Reviewer #1 (Public review):

Summary:

Akkad et al. present an MEG study of overt picture naming, designed to identify oscillatory mechanisms underlying spoken language production. Participants named line drawings of common objects or responded "no" to scrambled versions of the same images. The authors focus on the period preceding articulation and report on an increase in theta power associated with picture naming in lingual cortex and left medial prefrontal cortex. Two networks are then identified: a left lingual-seeded network involving right ventral occipito-temporal cortex, interpreted as supporting object recognition. Second, a left medial prefrontal-seeded network involving medial temporal regions (and centres in the brain) supporting semantic-lexical retrieval streams. The authors further report increased theta-gamma phase-amplitude coupling in left fusiform and left inferior frontal regions, with stronger left fusiform PAC associated with slower naming responses.

Strengths:

The paper provides useful insight into the network-level and temporal dynamics associated with picture naming.

Weaknesses:

The results are somewhat over-interpreted, and the paper would benefit from a broader and more cautious discussion. The main concerns relate to the control condition and the interpretation of the theta-band effects. First, it is unclear whether the control condition adequately isolates the spoken-language network. Second, the reported theta-band effect appears broadband, raising the possibility that it reflects slow evoked responses rather than genuine oscillatory activity.

Reviewer #2 (Public review):

Summary:

In this MEG study, the authors assess the oscillatory dynamics of object naming in 27 participants. The authors observed two distinct theta-coupled networks: a ventral occipito-temporal network linked to object recognition and a medial fronto-temporal network linked to lexico-semantic retrieval. Moreover, when contrasting object naming to a scrambled image control task, they observed increased theta-gamma phase amplitude coupling in the LIFG and fusiform gyrus. The authors conclude that theta-coupling ensures the binding of recognition and retrieval processes in object naming, while the theta-gamma phase amplitude coupling ensures local computations within those networks.

Strengths:

Addressing the question 'which oscillatory dynamics govern speech planning' is interesting and timely, since not much empirical evidence on this topic is currently available. Whole-brain MEG assessing phase and phase-amplitude coupling for object naming are not commonly attempted, and the study boosts a lot of power. Furthermore, the writing is concise and clear, making the paper easy to follow and pleasant to read.

Weaknesses:

My overall assessment is that the claims and conclusions of this study are stronger than the evidence supports, and this is because of several design weaknesses which I will detail below. Moreover, this study gives too one-sided a perspective on the current state-of-the-art in the neurophysiology of speech planning/object naming, and the presented conclusions can solely be understood from that narrow theoretical perspective.

(1) One of my bigger concerns is the lack of any language-related manipulations that allows to independently isolate the processing components the authors discuss. Object naming (speech planning) is a complex, multifaceted mental operation where different representations and processing levels can overlap in time and space (e.g., Indefrey, 2011; Hickok, 2012; Dell et al., 2013; Munding et al., 2016; Strijkers & Costa, 2016; Nozari & Pinet, 2020; De Zubicaray, 2023; Pickering & Strijkers, 2025). Without attempting to isolate those specific representations and/or processes and solely looking at object naming in general, the only manner to interpret the data is by relying on a priori defined and often one-to-one mappings of space and function in light of a specific theoretical perspective. This is indeed what the authors do in the current study, by linking certain brain regions they observe (e.g., more occipital for object recognition and more fronto-temporal for lexico-semantics) to the function assigned in dual-route models (note also that the authors rely on the dual-route models of comprehension, not production per se; see below). While doing so is of course legitimate, it does strongly reduce the impact of the results since they do not concern a direct empirical demonstration of the authors' conclusions, but an indirect inference based on a single theoretical framework. To give a few examples of how this weakens the conclusions: How do the authors know the fronto-temporal network is lexico-semantic and not phonological, as many other models would pose (e.g., Indefrey & Level, 2004; 2011; Hickok, 2012; 2014; De Zubicaray, 2023)? Similarly, theta-coupling in production is not uniquely related to lexico-semantics, but could also be linked to the syllabic rate (speech rate; e.g., Giraud & Poeppel, 2012; Meyer, 2018), or to working memory in production (e.g., Piai & Zheng, 2019). The occipito-temporal network may be involved in object recognition, but it may also reflect (embodied) word semantics, in particular for imageable objects as in the current study (e.g., Strijkers & Costa, 2016; Pulvermuller, 2018). In my opinion, given the lack of independent manipulations, these (and other) alternative conclusions are equally plausible, and the authors' interpretations of the data pattern are tentative at best; this is a substantial limitation in my view.

(2) The authors may object that they do have a contrast, namely the control condition. However, the control condition and the object naming condition differ in so many crucial aspects that it does not serve as a reliable control to address the above issues with interpretational strength. The control condition solely deals with low-level visual input, but not with conceptual and language-related processing, nor with motor preparation and articulation (since repeatedly saying 'no' is a flawed control for the more complex and variable naming responses required in object naming).

(3) Moreover, the timings between the control and object naming conditions are confounded: Naming and control RTs differ by 270 ms. The 1 s pre-response window therefore spans 0.08 to 1.08 s post-stimulus in naming, but −0.19 to +0.81 s in control. Hence, part of the contrast may rather reflect 'when' something was measured rather than 'what' processing differences it is supposed to reflect.

(4) As far as I can tell, the authors did not assess potential pre-articulation motor confounds in the data via ICA and/or recorded EMG activity (e.g., Vos et al., 2010; Porcaro et al., 2015; Strijkers et al., 2017; Abbasi et al., 2021). This may be relevant since motor preparatory activity is known to emerge well before actual articulation (e.g., Ries et al., 2013), and may (pre-)track articulatory speech rate in the theta range (e.g., Abbasi et al., 2023).

(5) Why are items not modelled as random intercepts/slopes? With 200 different stimuli, item variability seems relevant to include in the statistical models.

(6) I found that the authors gave a very restricted and not up-to-date literature overview on the neural basis of object naming. They mainly consider a dual route architecture. I understand that the authors don't wish (nor have to) give a complete overview of the different neurobiological models of object naming. However, the dual route model they cite is the speech processing and comprehension model (e.g., Hickok & Poeppel, 2004; 2007), which has no clear link to object naming, and they don't mention the production versions of a dual route architecture (e.g., Ueno et al., 2011; Hickok, 2012). Moreover, as mentioned also in comment 1, several other critical models (and more relevant for object naming specifically) are neglected: classical sequential object naming models (e.g., Indefrey & Levelt, 2004; Indefrey, 2011; Roelofs, 2014), interactive models (e.g., Dell et al., 2013; Dell & Chang, 2014), or more recent parallel models (e.g., Strijkers & Costa, 2016; Pickering & Costa, 2025) (for recent reviews see: e.g., Nozari & Pinet, 2020; Kerr et al., 2023; de Zubicaray, 2023). If the authors prefer to solely focus on a single class of models, that's fine (though a model that is more tightly linked to object naming would have been more relevant), but that limited scope should at the very least be acknowledged.

Reviewer #1 (Public review):

Summary:

This study presents a workflow for nanoscale imaging of endogenous synaptic receptors in intact adult brain tissue. By combining live-tissue chemical labeling of native surface AMPA receptors (AMPARs) using the CAM2 probe, two-color 3D super-resolution microscopy, adaptive optics, in situ point spread function retrieval, and chromatic aberration correction, the authors establish a platform for quantitative super-resolution mapping of synaptic architecture deep within brain tissue.

The authors provide convincing evidence that AMPAR organization differs between the hippocampus and cortex and demonstrate that early tauopathy is associated with selective disruption of extrasynaptic and synaptic nanodomain receptor organization in the hippocampus prior to overt neurodegeneration.

Beyond the specific biological findings, the work represents a significant technical advance that enables quantitative investigation of endogenous synaptic receptor architecture in native brain tissue and will be of broad interest to researchers in synaptic biology, super-resolution microscopy, and neurodegeneration.

Strengths:

(1) Introduces and validates a strategy for nanoscale imaging of endogenous surface AMPARs in adult brain slices using CAM2 labeling and two-color 3D super-resolution imaging.

(2) Achieves 10s of nanometers localization precision in thick tissue and validates synaptic structural measurements against previous literature benchmarks.

(3) Reveals regional differences in AMPAR organization, including a larger extrasynaptic receptor pool in hippocampal regions compared with neighboring cortical regions.

(4) Identifies early, region-specific alterations in AMPAR distribution and nanodomain organization in the PS19 tauopathy model.

Weaknesses:

(1) Statistical power is limited by the relatively small number of animals analyzed, although large numbers of synaptic structures were sampled within each mouse.

(2) Synaptic classification relies on PSD-95 cluster detection criteria that may bias analysis toward more strongly enriched synapses, as acknowledged by the authors.

Reviewer #2 (Public review):

Summary:

This is a technically sophisticated effort to visualize the nanoscale organization of native surface AMPA receptors in adult mouse brain. The authors combine chemical labeling of endogenous AMPARs with 3D, 2-color super-resolution microscopy. They use this to compare hippocampal and cortical AMPAR organization and to characterize changes in a P301S mutant mouse tauopathy model. The authors report a greater density of surface AMPAR localizations in hippocampal CA1 than in two examined cortical regions, as well as a smaller fraction of AMPARs organized in synaptic clusters. They report that PS19 tauopathy is associated with reduced hippocampal AMPAR localization density, a relative depletion of the population classified as extrasynaptic, and reduced organization of receptors within synaptic nanodomains.

Strengths:

The methodological contribution is substantial. The authors developed a valuable set of methods for examining endogenous surface AMPAR organization in brain tissue. The imaging methodology could be useful across many questions in synaptic neuroscience.

Weaknesses:

While the biological observations are interesting, several aspects of the neuroscience interpretation require clarification, and some of the biological conclusions should be weakened unless the measurements can better justify them. I provide several comments intended to strengthen this interesting manuscript.

(1) The authors measure fluorescent localization counts but often interpret these as AMPAR numbers. I believe that individual fluorophores can generate multiple localizations and that labeling efficiency can vary, challenging their frequent interpretation as AMPAR numbers. Importantly, AMPARs are tetrameric complexes with potentially different subunit compositions, so one AMPAR could be observed as 0-4 fluorescent localizations. The uncertainty is particularly important for comparisons of AMPAR abundance per cluster and nanodomain. The authors should consistently distinguish localization density from receptor number and clarify which conclusions depend on assumptions about labeling and the assumptions of photophysical equivalence between experimental conditions. The paper would be more rigorous and the claims more legitimate if the authors were disciplined throughout about using empirical descriptors instead of interpretations.

(2) The distinction between synaptic and extrasynaptic receptors is central to the manuscript. The authors identify synaptic receptors either through density-based clustering or proximity to PSD-95 clusters. However, neither measure directly establishes anatomical synaptic localization. This is particularly consequential because only ~1/3 of morphologically identified YFP-positive spines contain PSD-95 clusters that meet the detection criteria. It seems to me that AMPARs associated with weakly-labeled or undetected synapses could then be erroneously classified as extrasynaptic. PSD-95 detection should be assessed across regions and genotypes, and a sensitivity analysis undertaken to ensure that the conclusions are robust to the choices of clustering and distance thresholds.

(3) The authors suggest that the larger extrasynaptic AMPAR population in the hippocampus provides a reserve for rapid synaptic recruitment and that its reduction in tauopathy constrains plasticity. This is plausible, but receptor abundance does not establish receptor mobility or availability for synaptic capture. The importance of AMPAR surface diffusion for hippocampal LTP and contextual learning has been demonstrated (see Penn et al., Nature, 2017), but the current study does not measure diffusion or receptor exchange. The authors should temper their interpretation and explain the caveats.

(4) The authors infer that there has been a preferential extrasynaptic AMPAR loss from the reduced total AMPAR localization density and the increased synaptic fraction they measured. Because both synaptic and extrasynaptic populations could decrease even when the synaptic fraction increases, they should calculate the synaptic and extrasynaptic localization densities separately for each mouse. This would clarify the magnitude and selectivity of the changes that they report and help to reconcile the potentially contradictory increased synaptic fraction with reduced AMPAR localization density within synaptic clusters and nanodomains.

(5) The authors adjust DBSCAN parameters for PS19 hippocampus in response to reduced overall localization density. Because the resulting clustering measurements are themselves used to establish genotype differences, it is important to demonstrate that the conclusions are robust to parameter selection. Analyses using identical parameter sets across conditions, together with simulations in which WT localization patterns are subsampled to match PS19 localization density, would help determine whether the reported changes reflect biological reorganization rather than density-dependent detection effects. Similar validation is important for the nanodomain analysis. I found that, in general, the authors should have made a greater effort to ensure that their measurements are robust to the parameter choices.

(6) CA1 comparisons with motor/somatosensory cortex require more precise anatomical characterization. What cortical layers and hippocampal dendritic compartments are being compared? These are not homogeneous structures in almost any regard. AMPAR or, more empirically, fluorescence localization density per imaging field is not necessarily equivalent to AMPAR density per dendritic membrane area or per synapse. Differences in neuropil composition, spine density, and synapse density could contribute to the observed differences when there is, in fact, no AMPAR density per dendritic membrane area. Proper anatomical normalization or a stricter comparison of equivalent neuronal compartments would strengthen the interpretation. I believe that the authors are aware of the issue, as they did an analysis along a single dendrite, but this has to be done more thoroughly for them to justify the conclusions they assert.

(7) The main comparisons involve three mice per group, and the authors correctly analyze mouse-level averages. Nonetheless, the small number of biological replicates limits the strength of the conclusions about regional specificity and disease effects. The test statistics and degrees of freedom, not just the p-values, should be presented. In addition, effect sizes and individual mouse values should be presented. The absence of a statistically significant cortical effect does not establish that cortex is unaffected. There could be genotype-by-region interactions, which the authors should check.

(8) The authors describe that 6-mo PS19 mice precede neurodegeneration and they assert that the observed AMPAR-associated changes relate to the onset of synaptic dysfunction. However, Yoshiyama et al., Neuron, 2007 demonstrate hippocampal synapse loss and impaired synaptic function at three months in PS19 mice, before detecting fibrillary tau. The present observations likely occur after synaptic pathology in thePS19 mice. The authors should distinguish structural correlates of established dysfunction from the mechanisms that may have initiated that dysfunction. More importantly, the assertion that neuronal or synaptic anatomy is preserved in the PS19 mice should be supported by appropriate measurements.

(9) The reduction of the AMPAR nanodomain organization is potentially important. However, the authors do not measure presynaptic release sites or trans-synaptic alignment. To be rigorous, the data establish altered postsynaptic receptor organization but do not demonstrate disruption of trans-synaptic nanocolumns or establish the functional consequences for quantal transmission. If the authors do not provide evidence for these claims they should not make them and make it clear these are (reasonable) speculations for which they did not collect the data.

Reviewer #1 (Public review):

Summary:

Hsiung et al. investigated whether the effects of autophagy gene knockdown on the lifespan of long-lived C. elegans mutants depend on experimental conditions. The authors first compiled published data on autophagy-dependent lifespan regulation in daf-2 and wild-type backgrounds, highlighting that prior results are notably inconsistent and likely context-dependent. They then systematically tested the lifespan effects of RNAi knockdown of six autophagy genes (atg-2, atg-4.1, atg-9, atg-13, atg-18, and bec-1) in wild-type (N2), daf-2 (reduced insulin/IGF-1 signalling), and glp-1 (germlineless) animals, while varying temperature, daf-2 allele, FUDR concentration, and bacterial infection status.

The key findings are as follows. In wild-type animals, lifespan suppression by most autophagy gene knockdowns was more pronounced at 20{degree sign}C than at 25{degree sign}C, where little or no effect was observed. In daf-2 mutants, stronger lifespan suppression was seen in the weaker daf-2(e1368) allele at 20{degree sign}C, but not in the stronger daf-2(e1370) allele, and effects were largely absent at 25{degree sign}C. In glp-1 mutants, four of six gene knockdowns suppressed lifespan to a greater extent than in N2, though again in a temperature-dependent manner. FUDR at a high concentration (800 µM) abolished the life-shortening effects of most knockdowns and, in the case of atg-9 and atg-13, led to lifespan extension. Kanamycin treatment to eliminate bacterial proliferation did not fully account for the lifespan effects, suggesting that increased susceptibility to infection is not the primary mechanism. The authors also tested the programmed aging hypothesis that autophagy promotes lifespan reduction through biomass repurposing, but found no changes in vitellogenin levels upon knockdown of any of the six genes.

Altogether, among all genes tested, atg-18 knockdown produced the strongest and most consistent lifespan suppression across nearly all conditions, including both daf-2 and glp-1 backgrounds. The authors probed whether atg-18 acts through the FOXO transcription factor DAF-16 by examining dauer formation and ftn-1 expression, but found no evidence for this, suggesting a DAF-16-independent mechanism.

Strengths:

The primary strength of this work lies in its systematic and comprehensive approach to dissecting how experimental variables influence the outcome of autophagy-lifespan epistasis tests. The compilation of prior data alongside the authors' own multi-condition dataset is a genuinely useful resource for the field. The study raises a timely and important point about condition selection bias in interpreting autophagy lifespan relationships, with broader relevance to C. elegans studies. The finding that atg-18 behaves distinctly from other autophagy genes across a range of experimental conditions is particularly noteworthy and provides an interesting direction for future mechanistic investigation.

Reviewer #2 (Public review):

Summary:

This study examines how genes involved in cellular recycling (autophagy) influence lifespan under different experimental conditions. The findings help clarify why previous studies have reported conflicting results about whether blocking autophagy shortens or extends lifespan. The work will be of interest to researchers studying aging and cellular stress responses, particularly those using model organisms.

Strengths:

The findings are valuable, as they help resolve inconsistencies within a specific subfield of aging research. The evidence presented is solid, as the data broadly support the primary claims of the study. In addition, the discussion is thorough and thoughtfully integrates the findings within the broader context of the field.

Reviewer #1 (Public review):

Summary:

This manuscript asks how the uterine lumen is remodeled across the peri-implantation window and whether this remodeling is functionally linked to embryo attachment and subsequent pregnancy establishment. The authors combine whole-organ three-dimensional imaging of optically cleared mouse uteri with single-cell and spatial transcriptomic profiling, conditional deletion of p38α at the uterine-wide versus epithelial-restricted level, and rescue experiments using progesterone and leukemia inhibitory factor. Based on these datasets, the authors propose that the luminal epithelium undergoes a previously underappreciated phase of organ-scale architectural reorganization before attachment, and that a p38α-dependent stress-responsive program coordinates epithelial remodeling together with epithelial-stromal communication required for implantation competence.

Strengths:

By moving beyond local attachment-site morphology to a horn-level representation of luminal topology, the work provides anatomical context that is difficult to reconstruct from conventional section-based approaches and should be broadly useful to the implantation community. The integration of organ-scale morphology with single-cell and spatial transcriptomic datasets, together with genetic perturbation and rescue experiments, adds breadth and increases the potential long-term utility of the dataset for investigators interested in uterine receptivity and embryo-uterine interactions.

The revision has addressed several important concerns from the original review. The added methodological details and comparison with conventional two-dimensional histology provide greater confidence that the luminal features observed by whole-organ imaging are not artifacts of tissue clearing or reconstruction. The additional measurements of epithelial folding and orientation also provide better quantitative support for luminal remodeling. The mechanistic interpretation of the p38α findings has also been improved.

Weaknesses:

Most of the major concerns raised in the original review have been addressed. I have only a few remaining comments.

First, the authors have appropriately toned down the causal language regarding embryo positioning. However, because different animals were analyzed at different time points, the direction of the relationship between luminal remodeling and embryo position cannot be determined. A few statements still sound somewhat causal, such as luminal movement "contributes to embryo spacing" and persistent epithelial branching "led to randomized embryo positioning." These could be further softened to reflect associations rather than causality.

Second, some mechanistic claims could also be more cautious. For example, the Figure 9 title states that embryo invasion failure occurs "owing to sustained epithelial polarity." The persistence of E-cadherin and β-catenin is consistent with altered epithelial polarity, but does not establish it as the cause of invasion failure. "Associated with sustained epithelial polarity" would be more appropriate.

Third, the added quantitative analyses are helpful, but the individual animal should remain the biological replicate. When multiple sections from the same dam are analyzed, these should not be treated as independent biological replicates.

Finally, the Figure 9c legend refers to β-actin, whereas the Methods and figure indicate β-catenin. This should be corrected.

Reviewer #2 (Public review):

Summary:

In this study, the authors investigate luminal architectural reorganization during embryo implantation. Using 3D histological reconstruction, single-cell RNA sequencing, spatial transcriptomics, and genetic mouse models, the authors the uterine luminal epithelium undergoes rapid morphogenetic remodeling during the implantation. They further propose that a stress-responsive p38α signaling program coordinates epithelial remodeling and epithelial-stromal communication to establish an implantation-competent uterine lumen.

Strengths:

This study clearly described the changes of luminal architecture during implantation. Moreover, they also used integration of multiple advanced techniques, including 3D tissue reconstruction, single-cell transcriptomics, spatial transcriptomics, and genetic mouse models, which together provide a detailed description of the molecular characters of the uterine architecture during implantation.

Weaknesses:

The principal knockout model uses Pgr-Cre, which deletes p38α in both epithelial and stromal compartments. Importantly, they also added epithelial-specific knockout (Ltf-Cre) demonstrates that epithelial deletion alone produces only mild abnormalities and does not recapitulate the severe implantation phenotype observed in the uterine knockout. These data suggest that the critical function of p38α likely resides in stromal cells or in epithelial-stromal interactions. Consequently, the manuscript's title and central conclusion currently a little bit overstate epithelial regulation.

The data of this study are now support the main conclusions.

Impact of the work on the field:

This work will likely become an important resource for researchers studying embryo implantation because it provides a detailed atlas of peri-implantation uterine morphology integrated with spatial and single-cell transcriptomic datasets. The imaging methodology and quantitative description of luminal remodeling are likely to be widely useful.

Reviewer #1 (Public review):

Summary:

In this manuscript by Rezaei F. et al., the authors determine a cryo-EM structure of the human ABCG5/G8 ABC transporter that was expressed in Pichia Pastoris. The structure was nearly identical to previous crystal and cryo-EM structures of ABCG5/G8, and displayed a non-protein density in the central transport pocket between both halves of the transporter. Since the expression host Pichia pastoris natively makes ergosterol rather than cholesterol, and cholesterol hemisuccinate (CHS) was added during protein solubilization and purification, the authors used molecular dynamics simulations to probe the stability of binding for cholesterol, CHS, and ergosterol in the central pocket where the density was identified. These simulations suggested that ergosterol, rather than CHS, occupies the central pocket in the cryo-EM structure.

The authors then went on to investigate the effect of ergosterol on ABCG5/G8 ATPase activity. Interestingly, ergosterol was more potent than cholesterol or CHS in stimulating ABCG5/G8 ATPase activity. It was further demonstrated that the hydroxyl moiety of Y342 in ABCG5 is essential to achieve full stimulation of ATPase activity by ergosterol, but not cholesterol. This assay highlights a key residue (Y342) in ABCG5 that contributes to differential sterol sensitivity of ABCG5/G8.

Overall, this is a compelling story with solid biochemical kinetic data that largely support the interpretation that binding of ergosterol gives rise to the sterol-like density in the transport pocket of ABCG5/G8.

Strengths:

(1) The finding that ABCG5/G8 responds to ergosterol more strongly than cholesterol is very interesting. This suggests a plausible role for ABCG5/G8 in regulating absorption of exogenous sterols from the human diet.

(2) The biochemical kinetics data appear to be quite strong, with appropriate replicates and statistical analyses in most locations.

(3) The cryo-EM density map appears to be of good quality despite an overall resolution of ~3.6 Å.

(4) The manuscript and figures are well prepared and easy to follow.

Weaknesses:

(1) While I agree with the conclusion that the central density is likely not CHS, how can the authors be sure that this is not cholate (which was included throughout solubilization and purification)?

(2) The authors do comment on the role of the hydroxyl on Y432 being important for differential regulation of the transporter by sterols. However, it was not clear to me how the hydroxyl of Y342 could contribute to enhanced activity with ergosterol and not cholesterol. These two molecules are very similar and bind in essentially the exact same location. Could it be that the additional double bond (creating a conjugated double-bond system) in the B-ring of ergosterol interacts with Y342 in a favorable manner that is not possible with cholesterol, which lacks this double bond? It seems like more discussion on the chemical similarities and differences between ergosterol and cholesterol is warranted in order to potentially explain why the Y342 hydroxyl moiety is so critical for stimulation with ergosterol but not cholesterol.

(3) Minor weakness: Enthusiasm for the cryo-EM structure is slightly tempered by the fact that the structure is essentially identical to a previous ABCG5/G8 cryo-EM structure bound to cholesterol.

(4) I am a little confused by Figure 1D. If the RMSD is calculating the ligand position relative to its initial position in the first frame, then shouldn't the RMSD value for all ligands start at zero when the time is zero? Why does RMSD not start at 0 for all ligands and then gradually increase as the simulation progresses? Similarly, why is the starting RMSD at time 0 so different for ergosterol, cholesterol, and CHS?

(5) It would be good to include a "no sterol" control for the experiments in Figure 3B. Is the basal ATPase activity without sterols the same for WT and Y342F constructs?

(6) In Figure 4D and Table 1 (bottom), ATPase activity is measured as a function of sterol concentration, and the data are fit using a Michaelis-Menten equation, with Vmax and Km reported. I do not think that interpreting these parameters as Vmax and Km is appropriate for this experiment. Although a saturating Michaelis-Menten-type equation can be used to describe the dependence of ATPase activity on sterol concentration, sterol is not the substrate being directly measured in the ATPase reaction. Rather, the experiment measures sterol-dependent stimulation of ATP hydrolysis. Thus, these data are more appropriately described as a sterol dose-response or activation curve, and an apparent EC50 would be a more appropriate parameter to report. A true Km for sterol would require measurement of the sterol transport reaction as a function of sterol concentration.

(7) It would be good to include statistical analyses of the interaction energy decompositions from molecular dynamics (Figure 2C) where appropriate. For instance, is the difference between interaction energies for (G5)-Y424 really different for cholesterol and ergosterol? The error bar for ergosterol makes it hard to tell if this difference is statistically significant.

(8) The changes in side-chain orientations noted in the paper (Figure 2B) are really very, very small changes. I am not quite sure that these represent true changes due to ligand binding, versus small changes in model refinement into intermediate resolution range maps (~3.6Å cryoEM and ~4Å crystal structure).

(9) The discussion surrounding an alternative sterol binding pocket, and particularly its involvement in sterol flip-flop (Figure 4B), seems very speculative.

(10) The authors included AMP-PNP and MgCl2 in their sample for cryo-EM, but did not observe a closed state in 3D classification. Any speculation as to why the open conformation was obtained, or, more importantly, why AMP-PNP was included at all?

Reviewer #2 (Public review):

Summary:

Rezaei et al. determined the cryo-electron microscopy structure of human ABCG5/8 in complex with ergosterol, revealing a conserved sterol-binding site at the transmembrane domain (TMD) interface, signifying the role of a specific key residue, Y432, in the interaction. ATPase assays showed the effective stimulation of ATPase activity of ABCG5/8 in the presence of ergosterol than cholesterol and CHS. The role of Y432 in the interaction with the transporter and stimulation of its ATPase activity was further supported by a mutagenesis study.

Strengths:

The study has been supported well with the structural and biochemical data combined with molecular dynamics simulations. The methods are very well detailed, which is helpful for the reader.

Weaknesses:

A few more experiments along similar lines (structures and mutagenesis and ATPase experiments) would have strengthened the molecular mechanism of sterol transport. Also, the physiological relevance of this sterol-ABCG5/8 structure has not been elaborated or connected via any experiments.

Reviewer #3 (Public review):

Summary:

This study provides structural and functional insights into the sterol recognition mechanism of ABCG5/G8.

Strengths:

The modeling of ergosterol into the density map is plausible, considering that the protein was heterologously expressed in yeast, only CHS was added during purification, and MD simulations rendered CHS binding to this site unlikely. The identified ergosterol-binding site in the central TMD cavity closely aligns with the location previously observed in a cholesterol-soaked crystal structure, strongly supporting the notion that this cavity serves as the primary substrate-transport pocket. Furthermore, mutagenesis of the key Tyr residue abolishes the ergosterol-specific enhancement of ATPase activity, providing robust functional support for the structural findings.

Weaknesses:

However, several caveats should be considered when interpreting these results:

First, while local resolution in the TMD region appears sufficient to trace side chains, the overall resolution of 3.5 Å poses challenges for precisely discerning subtle side-chain movements or rotamer changes. As the structural comparison with the apo and CRL-bound forms reveals no major helical shifts-remaining confined to side-chain rearrangements-caution is warranted when attributing mechanistic significance to these localized variations without exhaustive functional validation.

Second, a major limitation lies in the mechanistic model proposed by the authors. The manuscript suggests that the peripheral cholesterol-binding site (CRL) observed exclusively in previous crystal structures represents an intermediate state of sterol flip-flop. However, the authors provide no new experimental or computational evidence in this study to substantiate this hypothesis. Consequently, this model remains speculative and lacks sufficient empirical backing at this stage.

Reviewer #1 (Public review):

Summary:

The manuscript presents several reinforcement learning (RL) approaches to control activity in small, ring-shaped neural networks. The paradigm is to find temporally and spatially patterned stimuli applied to axons that maximize the length of activity propagation along the network. Several RL versions were compared. Some RL-designed stimulation patterns worked better than others.

Strengths:

The work is technically and statistically very sound, and important controls were done that are missing in some earlier work along this line of research. The statistics and technical solutions seem solid, though I am no specialist in RL. The figures are well done and informative, with matching quality of the captions. The work presented is of value mainly for someone who wants to build a good closed-loop stimulation system to experiment with neuronal networks in-vitro.

Weaknesses:

The manuscript appears undecided about whether it wants to be about RL control, about a technical implementation of long-term stimulation in vitro, or about the properties of neuronal networks and interaction with them. The introduction is well written, comprehensive and insightful, focusing on biological aspects. Methods are then extensively about RL algorithms, without explaining why several were used or why these in particular, but with specialist language hard to understand for neuroscientists. The results then quantitatively compare the performance of the RL but do not really explain what this teaches us about neuroscience or what we learn about the networks beyond that they can be stimulated for longer propagation patterns. Extensive supplementary material almost advertises the hardware built by the team. Some figures suggest, though I'm not 100% certain about this, that different algorithms find different optimal stimulation patterns in the same network - which I find puzzling. What then does this tell us about the stimulation patterns and the variability of the responses? There is some speculative mechanistic reasoning, but no data to support this further. The conclusions hardly address the initial motivation of the manuscript. To me, it is not clear what can be learned that was not, in one way or another, presented previously, with as well as without RL.

Reviewer #2 (Public review):

The authors developed a reinforcement learning framework to identify stimulation patterns that produce a predefined activity pattern in neuronal networks cultured on a microelectrode array. The main contribution of this study lies in the development and validation of the experimental framework, rather than in providing new insight into neuronal response properties or the biological mechanisms underlying network activity.

A major strength of the work is that the framework is implemented using open-source software. Electrical stimulation through microelectrode arrays is already widely used, and the proposed approach is therefore likely to be of interest to researchers seeking to automate the exploration and optimization of stimulation parameters. The authors also provide the software, hardware configuration, and experimental data, which substantially improves transparency and should facilitate reproduction and further development of the system by other laboratories.

The experiments provide a useful proof of concept showing that the framework can search for stimulation patterns associated with the predefined task in the tested neuronal network. The evidence is solid for demonstrating the feasibility of the approach within this specific experimental configuration. In particular, the closed-loop integration of stimulation, recording, evaluation of the neuronal response, and subsequent selection of stimulation patterns is clearly implemented and experimentally tested.

An important limitation is that the framework was evaluated using a relatively small and highly structured network. Four stimulation electrodes were positioned around a single network, and stimulation was delivered to microchannels in which axons were concentrated. This configuration is well suited to the initial demonstration, but it remains uncertain whether the same approach will perform similarly in conventional monolayer dissociated cultures, larger networks, or systems with different numbers and spatial arrangements of electrodes. Additional validation across a broader range of network structures and experimental configurations would therefore be needed to establish the general applicability of the framework.

Overall, this study presents a valuable and reproducible methodological framework for the closed-loop optimization of electrical stimulation in cultured neuronal networks. Its likely impact lies primarily in providing an accessible experimental and computational platform that can be adapted for studies requiring systematic exploration of stimulation patterns, although the extent to which the current findings generalize beyond the tested network configuration remains to be determined.

Reviewer #3 (Public review):

Summary:

This study integrates living neuronal circuits with a real-time reinforcement-learning framework to enable closed-loop optimization of directional firing sequences at single-spike resolution. By using the spatiotemporal structure of neuronal firing as feedback, the system adaptively searches for stimulation patterns that increase a predefined propagation reward. The work represents an exciting step toward systematic and adaptive control of living neuronal networks.

Strengths:

The study presents a cutting-edge closed-loop platform that combines neuronal cultures, high-temporal-resolution electrophysiology, and reinforcement learning with millisecond-scale latency. The ability to optimize directional activity propagation at single-spike resolution is particularly novel. More broadly, the work provides a compelling framework for interacting with biological neural networks in an adaptive rather than purely predefined manner.

Weaknesses:

Several aspects of the analysis and interpretation require further clarification. In particular, the definition and computation of directional propagation and reward are not always clear. The generalizability of the optimized stimulation patterns across cultures also remains unclear.

Reviewer #1 (Public review):

Summary:

The authors examine the roles of CKAP2 and CKAP2-Like in ciliogenesis. They assess the localization of both proteins in primary and motile cilia of the human male reproductive tract and use hTERT-RPE1 cells to investigate CKAP2 function. They report that CKAP2 localization is associated with cell-cycle progression and that its intrinsically disordered region is required for ciliary localization. Loss of either CKAP2 or CKAP2-Like results in elongated cilia, whereas loss of both proteins reduces ciliogenesis and restores ciliary length to approximately wild-type levels. Based on these findings, the authors propose compensatory interactions between the two paralogs.

Strengths:

The study combines tissue localization, knockout cell lines, quantitative analysis of ciliogenesis and ciliary length, and live imaging of CKAP2 dynamics. The findings extend previous work implicating CKAP2 and CKAP2-Like in microtubule regulation and support roles for both proteins in ciliogenesis and cell-cycle-associated ciliary dynamics. Overall, the study is convincing and should be of interest to readers.

Weaknesses:

The proposed compensation model requires further support. Because cilia are longer in the single-knockout cells, the ciliary fluorescence signals of CKAP2 and CKAP2-Like should be normalized to ciliary length. The same issue applies to the acetylated-tubulin fluorescence measurements. Furthermore, the ciliary-length phenotypes and increased localization of the remaining paralog do not by themselves establish functional compensation. Additional experiments are needed to determine whether acute depletion of the remaining paralog in each single-knockout background reproduces the double-knockout phenotype and whether expression of either paralog can rescue the double-knockout cells.

Reviewer #2 (Public review):

Summary:

The authors build on previous work demonstrating that the microtubule-associated protein CKAP2 functions at the mitotic spindle to regulate microtubule dynamics for proper chromosome segregation. Here they show that CKAP2 and its paralog CKAP2L also function at the cilium to regulate cilium formation and Hedgehog signaling.

Strengths:

A major strength of the manuscript is the use of GFP-CKAP2 knockin cells and the examination of single and double CKAP2 and CKAP2L knockout cells. The authors use live imaging of the knockin cells to show that CKAP2 localizes to the primary cilium of RPE1 cells after assembly.

The authors use the knockout cells to show that loss of either CKAP2 or CKAP2L results in longer cilia and a dampened Hedgehog response, whereas loss of both CKAP2 and CKAP2L results in shorter cilia and an even more dampened Hedgehog response.

Weaknesses:

The data are compelling and support the conclusions. However, the findings would be significantly strengthened by using additional markers of the cilium, not just acetylated tubulin.

Reviewer #1 (Public review):

This manuscript by Lin et al. was a pleasure to read, and the results were quite surprising. The first surprise was the strength of the effects of the [MRPL10+] yeast prion on Drosophila locomotory behavior and chill recovery. The second was that this effect is highly polymorphic in different Drosophila lines, allowing the authors to perform a GWAS and implicate a number of genes involved in gut-brain signaling, thereby establishing a clear mechanism for this effect. The third was that many of these GWAS hits were validated by RNAi, giving further support to their involvement. I only have a few minor questions.

(1) Does the evidence really "support a model in which [MRPL10+] yeast promotes cold tolerance by activating serotonin signaling while simultaneously suppressing octopaminergic signaling"? I agree about serotonin, but the role of octopamine seems less clear. Figure 3d shows that mutants for genes involved in octopamine synthesis (Tdh2) and a receptor (Octβ2R) have higher cold tolerance, irrespective of [MRPL10+]. So while this does establish a role for these two genes in cold tolerance, what is the evidence that [MRPL10+] suppresses octopaminergic signaling? These seem to be two different questions. In other words, maybe any mutant with increased cold tolerance would show no response to [MRPL10+], regardless of whether the mutated gene is involved in mediating [MRPL10+]'s effects.

(2) I was also somewhat confused by the results of Supplementary Figure 4. In S4a, inhibition of octopaminergic neurons (TDC2 > TNT) seems to decrease locomotory behavior in response to [MRPL10+], which is the opposite of what I would expect from the cold tolerance experiments in Figure 3d. And then in the S4c legend, it is stated that "Loss of the octopamine biosynthesis gene Tdc2 or its receptors Octβ2R and Octβ3R triggers elevated locomotor activity even in flies fed wild-type yeast, mimicking the [MRPL10+] phenotype." I can see this for the two receptors, where both the red and black lines show high locomotor activity (>1000 passes) near the middle of each 24-hour experiment, but the Tdc2 graph in S4c looks quite different, with the [MRPL10+] activity never going above ~200 passes at any time point and the wt activity showing high variability. So if I understand the data correctly, it seems that Tdc2 mutants have higher cold tolerance (Figure 3d) but not higher locomotory behavior (Figure S4c).

(3) To summarize, I don't see how the data in either Figure 3d or Supplementary Figure 4 support a role of octopamine in the [MRPL10+] mechanism. Even in cases where perturbing a gene/neuron type abolishes the effects of [MRPL10+] on locomotory behavior or cold tolerance, this establishes a role for them in locomotory behavior or cold tolerance, but not for mediating [MRPL10+]'s effects (for the same reason given in #1 above). In contrast, the 5-HT2A results in Figure 3d do establish mechanistic relevance for serotonin, since the mutant affects only the response to [MRPL10+], but not wt.

(4) Finally, I am intrigued by the idea at the end of the paper that this represents a symbiotic adaptation. Have [MRPL10+] yeast ever been found in the wild? If not, perhaps its effects on flies are unlikely to represent anything adaptive? And if the prion is present in the wild, I wonder: if it's to a fly's advantage to have higher cold tolerance or locomotory behavior, why couldn't it evolve that itself, without needing a prion to induce it? Given the incredible adaptability of flies, I would guess that any physiological effects of a yeast prion would more likely push a fly away from its fitness optimum, and only benefit the yeast-- for example, by increasing yeast dispersal at the cost of a fly's fecundity. The main exception to that would be if [MRPL10+] yeast were only present in some specific environments that the flies couldn't adapt to on their own, but that seems unlikely.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors report on how a prion protein originating in yeast inside the gut interacts with a host insect's physiology to influence organismal traits important to fitness. Other recent studies have strongly found that interactions between gut yeasts and their Drosophila hosts are important to feeding behaviour, growth performance, and cold tolerance. They even point to the gut-brain axis. The authors extended from this work, combining screening approaches, genome-wide association studies, and forward genetics to determine that octopamine and serotonin signalling are important to these effects.

Strengths:

The data represent a valuable addition to the literature. There is a growing appreciation that host-microbiome interactions are important to animal performance and fitness, and this work provides strong evidence for a causal role of a prion protein in such a relationship. The high-throughput screening approaches and sequencing were, to the best of my knowledge, completed correctly. The idea that prion proteins could influence host physiology in beneficial ways is compelling, and the authors have done a great job of walking the reader through their reasoning and the multiple lines of evidence that support their reasoning.

