the turnover. We view the additional learning acquired during subsequent retrieval sessions as refining the represented values of the CS+ and CS− and, if these changes persist, as requiring incorporation into existing memory representations through updating and reconsolidation. These processes therefore complement, rather than compete with, additional learning. The revised Discussion distinguishes repeated testing as the most direct explanation for the sharpening of discrimination from the broader memory processes that may accompany this learning and contribute to cortical ensemble reorganization.

“In summary, PL population responses formed generalization gradients that paralleled behavioral generalization and were primarily organized according to tone-learned threat value. The overlap among responses to conditioned and novel tones was consistent with their perceptual similarity, whereas repeated nonreinforced testing was accompanied by progressive sharpening of both behavioral discrimination and the response gradients expressed by neurons recruited after conditioning. Together, these findings provide a potential neural framework through which stored threat associations may guide the evaluation of perceptually similar cues.”

“The coexistence of these stable neurons with dynamic ensembles may allow repeated retrieval to refine a memory while preserving core features of its original representation (Mau et al., 2020; Tome et al., 2024; Zaki & Cai, 2024). Determining whether these stable graded neurons are causally required for memory storage or retrieval—and whether they constitute a persistent cortical memory trace—will require longitudinal imaging combined with selective manipulation of this population.”

(4) Re the GLM analysis - The authors write that: "the fact that the GLM analysis indicates that these neurons reflect learned threat value more than freezing behavior, suggests that they encode an abstract property of the learned stimulus rather than simply mirroring behavioral output."

This is fine if freezing fully indexes the state of conditioned fear and there are no other behaviours in which animals express their fear. If, however, fear is expressed in a range of other behaviours that are likely coordinated by the PL (e.g., startle, vigilance, scanning, orienting to source of danger), this interpretation of the GLM analysis is unwarranted. This is an important point and would be worth noting somewhere in the paragraph where the statement appears.

We agree with the reviewer. Our GLM demonstrates that the graded neuronal responses cannot be explained by freezing behavior alone, but it does not exclude contributions from other unmeasured manifestations of conditioned fear, including vigilance, scanning, orienting, startle, or physiological responses. We have therefore removed the claim that these neurons primarily encode threat value and revised the Discussion to acknowledge this limitation explicitly.

“Freezing, however, does not exhaust the conditioned defensive state, and we cannot rule out contributions from unmeasured behavioral or physiological correlates of fear, including vigilance, scanning, orienting, startle, and changes in autonomic state. Our findings are therefore consistent with PL neurons representing the learned significance of the stimuli, but they do not establish that this representation is independent of all fear-related behavioral and physiological states.”

Reviewer #3 (Public review):

Summary:

Normandin et al. explore the coding of stimuli predicting an aversive event in the prelimbic cortex. Stimuli could either be explicitly paired, explicitly unpaired, or novel but with an inferred association with the aversive event (generalization). Long-term tracking of GCaMP positive neurons allowed them to examine how coding evolves out to a month following training. In general, they found two types of ensemble codes. One was ensembles coding for each stimulus independently, but with enhanced responding to the one eliciting a freezing response. The other was ensembles that responded to all stimuli in proportion to their similarity to the stimulus paired with the aversive event, either increasing or decreasing their activation with the degree of freezing elicited by a stimulus. Importantly, this second set of ensembles was more stable across days, potentially providing a memory trace.

Strengths:

(1) The authors track ensembles in prelimbic cortex over long time scales, providing valuable information on the consolidation of neural codes.

(2) Neural coding of generalization is examined, which is under examined in the field.

Comments on revised version.

The authors have convincingly and thoroughly addressed my concerns. I have no further issues regarding this study.

We thank reviewer 3 for his thoughtful and constructive comments and the suggestion to use the GLM which greatly improved the interpretation of our data.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

One small point is that the authors could report the beta coefficients for the tone and freezing predictors from the GLM analysis shown in Figure 4. Providing these values would make it easier to directly compare the relative contributions of tone-related and freezing-related activity to the model.

We now include this analysis in Figure 4c and 4g

eLife Assessment

This study presents a valuable human organoid platform for investigating neuron-immune interactions in Alzheimer's disease and modeling the interplay between innate and adaptive immunity in the context of amyloid pathology. The system has the potential to advance the field by enabling the study of human-specific neuroimmune interactions that is difficult to recapitulate in rodent models. The evidence on the microglia-T cell crosstalk are convincing. The study will interest researchers in neuroimmunology and Alzheimer's disease.

Reviewer #2 (Public review):

Summary:

In this study, the authors developed a human forebrain organoid model that incorporates both iPSC-derived microglia and CD8⁺ T cells, allowing them to recreate and investigate multicellular aspects of AD pathology in a human-relevant system.

Their findings show that microglia help clear amyloid-β deposits, but they also promote inflammatory responses. Activated microglia recruit CD8⁺ T cells by releasing the chemokines CCL4, CCL5, and CXCL10, which signal through the receptors CCR1/CCR5 and CXCR3. Pharmacological inhibition of CCR5 or CXCR3 prevents T-cell recruitment and alters autophagy pathways in a microglia-dependent manner.

Strengths:

The manuscript has several strengths, including its innovative multicellular organoid model, the combination of complementary experimental approaches, and the identification of potentially relevant immune signaling pathways.

Comment on the revised version.

Overall, the revised manuscript is considerably improved, and the major conceptual concerns raised in the initial review have been adequately addressed.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

A growing body of evidence indicates that Alzheimer's disease is not simply a disease of neurons accumulating toxic protein aggregates, but one in which the immune system, both its resident brain component and its circulating peripheral arm, plays an active and sustained role. Understanding how these two immune compartments interact with one another and with diseased neural tissue has been hampered by the fact that the mouse immune system differs fundamentally from the human one in ways likely to matter for disease progression. The authors set out to address this gap by building a modular laboratory model that brings together three human cell types in a three-dimensional setting: brain organoids derived from human stem cells to provide a neural substrate, stem cell-derived brain immune cells (microglia) to represent the resident immune compartment, and circulating immune cells (CD8-positive T cells) harvested from human blood to represent the peripheral adaptive immune response. By exposing this tri-cellular system to a toxic form of amyloid protein, the hallmark aggregating molecule of Alzheimer's disease, the authors aimed to dissect, step by step, how microglia respond to amyloid stress, what inflammatory signals they release as a consequence, and whether those signals are sufficient to attract T cells into the neural environment. They further aimed to test whether blocking the molecular receptors that guide T cell movement could interrupt this process, with the broader goal of positioning the platform as a tool for human-relevant drug screening.

Strengths

The conceptual architecture of the platform is one of its clearest strengths. The decision to add immune components in a stepwise, modular fashion, first characterising the neural response to amyloid, then adding microglia, then adding T cells, makes it possible to attribute observed changes to specific cellular contributions in a way that a more complex all-at-once model would not allow. This staged design is well thought-through, and its logic is clearly communicated. The combination of single-cell transcriptional profiling, calcium imaging for real-time functional readouts, transwell migration assays, and protein secretion measurements gives the study a genuinely multi-modal character that goes beyond what purely transcriptomic or purely imaging-based approaches can offer. The observation that T cells failed to migrate toward amyloid-treated organoids in the absence of microglia is a clean and conceptually important result, clearly supporting the idea that the resident immune response acts as an intermediary between amyloid pathology and the recruitment of peripheral immune cells. The identification of specific chemokine receptor pathways mediating T cell movement and the demonstration that pharmacological blockade of those receptors reduces migration and provide a degree of mechanistic resolution useful for thinking about future therapeutic strategies.

Weaknesses

Despite these strengths, several aspects of the work as presented substantially limit the confidence one can place in its conclusions.

The most consequential issue concerns the origin of the cells used in the model. The three cellular components: the brain organoids, the microglia, and the T cells are derived from genetically unrelated individuals. The T cells, in particular, come from healthy blood donors unrelated to the stem cell lines used to generate the neural tissue. This means the immune cells and the tissue they are interacting with carry different molecular identity markers (the proteins that the immune system uses to distinguish self from non-self). In this setting, any T cell activation or directed movement could reflect a generic rejection-like response to foreign tissue rather than a disease-relevant, chemokine-directed recruitment process. This is not a subtle concern: it represents a fundamental ambiguity at the heart of the model's central finding, and it is not acknowledged anywhere in the manuscript. For the transwell migration data to be interpretable as a model of Alzheimer's disease rather than of immune incompatibility, the authors would need to demonstrate that migration is driven by the specific chemokine environment and not by the genetic mismatch between cells, for example, using cells from the same donor or from matched donors, or by showing that blocking identity-marker recognition does not alter migration.

A related concern is that the T cells used are from healthy individuals, whereas T cells from people with Alzheimer's disease are known to differ in their activation state, surface receptor expression, and functional behaviour. The platform cannot yet claim to model the specific T cell biology of Alzheimer's disease until disease-relevant T cells are incorporated.

Beyond this foundational issue, the study frequently describes findings in causal terms that the experimental design does not support. The resident immune cells are said to "drive" T cell recruitment and "establish" a feedback loop. These are strong mechanistic claims. The evidence presented indicates that when microglia are present, more T cells migrate, and that blocking T cells receptors reduces migration. What is missing is direct evidence that the specific molecules measured, particularly the chemokines CCL4 and CCL5, are the agents responsible, as opposed to other signals also present in the conditioned environment. No experiment directly neutralises these chemokines to test whether their removal is sufficient to abolish T cell recruitment. Without such an experiment, the receptor-blocking data show only that the receptors matter, not that the measured ligands are the ones activating those receptors.

The abstract describes one particular molecule, CXCL10, as a contributor to T cell recruitment, but the data in the paper itself show no significant change in CXCL10 levels between conditions. This discrepancy between the abstract and the results is misleading to readers who may not read the figures in detail.

The single-cell sequencing data, which form the basis for claims about changes in cell populations following amyloid treatment or microglia addition, are presented without validation of the cell type labels against established reference datasets from human brain tissue. The proportional shifts in cell populations between conditions (Figures 1H and 3E) are described as significant findings but are shown without any statistical test appropriate for this type of compositional data. Comparisons of cell-type proportions derived from single-cell sequencing require specialised statistical approaches that account for the interdependence of proportions and the variability between samples; standard tests are not appropriate here, and none are applied.

There is also an unresolved inconsistency in the age at which the organoids were analysed by single-cell sequencing: the text states day 90, while the figure legend states day 60, and the methods section contains a passage describing experimental conditions (including a cholesterol treatment and a drug called semaglutide) that are entirely unrelated to this study and appear to have been copied from a different manuscript. These issues raise concerns about the rigour of the manuscript preparation and should be corrected.

Finally, the sample sizes underpinning several key conclusions are small (typically three to four organoids per group), particularly for the protein-secretion measurements used to identify the inflammatory signals responsible for T cell recruitment. While organoid studies are inherently limited in scale, the strength of the mechanistic claims made here would benefit from larger sample size or independent experimental replication.

Conclusion:

The authors have built a platform that is conceptually well-conceived and generates data consistent with a role for microglia in bridging amyloid pathology and T cell recruitment. In that sense, they have made meaningful progress toward their stated aims. However, the platform, as described, cannot yet deliver the human-specific mechanistic insight it claims to provide, primarily because the non-autologous configuration of the model introduces an uncontrolled variable that confounds the interpretation of the immune interaction data. The claim to have provided "the first human-specific mechanistic demonstration" of microglial activation as a bridge between amyloid pathology and adaptive immune recruitment is not supported by the evidence presented. The data are consistent with this interpretation but do not establish it.

The general approach, building increasingly complex human neural-immune models by adding components in a controlled, stepwise manner, is a valuable direction for the field and one that other groups working on neuroinflammation will find useful to consider. The combination of live calcium imaging and transcriptional profiling in the same experimental system is a practical contribution that demonstrates the kind of multi-modal readout this class of model can support. If the autologous confound is resolved in future iterations and if the mechanistic claims are grounded in more direct experimental evidence, this type of platform could become a genuinely useful tool for investigating human neuroimmune biology and for screening candidate therapeutic compounds in a human-relevant context. As currently presented, however, readers and researchers considering adopting this approach should be aware that the immune interaction data may reflect genetic mismatches between cell sources rather than disease-specific biology, and that the causal conclusions drawn from the chemokine and migration data go beyond what the experiments can support.

Reviewer #2 (Public review):

Summary:

In this study, the authors developed a human forebrain organoid model incorporating both iPSC-derived microglia and CD8⁺ T cells, enabling them to recreate and investigate multicellular aspects of AD pathology in a human-relevant system.

Their findings show that microglia help clear amyloid-β deposits, but they also promote inflammatory responses. Activated microglia recruit CD8⁺ T cells by releasing the chemokines CCL4, CCL5, and CXCL10, which signal through the receptors CCR1/CCR5 and CXCR3. Pharmacological inhibition of CCR5 or CXCR3 prevents T-cell recruitment and alters autophagy pathways in a microglia-dependent manner.

Strengths:

The study presents a versatile human organoid platform for investigating neuron-immune interactions in Alzheimer's disease. It highlights the critical role of microglia-driven recruitment of CD8⁺ T cells in sustaining neuroinflammation and identifies CCR5 and CXCR3 signaling pathways as promising therapeutic targets for neuroinflammatory conditions.

This study is interesting and presents novel findings supported by state-of-the-art approaches, including single-cell RNA sequencing, a three-dimensional cerebral organoid model, and co-culture systems involving two distinct immune cell populations.

Weaknesses:

Several aspects of the study require clarification and further improvement. For example:

(1) Figure 1H is missing statistical analyses.

(2) The scRNA-seq analysis shows a reduction in the proportion of cells occupying transcriptional states associated with later pseudotime values, which the authors interpret as evidence that Aβ treatment inhibits neuronal maturation. However, the data presented do not appear sufficient to support this conclusion. An alternative explanation is that Aβ preferentially affects the survival of more mature neuronal populations, leading to their depletion, consequently, an apparent enrichment of cells at earlier pseudotime states. Therefore, the observed pseudotime shift does not necessarily demonstrate impaired maturation per se. The authors should revise the interpretation of these results in the first paragraph and either provide additional evidence supporting a maturation defect or discuss alternative explanations such as selective loss of mature neurons.

(3) A similar concern applies to the scRNA-seq data presented in Figure 3. The authors interpret the shift toward later pseudotime states in the presence of microglia as evidence of enhanced neuronal maturation. However, the data do not exclude alternative explanations. For instance, microglia may preferentially promote the survival of more mature neuronal populations or protect them from cell death, thereby increasing their relative abundance in the dataset. Consequently, the observed pseudotime distribution cannot be taken as direct evidence of enhanced maturation. The authors should revise their interpretation accordingly and discuss the possibility that the observed effect reflects differential survival rather than accelerated neuronal maturation.

(4) In Figures 4A-E, the authors should report the levels of the secreted proteins in pg/mL instead of relative values, as this would better reflect the actual amounts produced. In Figure 4H, the inhibitor-treated control T-cell samples should be included. Furthermore, it should be explicitly stated that the inhibitor-treated data points currently shown refer to T cells cultured in the presence of myeloid Aβ.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Addressing the allogeneic confound

To determine whether observed T cell migration reflects chemokine-driven recruitment rather than allogeneic recognition, the authors should perform one or more of the following: (a) repeat transwell migration assays using HLA-matched donors for T cells and iPSC lines; (b) include a blocking condition using anti-HLA class I antibody to suppress allogeneic recognition and test whether migration is reduced; (c) compare migration toward conditioned media alone (without cells) versus co-culture conditions to establish whether secreted factors are sufficient to drive migration independently of direct cell contact. If HLA-matched material is not currently available, the authors could, at a minimum, use conditioned media transfer experiments to dissociate chemokine-mediated from contact-mediated effects.

We agree this is an important limitation. We have not performed HLA-matched migration assays, anti-HLA class I blockade, or conditioned-media-only migration experiments. We note that in our transwell assay design (Fig. 4G–H), T cells are seeded in the upper chamber and organoids in the lower chamber, separated by a porous membrane; while this precludes direct T cell–organoid cell contact, live organoid/microglial cells are present throughout the assay rather than their conditioned medium alone, so we have not directly tested part (c) as the reviewer describes it.

We would also note that the CD8⁺ T cells used in this assay were derived from a single healthy donor, while the organoids and iMGLs were derived from a separate iPSC line (DYR0100); the same T cell donor and the same organoid/microglial line were used across all conditions (CTR, Aβ42, Aβ42+iMGL). The T cell–organoid pairing is therefore allogeneic, but identical in every condition. Any contribution of allogeneic recognition to baseline migration should, in principle, be present equally across conditions and would not by itself account for the increased migration specifically toward the Aβ42 and Aβ42+iMGL conditions relative to CTR.

(2) Direct validation of CCL5 as the responsible ligand

To substantiate the claim that microglia-derived CCL5 is responsible for T cell recruitment, a CCL5-neutralising antibody should be added to the transwell assay. Similarly, a CCL4-neutralising antibody should be tested independently. This would allow the authors to attribute the migration effect to specific molecules rather than to the overall conditioned environment and would substantially strengthen the mechanistic interpretation.

We appreciate this comment and agree that ligand-neutralization experiments would substantially strengthen the mechanistic interpretation. We have not performed these experiments in the current study but will consider including CCL5- and CCL4-neutralizing antibody conditions in future follow-up work. We have revised the Results/Discussion to make clear that our receptor-blockade data (Fig. 4H) establish that CCR5/CXCR3/CCR1 signaling on T cells is necessary for recruitment, but do not by themselves attribute this effect to CCL4 or CCL5 specifically, as opposed to other chemokines present in the conditioned environment.

(3) Cell-type annotation validation for single-cell data

The authors should add a supplementary figure showing a dot plot or heatmap of canonical marker gene expression across all annotated clusters, cross-referenced to at least one published human brain atlas or human organoid single-cell reference dataset. Module score analysis using published cell-type gene signatures (e.g., Velmeshev et al. 2019, for neuronal subtypes or established microglial signature sets) would further validate the annotations. The specific software tool and reference dataset used for annotation should be explicitly named in the Methods section.

We thank the reviewer for this suggestion. Canonical marker gene expression supporting our cluster annotations is provided in Supplementary Figure S1 (violin plots of marker genes across annotated clusters.

(4) Statistical testing for cell-type proportion comparisons

Figures 1H and 3E should be reanalysed using a compositional statistical framework. The authors are encouraged to use the propeller method (Phipson et al., Bioinformatics, 2022) or scCODA (Büttner et al., Nature Communications, 2021), both of which are designed for this type of comparison in single-cell data. Individual organoid-level proportion values should be shown as overlaid data points to make biological variability is visible.

We agree and have reanalysed both comparisons with scCODA (Büttner et al., 2021), using cell-type counts aggregated per library (n = 2 per condition). Because scCODA estimates are conditional on a reference population, we specified migrating neurons as reference — the only population with a near-unity fold change (1.19×) and no credible change under any alternative reference. The results are shown in Supplementary Table 1.

We note that scCODA reports posterior inclusion probabilities rather than P values, and have removed P-value notation from all proportion comparisons. Figures 1H and 3E now display composition for each individual library as separate stacked bars, so that between-replicate variability is directly visible.

(5) Functional validation of microglial-promoted neuronal maturation

To support the claim that microglia promote neuronal maturation, at least one functional or morphological measurement attributable specifically to the microglia co-culture condition should be provided. Suggested approaches include: quantification of neurite length or branching complexity by automated image analysis comparing organoid slices with and without microglia; or synaptic puncta density measurements (already used elsewhere in the manuscript) comparing Aβ42 and Aβ42+iMGL conditions.

Thanks a lot for pointing this out. We agree that trajectory inference alone cannot support a claim that microglia promote neuronal maturation, and we regret that we are unable to provide the requested measurement: synaptic puncta quantification in this study was performed only for the CTR and Aβ42 conditions, and the material required to extend it to Aβ42+iMGL is no longer available. We have therefore revised the interpretation rather than defend the original claim.

We now describe the effect as a shift in organoid cell-type composition and transcriptional state toward more differentiated populations, rather than as microglia-driven neuronal maturation. The Results text has been changed from "…indicating that microglia promote neuronal maturation and partially reverse the Aβ42-induced immature state" to:

" Pseudotime analysis showed that microglial co-culture shifted cells toward higher pseudotime values compared with Aβ42 alone (Fig. 3F–G), consistent with a shift in organoid cell-type composition toward more differentiated populations (Fig. 3E) and a partial reversal of the Aβ42-associated skew toward progenitor states.”

(6) Chemokine secretion follow-up after T cell addition

To begin closing the proposed feedback loop, the authors should measure CCL4 and CCL5 levels (and ideally a broader cytokine panel) in conditioned media from the Aβ42+iMGL+T condition and compare them with those from Aβ42+iMGL. If T cells amplify microglial activation (as shown by calcium imaging), one would predict increased chemokine output. Including this measurement would substantially strengthen the feedback loop claim.

We would first clarify the scope of our claim. The feedback loop described in the manuscript operates at the level of cellular activation state: microglia-derived chemokines recruit CD8⁺ T cells (Fig. 4A–E, 4G–H), and recruited CD8⁺ T cells in turn amplify microglial activation (Fig. 4L). Each step is supported by direct measurement, and we do not claim that T cells increase microglial chemokine output or drive a further round of recruitment.

We agree that measuring chemokine secretion after T cell addition would test an important extension of this model — whether T cell-driven amplification of microglial activity translates into increased chemokine output and thus a self-sustaining recruitment cycle. We are unable to perform this experiment within the revision period, as the tri-culture conditioned media were not retained.

We would also note that this measurement is not straightforward in bulk conditioned media. CD8⁺ T cells are themselves major producers of CCL4 and CCL5, releasing preformed CCL5 from cytotoxic granules within hours of activation, so an increase in the Aβ42+iMGL+T condition could not be attributed to microglia. A rigorous test would require cell-type-resolved output — intracellular cytokine staining, single-cell profiling of the tri-culture, or physical separation of the two populations — and we now identify this explicitly as the next step.

(7) Time-course data for the protective-to-pathological transition

The dual functionality narrative requires temporal data to be credible. The authors should consider measuring Aβ clearance, pseudotime distribution, and chemokine secretion at multiple time points after microglial addition (e.g., 6, 24, and 48 hours) to determine whether the protective and inflammatory outputs are sequential or whether they co-occur from the outset.

We agree that a single 48-hour timepoint cannot determine whether protective and inflammatory microglial outputs are sequential or concurrent, and we are unable to add a time course within the revision period.

We have therefore moderated our interpretation. The Discussion previously stated that "microglial activation is not a binary state but a spectrum, where sustained Aβ stress drives the transition from a protective to a pathological, T-cell-recruiting state." This has been revised to: "This duality indicates that microglial activation is not a binary state: within the Aβ42 environment, clearance and neuroprotective functions are detectable alongside inflammatory, T-cell-recruiting outputs at the same timepoint." The temporal claim implied by "transition" has been removed, as our data establish co-occurrence at 48 hours rather than a sequence.

Recommendations for writing and presentation

(8) Abstract correction

CXCL10 must be removed from the mechanistic description of T cell recruitment in the abstract, as Figure 4E shows no significant change in CXCL10. The abstract should also moderate the language around "establishing a feedback loop" to reflect that the loop was observed and partially characterised rather than mechanistically closed.

CXCL10 has been removed from the mechanistic description in the Abstract, as Fig. 4E shows no significant change in its secretion. CXCR3 has been retained, as pharmacological blockade reduced T cell migration (Fig. 4H), but is now presented as a receptor-level finding without an identified ligand. We have also moderated the concluding clause, which now describes a neuroimmune circuit in which recruited T cells amplify microglial activation, rather than stating that a feedback loop is established. The Abstract sentence now reads: Using this platform, we demonstrate that microglia mediate amyloid-β clearance and shift organoid cell composition toward more differentiated states, but also become inflammatory and recruit CD8⁺ T cells through CCL4/CCL5 signaling via CCR1, CCR5, and CXCR3, forming a neuroimmune circuit in which recruited T cells further amplify microglial activation.

(9) Resolve the day 90 / day 60 inconsistency

The discrepancy between "day 90" in the Results text (line 88) and "day 60" in the Figure 1G legend must be corrected throughout the manuscript.

"Day 90" in the Results text (line 88) has been corrected with “day 60”.

(10) Rewrite the scRNA-seq library preparation methods

The methods section (lines 357-360) must be rewritten to describe the actual experimental conditions used in this study. The passage referring to cholesterol-treated and semaglutide-treated organoids on day 30 must be removed entirely.

The methods section has been now revised as: For isolation of iPSC-derived forebrain cells, cells were collected from CTR and Aβ42-treated organoids at day 60, and from Aβ42-treated organoids with and without a 48-hour iMGL co-culture (Aβ42 and Aβ42+iMGL). Two biological replicates were included in each group. Three organoids were pooled within each replicate and washed three times with pre-chilled PBS. Single-cell suspensions were prepared by incubating with 0.5 mg/mL papain for 30 min at 37 °C in a water bath. Suspensions were filtered through a 70 µm cell strainer (BD Falcon, 352350). After centrifugation at 500 g for 5 min, the cell pellet was resuspended in PBS + 0.01% BSA.