Weaknesses:

While this is an interesting topic that is worthy of investigation, and identifying a causal role for a prion protein in host effects is a significant advance, other aspects of the novelty of the work are strongly overstated. No clear justification is provided for why cold tolerance was a particular trait of interest in the present study. Yet, a recent publication in the Journal of Experimental Biology clearly demonstrated a role of gut yeasts in Drosophila cold tolerance and is not cited or otherwise acknowledged [see: Jiménez-Padilla and Sinclair. Gut yeasts accelerate chill coma recovery in Drosophila melanogaster. J Exp Biol (2026) 229 (9): jeb251533]. I trust this is an oversight and will be corrected. Integrating this knowledge into the narrative of the paper would strongly improve the reasoning for this study.

The authors rely on a review of chill coma mechanisms from 2011 as their primary source of information for interpreting their results in relation to insect cold tolerance. A great deal of work has been done by several research groups on the physiology of cold tolerance in chill-susceptible insects in the past 15 years, much of which has relied on Drosophila as a model system. I think this is important and could inform the conclusions being reached and future work that extends from this work. For example, it is now well established that the renal system is centrally important to insect cold tolerance, including chill coma recovery phenotypes, but this is not being acknowledged or integrated into the narrative here and should be. Many of the mechanisms of interest highlighted in the present work are also directly relevant to other ionoregulatory epithelia beyond nervous tissue, and global knockdowns using the UAS/Gal4 approach will impact all tissues in which these genes are expressed. Figure 2D shows how these genes are enriched in the CNS, but also the midgut and Malpighian tubules, two ionoregulatory organs of import to cold tolerance.

The method the authors used to assess cold tolerance is not typically preferred by researchers who commonly study these phenotypes. Holding flies continuously at 4-6{degree sign}C and assessing whether or not they remain active is a reasonable approach, and I am confident that the differences observed among groups are real. However, chill coma onset and recovery are thought to be mediated by a complex combination of temperature effects on nervous, muscle, and renal function, and this assay method may conflate chill coma resistance with the capacity for chill coma recovery. This means variation in this assay could arise from differences in initial CTmin, plasticity in CTmin induced by RCH before chill coma is induced, or plasticity in neurumuscular/renal function that allows for recovery during the assay. I say this in part because Drosophila are documented to enter chill coma and then recover while the assay is ongoing, particularly around temperatures close to the CTmin [see: MacMillan et al., The capacity to maintain ion and water homeostasis underlies interspecific variation in Drosophila cold tolerance. Sci. Rep. 5:18607]. Therefore, flies active after 2 hours may never have entered chill coma, or may have entered and then recovered. Serotonin and octopamine signalling may be critical to one or both of these possibilities, and maybe in different ways, especially because these hormones play critically important roles in both renal and nervous function.

Infectious prions are known to cross gut epithelia and the Drosophila gut is known to take up large organic molecules via endocytosis and exocytosis, so I am not entirely convinced that the effects observed necessarily result through the gut-brain axis. Future studies could be focused on observing whether these prion proteins remain in the gut, or act directly on other tissues via the hemolymph.

The CAFÉ assay used in the study is a tried and true way to measure feeding behaviour in Drosophila. The data in Figure 1H look like a single measurement per individual, unless they have been modified for presentation. From the text provided, it is not clear to me how the authors accounted for changes in feeding behaviour at different times of day. Feeding behaviour is regulated by the circadian rhythm in digestive tissues. If activity is enhanced at night, as in the present study, are MRPL10+ flies also feeding during the night more than the WT flies?

Reviewer #3 (Public review):

Summary:

This manuscript shows how a change in food source can lead to organismal adaptation to stress. Namely, different yeast strains impact the response of Drosophila to cold stress. An intriguing connection between food intake, gut, and neuronal signaling is described.

Strengths:

The genetic association studies suggest how pathways can be altered to provide cold tolerance in Drosophila.

Weaknesses:

[MRPL10+] is described here as a yeast prion, yet there is no solid evidence supporting this. It is unclear whether the prion exists; therefore, the primary conclusion is unclear. More biochemical analyses and additional characterization are needed to support the idea that MRPL10 is, in fact, in a prion state in the strains the authors received and utilized in this manuscript. It is unclear whether the mating scheme to produce daughter cells without the prion would actually work as described, and no follow-up work verifies the lack of the prion state. In addition, more common prions were omitted from the study, and it is unclear whether they might be present in the strains used as well. There is no [PSI+], [RNQ+], or [URE3] strain assessed, and it is possible that there is another prion in the [MRPL10+] strain.

Reviewer #1 (Public review):

Summary:

This manuscript calculates a measure of fitness flux for influenza and SARS-CoV-2 viruses, normalising by a generation time go generate comparable measures of viral adaptation over time. Potential correlates with gain in fitness flux, such as the number of mutations in different regions of the virus, are evaluated in terms of their correlation with the measured gain. A count of mutations in the S1 subunit of Spike performs slightly better in explaining observed fitness changes than previous deep-learning models describing SARS-CoV-2 evolution.

Strengths:

I enjoyed reading this manuscript. I liked the characterisation of fitness effects in a way that makes influenza and SARS-CoV-2 directly comparable. This is a neat new result.

I thought the retrospective regression against numbers of variants was a simple and interesting analysis. There is some precedent for examining correlates of fitness in key viral sites, for example in Bush et al., 1999 and Luksza and Lassig 2014: This carried on a useful tradition.

This paper is clearly written and well-constructed. The figures are well produced. There is an absence of hype in presenting results in a simple and straightforward manner.

After posing the question, I came to the conclusion that the comparison between S1 mutations and EVEscape was a fair one. The question here is that the details of the relationship between S1 mutations and fitness is derived in retrospect, from a large quantity of data, whereas PLM-based scores are advertised as having utility on the basis of only a single genome sequence. However, comparison was made with a fine-tuned model, which in some ways levels the playing field. Maybe further discussion could have been added around this point?

Weaknesses:

(1) I wasn't clear about whether the comparison with Fisher's fundamental theorem was a useful check on the analysis, or simply an inevitable consequence of any estimate of fitness scores. The fitness of a strain is measured in relative terms, as the difference in a fitness score relative to the mean of that score for the whole population. More rapid adaptation occurs when the relative difference to the mean is large, which may necessarily correlate with an increased overall variance in the fitness of strains.

(2) I would have valued more discussion on the potential implications of the findings of this manuscript. Two questions I was left with:

a) Thinking about application to a potential future emergent pathogen, to what extent is prior knowledge being leveraged in these methods? While a comparison is made of fitness gain versus statistics of multiple genes, in one sense we 'know' that the more accessible parts of the viral glycoprotein are going to be of higher relevance for viral fitness and evolution, simply from an understanding of the necessary geometry of antibody-viral interactions. Similar knowledge is leveraged in the Luksza and Lassig 2014 study: Characterising fitness by a number of epitope substitutions in that case rests on biological knowledge of which are the important epitope sites. The EVE family of methods use a similar approach where factors such as residue accessibility are combined with outputs from protein language models. But does this work have implications for how we evaluate emerging variants of existing viruses, notably SARS-CoV-2 or influenza? The H3N2/K substrain of influenza makes me want to ask this question: In that case a large number of non-synonymous changes in HA was not accompanied by a noticeable increase in the severity of seasonal influenza.

(b) What is the implication of this work for the use of PLM-based models for understanding virus evolution? One analysis that was not done is evaluating the performance of combined models, encompassing both mutation counts and PLM data. Models such as EVEscape already utilise multiple metrics alongside PLMs. Do PLMs contribute addition knowledge to a 'number of mutations on the outside of the glycoprotein' count?

Reviewer #2 (Public review):

Summary:

The author uses multinomial logistic regression to assign fitness values to SARS-CoV-2 and Influenza H3N2 clades. The mean population fitness, referred to as the cumulative fitness flux, is tracked throughout evolution to describe the rate of adaptation. The author shows a clear decrease in the rate of adaptation for SARS-CoV-2 after mid 2022, coinciding with the emergence of the Omicron clades; the rate of adaptation of H3N2 is much slower, but inferred to be constant in time. With this analysis, the author confirms Fisher's fundamental theorem of natural selection. Using a fine-grained clade definition scheme, the author attributes changes in fitness to substitutions in different genomic regions, highlighting the importance of the spike and, in particular, the RBD region of spike. A fitness model based on a multinomial regression is shown to perform better than EvEscape and protein-language-model semanticity to predict changes in fitness.

Strengths:

The author provides an interactive reading experience on the github.io hosted website, which has additional interactivity with figures and offers simple manipulation of what is shown. The methods are well explained and are easy to follow. The conclusions of the study- the decrease in the rate of adaptation of SARS-CoV-2, mutations in Spike S1 as the main driver of evolution, and the Spike S1 mutational count as predictor of fitness change - are clear to follow.

Weaknesses:

(1) The main conclusions that (i) the rate of adaptation of SARS-CoV-2 has decreased after Jun 2022 and is lower than in Influenza H3N2 and (ii) that mutations in Spike S1 are the main drivers of evolution are not novel.

(2) At the core, the multinomial logistic regression assumes a time-independent fitness value for each viral clade, while the clade fitness is not constant and depends on the population immunity, which will change over time. As a result, the fitness increase can be wrongly interpreted: The author observes a doubling of the mean fitness every 6 months from Jan 2021 to Jun 2022, and every 2.4 years from July 2022 to Dec 2025. We would then expect that the mean fitness in Dec 2025, \bar{f}_t, has increased more than 2 to the power 4, as compared to the mean fitness in Jan 2021, \bar{f}_0 (\bar{f}_t > 2^{4} \bar{f}_0). Is the mean viral fitness in Dec 2025 more than 16 times higher than in Jan 2021? Fitness differences between viral populations at different times cannot be meaningfully compared because the fitness landscape is time-dependent. The increase in fitness, without accounting for the change in population immunity, is in part an artifact of the multinomial regression.

(3) The multinomial regression treats the fitness landscape on which the virus evolves as static. However the fitness landscape is actually time-dependent, as population immunity changes. For a static fitness landscape, the cumulative fitness flux is the mean population fitness. However, for a dynamic fitness landscape, this is no longer the case: the (mean population) fitness changes both because of adaptation, and because changes of changes in the fitness landscape, i.e., an increase in population immunity will decrease fitness non-uniformly, also affecting individual selection coefficients s_i(t). This leads to cases where the cumulative fitness flux between t_0 and t_n can be positive, but the fitness remains the same. This study neglects the time-dependence of the fitness landscape and therefore incorrectly calculate the fitness flux, leading to an overestimation of the rate of adaptation.

Reviewer #3 (Public review):

Summary:

Bedford considers how the fitness of SARS-CoV-2 and influenza H3N2 variants have changed over time. The fitness of viral variants are estimated from trajectories of variant frequencies using multinomial logistic regression (MLR). The MLR approach was previously developed and is well-validated. Changes in mean population fitness (i.e. fitness flux) is then derived from changes in the fitness of circulating variants through time.

Strengths:

The manuscript makes some noteworthy observations. For one, it is reassuring to know that fitness variation well predicts the rate of fitness change in viral populations, as expected under Fisher's fundamental theorem. Similarly, it is interesting that simple counts of mutations perform as well as much more sophisticated protein language models in predicting variant fitness.

Weaknesses:

My two main concerns both relate to the interpretation of fitness flux and how confident we should be that it is quantifying changes in absolute fitness as opposed to environmentally-dependent changes in fitness through time.

(1) Interpretation of fitness flux:

I'm not entirely convinced that mean population fitness can be meaningfully compared through time, at least not as a measure of fitness change on an absolute scale. Here, mean population fitness is defined as the weighted sum of the relative fitness of each variant, so changes in mean pop fitness necessarily reflect changes in relative fitness. To obtain a fitness value of each variant that is comparable across time, a "scaffolding approach" is used to estimate window-specific effect and the global fitness (f_i) of each variant. The major assumption here is that by accounting for the window-specific effects, the global fitness of each variant becomes directly comparable. This assumption seems somewhat suspect. It seems impossible to know whether the window-specific effect is capturing the full environmentally-dependent component of fitness in a given window. There could also be a high degree of temporal autocorrelation in window-specific effects between neighboring windows due to similarities in environment that would decay over time.

To put this in another way, say we directly competed a 2020 SARS-CoV-2 variant with a 2025 variant in the distant future after all host-immunity to these strains had waned. Would we really be confident in estimating the fitness advantage of the 2025 variant over the 2020 variant? Or would this estimates of relative strain fitness still reflect the environments in which they were measured in, including the NPIs that were in effect in 2020 and the complex immune structure of the host population in 2025?

(2) Inability to separate different components of fitness:

Earlier work, like Meijers et al. for SARS-Cov-2 (Cell, 2023), decomposed overall changes in fitness into different components of fitness such as changes in intrinsic fitness (transmission potential) and immune escape. While the current model is simpler, in some ways this earlier work was more elegant and more powerful in its ability to explain what components of fitness drove the overall change in population-level fitness.

Reviewer #1 (Public review):

Summary:

The authors examine the role of retinoic acid signaling in the formation of lengthened outer segments in UV cones in a localized region within the ventral temporal zebrafish retina. The authors demonstrate that the formation of this region of increased sensitivity depends on the degradation of retinoic acid by Cyp26, which is expressed in MG. Inhibiting Cyp26 or stimulating RA expression reduces OS length and visual sensitivity.

Strengths:

A key strength is the use of several experimental strategies to support conclusions. For example, the authors localize key enzymes in Müller glia (MG) and, in a separate experiment, to highlight the overall importance of MG, they ablate them. High acuity zones are critical visual specializations, and understanding their formation is important for vision research, retinal disease, and regenerative medicine. The manuscript also addresses a fundamental question in neuroscience: What are the specific signaling mechanisms that occur between neurons and glia during development?

Weaknesses:

The primary weakness is the use of inhibitors, which have systemic effects. This caveat has been appropriately addressed in the discussion.

Reviewer #2 (Public review):

Summary:

This manuscript by Lahne et al. connects retinoic acid (RA) signaling regulation to the length of outer segments (OS) in UV-sensitive cone photoreceptors located in a specialized region of the zebrafish retina called the high acuity zone (AZ). The authors provide potentially compelling, but as it stands, incomplete, evidence that the Müller glia (possibly through expression of the Cyp26 RA-degrading enzyme) may act to regulate spatially restricted RA availability to UV cones in the AZ, supporting these UV cones to grow longer OS. While the evidence presented is indeed suggestive, it is not directly linked and is insufficient to support the full conclusions presented.

Strengths:

(1) The experiments make outstanding use of the strengths offered by the zebrafish model, including excellent reporter lines for RA signaling and Müller glia visualization, fluorescent in situ hybridization, high resolution fluorescent microscopy, and pharmacological manipulations; tools which are all well selected and utilized.

(2) The pharmacological manipulations allow temporally controlled modulation of RA signaling and Cyp26 enzyme activity at developmental timepoints of interest.

(3) Manipulation of RA signaling impacts cone OS lengths.

(4) The Müller glia express mRNA transcripts encoding the RA-degrading enzyme Cyp26 and respond to RA signaling modulation in a manner consistent with a role in regulating RA signaling.

(5) The use of DAPT to prevent Müller glia differentiation in the retina is used to attempt to implicate the Muller glia in the regulation of RA signaling and UV cone OS length.

Weaknesses:

(1) The experiments cannot rule out a role for other cell types in driving the outcomes studied (UV cone OS length). The expression of Cyp26 transcripts by the Müller glia does not specifically align with the high acuity zone, and other cell types show signal for these transcripts. Impacts on RA signaling, as well as Cyp26 expression can be detected in regions potentially implicating cell types other than the Müller glia. One region of Cyp26 transcript signal is consistent with the Retinal Pigment Epithelium (RPE), and cells in this same region also show RA signaling changes in response to pharmacological treatments.

(2) The analysis following pharmacological manipulations lacks quantification of UV cone numbers and their morphology after the treatments, which could indicate broader impacts on cones that may manifest in their outer segments.

(3) The cell-type assignment of RARE:GFP-positive ONL cells is central to the proposed non-cell-autonomous mechanism, yet representative colocalization images supporting the quantification are not fully shown.

(4) The SyGCaMP6f activity reporter experiments are a nice addition, but the results are not necessarily directly connected to OS length or to the Müller glia.

(5) The experiments using DAPT to prevent Muller glia development are not sufficiently executed to support the conclusions presented, and their efficacy in inhibiting Müller glia development, as well as UV-cone-specific impacts, are not demonstrated. These treatments could have broad impacts on photoreceptor maturation, retinal organization, or trophic support.

(6) The title refers to glial regulation of "local retinoic acid levels." However, the study measures: A synthetic RARE reporter, RA-responsive genes and pharmacological responses.

Reviewer #3 (Public review):

Summary:

The manuscript titled "Glia regulate local retinoic acid levels to specify neuronal specialisation for high-acuity vision" by Lahne et al. examines the interaction of cellular and signaling mechanisms involved in neuronal specialization. While there have been rapid increases in the discovery and cataloguing of different cell types based on transcriptional signatures that can be uncovered by single-cell approaches, there is much less known about how variations in cell morphology within a cell type are governed. The highly stereotypical specializations in photoreceptor morphology found in high acuity zones of various species are an excellent example. This study implicates retinoic acid signaling as a functional driver of these photoreceptor specializations in addition to its previously described role in establishing the spatial positioning of high acuity zones within the neural tissue. Furthermore, evidence is presented that retinoic acid does not directly signal through photoreceptors, but instead this signal is received by Müller glia to non-cell-autonomously affect the photoreceptors. Overall, this study identifies a potential mechanism that integrates the broad patterning role of retinoic acid with its local effects on specializations within a cell type and suggests that glial cells are integral to this mechanism.

Strengths:

The major strengths of this study are the well-executed experiments and clearly communicated results. The application of pharmacological agents is useful for precise timing of target inhibition and to prevent effects on other retinoic acid-mediated processes.

Weaknesses:

There are two issues with the study that weaken the conclusions that are drawn. The first is that the primary evidence that Mueller glia are the cells receiving the retinoic acid signal is that the RARE reporter is active in these cells. However, it should be considered whether this reporter is capable of responding to all retinoic acid signaling. Is it possible that the construct's binding site sequences and/or their configuration will limit the ability to detect other receptor complexes that respond to retinoic acid? For example, will complexes that contain RorBeta or RxrGamma (two established retinoic acid receptors) in complex with thyroid receptors be able to activate this reporter? If that is the case, then it could be that the Mueller glia are shaping the retinoic acid availability in the local environment of cones through their expression of the Cyp26 genes, but the cones as well as the Müller glia are directly responding to the retinoic acid signaling. If there are methods to test this, such as directly activating/repressing retinoic acid signaling in cones or MG with some cell type specificity, that would greatly strengthen the argument that it is a non-cell autonomous effect. One experiment that does argue in favor of this is that the loss of MG leads to a small outer segment, but this is where the second issue should be considered. The study uses three methods (including genetic loss of MG) that block the acuity zone-specific elongation of the photoreceptors, but one concern is that the shortening of these outer segments is a non-specific effect. In all three of the treatments (Figures 3, 5, 9), the segments look somewhat disorganized and not simply like a conversion of the Acuity zone outer segments to the Dorsal state. It would be powerful to complement these approaches with a retinoic acid-related manipulation that does the opposite - that converts Dorsal outer segments into a longer Acuity zone-like morphology. That would be strong support for the proposed hypothesis.

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

(1) I am pleased that the authors revised their section on external calcium They now approach this issue by calculating the effect of low external calcium on plasticity. These calculations are based on studies of numerous types of synapses, which are unlikely to be directly comparable to hippocampal synapses. They focus on PPR rather than the overall response during more sustained activation that is likely to produce more complex responses. Obviously, it would have been preferable to simply measure the responses in the appropriate external calcium.

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

Reviewer #3 (Public review):

Summary:

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

Strengths:

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

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

Weaknesses:

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

Reviewer #2 (Public review):

This study investigates STX, a non-steroidal, CNS-selective estrogenic compound known for its neuroprotective effects in stroke and Alzheimer's disease models. The authors successfully identify VDAC proteins, specifically VDAC1, VDAC2, and VDAC3, as the direct mitochondrial targets of STX. To characterize this interaction, the researchers employ a comprehensive approach combining chemoproteomics, single-cell qPCR, planar lipid membrane electrophysiology, and Seahorse metabolic flux analyses. The manuscript frames the physiological characterization of the STX-VDAC mechanism within POMC neurons, which serve as a metabolically sensitive and estrogen-responsive system, while appropriately positioning its specific role in neurodegeneration as a direction for future research.

A major strength of this study is its innovative methodology, particularly the development of a novel bifunctional STX probe (BF-STX) featuring a photo-crosslinkable diazirine group and an alkyne handle to capture transient STX-protein interactions in living cells. The experimental design is rigorous, incorporating essential controls such as no-UV negative controls and competition assays with excess unlabeled STX. These controls provide convincing evidence that the identified VDAC interactions are genuine rather than nonspecific artifacts. Furthermore, the authors establish a solid physiological rationale for utilizing POMC neurons to investigate these estrogen-sensitive mitochondrial mechanisms. The mechanistic claims are well supported across multiple complementary platforms, offering a clear view of how STX affects VDAC channel properties and mitochondrial bioenergetics. The authors also demonstrate scientific rigor by properly scoping their conclusions and recognizing all three VDAC isoforms as candidate targets without overstating the exclusivity of any single isoform.

The manuscript thoughtfully addresses the current boundaries of the study within the Discussion section. The authors transparently acknowledge their reliance on immortalized cell lines, correctly identifying the need for primary neurons or whole-animal models in future studies to fully establish the physiological significance of these findings. The study also notes that defining the exact structural binding site of STX and performing targeted loss-of-function experiments, such as neuron-specific VDAC manipulation, remain necessary next steps. Finally, the authors address the non-linear dose-response observed at higher STX concentrations by offering a logical, multi-target hypothesis to explain the complex data.

Reviewer #1 (Public review):

Summary:

This study investigates a fundamental question in cognitive science: is our ability to reason about the physical world an abstract mental process, or is it "embodied"-directly rooted in our real-time physical interactions with the environment? The authors compared participants' performance in computerized reasoning games with and without Galvanic Vestibular Stimulation (GVS). They suggest that participants failed more often and utilized suboptimal strategies under GVS compared to a sham stimulation condition. Furthermore, they suggest that this detrimental effect of GVS was reduced when the games were governed by altered gravity (hyper- and hypo-gravity). Consequently, the authors conclude that the physical experience of the body modifies high-level cognitive skills, such as reasoning.

Strengths:

The manuscript is well-written, organized, and easy to follow. Also, combining a specialized physical reasoning task with real-time vestibular disruption (GVS) is an intriguing approach to testing the boundaries of embodied cognition.

Weaknesses:

The empirical evidence supporting the conclusions, as currently stated in the Abstract, remains weak. The overall effect of GVS is limited, and the conclusions regarding its impact on strategy use rely on sophisticated clustering and classification methods whose reliability and validity are not clearly demonstrated in the current manuscript. The differences between Studies 1 and 2, which are critical to establishing the effect of altered gravity, are also not robust overall.

Reviewer #2 (Public review):

Summary

The paper investigates whether the real-time physical experience of the body shapes high-level physical reasoning. Participants played a set of computerized tool-use reasoning games (the Virtual Tools paradigm) in which they must use knowledge of physical laws - including gravity, collisions, and inertia - to guide a ball into a target area. In Study 1, participants played the games under terrestrial gravity while receiving either Galvanic Vestibular Stimulation (GVS), which introduces noise into the vestibular organ and disrupts gravitational signalling, or a Sham condition with matched skin sensation. In Study 2, a separate cohort played the same games redesigned under hypogravity (0.5 g - half Earth g) or hypergravity (2 g - double Earth g), again with concurrent GVS or Sham stimulation. Performance was assessed through success rate, number of attempts, and time per attempt; strategy was assessed through the spatial distance between successive tool placements and the frequency of tool switching across attempts. A post-hoc gravity-weighted index (GWI) was computed to compare the effect of vestibular perturbation across the two studies. The main finding is that GVS impairs performance in gravity-dependent games under terrestrial gravity, yet the same perturbation appears to be neutral or even beneficial when the game environment involves non-terrestrial gravity - a result the authors interpret as evidence for an adaptable, body-grounded internal model of physics.

Strengths

One of the most notable strengths of this work is its conceptual positioning at the intersection of embodied cognition and physical reasoning. Rather than treating the human body either as an abstract information-processing device or as a purely biomechanical system, the authors take seriously the idea that cognition is scaffolded by ongoing sensorimotor state - and they test this idea with a paradigm that is both tractable and theoretically motivated. The use of the Virtual Tools paradigm is well-suited to this goal: the games vary systematically in their reliance on gravitational predictions, allowing selective impairment (rather than general disruption) to serve as a signature of embodied physical reasoning.

The dual-study design is another strength. Testing the same vestibular perturbation under terrestrial and altered game-gravity conditions and observing a reversal in its effect depending on context, provides a form of internal control that is conceptually compelling. The additional clustering analyses (Dirichlet Process Gaussian Mixture Model and leave-one-out kernel density classification) strengthen the strategy results beyond raw distance measures, confirming that GVS systematically shifts participants' spatial exploration strategies.

The paper is also clearly written and engages meaningfully with relevant theoretical frameworks - predictive coding, embodied cognition, and stochastic resonance - making it accessible and stimulating for a broad audience.

Weaknesses

(1) Absence of multiple-comparisons correction. A large number of game-level pairwise t-tests are conducted in both studies (upward of twenty per study) without correction for familywise error rate. The game-level effects that anchor the main narrative - in Study 1 alone: Remove, GoalMove, Spiky, Falling_A, Shafts_B, Gap, and Chaining - arise from an uncorrected pool of comparisons. The probability that some of these constitute false positives is non-trivial. The authors should apply a correction (e.g., Benjamini-Hochberg) or at minimum discuss this limitation explicitly.

(2) The facilitation claim rests on a post-hoc and arbitrarily parameterized index. The gravity-weighted index (GWI), which drives the central cross-study comparison uses integer coefficients (1, 2, 3) to weight games by gravity dependency level. These coefficients are entirely arbitrary and bear no principled relationship to the actual gravitational magnitudes used in the study. Why not use the gravity dependency ratings themselves, or the empirically estimated gravity impact scores from the computational modelling mentioned in the Methods? The choice of weights should be either principled or tested across a range of values to demonstrate robustness. Furthermore, the notation in equation (1) as currently typeset reads as "Gravity minus Weighted Index" rather than "Gravity-Weighted Index"; this should be corrected.

(3) The "facilitation" interpretation exceeds what the data in Study 2 directly support. Across all games in Study 2, GVS versus Sham differences in absolute performance are non-significant in all directions. The facilitation claim derives entirely from the GWI being higher in Study 2 than in Study 1 - a between-subjects comparison involving different participant groups and a non-pre-registered metric. The language of "facilitation" should be tempered accordingly, or the authors should provide additional analyses to support this framing.

(4) Gravitational manipulation is visual only, and the vestibular system is only one component of the gravity-sensing network. Gravity perception results, as the authors very well know, from a distributed multisensory integration process that involves, in addition to the vestibular system, visual, proprioceptive, and visceral inputs. The present paradigm manipulates gravitational context solely through visual cues and targets the vestibular system through GVS - a point the authors acknowledge but do not discuss in sufficient depth. It is important to distinguish clearly between real gravitational alterations (as achieved in parabolic flight or centrifuge environments, where the entire body is physically subjected to a different gravitational vector) and virtually altered gravity, where only one sensory modality is targeted while others remain anchored to 1 g. The scope of the conclusions should reflect this distinction.

(5) The choice of 0.5 g and 2 g may lack sensitivity. Combining the two altered-gravity conditions in Study 2 because no significant effect of hypo versus hypergravity was found is statistically pragmatic but conceptually unsatisfying. There is evidence in the space physiology literature that gravitational processing is not linearly symmetric around 1 g: threshold effects exist below and above terrestrial gravity that may not be captured by modest deviations (half and double g) - see refs below. It is worth discussing whether the absence of a hypo/hyper distinction in Study 2 reflects a genuine equivalence or a lack of sensitivity, and whether more extreme conditions (e.g., near-zero g or 4-5 g) might reveal different processing regimes. Whether 0.5 g and 2 g were sufficient to saturate the system or merely insufficient to perturb it remains an open question with direct implications for the interpretation of the null GWI effects on strategy measures.

Lee SMC, Ribeiro LC, Martin DS, Zwart SR, Feiveson AH, Laurie SS, Macias BR, Crucian BE, Krieger S, Weber D, Grune T, Platts SH, Smith SM, and Stenger MB. Arterial structure and function during and after long-duration spaceflight. J Appl Physiol (1985) 129: 108-123, 2020.

de Winkel KN, Clément G, Groen EL, and Werkhoven PJ. The perception of verticality in lunar and Martian gravity conditions. Neurosci Lett 529: 7-11, 2012.

Clément G, Moore ST, Raphan T, and Cohen B. Perception of tilt (somatogravic illusion) in response to sustained linear acceleration during spaceflight. Exp Brain Res 138: 410-418, 2001.

Benson AJ, Kass JR, and Vogel H. European vestibular experiments on the Spacelab-1 mission: 4. Thresholds of perception of whole-body linear oscillation. Exp Brain Res 64: 264-271, 1986.

(6) High-level reasoning is not defined with sufficient precision. The term "high-level reasoning" appears from the title onward and in the heading of the Study 1 results section (line 138), but it is never formally defined. The reader needs a clearer account of what distinguishes high-level physical reasoning from low-level sensorimotor prediction, and where the games used here fall along that continuum. What specific physical competencies - ballistic trajectories, free-fall predictions, collision dynamics, frictional forces, inertial effects - are required across the game set? When describing the subset of games that drive key effects, this information is critical for evaluating whether effects are specific to gravity reasoning or to some other physical concept.

(7) Performance measures are disconnected from underlying kinematics. The performance measures (success rate, number of attempts, time per attempt) are coarse, high-level summaries. Time per attempt is used as a proxy for performance efficiency, yet participants received no instructions regarding speed, and different individuals may have adopted systematically different speed-accuracy trade-offs. It would be valuable to know whether time per attempt correlates with attempt number within a given game (which would indicate within-game learning) and whether mouse movement data - trajectory, velocity, hesitation - were recorded and could be analysed to provide more mechanistic insight into strategy formation.

Comments on revised version.

My overall assessment remains positive. I consider the findings important and the evidence solid. The study uses an original experimental approach to address a theoretically significant question, and I consider the data sufficient to support the more constrained conclusion that ongoing vestibular information can influence physical reasoning in a context-dependent manner.

I agree with the other reviewers that the game-level multiple comparisons require appropriate statistical treatment and that the Gravity-Weighted Index should not carry more inferential weight than justified by its construction. I also agree that some of the broader mechanistic interpretations should be presented cautiously. These issues concern primarily the strength and scope of interpretation rather than the validity of the experimental findings themselves.

I do not, however, consider the absence of preregistration of the exploratory analyses to constitute a methodological weakness in itself. Preregistration is desirable when analyses are intended to provide confirmatory evidence, but it is not a prerequisite for a scientifically informative exploratory analysis. The important distinction is that exploratory analyses should be transparently identified as such and their conclusions should be appropriately qualified. In my view, the relevant concern here is therefore the inferential weight placed on these analyses, rather than the fact that they were not preregistered.

I would consequently retain a rating of solid for the strength of evidence rather than incomplete. The main claims are supported provided they are formulated at an appropriate level of specificity; the evidence is less secure for the broader mechanistic claims concerning general recalibration of internal models of gravity.

Reviewer #3 (Public review):

Summary

This manuscript investigates whether high-level physical reasoning is influenced by ongoing vestibular and bodily signals rather than operating as a fully abstract process. The authors combine Galvanic Vestibular Stimulation (GVS) with the Virtual Tools task to test the effects of vestibular perturbation during reasoning under terrestrial gravity in Study 1 and visually simulated altered gravity in Study 2. The experimental approach is original and provides a potentially useful bridge between research on vestibular processing, physical cognition, and embodied reasoning.

The revised manuscript is substantially improved. The authors have responded carefully to many of the methodological concerns raised in the previous review. In particular, they have removed the original arbitrarily weighted Gravity-Weighted Index, introduced mixed-effects models that account for participant-level and game-level variability, clarified the basis of the gravity-impact classification, and more clearly distinguished preregistered from exploratory analyses. The interpretation of the strategy measures and the treatment of the 0.5g and 2g conditions have also been improved. These revisions provide a substantially stronger and more transparent analytical framework for evaluating the hypotheses.

Strengths

The principal strength of the study is its conceptual and methodological originality. Combining vestibular stimulation with a relatively high-level physical problem-solving task provides an innovative approach to testing whether ongoing bodily information is associated with physical reasoning. The comparison of games that differ in their dependence on gravity is also potentially informative for distinguishing general effects of vestibular perturbation from effects more specifically associated with gravity-relevant reasoning.

The revised analyses represent another important strength. The mixed-effects models provide a more principled basis for inference than reliance on individual game-level comparisons alone, while the revised Gravity Index removes the arbitrary weighting used in the original manuscript. The clearer treatment of exploratory analyses also makes it easier to distinguish the primary evidence from complementary observations. Overall, the revision has addressed many of the methodological concerns raised previously and has made the empirical pattern considerably easier to evaluate.

Weaknesses

The main remaining concern is the correspondence between the strength of the empirical evidence and the strength of the manuscript's central claims.

In Study 1, the aggregate measures provide little evidence for an overall effect of GVS on performance or strategy. More importantly for the proposed gravity-specific account, the newly introduced mixed-effects analyses do not show significant stimulation-by-gravity-impact interactions for the principal performance or strategy measures. Some gravity-level-specific and game-level effects are present, including a difference in placement distance for high-gravity-impact games, and the exploratory spatial analyses provide additional evidence that vestibular perturbation may influence aspects of strategy. These findings are potentially informative, but the overall pattern is selective rather than a consistent and convergent demonstration that greater dependence on gravity systematically increases the detrimental effect of GVS.

The evidence in Study 2 is more limited. Aggregate differences between GVS and Sham are small across the main performance and strategy measures, and the mixed-effects analyses do not identify reliable stimulation effects across the low-, medium-, or high-gravity-impact categories. Study 2 therefore does not directly demonstrate that GVS facilitates physical reasoning under altered gravity.

The cross-study Gravity Index analyses provide some evidence that the effects may differ across gravitational contexts, but the pattern remains heterogeneous. For success rate, the high-gravity-impact contrast is in the predicted direction but remains a directional trend, with the credible interval including the point of equivalence. Other performance measures do not provide convergent support for the same pattern. The distance index shows reliable cross-study contrasts at some gravity-impact levels, but these form a crossover pattern rather than a simple reduction of the GVS effect as gravity dependence increases. The principal study-by-gravity-impact interactions are also not robust. In addition, this Gravity Index analysis was not preregistered and compares two separate participant samples. Taken together, these findings are more consistent with suggestive evidence for a context-dependent influence of vestibular perturbation than with a definitive demonstration of facilitation or rapid adaptation under altered gravity.

A second concern is the mechanistic interpretation. The experiment directly measures behavioral performance and strategy under GVS and Sham conditions. It does not directly measure the strength of a terrestrial gravity prior, prediction errors, sensory reweighting, internal-model updating, or stochastic resonance. Predictive coding and related frameworks provide plausible interpretations of the findings, but the present behavioral data cannot distinguish among these mechanisms. Statements that GVS downregulates a terrestrial gravity prior, accelerates revision of an internal model, recalibrates cognitive expectations, or provides a vestibular "teaching signal" therefore imply a level of mechanistic specificity that is not directly established by the current experiments.

Overall, the study remains innovative and potentially valuable, and the revision has substantially strengthened the analytical framework. The empirical results support a more circumscribed conclusion that vestibular perturbation can influence selected aspects of physical reasoning and strategy, with suggestive evidence that these effects may vary across gravitational contexts. The evidence is less conclusive for the broader claims that real-time embodied experience generally determines high-level physical reasoning or that vestibular perturbation facilitates rapid adaptation through specific mechanisms of gravity-prior updating.

Reviewer #1 (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:

In the manuscript by Winke et al, the authors present evidence that fear-induced analgesia is mediated by somatostatin projection cells from the vlPAG to the RVM. This study uses a mouse model of fear-induced analgesia, and incorporates optogenetic circuit manipulation with behaviour and electrophysiology to gain a meaningful insight into a novel circuit involved in fear-induced analgesia.

Strengths:

(1) This is a well-constructed study with appropriate controls and analyses.

(2) Alternative interpretations of the data are systematically considered and eliminated via rational experiments. The authors are commended for a nice piece of experimental work.

(3) The vlPAG is a known region of pain modulation, and this study adds valuable insight to the circuit involved in fear-associated analgesia.

Weaknesses:

Only male mice are included in this study. [This has been explained and noted as a limitation.]

Reviewer #2 (Public review):

Summary:

Wenke et al. investigated the role of vlPAG somatostatin-expressing neurons in the mediation of analgesia during defensive states. A newly developed paradigm of cued fear-conditioned analgesia, which consists of a combination of an auditory fear retrieval session and a pain test, was used to evaluate this cell population's contribution to fear-mediated analgesia. Optogenetic manipulation of vlPAG SST+ neurons modulated the responses to a nociceptive cue (Hot Plate) presented concomitantly with an aversively conditioned tone. At the same time, alterations in the freezing levels could be observed during optogenetic activation of vlPAG SST+ neurons. In order to disentangle the impact of these cells on analgesia from their impact on the expression of defensive behaviors, the authors performed electrophysiological recordings from the dorsal horn in the spinal cord of anesthetized mice. A vlPAG-RVM-DH pathway was identified to trigger nociceptive C-fibers upon optic activation of the RVM. Finally, pathway-specific activation of SST+ vlPAG-RVM neurons could abolish CS-induced analgesia.

Strengths:

The study addresses a relevant topic, that is, brainstem circuits for pain-modulatory mechanisms as part of defensive states evoked by threat. This is important because the circuit mechanisms underlying pain are still not fully understood, and defining molecular markers of cellular circuit substrates may support the identification of potential pharmaceutical targets in treating pain. The authors confirm a previous study in that a somatostatin-positive cellular population presents a crucial vlPAG circuit element mediating anti-nociceptive effects. Key novelty aspects of the present study are the demonstration that these neurons seem to play a role specifically in threat-induced analgesia. This was possible by the elegant design and application of a novel fear analgesia paradigm, combined with cell- and pathway-specific optogenetics.

Reviewer #3 (Public review):

Summary:

Conditioned analgesia refers to the ability of a learned fear cue to suppress pain-related behavior and neural activity. Understudied, the authors developed a novel conditioned analgesia procedure in which a cue that had been paired or unpaired with shock was played while a hot plate increased temperature. Compared to several control conditions, the authors found increased latency to a nociceptive response (paw licking). The authors identified somatostatin neurons in the periaqueductal gray as a likely mediator of the behavior. They then showed that: (1) stimulating vlPAG-SST neurons blocked nociceptive response latency increases to the CS+, (2) stimulating vlPAG-SST neurons suppressed fear retrieval freezing, (3) stimulating vs. inhibiting vlPAG-SST neurons drove opposing modulation of c-fibers and Aδ-fibers, (4) direct-projecting vlPAG SST neurons modulate freezing while RVM-projecting vlPAG SST neurons modulate conditioned analgesia.

Strengths:

These experiments have many strengths. The behavioral assay is chief among them. The assay is robust and controls for confounding factors to reveal a repeatable effect of a shock-paired cue to delay nociceptive responding. The optogenetic experiments provide the correct level of temporal precision, given the authors' time-specific interest in cued responding. Combining neuronal manipulations with spinal recordings is particularly innovative, especially in the context of more behavioral neuroscience-based assays. All-in-all, I found this to be an exceptionally strong set of experiments.

Weaknesses:

No obvious weaknesses were identified by this reviewer.

Reviewer #1 (Public review):

Summary:

Zhang et al. report on an ambitious study that investigates multiple aspects of the neural and behavioral underpinnings of auditory-motor surprisal in the context of an auditory-motor learning paradigm (piano keyboard). Using an intricate design comprising several sub-parts and control procedures, they report that early ERPs (50-100 ms latency) reflect violations of established key-pitch mappings.

Strengths:

The paradigm is quite intricate and at the same time addresses multiple aspects of auditory-motor learning and does so in an experimentally rigorous way.

Weaknesses:

In its current form, the analyses of the ERP data remain a weak point.

Reviewer #1 (Public review):

This study demonstrates sexual selection on spatial cognition via extra-pair paternity in socially monogamous, non-migratory mountain chickadees (Poecile gambeli). Males rely on spatial memory to recover food caches, with abilities linked to survival, longevity, and heritability. In a wild population, authors quantified extra-pair young (EPY) and compared the cognition of extra-pair sires to cuckolded social males using feeder-array assays. Better-performing males sired more EPY and heavier offspring in their nests; extra-pair sires significantly outperformed social males. Results support the good-genes hypothesis: females gain indirect genetic benefits via EPY from cognitively superior mates.

Reviewer #2 (Public review):

Summary:

In this study, the authors ask whether spatial cognition is under sexual selection in mountain chickadees. To do so, the authors examined a large dataset that includes a) spatial cognition data for both males and females (obtained via use of a clever RFID-based feeder system) and b) social and extra-pair paternity nesting data. As predicted, males with higher spatial cognition sired more extra-pair offspring, and extra-pair sires had, on average, higher spatial cognition scores than the males they cuckolded. Interestingly, females with lower spatial cognition scores were more likely to seek extra-pair copulations, potentially to compensate for their own low spatial cognition. Surprisingly, there was no difference in spatial cognition scores between males that sired their own offspring and those that lost paternity at the nest. Also surprising was the fact that there were no differences in patterns of extra-pair paternity and spatial cognition between high- and low-elevation sites. The latter is particularly surprising in that spatial cognition should be under stronger selection at the high elevation site. Overall, this is a fascinating study that demonstrates that spatial cognition - a trait under natural selection as it directly impacts winter foraging and survival behaviour -is also under sexual selection.

Strengths:

The authors have a robust dataset (n = 732 offspring sampled over 3 years), high-quality spatial cognition data collected with a procedure that has been well-honed over the years, and couple the data with solid statistical procedures that address many potential covariates and potentially confounding factors. In addition, the authors are careful in the discussion to elaborate on the many potential alternative explanations from the results and questions that are likely to arise in the minds of readers (e.g., how are females assessing male spatial ability?)

Reviewer #3 (Public review):

Summary:

The authors presented evidence that spatial cognition in this population is under sexual selection, with extra-pair males, primarily chosen by the females, having better spatial cognition than males they cuckolded and males with better spatial cognition having more extra-pair young.

Strengths:

This cognitive ecology study was conducted on a well-known long-term study population of free-ranging mountain chickadees. This strong base, alongside a thorough study design and extensive statistical analyses, enabled the authors to address research questions that few other labs can address, making this a potentially powerful study of broad general interest.

Reviewer #1 (Public review):

Summary:

This study investigates how temporal and spatial discrepancies between an action and its visual feedback are combined when people judge whether an observed movement corresponds to their own action. Using a virtual-reality reaching task and computational modeling, the authors show that both temporal and spatial discrepancies reduce self-attribution and that a Multiplicative model better explains judgments than the prespecified Minimum and Mean alternatives. Importantly, the main model comparison was confirmed in a preregistered replication.

Strengths:

The study addresses an important question about how multiple sources of sensorimotor information contribute to the sense of agency. The factorial manipulation of temporal and spatial discrepancies provides a clear experimental approach to this question, and the distinction between an exploratory study and a preregistered replication is a major strength. The behavioral effects were consistent across the two samples, and the replication provides confirmatory support for the advantage of the Multiplicative model among the prespecified candidate models.

Weaknesses:

The main limitation concerns the strength of the theoretical conclusions drawn from the model comparison. Although the Multiplicative model outperformed the prespecified Minimum and Mean models, this does not uniquely establish multiplication as the underlying computational operation, because other nonlinear integration rules were not tested. The evidence therefore more directly supports cross-domain integration than a specifically multiplicative computation.

Similarly, the behavioral results do not by themselves establish that this integration occurs within a domain-general representation of agency. The binary judgment used in the task is also closely related to judging whether the seen and performed movements match, leaving open whether the observed integration reflects agency computation itself or a later decision process. These considerations do not undermine the main empirical findings, but they suggest that the broader computational and representational claims should be stated more cautiously.

Reviewer #2 (Public review):

Summary:

Harduf et al. investigated the mechanisms underlying the sense of agency (SoA), the feeling of being in control of our actions. SoA is thought to arise from the comparison of action outcome predictions, emerging from forward models, with the actually observed outcomes. Current literature has not elucidated how cues from different forward models predicting different features of actions are combined to form a final agency judgement. The authors investigate this gap by introducing various combinations of spatial and temporal mismatches during a virtual reality (VR) based reaching task, and recording participants' agency judgements. Then, they fit different models of cue combination to behavioural data and compare them. The authors find compelling evidence that a model in which the effects of spatial and temporal incongruence are multiplied provides the best fit, outperforming models that do not combine spatial and temporal incongruences, and one model that combines them by averaging rather than multiplying. The authors argue that sense of agency emerges from the domain-general integration of different forward models.

Strengths:

The experiments are well designed, and model validation is compelling thanks to the comparison with an appropriate set of alternative models and replication of the results in a first exploratory cohort and in a pre-registered validation cohort. The writing is generally very clear, and the presentation of the results is exhaustive yet compact, making the paper very readable. I also commend the authors for empirically addressing whether and how the integration of different cues contribute to the sense of agency, an idea which has been more widely proposed conceptually than empirically investigated.

Weaknesses:

(1) The terminology is not always clearly defined, and the authors are not sufficiently rigorous in specifying what gap their study aims to address exactly, and to what extent it succeeds. The authors acknowledge that the idea that cue combination underlies sense of agency was already proposed, yet frame their contribution as showing that "integration" underlies sense of agency. However, it is unclear what the authors exactly mean by "integration". Also, it is not well specified what a domain-general representation is exactly, and how such a notion is not already included in the previously proposed cue combination theory. Overall, the authors seem to imply the main contribution of the paper is to elucidate both whether and how cue integration is performed. However, the most novel contribution of the study appears to concern the "how" rather than the "whether".

(2) The authors should have discussed their findings in light of Bayesian inference, which has already been proposed as the basis of cue combination for sense of agency. The fact that a multiplication of the different cues fits the data better than an averaging makes it too tempting to think about Bayesian inference to ignore such idea. Indeed, if cues are assumed to provide statistically independent evidence about the probability of self-causation, then they should combine in a multiplicative way rather than by averaging. Even if the experimental design or pre-registration constraints preclude a formal Bayesian analysis, this point should be discussed and related to previous literature.

Reviewer #1 (Public review):

This work uses a compelling pairing of controlled task design with rich, naturalistic behavior. It is ambitious, with eight experiments, both correlative and causal demonstrations, delayed assessments, and generalization of the phenomena to a very different domain.

The stated goal of the paper is to understand how learning different curricula "promote successful learning of complex tasks in human adults," which is a very broad scope. The evidence for generalization to a non-spatial task is compelling, but the structure of the two tasks is isomorphic, and it is still difficult to claim likely generalization to all complex tasks. For example, one could wonder to what extent demands of the task or online setting may have explicitly or implicitly encouraged participants to prefer trials that can be completed more quickly, biasing them towards choosing discovery transitions. Is it possible that they believed that the experiment might end more quickly if they chose trials that were faster to complete?

Reviewer #2 (Public review):

Summary:

This paper investigates how curricula should be structured to support learning in complex tasks, focusing on the distinction between concept discovery (learning new components) and concept implementation (learning how to use them in increasingly complex sequences). The main finding is that participants tend to prioritize discovering new concepts, even though learning outcomes are better when they instead practice implementing known concepts in increasingly complex ways.

Strengths:

A major strength of the paper is the experimental paradigm. The grid-world task is a novel way of independently manipulating two dimensions of complexity that are often confounded: the number of concepts that need to be learned and the complexity with which those concepts must be deployed. Participants have to learn how the underlying tools operate and use them in different configurations, which provides an interesting setting for studying variability in how individuals structure their own learning. Additionally, the experiments progress from correlational analyses of self-directed learning, to randomized experimental comparisons of curricula, and finally to transfer and adaptive curriculum tests. Overall, this paper addresses an important question about whether the complexity of concept discovery versus implementation is better for structuring learning.

Weaknesses:

The main concern is that the paper's conclusions do not seem to fully match the evidence. The authors present the results as identifying a relatively general principle of complex learning, such that we should master a concept's implementation before introducing new concepts. There was no implementation-first advantage in the transfer phase, and when testing was delayed by one week, the curriculum difference was no longer detectable. Although the implementation-first curriculum improves immediate performance within the constraints of these experimental paradigms, it is less clear that it produces more generalizable learning. Additionally, it is not sufficiently clear how the "flow" measure was created, what "flow" means in the context of subjective task experience, or more broadly in everyday learning, and what inferential role the measure plays in the paper.

Reviewer #3 (Public review):

Summary:

The authors report findings from a set of experiments that compare learning outcomes from two broad classes of training regimens. The first, concept discovery, emphasizes the identification of task components. The second, concept implementation, emphasizes the procedural deployment of task components. Learners tend to self-schedule the former, but task performance and performance on an immediate test are supported by the latter.

Strengths:

The authors address a novel research question with clear application value. The experiments that are reported in the manuscript are effectively designed to answer the research questions of interest. However, as I will expound on below, the authors ultimately misinterpret their findings.

Weaknesses:

This manuscript makes no mention of the distinction between learning and performance (e.g., Schmidt & Bjork, 1992; Soderstrom & Bjork, 2015). It is well-known in the human learning literature that valid tests of learning are ones that entail a separation of context from an initial acquisition phase. This separation may be temporal (i.e., a delayed test) or feature-based (i.e., a test of transfer on novel iterations of a task). In any case, contextual differentiation between test and acquisition is critical to provide an accurate assessment of learning. To the authors' credit, they do report results from both a delayed test and tests of transfer. However, they do not appropriately interpret the results of those tests, which demonstrate no impact of training schedule on learning. They instead rely on findings from immediate tests to support their claims that graduated concept implementation supports learning. In truth, concept implementation is neither preferred by learners nor beneficial to learning. These findings are accordingly quite limited in terms of generating insights for effective training conditions.

Compounding my primary concern above, I will note that the authors report fitting Bayesian multilevel models (MLMs) to their data, yet rely extensively on analyses of participant means (e.g., permutation t-tests) when a proper MLM would suffice, and in fact would be more appropriate. Bayesian MLMs are an incredibly flexible and robust analytic tool (e.g., Fiechter, 2024), and I would have liked to have seen a more comprehensive approach in this manuscript.

Reviewer #1 (Public review):

Summary:

The authors aim to characterize how executive function (EF) subdomains (shifting/learning, inhibitory control, working memory maintenance, and working memory updating) are organized in NHPs. They train six macaques on four touchscreen tasks per session and derive a battery of behavioral metrics. They use reliability screening, correlation analyses, unsupervised clustering, and latent factor models to argue for separable EF factors and consistent cross-session cognitive phenotypes.

Strengths:

(1) Clear behavioral effects within tasks.

(2) Battery approach with repeated sampling.

(3) Scalable.

Weaknesses:

(1) Fixed task order may be a confound for between-task correlations. Curious about the potential impact of motivational changes, reward satiety, fatigue, etc., especially if later tasks have lower accuracy or higher variance?

(2) The claim about the common EF factor is limited with only 6 animals.

(3) The claim about phenotypes and clustering is limited as one cluster is a single animal (subject F).

(4) Framing of the AS task as such is inappropriate, as it is a manual response task and is not interchangeable with classic oculomotor AS paradigms.

The authors demonstrate with solid evidence that a multi-task battery can yield repeatable performance metrics across multiple EF-relevant tasks in macaques. The data support the idea that multiple separable dimensions can summarize performance in this cohort and that individuals differ consistently across sessions. However, the claims about the three cognitive phenotypes, four-factor EF architecture, and lack of common EF factor in NHPs are only partially supported given the fixed task order, small sample size, and ambiguity about whether factors reflect stable traits or covariance between sessions. These claims would be strengthened if the authors analyze effects of the fixed task order and time since session start.

Reviewer #2 (Public review):

Summary:

The authors set out to characterize how four studied components of executive function (Inhibitory Control, Shifting, Updating, and Working Memory) are organized in rhesus monkeys, using a battery of four touchscreen tasks performed repeatedly across many sessions. They report that individual monkeys fall into distinct "cognitive phenotypes," and that statistical modeling of the task scores reveals four separable latent factors, which they interpret as evidence against a single shared "general" executive function factor in this species. The four latent factors (Shifting/Learning, Exogenous Inhibitory Control, Endogenous Inhibitory Control, and Working Memory Updating) are slightly different from those mentioned in the introduction, which is of interest to refine the definition and assessment of executive functions in non-human primates.

Strengths:

(1) The multi-task, repeated-measures design is a substantial undertaking and yields a large, richly characterized behavioral dataset from the same animals across many sessions. The use of 4 different cognitive tasks is uncommon in this field and a real asset to the study.

(2) The overall approach of testing the reliability of each behavioral measure before including it in further analysis is a sound and appreciated practice, backed up with overall appropriate data analysis strategies.

(3) The attempt to move beyond single-task designs, which dominate the non-human primate literature, toward a broader profiling of executive sub-functions is conceptually valuable and timely.

Weaknesses:

(1) The four factors introduced early in the paper are not the same four factors that emerge from the final statistical analysis, and this shift is not clearly flagged or explained to the reader, which is likely to cause confusion about what the paper is actually demonstrating. In addition, working memory vs. updating are not clearly defined or distinguished. The introduction and discussion sometimes treat "updating" and "working memory" as separate executive functions, but the literature the authors themselves cite (e.g., Friedman & Miyake, 2017) treats updating as a component nested within working memory rather than a fully independent dimension. This conceptual ambiguity carries through the paper and affects how the reported four-factor structure should be interpreted.

(2) The grouping of very different types of behavioral measures (accuracy-based executive function metrics, reaction-time/processing-speed metrics, and reward/loss motivational-effect metrics) under a single "cognitive metric" label in Figure 2 is potentially misleading, since these are not conceptually equivalent, and the paper later treats them separately in supplementary analyses. This could give readers the impression that all reported metrics are equally informative tests of the four-domain hypothesis, when only a subset actually is.

(3) The rationale for how motivational & valence effects (gains/losses) were analyzed is not well supported. Effects of loss versus gain may reflect risk attitudes or loss-aversion documented in the primate literature, rather than motivation per se, and this alternative explanation is not discussed.

(4) The Discussion would benefit from acknowledging other factors that could influence performance and phenotype membership across sessions (such as age, sex, social rank, or stress) and from clarifying whether the identified cognitive phenotypes are expected to be stable traits or could shift with further training. Additionally, some interpretive statements appear in the Results section rather than the Discussion, which is inconsistent with how results and interpretation are normally separated, and could give undue weight to preliminary interpretations.

(5) Concerns about the reliability of some response-time-based measures. In the Continuous Updating task, reaction times appear to drop unexpectedly at the highest difficulty levels for each animal, which may reflect animals disengaging from the task (e.g., random choice heuristic) rather than a genuine cognitive effect, and could also reflect thinner, unevenly sampled data at these levels rather than a true average. If so, the slope measures derived from these data may need to be recalculated after appropriately filtering the trials. Related to this, individual differences in hand-resting position in front of the screen are acknowledged by the authors as a source of noise in reaction times across tasks, but no correction or normalization for this is applied.

(6) The Supplementary Methods referenced in the text (e.g., for the variance decomposition and additional factor analyses) do not appear to be included anywhere in the submitted materials, only Supplementary Results, making some analyses difficult to fully evaluate. There is no information about the subject age, sex, species, etc.

Achievement of aims and impact:

The authors largely achieve their stated aim of demonstrating that monkeys' executive function performance is reliable and structured in different dimensions rather than guided by a single factor, and the discovery of stable individual "cognitive phenotypes" across sessions is a genuinely interesting and useful contribution. However, the conceptual framework of the study needs to be better clarified (i.e. are working memory and updating truly separable?) and enriched with relevant inputs from the fields of comparative cognition and cognitive ethology in non-human primates and beyond. The conclusions about Response Times (RT) may change after proper or further analysis of these metrics; additional relevant dimensions may then be disentangled by considering the sources of variability in these RT data (i.e., motivation, emotional state). With clarification of these points, this work has the potential to become a useful reference and methodological resource for the field of comparative cognition and non-human primate cognitive neuroscience.

Reviewer #1 (Public review):

Summary:

This study has a very well-posed question and interesting proposed finding. It proposes that because LC activity has been shown to correlate with arousal, perhaps its activity is related to mobilizing resources for cognition and action. They use chemogenetics to inactivate LC neurons while monkeys perform a foraging task with homogeneous reward options and a working memory component. They use two task conditions, one where the grid of reward wells is visible and one where they are opaque, and the monkey has to open them to retrieve the food inside and remember where he has been. The authors claim that inactivation of LC had a selective effect on the opaque well task by increasing the number of revisits to the same wells without affecting total rewards, response times, or overall motivation, which they interpreted as reduced efficiency rather than disengagement. This is a particularly appealing outcome because it implies that LC suppression, which should lower arousal, does not cause disengagement, and rather affects working memory in some fashion. However, there are many issues with this study that make the abstract misleading, in a concerning way. The abstract and introduction are written well, but the data do not support the overall claims, and there are fundamental flaws that aren't easily resolvable.

Strengths:

The bigger question is very interesting and has broad appeal. The writing of the abstract and introduction sets the paper up clearly.

Weaknesses:

(1) The title and abstract claim effort; the paper repeatedly discusses working memory. It does not appear that any metric of effort was measured or manipulated in this study (no pupillometry, no effort-cost model, no offered choice between effort levels).

(2) The authors cite their previous paper as strong evidence of chemogenetic manipulation of LC neurons. They use that paper to justify the dose they use of DCZ, the activator of the chemogenetic construct. That study recorded only 5 neurons at that dose, and 3 of them had a reduction in rate. The statistical significance of that result is questionable (given that I think the authors averaged % change across 3 neurons and it was 15%). The authors treat that as a robust result in multiple places, for example:

"...induced a reliable 15% decrease in the firing of LC neurons..." The only significance test reported in the source paper for that data is t(5.8) = -3.6, p = 0.01, and that test compares low-dose against high-dose neurons. It establishes dose-dependence. It does not establish that 0.1 mg/kg produced a reliable decrease in firing.

"...the dose of DCZ was chosen based on its known influence on LC activity in monkey Jf, i.e. a 15% decrease in firing lasting over 30 minutes...".

This is misleading to readers with regard to the effectiveness of chemogenetics in LC and for creating a foundation for this paper.

(3) The authors seem to undermine their main argument that the opaque task requires working memory at all, and I am not convinced the monkeys were not just operating like a random agent. The random agent model seems to sample uniformly with replacement and an arbitrary termination rule, which is a straw man argument for a model. It does not allow for testing memoryless vs. memory. A monkey executing a systematic scan with short, coherent moves will avoid revisits without using working memory at all. The correct control is an agent matched to the animal's own movement statistics (step-length and turn-coherence distributions) with no memory of visited wells and with memory of visited wells. There's currently no evidence that the monkeys are using working memory in the opaque well task.

(4) The models used are not described sufficiently for interpretation or replication. The methods are brief, and the models seem pulled out of thin air with no reference to other work in foraging or any mathematical construct. If the authors have used these models before, then they should cite them, but the statements "...performance of a random agent is harder to evaluate intuitively...", "random agents have no reason to stop generating actions...", "...the number of trials was set arbitrarily...", and the qualitative comparison of performance "was intermediate between that of the optimal and average random agent..." raised concern as to whether the models were principled at all. The distance model was strange, although fine, but why not use geometry? It is also not clear why a reach would have this kind of spatial relationship when the monkey eats food between visiting locations and does not go from one box to the other without a reach to his mouth and a reach back to the board in between.

(5) The figures in this paper need work; axes are not labeled properly, or have labels that are undefined. Legends are not labeled clearly or described properly in the figure legends to interpret the figures. In multiple cases, the box and whisker plots have too little data, and the edges of the boxes collapse on themselves because IQR doesn't make sense for only 6-7 data points.

(6) The statistics seem questionable; although they used parametric and non-parametric tests, they report results of tests that assume normality for small sample sizes <10. Other choices regarding the trial number to stop counting data (e.g., on the 20th or 23rd) are suspicious and seem arbitrary, not data-driven. Some choices regarding analysis are stated in the text as arbitrary when they could be derived from hypotheses or rigor. The extremely small p-values for the ANOVA result testing performance made me suspect that this was combining all trials across sessions (given there were only 6 or 7 sessions per animal) and there was no repeated measures or nesting to account for repeated sampling within an animal. Sessions within an animal under matched conditions are the natural paired unit. So a paired or mixed-model treatment would be both more powerful and more appropriate.

(7) Lastly, there is no evidence that chemogenetics actually worked in this experiment in a way that tests their hypothesis. In Figure 7, they show their only effects that passed statistical significance (p=0.03 and p=0.028) for two monkeys, comparing across saline (D) and DCZ (D) sessions, and show a small effect on mean performance. I don't think there were corrections for multiple tests across all their monkeys and performances. But that aside, the monkeys' performances were not different from those of their random agents on mean performance, as shown in Figure 5(A). So if they are performing randomly, what would inactivation be affecting?

(8) There seems to be an ordering confound of weeks 1 and 2 being saline and weeks 3 and 4 being entirely DCZ, and only the last 2 weeks are randomized, so for 20 of the 28 sessions per animal, treatment is confounded with time.

(9) There does not appear to be any group x treatment interaction test for any analyses. Claims rest on statements like "significant in monkey 1 but not in monkey 3," etc.

(10) There are duplicated statistics between pages: "The effect reached significance for monkey Jf (T-tests, Jf: t(10.79) = -2.31, p = 0.042), but only approached significance for monkey Js (t(8.89) = 2.04, p = 0.072)." on page 12, "The number of trials performed after the 23rd reward increased under DCZ for monkey Js (T-test, t(10.79)=-2.31, p=0.042) and Jf only showed a non-significant trend (T-test, t(8.89)=-2.04, p=0.072)." on page 13 for a separate section.

Reviewer #2 (Public review):

Summary:

The authors investigate the causal role of the LC in mobilizing cognitive resources. Two rhesus macaques expressing TH-dependent inhibitory (hM4Di) DREADDs in the LC, alongside one non-transduced control, performed a spatial foraging task under visible (transparent) and hidden (opaque) reward conditions. The authors report that systemic DCZ (0.1 mg/kg) administration selectively impaired performance in the memory-guided opaque condition in the DREADD animals, concluding that LC activity is causally required for allocating cognitive effort

Strengths:

(1) Achieving cell-type-specific, reversible chemogenetic inhibition in the macaque LC is a substantial technical achievement that successfully bypasses the limitations of systemic noradrenergic pharmacology.

(2) The experimental setup elegantly isolates memory-guided action selection from global arousal, sedation, or motivational deficits, providing a useful quantitative constraint for LC functional models.

(3) The introduction and discussion clearly identify the limitations of using indirect pupillometry to assess locus coeruleus activity. The authors thoughtfully frame their targeted manipulation as a critical complement to existing literature without overstating their claims.

(4) Demonstrating that the DREADD animals navigated the board similarly regardless of reward visibility is a valuable null finding. This specific result provides crucial evidence for addressing the memory-versus-effort debate. Elevating this insight from a subordinate clause to a more prominent position will further maximize the paper's impact.

Weaknesses:

(1) The current behavioral metrics-specifically mean inter-choice distance and success rates bounded by a "random agent" baseline-cannot distinguish between a working memory deficit and a fundamental shift in search strategy. Because performance is a many-to-one function of memory quality and search policy, animals could achieve the observed outcomes either by executing a tight local sweep with "leaky" memory for visited wells, or by abandoning tight spatial locality for a dispersed, near-random walk with intact memory. Without a detailed characterization of the animals' actual step-by-step visit sequences and spatial consistency across conditions, the data cannot adjudicate whether LC inhibition degrades an existing habitual policy (a memory/maintenance deficit) or impairs the adoption of a structured policy (an effort-mobilization/task-set deficit). Clarifying this is critical, as the two interpretations engage distinctly different LC-prefrontal mechanisms.

(2) The analyses of within-session behaviors rely on arbitrary reward-inclusion thresholds (e.g., 20 or 23 rewards) and censoring rules that obscure the temporal dynamics of the task. Because wells are depleted without replacement, the difficulty and working memory burden rise steeply as the board empties. A constant, time-invariant memory deficit could readily produce the observed early vs. late performance pattern, as the detectable cost of forgetting accrues heavily after the 20th reward. Furthermore, early-session failures to maintain an effective policy naturally lead to continued responding after depletion. However, the imposed time caps compress variance exactly where this within-session causal chain would be most evident, leaving the claimed independence of the early and late deficits unsupported.

(3) The experimental timeline heavily confounds chemogenetic manipulation with elapsed time. Test weeks 1-2 were exclusively saline, and weeks 3-4 were exclusively DCZ, with treatment alternation only occurring in weeks 5-6. Consequently, the critical contrast between opaque saline and DCZ conditions is largely a between-block comparison across a month of testing. Plausible time-varying factors-such as habituation, declining novelty of a daily home-cage task, and accumulating satiety-all directionally align with the reported DCZ impairment, undermining the isolation of the chemogenetic effect.

Reviewer #1 (Public review):

Summary:

Drp1 promotes mitochondrial fission, whereas viral sensing can trigger mitochondrial fusion, promoting MAVS aggregation and the type I interferon response. In this manuscript, Fang et al. describe an unexpected role of caspases induced upon Rift Valley fever virus (RVFV) infection in inactivating Drp1. They show that multiple caspases cleave Drp1 in virus-infected cells and propose that this cleavage boosts mitochondrial elongation and type I interferon signaling. Finally, the authors establish the generalisability of the proposed mechanism in the context of cellular infections with H1N1, SeV, and HSV-1. Caspase-dependent and caspase-independent cell death are important components of host defense against viruses. This work suggests an additional antiviral role for caspases through the mitochondrial type I interferon axis. Although the authors have addressed most of the reviewers' concerns in a rigorously revised manuscript, one aspect of the proposed mechanism requires further validation.

The data in Figures 6E and 6F remain difficult to reconcile with the study's central thesis. The authors propose that caspase-mediated cleavage of full-length Drp1 enhances the type I interferon response in virus-infected cells. To test this model, they overexpressed the caspase-resistant mutant Drp1-3DE. Yet RVFV infection reduced Drp1-WT and Drp1-3DE levels to a similar extent (Fig. 6E), while progeny virus yield was higher in cells overexpressing Drp1-3DE (Fig. 6F). This observation contradicts the notion that the abundance of Drp1 in virus-infected cells is primarily regulated by Caspases and also weakens the potential link between Caspases and viral propagation through Drp1. The authors' rebuttal that the transcription-inhibitory function of NSs may have contributed to the reduction of both Drp1-WT and Drp1-3DE is neither persuasive nor helpful in resolving the mechanistic discrepancy. Because this is a very significant point, clarity on this matter will be critical.

Reviewer #2 (Public review):

In the present study, the authors report the role of virus-induced apoptosis in positively regulating innate immune response. Upon infection, host cell apoptosis is triggered as a defense mechanism against virus replication. Culmination of infected-cell death impairs replicative potential for viruses hence attenuating virus propagation. Reports exist denoting inhibitory effect of apoptosis upon innate immune signaling. Contrary to that, findings of this manuscript underscore possible role of apoptosis in enhancing innate immune signaling and effector response. Infection-induced activation of caspases (3, 6, 7 and 8) has been demonstrated to cleave DRP1 protein. DRP1, acting as positive regulator for mitochondrial fission, upon degradation leads to altered mitochondrial morphology (elongation).

Mitochondria being a hub for innate immune signaling (via operation of RLR-MAVS-downstream effector molecule-axis), upon elongation as a result of DRP1 depletion results in greater innate immune signal flux and interferon induction. Increased interferon induction thus acts to inhibit virus propagation, as demonstrated by the authors using cell-culture models.

Strengths:

(1) The findings presented by the authors have been validated by employing elaborate biochemical experimental approaches. The study entails extensive biochemical characterization of DRP1 residues targeted by activated caspases, in vitro assays validating caspase-mediated DRP1 cleavage & caspase-DRP1 interaction.

(2) This study possesses broad implications since authors demonstrate role of caspase-mediated DRP1 cleavage in promoting innate immunity, in context of infection by diverse viruses (both RNA and DNA viruses).

Weakness:

Although the authors undertook a thorough experimental approach attempting to validate their findings, all the experiments were performed using either cell-culture models for infection or in vitro biochemical assays (cleavage and protein-protein interaction). Additional experimentation using animal models (in vivo) will further help strengthen biological significance of their findings under more physiological settings.

Comments on revised version.

I am satisfied with the revised version of the manuscript.

Reviewer #1 (Public review):

I thank the authors for a thorough revision. The correction to the QUEEN reporter sign convention resolves what was the central issue in my original review: with the reciprocal (1/488 nm) now plotted in Figure 5, the single-cell reporter data and the LC-MS/MS measurements in Figure 2 are internally consistent, and I appreciate the added metabolomics (Figure S2B) and transcriptomics (Figure S2A, S1-S3) that support reduced de novo purine biosynthesis as the source of the lower baseline ATP in NTT1 cells, as well as the quantified Hog1 phosphorylation data (Figure 4C, Figure S8). However, several points from my original review are not yet fully resolved, and I would like the authors to address them before I can recommend acceptance.

(1) A residual, uncorrected statement about QUEEN signal directionality. The Results section (subsection "Altered intracellular ATP level modulates lifespan") still states: "...only 488 nm excitation was used in these experiments, and the resulting QUEEN fluorescence signal is inversely correlated with intracellular ATP levels (Fig. 5A-C)." This directly contradicts the corrected Methods section ("...plotted the inverse of fluorescence measurements (1/488nm), as an indicator of ATP abundance, in Fig. 5, A-C") and the Figure 5 legend and color scale, both of which now correctly state that the plotted quantity increases with ATP abundance. Given that this exact ambiguity was the source of the original contradiction the reviewers raised, I ask the authors to correct this sentence and re-check the rest of the text for any other place where the old (pre-correction) sign convention may still be described.

(2) AMPK/Snf1 validation remains indirect. I had asked for AMPK-pathway controls alongside the Hog1 quantification. The revision addresses this only through transcriptomic inference - downregulation of Snf1 target genes (MIG1, HXK1, HXK2, HXT3; Figure S7) is used to argue for low Snf1 activity under high ATP. This is a reasonable correlative observation but is not a direct validation of Snf1/AMPK activity (e.g., Snf1 Thr210 phosphorylation status or a kinase activity assay), which is what I intended by "AMPK controls." Please either add a direct biochemical readout of Snf1 activation status analogous to the Hog1 blots or explicitly temper the claims about Snf1-mediated metabolic rewiring to reflect that they rest on transcriptomic inference alone.

(3) Bidirectional-transport hypothesis addressed indirectly, not experimentally. The new metabolomics (ATP/ADP/AMP all reduced in untreated NTT1 cells) and the coordinated downregulation of the purine biosynthesis pathway are a coherent case for "reduced synthesis" as the parsimonious explanation, and I appreciate this analysis. However, this remains a correlative/transcriptomic argument rather than the direct flux experiment I suggested was feasible (e.g., an isotope-labeled ATP efflux/uptake assay to directly test whether NTT1 exports as well as imports ATP). A contraction of the adenylate pool via reduced synthesis and a bidirectional transporter are not mutually exclusive, and the current data cannot fully distinguish them. I would ask the authors to either perform such a direct test or explicitly acknowledge this as a limitation and an alternative that current data do not rule out.

In summary, the revision has substantially improved the manuscript and resolved the central ATP-directionality contradiction, but points 1-3 above should be addressed, particularly point 1, since it re-introduces the same ambiguity, the revision was meant to eliminate, before I can consider my concerns fully resolved.

Reviewer #2 (Public review):

Summary:

This work presents interesting findings where addition of exogenous ATP extends replicative lifespan of yeast cells in a way that seems uncorrelated with actual increased intracellular ATP levels or mitochondria. To be clear, addition of ATP to yeast growth media increases the number of cell divisions per cell in yeast. Expression of the NTT1 ATP transporter gene increases intracellular ATP levels according to LCMS analysis, but the effect on replicative lifespan works without the NTT1 gene and without an intracellular increase in ATP (possibly with a decrease in intracellular ATP), so the effect appears to be independent of the effect on intracellular ATP levels or mitochondria, as mitochondria-less R0 yeast cells also have increased numbers of cell division when grown with extracellular ATP. I would not state that the data support a role for ATP availability regulating aging because human cells do not import ATP from the environment; maybe for yeast or microbes that import ATP unlike normal human cells that make all their own. I would not state that the data support a role for ATP in increasing replicative lifespan since there is no correlation between increased lifespan an increased ATP- rather the opposite is shown - you got no correlation between intracellular ATP at replicative lifespan. What you show is that you can increase replicative lifespan when you increase extracellular ATP in a way that doesn't matter if you further increase intracellular ATP with NTT1, but maybe you were saturated. But then, intracellular ATP doesn't correlate either. So, it doesn't make sense to say that the paper shows that increasing ATP increases replicative lifespan. You gave the cells what seems like an osmotic stress and it didn't even matter if they had the mitochondria to respond. Lifespan didn't correlate with more ATP at all. So, it seems incorrect to indicate that ATP regulates lifespan in yeast, when you haven't shown that it just wasn't osmotic stress and you have shown that it doesn't really have anything to do with how much ATP each cell has. Rather, it seems more like it's the robustness of some other response to the ATP and not how much they imported.

The authors point out in their rebuttal that, paraphrased, with the QUEEN reporter gene that quantifies ATP via ratiometric fluorescence, some cells increase atp with age, some cells decrease it and others show no age related changes, so it would not be meaningful to make an ATP measurement in old cells. Essentially, that line of reasoning further supports that, while adding extracellular atp seems to increase replicative lifespan, the lack of correlation between intracellular ATP and replicative aging suggest that they are eliciting a stress response to having high extracellular ATP. The increased replicative lifespan seems to be caused by some kind of stress response to the extracellular ATP, possibly osmotic. So, this is an interesting result that suggests that there are mechanisms to respond to high extracellular ATP that result in increased replicative lifespan that aren't caused by the ATP per say, but by having a high concentration of ATP, outside the cell. This paper seems like it might relate to the Kaeberlein paper about high osmolarity increasing replicative lifespan, but I don't know if this condition qualifies as high osmolarity.

As an aside, this seems like a better model for increased tumor cell growth in the presence of increased extracellular ATP, which happens in some cancers.

Strengths:

Longitudinal imaging of single cells. Analyzed ATP levels with two approaches. Creative approach to use NTT1 transporter to increase intracellular ATP levels (that did nothing for lifespan). Solid replicative lifespan data. Seemingly clear lack of correlation between ATP and replicative lifespan among individual cells strongly pointing so some kind of stress response, possibly some kind of osmolarity response like Kaeberlein 2002.

Weaknesses/inconclusive data:

The LCMS data seems better than the microscopy data on ATP because it does not suffer from signal interference/befuddlement from autofluorescence or pH or age-related changes in either of those parameters. The authors seem to have subtracted an average autofluorescence from each cell in their revised analysis, but it is unclear if this value changes with age to account for age related changes in autofluorescence; it is also unclear if signal attenuation as a function of age-related intracellular pH change was accounted for. They may have age-related values for autofluorescence or age-related changes in intracellular pH that affect fluorescence of GFP if they go back to their raw data, which might be useful for signal cleanup.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. All the reviewers' comments have been adequately addressed and taken into account.]

Objectives of the study and impact of the work

The authors of this article primarily aim to reconstruct the evolutionary history of the insect odorant receptor (OR) family, which is responsible for the detection of odorant signals by olfactory neurons. Due to the lack of phylogenetic signal present in the sequences of this multigene family, which evolves very rapidly, phylogenetic analyses have so far never made it possible to precisely retrace how ORs diversified prior to the appearance of present-day insect orders, and what the drivers of this diversification were. For example, one may suspect that the adaptation of ORs to odors emitted by plants constituted a critical step in insect evolution during the "angiosperm terrestrial revolution," which occurred at the end of the Cretaceous, but nothing currently allows this to be asserted.

There are very nice examples, notably in drosophilids, derived from comparisons between closely related species and documenting mechanisms of OR adaptation to certain signals. However, what the authors attempt to do in this work is to produce a macroevolutionary analysis at the scale of insects as a whole, based almost exclusively on bioinformatic analyses. To do this, they annotated OR genes in about one hundred insect species and developed pipelines for analyzing sequence similarity, structural similarity and functional similarity, the latter being estimated through a molecular docking approach. An important element in the evolution of insect ORs is the appearance of a unique co-receptor, called Orco, which appears to be an OR that has lost the ability to bind odorants. In addition to the large-scale bioinformatic analysis, the authors also aim to explore more specifically the factors that favored the emergence of Orco and the selective advantage conferred by the existence of OR-Orco complexes.

Given the importance of odorant receptors in insect biology and in their adaptation to different environments and lifestyles, retracing their evolutionary history is indeed a major question in evolutionary biology. In principle, this type of work therefore has the potential to become a reference in the field and to provide a basis for significant scientific advances.

Major strengths and weaknesses

The sampling chosen for collecting OR sequences is very impressive, with more than 100 insect families represented, covering most of the major orders. This sampling appears appropriate for the question being addressed. The analysis pipeline used to collect the sequences makes sense, relying on homology-based annotation tools coupled with a structure-based filter. Nevertheless, one can note aberrant numbers of ORs for certain species (much lower than reality). A lower number of OR genes is somewhat expected, as the authors chose to apply a fairly stringent filter on sequence quality (based on predicted 3D structure), which reduces the number from 14,000 to 9,000. This choice seems logical given the subsequent use of these data, but it inevitably leads to data loss. However, the low number of genes also results from the fact that the pipeline did not function correctly for all genomes.

In the revised version of the manuscript, the authors included a benchmarking step, which is a good point. They compared their OR gene annotations with previous reports in the same species. Unfortunately, this comparison is irrelevant because the chosen reference OR repertoires are actually a mix of transcriptome and genome annotations. Furthermore, comparisons with entire OR gene repertoires essentially demonstrate that their annotation was of good quality for species in which OR sequences were already present in the query OR database, but poor for species in which they were not. Therefore, these supplementary analyses made by the authors are not particularly in favor of an overall good quality of OR gene repertoires in the >110 species studied. The fact that some OR genes may be missing and that the total number may not be exact for each species is not prohibitive for studying the evolution of the family on a broad scale. However, it does call into question the correlation between the number of ORs and lifestyles and diets.

From the dataset collected, the authors attempted to categorize ORs in several ways, starting with the reconstruction of sequence similarity networks. The approach is interesting, but fails to reveal homology relationships between ORs from species belonging to different insect orders. So, it is unclear what the advantage of this approach is compared with the "classical" phylogenetic approach.

The clustering based on structure also leads to the identification of a majority of "order-specific" clusters, which does not provide major insights into the evolution of ORs. However, the authors highlight a group of ORs in flies that appear to possess an unusual intracellular region, as well as a cluster of OR shared across many insect orders that exhibit a larger binding cavity. This is really interesting, although more relevant to OR structure than to their evolution.