(11) Report the number of organoids per scRNA-seq replicate

The Methods section should explicitly state how many organoids were pooled per biological replicate for each single-cell sequencing experiment and how many replicates were included per condition.

The Methods section has been revised to state explicitly the number of organoids pooled per biological replicate and the number of replicates per condition for each single-cell experiment, as described in our response to comment (10). Two biological replicates were included per condition, each prepared from 3 pooled organoids.

(12) Attribute iPSC lines to specific experiments

A table or supplementary note should specify which cell line (H9, DYR0100, or DXR0109B) was used for each experiment and figure. If different lines were used interchangeably within the same figure, this should be stated and any resulting variability discussed.

All organoid data presented in this manuscript were generated from a single line, DYR0100; the H9 and DXR0109B lines were not used for any experiment reported here. We have removed them from the Methods to avoid ambiguity, and the Methods now state that DYR0100 was used for all organoid experiments. No experiment or figure combines material from different lines.

(13) Moderate the use of "human-specific"

Throughout the manuscript, claims of human specificity should be restricted to contexts where a direct comparison with rodent data has been performed or cited. When the platform uses only human cells, the appropriate phrasing is "human-derived" or "in a human cellular context" rather than "human-specific mechanisms."

We have replaced "human-specific" throughout with "human-derived" or "in a human cellular context," at four locations: the Abstract, the final paragraph of the Introduction, the second paragraph of the Discussion, and the legend of Fig. 4O.

(14) Revise the "first demonstration" claim

The claim to provide the "first human-specific mechanistic demonstration" (line 218) is not substantiated and should be removed or substantially qualified.

This claim has been revised.

(15) Immunofluorescence panel legibility

Protein label text in Figures 1B-E and 3B should be rendered in a contrasting colour (e.g., white with a black outline, or placed on a coloured background tab) so that they are readable against the fluorescence image background. Scale bars should be present and consistent across all panels within a figure.

Protein label text in Figures 1B–E and 3B has been re-rendered in a contrasting colour so that it is legible against the fluorescence background. Scale bars are present in all panels, and their dimensions are stated in the corresponding figure legends.

(16) Remove or justify the Animals section in Methods

If no mouse data are presented in the paper, the Animals section should be removed. If mouse experiments were performed and the data are available, a corresponding figure or supplementary figure should be included.

Animals section description has been removed from Methods.

Corrections & Clarifications

(17) The following must be corrected before resubmission:

(a) Replace "(ref)" placeholders on lines 46 and 63 with full citations.

(b) Replace "(cell reports 2023)" on line 48 with a properly formatted citation. This appears to refer to Feng et al., Cell Reports 42, 113313 (2023), which is already reference 9 in the list - it should simply be cited as such.

(c) Reference 14 (Feng et al., STAR Protoc, glioma organoid protocol) does not support the CCL5-CCR5 claim for which it is cited and should be replaced with an appropriate reference.

(d) Reference 20, cited in the text (line 56), does not exist in the reference list. The intended citation must be identified and added.

(e) Reference 3 (Michell-Robinson et al.) is listed but not cited in the text. It should either be cited where appropriate or removed from the list.

We have carefully reviewed the manuscript and corrected the incomplete and incorrect references.

(18) GEO accession numbers

The manuscript states that bulk RNA-seq data have been deposited at GEO but does not provide an accession number. The accession number must be included in the Data Availability section.

Accession numbers have been added to the Data Availability section: bulk RNA-seq data are deposited under GSE339404 and single-cell RNA-seq data under GSE339602. Both datasets are publicly accessible.

(19) Single-cell RNA-seq data availability

The single-cell RNA-seq data are not mentioned in the Data Availability statement. These data should also be deposited in a public repository (GEO or a single-cell-specific repository such as the Human Cell Atlas data portal), and the accession number should be provided.

Mentioned in comment (18).

(20) Zenodo DOI

The Code Availability section states that code has been deposited at Zenodo, but no DOI is provided. The Zenodo DOI must be included.

Zenodo DOI has been added in the Methods: Single-cell RNA-seq data have been deposited at GEO under accession GSE339602 and bulk RNA-seq data under accession GSE339404; both are publicly accessible as of the date of publication. Microscopy data are available at Zenodo (DOI: 10.5281/zenodo.21686712). All other raw data, including cytokine array images, and all original code are available at https://github.com/FengYilinElaine/2-3D-AD-oranoids.

(21) Ethical approval for human blood collection

The manuscript states that blood was collected from healthy donors at Zhangzhou People's Hospital but does not mention institutional ethical approval for this collection or informed consent procedures. A statement confirming ethical approval (with approval number) and donor-informed consent must be added to the Methods section in accordance with eLife's policies on human subjects research.

Ethical approval for this study was granted by the First Affiliated Hospital of Zhengzhou University (2021-KY-0875-003) and Tsinghua Shenzhen International Graduate School (2024-F125). It has been added to the Methods.

(22) Microscopy data availability

The manuscript states that microscopy data will be shared upon request. eLife's data policy requires that primary data supporting the figures be made publicly available at the time of publication. The authors should deposit representative raw imaging data (or processed calcium imaging traces) in an appropriate repository such as Figshare, Zenodo, or the Image Data Resource and provide the link in the Data Availability section.

Mentioned in comment (20)

Reviewer #2 (Recommendations for the authors):

This study is interesting and presents novel findings supported by state-of-the-art approaches, including single-cell RNA sequencing, a three-dimensional cerebral organoid model, and co-culture systems involving two distinct immune cell populations.

These innovative methodologies provide valuable insights into the mechanisms under investigation. Nevertheless, several aspects of the study require clarification and further improvement.

The authors should address the points in the public review and the following additional points:

(1) Throughout the manuscript, the figure legends contain conclusions and interpretations of the data. These statements should be removed from the figure legends and incorporated into the Results section, while the legends should be restricted to describing the experimental conditions and the data displayed.

Revised manuscript and legends fixed the problem.

(2) The reference list and in-text citations appear to be incomplete. In several instances, the manuscript contains placeholder citations (e.g., "Ref") instead of full references. The authors should carefully review and complete all citations.

We have carefully reviewed the manuscript and corrected the incomplete and incorrect references. All placeholder citations have been replaced with the appropriate references, and the reference list and in-text citations have been checked for completeness.

eLife Assessment

This study presents an important examination of the role of cis-acting versus trans-acting genetic variation on DNA methylation divergence between humans and chimpanzees, including its consequences for gene expression. By differentiating fused interspecies tetraploid cell lines into multiple cell types, the study provides compelling evidence for the importance of cis-acting changes and solid evidence for the relevance of these changes to adaptive evolution in humans. This work will be of interest to biologists and evolutionary anthropologists studying the evolution and genetics of gene regulation, particularly in primates.

Reviewer #1 (Public review):

Ma et al. use human-chimpanzee tetraploid cells, across different cell types, to identify the genetic causes and then transcriptomic consequences of divergence in DNA methylation. They conclude that the evolution of DNA methylation is driven primarily by cis-regulatory changes, and that the evolution of CpG sites contributes to cis-regulation while transcription factor expression underlies some trans changes. They then argue that divergence in DNA methylation is associated with changes in gene expression and may contribute to human phenotypes.

The tetraploid model is able to provide compelling evidence that most regulatory evolution occurs due to cis-regulatory changes, and that sites that have diverged in DNA methylation level cluster together into DMRs which share similar divergence patterns and genetic architecture. This stands in intriguing contrast to trans-mechanisms which explain most variation within modern human populations. The authors proceed to show that trans-effects can be explained, in part, by nearby TF binding motifs and many cis-regulatory changes are explained by CpG-disrupting variants. While these mechanisms clearly contribution to divergence in DNA methylation, the degree to which they explain cis- and trans-regulatory divergence would be valuable.

Next, the authors seek to show that differences in DNA methylation are functionally relevant. Consistent with previous results, they show that differences in DNA methylation are (weakly) associated with changes in gene expression. They hypothesize that genes with concordant regulatory should exhibit great methylation-expression coupling than other genes and show that cis-expression/cis-methylation pairs are more strongly correlated than trans/trans pairs. I think that looking at cis/trans or trans/cis changes would also be useful. Another limitation is that this analysis is limited to promoter regions. It is not clear how many divergent DMRs that includes and how many of those genes have differences in expression. The key question is whether differences in DNA methylation are functionally important, and the answer provided by these analyses is "sometimes".

Finally, the authors make a case for lineage-specific selection on DNA methylation that is connected to human traits. Using a sign-test, they identify sets of genes which have likely experienced selection in humans and may underlie human phenotypes.

In conclusion, I think this study provides a valuable resource for differences in DNA methylation between humans and chimpanzees across tissues and provides important insight into the relative abundance of cis and trans regulatory divergence. Additional research is necessary to investigate the underlying regulatory mechanisms and more care needs to be taken in exploring the functional consequences.

Reviewer #3 (Public review):

Summary:

Ma et al. use human-chimpanzee tetraploid cells to examine species differences in DNA methylation. They identify differentially methylated regions under cis or trans regulation. Cis-DMRs are enriched near SNVs that disrupt or create CpGs, providing a plausible mechanism for cis changes in methylation. They also seek to identify transcription factors that might affect methylation in trans, as well as gene sets with evidence for consistent changes in methylation and expression between humans and chimpanzees, suggesting that they may underlie lineage-specific traits.

Strengths:

The authors have generated a new dataset across multiple different cell types examining differences in DNA methylation between humans and chimpanzees using human diploid cells, chimpanzee diploid cells, and human-chimpanzee tetraploid cells. Using this dataset, they identify that cis-DMRs are enriched near SNVs that disrupt or create CpGs compared to trans-DMRs and identify transcription factors as candidate trans-acting factors. Both identified SNVs and transcription factors are good candidates for future experimentation. The authors also find that cis-DMRs are more highly correlated with cis-expressed genes than trans-DMRs with trans-expressed genes, providing evidence that methylation and expression are linked genome-wide. Further, they apply a clever sign test approach to identify gene pathways with evidence for lineage-specific selection.

Comments on revised version.

They authors have addressed my concerns from their initial manuscript. In particular, the authors have noted the limitations of their study as appropriate, including the use of permissive FDR cut-offs.

Author response:

Summary of changes:

(1) Framing of the sign test results. Throughout the manuscript we have clarified that the sign test provides direct evidence that the implicated gene sets are under lineage-specific selection, while the connection of this selective signal to any specific human phenotype is inferential and would require experimental validation. We also now emphasize that some sign test results are expected to be false positives, as indicated by the FDR.

(2) FDR and cis:trans quantification. We have added explicit statements that (i) the cis dominance is consistent across a range of FDR thresholds (FDR < 0.25, 0.20, 0.10, 0.05, 0.01), (ii) the mean proportion of divergent sites explained by cis-regulation is 91%, and (iii) using the changepoint detection method, we identified 9159 cis-DMRs and 2046 trans-DMRs in total for downstream TF motif and SNV analysis. A power analysis comparing sensitivity to detect cis vs. trans effects is provided as author response image 1.

(3) Clarification of regulation groups, including pure cis, pure trans, conserved, cis × trans and cis + trans. We have added explicit definitions of these categories in the Results.

(4) Cis-gene direction-of-effect definition. We have clarified in the text that cis-regulated genes are defined as those where the direction of allelic difference is consistent between hybrid and parental samples. We note that the scatter plots in Figure 2B as well as Figure 2 supplemental figures plots the per-sample average percent difference in methylation. Cis genes appearing to have opposite direction-of-effect along the y=x diagonal on the scatter plot were due to a difference between this average, used only for visualization, and the values used for analysis in our statistical model. For values close to zero, average log2FC or per cent difference can flip sign even when the model correctly identifies the site as cis-regulated. The regulation classification is based on a statistical model and not the direction of average difference, so there will naturally be some small deviation around the axes when visualizing the results as a scatter plot.

(5) New limitations. We have added four new limitations to the Discussion: (i) absence of an outgroup species; (ii) TFBS-disrupting mutations as an alternative cis mechanism; (iii) the need for experimental validation of SNV-methylation and TF-methylation links; and (iv) the scope of cell types examined.

(6) Quantitative reporting. We have replaced "substantial" with specific numbers throughout.

(7) Additional supplemental resource. A list of cis–cis regulated promoters and their associated genes has been added as Supplemental File 8.

(8) Minor corrections. Missing citation for Hallgrímsdóttir et al. (2024) added; "Preprint at" removed from published paper citations; sequencing coverage reported in Methods.

eLife Assessment:

This study presents an important examination of the role of cis-acting versus trans-acting genetic variation on DNA methylation divergence between humans and chimpanzees, including its consequences for gene expression. By differentiating fused interspecies tetraploid cell lines into multiple cell types, the study provides compelling evidence for the importance of cis-acting changes, but incomplete evidence that these changes are of importance for adaptive trait evolution in humans. This work will be of interest to biologists and evolutionary anthropologists studying the evolution and genetics of gene regulation, particularly in primates.

We appreciate the assessment and agree that the evidence for adaptive trait evolution is indirect. We would like to clarify what the sign test does and doesn’t establish. By rejecting a rigorous neutral null model, the sign test provides strong evidence for lineage-specific selection on DNA methylation divergence. Since the coordinated directional divergence we observe is not expected under neutral evolution, we are confident that the data are evidence of selection. However, the sign test does not identify the specific traits that selection acted upon; the connection between the signal of selection and any phenotype is speculative. Accordingly, we have now revised the manuscript to describe the sign test results as evidence of selection while keeping the interpretation of specific traits explicitly speculative. We also added discussion of the limitations on the trait-level inference (such as the absence of an outgroup, reliance on clinical HPO ontologies, etc.).

Reviewer #1 (Public review):

Ma et al. use human-chimpanzee tetraploid cells across different cell types to identify the genetic causes and then transcriptomic consequences of divergence in DNA methylation. They conclude that the evolution of DNA methylation is driven primarily by cis-regulatory changes, and that the evolution of CpG sites contributes to cis-regulation, while transcription factor expression underlies some trans changes. They then argue that divergence in DNA methylation is associated with changes in gene expression and may contribute to human phenotypes.

We thank Reviewer 1 for a detailed summary of our work.

The tetraploid model is able to provide compelling evidence that most regulatory evolution occurs due to cis-regulatory changes. My only concern is that the extent of trans-changes may be overstated, as almost all are eliminated by changing from a nominal p-value criterion to even a 25% false discovery rate.

We agree that trans-effects are more sensitive to FDR thresholds than cis-effects, and we have addressed this directly. This is a well-recognised limitation of existing cis/trans classification frameworks, and we acknowledge this limitation in the discussion and have added suggestions in experimental set-up to mitigate it. To address the reviewer's concern directly, we have added a formal power analysis quantifying the relative power to detect cis and trans effects as a function of read depth as well as biological noise (dispersion). We now explicitly state in the Results that the cis dominance over trans is consistent across a range of FDR cutoffs (FDR < 0.25, 0.20, 0.10, 0.05, 0.01; Figure 2—figure supplement 1–2), and we note that the greater FDR-sensitivity of trans-DMRs likely reflects systematically smaller effect sizes rather than false positives. We have added a power analysis in Author response image 1 that formally compares our sensitivity to detect cis vs. trans effects. We also note that DMR-level analyses recover both cis and trans effects at meaningful FDRs, consistent with the idea that trans effects are real but requires more replicates as well as a higher sequencing depth to make significant calls at the same level as cis changes at the individual CpG level.

Author response image 1.

Power analysis of cis and trans effects detected by the beta-binomial GLM framework. For each combination of effect size, per-unit read depth, and overdispersion (φ), we simulated a genome of 10,000 units — either individual CpG sites or regions/DMRs — comprising 2,000 true-effect units and 8,000 null units. The simulation is unit-agnostic: a "unit" represents a single CpG when modeling the per-CpG analysis and an aggregated region when modeling the regional (DMR-level) analysis, with read depth interpreted as the per-CpG coverage or the region-level (aggregate) coverage, respectively, and effect size as the corresponding per-CpG or region-level H–C methylation difference.

Effects were classified using the same two-model scheme as the main analysis. A unit was called cis if the hybrid allelic (H–C) test was significant and the allele-by-generation interaction was not significant, and trans if the interaction was significant and the hybrid allelic test was not significant; all tests were Benjamini–Hochberg–corrected across the genome at the stated FDR threshold. Each unit was simulated with the full six-measurement design (two parental samples and four hybrid alleles from two hybrids), both models were fit, each set of p-values was BH-corrected across the genome, and "power" is the fraction of true units that land in the correct class.

Cis-effect units were simulated with an equal H–C difference in both parents and hybrid (zero true interaction); trans-effect units with a parental H–C difference and no hybrid allelic difference (full-magnitude interaction); null units with no difference in either parents or hybrid. Sequencing depth was treated as a fixed design parameter: every sample at every simulated unit was assigned the same total read depth (the value on the y-axis of the heatmaps), corresponding to per-CpG coverage for the site-level analysis or aggregate per-region coverage for the regional analysis.

We estimated the beta-binomial overdispersion (φ) directly from the data for each cell type used in this study: DA = 0.024, CNCC = 0.016, IPSC = 0.013, SKM = 0.014, and HEP = 0.011 (median = 0.014). To span this empirical range and to assess robustness to higher-than-observed dispersion, we evaluated power at φ = 0.015 (approximating the empirically observed median), 0.05, and 0.10; the latter two represent substantially more conservative (higher-noise) scenarios than any cell type in our data. Because power declines monotonically with φ, the φ = 0.015 row reflects the sensitivity expected under realistic conditions, while the higher rows bound the worst case. For each unit, a methylation probability was drawn from a beta distribution whose mean equals the unit's true methylation level and whose dispersion is set by the overdispersion parameter φ, and the number of methylated reads was then drawn from a binomial with that probability and the specified total depth. Consequently, the reported power describes the sensitivity expected at a given uniform per-unit (per-CpG or per-region) depth, spanning 10× to 200×, and is interpreted as the proportion of true-effect units assigned to the correct class.

The follow-up analyses are incomplete with major gaps. The authors focus on single potential mechanisms for cis- and trans-changes, but it is not clear to what degree these mechanisms explain the extent of cis and trans changes. There are also other mechanisms which are not investigated, such as the importance of TF binding sites for cis-regulatory evolution.

We agree that CpG-disrupting SNVs and TF binding motifs are just two out of many possible mechanisms, and we have added explicit acknowledgements of this in the text. Our goal was not to investigate all possible mechanisms, but rather to focus on two that showed promising results. For cis-regulation, we now state that TFBS mutations and other sequence variants could also contribute. We agree that further mechanistic investigation is an important direction for future work, and we have noted this explicitly in the Discussion.

Next, the authors seek to show that differences in DNA methylation are functionally relevant... I worry that this result could be confounded by larger effect sizes for cis-changes than trans effects.

We agree that larger cis-regulatory effect sizes could contribute to this result, and have now mentioned this in the Discussion: “This finding suggests that the repressive effects of species-specific methylation are strongest when both layers of regulation are driven in cis, perhaps because cis-regulated methylation changes tend to have larger effect sizes than trans-regulated changes.”

Finally, the authors make a case for lineage-specific selection on DNA methylation that is connected to human traits. This evidence was not convincing. In fact, it is even said that these tests cannot be interpreted as evidence of lineage-specific selection (lines 399-401), so I am confused why these results are framed as testing for selection.

We appreciate this comment but want to clarify. Lines 399–401 in the original manuscript state that the dental pulp stem cell (DPSC) sign test results specifically should not be interpreted as evidence of lineage-specific selection, because DPSCs use parental rather than hybrid cell lines. This caveat applies only to DPSCs. For all other cell types (iPSC, DA, CNCC, SKM, HEP), which use hybrid cell lines that control for trans-acting confounders, the sign test does indeed provide evidence of non-random directional bias inconsistent with neutral evolution, thereby constituting evidence of lineage-specific selection. We have added a clarifying sentence to make this distinction explicit: "For all other cell types (iPSC, DA, SKM, HEP, CNCC), which use hybrid cell lines, the sign test results provide direct evidence of lineage-specific selection on the implicated gene sets, as the hybrid system controls for trans-acting confounders."

To be clear about the scope of the claim: the sign test directly demonstrates that the implicated gene sets are under lineage-specific selection. What remains inferential is the connection between this selective signal and any specific human phenotype, which would require experiments or further validation to establish; we have revised the framing throughout to keep this distinction explicit.

Reviewer #1 (Recommendations for the authors):

(1) Line 96: How many iPSC lines were used for each species? When a replicate is mentioned (e.g., Figure 1B), are those technical or biological replicates?

We have added the iPSC line counts to both the Results and Methods sections: two human and two chimpanzee iPSC lines were used. Replicates shown in Figure 1B are biological replicates (independent differentiation experiments from the same iPSC lines).

(2) Line 98: How many donors for the DPSCs?

We have added DPSC donor counts to the Methods: two human and two chimpanzee donors.

(3) Line 103: PCA and other analyses combined data from WGBS and RRBS cell types. Some clarification about how this was done (e.g. restricting to RRBS sites?) would be useful in the main text as well as an acknowledgement of potential biases. And

(4) Line 103: Related, what is the number of CpG sites considered?

We have added a clarifying sentence to the Results: cross-cell-type analyses including Figure 1B heatmap and Figure 1C PCA analysis were restricted to CpG sites covered in all samples (i.e., the intersection of all covered sites, after phasing the hybrid samples), totaling 561,762 shared CpG sites. Within-cell-type PCA analysis in Figure 1—supplemental figure 1 was restricted to CpG sites shared across samples of the same cell type, which contains 31,802,196 sites for CNCC samples, 26,163,237 sites for DA, 29,787,850 sites for DPSC, and 1,006,674, 935,636 and 952,835 sites for IPSC, SKM and HEP, respectively. We acknowledge that this restriction to the intersected CpG sites result in PCA performed on sites covered by both WGBS and RRBS, which are most frequent in CpG-dense regions.

(5) Line 103: For Figure 1B, it would be useful to first mention how human/chimp reads were parsed and for how many CpG sites this was possible.

We have added a brief description of the allele-parsing approach (SNPsplit using species-specific SNV positions). For hybrid WGBS samples (DA and CNCC), on average, 48.2% ± 0.2% of all aligned reads are unassignable using SNPs between human and chimpanzee genome, 25.9% ± 0.2% of the reads are specific to human, and 25.1% ± 0.2% of reads are specific to chimpanzee. For hybrid RRBS samples (IPSC, SKM and HEP), on average, 88.4% ± 0.3% of all aligned reads are unassignable using SNPs between human and chimpanzee genome, 5.3%±0.1% of the reads are specific to human; 5.3%±0.1% of reads are specific to chimpanzee. We have added information above to the main text. Per sample splitting reports containing the exact number of reads assignable to each of human and chimpanzee are provided as a comprehensive table at Supplemental File 1. The lower assignment rate in RRBS is expected, and we have performed two additional analyses to demonstrate why. First, the reduced representation strategy concentrates coverage in CpG-dense promoters that are highly conserved between human and chimpanzee and therefore SNV-poor, while the short MspI fragments that dominate these libraries frequently fail to reach an informative SNV even when one is nearby. Quantifying this directly: among the 16,845,376 CpG positions covered by the union of all unphased hybrid RRBS libraries, 65.1% contain a human–chimpanzee SNV within ±50 bp (the reach of a typical RRBS read), compared with 90.8% within ±150 bp (the reach of a typical WGBS read pair) — a 1.40-fold difference in SNV accessibility at the very same CpGs. Second, we compared the aligned-length distributions of allele-resolved and unassigned reads across all ten hybrid libraries (Author response image 2). In the four WGBS libraries the two distributions are indistinguishable, confirming that read length is not driving mappability. In contrast, for all six RRBS libraries, allele-resolved reads are consistently longer than unassigned reads, with the effect reproducible across every cell type and replicate.

Author response image 2.

Aligned read length determines allele-assignment success in RRBS but not in WGBS. Aligned read lengths were extracted from the Bismark-aligned BAM files produced by phasing all ten hybrid bisulfite libraries: four WGBS libraries (CNCC and DA, two replicates each; left) and six RRBS libraries (HEP, iPSC and SKM, two replicates each; right). For each library, reads assigned to either the human (genome1) or chimpanzee (genome2) alleles were pooled into a single phased set (blue) and compared with the reads that could not be phased (grey); distributions were computed from subsampled reads and are shown as boxplots (box, interquartile range; line, median; whiskers, 5th–95th percentiles). In the WGBS libraries, phased and unassigned reads have effectively identical length distributions (median 150 bp for both; means 147.4–147.8 vs 142.1–143.1 bp), indicating that read length does not drive mappability in WGBS. In the RRBS libraries, which are dominated by short MspI fragments, phased reads are consistently longer than unassigned reads across every cell type and replicate (medians 70–75 vs 49–50 bp; means 80.5–85.7 vs 58.6–60.6 bp, ~1.4-fold). Because a read can be assigned to a parental allele only if it spans an informative human–chimpanzee SNV, these results show that the short fragment length characteristic of RRBS — together with its enrichment for SNV-poor, evolutionarily conserved CpG-dense promoters — accounts for its lower allele-resolution rate relative to WGBS.

(6) Line 103: Hybrid/parental line isn't noted in the PCA. Is this just the parental samples?

We clarify that Figure 1C shows both parental and hybrid samples, and we have updated the figure caption for Figure 1C to note that both hybrid and parental samples are plotted in the PCA. The parent/hybrid stratifications are shown in Figure 1—figure supplement 1 and referred to in the main text.

(7) Line 149: No citation # is given for the Hallgrimsdottir paper.

Corrected. Citation number 50 (Hallgrímsdóttir et al., 2024) has been added.

(8) Line 167-169: Some explicit test here would be useful. Is this more than we'd expect just because the majority of CpG sites have conserved methylation levels? How much more do divergent CpG sites cluster than expected by chance?

We agree that an explicit test of clustering would be informative, and we want to be clear about what our analysis does and does not establish. The changepoint algorithm is not a test of non-random clustering: it detects shifts in the local composition of regulatory classifications along the genome and segments each chromosome into locally homogeneous stretches. Its purpose here is enrichment rather than inference, because it selects regions in which neighboring CpG sites share both a regulatory classification and a consistent direction of species bias, so that the downstream motif-enrichment and CpG-SNV proximity analyses operate on interpretable units rather than on mixtures of mechanisms. Because the segmentation is not compared against a null model, it cannot by itself establish that divergent sites co-localize more than expected given that 83–93% of all sites are conserved. We have therefore revised the text so that Figure 2D reads as a descriptive summary of the neighbourhood composition of each regulation group, and removed any implication that the co-localization has been tested against a chance expectation. Asking whether divergent sites cluster more than expected is a genuinely different question from the one our DMR-calling addresses and answering it well would require a dedicated null model. We think this is a worthwhile analysis and a natural extension of this framework, but it is separate from the claims we make here, and we have not attempted it in this revision.

(9) Line 186-187: It should be made clear that you looked to cis, trans, and cis + trans DMRs independently.

We have revised this sentence to make explicit that cis-DMRs, trans-DMRs, and cis+trans DMRs were identified independently using the changepoint detection method applied separately to each regulatory class.

(10) Line 190-192: Some quantification of the degree to which cis effects exceed trans effects would be useful. What proportion of total divergence (e.g. mean and s.d.) is explained by cis factors?

We have added this quantification: “At FDR < 0.05, cis-regulation accounted for a mean of 91% of divergent sites and trans-regulation a mean of 4.5% across cell types, and cis remained the dominant category at every FDR cutoff tested (FDR < 0.25–0.01; Figure 2C, Figure 2—figure supplement 1–2, Supplemental Files 1–2).”

(11) Line 194-196: It should be made clear that motif enrichment was done in the human genome, right? Are the results consistent if motif enrichment was done in the chimpanzee genome?

We have clarified in the Methods that HOMER motif enrichment was performed using the human genome (hg38) as background. Repeating the analysis using the chimpanzee genome as background is a valuable future direction; we acknowledge this has not been formally tested.

(12) Line 208: For TFs other than FOXM1 and FOXA2, is TF expression generally associated (positively or negatively) with trans DMRs favoring the chimpanzee or human lineage? An idea of the distribution would be useful.

We plotted the distribution of differential TF expression for those with predicted binding sites enriched in Hu>Ch trans-DMRs versus Hu<Ch trans-DMRs in DA and CNCC. In neither cell type do the two distributions show a clear separation of directional shift. TF expression differences are broadly overlapping regardless of whether the associated trans-DMR favors the human or chimpanzee lineage. We speculate the lack of separation reflects multiple trans-acting inputs shaping methylation divergence such that single TF expression does not predict it. Aggregating across TFs with potentially opposing effects could further contribute to this observation as well (Figure 3—figure supplement 1). FOXM1 and FOXA2 are individual cases where a suggestive relationship was visible rather than evidence of genome-wide pattern.

Author response image 3.

Distribution of differential expression of TFs with predicted binding sites enriched in trans-DMRs. Density distribution of TF expression difference in human versus chimpanzee parental samples. There is a lack of separation between expression of TFs with predicted binding sites enriched in Hu>Ch trans-DMRs versus Hu<Ch trans-DMRs, in both DA and CNCC.

(13) Line 211-212: Stats are needed.

This statement is intended as a qualitative description rather than a quantitative statement. With only 4 cell types per comparison (Figure 3B), we do not have enough statistical power to establish a significant correlation, therefore we present this result as an exploratory observation rather than a statistically significant finding. We have therefore removed "consistent with this expectation," reframed the FOXM1 and FOXA2 results as descriptive observations from individual factors, and added an explicit statement that they are exploratory and hypothesis-generating rather than evidence of a genome-wide pattern.

(14) Figure 3C: Direction is not given. It should be made clear that this is a gain/loss in humans.

We have updated the Figure 3C caption to explicitly label the three SNV categories as: CpG gains in humans (human allele creates a CpG), CpG losses in humans (human allele disrupts a CpG), and no CpG change.

(15) Figure 3C: Most cell types have a bias towards increased DNA methylation when there are no nearby CpG sites (gray bars). Why? Is this a consequence of a reference bias?

We thank the reviewer for raising this. The grey bars correspond to methylation levels of conserved CpG sites near SNVs with no CpG-altering substitution and serve as the genome-wide background/control category, against which the substitution-containing categories are compared. Their modest skew toward higher methylation reflects a global offset shared by all categories rather than a substitution-specific effect. We suggest two non-exclusive explanations for this baseline offset: a genuine genome-wide difference in the distribution of human- versus chimpanzee-biased methylation, and/or a possible contribution of reference genome mapping bias arising from alignment to the human genome. Importantly, this does not affect the conclusions drawn from Figure 3C. Because the genome-wide offset is shared across all categories, the substitution-attributable signal is reflected in the difference between the CpG-gain/loss categories and the no-change (grey) baseline, and any genome-wide baseline shift — biological or technical — cancels in that comparison. We therefore interpret the grey-category asymmetry as a background property and explicitly do not attribute it to the substitutions themselves. Future work such as analyzing with reads mapped to the chimpanzee or a masked consensus genome or restricting to mappability- and coverage-matched regions could directly quantify any reference-bias contribution, and we note these as promising directions.

(16) Line 258-269: Figure 3D is not referenced in the text.

We have added a reference to Figure 3D in the relevant paragraph of the Results: “To test this, we compared the genomic distance between each DMR and its nearest CpG SNV. Consistent with our model, we found consistently shorter distances for cis-DMRs than trans-DMRs across all cell types examined: Median distances to the nearest CpG SNV were 24 ± 6 bp for trans-DMRs vs. 11 ± 2 bp for cis-DMRs (Figure 3D; Mann-Whitney p < 0.001 for all comparisons) [65].”

(17) It is unclear why Figure 4A-C focus exclusively on cis-regulated promoters. Is this for biological or technical reasons?

Both. Biologically, cis-regulated promoters are the most interpretable for assessing cell type-specificity, because cis effects are allele-intrinsic and not confounded by differences in trans-acting environments across cell types. Technically, trans-regulated promoters show methylation differences that depend on the trans-environment, making cross-cell-type comparisons less straightforward.

(18) Line 371: How many DMRs are being considered?

We have added the total number of DMRs (promoters) considered in the sign test analysis: 6,283.

(19) Line 371-372: What is the ASM/ASE concordance test? I thought you were restricting the analysis to genes with a negative association between ASM and ASE (lines 366-367), so this needs to be clarified.

We have clarified this in the text. The two-step procedure works as follows: (1) a binomial sign test is applied to all genes with promoter ASM to identify gene sets with directional bias in methylation; (2) separately, a binomial sign test is applied to the subset of genes where ASM and ASE show a negative (repressive) relationship. Gene sets that pass both steps are reported as candidates. The "ASM/ASE concordance test" refers to step 2. We have revised the text to make this two-step logic clearer.

(20) Line 379: It may be worth mentioning that these are the DMRs which are most likely to be functionally relevant in shaping expression levels.

We have added this sentence: " This subset represents cases where methylation changes are most likely to have a simple and direct repressive effect on transcription, filtering out more complex regulatory scenarios where methylation and expression changes may be uncoupled or subject to competing regulatory influences."

(21) Line 387: The test here needs to be clearer. Does a significant result mean an enrichment of differences in that gene set, or a bias in the ratio of Hu/Ch differences?

We have clarified: a significant result from the binomial sign test indicates a statistically significant bias in the ratio of human-biased to chimpanzee-biased changes within a gene set, relative to the genome-wide background ratio. It does not test for enrichment of the number of differences, only for non-random directionality.

(22) Line 403: Why the focus on expression, when the rest of the paper is focused on the methylation patterns?

Gene expression is the most direct functional readout of promoter methylation changes. The two-step sign test uses expression data in the second step precisely because it allows us to identify cases where methylation divergence has a demonstrable downstream consequence on transcription, which is the canonical mechanism by which promoter methylation affects phenotype. We have added a brief justification of this rationale to the text.

(23) Line 456: Not clear where there is actually evidence of lineage-specific selection.

We have added an explicit sentence in the Discussion describing what the evidence consists of: "Specifically, the evidence rejecting a neutral null model of cis-regulatory evolution consists of statistically significant directional bias in both promoter methylation and gene expression within functionally coherent gene sets, assessed using a two-step binomial sign test with permutation-based FDR correction." This constitutes direct evidence that the implicated gene sets are under lineage-specific selection; the separate question of which specific human phenotypes that selection shaped remains inferential and is framed as such throughout.

(24) Line 457-459: I think this line needs to be further explained: "Our use of hybrid cell lines was critical to this discovery, as it allowed us to isolate cis-acting regulatory changes from confounding trans-acting and environmental effects." Specifically, it's not apparent why cis-regulation is important for demonstrating evidence of selection.

We have added an explanation: "Isolating cis-acting changes is critical because the sign test requires that each promoter represents an independent observation; in hybrid cells, each allele's methylation is determined by its own cis-regulatory sequence, making observations across promoters genuinely independent and thus satisfying the assumptions of the binomial test."

(25) Line 460-465: The concluding claims throughout this paragraph appear to be overstated.

We have revised the concluding paragraph of the Results and the Discussion conclusion to soften the language.

(26) Line 487: Provide the actual numbers instead of saying "substantial".

We have replaced "substantial numbers of allele-specifically methylated promoters" with the actual count: 6,283 allele-specifically methylated promoters across all cell types.

(27) Line 502: I question this interpretation. While it could be that there is a shared mechanistic basis, it could also be that the cis effects tend to be larger than the trans effects, providing additional power to identify strong correlations.

We agree and have added this alternative explanation explicitly to the Discussion (see response to public review comment above).

(28) Line 510: But the results section states that it's not possible to interpret these as lineage-specific selection.

The caveat at lines 399–401 applies specifically to DPSCs, not to hybrid cell types. We have revised the text to make this distinction unambiguous.

(29) Line 601: What coverage was the methylation data?

We have added sequencing coverage and the number of CpG sites assayed below “Bisulfite-seq library preparation, sequencing and mapping” section in Methods. WGBS libraries achieved a mean coverage of 9.68× per CpG site, covering 43.6M unique CpG positions in CNCC (hybrid) and 43.4M in CNCC (parental), 41.9M in DA (hybrid) and 38.8M in DA (parental). RRBS libraries achieved a mean coverage of 5.02× per CpG site, covering 5.0M, 4.8M, and 4.5M unique CpG positions in the hybrid HEP, IPSC, and SKM libraries respectively, and 3.3M, 3.4M, and 3.2M in the corresponding parental libraries. The total number of CpG sites (union) of all WGBS samples is 48,994,320 sites, and the union of all CpG sites of RRBS samples is 7,289,251. The union of all samples (including WGBS and RRBS) is 49,049,052. We have also included coverage information per sample as a table in Supplemental File 1.

(30) Line 820: citation shouldn't include "preprint at".

Corrected. "Preprint at" has been removed from all published paper citations in the reference list.

Reviewer #2 (Public review):

This manuscript investigates the causes and consequences of human-specific DNA methylation divergence relative to chimpanzees... This study provides a valuable dataset and a compelling framework for understanding how local sequence variation contributes to epigenetic and transcriptional divergence, with likely broad impact in comparative and evolutionary genomics.

We thank Reviewer 2 for this positive assessment and for the constructive suggestions.

Although the authors identify transcription factors associated with differential methylation, it is unclear what proportion of differentially methylated CpGs or DMRs can be attributed to these factors. Providing a quantitative estimate would help assess the relative contribution of trans-acting regulation.

We agree that a quantitative estimate of the proportion of differentially methylated CpGs or DMRs attributable to these transcription factors would be informative in principle. In practice, however, such an estimate is challenging to produce reliably: predicted binding sites are not all occupied or functional, individual DMRs are typically influenced by multiple trans-factors, and we lack the per-site functional data needed to assign methylation differences to specific TFs with confidence. More importantly, even if we could generate such a number, an association-based estimate would not establish that these factors causally drive the observed methylation differences. We have added a note to the main text clarifying that our analysis identifies candidate trans-acting factors associated with differential methylation rather than quantifying their causal contribution.

The analysis of CpG-disrupting mutations is interesting but raises two concerns. First, other classes of variants—such as transcription factor binding site-disrupting mutations—could also influence local methylation patterns and are not considered here. Second, the causal direction remains ambiguous: CpG-disrupting mutations may result from methylation-associated mutational processes (e.g., C->T transitions at methylated CpGs) rather than being the primary drivers of methylation divergence.

We have addressed both concerns in the revised manuscript. On the first point, our goal was not to suggest that CpG-disrupting variants are the only causes of local methylation divergence. We now explicitly acknowledge in the Results that TFBS mutations and other variant classes could also contribute to cis-methylation divergence and represent an important avenue for future investigation. On the second point: while CpG-disrupting mutations are indeed expected to be enriched in highly methylated regions, they would be expected to associate with methylation level rather than methylation divergence, and thus cannot explain the patterns we observe.

Regarding the discussion comparing the distance between CpG-disrupting SNVs and trans-DMRs, without information on the absolute or relative distance distributions, it was difficult to assess the magnitude of the observed differences. Moreover, trans-DMRs, by definition, are not driven by local (cis) variation, and the lack of proximity to CpG-disrupting SNVs is expected. Clarifying what additional insight this analysis provides beyond this expectation may improve this section.

We agree that the lack of proximity of trans-DMRs to CpG-disrupting SNVs is expected. We have revised the text to clarify that this analysis serves as an affirming result: it is consistent with the fact that cis-DMR are under local sequence-driven regulation, and that the CpG-disrupting SNV mechanism is more closely associated to cis-DMRs than trans-DMRs. The quantifications for distance distributions are shown in Figure 3D, and we have added a sentence noting the median distances for trans-DMRs vs. cis-DMRs: 24 ± 6 bp vs. 11 ± 2 bp.

One potential extension would be to examine whether the same cis-acting SNVs are consistently associated with methylation differences across multiple cell types.

We thank the reviewer for this suggestion and have performed this analysis below. For each of the three regulatory region classes (promoters, enhancers, CTCF binding sites), we intersected CpG SNVs (±100 bp window) with cis-classified DMRs (pure_cis or cis_plus_trans at BH-corrected FDR < 0.05) across the five cell types (CNCC, DA, HEP, IPSC, SKM), and counted the number of cell types in which each SNV overlapped a cis-DMR. To assess significance, we compared this distribution to a permutation null in which, for each cell type, we randomly sampled the same number of regions from that cell type's pool of tested-but-conserved regions of the same class (1,000 permutations); SNVs were restricted to those falling within the tested universe across cell types.

Local methylation effects of CpG SNVs were shared across cell types substantially more than expected by chance in all three region classes. The observed mean number of cell types sharing per SNV-in-cis-DMR was 1.244 vs. 1.077 ± 0.006 in the null for promoters, 1.133 vs. 1.042 ± 0.001 for enhancers, and 1.171 vs. 1.061 ± 0.002 for CTCF binding sites (all p < 0.001). Fold-enrichment scaled sharply with the degree of sharing: at the highest sharing level (cis-DMR in all five cell types), observed counts exceeded the permutation null by ~3,500-fold for promoters, ~800-fold for CTCF, and ~700-fold for enhancers. The slightly stronger consistency signal at promoters relative to enhancers is consistent with the more constitutive activity of promoter elements across cell types. These results indicate that the same cis-acting variants tend to drive methylation divergence across multiple cell types, supporting a shared mechanistic basis for cis-methylation divergence. We have added the figure in the main text as Figure 3—figure supplement 2.

Regarding their two-step sign test analysis, because enrichment-based approaches can sometimes overemphasize statistical significance without reflecting effect size, I wonder if incorporating the magnitude of methylation change would provide additional information.

We agree. The magnitude of methylation change (effect size) for each gene and gene set is now provided in Supplemental File 7 alongside the directional bias statistics. We have added a sentence to the Results pointing readers to this resource.

Strength:

I recommend that the authors provide a list of cis-cis-regulated promoters and their associated genes, which would be a valuable resource for the field.

We have added this list as Supplemental File 8.

Reviewer #3 (Public review):

Ma et al. use human-chimpanzee tetraploid cells to examine species differences in DNA methylation... Both identified SNVs and transcription factors are good candidates for future experimentation. Further, they find that cis-DMRs are more highly correlated with cis-expressed genes than trans-DMRs with trans-expressed genes, providing evidence that methylation and expression are linked genome-wide.

We thank Reviewer 3 for this summary and for the detailed recommendations.

Weakness

(1) Strengthening their cis/trans analysis, including: (a) only showing or analyzing genomic regions that pass FDR correction; (b) clarifying how cis genes are defined (Figure 2B shows some genes labeled as cis where the direction-of-effect differs between hybrid and parent cells); (c) assessing how well powered they are to perform each analysis.

(a) Figure 2B has been updated to show regulatory classifications of promoter regions in cranial neural crest cells (CNCCs) at FDR < 0.05. Scatter plots and bar plots for all cell types at the level of individual CpG sites have been moved to Figure 2—figure supplement 1, and the corresponding promoter-level plots for all cell types other than CNCCs to Figure 2—figure supplement 2. We have clarified in the Figure 2—figure supplement 1 caption that nominal p-values are used to preserve the full dynamic range of the data, whereas FDR-corrected thresholds are applied for visualization of promoter scatter plots as well as all formal inference and for reporting significant candidate loci. FDR-corrected results are presented in Figure 2—figure supplements 1–2, and we have added explicit statements in the Results confirming that the cis: trans ratio is stable across FDR thresholds.

(b) We have clarified the definition of cis-regulated genes in the text: cis-regulated genes are defined as those where the direction of allelic difference is consistent between hybrid and parental samples for both methylation and expression. We have verified that this definition is applied consistently throughout the manuscript and downstream analyses.

(c) We have clarified the FDR correction approach for the sign test in the Methods: FDRs are estimated by permutation (10,000 permutations), and we report results at FDR < 0.25 for the two-step test with supporting evidence from the methylation-only sign test (nominal p < 0.05). We acknowledge that this is a relatively liberal threshold. The sign test itself provides direct evidence that the implicated gene sets are under lineage-specific selection; what we have toned down is the downstream interpretation, framing the link between these gene sets and specific human phenotypes as inferential and requiring experimental validation rather than as confirmed.

(d) We agree that experimental validation would strengthen the mechanistic claims. We have added this explicitly to the Limitations section: "definitive demonstration of causality requires targeted experimental perturbations such as base editing (for CpG-disrupting SNVs) or TF knockdown/overexpression experiments (for trans-acting TFs)."

(2) Softening claims about human evolution or human specificity for several reasons: (a) Their comparison lacks tetraploid controls (e.g. human-human tetraploids and chimp-chimp tetraploids) or experimental follow-up in diploid cells, making it hard to be certain that observed effects are not due to ploidy. (b) There are no outgroup species included in the analysis. (c) The use of no or very loose FDR corrections with the sign test makes it difficult to draw conclusions. (d) Experimental data to link SNVs to changes in cis methylation or identified transcription factors to changes in trans methylation would be needed to validate the authors' predictions.

(a) The concern about ploidy effects is noted. We note, however, that the primary evidence for cis-regulation comes from allele-specific methylation within the same tetraploid nucleus, where both alleles experience identical ploidy and trans-environments. Ploidy effects would be expected to affect both alleles equally and would therefore not produce the allele-specific differences we observe. We acknowledge that single-species tetraploid controls would provide additional confidence and represent a valuable future experiment.

(b) We have added the absence of an outgroup species as an explicit limitation in the Discussion.

(c) We have clarified the FDR correction approach for the sign test in the Methods: FDRs are estimated by permutation (10,000 permutations), and we report results at FDR < 0.25 for the two-step test with supporting evidence from the methylation-only sign test (nominal p < 0.05). We acknowledge that this is a relatively liberal threshold and have emphasized this by adding a new sentence: “However, as indicated by the FDR, we do expect some fraction of these candidate gene sets to be false positives.”

(d) We agree that experimental validation would strengthen the mechanistic claims. We have added this explicitly to the Limitations section: "definitive demonstration of causality requires targeted experimental perturbations such as base editing (for CpG-disrupting SNVs) or TF knockdown/overexpression experiments (for trans-acting TFs)."

Reviewer #3 (Recommendations for the authors):

(1) Why are dental pulp stem cells so different from the other cell types transcriptionally (e.g. Figure 1C)? Is this due to being primary cells vs. stem-cell-derived cells?

The transcriptional distinctiveness of DPSCs is most likely attributable to their status as primary cells rather than iPSC-derived cells. Primary cells retain the epigenetic and transcriptional signatures of their tissue of origin and have not undergone reprogramming, whereas iPSC-derived cell types share a common pluripotent origin that may reduce inter-cell-type transcriptional distance. Additionally, DPSCs are mesenchymal stem cells with a distinct developmental lineage and were obtained from adult donors rather than differentiated in vitro, which may further contribute to their distinct profile. We have added a brief note to the Results acknowledging this.

(2) I am concerned about how cis genes are defined. In Figure 2B, there are genes labeled as cis, where the direction-of-effect differs between hybrid and parent cells. I believe cis should only include genes with the same direction-of-effect between hybrid and parent cells, as illustrated in Figure 2A. This fix should propagate through the ensuing figures and results.

We have clarified the definition of cis-regulated genes in the text (see response to Weakness 1b above). The classification framework assigns a site to "cis" when the allele effect test is significant in hybrids and the System × Allele interaction term is not significant, meaning there is no detectable change in the allelic difference between the hybrid and parental systems. Sites where the allelic difference genuinely differs between systems — that is, where the interaction term is significant — are classified as cis × trans (interactive) or cis + trans (additive) rather than pure cis, depending on whether the two systems disagree in direction or only in magnitude.

We note that Figure 2B plots parental and hybrid methylation differences as the per-sample average difference in fractional methylation, which is used for visualization only. Points labeled cis that fall on the opposite side of the y = x diagonal are an artifact of this averaging: where the underlying difference is close to zero, the coverage-weighted per-sample average can flip sign even though the beta-binomial model, which fits the read counts directly and accounts for coverage and overdispersion, finds no significant interaction. The regulatory classification is based on the model, not on the sign of the averaged difference, so a small amount of scatter around the diagonal is expected. We have verified that this definition is applied consistently throughout the manuscript and downstream analyses and have clarified the caption of Figure 2B to make this explicit.

(3) Are you equally powered to detect cis and trans effects?

At the single-CpG level, the two hypotheses do differ in statistical power, but at the regional level this difference is mitigated by the higher effective read depth, and we now state this explicitly in the revised manuscript.

The first hypothesis in our classification framework tests allele-specific methylation directly, whereas the second hypothesis includes an interaction term that evaluates whether allelic differences shift between the parental and hybrid systems. Because the interaction test is inherently less powerful, it requires greater sequencing depth and, ideally, additional replicates to yield comparably confident estimates and to assign sites to certain classification categories with significance. As a consequence, at the single-CpG level, trans effects are more sensitive to FDR thresholds than cis effects of equivalent nominal significance, which reduces our power to detect them. At the regional level, however, as well as in CpG-level analyses with high-coverage samples, this disparity in power between cis and trans largely disappears.

This is the technical component of the issue. From a biological standpoint, cis effects are also intrinsically easier to detect than trans effects: estimates of trans effects necessarily incorporate not only trans-acting molecular mechanisms but also environmental and technical noise, so cis estimates will always be cleaner. This is a well-recognized limitation of existing cis/trans classification frameworks, and we acknowledge this limitation in the discussion and have added suggestions in experimental set-up to mitigate it. To address the reviewer's concern directly, we have performed a formal power analysis quantifying the relative power to detect cis and trans effects as a function of read depth (See Author response image 1).

(4) Are the results shown for SNVs in CpGs in Figure 3C only for cis-DMRs or for all DMRs? If the latter, please show cis-DMRs and trans-DMRs separately and explain why trans-DMRs show the same pattern as cis-DMRs. In addition, I would expect that the CpG that contains an SNV leading to CpG loss or gain would be the most affected in terms of methylation status, rather than CpGs within 25bp vs. 50bp vs. 100bp. It would be helpful to see that plot as well.