The analysis of structural diversity then leads the authors to focus on the Orco co-receptors, which are characterized by modifications of the binding pocket and the appearance of an extracellular loop that could explain the loss of the ability to bind odorant molecules. This part, which relies on in vitro experiments, is interesting and constitutes the most striking result of this study, which could in itself have been the subject of a separate manuscript.

The rest of the manuscript is based on the prediction of OR response spectra using molecular docking. The work that has been carried out is extremely substantial, and the objective of linking clusters based on sequence similarity or 3D structural similarity with functional categories is entirely relevant. The docking score threshold used was chosen thoughtfully, which is very good, and according to the calculation performed should ensure a true positive rate of more than 20%, which is excellent in such a docking analysis. But in the absence of functional validation, this 20% true positive rate is not sufficient to extrapolate OR function, and docking-derived binding breadth measures used in the remaining of the manuscript have to be taken with caution, as acknowledged by the authors themselves. Consequently, the chance that results of this part of the work will enlighten the evolution of OR on a broad scale is low. For example, the fact that insect lineages that emerged after the Permian-Triassic extinction have more broadly-tuned OR is an interesting observation, yet remains highly speculative.

In summary, despite the large number of analyses performed, the authors do not really succeed in achieving the stated objective of reconstructing the evolutionary history of insect ORs, and the results obtained do not strongly support all the conclusions regarding the links between OR repertoires and environment or lifestyle.

Reviewer #2 (Public review):

The remarkable evolvability of the olfactory system enables animals to rapidly adapt to dynamic and chemically complex environments. Over the past two decades, substantial effort has been devoted to uncovering the evolutionary principles that drive the diversification of odorant receptors (ORs), yielding key insights into the forces shaping their striking variability in both vertebrates and insects. In this manuscript, Zhang and colleagues analyze the OR repertoires of over 100 insect species, leveraging sequence and structural similarity to infer patterns of gene family evolution within this diverse and ecologically important clade. By integrating sequence-based and structure-based comparisons, their study builds on a compelling and recently emerging line of research made possible by the advent of AlphaFold, which has previously clarified the phylogenetic relationship between insect Ors and the gustatory receptor gene family and revealed the unexpectedly deep evolutionary origins of this ancient structural fold.

Applying this approach to a large set of ORs derived from species throughout the insect phylogeny, the authors confirm many previously reported patterns of OR evolution. More importantly, with their large-scale approach the authors found new structural features of different Or clades, resulting in intriguing testable hypotheses about Or evolution that have the potential to support future directions in studying this important gene family. For example, the authors identify a structural feature mostly unique to the OR co-receptor ORco, a beta-sheet in EL2, which they functionally show reduces odorant binding affinity - a key aspect of ORco, which does not bind ligands in the ancestral ligand-biding site. This is a particularly strong part of the manuscript, since the authors support their in silico-derived hypothesis with functional data.

In an attempt to assess the relationship between sequence identity and structure on one hand and function on the other, the authors perform an in-silico structure prediction and chemical docking analysis. While not suitable to assess the actual function of individual receptors without functional testing, this strategy revealed potential receptor clades with differences in the number and type of docked chemicals. As a response to the previous reviews, the authors now changed their writing to refer to these results as 'docking-derived function' instead of just 'function'. While I appreciate that the authors changed their wording, this semantic change still can be read as referring to docking-derived predictions as conclusions of actual biological function. However, this is not the case. Any functional claims based solely on the docking approach need to be interpreted with caution, as in silico-only approaches are currently not well enough predictors for actual receptor function. Accordingly, I strongly recommend to remove the parts that connect receptor function to structure or ecology.

Assessing their docking analyses with respect to species ecology, the authors identify correlations suggesting that Or repertoires might follow predictable evolutionary trajectories broadly aligned with species ecology. These are interesting hypotheses. However, due to the inability to predict actual receptor function the author's claims about ecology-function relationships are not well supported. Accordingly, the authors should change the respective parts of the manuscript in way that it is clear these are currently untested hypotheses. This includes adjusting the title, since the work does not find any experimental support for ecological tuning.

I believe that future studies combining functional testing with an explicit evo-eco framework could benefit from this work and the explicit hypotheses it generates. But the authors should be careful to not overstate their in-silico derived results.

Reviewer #1 (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:

The authors aim to understand, in the context of leaf shape, how the constraints imposed by development inform evolution. Leaf shape is a good place to study the influence of development on evolution because it is a trait that exhibits a lot of diversity, and the developmental mechanisms that give rise to leaf shapes are apparently rather conserved across angiosperms.

As part of the motivation for their work, the authors cite a previous study (Geeta et al), which found that in angiosperm phylogenies, transitions from complex to simple leaf shapes occur through evolution more often than transitions in the opposite direction. Is this due to developmental constraints or adaptation?

The authors undertake two parallel lines of work:

(1) Extending the study of Geeta et al with more data, consisting of both phylogenies and a shape classification dataset. The conclusion from this line of inquiry is that transitions from lobed to unlobed leaves are more common than transitions away from unlobed leaves.

(2) The authors conduct evolution simulations in a computational model of leaf development. Here, they look at {\it neutral} mutations and whether simply neutral evolution is sufficient to drive the observed trend.

The conclusion of the second part of the work is that the driver of the evolution toward simple leaf shape is entropy: there are more ways to make unlobed leaves than to make lobed leaves (at least in terms of gene regulation parameters that will produce the two leaf types). The argument is that random gene regulatory networks are more likely to produce unlobed leaves than lobed leaves; therefore, neutral evolution drives this trend.

Data Analysis:

Roughly $9000$ images of leaves were classified into 4 categories: unlobed, lobed, dissected, and compound. These labels were applied to the tips of 5 phylogenetic trees of angiosperms (3 resolved at the genus level and 2 at the species level). By fitting a continuous-time Markov chain to the labelled trees, the authors claim that there is a significantly higher rate of transition to the unlobed leaf shape compared to transitions to more complex shapes.

Simulation:

First, the authors validate a computational model (Runions et al) for leaf growth on an experimental dataset. By changing parameters in the model, they can recapitulate the morphological changes in the shapes of Arabidopsis leaves engendered by expression of two particular genes.

Then the authors run an evolutionary model (without selection, just random mutations) on top of the computational leaf development model. As the random walk in parameter space reaches a stationary distribution, they look at both the proportions of the leaf categories in the steady state as well as the transition rates between different categories. The result is that transitions to unlobed leaves are more common than from unlobed leaves.

Reviewer #1 (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:

Maigler et al. set out to test the hypothesis that individual differences in taste preferences are (in part) due to individual differences in central taste processing. They first tested rats' preferences for a variety of taste stimuli on multiple days. They then recorded responses of neurons in taste cortex to the same tastes on two consecutive days.

Strengths:

The authors collected high-resolution behavioral data from the same animals across multiple days, allowing for a detailed characterization of individual variation in taste preferences. They then performed recordings from the same set of animals in response to the same stimuli, allowing them to draw parallels between behavioral and neural responses.

Weaknesses:

(1) Recordings were performed only after multiple days of preference testing, and preferences were not tested in between/following recording sessions. This design precludes a direct comparison between neural and behavioral responses.

(2) Similarly, correlations between neural responses and behavioral measures are not analyzed/reported on an animal-by-animal basis.

Reviewer #2 (Public review):

Summary:

The study from Maigler et al investigates how between- and within-animal differences in taste preference relate to differences in neural responsiveness. The experiments rely on an elegant combination of behavioral assays to measure preference (e.g., repeated brief access testing, BAT) and electrophysiological recordings to monitor the activity of ensembles of neurons in the gustatory cortex (GC) of rats.

BAT with distinct batteries of tastants revealed pronounced variability in preference (measured as licking bout size) across individuals. This variability across individuals persisted after repeated testing. Repeated BAT also revealed that each individual rat's preference for different tastants changed across time.

Electrophysiological responses of GC neurons to batteries of tastants showed that firing in the "late epoch" of taste processing (i.e., 500ms post taste delivery) correlated more strongly with the individualized rat's BAT preference rather than with a canonical preference ranking. Importantly, this correlation was stronger for the last BAT session compared to the first. Finally, the authors show that the correlation disappeared in a second, consecutive recording session, indicating that exposure to tastants reconfigure preferences.

Strengths:

(1) The experimental design allows for an unprecedented look at the relationship between individual variability in taste preferences and neural processing.

(2) The study demonstrates that taste preference variability is not mere experimental noise but reflects the dynamic nature of taste. A key strength is the clear evidence that behavioral variability is reflected in neural activity patterns, establishing a strong correlation between brain and behavior.

(3) The evidence that simple exposure to familiar tastes can reconfigure preferences and taste representations is interesting.

Reviewer #3 (Public review):

Summary:

Maigler & Lin et al present a convincing set of behavioral and electrophysiological experiments and analyses exploring how individual differences in taste preference map onto neural responses in the gustatory cortex (GC). They go on to examine how both preferences and neural responses shift following intervening taste experience. Their experiments are strengthened by examining tastes of distinct identities and palatability (sweet, sour, salty, bitter) and correspond each animal's individual preference to the palatability-related late phase of the neural response.

Strengths:

(1) They demonstrate a relationship between the behavioral expression of taste preference and palatability-related GC neural responses. The direct correlation of expression of taste preference with GC neural responses indicates that taste preference behavior may be less noisy than previously thought, reflecting actual neural activity.

(2) They address the stability of individual taste preference by comparing within and between session expression. This finding indicates that individual preference on any given trial or test session can differ from canonical palatability.

(3) The animal's preferences for various tastes are reflected in the neurophysiological recordings, despite that behavior and physiology sessions are separated by several weeks, with an intervening surgery, across multiple delivery methods (active licking vs passive delivery), and across homeostatic states (thirsty vs sated).

(4) They provide evidence that representational drift in palatability coding may arise from sensory experience rather than from the passive passage of time.<br /> The findings are novel and impactful, and the results are relatively complete.

Weaknesses:

(1) The authors state that "no differences in effects were observed between taste batteries" (Methods), but it is not clear which analyses were performed to determine this, especially considering that many of the analyses are within-animal. Without more clarity, it is difficult to evaluate whether the interaction of different tastes within the sets of stimuli bias the main conclusions.

Reviewer #2 (Public review):

I appreciate the substantial amount of work the authors have invested in revising the manuscript. The response is extensive, and the addition of pooled frequentist and Bayesian analyses represents a considerable and technically sophisticated effort to address the concerns raised during review. The authors have also improved the use and presentation of the continuous pain-rating data and have responded constructively to several methodological points.

Nevertheless, with respect to my original review, I do not think the revisions have yet aligned the manuscript's central claims with the specificity and uncertainty of the evidence. The additional analyses provide some evidence consistent with a contribution of fitness to heat-pain modulation, but they cannot fully resolve the limited internal replication, selected sample or differences in measurement procedures between studies. Nor do they establish that sex has no effect on pain modulation. In my view, the evidence supports a modest, exploratory conclusion that fitness may contribute to variability in heat-pain modulation under specific conditions, rather than the more categorical conclusion that exercise-induced pain modulation depends on fitness but not sex. The manuscript would therefore be strengthened by reflecting this distinction more consistently in the title, abstract, Discussion and Conclusion. My remaining concerns, organised in relation to the original review, are detailed below.

(1) The core interpretation may not be fully supported by the data

(1.1) Lack of baseline condition

I am satisfied with the authors' substantive response to Comment 1.1, however I note that the authors are still attributing their findings to "hypoalgesia" in the Discussion.

(1.2) Lack of internal replication across conditions

The pooled analyses do not resolve the original lack of internal replication. The substantive effect remains largely restricted to heat pain at the highest stimulus intensity and is not clearly reproduced across stimulus intensities or for pressure pain. The authors' response describes the evidence more cautiously, stating that fitness "contributes to variability in exercise-induced pain modulation". However, the title and principal conclusions do not reflect the exploratory, modality-specific and statistically uncertain nature of the evidence.

(1.3) Deviations from the original study and selective use of data

I appreciate the addition of analyses using the continuous pain ratings, which addresses my concern that the richness of the data from the current study was not being fully used. However, the decision to pool the current and previous datasets introduces a related and potentially more consequential comparability problem. The previous study used retrospective post-stimulus ratings, whereas the current study used continuous ratings from which peak values were extracted. Rescaling these measures to a common numerical range does not establish their measurement equivalence. This is particularly important because study membership is closely confounded with the participant characteristics central to the manuscript: the higher-fitness female group was recruited and assessed in the current study, whereas the comparison groups were assessed using the earlier procedure. Consequently, apparent effects of fitness may partly reflect differences in outcome acquisition between studies. Indeed, including study membership improves model fit substantially more than including fitness.

(1.4) Over-reliance on null results regarding sex differences

I do not think the new Bayesian analyses resolve my original concern regarding the interpretation of the null sex effect. The authors state that the analyses provide no evidence for a moderating role of sex, but they do not report a Bayes factor clearly supporting the null hypothesis for the exercise intensity × sex interaction. In fact, Figure 5 clearly shows that the association between fitness and pain modulation is significant in males but not females. Panels D-F indicate uncertainty regarding a differently specified exercise intensity × sex interaction, rather than evidence for its absence. The figure therefore suggests that the role of sex remains unresolved and may qualify the association attributed to fitness. The authors should therefore distinguish absence of evidence from evidence of absence and temper the conclusion that exercise-induced pain modulation depends on fitness "but not sex".

(2) Limited sample and lack of diversity

The manuscript does not acknowledge the limited generalisability of this small, highly selected sample of physically active women recruited primarily from cycling clubs. Although the rebuttal states that the findings should be interpreted within the context of the sample studied, this qualification is absent from the Limitations section. It should be added, and the conclusions restricted accordingly.

(3) Methodological choices limit interpretability of the data

(3.1) The use of a non-standard VAS scale (0-150 with a fixed pain threshold at 50) is unconventional and may influence how participants report pain, while limiting comparability with related literature.<br /> The authors' response explains the rationale for the modified scale but does not fully address its implications for measurement comparability. In particular, setting all ratings below 50 to zero is not merely rescaling: it collapses distinct responses into a single value and may alter the distribution of the outcome. The cited study addresses the relationship between real-time and retrospective ratings, but does not validate this scale or transformation.

Reviewer #1 (Public review):

The idea is super interesting, and the subsequent work is potentially significant because it links peripheral inflammation to remodelling of perinodal adipose tissue and draining lymph nodes. This suggests an antigen-independent manner by which local tissue inflammation can communicate with and reshape immune organ structure and tissue metabolism. However, the evidence is suggestive. For instance, many conclusions rely on correlational weight/cellularity relationships, models with confounders (spontaneous wounding; potentially systemic IMQ), and macrophage dependence inferred from a single pharmacologic approach without definitive depletion/lineage or tracer-based causal link.

Comments on revised version:

Overall, the rebuttal addresses most of the original concerns constructively, with additional data and appropriate moderation of several claims. However, some of the key mechanistic conclusions remain over-stated. In particular, macrophage origin, the contribution of systemic inflammation, and the mechanistic relationship between fat-pad remodelling and lymph-node expansion remain incompletely resolved. The manuscript would nevertheless be acceptable if these limitations are clearly acknowledged and the mechanistic language toned down. That said, I think the rebuttal is broadly satisfactory.

Reviewer #2 (Public review):

Summary:

The authors aim to demonstrate skin inflammation is associated with fat pad atrophy and lymph node expansion. They further propose that these phenotypes are driven by the recruitment and lipid metabolism of CCR2-independent macrophages.

The authors took advantage of two skin inflammation models, fight-induced and imauimod-induced skin inflammation and analyzed multiple tissues, including skin, fat pads, and lymph nodes. Using a macropahge-depletion method (e.g., CSF-1R inhibitor), the authors further suggest the inverse correlation between fat pads atrophy and lymph node expansion is macropahge-dependent.

Comments on revised version:

The authors improved their manuscript with additional data and discussion. However, the authors need to clarify their terminology in the experiments. To strengthen their conclusion, authors need some additional experiments addressed below.

Clarify cohousing conditions in Fig. 1 through 3: the authors used 'resting' ,'alone', 'together'. These are unclear. Please state whether 'resting' mice were singly housed or co-housed in Fig. 1. If they singly house, specify when they were separated from their littermate or cage mates. In Fig. 1-3. If they were co-housed ('together'), specify whether their cage mates were littermate or non-littermate Ccr2-/- mice in the manuscript, including line 107.

Strengthen the link between fighting and the observed phenotypes: Co-housed Ccr2-/- males had increased lymph node (LN) weight and reduced fat pad weight. To test whether these changes are associated with fighting-induced skin inflammation, please consider comparing mice that are singly housed after three weeks of co-housing with mice that are singly housed throughout the same period.

Clarify the monocyte analysis: At line 141, please use 'monocytes' rather than 'inflammatory monocytes' if the analysis does not include inflammatory markers/phenotypes. Please also label the monocytes and macrophage populations in Fig. 3Di and 3Dii as was done for neutrophils and eosinophils in Fig. 3B.

Recruitment vs. Self-renewal: At line 144, CD11b expression alone does not distinguish recruited cells from cells expanded by local proliferation; Inflammation itself can alter CD11b expression. Please consider providing the evidence that distinguish these possibilities. Fate mapping would be an ideal approach, while Ki67 staining or BrdU incorporation assay could alternatively assess proliferation.

Reviewer #1 (Public review):

Summary:

This theoretical study of a simple system of stem, transient progenitors and fully differentiated cells provides interesting results about how tissues can reach homeostasis with different proportions of these cell types. The key ingredient is the feedback due to pressure, which regulates the proliferation rate. The study shows that by varying the rates at which stem cells switch to progenitor cells, and progenitor cells to differentiated cells, the final composition of the tissue can be tuned. In addition, the model shows that clusters of stem cells can arise in this model due to their effective immobilization and therefore that stem-cell niches can arise even in the absence of specific adhesion between different cell types.

The model is calculated using both cell-based simulations and continuum dynamics, and is thoroughly analyzed in its spatial and temporal characteristics.

Strengths:

The model is simple, yet leads to very rich results. The authors demonstrate the results of the model using both particle-based simulations and a continuum model, thereby enhancing our understanding of this complex system.

Weaknesses:

The origin of the stem cell niche is not so clearly explained.

Reviewer #2 (Public review):

Summary:

This is a theory/computational paper that explores a model of a two-dimensional tissue undergoing homeostatic turnover. The motivation is to explore how the rates of cell division and cell loss in a tissue can be precisely balanced to maintain tissue integrity. It is already well appreciated that this can be achieved by a feedback mechanism whereby cells tune their division or loss rate in response to a change in cell density relative to a homeostatic set point (e.g. PMID 30269903 and other papers cited in the introduction to this new manuscript). Cell density can be sensed locally by mechanical pressure.

Here, the question asked is whether pressure-dependent homeostatic control can maintain not only cell density (as previously known) but also cell type proportions when a tissue has a proliferative hierarchy. The specific example considered is a 3-tier hierarchy with stem cells (S) that give rise to transit-amplifying cells (T) that give rise to terminally differentiated cells (D), which are then lost. Next, the authors notice in simulations that in such a model of density-dependent cell division, stem cells undergo spontaneous clustering without any need for cell adhesion. Thus, the key result of the paper is that a simple pressure-based homeostatic feedback control leads to spontaneous formation of stem cell clusters, which the authors call "niche-like". They characterize these clusters numerically.

Overall, the work is elegant and presented in a pedagogical manner. But I think its central result has already been previously described (DOI 10.1103/PhysRevE.77.031907), albeit without the use of terms such as "niche-like" that increase the relevance of the work, and using a different detailed choice of model. Essentially, clustering is the outcome of a log-divergence of the density of random walkers undergoing a critical birth-death process in two dimensions, as discussed in the 2008 paper. Essentially, once stem cell division is coupled to total density (rather than just stem cell density), then the stem cells follow a critical birth-death process in 2D, and the clustering is an inevitable outcome. This is the precise point of the previous paper. As such, my review will focus on novelty compared to prior work.

Strengths:

The first strength of the paper is that it gives a clear and biologically oriented presentation of how pressure-dependent (or more simply, density-dependent) feedback can be sufficient to maintain steady-state homeostasis with defined proportions of stem, transit-amplifying, and differentiated cells. The authors scan parameters in numerical simulations using an established agent-based model of cells under mechanical tension, and show that tissue can be maintained provided that stem cell division rates are able to match loss rates. This is not very surprising, but I believe it has not been laid out before in this way, and it is clearly presented.

A second strength is that the paper may make a useful contribution by drawing attention to the connection between mechanical homeostatic feedback and the spatial organization of stem/progenitor cells. Even though there is a precedent for this point (see overview above), the work is more biologically oriented than the prior paper, and may therefore be useful to readers interested in how simple local rules can shape tissue organization. The current paper uses a more biophysically informed particle-based model for simulations than the prior work, and it provides a useful framework for studying the interaction between mechanical feedback, tissue homeostasis, and cell-type hierarchy that could be generalized. The simulations are well motivated, and the results are presented in a pedagogical manner. More on the comparison to the 2008 paper below.

Weaknesses (or rather, comparison to prior work):

The main weakness is that the central result of the paper appears to have already been previously described, albeit using different terminology and a different detailed choice of model. I will describe the similarities and differences between the two papers below.

The 2008 paper...

• ...is motivated by asking how a critical birth-death process can maintain uniform density in 2D. This is different from the current paper, which asks whether a birth-death process can be tuned by total density and still maintain cell type proportions. As such, the questions motivating the work are subtly different, although both worry about how homeostasis is maintained.

• ...considers a 2-tier model consisting of progenitor and differentiated cells (A->B->0). This is different from the current paper, which considers a 3-tier model (S->T->D->0). But the current paper is aiming to be general rather than specific, and I would propose that complexifying the model from a 2-tier hierarchy to a 3-tier hierarchy doesn't make the new paper qualitatively different.

• ...shows that "the population of progenitor cells should cluster over time" (quoted from the paper). This is shown for A cells in the 2008 paper, and is shown for stem (S) cells in this new paper. As such, the prior paper already shows the key result of this new paper.

• ...uses slightly different rules, which are clunkier: it allows for symmetric and asymmetric division of A cells, does not allow direct A cell differentiation (no A->B allowed), and it uses a hard-core lattice-based model with hole-diffusion to model density-dependent cell division. By contrast, the current paper uses a more biophysically informed two-particle agent-based model for simulations, and it only considers symmetric divisions and direct differentiation. As such, the current paper is a more realistic treatment than a lattice-based model, and simply different (not more or less realistic) in terms of ignoring epigenetic heritable sister cell correlations. But since clustering is a large-scale phenomenon, as is often the case in statistical physics, the microscopic implementations should not be important. As such, I would not expect the difference in rules to be important to the clustering.

• ...derives a long-term asymptotic form for the clustering dynamics of progenitor cells (Equation 15 of that paper, and the unnumbered equation at the top of column 2 of page 7 of the paper). This goes beyond the new paper, which only describes the phenomenon numerically. The 2008 paper also explains the phenomenon in terms of prior work on random walkers undergoing birth-death processes, which better links the phenomenon to prior statistical literature.

• ...shows experimental evidence for clustering of progenitors in mouse epidermis. This goes substantially beyond the current paper, which is entirely computational. That said, despite the excellent fit of data to the theory, I am myself not convinced that the clustering seen in epidermis is the result of this phenomenon alone.

• ...studies clonal dynamics and shows that it is consistent with a voter-model-like behavior, with clone size growing as t/log(t). The scaling law is different from that reported in the current paper.<br /> Thus, the key result that progenitor cells undergo clustering seems to have been mathematically described in the 2008 paper and even shown in that paper to be consistent with experimental data in one tissue.

That said, I do think that this new paper may make a useful contribution. It is certainly more biologically oriented (despite lacking experimental data, which the prior paper has). And it may be that the quantitative dynamics of clustering and clonal competition are subtly different in this model. So, with certain revisions, I am supportive of this work.

Specific suggestions:

(1) The new paper should appropriately cite precedent. The paper should avoid making claims that progenitor clustering in this model of birth-death with spatial density control is a major novel discovery. This was a key result of the previous paper. The new paper should also cite the 2008 paper for evidence that clustering of this type has been proposed to be seen experimentally. The differences between the papers discussed above could be used as needed in highlighting the contribution of the new work.

(2) There is still a question about whether microscopic details of the simulation may alter the asymptotic dynamics of the clusters and clones. The authors could compare the dynamics of clustering between their simulations and the 2008 lattice-based result (Equation 15 of that paper, the "1/log(t)" behavior of the density radial correlation function) derived in the original paper, and similarly compare clonal dynamics in that paper to this new paper. Whatever they find is interesting: if they confirm that the same dynamic behaviours occur, it will reinforce the results of the prior work, rephrase the problem in more relevant terms, and help make it accessible to a broader audience. If they show that their model leads to different quantitative dynamics, they could explore (in a supplement perhaps?) what is the origin of the difference, given that the models are superficially similar.

Reviewer #3 (Public review):

Summary:

The manuscript studies a minimal model of tissue homeostasis in which stem (S), progenitor/transit-amplifying (T), and differentiated (D) cells interact through stochastic fate decisions and mechanically regulated proliferation. Combining a compartment-level analytical description with particle-based simulations, the authors show that pressure-dependent growth can stabilise cell populations and maintain tissue homeostasis over a broad parameter range. They derive homeostatic cell fractions and identify distinct regimes, including tissues maintained by rare stem cells or by long-lived progenitors. Most notably, the simulations reveal the spontaneous emergence of persistent stem-cell clusters and renewal-unit-like structures in the absence of explicit niche signals or differential adhesion. The authors further analyse spatial correlations, cluster statistics, lineage dynamics and neighbourhood compositions, and argue that stochastic fate decisions qualitatively alter the spatial organisation of mechanically regulated tissues. Based on the annotated manuscript, several of these central claims concern the emergence and stability of stem-cell clusters and their interpretation as self-organised structures.

Strengths:

The manuscript is clearly written, technically competent, and combines analytical calculations with large-scale agent-based simulations in an elegant way. The systematic analysis of spatial observables, including pair correlations, cluster-size distributions, void statistics, neighbourhood composition, and lineage tracing, provides a rich characterisation of tissue organisation. The comparison with the authors' previous work on deterministic stem-cell hierarchies is particularly interesting, as it demonstrates that altering the fate-choice scheme can qualitatively change the resulting tissue architecture from stem-cell repulsion to stem-cell clustering. The study therefore generates a number of experimentally testable predictions regarding stem-cell spatial organisation and lineage dynamics. I also found the attempt to connect microscopic fate decisions to mesoscopic tissue-level organisation valuable, as this remains a relatively underexplored area at the interface of stem-cell biology and tissue mechanics.

Weaknesses:

My main concern relates to novelty and positioning within the existing literature. The manuscript frequently presents mechanical feedback as a mechanism capable of generating tissue homeostasis and robust cell-type proportions. However, the idea that crowding- or pressure-dependent feedback can robustly stabilise renewing tissues is already well established, both in mechanical homeostasis models and in more general feedback-based theories of tissue regulation. Consequently, the homeostasis aspect of the present manuscript appears more as an application of existing principles to a particular mechanical framework than as a fundamentally new conceptual advance. The authors should position their work more clearly with respect to these studies and explain more explicitly what genuinely new biological or mathematical insights are provided beyond the existence of homeostatic steady states.

The manuscript therefore derives its novelty primarily from the spatial phenomena emerging from the coupling of stochastic fate decisions and mechanical interactions. While the observed stem-cell clustering is intriguing, the mechanistic explanation remains incomplete. The authors attribute clustering to stochastic symmetric divisions combined with mechanical control, yet it remains unclear whether the observed structures genuinely arise from a new self-organised mechanical mechanism or simply reflect local genealogical correlations generated by repeated symmetric divisions. Several of the strongest conclusions, including long-range order, renewal-unit formation, and stable niche-like organisation, require more rigorous support. In particular, the manuscript currently lacks appropriate control models that would disentangle the effects of mechanics, stochasticity, and daughter-cell placement. Furthermore, the definition of clusters via a specific distance threshold appears somewhat arbitrary and may itself influence the inferred cluster sizes and conclusions regarding finite renewal units. It would be important to demonstrate robustness with respect to this choice.

I also have concerns regarding the simulation methodology and interpretation of the spatial statistics. Large tissues are assembled from smaller pre-equilibrated patches. While this may be computationally convenient, it raises concerns about whether long-range structures can emerge naturally and whether the reported spatial organisation could be affected by the construction procedure. Given that one of the central claims concerns spatial ordering over large scales, it would be important to demonstrate explicitly that the patching procedure does not influence the results. Similarly, the manuscript interprets pair-correlation and void statistics as evidence for long-range ordering of stem-cell clusters, but does not sufficiently exclude alternative explanations arising from finite system size, patch construction, or simple genealogical clustering.

Conclusion:

Overall, I find the manuscript interesting, whilst I also believe it should have a major revision. The most valuable contribution of the study is not the demonstration that mechanical feedback can maintain homeostasis, but rather the suggestion that stochastic fate decisions can qualitatively reshape the spatial organisation produced by mechanically regulated tissues. For a broad-interest journal, however, the authors should sharpen the positioning of the work relative to prior homeostasis theory, establish more clearly the mechanistic origin of the reported stem-cell clustering, and provide additional evidence that the observed structures are genuine emergent features of the model rather than artefacts of modelling assumptions or analysis choices.

Reviewer #1 (Public review):

Summary:

The manuscript entitled "NUDT2 loss defines quantitative limits for dinucleoside polyphosphate action on the cGAS-STING-TBK1 axis" investigates whether intracellular levels of dinucleoside polyphosphates can influence signaling through the cGAS-STING pathway. The study was motivated in part by a previous report proposing that Ap4A can bind to STING and inhibit its activity.

In the present work, the authors prepared recombinant human and mouse cGAS, STING, and TBK1 and systematically investigated their interactions with Ap3A, Ap4A, and Ap4G, which represent biologically relevant dinucleoside polyphosphates. To characterize these interactions, they employed a broad range of biochemical and structural approaches, including isothermal titration calorimetry (ITC), HPLC analysis of enzymatic reactions, X-ray crystallography, and a time-resolved fluorescence kinase assay.

First, the authors prepared human and mouse STING in both wild-type form and as specific mutants previously associated with altered binding of the canonical STING ligand cGAMP. ITC measurements showed that, whereas cGAMP binds STING with nanomolar affinity, none of the tested dinucleoside polyphosphates displayed detectable binding to any of the STING variants. The authors then investigated binding of ATP, GTP, and the dinucleoside polyphosphates to a mutant form of cGAS by ITC. Interestingly, all three dinucleoside polyphosphates showed apparent binding in a range similar to that of the tested NTPs. However, subsequent structural analysis did not reveal electron density corresponding to the dinucleoside polyphosphates in the active site.

The authors further examined the effect of Ap4A on TBK1 and found that Ap4A can inhibit TBK1 activity, but only at very high concentrations. Finally, they quantified intracellular ATP, GTP, Ap3A, Ap4A, and Ap4G levels in NUDT2-knockout cells. Although Ap4A and Ap4G concentrations increased substantially upon NUDT2 deletion, the measured intracellular concentrations generally remained below those required to significantly affect components of the cGAS-STING-TBK1 pathway in vitro.

Overall, the manuscript is clearly written and represents a careful and rigorous piece of biochemical work. I particularly appreciate the authors' effort to critically examine and clarify conclusions from previous studies. The experimental work is comprehensive.

Strengths:

A major strength of the study is the breadth and rigor of the experimental strategy. The authors combine binding measurements, enzymatic assays, structural analysis, kinase assays, and direct measurements of intracellular metabolite concentrations. Their data provide convincing evidence that the tested dinucleoside polyphosphates do not bind STING with physiologically relevant affinity and that inhibition of TBK1 by Ap4A occurs only at concentrations substantially higher than those normally reached in cells. Importantly, the authors also quantify the intracellular concentrations of these metabolites in cells lacking NUDT2 and show that, although Ap4A and Ap4G levels increase significantly, they generally remain below the concentrations required to affect the tested signaling proteins in vitro. This quantitative comparison between biochemical effects and intracellular metabolite levels is particularly valuable and strengthens the physiological interpretation of the study.

Weaknesses:

Interpretation of the pppGpA density in the cGAS structure.

Importantly, when Ap4G was used in the crystallographic experiments with cGAS, the authors observed density corresponding only to pppGpA. They interpret this observation as potentially resulting from processing of Ap4G by DNA-bound cGAS to generate a canonical reaction intermediate.

Based on my direct experience with structural studies of an unrelated enzyme using commercially supplied Ap4G from Jena Bioscience, I believe that an alternative explanation should be carefully considered. In our experience, Ap4G preparations can contain small amounts of pppGpA, likely at the per mille level, as a side product of the chemical synthesis. If the studied protein has substantially higher affinity for pppGpA than for Ap4G, even such a minor contaminant can become strongly enriched in the active site during crystallization and consequently dominate the observed electron density.

Indeed, traces of a corresponding contaminant may already be visible in the HPLC profile presented in Figure S2.3C. I therefore strongly suggest repurifying Ap4G by HPLC and repeating, at minimum, the HPLC-based experiments shown in Figure S2.3C using the purified material. Ideally, the purity of the Ap4G preparation used for crystallography should also be carefully documented.

Until this possibility has been excluded experimentally, I would recommend that the authors substantially temper the conclusion that pppGpA observed in the crystal structure originates from cGAS-mediated processing of Ap4G.

Reviewer #2 (Public review):

Summary:

Dinucleoside polyphosphates have been found to increase in responses to cellular stress and are involved in the regulation of transcription, antibiotic resistance, DNA replication and innate immunity in metazoa. Increased Ap4A levels have been previously found to regulate the cGAS/STING pathway, leading to the proposal that modulation of Ap4A levels may be a suitable pathway to pharmacologically modulate cGAS/STING signalling (Guerra et al., 2020). Here, Weiland et al. present compelling biochemical, biophysical and structural evidence that dinucleoside polyphosphates (Ap3/4A and Ap4G) do not interact with STING nor are likely to affect cGAS signalling in vivo.

The evidence that they present evaluates the interactions of Ap3/4A and Ap4G s with cGAS, STING and TBK1 kinase as key signalling molecules in the cGAS/STING innate immune response. Previous work has identified Ap4A as a regulator of cGAS/STING signalling, and through precise characterisation of the biophysical interaction, crystallographic as well as modelling data provide evidence that these effects are too weak to affect these processes in vivo. Their work identifies that there are no direct interactions between STING and dinucleoside polyphosphates at physiological concentrations and at hyperactivated levels in NUDT2 mutants. There are detectable interactions of both Ap4A/and Ap4G with cGAS. In the presence of DNA, cGAS shows either ATP when bound with Ap4A or an intermediate of the cGAMP synthesis when crystallised with Ap4G. This is an interesting observation, showing Ap4G appears to serve as a weak substrate for canonical cGAMP production in the presence of DNA. Finally, the effect of Ap4A on the catalytic activity of TBK1 was evaluated and showed very weak effects. Competition assays in the presence of ATP and Ap4A/Ap4G showed a higher inhibitory effect for Ap4G, but only at concentrations 5x or greater than intracellular ATP levels and much weaker effects for Ap4A (~32x ATP levels).

Strengths:

The approaches used provide robust data for a subset of physiological Ap4Ns. The strength of their evidence comes from the complementary structural and biophysical approaches investigating the interactions of cGAS, STING and TBK1 independently. These data, including the dissociation constants for Ap4A and Ap4G with cGAS, allow for comparison with physiological levels of the dinucleoside polyphosphate in vivo. The use of quantitative mass spectrometry provides some increased rigor to the conclusions by integrating the in vitro and in vivo studies.

Weaknesses:

The data presented for Ap4G and Ap4A are convincing, and conclusions are consistent with the evidence presented. However, there are other Ap4Ns (Ap4C/U) that may be active against cGAS/STING/TBK1 that are not included in this study, which weakens the conclusions. This could be rectified relatively simply. The data would be more robust if the effects of Ap4C and Ap4U were included for cGAS using ITC, and also the additive effect of competition assays with physiological ATP and the levels of all Ap4Ns in the same reaction as in Figure 3A. At present, each Ap4N is investigated in isolation. To determine the effect of physiological Ap4N levels, reactions with all 4 Ap4Ns at maximum physiological levels as determined from NUDT2 KO cells would provide a robust test of their activities.

Overall, the in vivo data suggest that Ap4A and Ap4G can reduce cGAS activity, but only weakly and only at levels that are unachievable even where NUDT2 is inactivated. The data suggest that Ap4A/Ap4G do not affect cGAS/STING/TBK1 signalling at physiological levels and that NUDT2 targeting would be ineffective for the pharmacological modulation of cGAS/STING/TBK1 signalling. This conclusion is accurate only if Ap4C/U do not contribute to this inhibition. At present in the absence of these data, this conclusion cannot be made, as their activity could in principle affect cGAS/STING signaling.

Reviewer #3 (Public review):

Recent work reported that STING binds Ap4A and proposed that elevated Ap4A levels could modulate the cGAS-STING pathway. Intracellular Ap4A levels are controlled by the hydrolase NUDT2, itself a cancer drug target, and loss of NUDT2 raises cellular Ap4A pools. Building on this, the authors set out to investigate whether and how Ap4A modulates the cGAS-STING pathway. This question was motivated by the fact that the mechanism by which STING might bind a linear dinucleotide such as Ap4A remained unclear, and by the existence of alternative routes of crosstalk between Ap4A and the pathway. These include the chemical similarity between Ap4Ns and pppGpA, the linear intermediate generated by cGAS during cGAMP synthesis, raising the possibility that Ap4A could inhibit cGAS directly, as well as a potential downstream effect on the kinase TBK1.

Using in vitro biochemistry, the authors show that STING does not, in fact, bind Ap4A, contrary to what was previously claimed, and they further examine the impact of NUDT2 loss on the cGAS-STING pathway. This clarifies for the field whether Ap4A could influence the pathway in any way, whether through binding to cGAS, STING, or TBK1.

The authors find that cGAS can bind Ap4A but cannot process it. cGAS also binds Ap4G, but processes it only inefficiently and only when supplied at very high concentrations in vitro. This argues against physiological relevance in cells, since inhibition of canonical cGAMP synthesis would require Ap4Ns to be present in excess over ATP and GTP, a condition unlikely to be met at physiological nucleotide concentrations even when NUDT2 is absent. The authors also test for effects on TBK1, showing that while it can bind Ap4A, the concentrations required for inhibition are similarly not physiological.

The authors conduct a thorough series of biochemical and biophysical experiments to clarify the underlying mechanism, systematically ruling out a plausible effect of Ap4A in cells at each step. Even where an effect on cGAS or TBK1 can be detected at very high, non-physiological concentrations, this remains confined to in vitro conditions. The experiments are sound and conducted with scientific rigor, and the results support the authors' conclusions.

This work provides clear evidence that STING does not bind Ap4Ns, and that even where binding does occur elsewhere in the pathway, there is no plausible mechanism by which Ap4Ns could modulate the cGAS-STING pathway under physiological conditions. This resolves an open question for the field: if Ap4Ns do have biological effects related to this pathway, these are unlikely to arise from a direct interaction with cGAS, STING, or TBK1, and must instead be mediated through other processes. The methods and data will be a useful reference for the community when evaluating future claims of nucleotide second-messenger crosstalk.

Prior studies have shown that NUDT2 disruption, which elevates cellular Ap4A levels, is associated with down-regulation of interferon-response pathways. This is notable in light of the current findings, which show no direct biochemical interaction between Ap4A and cGAS, STING, or TBK1. Together, this suggests that if elevated Ap4A does suppress IFN production, it likely does so indirectly, through mechanisms other than direct engagement of the cGAS-STING-TBK1 axis.

Reviewer #1 (Public review):

In this study, Chaudun et al use optogenetics and genetically encoded neuromodulator sensors to test to what extent dopamine neuron stimulation produces striatal serotonin release, and vice versa. The study is timely given growing interest in dopamine/serotonin interactions, but important controls are missing. The authors find that striatal dopamine and serotonin afferents function largely independently, with dopamine neuron stimulation producing no striatal serotonin release and serotonin neuron stimulation (possibly) producing minimal striatal dopamine release.