We thank the reviewer for the opportunity to clarify. Figure 3C is not an analysis stratified by cis-DMRs or trans-DMRs. Rather, it examines local methylation changes at conserved CpG sites located within 25 bp, 50 bp, and 100 bp of a CpG-disrupting SNV. The purpose of this analysis is to test a specific mechanistic hypothesis: that a CpG-disrupting mutation may influence the methylation status of nearby, intact CpG sites in cis. The analysis is therefore agnostic to cis/trans-DMR classification, as it asks a different question, namely whether sequence disruption at one CpG propagates locally to neighboring CpGs.

We note that Figure 3D addresses a related but distinct question, showing that cis-acting sequence changes more broadly (not restricted to CpG-disrupting mutations) are more strongly associated with cis-DMRs than with trans-DMRs. Together, Figures 3C and 3D support complementary aspects of the cis mechanism: the local propagation of methylation changes around disrupted CpGs (3C) and the broader association of sequence variation with cis-DMRs (3D).

Regarding the reviewer's second point: we agree that the CpG site directly disrupted by the SNV would itself be the most affected, by definition, since the CpG dinucleotide is destroyed (in the case of CpG loss) or newly created (in the case of CpG gain). Because methylation cannot be measured at a CpG that no longer exists (or has only just been created on one allele), this site cannot be included in a comparative methylation analysis across alleles or species. The 25/50/100 bp windows were therefore chosen specifically to test the local effect on conserved, measurable CpGs surrounding the disruption. We have clarified this rationale in the revised text/figure legend.

(5) The finding that cis-DMRs and cis-expressed genes are more correlated than trans-DMRs with trans-expressed genes is nice to see. What is a potential explanation for why the patterns across the genomic interval surrounding the TSS are so different across cell types, and even positively correlated near the TSS in dopaminergic neurons? Why do you not see a difference between cis and trans in CNCCs? In addition, it would be nice to see the correlation between cis-DMRs and trans-expressed genes, and vice versa, as a control for these plots.

We have added the suggested control analysis. For the cis-DMR/trans-expressed-gene and trans-DMR/cis-expressed-gene sets in both DA neurons and CNCCs, the correlations around the TSS are less consistently negative than for the cis-DMR/cis-expressed-gene set. In both cell types, cis-methylation and cis-expressed genes show the strongest opposing (negative) relationship to one another, which supports the specificity of the cis–cis coupling reported in Figure 4G. Regarding why the correlation profiles across the TSS-flanking interval differ so markedly across cell types—including the positive correlation near the TSS in dopaminergic neurons—and why the cis–trans distinction is less pronounced in CNCCs, we are not able to offer a confident explanation. The variation may reflect cell-type-specific regulatory architecture, but a great deal remains unknown about how methylation and transcription are coupled in a cell-type-specific manner, and our four cell types do not allow us to distinguish among the possible explanations. We think this is an open and interesting question, and that analyzing additional cell types with matched WGBS and gene expression data would be the most informative way to establish how general these patterns are and what drives the between-cell-type variation. We have noted this explicitly in the main text.

Author response image 4.

Spearman correlation of expression and methylation for CNCC and DA for subsets of genes with cis-regulated methylation and trans-regulated expression (orange), as well as genes with trans-regulated methylation and cis-regulated expression (blue). Two kb surrounding each transcription start site (TSS) is shown, split into 10 bins of 200 bp where individual CpG sites are pooled and averaged as fractional methylation values and correlated with expression values of the neighboring genes (in TPM).

(6) The use of the sign test to identify pathways with the same direction of effect is a great approach. However, I am concerned with the use of no or very loose FDR corrections (e.g. FDR < 0.25 in line 372 and no FDR correction in line 374). Combined with Figure 6, where many of the signals appear to be weak or driven by a few genes (e.g. highly arched eyebrow and poor speech), it makes it difficult to draw robust conclusions. It is notable that the strongest signal is seen in DPSCs, which the authors note contains experimental confounds. We also think that the authors should tone down their biological interpretations, particularly for stem cells. For instance, COLEC11 is involved in neural crest cell migration but is identified from the iPSC analysis and not the CNCC analysis. Why not?

We have added a sentence to emphasize the possibility of some false positive sign test results (“However, as indicated by the FDR, we do expect some fraction of these candidate gene sets to be false positives”), and we have toned down the biological interpretations accordingly.

We want to clarify that the sign test directly demonstrates that these gene sets are under lineage-specific selection. We have clarified that the test does not establish a definitive link between these gene sets and specific human phenotypes; that link is inferential and would require experiments or further validation, and we have toned down the biological interpretations accordingly.

Regarding COLEC11: in response to this comment, we directly examined COLEC11 expression and methylation in CNCCs and found that it is in fact significant in this cell type. In CNCC hybrid cells, COLEC11 shows significant chimpanzee-biased allele-specific expression (log2 fold change [human/chimpanzee allele] = –2.45; DESeq adjusted p = 0.005), together with significant human-biased methylation (fractional methylation [human – chimpanzee] = 14%; adjusted p < 0.001). The direction of this divergence is therefore consistent with IPSC. The reason COLEC11 did not surface at the pathway level in CNCCs is that other genes in the same pathway contribute to the directional signal for that cell type; we would not expect every individual gene to emerge in the cell type where its pathway is most relevant. We have added a note making this point and cautioning against over-interpreting any single gene example.

(7) We appreciate that the authors provide a careful list of limitations of their study. In addition to the limitations listed, the authors should also include that experiments would be needed to validate that SNVs disrupting or creating CpGs affect methylation.

We have added this to the Limitations section: “definitive demonstration of causality requires targeted experimental perturbations such as base editing (for CpG-disrupting SNVs) or TF knockdown/overexpression experiments (for trans-acting TFs).”

(8) We also caution the authors in describing their findings as "human-specific" because there is no outgroup in this study.

We agree and have added the absence of an outgroup as an explicit limitation in the Discussion.

We thank all three reviewers again for their thorough and constructive engagement with our work. We believe the revised manuscript is improved as suggested.

eLife Assessment

This computational study constitutes an extension to prior work on biophysical calcium-based synaptic plasticity rules, investigating how the regulation thresholds for strengthening and weakening connection help solve learning tasks. This important work presents a significantly simpler solution to the studied problem with potentially broad applicability, the evidence to support the core conclusions is solid.

Reviewer #1 (Public review):

Summary

This computational modelling study investigates the functional role of metaplasticity in a calcium-dependent synaptic plasticity rule, using a biophysically detailed model of a striatal projection neuron. The learning rule is deliberately simple: local calcium signals derived from different sources regulate LTP and LTD through separate plasticity thresholds, while dopamine provides a reward-related signal that determines the direction of synaptic updates. The author uses linear and nonlinear feature-binding problems (FBP and NFBP) as learning tasks to illustrate the mechanics of competing LTP and LTD processes in this rule. The central aim is thus to use these classification tasks to understand what metaplasticity in the two calcium thresholds contributes to learning.

The study identifies complementary roles for metaplasticity in the LTP and LTD thresholds, enabling synapses exposed to competing plasticity processes to converge toward a stable outcome. In reversal-learning tasks, relaxing the conditions for metaplasticity allows previously stabilized synaptic states to become flexible again and permits relearning. Finally, the manuscript investigates whether two separate calcium thresholds are themselves necessary. While a modified rule with a single adaptive calcium threshold can solve the same tasks comparably well, two thresholds allow separate control over synaptic strengthening and weakening.

Strengths

A major strength of the study is the simplicity of the learning rule, which makes it possible to dissect the roles of individual components while retaining a connection to experimentally motivated mechanisms of cortico-striatal plasticity. The use of shared features in the FBP and NFBP is useful for exposing the interaction between competing LTP and LTD processes and for showing how adaptation of one plasticity threshold can indirectly permit expression of the opposite form of plasticity.

The manuscript also provides a much more systematic analysis of the rule than the original version. In particular, the expanded parameter analyses explore both successful and failing regimes for the learning and metaplasticity rates, while the scan over the maximum synaptic weight provides a clear mechanistic motivation for the additional upper LTP threshold.

Importantly, the single-threshold simulations directly address whether two calcium thresholds are computationally necessary. These additional simulations clarify that the principal advantage of two thresholds is not that they uniquely enable nonlinear learning, but that they permit independent regulation of strengthening and weakening. This considerably strengthens the conceptual conclusions of the study.

Weaknesses

The main limitations concern the scope and biological generalizability of the results. The simulations in this paper are based on a particular detailed SPN model and depend on several specific biological and modelling assumptions. Most notably, solving the nonlinear task requires appropriately clustered excitatory inputs, but the learning rule itself does not provide a mechanism for generating these clusters. The manuscript now discusses this limitation explicitly and appropriately identifies structural plasticity as an important direction for future work.

A second important assumption is the upper calcium threshold that prevents LTP once sufficiently strong supralinear responses are reached. This mechanism plays an important functional role in the model but has not been experimentally established for cortico-striatal synapses. The manuscript appropriately identifies this as a major assumption and discusses potential molecular mechanisms that could implement such an effect.

Overall assessment

The revised manuscript is substantially stronger. The conclusions are carefully matched to what is demonstrated by the simulations, and several important alternative explanations and model configurations are tested directly. In particular, the revised framing provides a more specific mechanistic account of what metaplasticity in two separate thresholds contributes within the proposed rule. The work therefore provides a valuable contribution to computational studies of synaptic plasticity and metaplasticity, with convincing evidence supporting its principal conclusions.

Reviewer #2 (Public review):

Summary:

The manuscript proposes interesting synaptic plasticity rules grounded in experimental data. Its main features are: (1) plasticity depends on local calcium concentration driven by presynaptic activity and is independent of somatic action potentials, (2) the rules incorporate metaplasticity, and (3) they demonstrate how a single neuron could address the feature-binding problem at the dendritic level.<br /> The work extends a previous study (https://doi.org/10.7554/eLife.97274.2), to which the author also contributed.

The author models two calcium thresholds (LTP/LTD) from two different calcium sources (NMDA/VGCC) and these thresholds are flexible (metaplasticity rule, similar to BCM) which is claimed to be necessary for successful learning of both FBP and NFBP (linear and nonlinear feature binding problem with 1 or 2 patterns). The role of each threshold seems to be is opposite and complementary. One extra condition has been added : an upper threshold for LTP. This threshold serves to stop synaptic strengthening once synapses are strong enough to evoke a plateau. With that, synapses are not strengthened to the maximal value, avoiding strong supralinear integration for irrelevant patterns.

Strengths:

The current model implements not only local synaptic plasticity but also metaplasticity and solves the FBP at the dendrite level. Another strong aspect of the model is that metaplasticity in the LTD threshold protects strengthened synapses from weakening. In this way, as the author mentioned, metaplasticity is able to protect learned patterns from being forgotten or weakened and prevent irrelevant patterns from being stored. This is a nice modelling example of metaplasticity being helpful in preventing the catastrophic interference or forgetting (as has been explicitly discussed in a recent article https://doi.org/10.1016/j.tins.2022.06.002). The author might want to briefly mention or emphasize this aspect of the model, which might be interesting also for the AI community.

Comments on revised version:

The author improved the paper significantly. He conducted new simulations on relearning. He addressed the problems and limitations, added new simulation results and reasoned better in the discussion and the introduction. Also, the figures are improved.

Author response:

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

The goal of the study was to demonstrate the role of the two thresholds in learning, i.e. the role of metaplasticity with a learning rule that is both as simple as possible, but also biologically-based (hence the use of the detailed SPN model, as well). The goal was not to solve the FBP and NFBP with a different rule. However, the text likely gives that impression. Therefore, in addition to addressing the reviewers’ comments, the text has been substantially revised to reflect the following:

Main results

(1) Metaplasticity enables synapses that undergo both LTP and LTD to ultimately express just one plasticity outcome (either LTP or LTD).

(2) Metaplasticity in the LTP threshold allows LTD to be expressed, and vice versa. (That is, the threshold regulating one plasticity process allows the expression of the opposite plasticity process.)

Reason for using the FBP and NFBP

The reason why the FBP and NFBP are particularly useful to demonstrate the thresholds’ roles is that the patterns in the tasks share features. (For example, in the FBP, the feature ‘strawberry’ is shared between both ‘red strawberry’ and ‘yellow strawberry’.) The synapses for these shared features experience precisely such competing LTP and LTD processes where the role of metaplasticity becomes evident. Specifically, the role of the LTD threshold is visible in shared synapses that need to be strengthened during learning (such as the shared ‘strawberry’ synapses in the FBP), while the LTP threshold’s role is visible in shared synapses that need to be weakened (there are no such synapses in the FBP, but there are in the NFBP, which is why it is needed in this article). In addition, feature binding is relevant for the striatum (now described in the introduction).

In the first version of the article there are sentences that are likely confusing and misleading regarding the goal of the study, and these have been removed (lines 98-100 in the tracked changes file).

The revised article now contains 4 new main figures and 15 new figure supplements prompted by the reviewers’ comments, thus expanding the scope of the study and hopefully clarifying its content, the mechanisms, and the conclusions.

Finally, the question whether this rule can solve the NFBP with excitatory synapses alone is being addressed in a new, ongoing study, as written at the end of the Discussion section in the first version of this article. The new study tests 100+ SPN models (71 dSPN and 34 iSPN models differing in ion channel composition, with two different morphologies), different locations of the synaptic clusters along the dendrites (from proximal to distal), and two different learning regimes (suprathreshold – where the neuron initially spikes for all patterns, and subthreshold – where the neuron is initially silent for all patterns, as in this study) containing both clustered and distributed synapses in the same setup. Where necessary, preliminary results from this study are attached in the responses.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This computational modelling study addresses the important question of how neurons can learn non-linear functions using biologically realistic plasticity mechanisms. The study extends the previous related work on metaplasticity by Khodadadi et al. (2025), using the same detailed biophysical model and basic study design, while significantly simplifying the synaptic plasticity rule by removing non-linearities, reducing the number of free parameters, and limiting plasticity to only excitatory synapses. The rule itself is supervised by the presence or absence of a binary dopamine reward signal, and gated by separate calcium-sensitive thresholds for potentiation and depression. The author shows that, when paired with a strong form of dendritic non-linearity called a "plateau potential" and appropriate pre-existing dendritic clustering of features, this simpler learning mechanism can solve a non-linear classification task similar to the classic XOR logic operator, with equal or better performance than the previous publication. The primary claims of this publication are that metaplasticity is required for learning non-linear feature classification, and that simultaneous dynamics in two separate thresholds (for potentiation and depression) are critical in this process. By systematically studying the properties of a biophysically plausible supervised learning rule, this paper adds interesting insights into the mechanics of learning complex computations in single neurons.

As mentioned in the introductory response above, the goal of the article was not to solve the NFBP, but to study the role of metaplasticity. The text has now been substantially revised to reflect that. One of the primary claims that “metaplasticity is required for learning non-linear feature classification, and that simultaneous dynamics in two separate thresholds (for potentiation and depression) are critical in this process” is now removed from the abstract. Instead, the abstract now focuses on the main results regarding the role of metaplasticity, as well as the results which arose from addressing the reviewers’ comments. However, I guess I should note that to be able to study the role of metaplasticity using the FBP and the NFBP, it was first necessary to have a rule that solves these tasks – that allows to later observe the effects of systematically fixing or modifying parameters in the rule. Another aspect which may have added to the confusion about the study’s goal may be due to the NFBP being a complex task requiring supralinear dendritic integration. Because of this, plateaus have received significant attention in the article, possibly diverting from the main focus. This is also now clarified in the article.

Strengths:

The simplified form of the learning rule makes it easier to understand and study than previous metaplasticity rules, and makes the conclusions more generalizable, while preserving biological realism. Since similar biophysical mechanisms and dynamics exist in many different cell types across the whole brain, the proposed rule could easily be integrated into a wide range of computational models specializing in brain regions beyond the striatum (which is the focus of this study), making it of broad interest to computational neuroscientists. The general approach of systematically fixing or modifying each variable while observing the effects and interactions with other variables is sound and brings great clarity to understanding the dynamic properties and mechanics of the proposed learning rule.

It would indeed be great if this rule facilitates similar studies in other neuron types. The rule requires at least qualitatively accurate calcium dynamics, which at the moment are not widely available for other neuron types (but will likely appear in the future).

Weaknesses:

General notes

(1) The credibility of the main claims is mainly limited by the very narrow range of model parameters that was explored, including several seemingly arbitrary choices that were not adequately justified or explored.

The parameter range has now been expanded to address all comments below.

(2) The choice to use a morphologically detailed biophysical model, rather than a simpler multicompartment model, adds a great deal of complexity that further increases uncertainty as to whether the conclusions can generalize beyond the specific choices of model and morphology studied in this paper.

Regarding the plasticity rule and the role of metaplasticity, the conclusions should hold if the calcium dynamics of other (simpler or detailed) neuron models is qualitatively similar (i.e. shows the same monotonicity of “stronger synaptic input – stronger calcium”, and not something like Figs. 12A, B for which the rule was not tested).

As to whether the NFBP can be solved, that is being addressed in the new study with 100+ neuron models (71 dSPN models and 34 iSPN models, and two morphologies: one for the dSPNs and another for the iSPNs). So far, the results show that the important ingredient is the threshold nonlinearity provided by the plateau potential (both dSPNs and iSPNs exhibit this nonlinearity, irrespectively of where the synaptic cluster is located, see Author response image 1).

Also, plateaus can be evoked in passive SPN dendrites (as stated in the methods in lines 916-919, by “turning off” ion channels in the computational model as in Fig. S7 of Du et al. (2017) (see list of references provided)). Although plateaus are somewhat modified by active conductances, the main behavior important for the NFBP is given by NMDARs. The most striking contributions of the other ion channels in SPNs are the low resting potential around -85 mV, delayed first spike under current injection and strong inward rectification. Basically, SPNs require more input to be stimulated compared to other neurons that lack these properties. So, other neurons with NMDAR-dependent nonlinearities should in principle be able to solve the same task, but perhaps needing less inputs (provided dendritic integration is sufficiently supralinear – see response to comment (2) under Reviewer #2 (Recommendations for the authors)).

(3) The requirement for pre-existing synaptic clustering, while not implausible, greatly limits the flexibility of this rule to solve non-linear problems more generally.

In my view, the limitation of this rule is that there is no mechanism for structural plasticity with which clusters could be “grown”. For example, Hedrick et al. 2022 demonstrate that during learning in the motor cortex, existing functional clusters are “enlarged” by growing new spines. Devising a biologically realistic rule for structural plasticity is a separate research project, which would be very interesting to do.

In any case, to solve the NFBP with excitatory synapses alone, supralinear voltage elevations are necesssary (Tran-van-Minh et al. 2015). When it comes to NMDAR-dependent supralinear integration, clustering is basically necessary, within a smaller, e.g. 20 micron dendritic stretch, or more loosely, within a single dendritic branch (Losonczy and Magee, 2006; Branco et al. 2010). Also, synaptic clustering is quite present across different brain regions (such as the sensory and motor cortices, pallium, striatum, hippocampus, brainstem, the developing cortex, and across species, e. g. see the introduction of Kirchner and Gjorgjieva, 2021), so I suppose it is not that implausible. Inputs from motor cortex to striatum are also clustered (Hwang et al. 2022).

(4) In order to claim that two thresholds are truly necessary, the author would have to show that other well-known rules with a single threshold (e.g., BCM) cannot solve this problem. No such direct head-to-head comparisons are made, raising the question of whether the same task could be achieved without having two separate plasticity thresholds.

Although the goal of the study was not to solve the NFBP, this is a very interesting question related to the question “what is the use of having two separate thresholds for plasticity”? I have added simulations in which the rule is modified to use a single calcium threshold instead, showing that the FBP, NFBP, and reversal learning are solved just as well (Fig. 12 and Figure 12 – figure supplements 1 – 4). The results show that two calcium thresholds allow for separate control over the LTP and LTD processes (lines 687-706).

Specific notes

(1) Regarding the limited hyperparameter search:

(a) On page 5, the author introduces the upper LTP threshold Theta_LTP. It is not clear why this upper threshold is necessary when the weights are already bounded by w_max. Since w_max is just another hyperparameter, why not set it to a lower value if the goal is to avoid excessively strong synapses? The values of w_max and Theta_LTP appear to have been chosen arbitrarily, but this question could be resolved by doing a proper hyperparameter search over w_max in the absence of an upper Theta_LTP.

Thank you for raising this question – it is closely related to the very important question of when to stop updating the weights. Before providing the response, I should clear up any confusion made due to an error in notation. In this study, , and , meaning that during learning the weights can increase up to twice (up to 100% of) the initial value, and can decrease down to 1% of the initial value. Currently, it says w_max = 2, and w_min = 0.01, which is a mistake, and possibly a reason why the chosen values seem arbitrary.

The reason for introducing the upper threshold θ_LTP is most easily seen in the parameter scan for w_max done in the absence of θ_LTP (Figure 4 – figure supplement 4) – it is very difficult to choose a value for w_max with which all three tasks will be solved (FBP with linear integration, i.e. distributed synapses, the FBP with supralinear integration, i.e. clustered synapses, and the NFBP). Put differently, if there is a range of w_max values which solves all three tasks, it is very narrow. So, θ_LTP is introduced to solve all three cases without specially tuning w_max.

The following is a description of the results in Figure 4 – figure supplement 4, which is also present in the article in lines 383-396. The reason why a single preset value for w_max does not work is that distributed synapses sum only linearly at the soma, while clustered synapses sum supralinearly. This means that to trigger somatic spiking, the distributed synapses need to be strengthened more compared to clustered synapses. Concretely, this means that a is needed to solve the FBP with linear integration (distributed synapses), but it is already too strong to solve the NFBP (Figure 4 – figure supplement 4, column four: top panel shows that FBP with linear integration is solved, while the bottom panel shows the average performance for the NFBP is right at the border – pink line aligns with the dashed line). On the other hand, is enough in the FBP with clustered synapses and the NFBP to trigger glutamate spillover and a plateau potential, which drives somatic spiking (Figure 4 – figure supplement 4, column two). However, it is not enough to solve the FBP with linear integration. Larger values for w_max increase the performance on the FBP with linear integration, but lower the performance on the NFBP due to spiking for the irrelevant patterns (especially visible once ). As said, in this parameter scan, only the value solves all three tasks, with borderline performance on the NFBP (it is arguable whether the borderline performance means the NFBP is solved). This suggests that if a range of values for w_max exists which solves all three tasks, it is very narrow.

With the settings used in the study, the w _max threshold for triggering glutamate spillover is a number between 1.2 and 1.3 with many decimals – 1.230769231. A possibility could be to program spillover to always occur at , but this is also not a general solution. For example, other dSPN models from the model library in Lindroos et al. (2021) have different excitability, and that would mean a different, specific value of w_max would be needed for each neuron model.

θ_LTP is thus a solution that prevents “over-excitation” in a dendrite. The logic is that synapses in a cluster do not need to be as strong as distributed synapses to be effective in exciting the neuron. θ_LTP ensures that once plateaus appear, synapses are not strengthened further. This allows using the same value across all scenarios, i.e. avoiding tuning of w_max or tuning the number of synapses representing the features. (Also, preliminary results show this works well in the new study which tests all dSPN and iSPN models in the model library.) As for the value of θ_LTP, it can be set anywhere in the “blank” region in Fig. 2C₃ where the supralinear jump in [Ca]_NMDA occurs. What is important is that [Ca]_NMDA evoked by a plateau should be above θ_LTP – then no more strengthening will occur once plateaus can be evoked.

(b) The author does not explore the effect of having separate learning rates for theta_LTP and theta_LTD, which could also improve learning performance in the NFBP. A more comprehensive exploration of these parameters would make the inclusion of theta_max (and the specific value chosen) a lot less arbitrary.

I am not sure I have understood this comment properly, but hopefully this response addresses it adequately. In fact, the computer code does use separate variables for the learning rates for θ_LTP and θ_LTP, but for simplicity, they are set to the same value. In this response I have included some simulations in which they are set to different values (Author response image 2), but to understand their effect it is better to read the response to the comment under c) first. The metaplasticity rates determine how fast the synaptic weights are stabilized, i.e. how long the time window is where the synapses are “flexible”. When the thresholds reach the calcium amplitudes, the weights are “locked”.

If the metaplasticity rates are too low, the weights take a longer time to stabilize and solving the tasks takes a long time (Figure 4 – figure supplement 10 from the response to c). If they are too high, weights are quickly stabilized and, in the case of weakened synapses, prematurely so, leading to worse performance on the NFBP due to spiking for the irrelevant patterns. (Figure 4 – figure supplement 11).

One can use different values for the metaplasticity rates, as in the examples in Fig. 2 , and this affects the speed of learning. A large η_θLTD = 20 quickly prevents the LTD process (Figs. 2D₁, D₂), causing faster synaptic strengthening, but also quickly limiting weakening (Figs. 2B₁, B₂) – as a result, after learning, the neuron spiked for an irrelevant pattern (Fig. 2A₁). Conversely, a large η_θLTD = 20 quickly prevents the LTP process (Figs. 2C₃, C₄), prolonging synaptic strengthening and allowing faster weakening (Figs. 2B₃, B₄) – as a result, the NFBP is solved, but takes a longer time. However, this does not remove the need for using an upper threshold θ_LTP. If I have not understood the comment properly, please let me know so I can address it further.

(c) Figure 4 Supplements 3-4: The author shows results for a hyperparameter search of the learning rule parameters, which is important to see. However, the parameter search is very limited: only 3 parameter values were tried, and there is no explanation or rationale for choosing these specific parameters. In particular, the metaplasticity learning rates do not even span one order of magnitude. If the author wants to claim that the learning rule is insensitive to this parameter, it should be explored over a much broader range of values (e.g., something like the range [0.1-10]).

Thank you for bringing this up! I have expanded the parameter scan for both the learning rate η (Figure 4 – figure supplements 7 and 8) and the metaplasticity rate η_θ (Figure 4 – figure supplements 10 and 11) to cover three orders of magnitude (when taken together with the results already present in the article in Figure 4 – figure supplements 6 and 9).

Figure 4 – figure supplements 7 and 8: The learning rate η was was tested with the values 0.1 and 20. This shows a known result in other plasticity rules, which is that if the learning rate is too fast or too slow, learning is not successful or is too slow. For η = 0.1, learning takes very long (around 2000 patterns for FBP with linear integration), and for the NFBP is at the borderline score (Figure 4 – figure supplement 7E). As the LTD thresholds rise, they will prevent the slowly decreasing synaptic weights from decreasing sufficiently. For η = 20, the weight updates are too large and no pattern is stored because calcium quickly falls below the thresholds as a result of such large weight updates (Figure 4 – figure supplement 8E). This leaves some intermediate range of learning rates that “works”. (The three values {0.4, 0.85, 1.7} that were tested in Figure 4 – figure supplement 6 are roughly a factor of 2 apart.) Results are described in more detail in lines 409-414 of the revised article.

Figure 4 – figure supplements 10 and 11: The metaplasticity rate η_θ was tested with the values 0.2 and 20. This further demonstrates the role of metaplasticity as a “lock” on the learning process. η_θ determines how fast the weights stabilize (i.e. how long they remain flexible for learning). With the value η_θ = 0.2 the weights take a longer time to stabilize, because it takes a long time for the thresholds to reach the calcium amplitudes (Figure 4 – figure supplement 10). This affects the learning time on the NFBP only. In contrast, with the value η_θ = 20, the thresholds quickly reach the calcium amplitudes, and quickly stabilize the weights. While the neuron does learn to evoke plateaus, the weakened synapses are stabilized too early, resulting in spikes for the irrelevant patterns and lowering the performance on the NFBP. (Figure 4 – figure supplement 11). Results are described in more detail in lines 415-429 of the revised article.

(2) Regarding the similarity to BCM, the author would ideally directly implement the BCM learning rule in their model, but at the least the author could have shown whether a slight variant of their rule presented here can be effective: for example having a single (plastic, not fixed) Cadependent threshold that applies to both LTP and LTD, with a single learning rate parameter.

- As mentioned above, this is also a very interesting question, related to the important question of “what is the use of having two separate calcium thresholds?”. I have added simulations according to your second suggestion – using a single calcium threshold that applies to both LTP and LTD. A single threshold can solve the FBP, NFBP, and reversal learning equally well (Fig. 12 and Figure 12

- Figure Supplements 1, 2). This indeed raises the question what are two separate thresholds useful for? Figure 12 – figure supplement 3 shows that when keeping the single calcium threshold fixed, none of the shared synapses stabilize. Comparing this to Figs. 5 and 6, where the LTP and LTD threshold are kept fixed one at a time, it shows that having two separate thresholds allows separate control over the LTP and LTD processes.

I also tried an implementation of the BCM rule using a nonlinear (quadratic) function in the metaplasticity rule for updating the threshold:

where c_norm is a normalization constant set to 80 μM for [Ca]_NMDA and 20 μM for [Ca]_L-type (close to the maximal concentrations achieved throughout the article). In the BCM rule, a nonlinear function is necessary to prevent runaway growth (or collapse) of the weights. So, in principle, w_max and θ_LTP should be unnecessary with this quadratic metaplasticity rule. However, even though the weights seem to stabilize (around a high value), they are too strong and plateaus are triggered for all patterns (see Author response image 3). It is possible that only a narrow range of parameters in the quadratic function will allow weights to stabilize at appropriate values, similarly to the narrow range in w_max in the absence of θ_LTP (as described for comment 1a) above).

Below are some questions about how to “correctly translate” the BCM rule from its formulation for rate-coded inputs to a formulation for sparsely-coded inputs which are used in this article. I did not address these questions in detail. The following is meant for readers who might be interested in pursuing these questions.

Questions when translating the BCM rule for rate-coded inputs to a rule for sparsely-coded inputs:

The similarity of this study’s rule to BCM is only qualitative – a sliding threshold was added that follows an indicator of synaptic activity (in this study it is the amplitude of the calcium concentration). The original BCM rule is defined for rate-based synapses, and its threshold θ is a nonlinear function of the average (synaptic) activity:

where p and c₀ are positive constants, and c) is the average activity. The threshold θ is updated as the average activity c) changes (the averaging being done over a time interval) [1]. Changes in the rate-coded inputs drive changes in c) continuously, thus changing θ over time.

(1) What should be chosen as the average activity c̅ ?

In the BCM model, the average activity, and consequently the threshold θ, are global for the whole neuron (which is represented just by its firing rate), meaning that θ is the same for all synapses. In a morphologically realistic neuron model, what should be the average activity? Especially in the case of supralinear integration occuring in a dendrite, one could also consider average activities in dendrites. In the dSPN model, the calcium concentration decays by the time the next pattern arrives, so one probably needs another, low-pass filtered variable of the calcium concentration (or voltage), with a much longer time constant than that of the calcium decay. (I have chosen to slide the thresholds towards the amplitude of the calcium evoked by a pattern, which could be viewed as an approximation of such a long-lived variable. This is one possible “translation” of this aspect of the BCM rule.)

(2) How to update the chosen indicator of activity c̅?

Assuming an adequate indicator is chosen (different from the calcium amplitude that I have chosen), how should it be updated when using sparsely-coded inputs? Should it evolve continuously, or only when the sparsely-coded inputs are active? If updated continuously, it should not decay very fast when synapses are inactive (not activated by a pattern), while still change fast enough to detect changes in synaptic weight occuring due to learning. (I have chosen to slide the thresholds towards the evoked calcium amplitude only when synapses have been activated, so this is also one way of “translating” this second aspect.)

(1) which in the BCM article is replaced with the average over the input’s probability distribution

(3) What nonlinear function to use to update the threshold?

The BCM rule allows any function with p > 1, but how fast the synapses stabilize will likely depend on c₀, the normalization constant in the nonlinear function, and the power p. The role of the nonlinear function is to ensure stability of the synaptic weights (prevent runaway growth), meaning no θ_LTP nor w_max should be needed. However, achieving high performance on all three tasks might still require a specific tuning of these parameters, as w_max does if no θ_LTP is used. That is, these parameters will need to be chosen such that the threshold quickly goes up once a plateau appears, so weights are not allowed to strengthen further. Having in mind that there is a very narrow range in w_max where all three tasks are solved, there might similarly be only a narrow range in c₀ and p.

Since the goal of the article was to study the role of the two thresholds (not to optimize the rule’s parameters on the three tasks), I have only tried a quadratic function for the metaplasticity rule, and did not search for a region of parameters that could work.

(3) This paper is extremely similar (and essentially an extension) to the work of Khodadadi et al. (2025). Yet this paper is not mentioned at all in the introduction, and the relation between these papers is not made clear until the discussion, leaving me initially puzzled as to what problems this paper addresses that have not already been extensively solved. The introduction could be reworked to make this connection clearer while pointing out the main differences in approach (e.g., the important distinction between "boosting" nonlinearities and plateau potentials).

The last paragraph in the introduction now makes this comparison, highlighting the differences in approach, and mainly emphasizing that the goal of the two studies is different. The open question that this study addresses is to pinpoint the roles of the two calcium thresholds (present in dSPNs) in learning. Also see the response to the similar comment (1) from Reviewer #2 (Public review): Weaknesses.

(4) The introduction is missing some citations of other recent work that has addressed single-neuron non-linear computation and learning, such as Gidon et al (2020); Jones & Kording (2021).

Thank you for mentioning this. Since the first version of the article caused confusion regarding the goal of the study (which is to study metaplasticity), I avoided focusing on nonlinear computation in the introduction, and instead added these references to the Discussion (in line 850 the section regarding nonlinear computation).

(5) Figure 1: The figure prominently features mGluR next to the CaV channel, but there is no mention of mGluR in the introduction. The introduction should be updated to include this.

Thank you for noticing this. It is now included in the introduction in lines 50-53.

(6) Could the author explain why there is a non-monotonic increase/decrease in the [Ca]_L in Figure 2B_4? Perhaps my confusion comes from not understanding what a single line represents. Does each line represent the [Ca] in a single spine (and if so, which spine), or is each line an average of all the spines in a given stim condition?

Thank you for noticing this, that information was missing from the figure caption. The line is from a single spine which is placed at a random location on a randomly chosen dendrite. Because each line comes from a different trial with a different number of synapses, the spine it corresponds to is in a different location, resulting in different voltage and different calcium signals when using distributed synapses. (Clustered synapses are placed at approximately the same somatic distance, despite being on a randomly chosen dendrite, so this effect does not appear in Figs. 2C₃, C₄). The figure caption has been updated accordingly.

(7) Row 124 (page 4): L-type Ca microdomains (in which ions don't diffuse and therefore don't interact with Ca_NMDA) is a critical assumption of this model. The references for this appear only in the discussion, so when reading this paper, I found myself a bit confused about why the same ion is treated as two completely independent variables with separate dynamics. Highlighting the assumption (with citations) a bit more clearly in the results section when describing the rule would help with understanding.

Thank you for pointing this out! This assumption is now clearly stated with citations in lines 174176 when characterizing the plateaus in SPNs, and lines 205-207 when describing the rule (in addition to the existing description in the Methods).

(8) Row 149 (page 5): The current formulation of the update rule is not actually multiplicative. The fact that the update is weight-dependent alone does not make it a multiplicative rule, and judging by equation (1) it appears to simply be an additive rule with a weight regularization term that guarantees weight bounds. For example, a similar weight-dependent update is also a core component of BTSP (Milstein et al. 2021; Galloni et al. 2025), which is another well-known *additive* rule. An actual multiplicative rule implies that the update itself is applied via a multiplication, i.e. w_new = w_old * delta_w

For an example of a genuinely multiplicative rule, see: Cornford et al. 2024, "Brain-like learning with exponentiated gradients"). Multiplicative rules have very different properties to additive rules, since larger weights tend to grow quickly while small weights shrink towards 0.

Thank you for explaining the difference between “additive” and “multiplicative”. I have removed the word “multiplicative” from the description of the rule, as it is not necessary. (In the first version of the manuscript I followed the nomenclature by Gütig et al. (2003), which refers to the weight-dependent update as a multiplicative rule, while an additive rule has no weight dependence in the equation for Δw, which is Eq. 2 in Gütig et al. (2003).)

(9) Equation 1 (page 5): Shouldn't the depression term be written as: (w_min - w)? This term would be negative if w is larger than w_min, leading to LTD. As it is written now, a large w and small w_min would just cause further potentiation instead of depression.

Yes, a minus sign is missing in front of the depression term. Thank you for noticing this! It is now corrected.

(10) In the introduction, the teaching signal is described in binary terms (DA peak, or DA pause), but in Equation 1, it actually appears to take on 3 different values. Could the author clarify what the difference is between a "DA pause" and the "no DA" condition? The way I read it, pause = absence of DA = no DA

Yes, the “no DA” condition should say “baseline DA”. The DA signal does indeed take three different values. In the striatum, there is a baseline tone of dopamine. The DA peaks are transient increases from this tone, and the DA pauses are transient decreases. The basal dopamine level is now introduced in line 113 of the introduction, so that Eq. 1 should be clearer. In the computer code, DA is in effect a ternary signal, with three values, +1 for DA peak, -1 for DA pause, and 0 for baseline DA.

(11) Figure 3: In these experimental simulations, DA feedback comes in 400ms after the stimulus. The author could motivate this choice a bit better and explain the significance of this delay. Clearly, the equations have a delta_t term, but as far as the learning algorithm is concerned, it seems like learning would be more effective at delta_t=0. Is the choice of 400ms mainly motivated by experimental observations? On a related note, is it meaningful that the 200ms delta_t before the next stimulus is shorter than the 400ms pause from the first stimulus? Wouldn't the DA that arrives shortly before a stimulus also have an effect on the learning rule?

These time windows were chosen purely to keep the simulations as short as possible (since a computing cluster was used to run many trials). In reality, two patterns would probably arrive after a longer time window, as an animal should reach for the pattern (and in the case of these fruit patterns, eat it) which would last on the order of seconds. However, the calcium signals that trigger plasticity in these simulations are shorter than that (Figs. 2B_3,4, 2C_3,4), and only the amplitude of the signal is used to trigger plasticity. This gives an opportinity to not have to wait for several seconds between two patterns arrive (as might occur in reality), but shorten that interval and so shorten the simulation time. (This is now stated in lines 245-247 in the Results section where the rule is described, pointing to the Methods for more detials.)

Hence, the dopamine feedback is given at 400 ms after a pattern appears because the calcium amplitudes would have surely occurred by then (even if a plateau were evoked, see Figs. 2B_3,4, 2C_3,4). Similarly, the next pattern is given at 600 ms because the calcium signals would have decreased to baseline by then. (This is already explained in the Methods section in lines 1101-1117). The key implicit assumption here is that the calcium amplitude is somehow remembered by the synaptic circuitry. In experiments, dopamine feedback up to 2 seconds after synaptic stimulation can cause LTP, so it is OK to assume this (Yagishita et al., 2014). However, dopamine signaling before synaptic stimulation has no effect (Yagishita et al., 2014). (This assumption is now clearly stated in the Methods in lines 902-906.)

Lastly, in this rule, if the dopamine feedback coincides with the pattern, then whatever calcium levels were reached at that time would be used to check whether the thresholds are crossed, and these will most likely not be the maximal calcium levels (these are reached some time later, as seen in Figs. 2B_3,4, 2C_3,4).

One last note is that from your comment I got the impression that you may have understood Δt to be the time until dopamine feedback is provided. It is not, it is simply the time step in the simulation (already stated in line 211; now an additional explanation is added in lines 211-214, just in case).

(12) Figure 4C: How is it possible that the theta_LTP value goes higher than the upper threshold (dashed line)? Equation 3 implies that it should always be lower.

This is also just a choice of implementation: θ_LTP evolves independently of θ_LTP, reflecting an implicit assumption that different molecular machinery implements θ_LTP and θ_LTP. This assumption is similar to the findings in Figs. 4, 5 in Ngezahayo et al. 2000, where in weakened synapses the voltage threshold for LTD can increase (to -20 mV) above the voltage threshold for LTP (at -30 mV). (This assumption is now explicitly written out in lines 316-322.)

(13) Row 429 (page 11): The statement that "without metaplasticity the NFBP cannot be solved" is overly general and not supported by the evidence presented. There exist many papers in which people solve similar non-linear feature learning problems with Hebbian or other bio-plausible rules that don't have metaplasticity. A more accurate statement that can be made here is that the specific rule presented in this paper requires metaplasticity.

Yes, that is what is meant with that statement – that this specific rule requires metaplasticity. The text has been corrected. Thank you for noticing this.

(14) The methods section does not make any mention of publicly available code or a GitHub repository. The author should add a link to the code and put some effort into improving the documentation so that others can more easily assess the code and reproduce the simulations.

The link to the code is given in the Data availability statement. However, this statement might not appear in the manuscript files that you are receiving (it is available online and in the article PDF downloadable from eLife), so I am providing the link here, as well. The Readme.md file now describes the code, and how to reproduce figures in the article.

https://github.com/danieltrpevski/Plasticity/tree/metaplasticity

Reviewer #2 (Public review):

Summary:

The manuscript proposes interesting synaptic plasticity rules grounded in experimental data. Its main features are:

(1) plasticity depends on local calcium concentration driven by presynaptic activity and is independent of somatic action potentials,

(2) the rules incorporate metaplasticity, and

(3) they demonstrate how a single neuron could address the feature-binding problem at the dendritic level.

The work extends a previous study (https://doi.org/10.7554/), to which the author also contributed.

The author models two calcium thresholds (LTP/LTD) from two different calcium sources (NMDA/VGCC), and these thresholds are flexible (metaplasticity rule, similar to BCM), which is claimed to be necessary for successful learning of both FBP and NFBP (linear and nonlinear feature binding problem with 1 or 2 patterns). The role of each threshold seems to be opposite and complementary. One extra condition has been added: an upper threshold for LTP. This threshold serves to stop synaptic strengthening once synapses are strong enough to evoke a plateau. With that, synapses are not strengthened to the maximal value, avoiding strong supralinear integration for irrelevant patterns.

This is summarizes the learning rule well. What I should probably add is that, as mentioned in the introductory response, the article’s first version may cause some confusion about the study’s goal. The goal was to study the role of metaplasticity in the two thresholds, not to solve feature binding in particular. Nevertheless, feature binding is a very useful task to demonstrate the roles of each threshold because the patterns share features: the synapses for the shared features experience both LTP and LTD, and metaplasticity is necessary to express (or to converge to) just one plasticity state (either LTP or LTD). More specifically, the threshold for one plasticity process (e.g. LTD) is necessary to express the opposite process (e.g. LTP). However, to be able to study metaplasticity using feature binding, a prerequisite is to have a rule that can solve it. (So, in that sense, it was first necessary to show that the rule solves the tasks before exploring the roles of metaplasticity. The article has been revised to clearly state this.)

Strengths:

The current model implements not only local synaptic plasticity but also metaplasticity and solves the FBP at the dendrite level. Another strong aspect of the model is that metaplasticity in the LTD threshold protects strengthened synapses from weakening. In this way, as the author mentioned, metaplasticity is able to protect learned patterns from being forgotten or weakened and prevent irrelevant patterns from being stored. This is a nice modelling example of metaplasticity being helpful in preventing the catastrophic interference or forgetting (as has been explicitly discussed in a recent article https://doi.org/10.1016/j.). The author might want to briefly mention or emphasize this aspect of the model, which might be interesting also for the AI community.

This is a great suggestion, thank you! I have instead emphasized a related aspect of the model: that it can solve the plasticity-stability dilemma (when taking away the closed-loop implementation of metaplasticity). I did not focus on catastrophic forgetting, because in machine learning it has a slightly more specific meaning: forgetting that occurs in sequential learning of different tasks. Instead, I exemplified the plasticity-stability dilemma using reversal learning (the reward policy is switched in the middle of the simulation), which can be viewed as a special case of sequential learning of opposite tasks. So, strictly speaking, there is no demonstration that metaplasticity prevents catastrophic forgetting (in the more general sense), but there is a demonstration that it retains (stabilizes) what has been learned (within the same task). The latter does suggest that metaplasticity could help prevent catastrophic forgetting, as well.

Weaknesses:

(1) What is novel in the current paper as compared to Khodadadi et al. eLife 2025? That is not completely clear and should be made clearer. Is it only a minor difference related to the fact that the new learning rule has metaplasticity in both calcium thresholds and is simpler? This seems to be just an incremental increase in knowledge/methods. Can the author defend his paper against this point from the „devil's advocate"? How is the conclusion of the author in the abstract that „metaplasticity in both thresholds is necessary" reconcilable with his previous publication (Khodadadi et al. eLife 2025), in which only metaplasticity in one threshold was successful in solving the nonlinear feature binding problem?

Thank you for raising this question, since the answer was not clear in the first version. The study may be an incremental increase in methods, but is (in my view) a solid increase in knowledge, giving concrete new insights into metaplasticity (an area that is still comparatively little understood). The two main conclusions are:

(1) In synapses that are exposed to both the LTP and the LTD process, metaplasticity is necessary to ultimately express just one of them (converge to either LTP or LTD).

(2) Metaplasticity in the threshold regulating one plasticity process is necessary for expressing the opposite process (metaplasticity in the LTD threshold is necessary for expressing LTP, and vice versa).

The article has been substantially revised to clearly state these main conclusions (as well as the study’s goal), while a full list of all conclusions is given in points 1-7 the Discussion.

The conclusion in the abstract that „metaplasticity in both thresholds is necessary" is stated too generally, and it was meant to refer to this rule only. I have now removed it from the abstract, since the study’s goal was not to solve feature binding. Instead, the focus is on the two conclusions above as well as other conclusions obtained from expanding the study with reversal learning and using a single threshold (prompted by the comments from yourself and reviewer #1).

Lastly, the differences compared to Khodadadi et al. 2025 (eLife) are:

(1) Yes, the rule is simpler and has metaplasticity in both calcium thresholds, instead of just one in Khodadadi et al. 2025 that operates according to a different mechanism (where the threshold, along with the entire LTP plasticity kernel, moves in a direction opposite of the calcium signal).

(2) Plateau potentials are used here, versus the “boosting” nonlinearities in Khodadadi et al. 2025.

(3) The most detailed calcium diffusion model to date for SPNs is implemented in this study (by Dorman et al. (2018)). This was a necessary addition to avoid non-monotonous increases in calcium (shown in Fig. 13A, B). No calcium diffusion between neuronal compartments is implemented in Khodadadi et al., 2025. This is indeed a small methodological difference, but not trivial to implement.

The relation to Khodadadi et al., 2025 is now stated both in the introduction in lines 137-144, and at greater length in the discussion in lines 856-870.

Perhaps I should note that the two learning rules (this one and that in Khodadadi et al. 2025) developed in parallel, this one being based on formulations similar to Gütig et al. 2003 by adding metaplasticity, while the rule in Khodadadi et al. 2025 was inspired from the ideas in Schiess et al. (2016) and Urbanczik and Senn (2014) (see list of references provided). The two studies have different goals (and in that sense one was not meant to be an extension of the other):

- Khodadadi et al. (2025) studies whether the NFBP can be solved by SPNs,

- this article studies the role of metaplasticity in the two calcium thresholds that exist in dSPNs; it uses feature binding as a task because the role of metaplasticity is exposed precisely by the shared features in the task (they cause shared synapses to undergo competing LTP and LTD, and metaplasticity is necessary to direct synapses into just one outcome); importantly, feature binding is also relevant for the striatum (now described in the introduction in lines 126-136)

Finally, to obtain the conclusions in this study about the roles of the two thresholds, it was necessary to devise a suitable rule. They cannot be obtained neither with the rule in Khodadadi et al. 2025, nor with any other rule, because none have a formulation with two separate thresholds for LTP and LTD. Phrased more generally, one needs a new/different rule (new/different assumptions) to obtain new/different conclusions, even if the new rule may be related to existing ones. That said, a rule with a single threshold would have reached conclusion 1. above, as is now shown in the article in Fig. 12 and Figure 12 – figure supplements 1 – 4, but SPNs have two thresholds, prompting the use of a rule with two thresholds. Also, although not demonstrated with the cascade model (by Fusi et al. (2005) and its extensions), conclusion 1. should be obtainable with it, and is implied by the dynamics of the cascade model (which uses one threshold to control transitions between strong and weak synapses). More on the cascade model is given below and in the revised article.

Hopefully that provided a clearer answer. If you have more questions, please let me know so I can try to clarify further.

(2) As far as I can judge without testing the model, metaplasticity causes thresholds to monotonically increase during systematic pattern presentation, which stabilizes weights and allows pattern separation. Due to the closed-loop nature of the current implementation, where metaplasticity only happens if plasticity happens, this also effectively locks patterns in place. However, flexible learning is an essential mechanism for survival. Imagine a mutation event takes place and bananas suddenly become red and/or strawberries turn yellow. It seems that the current model would be unable to adapt to these new patterns even if rewards were to be shifted. While out of the scope of the study, due to its importance, I feel that pattern shifting/relearning should at least be briefly discussed. How could the model be improved to allow relearning?

This is a very important question, and I think it is in fact within the scope of the study, so it is now addressed using reversal learning as a task (the reward policy is switched in the middle of the simulation, after the FBP and NFBP are learned). As you pointed out, the closed-loop formulation of metaplasticity effectively locks the patterns in the dendrites, and reversal learning cannot be solved (Fig. 9). On the other hand, if the conditions for metaplasticity are relaxed by allowing any calcium levels to trigger metaplasticity (i.e. no longer have a closed-loop formulation requiring that [Ca]_NMDA or [Ca]_L-type be above their thresholds), reversal learning in both the FBP and NFBP is solved (Fig. 10 and Figure 10 – figure supplements 1 – 3). (Note that [Ca]_NMDA or [Ca]_L-type still need to be above their thresholds for plasticity to occur.)

Recommendations for the authors:

Reviewing Editor Comments:

While the reviewers were very positive, they highlighted limitations on the strength of evidence. Addressing these points could help revise this assessment.

Reviewer #1 (Recommendations for the authors):

(1) Framing the problem as "feature binding" is easy to understand, but it's a slightly narrow view of learning in general. Some mention of how NFBP relates to the XOR problem in the introduction would help you relate your solution to the much broader class of computational problems, since XOR is a more fundamental computational primitive. Non-linear feature learning is very general and relates to all machine learning problems and to computations that occur across every brain region.

Since the goal of the study was not to solve the NFBP or feature binding (but to study metaplasticity), the relation of the NFBP to the XOR is put in the Discussion instead (to avoid further confusion about the study’s goal). Nevertheless, this connection is clearly made in the introduction of the new study that uses 100+ SPN models.