In the revised manuscript draft, the authors increased sample sizes for some important experiments, removed inconclusive electrophysiology data, reorganized the figures, and added new anatomical tracing experiments. The critical fluorophore-only controls for the optostimulation experiments requested by reviewers were not done.

Unfortunately, with the exception of increased samples sizes, these revisions have done little to substantially improve the strength of the evidence behind the authors' conclusions. These conclusions, as reflected in the new title of the paper, have also slightly changed in a manner that puts them further at odds with the data presented. As a result, my opinion continues to be that the study is interesting and the experiments are useful, but important controls are missing, a more cautious interpretation is warranted, and the organization of the study is confusing. I explain my reasoning below.

(1) A major criticism of the original manuscript was that the electrophysiology experiments were only tangentially related to the question under study. The manuscript has now been reorganized in such a way that the cocaine experiments are similarly irrelevant. In the authors' own words, the central question of the study is "does activity in one [DA or 5-HT] system directly recruit transmitter release from the other, or do DA and 5-HT operate mainly through parallel circuits?". Optogenetically stimulating release of dopamine while recording serotonin activity (or vice versa) begins to answer this question, and in the original draft, cocaine-evoked dopamine and serotonin recordings were presented side by side with the opto-evoked dopamine/serotonin data. In this configuration, the drug-evoked recording data allowed readers to compare the magnitude of dopamine/serotonin release evoked by an artificial optogenetic manipulation to that evoked by a behaviorally relevant pharmacological treatment. This serves a purpose. In the revised manuscript, the cocaine experiments are presented in a standalone first figure. As the authors themselves note in their response to reviewer 2, cocaine independently evokes dopamine and serotonin accumulation is therefore poorly suited on its own to test how activating one neuromodulatory system affects the other. Thus, the cocaine data presented alone in this way neither address the paper's central question nor support the paper's conclusions.

(2 The original manuscript suggested that one way by which striatal serotonin activity could recruit striatal dopamine release would be if the same serotonin neurons project to both VTA and striatum. To test this, the authors use retrobeads to identify DS-, NAc-, and VTA- projecting dorsal raphe neurons. However, they neither identify whether the labeled neurons are serotonergic nor evaluate colocalization between the retrograde tracers as would be required to ascertain whether the same serotonin send axon collaterals to more than one region. Thus, the anatomical data presented do not answer the question of whether the same serotonin neurons innervate both targets.

(3) As noted in the original round of review, applying light stimulation to mice expressing a fluorophore-only construct without opsin is an important control in optostimulation experiments that is widely standard in the field. The omission of such a control is a weakness of the paper. The authors suggest that other results presented - such as the lack of green serotonin sensor activation when red light is applied in the midbrain in Fig 2G-H - argues against cross-talk between the red and green optical channels. This is technically correct, but ruling out cross-talk between optical channels is not the only reason such a control is necessary. The high intensity red light used for optostim travels several millimeters through tissue and can reach the retina. Although mice do not have cones to detect red light (and therefore cannot distinguish the color red from other colors), their rods are sensitive to red light. As a result, bright red intracranial optostim can be perceived by the animal as a flashing light, and this sensory stimulus can produce a neural response. The absence of such a response in the serotonin system in Fig 2G-H does not rule out the possibility that the small response in the dopamine system observed in Fig 3G-H is driven by sensory input rather than a bona fide physiological effect of serotonin neuron activation on striatal dopamine release. Crucially, sensory responses to the stimulating light would also show 2Hz entrainment to the frequency of the stimulating laser trains. In other words, without a fluorophore-only control, the entirety of the authors' results pertaining to serotonin-evoked dopamine release can be explained by artifactual effects of the optostimulation. If this opsin-negative control is absolutely impossible for the authors to perform, at the very least this major limitation should be clearly and explicitly addressed in the discussion because it pertains directly to the study's main conclusions. This brings me to my final point.

(4) Taken together, the authors' data appear to support two primary conclusions. First, optogenetic dopamine stimulation has no effect on striatal serotonin release. Second, synchronous and supra-physiological activation of the serotonin system has a very modest effect on striatal dopamine release that might be entirely explained by artifacts of the optostimulation protocol. The miniscule magnitude of the evoked dopamine response observed following maximally strong (15-20 mW) optogenetic serotonin stimulation also bears consideration here. It argues that even if the observed dopamine release effect is not an artifact of the optostimulation protocol, serotonin-evoked dopamine release is likely to be vanishingly small or absent in other conditions when serotonin neuron firing is neither supraphysiological nor synchronous. The new title strongly implies the existence of significant cross-talk, which is not well supported by the data. Claims throughout the text that call the cross-talk effect reliable or otherwise robust are similarly overstated.

Reviewer #3 (Public review):

The authors suggest that the small release of DA may be due to a release of glutamate from DRN 5-HT neurons to the VTA that stimulates weakly and in a transient fashion the VTA DA neurons, which in the end, produce a transient and small release of DA in the NAc.

Their findings give more information on the previously reported complex and partial known crosstalk between 5-HT and DA in the NAc.

Comments on revised version.

The authors have added several new experiments that address some of the prior concerns. However, there are still points of confusion. For example, the authors repeatedly argue that 5HT or DA are synaptic when in fact most of the transduction mechanisms for these neuromodulators and their transporters are extra synaptic, as indicative of volume transmission. This is not well articulated in the authors' interpretative scheme.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors investigated the relationship between the Tat system and MPIase, a glycolipid that facilitates protein integration into the bacterial cell membrane. The TAT (twin-arginine translocation) system is a unique membrane transport machinery that exports fully folded proteins containing a twin-arginine signal peptide. Using both in vivo and in vitro approaches, the authors demonstrated that a sufficient amount of MPIase is required for Tat-dependent protein translocation. Furthermore, the authors successfully reconstituted the Tat transport system by combining recombinant TatA, TatB, TatC, MPIase, and FoF1-ATP synthase.

Strengths:

The reconstituted system clearly demonstrated the requirement for each component, as substrate translocation occurred only when all components were present. Based on these findings, the authors proposed a mechanistic role for MPIase in facilitating Tat-mediated membrane translocation.

Previous studies have shown that MPIase is involved in Sec-dependent protein translocation and membrane protein integration, as well as YidC-dependent membrane insertion. The present study further demonstrated that MPIase also plays an essential role in the Tat translocation pathway.

Overall, this work highlights the central importance of MPIase in bacterial membrane protein biogenesis and provides new insights into the molecular mechanism of Tat-dependent protein transport.

Reviewer #1 (Public review):

Summary:

This study uses high-throughput bacterial cell surface display to identify LC3B interacting peptides in the human proteome. The screen is unbiased and this type of assay has not previously been used for selecting LC3B interacting peptides. The screen was done with library of 500,000 peptides and they ended up with 427 peptides that they scored as high-confidence LC3B binders. The experiments performed are solid and data are analyzed using well documented methods and statistics.

The aim for the authors was to isolate LC3B interacting peptides from the human proteome, and the screen succeeded in doing so. The selected set of peptides included several previously reported LIR motifs, but also many novel LC3B binding peptides that either contained or did not contain the canonical core LIR motif [WFY]xx[LVI].

Another aim was to identify binding determinants important for the LC3B interaction, and they made an interesting sequence logo based on selected LIR containing peptides. This study does not really extend our knowledge related to binding determinants essential for LIR motifs in LC3B binding, but it expands the number of exceptions to the canonical core LIR motif.

Strengths:

The approach used here (high throughput bacterial-surface-display) is new. The screen is unbiased and the fact that peptides are directly tested for LC3B binding may facilitate the discovery of non-canonical LIR motifs. The screen appears to be highly selective and manage to distinguish between peptides that interact with LC3B and peptides that do not interact.

Weaknesses:

It is a limitation that no proteins are analyzed in this study. Further work is therefore needed to verify that identified LIR motifs are functional in full-length proteins and in cells.

Comments on revised version.

It remains a weakness that none of the identified LIR motifs are tested in full-length proteins or cells, but all the specific comments in my initial review have been addressed.

Reviewer #2 (Public review):

Summary:

To discover peptides that interact with autophagy-related protein LC3B and profile the key binding determinants, the authors screened a library of ~500,000 36-residue peptides derived from the human proteome using bacterial cell-surface display. Analysis of the screening data revealed exceptions to the reported LIR motif and a strong preference for negatively charged residues adjacent to the LIR.<br /> These results support a refinement the LIR motif definition and expand the network of candidate LC3B interaction partners.

Strengths:

High-throughput approach

Weaknesses:

Lack of in vitro data and molecular dynamics simulations

Comments on revised version.

In the revised manuscript the authors did not provide in vitro and molecular dynamics simulations data.

Reviewer #3 (Public review):

Summary:

The LC3 family of proteins, which includes LC3B, are ubiquitin-like proteins that are covalently linked to phosphatidylethanolamine in the expanding autophagosomal membrane during autophagy. LC3 family members bind to short sequences of amino acids that reside within dynamic regions in a wide variety of proteins. These sequences, termed LC3 Interacting Regions (LIRs), were initially thought to function primarily to link LIR containing autophagy cargo receptors to LC3 family members to help facilitate their capture during autophagy. However, the functional importance of LIRs in autophagy has broadened to include more general functions in autophagy as well. While a general consensus for LIR sequences has been described as [FWY]0-X1-X2-[LVI]3 recent work has suggested that additional sequences outside of the canonical LIR sequence can bind LC3 family members and play important roles in autophagy. In this manuscript by Kosmatka et al, the authors perform a high throughput screen using bacterial surface display coupled with fluorescence associated cell sorting to identify which human sequences can bind to LC3B. They identify a variety of peptides capable of binding LC3B including peptides from proteins that have not previously been described as LC3B binding proteins. The results from the bacterial surface display were then used to guide sequence analysis, mutational analysis and structural studies to further characterize the range of LIR sequences that are capable of binding LC3B. Taken together, this work adds to the growing knowledge of how LIR sequences interact with LC3 family members and demonstrates which amino acids both inside and outside of the LIR sequence aid in binding. This work also identifies new potential LC3 binding proteins which may play unknown roles in autophagy regulation. Lastly, this work reinforces the importance of alternative LIR sequences such as the [WFY]0-X1-X2-[WFY]3 sequence which the authors have dubbed the LIR+ sequence.

Strengths:

The manuscript uses a robust approach to identify and characterize different peptide sequences that can interact with LC3B. They validate a large number of sequences using biolayer interferometry (BLI). The large number of LC3B binding sequences and their dissociation constants adds significant new information to the field that will help others understand what sequences can bind to LC3B. The authors are also very careful to accurately report on their data and not overly interpret their findings.

Weaknesses:

After the authors identify proteins from their bacterial display assay, the remainder of the manuscript is focused on characterizing the different types of sequences that are identified in addition to validating the LC3B-LIR interactions using BLI and X-ray crystallography. However, it's not entirely clear if the screen identified novel LC3B binders that interact with LC3B in cells. While I acknowledge that the focus of the manuscript is on the characterization of LIR sequences that can bind LC3B it seems like a missed opportunity to not validate a few of the novel LC3B binders in vivo.

Reviewer #1 (Public review):

Summary:

The authors present the most comprehensive phylogenomic study of free-living kinetoplastids to date, including newly generated transcriptomic data from 11 species. This dataset provides a solid foundation for future comparative evolutionary studies of kinetoplastids, a group that includes important human pathogens such as Trypanosoma brucei.

Strengths:

The study is clearly written, and the analyses are thoroughly described, well documented, and reproducible. The phylogenomic dataset comprises 444 proteins, which is larger than those used in many comparable phylogenomic studies. The main strength of the study is the substantially improved taxon sampling of neobodonids, which provides a much stronger framework for resolving evolutionary relationships among free-living kinetoplastids.

Weaknesses:

The phylogenomic analysis is based on a newly assembled dataset comprising 444 single-copy orthogroups. Using an established phylogenomic dataset, expanded to include the newly studied species, to confirm the inferred relationships would provide additional support for the robustness of the recovered topology.

Reviewer #2 (Public review):

Summary:

This is a highly competent and very throough phylogenomic study of the position of neobodonids within the Kinetoplastid phylogeny. The addition of new transcriptomic data for diverse neobodonids allows their relationships to be better understood, leading to convincing changes to neobodonid taxonomy.

Strengths:

The generation of transcriptomic data produces more phylogenetic characters than ever before from several, diverse neobodonid lineages. This represents a substantial increase in the data available for this relatively unstudied group. The methodology used to define the character set and then estimate the phylogeny is conventional, very thoroughly described and expertly executed. The phylogeny is highly robust, and we can be very confident of the result.

Weaknesses:

These changes to neobodonid taxonomy, or essentially the discovery that some 'neobodonids' actually represent distinct lineages at the base of the Metakinetoplastida, are not surprising. So undersampled are the Kinetoplastida, both in terms of molecular markers and phyletic diversity, that an investment in sampling on this scale is always likely to bring about changes. The significance of these changes is not immediately apparent. Since they do not concern the Eubodonidae, they have no implications for the trypanosomatids and the new Metakinetoplastid lineages are very distant from the origins of parasitism, such that comments on "preadaptations for disease" are not compelling.

Reviewer #3 (Public review):

Summary:

The manuscript by Zavadska et al. presents a phylogenomic study focused on the relationships among metakinetoplastids, specifically addressing the question whether Neobodonida are monophyletic. The authors collected eleven kinetoplastid strains affiliated with five out of six neobodonid clades identified in previous studies and sequenced their transcriptomes. These data along with SRAs available from public databases were processed via assembly, annotation and decontamination. The final dataset, representing all (non-trypanosomatid) kinetoplastids with genome and/or transcriptome data available as well as selected trypanosomatids and discoban outgroups, was used for protein orthology inference and identification of single-copy orthologs present in the majority of taxa, followed by phylogenetic analysis in maximum likelihood and Bayesian frameworks.

Strengths:

I find the new data and resulting phylogenetic reconstruction valuable and interesting, particularly given the paucity of genomic/transcriptomic data from free-living kinetoplastids. The study is well-designed methodologically, and the main finding (paraphyly of Neobodonida) appears indisputable, considering the provided phylogenimic evidence. Following best practices, the authors shared their primary data, scripts, and files resulting from the conducted analyses.

Weaknesses:

Several aspects of the presentation and interpretation would benefit from revision. In particular, the composition of the neobodonid lineages central to the study is insufficiently explained, and an 18S rRNA gene-based tree showing these lineages and the placement of the newly analysed strains would substantially improve the clarity of the study. The Introduction would also benefit from a more concise and better-structured account of previous phylogenetic evidence and a clearer explanation of the broader biological significance of kinetoplastids, while the Methods could be streamlined by removing redundant information and presenting some details in tables. Finally, the rationale for including the electron microscopy images in the supplement should be clarified, as these are currently not discussed in the text and represent only a single studied strain.

Reviewer #1 (Public review):

Summary:

This study addresses an important question of how recovery from conditioned fear can be characterized beyond the reduction of defensive responses. The authors combine multiple behavioral measures with a theory-guided hidden Markov model to identify recurring behavioral modes and examine how the organization of behavior changes during fear conditioning and extinction. The study provides an interesting and potentially valuable framework for examining recovery from conditioned fear as a broader change in behavioral repertoire rather than simply as a reduction in defensive behavior.

Strengths:

A major strength of the study is the attempt to characterize fear-related behavior as a dynamic organization of multiple behavioral measures rather than relying on a single conventional measure such as freezing. The integration of freezing, ultrasonic vocalizations, and food-reinforced behavior into recurring behavioral modes provides a potentially useful approach for capturing behavioral states that may be missed by analyses of individual responses. The study also presents a theoretically motivated framework for distinguishing defensive, quiescent, exploratory, and goal-directed behavioral modes, which could provide a useful conceptual basis for studying functional recovery following aversive experiences.

Weaknesses:

The main concern is whether the analyses and behavioral definitions provide sufficient support for the interpretation of these behavioral modes and, in particular, for the proposed concept of functional recovery. First, the data-driven model selection indicates substantially better predictive performance for eight states, whereas the authors retain four states primarily to conform to their theoretical framework. A stronger justification for prioritizing the four-state solution would therefore strengthen the interpretation of the results. Second, it is difficult to determine from the current behavioral measures whether the Quiescent state reflects safety and rest or behavioral inhibition associated with residual fear or anxiety. The marked reduction in exploratory and goal-directed behavior could potentially be consistent with either interpretation, making it important to consider alternative explanations for this state.

The definition of functional recovery also warrants further consideration. The authors propose the reinitiation of food-seeking behavior in the previously threatening environment as an important indicator of recovery. From an evolutionary and ethological perspective, however, an animal that has experienced a threat while foraging in a particular location may benefit from shifting its foraging to an alternative location rather than returning to the previously threatening location, even after extinction learning. Thus, the resumption of goal-directed behavior in the previously threatening environment may not necessarily represent a biologically appropriate benchmark for successful fear extinction or functional recovery, as functional recovery may involve substantial changes in motivational processes that cannot be captured by the simple return of a previously suppressed behavior. More broadly, the results may support the value of examining behavioral repertoire during extinction, but they do not yet establish that restoration of the broader repertoire, or specifically the return of goal-directed behavior in the previously threatening environment, is required for functional recovery.

Finally, the use of the no-shock control group could be more informative. The observed reduction in exploratory behavior during conditioning cannot by itself distinguish associative fear learning from habituation to novelty. A direct comparison between shock and no-shock groups would therefore help determine whether the changes in behavioral modes are specifically related to conditioning.

Overall, the study provides a potentially useful framework and an interesting conceptual perspective on recovery from conditioned fear. However, the strength of the evidence supporting the interpretation of the identified behavioral modes and the proposed definition of functional recovery is currently limited. Addressing these interpretational and analytical issues would strengthen the manuscript and help establish the extent to which this framework provides a meaningful advance in the study of fear extinction and recovery.

Reviewer #2 (Public review):

Summary:

The authors aimed to develop and validate a preclinical computational framework for assessing functional recovery after aversive learning. They argue that a reduction in defensive behavior (e.g., freezing) is insufficient to conclude recovery, and that a comprehensive assessment must also track the re-emergence of exploration and goal-directed action. To test this, they adapted a multimodal paradigm in rats, measuring freezing, 22-kHz and 50-kHz ultrasonic vocalizations (USVs), and food-reinforced lever pressing. Using a theory-guided hidden Markov model (HMM) with four states derived from tri-reference-point theory (Fear/Danger, Quiescent, Exploratory, Goal-directed), they decoded behavioral trajectories across fear conditioning, extinction, delay, and contextual relapse experiments.

Strengths:

(1) The study tackles a significant gap in animal models of fear and trauma-related disorders. It correctly identifies that a focus on a single defensive response like freezing may be misleading and that a broader behavioral assessment is necessary to understand the impact of interventions.

(2) The application of a hidden Markov model to combine multiple behavioral channels into a cohesive, theory-driven framework is a strength. This approach moves beyond simple summary statistics to capture the temporal dynamics of behavior and allows for the identification of distinct, recurring states.

(3) The authors demonstrate commendable rigor in their model selection and validation. They employ discrete-aware scoring to address the boundary issues of count data and conduct extensive stability analyses across restarts, variance floors, and studies. The association of the Fear/Danger mode occupancy with fecal boli, an independent autonomic measure, provides a convincing external validation.

(4) The study provides several important findings. For instance, it shows that during the first extinction session, although Fear/Danger occupancy declined, the dominant state was Quiescent, rather than Exploratory or Goal-directed. This directly supports the core premise that the absence of fear does not equal functional recovery.

Weaknesses:

(1) The authors transparently report that their results are not emission-family invariant. The failure of count-native models (e.g., negative binomial) to converge or produce the expected four-state solution is a major limitation. This suggests the theory-guided state structure is tied to the specific Gaussian representation chosen and may not be a robust and universal feature of the behavioral data. This limits the strength of the claim that the data naturally resolve into these four modes.

(2) The exclusive use of male rats from a single laboratory limits the generalizability of the findings to female animals and other experimental settings. The cross-study recurrence analysis is a helpful sensitivity check but does not substitute for true model transfer to an independent, out-of-sample dataset.

(3) Testing K=4 vs. K=8 raises the question of whether the four-state solution is the most appropriate level of abstraction for the questions being asked.

(4) The interpretation of the 50-kHz USV band as an Exploratory state is somewhat broad. 50-kHz calls are emitted in a variety of contexts, including social interaction and reward. While the use of the band is justified, it remains an indirect measure of exploration and should be interpreted with caution. The interpretation and link to the exploratory state should be toned down and discussed.

Reviewer #1 (Public review):

Summary:

The manuscript proposes an architecture and distance-regression-based logic for 3D cell segmentation.

The architecture combines a U-Net backbone with an xLSTM bottleneck layer and two novel components: a Zernike Phase Layer that is used for input normalization and the Scaled Grid Geocaps that link the input and bottleneck, inspired by the Capsule mechanism.

During training, the network predicts foreground vs. background and regresses a distance transform as output. During inference, these predictions are used as input to a watershed procedure to segment cells in 3D.

The method is evaluated by training on four different 3D cell/nucleus segmentation tasks and compared to StarDist3D and CellPoseSAM baselines, which are also trained on the respective datasets using the same train / val / test splits.

The authors report improved segmentation quality compared to the baselines.

Strengths:

The experiments are solid; ablation studies evaluate the main architectural components, and the software appears to be well documented (I did not have time to test it).

Weaknesses:

(1) This is not really a weakness but a general point: the main issue in microscopy segmentation is that a lot of training data is needed if training a network from scratch. This results in a very laborious data annotation process. This is what modern approaches like CellPoseSAM and microSAM address by providing strong pre-trained networks that work well out-of-the-box for many imaging settings and can then be fine-tuned with a few corrected images to achieve state-of-the-art results. Having a better 3D segmentation approach is of course still worthwhile, but does not address the main practical challenge. I would suggest clarifying this in the introduction.

(2) The authors implement a well-known strategy to segmentation in microscopy: regressing the distance transform. They acknowledge some prior work (Scherr et al., Lux and Matula), but this approach is more prevalent than acknowledged, including for 3D cell segmentation. For example, microSAM [1] implements cell instance segmentation by regressing the distance to the cell boundary and centroid, which is applied in 3D by CochleaNet [2]. See also [3] for an overview of different distance- or flow-field-regression-based cell segmentation approaches. I would suggest performing a more thorough literature review and acknowledging more prior work.

(3) The baseline comparisons are not described in any detail, are questionable for CellPoseSAM, and lack current state-of-the-art models:

3.1) The details on training and inference for the baseline methods are missing. This is particularly missing for CellPoseSAM. Here, it would be important to clarify whether the model is initialized randomly or with CellPoseSAM's pretrained weights and which of the two different 3D segmentation modes is used (see next point). It would also make sense to report both CellPoseSAM in zero-shot mode and finetuned for all cases.

3.2) CellPoseSAM supports two different 3D segmentation modes: either a "2.5D" segmentation mode, where the network is applied across all three axes, the resulting flow maps are merged, and then used for segmentation. And an "overlap-based stitching mode", where segmentation is applied only in the XY plane and slices are then merged based on overlap. It is unclear which of these modes is used. Ideally both should be reported; the "2.5D" mode often leads to worse results for anisotropic data, and we almost always prefer the overlap-based stitching in practice.

3.3) Two important state-of-the-art baselines are missing:

i) microSAM [1], which is widely used for cell segmentation based on a pretrained 2D network that is extended to 3D using a similar strategy as CellPoseSAM's overlap-based stitching mode. It would make sense to report both zero-shot and fine-tuned performance.

ii) uSeg3D [4]: this method implements a generalized 3D stitching approach that works independently of the underlying architecture and reports significant improvements.<br /> Improving and extending the baseline experiments would give a much better picture of the practical relevance of this work.

References:

[1] https://www.nature.com/articles/s41592-024-02580-4

[2] https://www.biorxiv.org/content/10.1101/2025.11.16.688700v1.abstract

[3] https://doi.org/10.6084/m9.figshare.32782521

[4] https://www.nature.com/articles/s41592-025-02887-w

Reviewer #2 (Public review):

Summary:

In their manuscript "Penumbria: Advanced 3D cell segmentation for biomedical imaging", the authors describe their 3D nuclei segmentation pipeline and compare it against state-of-the-art methods for nuclei and cell segmentation.

The introduction is clear, with state-of-the-art methods, for instance, segmentation of cells from microscopy images, and motivates the method with science that can be done with cell segmentation. Related work is appropriately mentioned with the caveat that it conflates cell and nuclei segmentation, and some related work is missing.

The Results section describes the loss, the architecture novelties, and evaluation results on nuclei segmentation, not cell segmentation. Here it becomes clear that Penumbria addresses 3D nuclei segmentation, i.e., instance segmentation of medium-sized, mostly convex-ish and well-separated objects in single-channel 3D volumes.

Penumbria combines several choices and innovations:

- loss: boundary distance regression<br /> - architecture<br /> - 3D U-VixLSTM<br /> - Zernike Layer<br /> - SGG<br /> - combine multiple scales in SGG<br /> - sampling strategy to look for bright and dark objects.

The authors show on four nuclei segmentation benchmarks from confocal images that Penumbria outperforms CellPose-SAM (in either zero-shot or fine-tuned mode) and Stardist-3D in most cases, except for some where Stardist-3D performs better. They report results of an IoU threshold sweep to measure instance segmentation performance.

Penumbria is available on GitHub under a non-commercial license. I have not tested it yet, and therefore assume that the code is in full working condition and reproduces the reported results.

Strengths:

(1) The method may outperform state-of-the-art methods for cell segmentation as shown in three of four 3D benchmarks.

(2) The code is available.

Weaknesses:

Major

(1) Similar to the established confusion across the literature, all the authors' evaluation datasets do not label cells, but cellular nuclei. This is important to understand because the methods they compare against, CellPose-SAM and Stardist-3D, demonstrate their performance on a variety of datasets, some of which label cellular membranes instead of nuclei. The cell segmentation task is often considered harder than the nuclei segmentation task, because objects consistently touch each other, the separation may have noise-induced holes, and object shapes may be more diverse than for nuclei.

(2) The addition of U-VixLSTM, SGG, multi-scale input, Zernike layers, and distance transform regression sounds great, but a comparison to architectures or conventional losses used to train any combination is missing. Five innovations/choices combined simultaneously without an attempt to attribute.

(3) There is no clear delineation of 2D and 3D approaches. E.g. CellPose-SAM is not 3D, but sequential 2D execution with optional averaging of doing this along all axes.

(4) For the 3-fold cross-validated evaluation: It sounds like they were all trained for each benchmark independently? Did Stardist-3D and CellPose SAM start from their existing 'general' weights or from scratch (not possible with SAM, I know). Not described at all.

(5) Experiments to evaluate generalization performance are missing (train on all datasets, compare across datasets, ...).

(6) The Zernike layer optimizes only coefficients {3,4,12}; the evaluation could be described as rudimentary. Table 3 is missing cross-validation. Since mouse_skull is (a lot) different and differences for the others are minor, I would be curious how significant these results are. The following text is unclear: "This reflects how we developed these modifications in turn." How so?

(7) Training and inference: input and output block size missing, GPU memory requirements undefined, discuss block size vs. batch size. 50% overlap block-inference with feathering not compared to other overlap ratios, just "works best". Test-time augmentation 8x rotation (what are those rotations? Why 8? How much does it contribute? Compare the cost for 8xs test time augmentation against skipping "background" heuristic.)

Minor

(1) What is the incoming contrast range and bit depth?

(2) Stardist-3D's weakness is not that it requires convexity (it requires star-convexity) but that it picks one hypothesis leading to low-resolution outlines. This has been overcome by Starfinity (https://linkinghub.elsevier.com/retrieve/pii/S0092867421013398; https://github.com/multiFISH/EASI-FISH).

(3) Heatmap regression is not the same as distance regression; the manuscript does not explain what it is and uses terms interchangeably. This should be clarified. The reference for heatmap is 14; for distances, there are others, e.g. doi:10.1007/978-3-030-00934-2_36.

(4) Only one evaluation example compares against CellPose-SAM zero-shot; I would add this to all of them. The mentioned place switch would be interesting to see in a plot instead of text.

(5) "We replicated this failure on multiple machines." How does the machine matter here? Did the authors do cross-validation across different computers, instead of different random seeds? This sounds expensive!

(6) Brightness-based sampling could be achieved by augmentation?

(7) In the text "We use the following bicubic upsampling factors[...]", I think the authors mean tricubic, or cubic (because they upscale only one axis). Bicubic makes no sense, but people say this in the literature; we can do better. Why integer upscaling factors instead of exact ones? Are the authors concerned about that one incomplete border pixel?

(8) "Furthermore, it is not confined to Linux-based environments such as Segmamba [32], an important consideration given that biologists often work with Windows machines."<br /> This is confusing. Is this a comment about somebody's publicly available repository? This is not relevant to evaluate the method and should be discussed separately. Does it work in WSL?

(9) Downsampling by factors >2 with bicubic interpolation sounds wrong; should the authors use averaging?

Reviewer #1 (Public review):

Summary:

The manuscript authors have used Martini 3-based CG simulations to study how S22 phosphorylation and two catalytic-pocket inhibitors, Nexturastat A and HPOB, regulate HDAC6 condensation.

In isolated IDR1 slabs, phosphorylation lowers the apparent saturation concentration without compacting single chains, and the manuscript attributes this to new contacts between the phospho-S22/D26 region and Arg/Lys-rich patches. The two ligands perturb these contacts differently. In full-length multichain systems, the C-terminal FD3 domain is the most frequent contact partner, and the ligands shift contacts from FD3-FD3 toward pocket-FD3. The manuscript proposes a two-layer mechanism by which pocket-binding ligands regulate multidomain condensates.

Strengths:

The question is well motivated by published experiments, the simulated IDR1 construct matches the experimental one, the phosphorylation contact pattern recurs across independent salt conditions, and the Discussion offers testable predictions. My main reservations are whether the full-length results are robust to the model and to sampling, and whether the evidence reaches the mechanistic and pharmacological conclusions drawn from it.

Weaknesses:

(1) The full-length conclusions rest on FD3-FD3 being the dominant domain contact. The water-interaction correction applies only to the disordered regions, so the folded domains retain standard Martini 3 behavior, which is known to overestimate protein association (e.g., Thomasen et al., J. Chem. Theory Comput. 2022). The contact maps are also normalized per bead, which favors a small domain such as FD3. Please test whether FD3-FD3 dominance survives a folded-domain correction, and show raw contact counts next to the normalized maps. Without this test, and without experimental evidence that this domain self-associates, frame the FD3 result as a model prediction.

(2) The ligand-treated IDR1 slabs are single trajectories with no statistical uncertainty on the saturation concentrations or on the contact-difference maps. The full-length systems have three replicates; contact numbers are still rising at the end of several trajectories (Figure S9), and most differences between Nexturastat A and HPOB overlap within error. The wild-type controls also reverse the ligand ordering (Figs. S12, S14), which suggests that trajectory-to-trajectory variation may drive the domain-level differences. Please add independent replicas for the ligand comparisons, show convergence over consecutive time blocks, and report uncertainties on the difference maps. Claims should then be limited to the differences that are resolved.

(3) The Discussion presents the simulations as explaining why Nexturastat A suppresses HDAC6 condensation more strongly than HPOB. However, every full-length system assembles at a high protein concentration, and total contacts and morphologies are similar across conditions, so the simulations do not show suppression. The IDR-level and domain-level mechanisms are studied in separate systems, and ligand distribution and IDR1 contacts are not analyzed in the full-length assemblies, so the coupling of the two layers named in the title is not tested. Please add an analysis that bears on condensation propensity and on this coupling, or recast "explains" as "is consistent with" and revise the title and abstract accordingly.

(4) For phosphorylation, the IDR1 fragment is strongly basic, so a simple reduction of net charge could lower the saturation concentration without a position-specific contact node. The phosphoserine charge state used is also lower than expected at neutral pH. Moving the same charge to a distal serine, and testing the fully charged phosphoserine, would distinguish these readings. For the ligands, the coarse-grained models show only weak pocket engagement, lack a non-pocket control, have unvalidated nonbonded parameters, and are simulated at millimolar concentrations. The ligand-IDR1 mechanism could therefore reflect nonspecific association. Please add a non-pocket surface control, validate the ligand parameters, and relate the simulated concentrations to those of the motivating experiments.

Reviewer #2 (Public review):

Summary:

The authors investigated the phosphorylation- and ligand-dependent regulation of HDAC6 condensates using explicit-solvent coarse-grained simulations. They found these regulations can be attributed to the reorganization of the interaction networks between multiple domains within the condensate.

Strengths:

Large-scale condensate simulations with multiple domains using explicit-solvent models are nontrivial, impressive, and provide a useful example of what can currently be studied using such simulation models.

Comparison between simulations with/without ligand and with/without phosphorylation at different salt concentrations provides a comprehensive framework for understanding conditional residue- and domain-level condensate organization.

The simulation results are mostly consistent with previous experimental observations and offer potential mechanistic understandings that extend those findings.

The proposed FD3-centered interaction network for phosphorylation- and ligand-dependent regulations is a novel hypothesis.

The study generates a few experimentally testable predictions regarding the IDR- and FD3-mediated interactions.

Weaknesses:

When going through the manuscript, especially the result section, I sometimes found it challenging to distinguish what has already been reported experimentally (mostly from Lu et al., Nature Cancer) from what is newly learned from the simulations. I do appreciate that the authors mentioned which results reproduce experimental trends; however, this is often after all simulations. It may help if each subsection first briefly states the known experimental observation and then explains the specific question addressed by or new mechanisms learned by the simulation. For instance, experiments have shown that phosphorylation enhanced and ligand suppressed phase separation.

The authors directly used Automartini to generate the ligand parameters and then checked the contact fraction between the ligand and the pocket. Such analysis only tells whether the ligand visits the pocket but does not test either specificity or binding affinity, and therefore does not support the claim of ligand pocket recognition. The simulation concentration is also in the millimolar regime, probably much higher than the experimental range, so it's not surprising to see ~10% to 20% contact fraction. Considering that no native interactions are used to restrain the ligand-pocket interactions, I suspect the ligand might also have similar contacts to the other regions of HDAC. The authors might want to be careful about their discussions.

The claim regarding the IDR dimension might be problematic. It's still an open question whether a coarse-grained model, or even current all-atom force fields, can reliably resolve the effect of a single phosphorylation on IDR dimensions. I agree that all current results, including the error estimate, support that Rg do not change that much, but the authors might still want to be careful about such claim considering such small perturbation in the sequence.

The proposed electrostatic rewiring is based on the difference between the contact maps of WT and phosphorylation variant. It looks like the difference is relatively small to the contact probabilities. There is also no error estimation or pattern validation from multiple simulations. The authors might want to quantify the uncertainties of such patch-level relative changes by either checking some independent simulations or time-block variations.

A similar comment applies to the claims on the charged-contact reorganization mechanism of two small inhibitors on LLLPS. Error estimates should be provided for these contacts when comparing different variant. In cases when errors are large (e.g. contact number with errors reported in Fig. 4K to N), statistical analysis (p-values) is needed to show the significance of the results.

Regarding the proposed "phospho-S22-centered" contact network, I had some difficulty recognizing the specific regions discussed in Figures 2 and 3. It might be helpful to mark these regions directly on the contact maps. The authors may also wish to consider whether "S22-centered" is the most accurate description, or whether the observed changes are better described as involving a broader segment spanning several residues around S22. And since phosphorylation is introduced at S22, observing changes near S22 is not unexpected and may not be sufficient to establish phospho-S22-centered network.

Within the last result section, the authors argued that FD3 plays an important role in both phosphorylation- and ligand-regulated HDAC assembly. However, only contact-based analysis instead of saturation concentration was presented. I understand the substantial challenge of obtaining converged saturation concentration for such system with multiple domains, if so, the authors need to discuss such caveats.

Though direct experimental evidence of such FD3-centered interaction network does not exist, the experimental paper did provide measurements for a couple domain-deletion constructs, including the deletion of the FD3 (BUZ) region. This might be worth discussing, considering the manuscript focuses on the role of FD3 region. In particular, deletion of the BUZ region did not appear to affect LLPS. This does not necessarily exclude a role for FD3 in phosphorylation- or ligand-dependent regulation. However, it may complicate the description of FD3 as the center of the condensate network. The authors might want to discuss how their model can be reconciled with these domain-deletion results and consider their corresponding conclusion.

Finally, the authors describe their mechanism as coupled networks. They might want to clarify the coupling they meant. If this refers to the coupling between different regions (e.g. S22 and FD3) or domains, they might want to consider more quantitive analysis, for instance by conditional/correlated contacts between domains. Changes in contact patterns at different conditions do not necessarily show the coupling between domains.

Reviewer #3 (Public review):

Summary:

In this work, the authors probe the combined role of phosphorylation of an intrinsically disordered region (IDR) and domain pocket interactions with small molecules on the assembly of a multidomain protein HDAC6 using molecular simulations. Their find that IDR phosphorylation and ligand interactions with domain pockets can together reshaped in the interaction networks; thereby, expanding mechanistic understanding of multidomain protein assembly in the context of phase separation beyond an IDR centric grammar. The work is supported by extensive simulations featuring several controls and analysis of the underlying interaction networks.

Strengths:

(1) They find an important role of phosphorylation and ligand binding in shaping multidomain protein assembly.

(2) They demonstrate that even if IDR:IDR interactions are important in isolated IDR systems, folded domain-folded domain interactions can dominate in the full-length protein. Furthermore, ligands can significantly perturb the interaction landscape, e.g., by redirecting folded domain-folded domain interactions to domain pocket ones.

(3) They also show that different ligands can yield differing impact on the interaction networks by both competing with and compensating interactions to varying degrees. This is demonstrated for two ligands (Nexturastat A and HPOB).

(4) They probe both the IDRs in isolation (including both the phosphorylated and unphosphorylated versions) and condensates formed via these IDRs. They also characterize assemblies of the full length proteins (with and without phosphorylation) in presence and absence of the ligands. The combined simulations, in general, support the key conclusions of the paper.

Weaknesses:

(1) There are areas where statistical tests can improve the quantitative presentation of the work. Specifically, the difference in the IDR ensembles for the isolated chains should be assessed for statistical significance.

(2) There appears to be considerable finite-size effects in some of the slab simulations that may affect the conclusions. In particular, the chains along the long axis appear to be interacting across the periodic boundary. This can happen if the slab long axis is not long enough/if the ratio of dilute phase to dense phase is not large enough.

(3) Some decisions in the simulation conditions require further justification/explanation. More specifically, the concentrations of small molecules used, as well as the decision to conduct simulations at 295 K, should be adequately justified.

(4) Given the size of the full-length protein, it is understandable that the full dense phase is not probed for the full-length protein. However, it would be useful to comment on how the conclusions may change in the context of the full length. For instance, there is no real interface that the small molecules need to diffuse across and so discussions on the role of partitioning in the paper should be better contextualized in light of this.

Reviewer #1 (Public review):

This manuscript describes a multi-modal study of associative learning and memory in humans that combines scalp EEG, pupillometry and behavioral analysis to explore the construct of mnemonic prediction errors (MPEs), in terms of their relationship to attention and cognitive control. Across two pooled studies, participants performed associative memory tasks in which they learned the relationship between a cue word (action verb) and subsequent picture (animate or inanimate) with a strong vs. weak (4 or 1 repetitions) encoding manipulation. At test, participants were encouraged to generate a prediction following the cue word to determine whether the subsequently presented picture was a match or mismatch. The timecourse of pupillary responses during match decisions were decomposed using temporal principal components analysis, which identified 6 distinct and overlapping processes. Some of the components (PC3/PC4) exhibited sensitivity to both the strength and mismatch conditions, as well as behavior (both RT and accuracy) and retrieval success on the subsequent trial. Furthermore, relationships were also observed between pupillary responses (specifically for PC4) and both frontal theta and posterior alpha power measures obtained from scalp EEG in Experiment 2, as well as for frontal theta and subsequent learning from mismatch stimuli (assessed using subsequent memory findings from a surprise recognition test). The authors suggest the findings indicate that MPEs elicit changes in attention, arousal and cognitive control which impact subsequent learning.