(2) Since the requirement for clustered synapses is one of the main limitations of this learning rule, it would help if there were some discussion of how clustering might occur (e.g., whether there are any other related learning rules or mechanisms that might promote clustering, or if you are assuming that this has to occur entirely through developmental wiring).

This is now discussed in lines 817-827 and related to developing a learning rule that would incorporate structural plasticity.

(3) Page 5, row 157: Another potentially relevant citation here is Bittner et al. 2017, showing that a dendritic plateau potential in silent CA1 neurons drives place field formation without any prior spiking activity.

Thank you, that is indeed a very relevant citation here! It is now added in line 222.

(4) Figure 4C: It would be helpful to add a sentence in the figure legend explaining what the dashed lines represent (even though you also mention it in the main text).

Added, thank you!

(5) Across all figures, the author should consider using color combinations that are more colorblindfriendly (e.g., cyan/red). As a R/G colorblind person, I find it slightly difficult to see which line is which in the panels that compare scores in the NFBP.

The panels showing the NFBP scores have been changed throughout the article, and all other figures have been checked. If there are any more difficult color combinations, please let me know.

(6) The conventional, widely used abbreviation for dopamine is "DA", not "Da".

Now changed.

(7) A few typos I spotted in the paper:

(a) Row 117 (page 3): missing parenthesis around citation

(b) Row 173 (page 5): "uner" --> under

(c) Row 248 (page 7): repeated sentence "...are first seen above..."

(d) Row 255 (page 7): "NBFP" --> NFBP

These are now fixed, thank you for reporting them!

Reviewer #2 (Recommendations for the authors):

(1) How are synapses distributed in the nonlinear integration case? Are pattern combinations branch-specific, or are features distributed randomly across the whole dendritic tree? Does this matter in any way? In any case, it should be clarified.

Yes, they are branch-specific. In the NFBP, the feature combinations from Figure 3 – figure supplement 1 (and later from Figure 10 – figure supplement 1) are placed on two dendrites, chosen at random from 8 dendrites, in a 20-micrometre dendritic stretch starting around 120 micrometers away from the soma. 12 different trials are run for each feature combination, meaning that 12 randomly chosen pairs of dendrites were tested for each feature combination. In the FBP, the clusters are placed in one dendrite chosen at random from 8 dendrites, at the same distance from the soma as in the NFBP. This information is now added in the caption of Fig. 3.

The idea behind placing clusters on the same dendrite is that, after learning, two strong clusters will produce a plateau (e.g. ‘red’ and ‘strawberry’), while one strong and one weak cluster will not (e.g. ‘yellow’ and ‘strawberry’), as in Figs. 3C₂, 3C₃ (with the weights shown in Figs. 4B₂, 4B₃). For this the clusters need to be in the same branch, so that two features are “bound” together “into” a larger, plateau-evoking cluster. Also, a strong and a weak cluster should evoke a sufficiently lower somatic amplitude so that any additional noise will not cause somatic spiking. This is assured by the large voltage jump in the plateau (the all-or-none quality of the plateaus, Fig. 2D₁).

If the clusters are distributed randomly on different dendrites, it might or it might not work. Fig. 10 of Oikonomou et al. (2012) shows that dendritic spikes (that individually do not evoke somatic spiking) summate sublinearly at the soma in pyramidal neurons: weak + weak cluster = no spiking (Fig. 10A); strong + strong = no spiking (Fig. 10B); but also strong + strong = spiking (Fig. 10C). To reliably solve the NFBP, a large enough supralinearity is necessary instead, so one should test how the soma integrates dendritic spikes/plateaus in SPNs. As the goal of this study was not to solve the NFBP, this is left for the future (perhaps within the new ongoing study focusing on the NFBP).

(2) To produce dendritic plateau potentials, the model (as in the previously published model - Trpevski et al. 2023) implements glutamate spillover activating extrasynaptic NMDARs. This is an interesting mechanism, but is there empirical evidence supporting this way of generating plateau potentials? Are synaptic NMDARs not sufficient? If not, which experiments support the role of nonsynaptic ones?

This is still an ongoing area of research, indicating that glutamate spillover is regulated by reuptake from glial cells, which could even reverse function and excrete glutamate (Rusakov and Stewart, 2021; Malarkey and Parpura, 2014).

Except for the experiments from Szapiro and Barbour, 2007 showing that climbing fibers in the cerebellum signal to molecular-layer interneurons exclusively through glutamate spillover, there are no other “in-vivo-like” experimental conditions which show that spillover activates extrasynaptic NMDARs (eNMDARs). The strongest other in vitro data come from the following experiments:

(1) Chalifoux and Carter (2011), where glutamate reuptake by transporters was blocked with TBOA, which promoted NMDA spikes evoked by synaptic stimulation, suggesting that glutamate spillover activates eNMDARs. A similar experiment was done in Suzuki et al. (2008), where, in addition, synaptic NMDARs were blocked, leaving only eNMDARs available to trigger plateaus.

(2) Glutamate iontophoresis, which ejects glutamate directly into the extrasynaptic space, activates plateaus once the iontophoretic current is strong enough (Oikonomou et al., 2012), with or without blocking glutamate reuptake (Suzuki et al. 2008).

(3) Repetitive synaptic stimulation is thought to produce glutamate spillover (Suzuki et al. 2008; Oikonomou et al., 2012). For example, two synaptic shocks trigger NMDA spikes, while 5 synaptic shocks trigger plateaus in pyramidal neurons (Oikonomou et al., 2012).

On the other hand, studies that employ glutamate uncaging at spines, which should activate eNMDARs much less, evoke NMDA spikes instead (Losonczy and Magee, 2006; Branco et al. 2010). Compared to plateaus, these have much smaller amplitudes, and the size of the supralinearity (the voltage jump) is much smaller than in the plateaus obtained with glutamate iontophoresis (compare Fig. 3 in Losonczy and Magee, (2006), Fig. 3B in Branco et al. (2010) to Fig. 4C in Oikonomou et al. (2012), Fig. 6 in Oikonomou et al. (2014)).

The reason why glutamate spillover was implemented is precisely this robust all-or-none quality of the plateaus, i.e. the large jump in somatic voltage (Fig. 2D₁) after a threshold level of stimulation (when the stimulus intensity increases in equal amounts). Without spillover, plateaus are graded in amplitude (and duration, Fig. 2B₁ in Trpevski et al. (2023)), and the NFBP cannot be solved (Fig. 6 in Trpevski et al. (2023)).

(3) The check for dependence on initial conditions of theta_LTP/LTD is missing. Especially for the conditions of the thresholds being fixed. How do you decide what fixed value to use? How about having a corresponding limit for weights and not for thresholds? Why is there still an increase in threshold going on even when weights reach the maximum?

The initial conditions for θ_LTP and θ_LTD are also an important question. The idea behind starting with low values of the thresholds (or fixing them to low values) is to make the synapses flexible for learning. One can view metaplasticity’s role as a “lock” on the weights, locking them once learning is done, and unlocking them (making them flexible) when something needs to be learned. Which signals determine when to lock or unlock the weights is what the metaplasticity rule implements, and is insufficiently understood experimentally. In any case, it makes sense to start with flexible synapses (low thresholds) at the beginning of learning; otherwise, no/little learning will take place (Figure 9 – figure supplement 2, the panels for “thresholded” metaplasticity). Throughout the article I choose the initial values of the thresholds to be lower than the calcium evoked by weakened synapses, ensuring that any calcium signal will trigger plasticity (but higher values also work).

Instead of doing a scan over the initial conditions of θ_LTP and θ_LTD, I chose to show the following:

(1) An example with initial threshold values higher than the calcium amplitudes: these “lock” the weights (Figure 9 – figure supplement 2, panels for “thresholded” metaplasticity) from the start and no learning can occur.

(2) An example initialized with high values for the thresholds, but where metaplasticity can be triggered by any calcium amplitudes (no closed-loop in the metaplasticity rule, Figure 9 – figure supplement 2, panels for “relaxed” metaplasticity): here the thresholds adapt and learning can take place afterwards.

This is supposed to illustrate a mechanism that can “unlock” weights. A scan over the initial conditions of θ_LTP and θ_LTD will give the lowest calcium level that the thresholds can be initialized to so that “thresholded” metaplasticity will work. But it is not important to know these precise values to obtain the conclusions in the article, which is why I did not do such a scan. (The above is treated in the article in the section on reversal learning, lines 569-577 and 628-633.)

Also, when the rule is used for learning, it is not meant to have fixed thresholds, as synapses cannot stabilize and nothing will be stored (Figs. 5, 6, and 8). Fixing the thresholds to a low value was meant to show what happens without any metaplasticity (or if metaplasticity were “dysfunctional”). If in reality a mechanism exists to fix the thresholds to a low value or a high value, fixing would be temporary (until necessary to keep the weights flexible or locked, respectively). 

I am probably not understanding this part of the comment: “How about having a corresponding limit for weights and not for thresholds?” There are two limits, the maximal and minimal weights in the rule w_max and w_min, and are initialized to random values within the interval [0.3, 0.35], but this is probably not what you mean.

When the weights reach their maximum, the thresholds still increase because they have not reached the calcium amplitudes evoked by the maximal weights. (This is most visible with supralinear integration, where strengthened weights evoke plateaus Fig. 4C₂-C₄.) The thresholds move towards the calcium amplitudes with a rate η_θ, which if made very high (as in Figure 4 – figure supplement 11), will make the thresholds rise as fast as the weights. But this is not good, as it will “lock” the learning processes in the synapses too soon (i.e. shorten the window where they are flexible). Neither is a too low η_θ good, as then the synapses are flexible for a very long time and learning of the NFBP is prolonged (Figure 4 – figure supplements 10B₃, 10B₄, 10E₃, learning simulations last longer than in Fig. 4).

(4) Calcium modelling: The author writes that the largest voltage plateaus do not correspond to the largest calcium amplitude because of the plateau's voltage approaching the NMDAR reversal potentials, which might be a problem for the plasticity rule. To solve this, the author tried to implement a monotonic increase of calcium with increasing plateau by implementing axial calcium diffusion and buffering. My question is, is the monotonic increase realistic? Is not the NMDAR reversal effect, described above, a realistic scenario in dendrites?

It seems to be realistic. The closest experiment that I know of is in Fig. 2C₂, D₂ in Oikonomou et al. (2012), where 2 synaptic shocks produce an NMDA spike, and 5 shocks produce a plateau. The calcium dye shows a higher response from the plateau, suggesting a higher calcium amplitude (with a monotonic increase). Moreover, in the detailed calcium model for SPNs by Dorman et al. (2018), larger synaptic clusters produce monotonically higher calcium amplitudes. These two pieces of evidence suggest the calcium amplitudes are not affected by the membrane voltage approaching to the reversal potential. Most likely, this happens because of strong intracellular calcium buffering.

Similarly, the experiments in Figs. 5 and 8 in Losonczy and Magee (2006) with glutamate uncaging at spine heads show a monotonic increase in calcium dye flourescence as the cluster size is increased. However, these experiments evoke NMDA spikes, which might not have approached the NMDAR reversal potential as closely as plateaus do (so, it is theoretically possible that monotonicity does not hold if a plateau were evoked, although it seems unlikely). This is now added to the Methods in lines 957-961.

(5) Function: What is the actual function of the SPN, and how does it relate to FBP/NFBP learning? SPNs are involved in motor control/decision making and generally in sensorimotor tasks. Rather, use an example for that than a visual stimulus, though I understand it is more easily illustrated. Is feature binding what SPNs do and have to solve?

It is not known yet what SPNs do precisely. The initial action selection role of the basal ganglia is currently being challenged or replaced by a role in movement initiation and/or invigoration (with action selection being done by the cortex, see e.g. Thura and Cisek (2017)). In any case, SPNs receive convergent input from sensory, motor, limbic and associative areas, as well as thalamic and neuromodulatory inputs (with topographical projections indicating functional specialization). In that sense, feature binding is particularly relevant for the striatum, as diverse features from different areas would arrive there. The basal ganglia participate in non-motor loops as well, so the striatum may have a role in initiation and termination of cognitive processes such as planning and attention, and in regulating emotional and motivated behavior (Purves et al. 2018).

The role of the striatum and the relevance of feature binding is now stated in the introduction in lines 126-136, and a task with features more suited for the striatum is given in Figure 1 – figure supplement 1 (inspired from similar tasks in Bernklau et al. (2024)). I have kept the example from the visual system in the main text simply because it is widely used throughout the literature and easily recognizable, while clearly stating that other features would be involved in the striatum and pointing to the example in Figure 1 – figure supplement 1. Hopefully this will make a good compromise between ease of reading and relevance to the striatum.

(6) The population of striatal projection neurons can express dopamine D2 receptors and not only D1 receptors. SPNs with different receptors thus undergo synaptic plasticity according to different rules. Would that lead to similar results? A combination of both populations?

This is also being tested in the new study, and preliminary results indicate the answer is “yes” (see Author response image 4). Contrary to the dSPNs, the indirect-pathway SPNs (iSPNs), which predominantly express D₂ receptors, are thought to be involved in suppressing competing or related movements. The learning rule is almost the opposite to dSPNs: to trigger LTP, a dopamine pause is needed, and to trigger LTD a dopamine peak is needed (Fig. 4B and Shen et al. (2008)). So, with such a rule, iSPNs will store the irrelevant patterns and spike to them, and be silent to the relevant patterns (which indeed happens after learning in Author response image 4F₂, F₃). This aligns well with their role to suppress movements – reaching for the irrelevant patterns will be suppressed, while reaching for the relevant patterns will be disinhibited (the indirect pathway inhibits movement initiation). 

(7) Other synaptic plasticity & metaplasticity models (possible comparison or discussion): https://pubmed.ncbi.nlm.nih./ https://linkinghub.elsevier.(https://link.springer.com/ For example, in the last model, there is only one modification LTP/LTD threshold, but it is different from the voltage threshold (which would be comparable to calcium thresholds in the current paper - see the voltage threshold different from the modification threshold here: https://doi.org/10.1371/). The modification threshold favors LTP or LTD - depending on the previous spiking activity of the cell and effectively works as an anti-Hebbian firing rate „homeostasis" mechanism. How is the firing rate homeostasis maintained in the current paper/model? Can you explain how this model is related to the previous models of Benuskova and Abraham, and also Clopath (there was also a metaplasticity version of the Clopath model), in terms of firing rate stability? The current model implements not only local synaptic plasticity but also metaplasticity, which is a nice feature, and seems to not only solve the FBP but also maintain firing stability. Is the stability of firing a consequence of the hard bounds for synaptic weights, or is it also a consequence of plasticity and metaplasticity? I like that each synaptic weight is changed independently based on local calcium concentration, with its own LTP and LTD thresholds.

I will first describe what happens to the firing rate in this model, and then compare with the references you mentioned. In the FBP with linear integration, yes, the firing rate stability is only maintained because of the hard bounds for synaptic weights (Figure 4 – figure supplement 5A₁, the neuron goes into depolarization block without w_max). Without w_max, the weights would grow until [Ca]_NMDA saturates in the spine (which does not happen for most spines within the simulation time in Figure 4 – figure supplement 5B₁).

In the FBP with supralinear integration and the NFBP, the weights are prevented from increasing by the upper threshold for LTP, θ_LTP. If θ_LTP and w_max are gone, synapses also grow without bound (Figure 4 – figure supplement 5B₂). Regardless of how high the synaptic weight becomes, firing rate stability is ensured by the plateau potential, as the maximally achievable voltage is limited by the NMDAR reversal potential (Figure 4 – figure supplement 5A₂, a somatic depolarization block does not happen as in Figure 4 – figure supplement 5A₁). This is part of the plateaus’ function to provide dynamic range compression, as shown experimentally in Figs. 3E, 4D and 12 in Oikonomou et al. (2012). (Of course, such high weights are unrealistic, but they happen in the model without w_max and without θ_LTP). This is now described in the text in lines 397-407.

Regarding the other studies, the second link did not work, so I will refer to Jedlicka et al. (2015), Clopath et al. (2010) and Zenke et al. (2013). (The rule in Jedlicka et al. (2015) is the same as in Benuskova and Abraham, (2007) but with a more detailed neuron model.) In these studies, there is a threshold representing a (weighted) average of the postsynaptic activity (postsynaptic voltage or spiking). In Clopath et al. (2010) and Zenke et al. (2013) it modulates only the amount of LTD, while in Jedlicka et al. (2015) it modulates the amounts of both LTP and LTD that occur due to plasticity. The threshold is global for a neuron (i.e. all synapses use the same threshold), and allows for heterosynaptic effects that compensate increased excitation from synaptic strengthening with stronger weakening in depressed synapses (thus maintaining stable firing rates). (However, the rule in Jedlicka et al. (2015) and Benuskova and Abraham, (2007) has only one threshold, there is no separate voltage threshold. Indeed, the threshold is a low-pass filtered variable of the input spike train, so is similar to calcium concentration.)

There are no such effects in the current learning rule. Some compensatory effects are visible when comparing supralinear integration with and without an upper threshold θ_LTP, as e.g. in Fig. 4B₂ and Figure 4—figure supplement 3B₁. With θ_LTP, synapses do not increase to w_max, and without it, they do. As a consequence, the weakened synaptic cluster is weakened less when using θ_LTP (‘yellow’ synapses in Fig. 4B₂), and more without θ_LTP (‘yellow’ synapses in Figure 4—figure supplement 2B₁). The increased weakening in the latter case is because the strengthened ‘strawberry’ synapses have reached w_max, and contribute to spiking for the irrelevant pattern (‘yellow strawberry’). As a result, the weakened ‘yellow’ synapses have to decrease more so no spiking for the irrelevant pattern occurs. In effect, the increased strengthening in the ‘strawberry’ synapses drives increased weakening in the ‘yellow’ synapses. However, this is a result of the task structure, i. e. that the patterns share features, and not from the learning rule.

The above is briefly explained in the Discussion in lines 778-786.

(8) The last sentence in the discussion is a bold claim: SPN can completely solve NFBP alone. Is that statement too strong, or is it a sign of multiple different mechanisms implementing the same function (i.e., degeneracy)?

The sentence was not meant to be a bold claim. It currently says:

“This indicates that ... SPNs might completely solve the task ... Whether this is true will be explored in another study …”

I have now toned this claim down, as the purpose was only to point to the new study that explores this question (using with 100+ SPN models, in two learning regimes and varying cluster location). Nevertheless, the preliminary results in the new study suggest that SPNs can indeed solve the NFBP (if the plateaus are all-or-none), so I agree that it is a sign of multiple mechanisms implementing the same function.

Figures/Table:

(1) Figure 2: The layout of the figure is confusing. B shows distributed input as in upper A, and C shows clustered input as in lower A. This should be illustrated better (e.g., as in Figure 3 or 4). The term cluster size is confusing as well because it also refers to the distributed inputs; better use the number of synapses here. The color choice is difficult, as similar colors are chosen for cluster size and for differentiating linear and nonlinear integration in D.

Thank you for the detailed comments! The figure has been reworked accordingly.

(2) Figure 4: C What are dashed lines?

They indicate the upper threshold for LTP, θ_LTP.Thank you for noticing this, it is now added in the figure caption, and in other figures where it was missing.

(3) Figure 5 and Figure 6: B is missing.

These figures have been reworked to match the revision of the text describing the role of metaplasticity in the shared synapses. Now, the FBP is described first, followed by the NFBP, so the figures have been merged with their figure supplements (where the FBP results used to be in the first version).

(4) Figure 4 Supplement 1: What do the colors and regions mean in B3? Why show here and not for others?

The main text in lines 311-312, 331-333, and 358-359 refers to these regions when explaining the dynamics of the calcium, the thresholds and the weights (e.g. the pink region shows that [Ca]_L-type in the ‘strawberry’ synapses evoked by ‘yellow strawberry’ is much lower than the calcium threshold for ‘strawberry’, protecting these synapses from weakening). They are simply highlighted with different colors, so readers know precisely where to look when reading the main text. The figure caption has been updated to state this.

Also, the figure caption says that the same regions exist in all panels, although they have not been highlighted. I could have chosen any panel to mark these regions, and I chose B₃ because it looked like it had the least visual clutter.

(5) Table 1: Typo for LTD

Now fixed.

(6) Line 21: „thehsold"

Now fixed.

(7) Line 50: Closing parentheses missing.

Now fixed.

(5) Line 55: "All metaplasticity models so far have only one modifiable threshold". This is not true as it stands. Multiple sliding thresholds have been proposed before:

- experimentally by Ngezahayo et al. (2000)

- multiple pathways reviewed by Abraham (2008)

- multiple structural LTP thresholds observed experimentally by Ueda et al. (2022)

- models of synaptic states and cascade models can be considered to employ multiple thresholds (depending on state); e.g., Fusi et al. (2005)

Thank you for providing these references! The sentence has been changed (it was supposed to refer only to computational models), and the studies have been added in the text where appropriate.

Importantly, Fusi et al. (2005) is now being discussed throughout the text, as it contains important results and conclusions about metaplasticity which are used as comparison. (In the first version of the article I did not include it because I was not sure about the interpretation of the thresholds – strictly speaking there is only one plasticity threshold (q, determining whether a synapse will switch sign), while the other is a metaplasticity threshold (p, determining whether the synapse will change its metaplastic state). However, the precise number of thresholds is not as important, as the study’s results are relevant to compare with.)

(9) Lines 117/118: Missing parentheses around reference.

Fixed.

(10) Line 140: "a small difference". I feel like "small" is a bit of an understatement here, as from what I can see, the differences are almost a magnitude -- see blue/black traces in Figure 2B4 vs. 2C4.

Thank you for noticing this. It was meant to refer only to the amplitude of the somatic voltage when the cluster size is small (in Fig 2D₁). The text has been clarified now.

(11) I think it's unnecessary to rewrite Eq. 1 in Eq. 3.

I decided to keep this.

(12) Lines 181-183: It would probably still be useful to show that NFBP can't be solved by distributed inputs.

It is now shown in Figure 4 – figure supplement 1, and briefly described in the text in lines 298300.

(13) Line 210: Typo, double "(the"

Fixed, thank you.

(14) Lines 248-249: Typo, double partial sentence.

Now fixed.

(15) Line 760: The year in the „STDP rule endowed with the BCM sliding threshold accounts for hippocampal heterosynaptic plasticity" should be corrected to 2007. Also, all other references should be checked for mistakes and missing pages, etc. (see e.g., also line 882).

Thank you for noticing this! The references have been checked.

References

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Author response image 1.

Plateau potentials (A1, B1) and their somatic amplitudes in dSPNs (A) and iSPNs (B) when the location of the synaptic cluster is varied. Distally evoked plateaus have a smaller somatic amplitude in both dSPNs and iSPNs, bust still exhibit a nonlinear jump in the somatic voltage. In (A2, B2) all 71 dSPN and 34 iSPN models were tested, color coded with respect to their excitability to a synaptic cluster of 10 synapses.

Author response image 2.

Two learning simulations on the NFBP where different metaplasticity rates for LTP and LTD were used. (Top) The metaplasticity rate for LTD is higher, stopping the LTD process prematurely (D1, D2), resulting in less weakening of the synapses (B1, B2) and spiking for one irrelevant pattern (A1). (Bottom) The metaplasticity rate for LTP is higher, preventing frequent synaptic strengthening(C1, C2). As a result, it takes a longer time for synapses to strengthen and trigger plateaus (B3, B4).

Author response image 3.

Learning on the NFBP with a nonlinear (quadratic) metaplasticity rule, which implements the BCM rule. (A) Somatic and dendritic voltage before and after learning. (B-D) Evolution of synaptic weights (B), LTP (C) nad LTD thresholds (D). Weights in (B) seem to stabilize around a high value once the LTP threshold reaches the maximal [Ca]NMDA; however, the value is too high and triggers plateau potentials for all patterns.

Author response image 4.

Learning to solve the NFBP in one dSPN and one iSPN model. (A, B) Schemes describing the requirements for cortico-striatal synaptic plasticity in dSPNs (A) and iSPNs (B). (C) Dopamine peaks are emitted from the midbrain after the relevant patterns, and dopamine pauses after the irrelevant patterns. (D) Stimulation protocol. (E, F) A single learning simulation in a dSPN (E) and an iSPN (F) model. Before learning the neurons spike to all patterns (due to additional feature-unspecific distributed inputs, shown with the third panels in E3, F3). After learning, the dSPN spikes only for the relevant patterns (E2) and the iSPN only for the irrelevant ones (F2). (E3, F3) The evolution of clustered and distributed synptic weights (In dendrite 1 of the iSPN, the synapses for 'red' experienced some strengtheneing after being weakened, but this does not seem to affect learning in this example.) The neurons in th enew study receive less background synaptic input than in the current article, and additional distributed synapses are needed along with a plateau for somatic spiking, making for a more challenging learning scenario.

eLife Assessment

This valuable study provides a practical computational framework for inferring latent neural states directly from calcium fluorescence recordings, bypassing the traditional need for a separate spike deconvolution step. The evidence supporting the method is convincing, featuring rigorous validation across multiple latent variable model families (including HMM, GPFA, and LFADS) using both simulated and experimental data. To further strengthen method's generality, it would require further application to a broader range of experimental datasets, such as recordings from different brain regions or using different calcium indicators.