Strengths:

This manuscript has many strengths, including a clever study design, thoughtful integration of multiple neurocognitive measures, and a set of rigorous and technically sophisticated analyses, which reveal a large set of relationships among the measures and behavior. The findings demonstrating brain/physiology-behavior relationships are particularly important, in that they point to potential functional consequences of MPEs.\

Reviewer #2 (Public review):

Summary:

The authors studied cognitive control and attention in response to mnemonic prediction errors (MPEs): situations in which the external reality violates internal memory-based predictions. The behavioral task first established strong versus weak predictions, and then either confirmed or violated these predictions. The authors examined markers of cognitive control (frontal theta) and attention (posterior alpha suppression, pupil response) while strong and weak predictions were confirmed or violated. They found increased cognitive control (frontal theta) for strong MPEs, which correlated with subsequent memory. Markers of attention (alpha suppression, pupil response) also accompanied strong MPEs but did not correlate with subsequent memory. Pupil response was investigated using an interesting approach that decomposes the response into different components, finding that different components respond earlier or later and show different correlations with MPEs and their strength. The authors also investigated how EEG, reaction time, and pupil responses correlated with one another, providing further insight into the mechanism underlying the response to MPEs. Together, the study points toward multiple control and attention mechanisms involved in MPE response and memory.

Strengths:

The study has a clear behavioral paradigm with multiple measures - behavioral, EEG, and pupillometry that offer an investigation into different aspects of MPE response and memory.

The study is also very comprehensive in looking at multiple phases in processing MPEs: the prediction phase (prior to the violation), the response to MPEs, and subsequent memory of MPEs, all within one study. Specifically, the link between neural mechanisms and subsequent memory is a major advancement, as most prior studies did not include this component. Mechanisms underlying subsequent memory of MPEs are theoretically important, as a primary function of MPEs is to promote learning and memory. As the authors mention, the different neural and pupillary signals are not robustly correlated, suggesting multiple mechanisms underlying MPE detections, which is interesting, offers avenues for future research, and can facilitate a better theory of how MPEs are processed in the brain. Finally, the decomposition of pupil response into different components and their correlation with behavior (RT during match/MPE detection) is interesting.

Reviewer #1 (Public review):

Summary:

The authors aimed to re-analyse two fMRI datasets of studies investigating the effect of cognitive emotional regulation on amygdala response during the viewing of negative images, in order to assess whether such effects might have been missed in previous reports of the results of these studies. In order to accommodate potential non-typical response profiles in the amygdala, they used a modelling approach that is agnostic about the shape of the BOLD response (finite impulse response modelling). Furthermore, the authors sought to differentiate between amygdala subregions using i) two previously published probabilistic atlases of amygdala subnuclei; and ii) a data-driven analysis focusing on temporal response profiles, which identified four clusters that mostly overlapped with anatomical parcellations. The analyses confirmed their previous results insofar as they did not find any impact of emotional regulation on the amygdala response in any subregion. However, their approach revealed differences in temporal response profiles between amygdala subregions: the centromedial amygdala showed sustained activation extending into the post-stimulus rating period, whereas laterobasal and superficial subregions peaked earlier during stimulus presentation. Overall, this study helps to clarify whether cognitive emotional regulation during negative image viewing alters amygdala response, and demonstrates the value of flexible response modelling to differentiate between functional subregions of an important brain structure.

Strengths:

The strengths of this study lie in the amount of data used (a combined N of 358 participants is rather high), the flexibility of the modelling approach (FIR), the exploratory nature of the data-driven clustering based on temporal response profiles, and clarity of the text and of the findings. One weakness would be the fact that no fMRI data acquired at higher field strengths were used for the aim of differentiating responses of amygdala subunits.

In my opinion, the authors achieved their aims of re-analysing these datasets with complementary methods, and helped to discover new aspects of the BOLD response in the amygdala during emotional regulation. The results support their conclusions.

This work is likely to stimulate discussion of the response of amygdala subnuclei during emotional regulation, and might encourage researchers to resort to more flexible analysis methods by demonstrating the information gain achieved with the FIR approach.

Weaknesses:

There are 7T studies of the amygdala response that have looked at differences in BOLD response across subnuclei. While I don't know of any that have investigated emotional regulation, I think these studies should nevertheless be mentioned and discussed in the Discussion, at least to compare the differences observed across subnuclei.

Reviewer #2 (Public review):

Summary:

In this paper, Bo et al. study the spatiotemporal organization of BOLD responses in the amygdala. They apply FIR modelling to a large sample (two cohorts tested at the same site and scanner, totalling >350 individuals) who completed a negative/neutral picture viewing and cognitive reappraisal task. Averaging voxelwise BOLD responses across two distinct probabilistic atlases of the amygdala, the authors found that a corresponding centromedial region showed sustained activation to negative stimuli beyond the stimulus period. Laterobasal and superficial subregions peaked earlier, within the stimulus presentation period. In all cases, reappraisal did not change these profiles. Lateralization effects (left-side dominance) were found in the CM region at later time points, and to a lesser extent in the superficial nucleus area at earlier time points. Data-driven clustering of voxelwise time courses could partly recover findings from probabilistic atlases, but nonetheless showed partial decoupling of anatomical and functional boundaries in the amygdala.

Strengths:

This is a well-written paper with a clear objective addressed by sound methods. The authors set out to address two main questions: (1) "do amygdala subregions exhibit distinct temporal dynamics in response to negative emotional stimuli?" and (2) "does cognitive reappraisal differentially modulate these temporal profiles across subregions?" Regarding question 1, FIR modelling results indicate strong differentiation of the centromedial region of the amygdala from other subdivisions, with strong and late responses to presented negative stimuli. On question 2, cognitive reappraisal does not seem to play a major role here, although I raise a question on this in the next section. Overall, all presented conclusions are supported by study findings. I would add that lateralization effects are not mentioned in the main objectives/questions of the paper, but this analysis represents a large section of the results that may warrant mention in the introduction as well.

Weaknesses:

(1) An important concern when looking at mesiotemporal regions such as the amygdala is signal-to-noise. Yet, this challenge in analyzing data from the amygdala was not addressed here but represents a potential confound if SNR varies within the amygdala along its major subdivisions.

(2) The authors analyze BOLD evoked response time courses, but I did not find a GLM analysis showing that the task reliably engaged the amygdala, either when analyzed with a canonical HRF or with the FIR model used here. We can see from Figure 2 that the task may not engage the entire amygdala (e.g. LB/LA subregions seem to show lower amplitude evoked-responses), yet the authors focus equally on time courses of subregions engaged and not engaged in the task. As such, differences observed between subregions may reflect different underlying processes (e.g. different processes of engagement in the task, or high/low engagement).

(3) The study uses two different probabilistic atlases to parse BOLD response time courses in the amygdala. However, methodological details on the processing of the atlas data are missing from the text. For example, it is unclear if the subregions were thresholded or overlap in any way, which would affect the strength of detected effects if there is substantial overlap between areas.

(4) The authors found no effect of reappraisal on BOLD response time courses. However, if I understand correctly, not all participants showed successful reappraisal according to their behavioural ratings (lines 125-126: "Eighty-one percent of participants showed a regulation effect in the same direction as the group-level effect"). Were these participants excluded from the reappraisal analysis on evoked response time courses? This is currently unclear, but holds significance in reliably answering question 2.

Reviewer #1 (Public review):

Summary:

Wang et al. report that changes in the levels of canonical Wnt signaling in CNS ECs modulate protein expression levels of VEGFR2 and VEGFR1. An increase in Wnt/beta-catenin signaling results in a decrease in VEGFR2 and an increase in the decoy receptor VEGFR1; conversely, reduction of Wnt signaling leads to the opposite changes in VEGF receptors in brain CVOs (less clear in the retina). Next to the solid quantitative immunostaining of VEGFR2 and VEGFR1 in multiple CNS regions using genetic mosaics and loss-of-function mouse mutants, the authors employ HEK293T cells to investigate the effect of activation of Wnt/beta-catenin signaling on multiple RTK signaling systems and on the level of overexpressed VEGFR2. The principal conclusions are that Wnt/beta-catenin regulates VEGF signaling. Two distinct levels of regulation are reported: one acts in vivo on receptor protein expression levels, the other acts in 293T cells, and the precise mechanism remains to be identified.

Strengths:

Strengths of the study include the use of genetic mosaics that allow for quantification of immuno-staining intensity with an internal reference and the significance of understanding the interplay of beta-catenin-dependent and VEGF pathways.

There are also some weaknesses noted:

(1) Experiments to restore the VEGFR2/VEGFR1 ratio in vivo, or to modulate VEGF signaling in vivo, and assess to what extent Wnt/beta-catenin LOF phenotypes can be restored by modulation of VEGF signaling have not been conducted at this point. In addition, it remains to be determined to what degree an experimental recreation of the aberrant VEGFR2/VEGFR1 ratio is sufficient to recreate (partially) some of the phenotypes observed with loss of Wnt/beta-catenin signaling in ECs.

(2) It would be useful to consider and discuss other essential components of the VEGF signaling system, especially Neuropilins. Wang et al. (2012, Figure 2, PMID: 23217714) reported that CNS ECs with loss of Norrin signaling gain Sema3F binding while not displaying VEGF-B binding sites, suggesting changes in VEGF/semaphorin co-receptor biology.

(3) Martowicz et al. (2019) PMID: 31533473  also investigated the influence of Wnt/beta-catenin signaling in CNS ECs on VEGFR2 and VEGFR3 expression and reported findings regarding VEGFR2 regulation that appear to differ from the present study. This should be discussed.

(4) Norrin/beta-catenin and Wnt/beta-catenin signaling have a critical role in CNS angiogenesis, and Wnt surrogates counteract neovascularization in the oxygen-induced retinopathy model. These findings highlight context-dependent roles of Wnt/beta-catenin signaling in normal and pathological ECs. How the modulation of VEGFR2/VEGFR1 may influence developmental and pathological angiogenesis could be discussed.

(5) When looking up the publicly available scRNA-seq datasets from Heng et al. (2019, PMID: 30988181) from Norrin KO mice, it appears that there is transcriptional regulation of VEGFR1/VEGFR2 consistent with the protein regulation reported here. If transcriptional regulation is important, CMV-driven VEGFR2 expression in Fig.5 supplement 2 may not model the regulatory mechanisms observed in vivo. Does CHIR99021 modulate VEGFR2/VEGFR1 transcripts and proteins in HRMVECs?

Reviewer #2 (Public review):

The manuscript by Wang, Nathans, and colleagues presents a compelling investigation into the regulatory crosstalk between Wnt/beta-catenin and VEGF signaling within central nervous system (CNS) endothelial cells. Overall, it is a very solid paper from a very respected research lab. The use of in vivo genetic mosaics to directly compare endothelial cells (ECs) with differing beta-catenin states within the same tissue is a particularly elegant approach to mapping receptor dynamics.

Major Comments:

(1) Distinguishing Receptor Abundance from Functional Signaling:

The study relies heavily on immunohistochemistry to assess total VEGFR1 and VEGFR2 levels, inferring that changes in receptor abundance directly equate to altered VEGF signaling. Because immunofluorescence does not establish plasma membrane localization, receptor phosphorylation, or downstream pathway activation, the definitive conclusion that beta-catenin "acts at the receptor level to reduce VEGF signaling" is currently overstated.

Recommendation: The authors should tone down the functional claims throughout the text (e.g., state that the receptor changes are "predicted to reduce VEGF signaling") or provide direct functional readouts of VEGFR2 activation in vivo, such as phospho-VEGFR2, phospho-PLCγ, ERK, or AKT.

(2) Limitations of the In Vitro HEK293T Model:

The HEK293T STF reporter system is utilized to argue for a "post-receptor physiological suppression" of VEGF signaling. While experimentally practical, this non-endothelial system does not definitively establish a physiological mechanism for CNS ECs. Furthermore, NFAT-luciferase is not uniquely specific to VEGFR2 and can be activated by broader calcium/calcineurin pathways. The authors also show that high Wnt1 expression reduces total VEGFR2 protein in these cells, but only at plasmid concentrations much higher than those required to suppress the VEGFR2/NFAT reporter.

Recommendation: Explicitly decouple the in vitro observations from the physiological in vivo claims. Remove the term "physiological" unless you validate post-receptor suppression in a primary endothelial system under endogenous signaling conditions.

(3) Regional Heterogeneity (Brain vs. Retina):

The retinal vascular mosaic data reveal that while VEGFR1 is reduced in BRB- ECs, VEGFR2 shows no obvious difference. The authors correctly acknowledge that Müller glial VEGFR2 expression complicates endothelial quantification, rendering Figure 4C a negative result with uncertain sensitivity. Consequently, the broad generalization that an "increase in Wnt/beta-catenin signaling produces an increase in VEGFR1 levels and a decrease in VEGFR2 levels" across all CNS ECs is not entirely accurate.

Recommendation: Embrace this biological nuance. Revise the generalized claims to reflect that beta-catenin regulates VEGFR1 consistently across the brain and retina, but VEGFR2 regulation appears context-dependent and is not clearly demonstrated in the retina. To resolve the Müller glia interference, consider orthogonal approaches to isolate the EC signal, such as EC-specific RNAscope or flow cytometry on FACS-sorted ECs.

(4) Statistical Rigor and Experimental Units:

The figure legends (e.g., Figure 1) explicitly state that data points represent the mean values from single confocal images. If multiple images were obtained from the same animal, treating them as independent units. Furthermore, the authors utilized unpaired statistics (Wilcoxon rank-sum) to compare BBB+ and BBB- ECs within the same mosaic tissue sections.

Recommendation: Reanalyze the data using the animal as the primary biological replicate if such data are available (averaging all image measurements within each animal). For mosaic comparisons within the same tissue image/animal, utilize paired statistical tests (e.g., paired t-test or paired Wilcoxon signed-rank test). Figure legends should clearly report the exact N (animals) and n (images/cells), the specific statistical tests used, and confidence intervals.

Reviewer #3 (Public review):

Summary:

The manuscript by Wang et al. describes the identification of a novel mechanism by which the canonical Wnt/beta-catenin pathway could regulate endothelial permeability in the central nervous system (CNS). Specifically, they show that in circumventricular organs (CVOs), in which the blood-brain barrier (BBB) is not established in vessels and endothelial cells are highly permeable, the previously reported low levels of Wnt/beta-catenin coincide with high levels of the vascular endothelial growth factor receptor 2 (VEGFR2, Flk-1), whereas the decoy receptor VEGFR1 (flt-1) is expressed at low levels. In order to test the hypothesis in vivo that the Wnt/beta-catenin pathway controls VEGF signaling in CNS vessels by regulating VEGF receptors, the authors analyzed mosaic cerebellar vessels of mice deficient for the Wnt receptor frizzled 4 (Fzd4), showing that BBB+ (normal condition) vessels show low VEGFR2 and high VEGFR1, whereas BBB- (Fzd4ko) vessels show high VEGFR2 and low VEGFR1. Similarly, although not as conclusively due to strong background from Müller cells, these effects were also visible in the retina of these mice. Conversely, dominant genetic activation of beta-catenin signaling in endothelial cells in vivo resulted in upregulation of VEGFR1 and downregulation of VEGFR2 in vessels of the CVOs as well as of the choroid plexus.

In order to better understand the direct relevance of Wnt/beta-catenin signaling for this regulatory theme, the authors activated the pathway in HEK293 cells, stably harboring the Super-Top-FLASH reporter construct in the presence of VEGFR2 and VEGF. Moreover, by transfecting Wnt1 into HEK293 cells, the authors analysed the effect of TGFbeta, EGF, and FGF signaling. Together, these experiments showed that Wnt/beta-catenin signaling potently suppressed VEGF signaling at low concentrations of Wnt1 transfection, whereas VEGFR2 suppression was only visible at relatively high concentrations. Also, the other pathways were suppressed, although to a lower extent.

In conclusion, the authors suggest a mechanism of VEGF signaling suppression by Wnt/beta-catenin 1) at the post-receptor level of VEGF receptors and 2) at the transcriptional level of VEGFR1 and VEGFR2, independent of VEGF signaling suppression.

Strengths:

(1) The present manuscript provides interesting additional information on top of the published work on the mechanistic function of vascular permeability control by Wnt/beta-catenin, specifically by the highlighted interaction with the VEGF pathway and the opposed regulation of the two VEGF receptors VEGFR1 and VEGFR2.

(2) They have used state-of-the-art animal models, high-resolution imaging, and appropriate in vitro analysis.

(3) This finding has potentially strong implications for future therapeutic strategies, aiming at Wnt/beta-catenin activation in various diseases of the CNS in which vascular repair is desired.

Weaknesses:

A detailed analysis of the post-receptor and transcriptional mechanisms remains largely unexplored and needs to be explored in the future.

Reviewer #1 (Public Review):

Summary:

In this paper, Li and colleagues have found mircoRNAs that affect levels of metamorphosis-regulating genes that can also affect levels of sesquiterpenoids (juvenile hormone and related compounds) and ecdysteriods, which regulate the timing and stages of insects, respectively. They first compared the transcriptomes of Drosophila at the third larval instar and at the white pre-pupa stage. They found thousands of differences in gene transcript levels between males and females, and between the two different stages. Among those genes that were differentially regulated they saw that genes involved in insect hormone biosynthesis were disproportionately represented. Many of the differentially regulated genes were involved in the insect hormone biosynthesis pathway and ascorbate and alderete metabolism. MicroRNAs were also differentially expressed during metamorphosis and were separately identified. The authors then considered genes and whether the differentially expressed microRNAs might regulate transcripts known to be involved in sesquiterpenoid production. In silico analysis of microRNAs predicted a list of 17 microRNAs that can regulate transcripts of sesquiterpenoid biosynthesis genes. The authors then used an in vitro luciferase assay to validate the binding and downregulation of 10 of the microRNAs to genes involved with sesquiterpenoid production in S2 cells.

Li and colleagues then focus on two genes they found were bound by microRNAs that have established roles in metamorphosis. The microRNAs miR-34 and miR-277 bind transcripts of two protein-coding genes that regulate metamorphosis Kr-h1, which encodes a transcription factor that is a JH-inducible transcription factor, and Allatostatin C Receptor 1, (AstC-R1), a G-protein coupled receptor that regulates the corpora allatum, the gland that produces sesquiterpenoids. Using a LAMP assay, one of the microRNAs, miR-277 was shown to bind to both AstC-R1 and Kr-h1 in in vivo whole-animal extracts. There is no mention of binding between either protein-coding transcript and the miR-34 microRNA. Temporal expression of all four transcripts shows that their abundance is anti-correlated; stages of high miR-34 or miR-277 expression correlate with low AstC-R1 or Kr-h1 expression. Homozygous deletions of both mircroRNAs result in 23% lethality, five days after adult eclosion. The authors also generated specific mutants in miR-34 or miR-277 and find differences in the expression of AstC-R1 and Kr-h1 and sex-specific differences in both sesquiterpenoids and ecdysteroids in the knock-out lines. If there were phenotypes associated with the specific knock-outs, those were not mentioned. Next, the authors examined the transcriptomes of the miR-3277 and miR-34 mutants and found several other GO-terms enriched among the differentially expressed genes. However, the sesquiterpenoid pathway and ascorbate and alderete metabolism are not listed.

Strengths:

This is an interesting manuscript that could make an important contribution to our understanding of the roles of micro RNAs at metamorphosis, and potentially of how sex-specific differences arise during metamorphosis. Strengths of the paper include the functional validation of microRNA binding, in vitro and in vivo-, as well as the characterization of sesquiterpenoid and ecdysteroid titers. The authors have also used CRISPR to generate specific knock-outs of miR-34 and miR-277. The transcriptomes will be a resource for future work to mine for differences in gene expression during metamorphosis.

Weaknesses:

(1) Spatial Expression of miR-34 and miR-277. If miR-34 and miR-277 regulate AstC-R1 and Kr-h1, then they must be expressed in the same cells. Although the authors show that the microRNAs do bind to the transcripts of AstC-R1 and Kr-h1 in S2 cells, and miR-277 binds AstC-R1 and Kr-h1 in vivo whole-animal homogenates, we do not know if the microRNAs are ever in the cells where AstC-R1 or Kr-h1 are expressed. AstC-R1 is only expressed in a few cells in the brain, so it is not at all certain that it is co-expressed with either microRNA. The creation of enhancer lines or in situ hybridization in Drosophila is straightforward and would sort this out.

(2) Phenotypes. Although a double deletion was used and specific knock-outs of both miR-34 and miR-277 were generated, the analysis of the mutants is very superficial. For the homozygous deletion of both microRNAs miR-34 and miR-277, only a decrease in survivorship was observed a full six days after adult eclosion - after the end of metamorphosis. No phenotype for either miR-34KO or miR-277-KO was given. The authors cite the work of others who have found specific phenotypes after manipulation of sesquiterpenoids or ecdysteroids, like Riddiford and Ashburner, but do not use any of these many studies to help them characterize the phenotype. If the loss of miR-34 and miR-277 affects so many pathways (including MAPK signaling, TGF-beta signaling, FoxO signaling, and Wnt signaling), as well as global titers of metamorphic hormones, then there shouldn't there be something different in the development to discuss?

(3) I think the reliance on GO term enrichment is getting in the way of biology. For instance, I would not describe Kr-h1 as a sesquiterpenoid biosynthesis pathway gene. Yet the authors say they were motivated to examine microRNA regulation of Kr-h1 because they saw differences in levels of the sesquiterpenoid biosynthesis pathway between WL3 and WPP, a period which also saw differences in expression of some microRNAs. I understand that Kr-h1 expression is regulated by JH, a sesquiterpenoid, but it is not directly involved with JH production, so relying on GO term enrichment has made the decision to focus on Kr-h1 feel arbitrary.

(4) The transcriptomes of miR-34 and miR-277 should have revealed genes encoding members of the sesquiterpenoid biosynthesis pathway as well as AstC-R1 and Kr-h1, but neither was mentioned. The functional tests of miR-34 and miR-277 were performed because they were shown to affect the levels of expression of genes in the sesquiterpenoid biosynthesis pathway. Figure 2 shows a significant decrease in AstC-R1 and Kr-h1 transcripts after the loss of miR-34 and miR-277. However, the results do not mention either (Lines 250-264). Instead, there is a list of 10 different GO terms (like arginine and proline metabolism or fatty acid degradation) that were enriched in miR-34 and miR-277 transcriptomes. If any of those ten types have any relationship to Kr-h1, AstC-R1, or metamorphosis, that has not been explained.

(5) Not enough care was taken in describing the stages. The methods describe wandering larvae (WL3) and white pre-pupa (WPP) for the transcriptomes, but in the text, different terms are used, like "larva", "pupa" and "L3 larvae instars" "early pupae" "late L3". Also, it seems like the small RNA libraries for sequencing were taken from "L3 larvae", but the stage of the L3 larvae was not mentioned. Staging is important, especially during metamorphosis, since differences in expression are expected to exist between different stages of L3, between early vs late wandering, and between WPP and early pupal stages.

Reviewer #2 (Public Review):

Summary:

This study proposes that the microRNA cluster miR-277/34 controls the generation of sexual dimorphism in Drosophila melanogaster during metamorphosis by acting on specific hormonal and developmental gene pathways.

Strengths:

Using a combination of mRNA and small RNA sequencing together with genome-wide in silico and in vitro analyses the authors identified a microRNA cluster that may be involved in metamorphosis and the generation of sexual dimorphism in Drosophila melanogaster.

Weaknesses:

Biological validation of the identified sexually dimorphic genes and a detailed understanding of how the microRNA cluster miR-277/34 might be involved in the regulation of sesquiterpenoids are needed.

Major suggestions:

(1) If AstC-R1 and Kr-h1 are targets of the miR-277/34 cluster and cause their downregulation, it is not clear why there would also be a decrease in the levels of these genes in the miR-277/34 mutants. This would suggest that the mechanism is not straightforward and that further epistatic experiments should be carried out in order to clarify this issue.

(2) The changes in the expression levels of AstC-R1 in pupae of miR-277-KO and mir-34-KO flies must be accompanied by photos of the respective larvae and pupae, as well as an analysis of the larvae-pupa transition on the mutants by gender.

(3) Biological validation of the identified sexually dimorphic genes in vivo will be necessary for the support of this work.

Reviewer #3 (Public Review):

Summary:

The authors show convincingly the complexity of gene up- and down-regulation at the outset of metamorphosis and identify substantial differences between the two sexes, even at this early time in development. The complexity of microRNA expression and the difference between the sexes are also nicely laid out. The functional significance of these differences, though, is harder to establish. The authors have focused on the roles of two families of developmental hormones, the ecdysteroids, and the juvenile hormones. The emergence of sex-specific differentiation of organs during metamorphosis is clearly downstream of the action of ecdysteroids and/or JH, but there is no evidence that the presence or lack of these hormones has any effect on the sexual identity of organ systems - i.e., that manipulations of JH or ecdysteroid result in either the masculinization or feminization of individuals or their organs. The precedence for the linkage of these hormones to sex determination is the 2002, Belgacem & Martin study, which describes the effects of JH on fly locomotion. These authors show that the number of stop/start bouts is sexually dimorphic, and removal of JH in males shifts their frequency into the female range while giving treated males exogenous JH moves it back. While this is referred to as a "feminization" of male behavior, this quantitative shift in frequency is not as compelling as would be a qualitative shift -- for example, the removal of JH causing males to show egg-laying behavior (a result that has never been seen). Also, these effects are in a fully mature system, rather than at the early metamorphic time examined in the present paper. In driving and coordination metamorphosis, JH and ecdysteroids are intimately involved in sexual differentiation, but I know of no compelling evidence that they play a role in sex determination.

While the summary of the effects or removal of specific microRNAs on the components of the biosynthetic pathway for the JHs and ecdysteroids (Figure 2E ,F) is quite compelling, I am concerned about the effects of the removal of mir-277 and mir-34 on the levels of both the JHs and 20E. My concern centers around the data from the control group (w[1118] animals in Figure 2D). These data are the first report of a marked sex difference in the titer of either JH or ecdysteroid at the start of metamorphosis in Drosophila. As expected, males show a 10-20 increase in levels of JH III, JHB3, and 20E between the L3 stage and the white puparium, but, surprisingly, the levels of these hormones in female L3 larvae are equal to or greater than that seen at pupariation! These data for females run counter to over 50 years of work on the effects of ecdysteroids in Drosophila!

As far as I can gather from the paper, the L3 data were obtained using wandering larvae. This stage lasts for about 12 hours and ends with pupariation. Larvae from this period need to be used with caution for hormone studies. Levels of both JH and ecdysteroid are low as larvae leave the food but rapidly rise to their peak levels at the white puparium stage 12 hours later. To deal with the rapidly changing hormonal landscape through this period, the researchers have used physiological markers to track this progression. Initially, it was the sage of "puffing" of the giant salivary gland chromosomes, but, for bulk collection of staged larvae, larvae are fed on food containing a blue dye, and progression is tracked by the loss of blue coloring from the gut. I could not find if the authors had any criteria for selecting larvae during the wandering period. Male and female larvae grow to different sizes. Might this difference in growth be biased when larvae were selected during their wandering phase?

The other hormone-related issue is the expression of Kr-h1 during larval stages and metamorphosis (Figure 1G). Kr-h1 is the main target of JH and Kr-h1 expression is often used as a proxy for the JH titer. The authors report that peak Kr-h1 expression occurs in the L3 (when the JH titer should be lowest!) and that it drops at wandering. This pattern is counter to that reported in the literature (e.g., FlyBase, ModEncode).

Reviewer #1 (Public review):

Summary:

In the manuscript entitled "Gene function and expression profiling in yeast spores, killifish diapause embryos, and their post-dormant offspring cells" the authors analyze dormancy at three levels: functional, transcriptomic and proteomic, using Schizosaccharomyces pombe spores, diapausing killifish embryos and human dormant cancer cells as models. The authors performed a genome-wide Bar-seq screen for gene deletions in fission yeast spores and then compared changes in mRNA and protein expression in young and old and heat-stressed cells in yeast and killifish. The main conclusions of the work include that dormancy is a dynamic not static state. The authors conclude that specific biological processes, rather than particular genes, are conserved across organisms during the dormancy, and that there is a clear disconnect between the mRNA and protein kinetics and behavior, particularly for ribosomal proteins and processes related to autophagy and mitochondrial metabolism.

In general, the manuscript is well structured and written, with carefully designed figures. The authors are also generally aware of the limitations of the work. The manuscript is interesting and valuable, but some interpretations should be moderated.

Major comments:

(1) The data presented provide in general good support for majority of conclusions presented in the manuscript. However, less support is provided for the theories that: there is a universal "core expression signature" of dormancy; the mRNA/ribosome protein uncoupling reflects a specific mechanism of preparation for exiting dormancy; and the observed changes provide evidence for an epigenetic "memory" of dormancy. These elements are currently more interpretive than evidentiary. I would recommend softening the language in these places and clearly labeling them as hypothetical.

(2) The authors propose that spores and post-dormancy cells retain a memory of time spent in dormancy or stress exposure. However, sporulation is also generally expected to reset or remove accumulated damage. Please clarify whether the observed long-term effects reflect classical "memory" of the cell, persistent regulatory state, or selection of cells with different fitness (carry-over effects). I would be careful in interpreting the effects as a form of memory associated mostly with epigenetic control - the statement seems stronger than what the data directly demonstrate.

(3) Validation of a small set of top hits by independent assays would substantially strengthen the conclusions. For example, targeted qPCR and/or biochemical assays for key genes (like ribosomal and autophagy) or pathways would help confirm the most important transcriptomic and proteomic trends. Without this, the suggestion of, for example, translational regulation remains possible but unproven.

(4) Overall, the study appears reproducible, with detailed methods, biological replicates, and appropriate statistical analyses. However, reproducibility could be improved by more clearly describing the limitations of the comparisons (especially with the published datasets) and the data-processing parameters, particularly for correlation and functional enrichment analyses. Some comparative conclusions are based on data from different studies, under different conditions and often with different depths of coverage. It is not always clear to what extent interspecies comparisons are fully methodologically similar.

Significance:

This is an ambitious work that combines a genetic screen with multi-omics analyses and cross-species comparisons. The novelty is less in known roles of autophagy, mitochondria and translation, but rather in integrating them into a comparative framework across S. pombe spores, killifish diapause embryos, and dormant human cancer cells, combined with Bar-seq screening and multi-omics. Its greatest strength is its coherent, broad concept: dormant cells are not passive, and the regulated processes and functions during dormancy are evolutionarily conserved rather than the individual set of genes. The contribution of this work lies more in demonstrating process-level conservation than in identifying a single universal gene. This significantly expands the literature on dormancy, but rather in terms of a framework of biological organization rather than a single mechanism.

The weakness of the manuscript is the tendency to draw broad, sometimes overly strong mechanistic conclusions based primarily on correlational data (sometimes with poor statistical significance) and on relative, rather than absolute, expression. The lack of biochemical validation, in my opinion, lowers the impact of the paper.

Audience: This work will be of interest especially to aging and dormancy specialists and comparative biologists. It is important to note that this is not a purely technical or model-specific work, but it has the potential to impact researchers interested in homeostasis, translation and adaptation to stress.

My expertise: My expertise is mostly in aging, sporulation, cell cycle control and ribosome biogenesis.

Reviewer #2 (Public review):

Summary:

In this manuscript, Hassan et al. examine dormancy in fission yeast spores and killifish embryos in diapause. The authors first performed a genetic screen in yeast spores to identify genetic modulators of spore longevity and resilience to heat stress, finding that there is a trade-off between stress resilience and longevity. Next, the authors performed transcriptomic and proteomic profiling of yeast spores and killifish diapause embryos, comparing active and dormant states, early and late dormancy, and with and without heat stress in each model. Comparison between the two models identified a shared set of gene expression changes in dormancy. Lastly, the authors tested whether stress in dormancy is able to reshape the transcriptome or proteome following exit from dormancy, finding that heat stress altered gene expression post-dormancy in both yeast spores and killifish diapause embryos.

This study is interesting because it provides valuable transcriptomic and proteomic datasets across a large number of conditions in both yeast spores and killifish embryos. Furthermore, these datasets reveal several interesting insights about dormancy, including shared gene expression changes in dormancy across diverse organisms, a trade-off between stress resilience and longevity in yeast spores, and memory of heat stress following exit from dormancy.

This interesting manuscript would be strengthened by additional characterization of the functional consequences of these gene expression changes.

Major comments:

(1) The finding that a set of gene expression changes in dormancy is shared between yeast spores and killifish diapause embryos is very interesting and raises the question of whether the genetic determinants of stress resilience or longevity in dormant states are also shared. For instance, do any genes identified in the genetic screen as critical for resilience to heat stress in yeast spores also show a similar phenotype in killifish diapause embryos?

(2) The authors show that gene expression changes in dormancy (old vs. young spores and late vs. early diapause) are poorly correlated with aging in stationary-phase yeast cells (Figure 4E) and killifish brain (Figure 5E). The authors suggest that this poor correlation might reflect a lack of aging during dormancy. Interestingly, the authors also show that in both yeast and killifish models, both time and stress in dormancy result in gene expression changes following exit from dormancy. Are these post-dormancy differences correlated with aging in stationary-phase yeast cells and adult killifish? Additionally, could the authors compare these changes with age-related changes in different adult killifish organs?

(3) In Figures 1C, 4F, and 5F, the authors find significant correlations between two comparisons with a shared condition (e.g. 2-week unstressed spores in Figure 4F). Using the same samples in both comparisons can inflate the correlation between the two sets of fold-changes because the two comparisons are not made independently. The authors should ensure that the correlations found in these figures remain significant even when different samples are used for the shared condition in the two comparisons.

Significance:

This study is interesting because it provides a comparison between different states of dormancy and identify shared pathways. This paper should appeal to a broad audience, including aging, stress pathways, and quiescence/dormancy.

Reviewer #3 (Public review):

Summary:

In this study, the authors use several genome-wide approaches to find commonalities and differences between distinct dormancy models, including S. pombe spores, killifish diapause embryos, and human dormant cancer cells. As G0 states are ubiquitous in nature, yet still understudied, this study provides not only a clear demonstration of an evolutionarily-conserved component in G0 regulation, but also a rich resource of genomics datasets, that will be especially of interest to S. pombe and killifish researchers.

The main conclusions of the study are that: (1) there are commonalities in dormancy programs across eukaryotic evolution; (2) the uncoupling between transcriptome and translatome is more pronounced in non-dividing cells, particularly at ribosomal protein coding genes; and (3) dormant cells retain dynamic responses to stress, changing their cellular state and maintaining this difference.

Overall, the study is clearly written, provides large data resources for future research in the dormancy field, and the conclusions are supported by the presented evidence (although point 3 would require further experimental clarification, see below).

Major comments:

A key consideration when comparing transcriptomes of cycling and dormant cells is the overall RNA quantity in the cells; however, it is not made clear in the manuscript whether this overall level was compared and/or if RNA-seq used spike-in quantification. However, this will directly affect some conclusions; for example, there is a conceptual difference between a transcript upregulated in spores and a transcript that appears upregulated in spores but is in fact 'less repressed than average' (resulting in higher FC). While the overall transcript diversity as described will be not affected, this analysis can provide important context. For the highlighted example of ribosomal protein mRNAs, this scenario could be what resulted in an apparent mRNA increase but protein decrease (which would be interpreted as both mRNA stabilization and translation inhibition); if the total mRNA is much lower, then the mRNA levels may be similar (which would then be interpreted as no change in transcription nor mRNA stability, but highlight the importance of translation inhibition).

This point was more clearly described in a previous seminal study by the authors (Marguerat et al 2012), and so should be made clearer here as well. What is the overall RNA level in cycling cells compared to quiescent cells, and compared to spores? Likewise, what is the overall reduction in total protein levels? Was the overall reduction comparable to the previous study? These overall levels should at least be quantified, which is a straight-forward experiment. The current mention of this limitation (two sentences in the last paragraph of the conclusion) is not enough.

Accordingly, the term "induced" (in Fig 2 for example) may be misleading, and could be separated into truly "induced" genes and "relatively induced" genes, when normalized to absolute levels. Likewise, Fig S2A and S2I are misleading due to this effect (normalization will tend to show a similar number of up-regulated and down-regulated genes). These panels should be clarified by plotting next to the relative quantification (current panels) a comparison taking overall RNA level into account. This will very likely strongly increase the number of downregulated genes and decrease the number of upregulated genes, and the new lists can also be subjected to GO analysis.

The same issue would be important to discuss for the killifish experiment as well.

For spore offspring stress experiments, the estimated number of cell divisions after spore germination should be indicated. It appears over 20, which would confirm the authors' conclusion that an epigenetic state is induced and persists over multiple rounds of replication and underlie improved heat resistance, indeed hinting at transcriptional memory through chromatin modification. As the phenotype is tested at a population-level, it is unclear whether every spore is equally able to impart this phenotype, and for how long the stress resistance response persists. Moreover, it may be clearer to test heat resistance in log-phase cells, as in the current experimental setup cells are grown to stationary-phase before plating; however, stationary-phase cultures are more heterogenous and more heat-resistant.

Note also that using 3-fold serial dilutions (instead of more commonly used 10-fold) means that the differences shown in Fig 3M are mild. Plating duplicates (at log-phase) and imaging at several times of growth would be necessary to have a clearer view of the result.

Significance:

Overall, the study provides a proof-of-concept that dormancy programs across vastly different eukaryotes display commonalities. This is not an entirely new concept, but this is the first demonstration of it using S. pombe and turquoise killifish and will therefore be of interest to a wide audience of researchers interested in quiescence and dormancy in general. A key finding (albeit also not entirely new) is the transcriptome/proteome difference, which appears increased in dormant cells; this hints at the existence of key post-transcriptional regulatory mechanisms in dormant and G0 cells.

A current key limitation is that only relative quantifications are discussed, which can currently give a misleading idea of overall transcriptional activity in dormant cells. Another limitation is that differentially-regulated genes, proteins and GO processes are mentioned, but with relatively limited biological interpretation, making some sections of the manuscript lengthy and descriptive.

Advance: The authors provide a vast amount of datasets for fission yeast spores (transcriptome, proteome, differential viability of a mutant collection) and killifish, which will be a very useful resource for researchers in the field. The authors identified several genes and processes that are commonly differentially regulated in dormant cells across several systems, including autophagy and ribosomal protein genes, which were previously known to be required for G0.

Reviewer #4 (Public review):

Summary:

This manuscript from Hassan et al presents a comparative study of the hallmarks of dormant cells in different systems. The authors first use a bar-coded knockout set to identify genes important for persistence of fission yeast spores in the dormant state (up to 6 months) and then use RNA seq and Mass spec to examine changes in transcript and protein abundance as fission yeast spores enter and exit dormancy. They then perform a similar transcriptomic and proteomic profile of Killifish embryos in diapause. The authors note certain functional classes of genes (e.g. autophagy-related genes or ribosomal proteins) that are similarly upregulated during dormancy in both systems and show that this applies in human dormant cancer cells as well. Importantly, this pattern applies to genes broadly in these functional classes, but not necessarily to any particular gene within the class. Finally, the authors examine the effects of stress (heat shock) on the transcriptomes and proteomes of young and aged spores as well as mitotic populations germinated from those spores.

Dormancy is relatively understudied at the cellular level and this study provides a number of potentially interesting observations, in particular the authors identify common features of dormancy-related expression changes in the different systems that may be a general hallmark of dormancy. Included in this is a fascinating disconnect between transcript and protein levels of ribosomal genes. That said, the work seems to be almost three different stories, none of which is entirely complete, and which only loosely fit together: (1) the identification of dormancy mutants in fission yeast; (2) comparative 'omics of dormancy in different systems; and (3) changes induced by stress in dormant cells.

Specific comments:

There is a dissonance between the apparent upregulation of autophagy genes during dormancy in both systems and the observation that loss of autophagy genes enhance dormancy. While the authors brush this off by noting "that genes regulated in a given cellular state often do not overlap with those functionally required for that state" (an argument that undermines their whole analysis), it raises the possibility that the process signatures they report are not, in fact, functionally linked to dormancy and could be coincidental. What would make the expression analysis more convincing would-be functional data showing that at least one of the upregulated genes in one of the systems is important for dormancy.

It is not clear how the bar-coding experiment was controlled for mutants that make defective spores (e.g. poor spore walls) rather than being required for dormancy per se. As the authors note, several of the mutants with the strongest effects (shortening lifespan of the spores) have been previously identified in screens for sporulation or spore wall defects, consistent with those genes playing a specific role in proper spore assembly rather than a general function in dormancy.

It would be helpful to make the data - or at least the lists of genes identified in the screen and the up and downregulated transcripts/proteins available as supplemental information.

There are at least two different points of diapause in Killifish. It was not entirely clear which diapause was analyzed here. This should be clarified.

The data that offspring from older or heat-shocked spores are more stress resistant (Figure 4M) is not convincing. Serial dilution assays as shown are more qualitative than quantitative and an actual quantitative measure (e.g. c.f.u.'s per cell plated) would be better and would allow statistical confidence to be calculated.

Significance:

This work provides a useful overview and comparison of gene expression changes occurring during dormancy in different systems. As this is a relatively understudied area the results are likely to be of great interest to researchers in this area. The primary weakness, as is often the case for systems studies, is that it provides a 'high level' view of changes, but it is unclear whether any of the specific changes documented are functionally relevant to dormancy.

I am a cell biologist and not qualified to critically assess the quality/appropriateness of the different statistical measures used to analyze their expression data.

Reviewer #1 (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.]

The authors sought to determine how Rif1 contributes to DNA replication timing (RT), transcriptional regulation, and embryonic development using zebrafish. They generated a maternal-zygotic rif1 knockout line and examined developmental phenotypes, genome-wide replication timing profiles, RNA-seq, and nascent transcription (SLAM-seq) during early embryogenesis.

Their major findings in this manuscript are.

(1) Rif1 is not essential for zebrafish viability, unlike its partially essential role in mice.

(2) Rif1 deficiency causes defects in female sex determination, delayed epiboly, and reduced primitive erythropoiesis.

(3) Genome-wide RT is altered by Rif1, but developmental stage has a much larger influence than Rif1 itself.

(4) Rif1 is required for the proper maturation ("sharpening") of the RT program during development rather than for specific developmental RT switches.

(5) Rif1 has a much stronger effect on transcription during zygotic genome activation (ZGA) than on replication timing at these early stages.

(6) Loss of Rif1 leads to increased expression of early zygotic genes, indicating that Rif1 normally suppresses widespread transcription during ZGA.

Overall, the work proposes that Rif1 independently regulates replication timing and transcription, with these two functions becoming most prominent at different developmental stages.

The major strengths of the manuscript are as follows.

(1) the study combines multiple genome-wide approaches including whole-genome RT profiling, RNA-seq, SLAM-seq in combination with gene KO and developmental analyses.

(2) One of the strongest points is that the authors conducted the analyses at multiple developmental stages rather than a single point.

(3) The most important conclusion is that the Rif1 regulates transcription during development in a manner largely independent of its RT function, which was further strengthened by the additional data provided in the revised manuscript.

Comments on revised version:

The authors responded to my comments in a largely satisfactory manner. They have conducted additional analyses and concluded that Rif1 regulates transcription during ZGA largely independently of its classical RT function, which is an important finding.

Although authors did not examine origin firing and replication fork rate in rif1 KO cells, which I suggested in my original review, this can be saved for their future studies.

I think the revised manuscript has been improved and provides important basic information on the functions of the conserved Rif1 protein in RT and transcriptional regulation.

I have no further recommendation for additional experiments or data analyses.

Reviewer #2 (Public review):

This study by Masser et al. analyzes global replication timing and gene expression in rif-1 null zebrafish. This work is an extension of their previous report of the normal replication timing pattern during wild-type zebrafish development. The major valuable finding here is that Rif1 is not essential for viability in zebrafish, and - counter to expectation from studies in cultured cells and other species - late replication does not strongly depend on Rif1. Instead, the data suggest that Rif1 subtly sharpens replication timing pattern during normal development rather than function generally to delay replication timing. In the absence of Rif1, the normal pattern establishment is somewhat delayed. The authors also document some changes in expression during development with more genes being repressed by Rif1 than activated at some early stages.

The study and analysis are generally rigorous, and the conclusions are supported by convincing data. Given the strong link between replication timing and cell type/development, studying timing in a whole developing organism is important. The experimental approach is technically challenging, particularly the bioinformatic analysis. The scientific advance here is largely confined to documenting the timing of Rif1-affected transcription, the unanticipated effect of the rif1 deletion on replication timing and on sex determination, though the latter is not explored. The difference in timing of the transcription phenotypes and replication phenotypes suggests they may be very distinct Rif1 roles. The overall study a useful set of findings and detailed data for future work.

Loss of Rif1 did not affect viability, but it did strongly influence sex determination, resulting in a lower population of females. This effect is the strongest organismal phenotype, but the study provides no mechanistic explanation for the loss of females from the data gathered here.

Comments on revised version:

We are generally satisfied with the revised version of this manuscript.

Reviewer #1 (Public review):

Summary:

Desingu et al. show that JEV infection reduces SIRT2 expression. Upon JEV infection, 10-day old SIRT2 KO mice showed increased viral titer, more severe clinical outcomes, and reduced survival. Conversely SIRT2 overexpression reduced viral titer, clinical outcomes and improved survival. Transcriptional profiling show dysregulation of NF-KB and expression of inflammatory cytokines. Pharmacological NF-KB inhibition reduced viral titer. The authors conclude that SIRT2 is a regulator of JEV infection.

Strengths:

This paper is novel because sirtuins have been primarily studied for aging, metabolism, stem cells/regeneration. Their role in infection has not been explored until recently. Indeed, Barthez et al. showed that SIRT2 protects aged mice from SARS-CoV-2 infection (Barthez, Cell Reports 2025). Therefore, this is a timely and novel research topic. Mechanistically, the authors showed that SIRT2 suppresses the NF-KB pathway. Interesting, SIRT2 has also been shown recently to suppress other major inflammatory pathways, such as cGAS-STING (Barthez, Cell Reports 2025) and the NLRP3 inflammasome (He, Cell Metabolism 2020; Luo, Cell Reports 2019). Together, these findings support the emerging concept that SIRT2 is a master regulator of inflammation.

Comments on revised version.

The authors have addressed my comments.

Reviewer #2 (Public review):

The manuscript by Desingu et al., explores the role of SIRT2 in regulating Japanese Encephalitis Virus (JEV) replication and disease progression in rodent models. Using both an in vitro and an in vivo approach, the authors demonstrate that JEV infection leads to decreased SIRT2 expression, which they hypothesize is exploited by JEV for viral replication. To test this hypothesis, the authors utilize SIRT2 inhibition (via AGK2 or genetic knockout) and demonstrate that it leads to increased viral load and worsens clinical outcomes in JEV-infected mice. Conversely, SIRT2 overexpression via an AAV delivery system reduces viral replication and improves survival among infected mice. The study proposes a mechanism in which SIRT2 suppresses JEV-induced autophagy and inflammation by deacetylating NF-κB, thereby reducing Beclin-1 expression (an NF-κB-dependent gene) and autophagy, which the authors consider a pathway that JEV exploits for replication. Transcriptomic analysis further supports that SIRT2 deficiency leads to NF-κB-driven cytokine hyperactivation. Additionally, pharmacological inhibition of NF-κB using Bay 11 (an IKK inhibitor) results in reduced viral load and improved clinical pathology in WT and SIRT2 KO mice. Overall, the findings from Desingu et al. are generally supported by the data and suggest that targeting SIRT2 may serve as a promising therapeutic approach for JEV infection and potentially other RNA viruses that SIRT2 helps control.

Comments on revised version.

We believe the authors of Desingu et al. have adequately addressed the major concerns of each reviewer. Thus, we believe the current version of the manuscript is significantly improved, and the data more strongly support the authors' conclusions.

We would like to point out that the statistics in Figure 8 are difficult to interpret and should be improved to make them useful to the reader and strengthen the paper. Also, line 70 has an extra period that should be removed.

Reviewer #1 (Public review):

This work reports the finding of a dissociable human Mediator complex subunit, MED16, and its recruitment of transcription factors UBP1 and TFCP2 that form a trimeric complex regulating cellular gene transcription and inhibiting HIV promoter activity, thus promoting MED16-targeting inhibitors as HIV latency-reversing agents for anti-HIV therapy. In this revision, the authors provide new data indicating that MED16 action occurs in the holo-Mediator complex, not as a free form, for its functional association with UBP1 and TFCP2.

Summary:

Characterization of a dissociable Mediator subunit implicated in cellular pathways, particularly lung alveolar function, and HIV latency is conceptually interesting.

Strengths:

The strengths of this study are:

(1) Demonstration of MED16 dissociation from the core Mediator complex and formation of a subcomplex containing MED16, upstream-binding protein 1 (UBP1), and transcription factor cellular promoter 2 (TFCP2) by elegant biochemical fractionation and immunoblotting analysis.

(2) Defining nine N-terminal WD-40 repeats (WDRs) of MED16 as a Mediator-incorporating module and the C-terminal ⍺β-domain (157 amino acids) important for interaction with the UBP1-TFCP2 heterodimeric complex.

(3) Illustration of a weak hydrophobic interaction between MED16 and the Mediator core that could be disrupted by 1,6-hexanediol, but not by its 2,5-hexanediol isomer nor by high salt (500 mM NaCl) disruption.

(4) Classification of UBP1-upregulated cellular genes typically containing binding sites flanking the transcription start site (TSS) in contrast to UBP1-downregulated genes often containing a TSS-overlapping UBP1-binding site;

(5) Presenting evidence for Mediator complex-dissociated free MED16-repressed HIV promoter activity through functional association with UBP1 and showing bromodomain-containing protein 4 (BRD4) inhibitor JQ1 that potentially disrupts BRD4-inhibited HIV-1 transcription elongation could lead to reversal of HIV-1 latency.

Weaknesses:

(1) No clear demonstration that MED16-UBP1-TFCP2 indeed form a trimeric core subcomplex in regulating cellular gene transcription and HIV-1 promoter inhibition.

(2) No validation of transcriptomic datasets and pathways identified.

(3) Use of mostly artificial reporter gene constructs and non-HIV host cells (e.g., human 293T embryotic kidney cells, human HeLa cervical cancer cells, and mouse HT pancreatic cancer cells) for examining MED16/UBP1-regulated HIV transcription.

(4) Inconsistent use of 293T and HeLa cells in the characterization of dissociated MED16 interaction with UBP1 and TFCP2.

(5) In vitro transcription using immobilized DNA templates was not performed to a high standard thus failing to convincingly show MED16/UBP1-inhibited HIV-1 transcription preinitiation complex formation.

In this revision, the authors stipulate that the action of MED16-UBP1-TFCP2 is through the holo-Mediator complex, not as a free trimeric complex, since deletion of the N-terminal Mediator-incorporating module abolishes the functional effect of MED16 even though its interaction with UBP1-TFCP2 persists. The authors also show that a predicted UBP1-binding site is indeed present in the promoter region not overlapping with the TSS in each of the UBP1/MED16-upregulated respiratory gaseous exchange genes, such as surfactant protein A1 (SFTPA1), SFTPA2, SFTPB and SFTPC. To demonstrate UBP1/MED16-inhibited HIV transcription in a more biologically relevant system, the authors employ an HIV-1 latency model derived from CD4+ T cells. Additional experiments are also performed to address other issues raised by the reviewers.

Overall, the revised manuscript has been improved by addressing some of the reviewer's comments. Additional issues that came up while reading this revision are: a) The statement, "UBP1 (as known as LBP-1) and TFCP2 (as known as LSF) belong to a subfamily of the TFCP2/Grainyhead transcription factor family" (lines 63-64), is confusing and needs to be clarified. My understanding is that LBP-1 has four family members encoded by two different genes (see Yoon et al., MCB 14: 1776-1785, 1994): LBP-1a and LBP-1b are probably UBP1, and LBP-1c and LBP-1d are likely TFCP2/LSF. If this is correct, the authors should clearly indicate which specific isoforms are analyzed in their UBP1 and TFCP2 proteins and clarify some of the text descriptions seemingly contradictory to the earlier findings.

The use of mostly artificial reporter templates and transfection assays conducted mostly in 293T and HeLa cells remains concerning. It is also unclear why overexpression of MED16 only, but not MED23 or MED24, inhibits HIV promoter activity (Figure 5) if MED16 action is through the holo-Mediator complex and overexpression of MED16 may titrate out key cellular factors, thus diminishing their action through holo-Mediator. Results based on this squelching type of experiment relying on overexpression of a single component needs to be carefully interpreted.

Reviewer #2 (Public review):

Summary:

The article from Zheng et al. proposes that the Med16 subunit of Mediator can dissociate from the complex, associate with transcription factor UBP1, and contribute to activation or repression of specific sets of genes in human cells. The question is potentially interesting, and the possibility of a distinct role for Med16 in UBP1-dependent transcription could be of interest to the field. However, I have substantial concerns about the experimental design, reproducibility, and interpretation of the data. In particular, several of the central conclusions rely on single experiments, indirect assays, or perturbations that are expected to cause broader changes in Mediator structure and transcription. In my view, the current data therefore do not provide sufficient evidence to support several of the principal mechanistic conclusions of the manuscript.

Strengths:

The authors provide preliminary evidence that Med16 may exist in an altered or partially dissociated Mediator complex and may be associated with specific transcriptional effects. The use of biochemical assays, reporter assays, RNA-seq, and Med16 knockout/rescue experiments provides several potentially useful approaches to investigating this question. In particular, the Med16 knockout/rescue RNA-seq experiment described in the rebuttal is a potentially informative experiment. Making the underlying IP-MS abundance and peptide-count data available is also an improvement over the previous version.

However, important limitations of these experiments need to be addressed before the proposed mechanism can be established.

Comments on the revised version:

In the previous review, I raised concerns that the evidence for a specific UBP1-Med16 interaction and for a mechanistic role of this interaction was limited. The revised manuscript does not resolve these concerns. In particular, whether UBP1 interacts specifically with Med16, whether this interaction is required for activation of UBP1 target genes, and whether UBP1 represses HIV-1 transcription through Med16 remain unresolved.

A stronger case for a specific UBP1-Med16 interaction would require more direct biochemical, structural, or biophysical evidence. The current experiments do not distinguish sufficiently between a specific Med16-dependent mechanism and broader consequences of perturbing Mediator structure or transcription.

The revision also does not include the additional biological replicates needed to assess the reproducibility of several foundational experiments. Consequently, a number of the central conclusions remain based on single experiments, which substantially limits the strength of the conclusions that can be drawn.

Major concerns:

Figure 1:

All of the data in Figure 1 are from single experiments without biological replicates. Because Figure 1 provides an important foundation for the proposed mechanism, this limits confidence in the reproducibility of the observations. Western blot experiments can show substantial experiment-to-experiment variability, and such variability appears relevant to several of the observations presented here.

A key experiment is the western blot analysis of the gel-filtration experiment in Figure 1D. Rather than migrating with Mediator, the majority of the detected Med16 appears to elute at a lower molecular weight. The extract was maintained at super-physiological salt concentrations from preparation through column loading and elution, which could potentially contribute to this result. Other possibilities include experiment-to-experiment variation or detection of a cross-reacting protein by the Med16 antibody. The latter possibility warrants consideration because the bands detected in fractions 28-31 appear to migrate at a different molecular weight from the Med16 bands in fractions 16-19. Additional replicated experiments and appropriate controls would be needed to establish that the lower-molecular-weight signal represents Med16 in a distinct complex.

Figure 2:

The data in Figure 2 are also based on single experiments without biological replicates. The biochemical experiments use protein fragments that do not occur as such in the native protein. Such experiments can be useful for mapping possible protein-protein interaction surfaces, but they can also generate false-positive or false-negative interactions depending on the experimental configuration.

Some of the results raise additional questions about the proposed interaction model. For example, the observations involving TFCP2 in panel B and Med1 and Med23 in panel F appear difficult to reconcile with a simple model in which UBP1 interacts with Mediator through Med16. Panel 2F is particularly relevant because Med1 and Med23 are not detected despite the proposed model involving UBP1 interaction with Mediator. These observations should be addressed when interpreting the specificity and mechanism of the proposed UBP1-Med16 interaction.

Figure 3:

The reporter assays provide potentially useful preliminary evidence for factors that influence transcription. However, the relatively long experimental timeframes (36-48 hours after transfection), use of artificial promoters, and overexpression of proteins introduce important limitations.

The data are consistent with the authors' model, but they are also consistent with a simpler explanation in which Med16 depletion broadly affects Mediator structure and function. Previous work from the Gross, Robert, and Roeder laboratories has shown that loss of Med16 can result in dissociation of Med23, Med24, and Med25 from Mediator. Importantly, the authors' own data in the rebuttal document appear to show similar effects following Med16 loss. These observations are important because Med23, Med24, and Med25 provide major interfaces for DNA-binding transcription factors, and Med16, Med23, Med24, and Med25 together represent a substantial fraction of the molecular mass of Mediator. The functional properties and stability of the resulting Mediator complex therefore need to be considered when interpreting Med16 depletion experiments.

The authors' data also suggest broader transcriptional effects: Med16 knockout causes loss of basal transcription in panel 3E. Conversely, overexpression of Med16 or Med16 fragments can cause broad defects in transcriptional activation, including through squelching. The relatively modest effects observed despite substantial increases in protein abundance are therefore also consistent with non-specific consequences of overexpression. These alternative explanations need to be considered when interpreting the reporter assays.

Figure 4:

RNA-seq is an appropriate approach for investigating possible effects of Med16 on gene expression. However, the experimental design has important limitations because Med16 depletion is expected to affect the composition of Mediator, including loss of Med23, Med24, and Med25. The knockdown also occurs over an extended timeframe (>24 hours), making it difficult to distinguish direct effects of Med16 from secondary effects arising from altered Mediator structure or broader changes in transcription.

The RNA-seq results could therefore reflect Med16-specific functions, but they are also consistent with a model in which loss of Med16 compromises Mediator structure and function and produces downstream gene-expression changes.

The presentation of the RNA-seq data in Figure 4E is also difficult to interpret. The volcano plot shows UBP1 overexpression versus the shCTRL vector, whereas the comparison central to the authors' interpretation concerns the effects of shMed16. Showing the volcano plot for the shMed16 comparison would allow readers to assess the statistical significance and magnitude of the relevant gene-expression changes directly. Instead, the authors superimpose "x" symbols for genes that "failed to be activated by UBP1 in the shMed16 cell line." Because the underlying Med16 comparison is not displayed, the p-values and fold changes for the comparison of interest cannot be evaluated. Moreover, positioning the "x" symbols according to the coordinates of the UBP1-overexpression volcano plot does not appear to represent their corresponding positions in a volcano plot of the Med16 comparison. This makes the figure difficult to interpret and could give a misleading visual impression of the underlying data.

Finally, the RNA-seq data are not spike-in normalized. This is potentially important because Med16 depletion is expected to cause broad effects on transcription and could result in an overall reduction in transcription across the genome. Appropriate normalization is therefore important for distinguishing gene-specific effects from global changes. I also did not identify information in the manuscript indicating where the RNA-seq data have been deposited in a public repository.

Figure 5:

The reporter assays in Figure 5 are subject to similar concerns. The authors' model may explain the observations, but the data are also consistent with broader disruption of Mediator structure and function following Med16 depletion, or with more general transcriptional effects caused by overexpression of Med16 or Med16 fragments.

A separate concern is the proposed mechanism for HIV-1 repression. The authors propose that UBP1 interacts with Med16/Mediator and that overexpression of Med16 enhances Mediator recruitment, although Mediator recruitment is not directly measured. The proposed increase in Mediator recruitment would, in isolation, be expected to promote transcription rather than repression. The authors instead invoke a UBP1-dependent mechanism to explain the repression. However, a simpler explanation is that overexpression of Med16 or selected Med16 fragments perturbs normal transcription through mechanisms including squelching. The authors themselves invoke a Med16 squelching model to explain reduced transcription at the UBP1 reporter in Figure 3G-I. The possibility that the same mechanism contributes to the results in Figure 5 should therefore be addressed.

Finally, a central component of the proposed model is recruitment of Mediator by UBP1 through Med16, but neither UBP1 occupancy nor Mediator occupancy at the relevant promoters is directly measured. These experiments would provide important evidence for the proposed mechanism. There is also no legend for Figure 5G,H, and the legend for Figure 5C,D appears to be incorrect.

Figure 6:

The title of Figure 6 states that "The position of the UBP1 binding site relative to the TSS dictates whether MED16-UBP1 activates or represses transcription." The data presented do not establish this conclusion.

Only one alternative location of the UBP1 binding site is tested, and the analysis in panel D compares only the 50 most up- or down-regulated genes in UBP1-overexpression experiments. The correlations shown are relatively weak, and a rigorous statistical analysis is not presented.

The authors cite Duttke et al. (Nature 2024) in support of the concept that transcription-factor position can influence regulatory activity. That study used genome-wide mapping of native TSSs, MPRA analysis of approximately 2,000 promoter variants, and targeted follow-up experiments. By contrast, Figure 6 relies on an artificial reporter and a single change in UBP1 binding-site position. The current data therefore support the possibility that binding-site position influences the observed reporter activity, but they do not establish the broader conclusion that the position of the UBP1 binding site relative to the TSS dictates whether Med16-UBP1 activates or represses transcription.

Figure 7:

The title of Figure 7 states that Med16 "interferes with HIV-1 PIC assembly," but the data presented do not establish this mechanism.

First, the proposed mechanism is described as acting through interaction with UBP1, but UBP1 is not measured in this experiment.

Second, Med16 knockout or overexpression has relatively modest effects on the estimated levels of bound PIC components, and these changes do not consistently correspond to the transcriptional changes shown in panel C. For example, in the WT versus Med16 KO comparison, there is no apparent difference in the levels of Pol II, Med1, IIB, or IIH based on the western blot data. The reduction in Med16 and Med23 is expected following Med16 knockout and therefore does not by itself establish altered PIC assembly. In the WT versus Med16 overexpression comparison, panel C suggests a meaningful reduction in transcription, whereas the changes in PIC-associated proteins do not follow the direction predicted by the proposed model: Pol II and IIB increase with Med16 overexpression, while Med1, Med23, Med16, and IIH appear similar.

Third, Cdk8 and Med12 are not PIC components. They are subunits of the CDK8 module, which can inhibit PIC formation. Even under a simplified interpretation in which reduced Cdk8 and Med12 levels were relevant to PIC formation, the direction of these changes is opposite to that expected from the "relative mRNA level" plots in panel C. Reduced levels of these proteins in the Med16 overexpression condition would, under this interpretation, be expected to promote rather than reduce transcription.

Finally, this is a single-replicate experiment, and quantitative comparisons are made across immobilized-template pulldowns using different nuclear extracts (WT, Med16 KO, and Med16 OE). Differences in protein concentration between extracts, differences in pulldown efficiency, and experiment-to-experiment variation could all contribute to the observed differences. Replicated experiments with appropriate normalization would therefore be needed to support the proposed PIC mechanism.

Figure 8:

Panel F presents a model that, in my view, goes beyond what is supported by the experimental data. In particular, there is currently insufficient evidence to establish the proposed Med16-UBP1-TFCP2 complex as a distinct functional complex.

The model also depicts the Mediator CDK8 module bound at promoters together with Pol II. The manuscript does not provide evidence supporting this arrangement, and there is substantial prior evidence that the CDK8 module can inhibit or prevent PIC formation. This aspect of the model therefore requires either experimental support or clarification.

Finally, the model depicts a separate Med16-UBP1-TFCP2 complex. This appears inconsistent with the authors' statements in the rebuttal that they did not intend to propose such an unsupported isolated complex. If this is not the intended model, Figure 8 should be revised to avoid conveying that interpretation.

Figure S1: IP-MS analysis:

The IP-MS data raise substantial concerns regarding the specificity of the proposed UBP1-Med16 interaction.

The authors state that they "have now reanalyzed the IP-MS data using a more precise quantification approach." However, the filtering procedure described in the Methods is difficult to evaluate and requires substantially more justification. The procedure includes multiple sequential criteria: detection in at least two of three replicates of the target bait; a minimum unique peptide count; detection in at least one additional Mediator bait; exclusion of Mediator/Pol II subunits, ribosomal proteins, histones, keratins, and common contaminants; and annotation with transcriptional or DNA-binding functions using GO terms. The rationale for this particular combination of filters and its impact on the candidate list should be explained and justified.

The resulting "bait-preferential score" is also difficult to assess. The reported mean_target and mean_other values are frequently negative, with some positive values, and the method appears to derive a positive score from the difference between these values after taking an absolute value. The biological and statistical interpretation of this score is therefore unclear. The reported scores are generally clustered around relatively narrow values, and the analysis does not appear to provide the statistical framework normally used to assess enrichment and reproducibility in IP-MS experiments.

Importantly, the candidate proteins identified by this approach do not appear to overlap with proteins identified in other published Med16 IP-MS analyses in human cell lines, including HCT116, MCF7, HEK293T, and HeLa. I was unable to identify a protein among the 37 Med16 candidates that was consistently observed in the cited resources, including BioPlex (Huttlin et al., Cell 2021) and Malovannaya et al. (Cell 2011). This lack of concordance raises questions about the specificity and physiological relevance of the proposed Med16-associated proteins and, in particular, about the evidence for a specific UBP1-Med16 interaction.

The peptide counts for UBP1 also illustrate the limitation of the current analysis. The total UBP1 peptide counts across the Cdk8, Med1, and Med16 IP-MS experiments are 12, 10, and 14, respectively, yielding bait-preferential scores of 1.07, 0.76, and 1.85. Given these relatively small differences and the absence of statistical significance measures, it is difficult to determine whether these observations provide evidence for a specific biological interaction.

The authors have now made the raw abundance values and peptide counts available as supplementary tables, which is useful. However, standard statistical measures for evaluating MS data, including FDR, p-values, and adjusted p-values, are not provided, nor is sufficient information given about how the reported scores were calculated. These additions would be important for readers to assess the robustness of the conclusions.

Concerns about the rebuttal document:

Several statements in the rebuttal appear inconsistent with the data shown in the revised manuscript or with the interpretation of the authors' own experiments. I highlight specific examples below.

(1) The proposed Med16-UBP1 complex:

I previously raised concerns that the manuscript overstated the evidence for a separate Med16 complex associated with UBP1 and lacked rigorous biochemical characterization of such a complex. The authors responded that the wording of the original manuscript may have created this interpretation and stated that this was not the mechanistic model they intended to convey. However, Figure 8 of the revised manuscript still depicts a separate Med16-UBP1-TFCP2 complex. The figure therefore appears to retain the interpretation that the authors stated they did not intend to convey. This should be clarified.

(2) Replication and experimental rigor:

I previously raised concerns about the absence of replication and the limitations of the experimental approaches used to infer roles for Med16 and UBP1. These concerns remain because no additional replicate experiments were performed for several of the key experiments. As a result, important conclusions continue to depend on single western blots, including foundational experiments in Figures 1, 2, and 7.<br /> Examples include the variable quantification in Figure 1A; the absence of detectable Med23 and Med1 in the UBP1 IP in Figure 2F despite the proposed interaction between UBP1 and Mediator; and the variable association of TFCP2 with Flag-MED16 fragments in Figure 2B, including lanes 7-9. Replication would be important for determining whether these observations are reproducible.

(3) IP-MS analysis:

The revised IP-MS analysis provides additional information compared with the previous version, but important concerns remain regarding the processing and interpretation of the data. The "bait-preferential score" approach is not sufficiently justified, and standard measures such as p-values, adjusted p-values, or FDR are not provided.

The analysis also identifies no proteins among the 37 Med16 candidates that appear to be consistently observed in other published Med16 IP-MS analyses in human cell lines. This is important when assessing the specificity of the proposed interaction.

The peptide counts for UBP1 are similarly low and do not show a clear Med16-specific enrichment: 12 peptides in the Cdk8 IP, 10 in the Med1 IP, and 14 in the Med16 IP, corresponding to scores of 1.07, 0.76, and 1.85, respectively. These observations do not by themselves provide strong evidence for a specific UBP1-Med16 interaction.<br /> In addition, the Med16 IP experiments identify approximately 800 proteins per replicate. This broad set of associated proteins highlights the importance of appropriate controls and statistical analysis when interpreting a co-IP as evidence for a specific protein-protein interaction.

(4) Interpretation of the 1,6-HD experiments:

I previously raised concerns that the IP-western data in Figure 1 did not establish a Med16-specific effect. The rebuttal states that "MED16 exhibits a uniquely pronounced dissociation by 1,6-HD that is consistent across three independent IPs using anti-CDK8, anti-MED1, and anti-MED12 antibodies." However, the quantitative data shown do not clearly support this interpretation.

In the CDK8 IP, CDK8 and MED23 appear to be lost to a similar extent as Med16. In the Med1 IP, Med12 shows a similar loss to Med16, with Med23 also showing a comparable trend. In the Med12 IP, CDK8 and Med23 show changes comparable to Med16. There are also unexplained increases in some Mediator subunits with increasing 1,6-HD concentrations. For example, Med12 and Med1 are variable across the 1,6-HD conditions, and Med1 and Med24 increase at higher concentrations. Similar trends are present in the CDK8 IP.

The Figure 1B data raise related concerns. Several Mediator subunits show substantial increases following the 2,5-HD condition compared with 1,6-HD, in some cases greater than the change observed for Med16. Thus, the available data do not clearly establish that Med16 exhibits a uniquely pronounced dissociation from Mediator.

(5) Evidence for the proposed mechanism:

I previously suggested that more rigorous approaches would be needed to distinguish a specific Med16-dependent mechanism from broader effects of Med16 perturbation. The rebuttal instead emphasizes that the authors' conclusion that the UBP1-TFCP2 heterodimer acts through Med16 is supported by multiple independent lines of evidence.

However, the different experiments do not independently establish the same mechanistic conclusion. Many rely on long experimental timeframes, overexpression, reporter assays, limited controls, or lack of biological replication. These approaches can provide useful preliminary evidence for effects on transcription but do not establish that a specific UBP1-Med16 interaction is required for UBP1 target-gene expression.

Additional approaches that directly test the proposed interaction and its requirement for transcriptional regulation would therefore be needed to establish this mechanism.

(6) Med16 rescue experiment:

The authors performed an RNA-seq comparison of WT, Med16 KO, and Med16 KO cells rescued by re-expression of WT Med16. This is a potentially informative experiment, and I appreciate that it was performed.

However, the heatmap shown in the rebuttal does not appear to demonstrate a clear rescue of UBP1 target-gene expression. The figure contains approximately 60 genes but provides no legend beyond "Gene profiling of MED16 KO and rescue effect." The authors describe the result as showing that re-expression of Med16 can largely restore expression of UBP1 target genes, but this conclusion is not readily apparent from the figure as presented. More information about the analysis, normalization, and comparisons would be needed to evaluate the claimed rescue. It would also be useful to include the relevant analysis in the revised manuscript rather than only in the rebuttal.

(7) Consequences of Med16 depletion:

A continuing concern is that the manuscript does not adequately account for the broader consequences of Med16 depletion or knockout. Loss of Med16 is known to cause dissociation of other Mediator subunits, including Med23, Med24, and Med25. The authors acknowledge this in the rebuttal and state that their new Co-IP and IP-MS experiments confirm partial dissociation of these subunits following Med16 knockout. They also acknowledge that this structural perturbation must be considered when interpreting phenotypes from Med16 depletion and that long-term knockdown or knockout approaches are susceptible to secondary effects and cellular adaptation.<br /> These are important caveats, but they are not adequately incorporated into the interpretation of the revised manuscript, and the new data demonstrating loss of Med23, Med24, and Med25 are not shown in the article.

This issue is particularly important for interpreting the transcriptional experiments. Loss of Med16 is expected to disrupt Mediator more broadly, including loss of Med23, Med24, and Med25, which provide important transcription-factor interaction surfaces. These changes could produce widespread transcriptional effects independently of a specific UBP1-Med16 mechanism. Given that the authors' own experiments now provide evidence for this structural perturbation, the possibility of indirect effects and altered Mediator function should be explicitly incorporated into the experimental interpretation.

Overall assessment:

The manuscript addresses an interesting question and presents several potentially useful observations concerning Med16, Mediator, and UBP1. However, the central mechanistic conclusions are currently not supported by sufficiently rigorous or independent evidence. The principal concerns are the extensive reliance on single-replicate experiments; the use of overexpression, artificial reporters, and long depletion timeframes; the absence of direct measurements of UBP1 and Mediator occupancy; the broad structural consequences of Med16 depletion; and the limited statistical support for the IP-MS analysis.

Taken together, the current data do not distinguish adequately between the proposed specific UBP1-Med16 mechanism and alternative explanations involving broader disruption of Mediator structure or transcription. Addressing this distinction is important because it affects the interpretation of much of the manuscript, including the RNA-seq and reporter-assay results and the proposed HIV-1 mechanism.

The authors have generated several useful datasets, including the Med16 knockout/rescue experiment and additional IP-MS information, but the manuscript would need to incorporate the associated caveats and provide stronger experimental evidence before the proposed mechanistic model can be established.

Reviewer #1 (Public review):

Summary:

This is a useful study by Angla et al that investigates the basis of observations made from previous studies where loss of Onecut (OC) transcription factors lead to changes in spinal interneuron populations that do not themselves normally express OC. The authors hypothesize that OC expression in spinal motor neurons has non-cell-autonomous effects on pre-motor interneuron (V1, V2a/b/c) population size and distribution. By knocking out OC in the motor neuron lineage (i.e., downstream of Olig2, a motor neuron progenitor marker gene), they indeed show that motor neuron-specific loss of OC expression decreases V2c interneuron number and alters the spatial distribution of V1, V2a, V2b, V2c populations. Using bulk RNA-sequencing of WT and OC conditional knockout (cKO) motor neurons, the authors identify that neurotrophic factor Ntf3 as another factor that is responsible for the non-cell-autonomous effects on the interneuron population; upon knock out of Ntf3 downstream of Olig2 they show that this leads to increased interneuron numbers and alters their spatial distribution, ultimately leading to dysregulation of spinal motor circuits and motor activity.

Strengths:

The authors use sophisticated genetic tools to precisely remove OC and Ntf3 expression in a lineage-specific manner and comprehensively assess the downstream effects across brachial, thoracic, lumbar levels of the spinal cord, as well as at two developmental timepoints, E12.5 and E14.5.

Weaknesses:

The evidence supporting their claims is incomplete. In figure 2 and 4, the control distributions (despite reporting the same populations in the same regions) look different, suggesting large sample-to-sample variance in distribution. The authors explain that this is due to several technical limitations in their study.

Furthermore, the way the Ntf3 results are framed can be misleading; it reads as though one of the main claims of this study is that OC acts through Ntf3.

Reviewer #2 (Public review):

The study by Angla et al. proposes a model in which NT-3 produced by motor neurons regulates interneuron numbers and distribution in a non-cell autonomous manner. The authors demonstrate that ablation of motor neurons (MNs) and global and conditional deletion of OC transcription factors lead to changes in interneuron distribution. They identify that NT3 is upregulated after MN-specific OC deletion in RNA-seq experiments and show that olig2-cre mediated NT3 deletion leads to increased ventral interneuron numbers, altered distribution and defects in locomotor behavior. The authors conclude that MN-derived NT3, under OC control, regulates interneuron development. While this is an intriguing hypothesis, the study does not consolidate the results from the different experimental models in a cohesive model to provide any mechanistic insights into how NT3 may accomplish this function.

(1) The authors utilize different experimental models (OC transcription factor global and conditional knockouts, DTA ablation and NT3 deletion) to show that MNs may influence interneuron numbers and positioning, but there doesn't seem to be a direct link into how each manipulation relates to the others in an informative way. For example, the relationship between OC and NT3 deletion data is not entirely clear, even though NT3 is downstream of OC transcription factors. Both deletions lead to changes in interneuron distribution but there doesn't seem to be any correlation between the two that relates to relative changes in NT3 levels. Although it is understandable that transcription factor manipulations may have additional effects, it is hard to derive any mechanistic insights into how exactly MNs influence interneuron differentiation or migration from the data presented here. Similarly, while the rationale for following up on NT3 seems to be the chick electroporation experiments, only a very minor decrease in Chx10 interneurons is shown in those experiments. Shouldn't NT3 overexpression lead to substantial decreases in IN numbers according to the authors' model?

(2) The study primarily quantifies interneuron numbers and distribution at different levels of the spinal cord and under different genetic manipulations. In different figures, the values and distributions shown for controls vary quite a lot. For example, in figure 2B vs figure 4B, the number of FoxP2+ V1 neurons at brachial levels is ~350 vs 125. Similarly, the control distributions in 2I and 4I are quite different. While this can be partially explained by technical issues, it remains challenging to determine whether the conclusions regarding the impact of each genetic manipulation on interneuron numbers and distribution are valid.

(3) It is not clear that the behavioral phenotypes seen in the olig2-cre mediated deletion of NT3 can be attributed to specific changes in interneuron development, connectivity or function. While the behavioral phenotype is in theory consistent with defects in motor circuits, there is a big gap between the embryonic changes shown here and behavior, with no in between circuit level changes in locomotor circuits shown. Thus, the behavioral experiments are not very informative as to how exactly components of motor circuits might be altered with the NT3 deletion.

Reviewer #3 (Public review):

This manuscript aims to investigate cell extrinsic mechanisms that regulate differentiation and distribution of interneuron types in the spinal cord. The authors demonstrate that the loss of motor neurons leads to changes in number and distribution of different interneuron types, specifically V0v, V1, and V2b (but not V2a). The authors then hypothesize that this phenotype may be controlled by the action of Onecut (OC) transcription factors in motor neurons. Conditional knockout of OC1 + OC2 in motor neurons using Olig2-Cre, however, does not lead to significant changes in numbers of V1, V2a, V2b interneurons, although there is a change in their spatial distribution. While the authors do not check V0v neurons in OC mutants, they do check V2c, which show a reduction in number and change in distribution. Why the same neurons are not checked across experiments is unclear. The authors then analyze existing RNA-seq data to identify factors that could be mediating effects of the OC factors in motor neurons. They identify Ntf3 as a candidate and confirm that it is upregulated in OC mutants. Conditional loss of function of Ntf3 (Olig2-Cre) leads to increases in V1, V2a, and V2b (but not V2c) interneurons and changes in distribution of all four interneuron types. However, the Ntf3 phenotypes do not necessarily suggest that it works in the same pathway as OC to control interneuron development. Finally, the authors demonstrate that these Ntf3 conditional mutants have major defects in motor function.

The main conclusions of the manuscript are that i) motor neurons non-cell autonomously control interneuron development, ii) that OC activity in Olig2 lineage cells non-cell autonomously controls aspects of interneuron development, and iii) that Ntf3 in motor neurons non-cell autonomously controls aspects of interneuron development. The mechanistic link between OC and Ntf3 activity is not clear. And the interneuron phenotype seen when motor neurons are depleted it not phenocopied by either loss of OC or Ntf3 from motor neurons. While the authors addressed some of my initial comments, the impact of this work on the field remains difficult to assess for the following reasons:

(1) The manuscript relies heavily on quantifying numbers and spatial distribution of interneuron populations. However, these do not seem to be consistent in control animals across experiments, making it difficult to interpret any changes observed in genetic manipulations. Specifically, in Fig. 2 and 4, the same markers are being used to quantify V1, V2a, V2b, and V2c interneurons in controls vs. OC (Fig. 2) or Ntf3 (Fig. 4) conditional knockouts, but the numbers of neurons and their distribution in control animals are variable between these two figures. For example, there seem to be a mean of >300 V1 neurons in E12.5 brachial sections of Fig. 2 controls, but this number is <150 in Fig. 4 controls. The cell distribution scoring is similarly variable between these controls without any explanation. The same is true for E14.5 controls used in Fig. S2 vs. Fig. S6.<br /> The authors explain in response to the 1st review that technical variability including different antibodies, different researchers performing experiments, and different mouse backgrounds may contribute to this variation, but do not include this explanation clearly in the manuscript where it would be useful for readers. It would have also helped, for example, if authors had labeled datapoints on bar plots based on the animal that they came from to understand inter-animal variability within experiments. Overall, the biological significance of the results remain difficult to interpret due to high technical variability.