Reviewer #1 (Public review):

Summary:

In this study, the authors elegantly combined latent variable models (i.e., HMM, GPFA and dynamical system models) with a calcium imaging observation model (i.e., latent Poisson spiking and autoregressive calcium dynamics (AR)).

Strengths:

Integrating a calcium observation model into existing latent variable models improves significantly the inference of latent neural states compared to existing approaches such as spike deconvolution or Gaussian assumptions.

The authors also provide an open-source access to their method for direct application to calcium imaging data analysis.

Weaknesses:

As acknowledged by the authors, their method is dependent on the quality of calcium traces extraction from fluorescence videos. It should be noted that this limitation applies to alternative strategies.

While the contribution of this study should prove useful for researchers using calcium imaging, the novelty is limited, as it consists of an integration of the calcium imaging model from Ganmor et al. 2016 with existing LVM frameworks.

Comments on revised version.

The authors addressed my comments and I have no further concerns.

Reviewer #2 (Public review):

Summary:

This compelling study proposes a framework to implement latent variable models using population level calcium imaging data. The study incorporates autoregressive dynamics and latent Poisson spiking to improve inference of latent states across different model classes including HMMs, Gaussian Process Factor Analysis and nonlinear dynamical systems models. This approach allows for a more seamless integration of existing methods typically used with spiking data to apply on calcium imaging data. The authors test the model on piriform cortex recordings as well as a biophysical simulator to validate their methods. This approach promises to have wide usability for neuroscientists using large population level calcium imaging.

Strengths:

The strength of this study is the flexibility in the choice of models and relatively easy adaptation to user-specific use cases.

Weaknesses:

The weakness of the study lies in its limited validation of biological calcium imaging data. Calcium dynamics in a task-specific context in a sensory brain region might be very different from slower dynamics in a region of integration.

Reviewer #3 (Public review):

Summary:

S. Keeley & collaborators propose a computational approach to infer time-varying latent variables directly from calcium traces (e.g., obtained with 2p imaging) without the need for deconvolving the traces into spike trains in a preliminary, independent step. Their approach rests on 1 of 3 families of latent models: GPFA, HMM and dynamical systems - which they augment with an observation model that maps latent variables to fluorescence traces. They validate their approach on simulated data as well as a single real dataset, showing that the approach improves latent variable inference and model fitting, compared to more traditional approaches (although not directly compared with the 2-step one; see below). They provide a GitHub repository with code to fit their models (which I have not tested).

Strengths:

The approach is sound and well-motivated. The authors are specialists of latent variable models. The manuscript is succinct, well-written and the figures are clear. I particularly liked the diversity of latent models considered, in particular latent models with continuous (GPFA) vs. discrete (HMM) dynamics, which are useful for characterizing different types of neural computations. The validation on both simulated and real data is convincing.

Weaknesses:

The main weakness point that I see is that the approach is tested only on a single real dataset (odor response dataset). The other model fits are obtained from simulated data. While the results are convincing, it would be useful to see the approach tested on other datasets, for instance datasets with different brain areas, different behavioral conditions, or different calcium indicators. This would help assess the generality of the approach and its robustness to different experimental conditions.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this study, the authors elegantly combined latent variable models (i.e., HMM, GPFA and dynamical system models) with a calcium imaging observation model (i.e., latent Poisson spiking and autoregressive calcium dynamics (AR)).

Strengths:

Integrating a calcium observation model into existing latent variable models improves significantly the inference of latent neural states compared to existing approaches such as spike deconvolution or Gaussian assumptions.

The authors also provide an open-source access to their method for direct application to calcium imaging data analysis.

Weaknesses:

As acknowledged by the authors, their method is dependent on the quality of calcium trace extraction from fluorescence videos. It should be noted that this limitation applies to alternative strategies.

While the contribution of this study should prove useful for researchers using calcium imaging, the novelty is limited, as it consists of an integration of the calcium imaging model from Ganmor et al. 2016 with existing LVM frameworks.

Reviewer #2 (Public review):

Summary:

This compelling study proposes a framework to implement latent variable models using population level calcium imaging data. The study incorporates autoregressive dynamics and latent Poisson spiking to improve inference of latent states across different model classes including HMMs, Gaussian Process Factor Analysis and nonlinear dynamical systems models. This approach allows for a more seamless integration of existing methods typically used with spiking data to apply on calcium imaging data. The authors test the model on piriform cortex recordings as well as a biophysical simulator to validate their methods. This approach promises to have wide usability for neuroscientists using large population level calcium imaging.

Strengths:

The strengths of this study are the flexibility in the choice of models and relatively easy adaptation to user-specific use cases.

Weaknesses:

The weakness of the study lies in its limited validation of biological calcium imaging data. Calcium dynamics in a task-specific context in a sensory brain region might be very different from slower dynamics in a region of integration. The biophysical properties of the data would also be dependent on the SNR of the imaging platform and the generation of calcium indicator being used.

Reviewers 1 and 2 correctly point out that our method depends on the quality of the upstream calcium trace extraction. As they noted, these traces can vary based on the specific indicator used, the signal-to-noise ratio (SNR) of the recording, and the region of the brain being imaged (such as sensory vs. integrative areas). As Reviewer 1 rightly mentions, this is a universal challenge that applies to alternative strategies as well, rather than a limitation unique to our framework. To address these points, we have added a paragraph to our Discussion section.

Reviewer #3 (Public review):

Summary:

S. Keeley & collaborators propose a computational approach to infer time-varying latent variables directly from calcium traces (for instance, obtained with 2p imaging) without the need for deconvolving the traces into spike trains in a preliminary, independent step. Their approach rests on 1 of 3 families of latent models: GPFA, HMM and dynamical systems - which they augment with an observation model that maps latent variables to fluorescence traces. They validate their approach on simulated and real data, showing that the approach improves latent variable inference and model fitting, compared to more traditional approaches (although not directly compared with the 2-step one; see below). They provide a GitHub repository with code to fit their models (which I have not tested).

Strengths:

The approach is sound and well-motivated. The authors are specialists in latent variable models. The manuscript is succinct, well-written, and the figures are clear. I particularly liked the diversity of latent models considered, in particular latent models with continuous (GPFA) vs.

discrete (HMM) dynamics, which are useful for characterizing different types of neural computations. The validation on both simulated and real data is convincing.

Weaknesses:

One advantage … is that one can inspect the quality of the deconvolution step independently from the latent variable inference step. For instance, if the inferred latent variables are not interpretable, how can one determine whether this is due to a poor choice of latent model (e.g., HMM with too few states), or a poor fit of the observation model (e.g., wrong parameters for the calcium dynamics)?

We agree with the reviewer that integrating the calcium likelihood introduces additional parameters that require careful diagnostics. However, for the vast majority of imaging datasets, there is no simultaneous electrophysiology to verify the deconvolution step. If the final latent states are not interpretable, it remains impossible to determine whether the error originated in the initial spike inference from deconvolution or the subsequent model fitting.

Our framework addresses this by maintaining the raw fluorescence as the fixed observation. We suggest for those using this model to employ cross-validation using this data to select model parameters. We outline how to do this below, but because the data itself does not change with each model fit, you can compare P(data | λ) across any model configuration. In contrast, different deconvolution methods change the data itself (the spiketimes) making comparison across models impossible.

Could the authors comment on whether their approach allows for instance to compare different forms of latent models (e.g., HMM vs. GPFA) in terms of model evidence, cross-validated log-likelihood or other model comparison metrics?

We thank the reviewer for highlighting this. In short: yes. Because our framework integrates the calcium observation likelihood with various latent variable models, we can assess held-out prediction P(data | λ) irrespective of the specific latent structure.

However, because fitting the LVM requires inferring the latent state z to determine the firing rate λ, proper cross-validation across models involves holding out both neurons and timepoints. A principled approach—which our framework supports—is as follows:

(1) Train both the latent states z and the model parameters (e.g., the mapping from latent space to observations) on a training portion of the recording.

(2) On a held-out test segment, withhold a subset of "test" neurons and infer the latent states using only the "held-in" neurons.

(3) Calculate the likelihood of the observed fluorescence for the test neurons given the inferred rates.

We clarify this procedure in the revised manuscript. While a comprehensive benchmarking across all possible LVM architectures is beyond the scope of this study, we provide the statistical infrastructure for users to perform such comparisons. Furthermore, we would like to emphasize that while predictive likelihood is a rigorous metric for model selection, the primary utility of these LVMs often lies in the interpretability of the latent states themselves, which can remain biologically informative even if cross-validated performance is not the sole optimization target.

While it certainly makes sense that models accounting for the full transformation of latent => spikes => fluorescence data should outperform the two-step (1) deconvolution => (2) latent variance inference approach, the amount of improvement is not clear. A direct comparison … would be useful

We thank the reviewer for this point. Figure 4 was designed to address this comparison directly. By using a biophysical simulator, we generated a pseudo-realistic spiking network with ground-truth latent trajectories governed by a Gaussian Process. This allowed us to explicitly compare our unified approach against the traditional deconvolution-then-Poisson-GPFA pipeline. While a first-order (AR1) calcium likelihood did not show improvement over the two-step deconvolution method in recovering the ground-truth latents, the second-order (AR2) process demonstrated an improvement. Because there are no ground-truth parameters in the model, we use the reconstruction error of the latent values as our primary metric for recovery. These results suggest that when the observation model sufficiently captures the underlying calcium kinetics, the unified approach offers a more accurate estimation of the neural state.

It would be useful to discuss the possible extension of the approach to other types of data that … have different observation models.

We thank the reviewer for this helpful comment. We agree that the general framing of the likelihood has potential use in a wider range of data modalities.

Specifically, all sensors (aside from some voltage sensors) have a rise and decay time in line with our model. Thus the autoregressive (AR) nature of the calcium likelihood we utilize makes the current implementation particularly well-suited for a broad range of fluorescence-based sensors with similar temporal profiles. The specific use and extension would depend heavily on the biological target of the sensor. For example Glutamate, dopamine, and similar indicators can be thought of as having a similar underlying Poisson firing model, as the release of these products is tied to neural firing. Other sensors that might relate to other biological processes, such as hemodynamics (via imaging or ultrasound) or broader neuromodulation (Norepinephrine imaging with nLight) might be more continually varying and therefore would require changing the Poisson with an appropriate alternative, for example a Gaussian Process or similar.

Voltage imaging is the one exception that may require more complex observation models. However, the challenge in voltage imaging is not the ability to identify individual spikes, but more that the speed and scope of imaging is inherently limited by the speed of the voltage process and signal-to-noise ratios induced by the low quantum efficiency and membrane-bound nature of these indicators. If imaged well, single spikes would be clearly visible and the two-stage likelihood would not be necessary—one could simply use the spike times in a Poisson model just as with electrophysiology. We have added a paragraph in the discussion highlighting these points.

eLife Assessment

This important study identifies underappreciated experimental factors that influence α-synuclein amyloid polymorphism, with practical implications for the reproducibility of in vitro fibril preparations. Extensive cryo-EM analyses provide convincing evidence that protein purity, monomer preparation, and agitation conditions influence polymorph selection, including substantial effects from small amounts of an N-terminally truncated variant. The study provides a substantial resource for researchers studying amyloid assembly and synucleinopathies, although the proposed nucleation mechanisms need stronger kinetic support and reliable protocols for producing specific polymorphs require further development.

Reviewer #1 (Public review):

In this work, Frey and colleagues have carried out a very large study of α-synuclein polymorphism as a function of aggregation conditions and sample preparation. They provide valuable insight into the many critical factors affecting α-synuclein polymorphism, thereby illuminating the need for detailed reporting in the literature as well as both rigorous and detail-oriented protocols when working with this protein. Indeed, their observations are in line with the difficulties of reproducing structural outcomes across different laboratories and experiments. The authors must be complemented on their openness about the difficulties experienced and the thoroughness of their work. Efforts like these are going to be crucial to achieve an understanding of the unparalleled structural plasticity of α-synuclein amyloid fibrils. It is particularly notable that the authors have managed to optimize protocols to form single-polymorph aggregation reactions with high reproducibility.

In this work, the authors focus on the influence of α-synuclein purity in aggregation reactions. They find that using reverse-phase HPLC to purify the protein significantly alters the aggregation behaviour. It is interesting, and rather uncommon in the field, to use reverse-phase HPLC as a final purification step, rather than SEC, which is commonly used in many laboratories. It would be useful to compare this new protocol even more directly and extensively with the commonly used SEC protocol. When mentioning their previously published work, it should be mentioned explicitly how the protein was purified in these previous studies.

On the point of protein purification, the authors lyophilize their protein prior to storage. In their work, they also find that pre-aggregation oligomer formation alters the aggregation pathway of α-synuclein. While they demonstrate that this can be solved by appropriate filtration, it should be discussed why the lyphilizaiton step was not reconsidered/omitted given that this process is known to facilitate oligomer formation. Do the authors have experience with aggregation studies using α-synuclein that has not undergone lyophilisation and are able to comment on the influence of this step in the protocol?

The authors make note of several degradation products affecting their aggregation reactions, which is why they employ a much more thorough purification protocol. However, they also point out that some of the degradation products found at the end of their reaction could form during the reaction itself. Unfortunately, they never investigate this further. In particular, it would be very useful to know if different aggregation conditions (pH, salt, agitation) lead to different and characteristic degradation patterns. HPLS/mass spec of the supernatant at the end of each aggregation reaction would have been a very insightful thing to do.

With respect to degradation products, in this work a NΔ4-variant is produced to mimic a disease-relevant degradation product and indeed it is found to alter the structural outcome even at low relative concentrations (5%). Have the authors investigated the minimal fraction of the NΔ4 variant necessary to still influence the structural outcome of the predominant WT protein? This type of analysis could have significant relevance to disease-related analysis, where several variants (truncations and PTM variants) are present in trace amounts.

While on this topic, the authors note that in several of their type 5 fibrils, they find unresolved peptide fragments in their cryo-EM structures. Can the authors speculate if these fragments are indeed peptide degradation products or residues wrapping around the fibril originating from the fibril-incorporated protein?

In this work, the authors have performed an extensive study of α-synuclein polymorphism. However, despite generating what is likely the largest single data set of fibril structures, they perform very little quantitative analysis of their data. It would be interesting to analyse the relative abundance of fibril polymorphs produced in each reaction. Perhaps from the particle-picking data it could be estimated the relative abundance of each polymorph as well as non-resolved fibrils to generate a more nuanced view of polymorphism beyond overall classifications of the resolved structures. Indeed, from such data it could also be studied if certain protofilaments are more prone to pair in asymmetric fibril structures over others or if fibril asymmetry can be attributed to random pairing of protofilaments in accord with their abundance. This latter point is particularly interesting for the type 1 fibrils. Perhaps, the propensity of α-synuclein to form specific symmetries could also be estimated.

The authors note that pH is a strong factor in determining polymorph selection. This does indeed appear to be the case, but other parameters do not appear to show any clear trend. Have the authors investigated the influence of aggregation parameters (agitation, duration) on structural outcomes systematically or quantitatively, such as with principal component analysis? Indeed, they also find that some fibril types that otherwise are not compatible at the same pH appear to co-exist when the shaking parameter is modified. Are the authors then confident in the claim that pH is a deterministic parameter?

It is evident from this and other work that amyloid aggregation is highly sensitive to kinetic effects. It is therefore curious that the effect of protein concentration and reaction time has not been systematically investigated. The authors have some data studying dilution series (Figure 6A) and different reaction times (reaction 56 & 57). Could the authors comment on the effects of these two parameters, and might there be more information touching upon this that could be highlighted in this work?

The authors state that this work likely underreports fibril polymorphisms in samples due to population size or data quality challenges. Could the authors, based on their extensive experience, try to quantify this statement?

Additionally, the authors point out that the current framework for classifying α-synuclein fibril polymorphism is not sufficient to describe the real complexity of this protein system. However, they do not seem to address some of the recent literature aiming to solve such issues (see Scheres 2026, Connor et al. 2025, Milchberg et al. 2025 & Price et al. 2025).

Was any biophysical/biochemical analysis performed of the many structures produced here, such as CD spectroscopy, Proteinase K digestion, dye binding or FTIR, which could act as low-resolution structure identifiers and might help to retrospectively explain some findings in the older literature? Such data would be very useful for the vast majority of researchers, who do not have access to cryo-EM.

Reviewer #2 (Public review):

Summary:

This manuscript describes insights gained during efforts to reproduce disease-relevant alpha-Synuclein (aSyn) fibrils using recombinant protein in vitro. It follows up on a similar article from this team published in 2024. Although the authors have not been able to produce fibrils with the structure of ex vivo fibrils isolated from patients, they share insights gained into which factors influence the formation of specific fibril polymorphs.

Strengths:

This is quite an unusual manuscript because it goes into minute detail about sample preparation that are usual just mentioned in the Materials and Methods sections of other manuscripts (if at all). This makes it very valuable for the scientific community working on exactly the problem of reproducing disease-relevant aSyn fibrils in vitro (which will be a major breakthrough in the field). The authors present an impressive array of cryo-EM fibril structures, some of which have not been described before.

Weaknesses:

A major concern with the manuscript is that its story and messaging are a bit murky. The authors describe a few new polymorphs, show that some polymorphs (type 1) have small variations, show that sample purity and fragmentation will influence polymorph formation, and present a helical-symmetry mystery. This all reads like a loose collection of findings without any major takeaway. Looking at Table 1, it still seems that the authors do not have a good control over any of these polymorphs. Are they able to make any of these polymorphs reliably? I think the impact of this work could be strengthened if it ended with a reliable protocol for the production of any of the polymorphs described.

A second major concern is the quality of the aggregation kinetics and their interpretation. Are these kinetics just done once per concentration? The figure caption talks about 'three independent samples' but it is unclear if this refers to the three different concentrations or NΔ4 percentages used, or true repetitions. Looking at the curves themselves, it seems that only one of the conditions was actually done in triplicate, which should be the minimum to draw conclusions. Further, it would have been helpful to characterize the kinetic data quantitatively. Finally, because there are only kinetic data for a fraction of the conditions tested, it is not clear what they add to the overall manuscript. My recommendation is to either remove the kinetics from the manuscript or substantially expand this section.

Author response:

Reviewer #1 (Public review):

In this work, Frey and colleagues have carried out a very large study of α-synuclein polymorphism as a function of aggregation conditions and sample preparation. They provide valuable insight into the many critical factors affecting α-synuclein polymorphism, thereby illuminating the need for detailed reporting in the literature as well as both rigorous and detail-oriented protocols when working with this protein. Indeed, their observations are in line with the difficulties of reproducing structural outcomes across different laboratories and experiments. The authors must be complemented on their openness about the difficulties experienced and the thoroughness of their work. Efforts like these are going to be crucial to achieve an understanding of the unparalleled structural plasticity of α-synuclein amyloid fibrils. It is particularly notable that the authors have managed to optimize protocols to form single-polymorph aggregation reactions with high reproducibility.

In this work, the authors focus on the influence of α-synuclein purity in aggregation reactions. They find that using reverse-phase HPLC to purify the protein significantly alters the aggregation behaviour. It is interesting, and rather uncommon in the field, to use reverse-phase HPLC as a final purification step, rather than SEC, which is commonly used in many laboratories. It would be useful to compare this new protocol even more directly and extensively with the commonly used SEC protocol. When mentioning their previously published work, it should be mentioned explicitly how the protein was purified in these previous studies.

On the point of protein purification, the authors lyophilize their protein prior to storage. In their work, they also find that pre-aggregation oligomer formation alters the aggregation pathway of α-synuclein. While they demonstrate that this can be solved by appropriate filtration, it should be discussed why the lyphilizaiton step was not reconsidered/omitted given that this process is known to facilitate oligomer formation. Do the authors have experience with aggregation studies using α-synuclein that has not undergone lyophilisation and are able to comment on the influence of this step in the protocol?

We will include details in our revised version on how samples were prepared in our previously published work. However we do not plan to do a comparison between SEC and HPLC as final purification steps because these are truly orthogonal separation methods. SEC is the gold standard for oligomer removal but not particularly useful for removing degradation products of similar size (which we believe to affect aggregation outcomes). In our hands, the highest purity and reproducibility come from HPLC-purified material followed by a stringent oligomer removal. Because oligomers in the solubilized sample are a concern, SEC as a final post-solubilization/pre-aggregation step might be ideal. However, as we mentioned in the manuscript, SEC dilutes the sample to the point that much of the sample is too dilute for our purposes (aggregation without seeds) and adding an additional concentration step would risk promoting the formation of new oligomers in the concentration device. That is why we resorted to using a 100 kD MWCO filter to remove oligomeric species.

We considered skipping the lyophilization step and dialyzing the HPLC-purified sample into the buffer of choice but stuck with lyophilization because it provides an easy control over the protein concentration in the solubilized sample.

To clarify the logic in this choice of sample preparation steps, we will add a section to the revised manuscript listing/explaining our suggested protocols for preparing alpha-synuclein samples for reproducible aggregation experiments.

The authors make note of several degradation products affecting their aggregation reactions, which is why they employ a much more thorough purification protocol. However, they also point out that some of the degradation products found at the end of their reaction could form during the reaction itself. Unfortunately, they never investigate this further. In particular, it would be very useful to know if different aggregation conditions (pH, salt, agitation) lead to different and characteristic degradation patterns. HPLS/mass spec of the supernatant at the end of each aggregation reaction would have been a very insightful thing to do.

In retrospect, we agree that this could have been important from the standpoint of understanding how in situ degradation during the aggregation at 37º C could also play a role in polymorph selection. We have begun to save frozen aliquots of our aggregation samples for subsequent MS analyses of the interesting samples in order to be able to address this in the future. However, it was outside the scope of our original search for the PD polymorph.

With respect to degradation products, in this work a NΔ4-variant is produced to mimic a disease-relevant degradation product and indeed it is found to alter the structural outcome even at low relative concentrations (5%). Have the authors investigated the minimal fraction of the NΔ4 variant necessary to still influence the structural outcome of the predominant WT protein? This type of analysis could have significant relevance to disease-related analysis, where several variants (truncations and PTM variants) are present in trace amounts.

We did not try lower than 5% because it was our goal to test if impurities at this level (which usually go undetected) could influence the aggregation outcomes. We think that directly relating the precise impurity level in these in vitro experiments to in vivo aggregation would be difficult due to the many factors we do not yet understand that appear to guide in vivo polymorph selection.

While on this topic, the authors note that in several of their type 5 fibrils, they find unresolved peptide fragments in their cryo-EM structures. Can the authors speculate if these fragments are indeed peptide degradation products or residues wrapping around the fibril originating from the fibril-incorporated protein?

We will add this speculation to the revised manuscript. The unassigned peptide density most likely originates from the C-terminal residues of the intact chains rather than from a degradation product. The levels of degradation products observed by MS in our other samples were far too low to account for the amount of peptide that would be required for >50% of the fibrils in sample 23 to contain this extra density. Furthermore, in the 5A polymorph the extra peptide density is sometimes present (e.g. sample 52) and sometimes absent (e.g. sample 3), despite the fact that in both samples the coexisting type 5 polymorphs (5m and 5B, respectively) have the peptide bound. Therefore, it appears that subtle differences between 5A polymorphs determine the presence or absence of this density, whereas for 5m and 5B it is consistently present.

In this work, the authors have performed an extensive study of α-synuclein polymorphism. However, despite generating what is likely the largest single data set of fibril structures, they perform very little quantitative analysis of their data. It would be interesting to analyse the relative abundance of fibril polymorphs produced in each reaction. Perhaps from the particle-picking data it could be estimated the relative abundance of each polymorph as well as non-resolved fibrils to generate a more nuanced view of polymorphism beyond overall classifications of the resolved structures. Indeed, from such data it could also be studied if certain protofilaments are more prone to pair in asymmetric fibril structures over others or if fibril asymmetry can be attributed to random pairing of protofilaments in accord with their abundance. This latter point is particularly interesting for the type 1 fibrils. Perhaps, the propensity of α-synuclein to form specific symmetries could also be estimated.

We agree that Cryo-EM datasets contain considerable information that could potentially be used to better understand polymorph populations. We have previously used particle counts as an approximate measure of polymorph abundance; however, the biases introduced during particle picking and subsequent curation are substantial, and we therefore do not consider these counts sufficiently reliable for quantitative comparison of polymorph populations.

Regarding the symmetry of paired filaments, it is clear that the overwhelming preference of all filaments is to pair as symmetric dimers. Among the in vitro polymorphs, type 1 is the most commonly observed to form an asymmetric dimer, either with itself or with the new type 7. However, the number of observations is too small to establish that this represents a statistically meaningful preference. Types 2 and 3 have also been observed to pair in asymmetric fibrils. Overall, we do not think that our dataset is large enough to add statistical weight to previous observations.

The authors note that pH is a strong factor in determining polymorph selection. This does indeed appear to be the case, but other parameters do not appear to show any clear trend. Have the authors investigated the influence of aggregation parameters (agitation, duration) on structural outcomes systematically or quantitatively, such as with principal component analysis? Indeed, they also find that some fibril types that otherwise are not compatible at the same pH appear to co-exist when the shaking parameter is modified. Are the authors then confident in the claim that pH is a deterministic parameter?