(2) In the initial review, it was noted that there is no data to support the claim that OC1/2 mutants have altered interneuron development because of higher Ntf3 expression. In response to this, the authors note that the manuscript does not claim that OC exerts its non-cell autonomous effects through Ntf3 and add a new paragraph in the discussion which now addresses the fact that it is difficult to compare the phenotypes observed the different genetic manipulations presented in the work. While this paragraph addresses the incomplete mechanistic link between OC and Ntf3, it also decreases the mechanistic impact of the work.

(3) In Figure 3E-3G, the authors show that some V1, V2a, V2b interneurons express the Ntf3 receptor TrkC. It is not stated (apologies if I missed it) what age this expression is, and from the images, it looks like in addition to medially located newborn neurons being negative, laterally located Gata3 interneurons are also broadly negative for TrkC, and many Foxd3 and Chx10 interneurons are also negative. Separate images of each channel and/or scoring would help clarify this. If many relevant interneurons are indeed TrkC negative, how this affects the conclusions should be addressed in the manuscript.

(4) Behavioral phenotypes are not necessarily caused by Ntf3's role in premotor interneuron development.

Reviewer #2 (Public review):

Summary:

Vertebrate spinal cord receives inputs from many supraspinal regions. The authors used optical backfilling to trace neurons in the zebrafish larval brain sending axons to the spinal cord . With two-photon microscopy, they managed to render a comprehensive 3D map of these neurons and drew homologs with mammalian brain structures.

Strengths:

The main strength lies in the precise 3D mapping. The fact that most of previously reported neuron groups have been confirmed by their approach is a solid endorsement of their methodology.

This study provides a comprehensive alternative anatomical reference framework for studying individual groups of supraspinal neurons with projections to the zebrafish spinal cord.

Weaknesses:

The backfilling approach does not reveal the full trajectories of axons, which is available to some degree by ZExplorer Atlas.

Reviewer #1 (Public review):

Summary:

The study by Fernandes et al used multiple types of experiments to study the increased metastatic activity conferred by p95-HER2 and presented evidence that biased downstream signaling was engaged by p95-HER2. Further studies demonstrated crucial phosphorylation sites and downstream transcription targets. Overall, this study will contribute to increased understanding of HER2 biology and breast cancer metastasis.

Strengths:

Multiple types of experiments to assess the increased invasion property by p95-HER2. Solid evidence was provided that p95-HER2 elicits a different transcription program, enhancing EMT. Convincing results were achieved in knockdown studies on crucial genes such as MRTFA and TGFB1I1.

Weaknesses:

To enhance the quality of this study, several points need to be addressed.

(1) First, as the background to this study, the authors stated in the introduction that different isoforms of HER2 lead to different invasive properties. Is this conclusion based on clinical observation or animal models? This needs to be specified to help readers grasp the importance of the paper.

(2) Second, this study is mostly performed on three cell lines generated from three tumor models, WT, d16, and p95. Were multiple cell lines generated from the same tumor model (e.g., p95), and how similar are these cell lines if they are from the same tumor model?

(3) Third, Figure 2 presented data from a very interesting experiment. However, the overall conclusion of this experiment is hard to grasp from the text.

Reviewer #2 (Public review):

Summary:

This is a significant study with implications for signal transduction, breast cancer, and metastasis research. The study uses cell lines from the innovative HER2BOW model mouse to compare and contrast properties of mouse mammary tumors induced by wt HER2, dex16 HER2, and p95 HER2. The linkage between p95 Y1139 and TGFB1I1, as well as MRTFA, is very interesting. The study involves mechanistic approaches to distinguish signaling from dex16 HER2 and p95 HER2 that will be well received by the field.

Strengths:

The study describes the development of novel cell lines for mouse mammary tumors induced by different forms of HER2. In vitro analysis includes a wide variety of assays, including high-resolution fluorescent imaging and tracing of cell movement/ECM degradation, and single-cell RNA-seq analysis. Several approaches are used to confirm p95 HER2 pY1139-induced signaling through nuclear MRTFA and TGFB1I1. shRNA and CRISPR/Cas9 were used to confirm signaling through this pathway.

Weaknesses:

The authors have only described one cell line for each HER2 form, a weakness which they acknowledge. The fact that these lines mimic characteristics that were described in their previous work on tumors induced by wt HER2 vs. dex16 HER2 vs. p95 HER2 is, however, supportive of their conclusions. In addition, the specific connection between p95 and nuclear MRTFA is confirmed in HEK cells. The manuscript could be improved with some discussion on how p95 p-Y1139 is likely to signal (what binds to this site?)

Reviewer #3 (Public review):

Summary:

The study aims to explain why different HER2 isoforms produce distinct cancer-cell phenotypes, with a particular focus on the poorly understood mechanisms by which p95-HER2 promotes the invasive and metastatic behaviors of HER2-positive breast cancer. The authors propose that functional selectivity at the HER2 receptor level, particularly signaling through Y1139, preferentially engages an MRTFA-TGFB1I1 transcriptional/cytoskeletal program, thereby shifting p95-HER2-expressing cells toward individual motility, matrix degradation, invasion, and metastasis rather than simply proliferation.

Strengths:

A major strength is the multi-level experimental strategy. Rather than relying on a single invasion assay, the authors integrate phenotypic profiling, single-cell RNA-seq, imaging of MRTFA nuclear localization, protein validation, cytoskeletal analysis, matrix-degradation assays, transwell invasion, 3D spheroid/organoid assays, and orthotopic transplantation. This provides relatively coherent evidence that p95-HER2 cells occupy a distinct biological state characterized by individual motility and invasion, accompanied by a myogenic/contractile transcriptional program and increased MRTFA nuclear localization. Another strong aspect is the attempt to connect the downstream phenotype to a specific HER2 phosphorylation site. The authors identify Y1139 as a candidate determinant of the "go" phenotype and show that mutation of Y1139 to phenylalanine eliminates MRTFA translocation as well as the associated motility and invasion phenotypes

Weaknesses:

The main limitation is that the evidence for the proposed signaling mechanism is stronger for functional dependence than for direct molecular mechanism. The data establish that Y1139, MRTFA, and TGFB1I1 are required for the p95-HER2 invasive phenotype, but they do not appear to fully establish how phosphorylation at Y1139 mechanistically couples p95-HER2 to MRTFA activation. In particular, a direct biochemical link between Y1139 and the machinery controlling actin polymerization/MRTFA nuclear translocation would make the proposed pathway substantially more convincing.

A second limitation is the model system used in the study. Much of the mechanistic work relies on three particular engineered HER2 isoform-expressing cell lines, while the in vivo experiments use NOD/SCID mice. This is useful for testing tumor-cell intrinsic invasion and metastasis, but it limits conclusions about the generality of the functional regulation across different cell contexts, and also limits the understanding of how the pathway operates in the intact immune microenvironment. This is especially relevant because the manuscript itself places p95-HER2 in the broader context of immune evasion and notes that MRTFA can regulate PD-L1; however, the current models cannot adequately establish whether the proposed pathway contributes to immune-mediated metastatic progression in vivo.

Finally, the distinction between "go" and "grow" signaling is conceptually attractive, but the extent to which it represents a general property of HER2-positive human breast cancers remains less certain. The study provides strong experimental evidence for functional selectivity in the models examined, but additional validation in independent patient-derived models and clinically relevant tumors would be needed before generalizing this mechanism across HER2-positive disease.

Reviewer #1 (Public review):

Summary:

The manuscript aims to mechanistically characterize the final step of the Lol lipoprotein trafficking pathway in Gram-negative bacteria, where triacylated lipoproteins are transferred from the periplasmic chaperone protein LolA to the outer membrane receptor LolB for subsequent insertion into the inner leaflet of the outer membrane. The crystal structures of LolA R43L-LolB, LolB L114G-lipoprotein, LolB Q44A (open), and LolB Q44A (closed) are reported. A combination of structural analysis, growth assays, pull-downs, and fluorescence spectroscopy was employed to characterize the behaviour of wild-type and mutant forms of Lol proteins. The authors then used previously published molecular dynamics simulations to propose a six-step model for the transfer and insertion of lipoproteins from LolA to LolB, and finally into the membrane.

The structural work is mostly solid, but the mechanistic conclusions drawn from it rely too much on interpolation between static states and on functional assays with limited dynamic range.

Strengths:

(1) The structure-guided mutagenesis was thorough and well designed. Mutants were tested both in isolation and in combination with one another, utilizing both alanine and charge reversal mutants, to fully tease apart which residues were most important for the interaction.

(2) The dissection of the Hook interactions allowed the authors to identify the importance of the identity of the hook apex residue, as well as the critical hydrogen bond that maintained the Hook geometry.

(3) The structure of the lipoprotein-bound LolB is a valuable addition to the body of knowledge around this pathway, and the way that the complex was produced was very clever.

Weaknesses:

(1) There is no raw data shown for any of the interactions or lipoprotein transfer experiments. All of the quantitative claims about LolA association and lipoprotein transfer rely on SDS-PAGE densitometry, and not a single gel image from those experiments is provided in the main text or supplemental.

(2) Pull-down assays are a fairly poor assay to use for protein interactions when there are so many quantitative alternatives that would be amenable to this experimental system, especially when the association and transfer of lipoprotein are the central claims of the manuscript.

(3) The crystal structures are under-refined for their resolution, with large R-factor gaps and somewhat concerning statistics contained in the wwPDB reports (e.g. >20% RSRZ outliers in 2/4 structures). The data also seem to be cut at strangely high I/sigI for the two Q44A structures with no explanation.

(4) In the LolB L114G structure, the Hook residue L68 is the most poorly fit in the whole structure. The validation report indicates the entire hook is poorly resolved, but without access to the maps and models, we are unable to assess this independently.

(5) There is no rubric for what constitutes a significant result for the DAUDA fluorescence spectroscopy. What level of increase vs wild-type is considered significant? I188G is incredibly close to L144G, but one is treated as a non-result and the other as something that should be further investigated.

(6) The conformational trajectory of the proposed model is on static endpoints.

Reviewer #2 (Public review):

Summary:

The manuscript by Jepson and colleagues presents the structural and biochemical study of the outer membrane LolB in complex with LolA in its apo and lipoprotein-bound states. The Lol system (LolABCDE) is essential in the translocation of lipoproteins to the outer membrane. Several studies have looked at the inner membrane complex. This study captured the last step of the process, the translocation of lipoproteins to the outer membrane via the LolB and LolA proteins. The crystal structures of LolB in complex with LolA revealed key interactions via the hook and charged belt motifs. Mutagenesis was not able to fully dissociate the complex or prevent the transfer of lipoprotein. The complex of LolB with LolA and lipoprotein revealed the 'final' step of engaging the complex for lipoprotein insertion into the outer membrane.

Overall, this is an excellent and exciting study for the Lol field as it captures the events happening at the outer membrane.

Strengths:

The authors have determined several high-resolution structures and validated them with excellent mutagenesis experiments. The key structure is that of LolB with LolA and the lipoprotein (even partially resolved).

Weaknesses:

The only 'weakness' is that the authors have used mutants of either LolB or LolA to capture the stable states, and the discussion section would benefit from commenting if these states could be dead-end states, as validation of the mutants has been done with a WT background. In addition, can they discuss whether a2 is likely to undergo further conformational changes to open a lateral gate to the OM for the acyl chains of the lipoprotein to insert?

Reviewer #1 (Public review):

Summary

The authors set out to address a critical gap in olfactory bulb research: the lack of a comprehensive annotation of neuron types and their connectivity in the adult zebrafish. Using a large serial block-face scanning electron microscopy volume, they reconstructed 459 neurons and performed a detailed morphological and ultrastructural classification. They identified 13 major neuron subclasses, including two projection neuron types (mitral cells and ruffed cells) and 11 interneuron types. A key finding is that despite the diffuse appearance of the lateral olfactory bulb neuropil, it is organized into discrete, segregated glomeruli. The authors also performed targeted synapse annotation, revealing systematic and selective connectivity patterns between projection neurons and specific interneuron subnetworks, and discovered distinct microcircuit motifs involving reciprocal and unidirectional connectivity. This work provides a crucial anatomical framework for understanding the circuit basis of olfactory computations.

Strengths

(1) The volumetric EM reconstructions capture fine ultrastructural features (e.g., spine shapes, neurite caliber variations, and varicosity morphology) at nanometer resolution across hundreds of neurons. The descriptive detail and 3D rendering provided for each subclass are remarkably thorough.

(2) The study goes beyond simple morphological descriptions by integrating ultrastructural features, such as spine shape, neurite diameter, and synaptic arrangements, to define neuron classes. This provides a more functionally relevant taxonomy. The classification was also cross-validated by independent neuroscientists.

(3) The targeted synapse annotation translates anatomy into testable circuit hypotheses, revealing distinct connectivity motifs (reciprocal vs. unidirectional, MC-selective vs. RC-selective) that provide structural substrates for computational functions such as normalization.

Weaknesses

(1) It is important to provide an estimate of the total neuronal population of the adult zebrafish OB and justify that their sample size is sufficient to claim a "comprehensive" neuron type classification.

(2) The classification was based on morphology and ultrastructure. If feasible, we recommend an unsupervised clustering analysis using only the synaptic connectivity matrix for fully reconstructed neurons to test whether connectivity patterns recapitulate the 13 morphological subclasses. Besides, cross-validation by independent annotators is great. However, when the annotators disagreed on a neuron's subclass, how was it resolved?

(3) A summarized reference table that includes features for each subclass is highly recommended (the main text cited several tables; however, I did not find them). This would facilitate community adoption of the classification.

(4) The schematic in Figure 20 could be optimized to reflect synaptic connections among 13 subclasses with connection strength annotated.

Reviewer #2 (Public review):

Summary:

The authors have used a previously published SBEM dataset of the adult zebrafish olfactory bulb and carefully reconstructed the fine structure of a large number (459) of neurons. Through manual classification of cells into 13 different anatomical classes, they provide a carefully annotated library of cells. Classifications have been validated by comparing the labeling of 5 human annotators, which revealed a large degree of reproducibility. Synaptic identification enables assignment of connectivity, revealing a major contribution of reciprocal connections (two-way synapses) that may support key computational features during olfactory processing. In general, the work provides a clean descriptive account of the organization of the zebrafish olfactory bulb, which should help to better understand principles of olfactory processing in vertebrates.

Strengths:

The authors provide a library of neurons in the olfactory bulb of adult zebrafish that will be highly useful to the broader circuit neuroscience community. Figures of classified cell types have been convincingly arranged to appreciate the high quality of the EM volume and reconstructions. Cells are easily accessible through a web interface to facilitate the assessment of classifications. An important result is that anatomical structures in zebrafish clearly follow the glomerular arrangement known in mammals, which argues against a microglomerulus model previously proposed for the zebrafish olfactory bulb.

Weaknesses:

The paper uses Wanner et al. 2016 as a main base dataset to generate a descriptive library of cells, in a limited volume (18%) of the zebrafish olfactory bulb. Annotations of cell types and synapses are largely human-based. Using a multi-human validation strategy helps to assess labeling, but it would benefit from more rigorous statistics, in particular for the synapse annotations. In general, the paper would be easier to read with a glossary of cell types. Some features are quite intriguing, like the cilia structures in some of the somata or the ruffs, but discussion of the potential computational roles of these fine structures is missing.

Reviewer #3 (Public review):

Summary:

The authors aimed to build a comprehensive understanding of the cell classes that make up the adult zebrafish olfactory bulb (OB) and their connectivity. Using an EM volume covering the three OB layers and several glomeruli, they aim to reconstruct a sufficient sample of all cell classes in the OB. Based on 459 proofread reconstructions, they identify 13 cell classes and a small number of subclasses and offer detailed expert neuroanatomical arguments, largely qualitative, for why these classes are distinct. While they do not have a synapse classification, they further build a manual wiring diagram of connectivity based on these reconstructions, which together offer a strong baseline understanding of the organization of the OB and useful properties to build into a future quantitative assessment of fish neuroanatomy in general.

Strengths:

The paper offers a powerful example of why expert assessment remains a vital tool in neuroanatomy. While quantification is deeply important to scale data, the kind of careful multimodal human investigation of neuronal shape, connectivity, and ultrastructure forms a key basis for discovering and differentiating neuronal cell types. The authors use multi-expert classification to validate qualitative assessments as well, which is a good way to handle cross-individual uncertainty. The descriptions of each type and their relationships are generally quite thorough, and there are enough cells to offer a satisfying baseline categorization. Anyone studying zebrafish OB is likely to get a lot out of this paper.

Weaknesses:

While I am a strong believer in expert neuroanatomical intuition alongside quantitative neuroanatomical approaches to cell typing (especially given the manageable number of cells and cell types), I would have liked a section explaining why this approach was taken as opposed to a more quantitative one from the beginning. I think that this is a case study in where the expert qualitative approaches are useful, especially with fascinating details like the unusual hand-shaped spines. A lot of the strength of the paper comes from this philosophy, in my view, and it would be nice to hear it elucidated by the authors. I would also be curious if the authors came to any conclusions about what might have been possible with a more data-driven approach, although this may be beyond the scope of the work or not terribly interesting.

There were some aspects of the cell typing that I didn't totally understand. Two of the most common issues with cell typing are that (1) it is unclear if cell types are discrete and (2) unusual cells appear that don't have enough peers to classify into an unambiguous type. Did those happen here? For example, it was not obvious to me how it was decided that mitral cells fell into three subclasses: small, medium, and large, and not a continuum from small to large. Similarly, some interneuron classes had subclasses. What anatomical qualities suggested that a split was a subclass-level split vs a class-level split? Were there any cells that were impossible to classify into a group, or was everything actually tidy? How confident are the authors that they have captured the complete diversity of the OB from this sampling?

I generally appreciated the numerous detailed figures and found them generally clear and informative. However, as someone who is not deeply familiar with zebrafish olfactory bulb organization, I would have liked to have at least some global context for each cell class in terms of how typical cells relate to the layers and glomeruli. Figure 18B does a nice job of this with many cells, but it would be clearer to see this along the way with the individual classes (and subclasses) as well.

For the connectivity analysis, I commend the authors for doing as much manual synapse annotation as they did, but the lack of completeness makes it less clear how to interpret the connectivity findings. In particular, how complete is the current assessment? For example, when describing connectivity between pairs of cells, how were the pairs selected? Did they necessarily have contact between the meshes, or innervate the same glomerulus, or were they just two cells of the same type in any location? This is useful to understand how to interpret the connectivity fractions measured.

Reviewer #1 (Public review):

Summary:

The authors sequenced 888 individuals from the 1000 Genomes Project using the Oxford Nanopore long-read sequencing method to achieve highly sensitive, genome-wide detection of structural variants (SVs) at the population level. They conducted solid benchmarking of SV calling and systematically characterized the identified SVs. While short-read sequencing methods, including those used in the 1000 Genomes Project, have been widely applied, they exhibit high accuracy in detecting single nucleotide variants (SNVs) and small insertions and deletions but have limited sensitivity for SV detection. This study significantly enhances SV detection capabilities, establishing it as a valuable resource for human genetic research. Furthermore, the authors constructed an SV imputation panel using the generated data and imputed SVs in 488,130 individuals from the UK Biobank. They then conducted a proof-of-principle genome-wide association study (GWAS) analysis based on the imputed SVs and selected traits within the UK Biobank. Their findings demonstrate that incorporating SV-GWAS analysis provides additional insights beyond conventional GWAS frameworks focusing on SNVs, particularly in improving fine-mapping.

Strengths:

The authors constructed a high-sensitivity reference panel of genome-wide SVs at the population level, addressing a critical gap in the field of human genetics. This resource is expected to significantly advance research in human genetics. They demonstrated the imputation of SVs in individuals from the UK Biobank using this panel and conducted a proof-of-concept SV-based GWAS. Their findings highlight a novel and effective strategy for integrating SVs into GWAS, which will facilitate the analysis of human genetic data from the UK Biobank and other datasets. Their conclusions are supported by comprehensive analyses.

Weaknesses:

The authors have addressed many of my previous comments, and I appreciate their efforts. However, I still have two related concerns.

(1) Shortly after reviewing this manuscript last year, my laboratory obtained access to the UK Biobank (UKB) Tier 3 dataset for an unrelated project. In August 2025, I searched the UKB Research Analysis Platform (UKB-RAP) for the imputed structural variant (SV) dataset described in this manuscript but was unable to locate it. After contacting UKB, I was informed that they were developing the system for releasing the data. To the best of my knowledge, the dataset remains unavailable. A major contribution of this work is the generation of an imputed SV resource for approximately 500,000 UKB participants with extensive phenotypic information. If this resource is not accessible to the research community, even to authorized UKB users, the practical impact and utility of the study are substantially diminished.

(2) Given that the imputed SV dataset is currently unavailable, it becomes even more important for the authors to provide a detailed, ready-to-run SV imputation pipeline for UKB-RAP, even if the "data processing simply consisted of running standard bioinformatics tools with the parameters exactly as described in the manuscript". In particular, the pipeline should include practical information such as computational requirements (e.g., memory and storage), expected running time, and estimated cost. Anyone with experience using UKB-RAP will agree that reproducing large-scale analyses on the platform can be both technically complex and financially expensive. Such pipeline would greatly improve the reproducibility and accessibility of this work.

Because my initial assessment of the manuscript was generally positive, I do not wish to change my overall evaluation, summary, or assessment of its strengths. However, I would view the work even more favorably if either (i) the imputed SV dataset became publicly available to authorized UKB users, or (ii) the authors extended their SV-GWAS analyses to the full range of UKB phenotypes and released the resulting summary statistics, analogous to the Pan UKBB ("https://pan.ukbb.broadinstitute.org/") resource. Although this would require considerable additional effort and computational resources, it would substantially enhance the long-term value and impact of the study.

Finally, I would like to emphasize that these comments are not intended to create unnecessary difficulties for the authors or the editors. Rather, I believe this highlights a broader issue in the use of this kind of large public datasets: reviewers cannot independently verify key results, and readers cannot readily build upon the work if the underlying resources are inaccessible, even after obtaining authorized access to the original dataset. I hope the authors, together with the eLife editors and UK Biobank where appropriate, can help facilitate the timely release of this valuable resource.

Reviewer #1 (Public review):

Summary:

The authors sought to develop a generalisable method for clearing and labelling large, highly complex human organs and tissues while preserving their three-dimensional structure, enabling visualisation at high resolution. The resulting body of work is substantial, encompassing a diverse range of tissues and labelling approaches, and demonstrates an impressive breadth of experimental work.

Strengths:

A major strength of the method is its systematic validation across a diverse range of human tissues, including several understudied tissues, in combination with labelling using multiple antibodies and fluorescent dyes. An additional strength is that the skin was retained on the finger throughout the clearing, labelling, and imaging procedures, allowing the tissue to be analysed in an intact state. This is particularly relevant to sensory neuroscience, where preserving the cutaneous sensory structures may be important. The use of tissue from donors aged 85 years and older is also a strength, as it provides a stringent test of the method in tissues with substantial age-related pigment accumulation and autofluorescence.

Weaknesses:

A major limitation is the lack of evidence that the method can be applied to formalin-fixed, paraffin-embedded (FFPE) tissue, which represents a substantial proportion of archived human tissue and is an important potential application of tissue-clearing approaches. Furthermore, the claim that the method is cost-effective is not sufficiently supported by the data presented, as there is no comparison of the costs of the proposed approach with those of existing methods.

Appraisal:

(1) Overall, I feel that the authors have broadly achieved their stated aims, although several aspects would benefit from further qualification or supporting evidence.

(2) Although magnetic resonance imaging (MRI) was performed on four tissues, the MRI data do not appear to be fully integrated with the microscopy data, and I did not find evidence of precise spatial correlation of structural information between the two modalities.

(3) The term "photoclearing" may be useful to describe the approach, but the underlying concept does not appear to be entirely novel, given that increased optical transparency can occur as a consequence of photobleaching. Furthermore, the evidence presented is not sufficient, in my view, to establish that the observed effects are attributable to photodegradation of pigments.

(4) I question whether the broader claims regarding the scalability of existing tissue-clearing approaches are sufficiently supported. In particular, the claim that aqueous- and hydrogel-based methods have limited scalability may require further evidence, given that perfusion-based approaches can facilitate processing of large tissue volumes. Similarly, the assertion that organic solvent-based approaches are better suited to large tissue volumes does not appear to be fully supported by the data presented, unless this refers specifically to the beneficial effects of tissue shrinkage during dehydration on imaging.

(5) More generally, a direct comparison of the clearing, labelling, and imaging outcomes for the thyroid samples fixed for 48 hours versus 8 years would be valuable for assessing the extent to which fixation duration influences the performance of the method.

Discussion:

The results have potential value for medical education, comparative anatomy, and research requiring the characterisation of human anatomy across spatial scales. The method could have applications across multiple disciplines and may be of interest to researchers who have access to human tissue from sources including archival material, biopsies, surgical resections, tissue banks, autopsy specimens, and donor tissue. However, the length and complexity of the protocol may limit its practical adoption, particularly in settings where throughput is an important consideration.

Context:

The results for the inner ear and ring finger are particularly notable because they demonstrate the ability of the method to clear, label, and image anatomically complex, highly calcified, and densely structured tissues. The successful clearing and immunolabelling of tissue fixed for 15 years is also significant, given the potential challenges associated with antibody penetration and preservation of epitopes following prolonged fixation. More broadly, successful imaging of large organs, such as the heart, is technically important given the challenges that their size and geometry present for light-sheet microscopy, and demonstrates the feasibility of applying the approach to intact human organs.

Technical concern:

The manuscript should acknowledge the hazardous and potentially toxic nature of several reagents used in the protocol, together with the challenges of safely handling and disposing of the relatively large volumes of chemical waste generated. These factors may have practical implications for implementation of the method.

Conceptual concerns:

The role and added value of photogrammetry in the study are not entirely clear. It would be helpful for the authors to clarify how photogrammetry was used beyond its presentation in the figures and what additional information or utility it provides relative to the other imaging modalities employed.

Reviewer #2 (Public review):

Summary:

The authors claim to present a generally applicable tissue processing pipeline for optical tissue clearing and labelling of whole human organs. To achieve this, they combine multiple previously published tissue pretreatment steps to enhance tissue permeabilization, and hence label penetration, as well as optical transparency. Most notably, the authors include LED photobleaching, or photoclearing as they call it here, to reduce both autofluorescent background and increase tissue transparency. Extending their previously published method towards a wide variety of large human samples encompassing multiple organs and tissues, they combine their clearing protocol with several small molecule dyes for general overview stains as well as immunofluorescence labelling. For some of the processed samples, they introduce a novel multimodal imaging pipeline, which includes photogrammetry, MRI, and 3D histology/microscopy. Both the multimodal pipeline and the described tissue clearing and labelling protocols seem highly useful for both pathology as well as fundamental research, especially since the modularity of tissue-clearing protocols allows for the integration of individual steps, such as photoclearing, into already established methods.

Strengths:

The transparency of the large, archival human samples is very impressive and, to my knowledge, constitutes the best human tissue clearing to date. The positive effects of photobleaching/clearing on autofluorescence reduction as well as transparency are obvious and highly interesting for the field, as this method can easily be implemented into any tissue clearing approach. It is highly appreciated that notes are provided in both the methods and results, on which steps of the pipeline had to be adjusted for different tissue types and sizes. However, this could be presented in a more structured way, by showing a graphical representation or at least a table of all used tissues and all the steps of the pipeline, with indications for which steps were skipped/adjusted per tissue type as well as the incubation times for every step. Table 2 already does that for light exposure and decalcification times, but it would be beneficial to do this for all steps to get a better overview. This would also aid replication and implementation of their method, as other groups can just look up the closest matching tissue type in the table and go from there rather than piecing this information together with the in-text notes.

The combination of different small molecule dyes, while in itself not new, has the potential to provide 3D alternatives for conventional histological overview stains. Other groups have already shown 3D H&E and Nissl stains, and it would be interesting what other routinely used stains could be mimicked in that way. Here, the combination of Eosin Y and Fast Green seems especially interesting.

The quality of the immunofluorescence labelling is extremely good, especially given the age of some of the samples (e.g. very high-quality SMA staining in 15-year-old material). It would be interesting to know if the authors encountered antibodies that were not compatible with their archival tissue and, if so, which ones.

Weaknesses:

It is not exactly clear to me how some of the image volumes were acquired. For example, the panels 1f-h: The regions these volumes originate from are indicated in the cleared heart (1e), but were these regions blocked out or was the entire heart somehow immersed in the imaging chamber? The latter would be, to the best of my knowledge, a novel scale of light sheet imaging and should be mentioned. If the regions were somehow blocked out, this should be described. In general, a lot of the imaging volumes seemed to have been acquired mainly towards the periphery of the sample, especially the higher magnification inserts. This immediately raises the question of whether this is because imaging was not possible in the centre and why (limitation of the imaging chamber size, light penetration, label penetration, or a combination of those?). While it is understandable that it is currently not possible to image, e.g. entire kidneys in light-sheet set-ups, the limits of feasible sample sizes should be mentioned somewhere to give the reader a better appreciation of the usefulness of the method. The authors demonstrate that it is possible to clear whole organs, but is it also possible to label whole organs? Is that possible with antibodies as well, or only with small-molecule dyes? And how deep can samples be imaged in the best-case scenario? Right now, the paper uses a common scheme in the tissue clearing literature, of showing a very large cleared sample and then imaging a smaller sub-volume while implying that, in principle, it is possible to do that for the entire organ, if the objective working distance and imaging chamber would allow. However, to scale their method up, the authors would first need to show that their labels would penetrate throughout the entire sample, and this is currently not done in an unambiguous manner.

The biggest limitation in the manuscript for me is the authors' claim: "We demonstrate the voxel-by-voxel alignment between MRI and microscopy datasets, merging cellular-scale detail and protein-specific labelling with macroscopic medical imaging." While technically true, the authors only show actual overlays of microscopy and MRI data for the inner ear sample in Figure 5. No overlays between MRI and the microscopy volumes are shown for the heart and finger data, which is a missed opportunity. Similarly, no overlays between all three acquired modalities (photogrammetry, MRI, 3D microscopy) are shown for any of the samples. This is a pity, as the authors put a lot of emphasis on this novel multimodal pipeline, even though side-by-side demonstrations of MRI and 3D microscopy in a similar manner have been shown already by other groups and a truly multimodal dataset with the different modalities, e.g. as different channels in a volume, would be very exciting.

Reviewer #1 (Public review):

Summary:

The authors introduce a foraging task designed to test whether movement and harvesting durations are governed by a common objective combining reward, effort, and time or by separate objectives. Participants generate wrist torque to move a cursor to a rewarding patch and then hold it within the patch while reward accumulates at a diminishing rate. The task allows reach and harvest effort, as well as delays before or between the two phases, to be manipulated separately.

Reach effort strongly affected reach duration but had little effect on harvest duration, whereas a delay imposed after reaching altered harvest duration without affecting the completed reach. Manipulation of harvest effort did not affect either duration. The authors also found consistency across individuals within each type of duration but no reliable association between reach and harvest durations. The separate model fit the behavioral results better than the common-utility model, particularly for the post-reach delay condition. The findings therefore support partly dissociable, but coupled optimization of harvest and movement in this task, while not excluding common optimization in other contexts.

Strengths:

The task provides a controlled way to manipulate the effort and delays associated with reaching and harvesting while measuring both durations. The control experiments alter the timing of delays, allowing the experimenter to test whether their effects depend on when they occur. These manipulations produce clear behavioral dissociations, particularly the selective effect of a post-reach delay on harvest duration. The delay and effort manipulations were verified, and most participants reported noticing the changes in effort and time.

The separate model extends a previous cost-of-time framework to a foraging task involving movement and reward harvesting. Its assumptions have a clear relationship to the experimental design: applied delays and actions enter the time offset for each separate cost function. This provides an intuitive account of why a delay occurring after the reach can affect harvesting without affecting the completed movement. The separate model also provides a better fit than the common utility model in both modeled experiments.

The individual-level behavioral analyses are also useful. Reach durations are correlated across reach conditions, and harvest durations are correlated across harvest conditions, indicating stable individual differences within each measure. The lack of a corresponding relationship between reach and harvest durations raises an important question about whether the two forms of vigor necessarily reflect a common individual tendency in their task.

Weaknesses:

The block design and familiarization made the changes in effort and delay learnable, and most participants reported awareness of these manipulations. The observed dissociation may reflect adaptation to this task structure. This does not weaken the behavioral result, but it limits how directly the findings can be generalized to tasks in which changes in reward, effort, or time are less explicit.

The main modeling limitation is that both models are fitted to ten group-level median observations in each experiment, rather than to individuals' behavior. The separate model has seven fitted parameters compared with three in the common model. Although the reported AIC penalizes additional parameters, the analysis includes no participant-level fitting, resampling, or cross-validation.

Reviewer #2 (Public review):

Summary:

The manuscript by Conessa and colleagues tests whether movement time and decision time are co-regulated in humans using a novel harvesting paradigm and computational modelling of the behavioral data. The data contradict the common utility model and are better supported by an alternative model where the costs of the harvesting and movement phases are optimized separately - rather than jointly.

Strengths:

The major strength of the study is the development of the novel paradigm where the forces applied during the distinct phases of the task (reaching and harvesting) can be perfectly controlled and measured.

This elegant manipulation allows precise estimation of subjective effort costs, and later can be used to better understand how these costs shape behavior.

The novel separate-cost model is also an interesting development.

Weaknesses:

In my opinion, the manuscript suffers from too many weaknesses to solidly support the general conclusions:

(1) The manuscript oversells the significance of the results;

(2) The novel model appears to be built ad hoc based on the results, and its ingredients are poorly motivated

(3) There are important methodological shortcomings. I develop all of these points below. The paper also lacks clarity, particularly when presenting the key concepts of the novel model.

Importantly, I also recommend that the authors follow open science policy and publish their data and code on a public repository.

(1) Significance

As mentioned above, the question of the co-regulation of the vigor of different behaviors is a very interesting topic, but I believe the significance of the results is overstated, for different reasons:

a) This is a harvesting task, which means that decisions are specifically about the duration of the reward period. In other words, more time directly provides more (immediate) reward, whereas in other types of tasks more time allows gathering and processing more information, and so reaching a more informed decision, which is a more indirect way of securing better outcomes - see e.g. Drugowitsch, Moreno-Bote et al. JNeurosci 2012 for optimizing decision time in this most common setting. This major difference is not discussed in the manuscript, and it is not clear whether the results found here would hold for the most common type of decisions. This is also different from the time to initiate a response, as explored by Morvan et al. in their cited preprint.

b) The title of the study mentions "flexible" co-regulation, but it's hard to see direct evidence for flexibility in the results. This flexibility is extrapolated in the Discussion, but in order to make such a statement, it is necessary to show that the co-regulation differs between different conditions, as predicted from the model.

c) The lack of impact of the harvesting effort on harvest time is very surprising, and the null value of the sensitivity to effort (d=0) in the model is intellectually uncomfortable. As some value of effort, it SHOULD matter. I am not very satisfied with the explanation provided in the Discussion ("possible hypothesis would be that the perceived effort of harvest was outweighed by the reward value"): this trade-off should be precisely dealt with by the model.

(2) Separate-Cost Model

The separate-cost model is poorly motivated and not clearly presented, in particular the indirect coupling between the two phases.

a) Some key components are motivated by the constraint to obtain a well-behaved optimization problem ('we need to find a cost that increases with time' ) rather than based on cognitive principles. Some other key components seem to have been placed there just to fit the data better, but their plausibility is not even discussed. Notably:<br /> i- The fact that the offset o_h includes the reaching delay is key to the coupling between t_h and t_r, but is not properly motivated. Why should this offset include all preceding intervals within the trial (leading to double counting of the cost of the reaching phase, in both G_r and G_d)? In this cyclic paradigm where participants aim at maximizing cumulative reward, it is not even clear that they parse behavior into different trials starting as they need to reach for a new target.<br /> ii- Why is there a free parameter d for the cost of harvest effort? If time and motor costs are converted into the same currency, and that conversion holds for all types of phases, then I believe we should have d=1. This free parameter seems to have been introduced a posteriori to accommodate the lack of effect of harvest effort on harvest time, but is not motivated.

b) The two models differ in two fundamental aspects: whether optimization is run separately on the different phases of the trial, or jointly; and how the different costs and rewards are assembled in the to-be-optimized metric. Which aspect is more important to capture behavior is not assessed.

c) The presentation of the "Separate-cost model" is very obscure. For example, the notion of a `cost of reward` is rather odd, and consequently the formula for R(t_h) appears arbitrary. I understand that this is the difference between the maximum reward that can be collected within a trial and the actual reward that is collected, but it is not even presented as such. The effort cost of harvesting seems to be discarded in the model presentation but does appear in equation 14.

(3) Methodological Weaknesses

I believe that there are numerous methodological weaknesses that really limit the inferences that can be drawn from the experimental and modelling results.

a) Sample sizes are small, especially for control experiments, and it is not clear how they have been selected. This is especially problematic because the only manipulation that shows no significant effect on behavior (harvest duration) is only tested with the smallest sample size (n=10), severely limiting the significance of this negative result.

b) The rationale for the different manipulations in different experiments is not clear. Notably, why were modulations of the harvest effort not included in the main experiment? Because not a single participant sees a modulation of both reach and harvest efforts, we cannot evaluate whether the model can capture both effects at the same time (i.e., with the same parameter values). The number of data points used for fitting directly depends on the number of conditions performed by the participant, and is very low compared to the number of parameters to be fitted. For example, the model used very different shapes for the costs of time (Figure 8) for different sets of conditions, but this cost of time should be fixed, so it's not clear whether a single cost of time function can accommodate all manipulations.

c) Best practice in behavioral modelling is to model single-subject data, as fitting the model jointly to all subjects completely obliterates subject heterogeneity. Fitting on single-subject data would also allow investigating whether the models reproduce the consistency of harvest durations and reach durations across conditions, and most importantly the absence of correlation across subjects between reach and harvest duration. At the moment, we're left wondering what the implications of these analyses for the original question are.

d) What is the rationale for comparing reach duration in one condition to harvest duration in another condition?

e) The study does not take into account the likely impact of delays on muscular fatigue and perceived effort: the effort associated with maintaining the cursor on target during harvest might be perceived as less effortful after a longer break, partially explaining the impact of delay on harvest duration.

f) I am confused by the reference to indirect effects in the separate-cost model (L692-7, Table 2). To fit this model, was the experimental value or theoretical value of the reach duration t_d used to determine the optimal harvest value (from Equation 14)? In both cases, the reach duration DOES increase with reach effort, so we should expect an impact on the harvest duration. This is indeed seen in Figure 7A. So why does Table 2 suggest that reach effort should not impact harvest duration in this model?

g) Could the effect of pre-reach delay on reach time be alternatively explained simply by longer reaction times as reported in Figure S2, e.g., a longer period to reactivate the muscles after a longer break? In other words, as far as I understood, here reaction times are subsumed in the motor time, against the tradition of splitting them into two independent (non-overlapping) behavioral metrics.

h) The EMG-time integral in the harvest phase should be largely proportional to the harvest duration, given that the applied torque is constrained to remain on target. Is this the case? If so, then how to interpret the significant effect of reach effort on this value, given that the main analyses did not identify an effect of reach effort on harvest duration?

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.

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.

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.

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.

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.

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.

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.

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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.

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.

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.

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.

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.

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.

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.

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.

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.