We did not systematically vary the agitation but in two cases where it was either intentionally or accidentally varied, we found surprising polymorph outcomes. We felt that these observations were worth reporting, but on their own they do not constitute a thorough study. We would rather conclude that pH is a strong selector and can be deterministic under certain conditions: pure sample, no seeds, continuous or intermittent moderate agitation. We will revise the manuscript to make this clearer.

It is evident from this and other work that amyloid aggregation is highly sensitive to kinetic effects. It is therefore curious that the effect of protein concentration and reaction time has not been systematically investigated. The authors have some data studying dilution series (Figure 6A) and different reaction times (reaction 56&57). Could the authors comment on the effects of these two parameters, and might there be more information touching upon this that could be highlighted in this work?

We did not collect sufficient data to draw conclusions about the effects of protein concentration or aggregation time, and therefore do not think that a quantitative analysis of these parameters is justified by the present dataset.

The authors state that this work likely underreports fibril polymorphisms in samples due to population size or data quality challenges. Could the authors, based on their extensive experience, try to quantify this statement?

Precise quantification would be difficult. The literature has many mentions of amyloids that could not be solved by Cryo-EM due to a lack of twist. In our hands it is very common to have a small subset of non-twisted filaments in a sample and some samples appear to be exclusively non-twisted. Low-abundance or low-quality fibrils are also rather common in our data but also difficult to quantify. Nevertheless, we agree that it would be useful to place a lower bound on this estimate, and we will re-examine our datasets to determine whether this can be quantified in the revised manuscript.

Additionally, the authors point out that the current framework for classifying α-synuclein fibril polymorphism is not sufficient to describe the real complexity of this protein system. However, they do not seem to address some of the recent literature aiming to solve such issues (see Scheres 2026, Connor et al. 2025, Milchberg et al. 2025 & Price et al. 2025).

We agree that we should have discussed this literature in greater detail and will do so in the revised manuscript.

Was any biophysical/biochemical analysis performed of the many structures produced here, such as CD spectroscopy, Proteinase K digestion, dye binding or FTIR, which could act as low-resolution structure identifiers and might help to retrospectively explain some findings in the older literature? Such data would be very useful for the vast majority of researchers, who do not have access to cryo-EM.

We did not perform these analyses precisely because they are low resolution. Retrospectively, such analyses might have been useful for interpreting past data, but most of these methods (particularly Proteinase K resistance) are difficult to compare between laboratories and work best with side-by-side controls. This is why developing a facile method for polymorph identification is one of our main future research goals.

Reviewer #2 (Public review):

Summary:

This manuscript describes insights gained during efforts to reproduce disease-relevant alpha-Synuclein (aSyn) fibrils using recombinant protein in vitro. It follows up on a similar article from this team published in 2024. Although the authors have not been able to produce fibrils with the structure of ex vivo fibrils isolated from patients, they share insights gained into which factors influence the formation of specific fibril polymorphs.

Strengths:

This is quite an unusual manuscript because it goes into minute detail about sample preparation that are usual just mentioned in the Materials and Methods sections of other manuscripts (if at all). This makes it very valuable for the scientific community working on exactly the problem of reproducing disease-relevant aSyn fibrils in vitro (which will be a major breakthrough in the field). The authors present an impressive array of cryo-EM fibril structures, some of which have not been described before.

Weaknesses:

A major concern with the manuscript is that its story and messaging are a bit murky. The authors describe a few new polymorphs, show that some polymorphs (type 1) have small variations, show that sample purity and fragmentation will influence polymorph formation, and present a helical-symmetry mystery. This all reads like a loose collection of findings without any major takeaway. Looking at Table 1, it still seems that the authors do not have a good control over any of these polymorphs. Are they able to make any of these polymorphs reliably? I think the impact of this work could be strengthened if it ended with a reliable protocol for the production of any of the polymorphs described.

It is true that the initial results were a collection of findings compiled while searching for the PD polymorph. However, the trends that we saw in these data inspired us to pursue a more systematic approach which was used to show how impurities play a crucial role in polymorph selection even at low levels. We agree that the impact of the work will be enhanced by summarizing the protocols that can be used to obtain the types 1, 2, 3 and 5 polymorphs and will add this to the revised manuscript.

A second major concern is the quality of the aggregation kinetics and their interpretation. Are these kinetics just done once per concentration? The figure caption talks about 'three independent samples' but it is unclear if this refers to the three different concentrations or NΔ4 percentages used, or true repetitions. Looking at the curves themselves, it seems that only one of the conditions was actually done in triplicate, which should be the minimum to draw conclusions. Further, it would have been helpful to characterize the kinetic data quantitatively. Finally, because there are only kinetic data for a fraction of the conditions tested, it is not clear what they add to the overall manuscript. My recommendation is to either remove the kinetics from the manuscript or substantially expand this section.

In Figure 6A, the three curves represent three independent samples; in panels B–D, each curve similarly represents one independent sample. We will try to clear up the ambiguity in the revised version. We agree that the kinetic data have limited utility for determining kinetic parameters of the aggregation. The data were collected primarily to determine when the aggregation reactions were complete so that samples could be prepared for cryo-EM. Nevertheless, we think that the kinetic traces provide two qualitative observations that are relevant to the structural results: 1) In panels A and C of figure 6, the type 5 polymorphs are associated with shorter lag times, suggesting that they either nucleate faster, or as we propose, arise from a small amount of oligomeric protein in the original sample. 2) The longer lag phase associated with the NΔ4 construct was reproducible (panels B, C and D), suggesting that its intramolecular self-chaperoning effect is enhanced due to the increased positive charge in its N-terminal region. Future studies will determine whether this same electrostatic change also gives rise to enhanced secondary nucleation.

eLife Assessment

This useful study reports potential loss-of-function variants, pseudogenes and gene presence-absence variation across multiple chicken genomes, with potential implications for understanding genome evolution and domestication. The evidence for the central claims is unfortunately incomplete, as the inferences of gene loss are not sufficiently robust to account for assembly and annotation artifacts, and, in addition, the analyses can not distinguish between positive selection and relaxed constraint. The overall claim of large-scale gene loss being adaptive and thus being a major driver of chicken evolution and domestication is therefore not sufficiently supported. The area of the study is of interest to colleagues in evolutionary and comparative genomics as well as animal domestication.

Reviewer #1 (Public review):

Summary:

The authors have assembled the genome of four local chicken breeds from China and analysed their gene content. They come to the conclusion that thousands of genes present in the current reference genome of chicken have become pseudogenized during chicken evolution and domestication. They argue that their study provides strong support for the importance of the "less-is-more" hypothesis for adaptive evolution.

Strengths:

The paper provides medium-quality genome assemblies for four individuals representing four local populations of chickens and analyses their gene content.

Weaknesses:

They have not excluded the possibility that the high rate of putative pseudogenes reflects the presence of errors in gene models, in particular in GC-rich microchromosomes that are challenging to assemble correctly. The paper contains no genotype-phenotype analysis, which means that the adaptive significance of a high rate of pseudogenization, if it exists, is unknown.

Reviewer #2 (Public review):

Summary:

The authors set out to investigate the evolutionary role of gene presence-absence variation and pseudogenization in chicken evolution and domestication. By comparing draft genome assemblies of four indigenous Chinese chicken breeds against the red junglefowl reference genome (GRCg6a) and four PacBio HiFi assemblies, the study proposes that the common ancestor possessed nearly 22,000 genes, and that each domestic lineage independently lost thousands of genes (identifying ~8,000 dispensable genes). The authors conclude that massive loss of function and pseudogenization represent major drivers of chicken evolution under the "less-is-more" hypothesis.

While the concept that gene loss can drive phenotypic diversification during domestication is compelling, the results do not convincingly support the central conclusions. The scale of reported gene loss and the specific patterns of pseudogenization appear to be potentially driven by well-known genome assembly gaps, annotation errors, and sequencing dropouts rather than genuine evolutionary events, and the authors do not provide enough convincing evidence that this is not the case.

Strengths:

(1) The study addresses an important and timely evolutionary question regarding the role of gene loss and loss-of-function variation in animal domestication.

(2) The inclusion of multiple indigenous Chinese chicken breeds alongside high-accuracy PacBio HiFi assemblies provides a valuable comparative genomic dataset.

(3) The authors attempt to evaluate pseudogene transcription using RNA-seq data and check for transcript isoforms that bypass candidate loss-of-function mutations.

Weaknesses:

(1) Unvalidated gene and pseudogene annotations: Long-read and consensus genome assemblies are known to suffer from residual indel errors that create artificial frameshifts and premature stop codons. The frequency of predicted pseudogenes in this study (~3.5%-4.5%) aligns closely with expected baseline annotation error rates. Although the authors state in their Methods that mutations were validated using short reads, this validation is never quantitatively demonstrated or shown in the results. The fact that most proposed pseudogenes are actively transcribed and lack a paralog strongly suggests that many are intact, functional genes affected by sequencing or annotation artifacts.

(2) Assembly gaps and GC-bias mistaken for gene loss: The claim that ancestral chickens possessed ~22,000 protein-coding genes and lost thousands of genes in only ~10,000-50,000 years is inconsistent with the evolutionary conservation of avian genomes. The missing genes are enriched for high GC content and preferentially located on microchromosomes. Avian microchromosomes and dot chromosomes are notoriously GC-rich, repeat-dense, and prone to severe assembly gaps in non-telomere-to-telomere assemblies. The reported gene absences reflect assembly fragmentation and coverage dropouts rather than evolutionary deletions.

(3) Lack of synteny validation: Genuine gene absence requires demonstrating conserved collinear synteny of flanking orthologous genes with an unambiguous sequence deletion at the locus. Relying on sequence alignment or short-read mapping failures across fragmented scaffolds substantially inflates false-positive gene loss calls.

(4) Positional bias of pseudogenization mutations: The observed concentration of pseudogenization mutations in the terminal 10% of coding sequences (the "bathtub" distribution) is characteristic of alignment boundary artifacts and non-canonical translation start/stop annotations, rather than positive selection to disrupt gene ends. Mutations in the terminal 3' region often produce functional proteins with slightly altered C-termini rather than complete loss of function.

(5) Inconsistent terminology: The manuscript alternates between identifying pseudogenes as unitary (lacking a functional paralog in the same genome) and evaluating sequence identity against "parental genes," creating substantial confusion regarding whether loci are duplicated paralogs or orthologous reference genes.

Reviewer #3 (Public review):

Summary:

The authors reanalyze genome assemblies of four indigenous chicken breeds from Yunnan Province together with the red jungle fowl reference (GRCg6a), and search for genes with disrupted protein-coding sequences. They catalog candidate pseudogenes and missing genes to estimate that 7,993 of the ancestral genes are dispensable. They characterize the positional distribution of pseudogenization mutations along coding sequences, their fixation in breeds, their estimated ages, and their pathway enrichments. Most results are replicated in four independent PacBio HiFi-based chicken assemblies. From the biased position of pseudogenization mutations toward CDS ends, their frequent fixation, and the phylogenetic signal in gene-loss patterns, the authors conclude that large-scale loss of function is a major driver of chicken evolution and domestication, consistent with the "less-is-more" hypothesis.

Strengths:

The catalog itself is a substantial resource: the comparison spans multiple closely related genomes, the main patterns are checked in a second, independently assembled set of HiFi genomes, and population resequencing data are used to ask whether the pseudogenization mutations are fixed rather than segregating. The finding that candidate loss-of-function genes are under relaxed purifying selection is well supported. The question of what gene loss contributes to domestication is worth asking, and this is a useful dataset for asking it.

Weaknesses:

The finding that genes carrying disruptive mutations are under relaxed selection is not particularly surprising, and the more interesting claim, that the observed patterns reflect positive selection for gene loss, is less certain in my opinion.

(1) Relaxed purifying selection versus positive selection. The bias of pseudogenization mutations toward the two ends of coding sequences is interpreted as positive or artificial selection, along with elevated dN/dS. But the alternative, that disruptive mutations at gene ends are simply better tolerated, is equally consistent with the results. Several mechanisms would produce this pattern under relaxed constraint without positive selection per se: alternative downstream start sites that rescue 5-prime disruptions; the small fraction of protein truncated by 3-prime disruptions; and the enrichment of disordered regions at protein termini.

(2) The functional status of the pseudogenes is assumed, not demonstrated. Genome-scale work cannot be expected to validate individual genes, but the language of the paper should reflect the candidate status of these calls. Nearly all predicted pseudogenes (~95%) were reported as transcribed in multiple tissues. It is possible for a nonfunctional coding sequence to retain intact regulatory sequences, but the observation deserves more attention in the paper, particularly because transcripts carrying premature termination codons can be the targets of nonsense-mediated decay, which is not discussed. These remain candidate pseudogenes defined by the presence of a putatively large-effect mutation (e.g. premature stop or frameshift).

(3) What "missing" means. For a gene to be scored as completely absent, it could be genuinely deleted, or its allele could be diverged enough that annotation and orthology/mapping no longer detect it. These are different phenomena. Related, since most pseudogenization mutations are reported as fixed or nearly fixed in their populations, the history of alleles matters: it is not clear how the authors established which state is derived, and whether the reference sequence assumed to be functional is in fact the "functional" version.

(4) Limited biological insight into domestication. The main biological interpretation rests on hierarchical clustering of dispensable genes followed by ontology enrichment within clusters (Figure 7a), with narrative connections to breed phenotypes. Only 19.6% of dispensable genes have Gene Ontology assignments, and the phenotype links are speculative. The section on the subspecies origin of the GRCg6a reference is only loosely connected to the loss-of-function story, and the population-genetic analysis supporting it is thin as described.

eLife Assessment

This study provides a valuable and comprehensive in vivo map of proteins in proximity to three vesicle-tethering complexes. The evidence supporting the overall proximity mapping is convincing. However, some aspects of the functional characterization of selected candidates remain incomplete.

Reviewer #1 (Public review):

Summary:

The CATCHR complexes are a family of five multisubunit complexes that act in vesicle tethering in several key transport steps. COG and GARP act at the Golgi, EARP acts on early endosomes, EXOCYST acts in transport to the cell surface, and DSL1 acts on the endoplasmic reticulum (ER). The authors have used in vivo proximity biotinylation and mass spectrometry to look for new neighbours of three of these complexes, COG, GARP, and EARP (despite the title, only two of the three are on the Golgi). The authors then follow up two of the hits, CCDC186 and WWOX, with more directed experiments.

Strengths:

The strength of the paper is that proximity biotinylation is of a high standard. To avoid overexpression, the authors express TurboID-tagged CATCHR subunits in cell lines from which the genes have been deleted. This allows them to confirm that the tagged proteins are functional and correctly located. Mass spectrometry is used to identify the proteins biotinylated in each cell line with four replicates, and the data are clearly presented in figures and supplementary tables. The authors make a good choice of proteins to follow up, as both CCDC186 and WWOX appear potentially interesting.

Weaknesses:

Overall, although the paper is based on a high-quality initial set of data, it seems somewhat incomplete and preliminary. There is undoubted value in presenting a through if descriptive set of in vivo proximity labelling data for a comprehensive overview of proteins or complexes. However, in this case the authors have only addressed three of the five CATCHR complexes, and so it is not a complete overview. It was also somewhat unclear why they examined VPS52 and VPS53, as these are present in both GARP and EARP, which adds some ambiguity, even if they did at least provide useful confirmation of some of the hits with EARP. Of course, a proximity biotinylation analysis does not need to cover all members of a family if it generates substantial biological insight.

However, the investigation of CCDC186 and WWOX does not provide significant insight into either function or mechanism. CCDC186 has already been identified in C. elegans as a protein involved in dense core vesicle biogenesis (CCCP-1, as the authors acknowledge), and work in C. elegans and mammalian cells has already linked it to EARP function. Less has been published on WWOX, but all that is found here are some small changes in Golgi appearance and glycosylation when it is reduced by RNAi. Thus, the paper falls between two stools: it is neither a comprehensive application of proximity biotinylation to the CATCHR family, nor is it the application of proximity biotinylation to reveal new insight into membrane traffic. I feel that for a broad-interest journal such, it should be one or the other of these.

Reviewer #2 (Public review):

In this manuscript, Aragon-Ramirez et al. present the first systematic proximity-interaction map of the three Golgi/endosomal CATCHR tethering complexes - COG, GARP, and EARP. They generated hTERT-RPE1 knockout lines rescued with C-terminally TurboID-tagged subunits (COG4, COG6, VPS50, VPS52, VPS53, VPS54) expressed from the COG4 promoter at near-endogenous levels, verified that each construct rescues its KO phenotype, and confirmed expected localization by immunofluorescence. Fifteen-minute biotin pulses followed by streptavidin capture and label-free DIA mass spectrometry, benchmarked against GFP-TurboID, yielded compartment-resolved neighbor lists. The central claim of this work is that each complex sits within a distinct "trafficking module" of coiled-coil tethers (CCTs), SNAREs, SM proteins, Rab GTPases, coats, and homeostasis regulators. COG neighbors nearly all Golgi golgins plus the STX5-SCFD1 fusion machinery, with COG4 and COG6 lobes showing overlapping but non-identical hierarchies - this is offered as in vivo support for a two-lobe model. GARP associates with TGN golgins GOLGA1/GOLGA4, STX16 and partners, TBC1D23, and CLINT1. EARP associates with GRIPAP1, RELCH, RAB11FIP5, and the VPS33B-VIPAS39 (CHEVI) SM complex; a VPS53 MUN-domain mutant loses VPS33B proximity while retaining VPS50 labeling. Two hits are followed up in this study. CCDC186, a poorly characterized coiled-coil protein, localizes to the TGN and, when ectopically anchored to mitochondria, captures ~60 nm vesicles - presented as direct evidence of tethering activity. WWOX, a tumor suppressor with no prior trafficking role, colocalizes with COG8 in the medial Golgi; siRNA knockdown reduces Golgi area, increases HPA and GNL lectin binding (O- and N-glycosylation defects), and displaces COPB2 from the Golgi. Based on these findings, the authors conclude that CATCHRs are not isolated tethers but organizing hubs that assemble compartment-specific tethering-and-fusion modules. Overall, this is a solid piece of work that will be of interest to cell biologists.

(1) The CCDC186 mitochondrial assay demonstrates sufficiency in a non-native context but includes no loss-of-function work, and the cargo-specificity result carrying most of the interpretation is "data not shown." At a minimum, the authors should show KO/KD and rescue data.

(2) The WWOX section rests on a single siRNA with no second oligo, no rescue, knockdown shown only by RT-PCR, and localization based entirely on overexpressed myc-tagged protein.

(3) Proximity of labeling does not distinguish direct from indirect interactions. When referring to "interactions", the authors either need to show recombinant protein binding data, or soften the tone to acknowledge potential indirect interactions.

(4) The VPS53 MUN-domain mutant design rests on a "manuscript in preparation," and the mutant's localization isn't shown (VPS50 labeling establishes complex incorporation, not correct targeting). The HEK293T WWOX replication is "data not shown." The authors should either show the data or delete these claims.

(5) References 73 and 78 are duplicates.

(6) "NZR" is used in the introduction. Should this be NRZ?

Reviewer #3 (Public review):

Summary:

This manuscript presents a comprehensive proximity proteomics analysis of Golgi- and endosome-associated CATCHR complexes, including COG, GARP, and EARP, using near-endogenously expressed TurboID-tagged subunits. The study aims to define how these tethering complexes organize distinct trafficking modules involving coiled-coil tethers, Rab-associated proteins, SNAREs, SM proteins, and other trafficking regulators. In addition to validating known associations, the authors identify CCDC186 as a candidate vesicle tether and WWOX as a potential regulator of Golgi homeostasis and glycosylation. The work provides a broad resource for understanding the spatial organization of CATCHR-associated trafficking networks. However, several conclusions require further experimental and statistical support, particularly those interpreting proximity-labeling data as physical interactions or evidence of discrete functional complexes.

Strengths:

The manuscript addresses an important question in membrane trafficking and provides a systematic comparison of the proximity interactomes of COG, GARP, and EARP complexes. The use of near-endogenously expressed TurboID-tagged subunits is a strength, as it may reduce artifacts associated with protein overexpression. The dataset is comprehensive and has the potential to serve as a valuable resource for investigators studying Golgi and endosomal trafficking. The comparative analysis identifies both known trafficking factors and potentially novel regulators, including CCDC186 and WWOX. The functional follow-up experiments add biological relevance to the proteomic findings and extend the study beyond descriptive mapping. Overall, the scope is well defined, and the manuscript proposes an interesting model in which CATCHR complexes act as organizing hubs for vesicle tethering and fusion.

Weaknesses:

A major limitation is that TurboID proximity labeling is repeatedly interpreted as evidence of physical interaction or assembly into discrete complexes, although the method primarily reports spatial proximity. The soluble GFP-TurboID control may not adequately account for enrichment caused by membrane confinement and high local protein concentration in Golgi/endosomal microdomains. Some spatial enrichment analyses do not reach statistical significance, weakening claims of compartment-specific labeling. Several low-fold-change SNARE hits are emphasized despite limited enrichment. Additional quantitative imaging is needed, including colocalization analysis of streptavidin labeling with Golgi/endosomal markers and localization of GFP-TurboID. The WWOX knockdown phenotype requires validation by rescue, independent siRNA, or CRISPR-based approaches. Several supporting data, quantifications, figure corrections, and nomenclature revisions are also needed.

eLife Assessment

This important study investigates how GDNF treatment restores nerve cells in the bowel of a mouse model of Hirschsprung disease, and proposes that this regeneration occurs through diverse resident precursor cells and a non-canonical signaling pathway. The evidence is solid for the ability of the treatment to induce new bowel nerve cells and for a contribution from multiple precursor populations, supported by extensive cell tracing and imaging experiments. This work will be of interest to researchers in developmental biology and peripheral neurobiology.

Reviewer #1 (Public review):

Gary, Soret et al., present an interesting and ambitious study investigating the cellular and signaling mechanisms by which GDNF induces enteric neurogenesis in a disease model of HSCR. The manuscript combines scRNA-Seq, pharmacological inhibition, and several lineage-tracing strategies. The lineage tracing experiments in particular are technically impressive and clearly represent a substantial amount of work. The figures are generally beautiful and high quality, and the biological question is an important one.

However, while I found the study interesting, I also think that several of the major conclusions are substantially stronger than what the current data support. In particular, the scRNA-Seq dataset that the study is founded on is difficult to interpret because of the RFP-based enrichment strategy, the lack of WT reference controls, and the very non-stringent FACS gating. Several mechanistic claims are also based primarily on expression patterns or sequencing results.

Major concerns:

(1) The G4-RFP based enrichment strategy raises some concerns. The authors note that 88-90% of SOX10+ glial cells (where did this number come from, it doesn't seem to match the range in the bar graph?) and only 70% of GDNF-induced neurons. They then sort in "yield" mode using a non-stringent gating strategy, but do not provide the flow graphs in the supplements for interpretation. Consistent with this, the initial dataset contains multiple non-ENS populations, including lymphoid, myeloid cells etc, suggesting that their strategy, in addition to missing cell populations, additionally includes potential negative cells based on background fluorescence.

(2) It's not clear to me why the authors did not include a wild-type control for comparison. Due to the RFP-enrichment strategy, it is additionally difficult to compare to integrated with scRNA-seq datasets. The comparison seems important because the central question is not only whether GDNF induces neurons in the mutant colon, but whether the induced cells and associated populations resemble those found in a normal ENS.

(3) The proportional changes in Figure 2 are hard to interpret. The authors write that GDNF treatment leads to an enrichment in enteric neurons, "at the expense of" SCPs. This seems to be a strange conclusion or writing, unless the authors are suggesting that certain cell populations are additionally depleted by GDNF treatment. I think the authors should provide stronger support, or dial down on conclusions based on cluster proportions, given the sorting strategy.

(4) Some of the mechanistic conclusions are far too strong for the evidence. For instance, the claim that GDNF signals through GFRa1/2 based on only expression UMAPs is not justified. The authors should at least confirm some of the major findings via smFISH (HCR or RNA-Scope), and dial down the mechanistic claims. The pharmacological data is more supportive but still indirect. This section would be stronger if the authors validated NCAM1/FAK activation in the specific progenitor populations proposed to respond to GDNF.

(5) The inhibitors are administered during the same P4-8 window as GDNF. Given that the authors report cellular-level responses as early as 6 hours post GDNF treatment, it is important to know whether the inhibitors were already active at the time of GDNF administration. Why were the inhibitors not administered prior to the start time of GDNF treatment?

(6) The authors draw inferences and conclusions based on IHC images, but do not provide any details on the analysis procedures. For example, in Figure 3, the authors interpret changes in NCAM and FAK expression level. However, it does not appear that there are notable differences in intensity between the two timepoints. There are however, differences in signal coverage. Without knowing what was actually measured and quantified, it is not possible to interpret the results. Please provide the necessary information for all experiments in the methods section.

(7) The final results section introduces one of the more surprising claims in the paper, that a non-neural crest-derived progenitor contributes to regeneration, but the section ends quite quickly and abruptly after introducing the observation. The authors should provide additional validation or interpretations of the data.