Reviewer #1 (Public review):

Summary:

The authors present MiPS, a platform combining DMD-based patterned illumination, automated microscopy, retrained DeLTA segmentation, and mother-machine microfluidics to selectively inhibit or eliminate cells based on dynamic phenotypes. The system enables targeted UV or red-light illumination in real time using segmentation-informed projection masks, allowing selective enrichment directly within mother-machine devices. The manuscript demonstrates proof-of-concept enrichment of mCherry cells from mixed GFP/mCherry populations, characterizes off-target effects, and performs computational simulations of iterative enrichment rounds. Overall, the engineering and systems integration are impressive, and the platform has strong potential for applications in directed evolution, biosensor optimization, and dynamic phenotype-based selection workflows.

Overall, I believe the work is suitable for publication after minor revisions and clarification of several aspects of the manuscript. In particular, the paper would benefit from additional context in the Introduction and Methods sections, clearer positioning relative to existing platforms, improved figure readability/captions, and a more careful revision of the English throughout the manuscript.

Major comments:

(1) The manuscript should better position MiPS relative to recent microscopy-based and DMD-enabled selection/control systems, particularly Lugagne et al., Nature Communications (2024), DOI: 10.1038/s41467-024-46361-1. That work also combines mother-machine microfluidics, DeLTA-based real-time image analysis, and DMD projection. The key distinction here appears to be physical selection/enrichment through targeted killing rather than optogenetic control, and this difference should be stated more explicitly.

(2) The manuscript currently compares MiPS mostly to FACS/MACS. However, the more relevant comparison may be recent image-based and microfluidic photoselection systems. A dedicated comparison table discussing throughput, temporal phenotyping, iterative selection, dynamic phenotype tracking, and enrichment capabilities would strengthen the paper.

(3) The enrichment experiment in Figure 4 represents a relatively simple classification problem (GFP vs mCherry). Since the proposed applications involve subtle continuous phenotypes, it would considerably strengthen the manuscript to include at least one experiment selecting for high vs. low expressors within a single fluorescent reporter population.

(4) The strongest enrichment result (~170-fold enrichment in Figure 5) is entirely simulation-based. Since the manuscript already states that ~45 min is sufficient between rounds for growth evaluation, a real 2-3-round enrichment experiment seems feasible and would substantially strengthen the platform's practical relevance. This experiment appears realistic within a relatively short time investment.

(5) The bimodal distributions in Figure 2 suggest that a fraction of cells may be stress-resistant rather than simply surviving randomly. It would be useful to discuss whether repeated rounds could progressively enrich UV-resistant subpopulations.

(6) The manuscript repeatedly uses the term "killed," although the data shown in Figures 2 and 4 mostly demonstrate strong growth arrest/inhibition. Please clarify how the cutoff of division rate <0.4 h⁻¹ was selected and whether an independent viability assay was performed.

(7) The off-target analysis in Figure 3 is one of the strongest parts of the paper and should probably be emphasized more. The conclusion that the dominant effects are global rather than local is interesting, but additional discussion about optical scattering, ROS diffusion, or device-wide coupling effects would strengthen the interpretation.

(8) UV exposure is inherently mutagenic in E. coli, and untargeted cells still receive a substantial fraction of the UV dose at high targeting fractions. Please discuss whether the MB/red-light modality may be preferable in applications where preserving genotype integrity is important.

(9) The manuscript discusses that methylene blue (MB) improves the on:off target ratio, but MB also appears to reduce baseline growth by ~40% even without red-light exposure. This is potentially important for iterative selection workflows. Please discuss whether this effect is reversible after washout and how rapidly cells recover.

(10) The manuscript states that the retrained DeLTA model used ~3,000 annotated fluorescence images, but no train/validation/test split or segmentation performance metrics are reported. Since segmentation directly impacts phenotype classification and projection targeting, these details are important for reproducibility.

(11) The manuscript would benefit from a stronger Methods description regarding DMD calibration, alignment procedures, projection accuracy validation, and computational timing requirements for the real-time analysis pipeline.

Significance:

General assessment: This is a creative and technically impressive study that combines mother-machine microfluidics, automated microscopy, real-time image analysis, and DMD-based photoselection into a unified platform for dynamic, phenotype-based enrichment. The strongest aspects of the work are the systems integration, the quantitative characterization of off-target effects, and the conceptual demonstration that dynamic microscopy-derived phenotypes can be linked to physical enrichment workflows.

The main limitations are that the biological validation remains largely proof-of-concept and the most compelling enrichment results are currently simulation-based rather than experimentally demonstrated across multiple rounds. In addition, the manuscript would benefit from stronger positioning relative to recent image-based and DMD-enabled microfluidic control systems.

Advance: The study extends the field of single-cell microfluidics and image-based selection by introducing a platform that links longitudinal microscopy measurements directly to physical enrichment decisions within mother-machine devices. To my knowledge, the combination of iterative feedback-driven selection, DMD-based targeted elimination, and dynamic phenotype tracking in this context is novel.

The closest related systems appear to be recent DMD-enabled mother-machine platforms for real-time optogenetic control, particularly those reported by Lugagne et al. (Nature Communications 2024, DOI: 10.1038/s41467-024-46361-1). However, MiPS introduces a distinct conceptual advance by using patterned illumination for selective enrichment/elimination rather than gene-expression modulation alone.

The advance is primarily technical and conceptual, with potential downstream applications in directed evolution, synthetic biology, biosensor engineering, and dynamic phenotype screening workflows that are difficult or impossible to implement using FACS alone.

Audience: The work will likely be of strongest interest to researchers working in synthetic biology, microfluidics, single-cell analysis, systems biology, bioengineering, and automated microscopy. It may also be of broader interest to communities developing dynamic phenotype screening technologies, closed-loop biological control systems, and next-generation directed evolution platforms.

The audience is likely specialized but multidisciplinary, spanning both engineering-oriented and biology-oriented researchers. The methods and conceptual framework may also influence future development of automated selection systems beyond the specific mother-machine context.

Expertise - My expertise includes: Microfluidics, Synthetic biology, Single-cell systems, Automated microscopy, Real-time image analysis, Bioengineering platforms, Dynamic phenotype characterization.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors reported Microscopic PhotoSelection (MiPS), a closed-loop automated robotic platform designed to link time-resolved imaging with physical sample recovery in mother machine microfluidic devices. By pairing a standard mother machine layout with a custom DMD optical path, an LED array, and an optimized DeLTA deep-learning model, the system tracks dynamic single-cell phenotypes and isolates specific cells via automated, targeted phototoxicity, i.e. selection by elimination. This is a novel technical development that addresses a clear limitation of snapshot sorting methods like FACS or MACS when screening for time-resolved, lineage-dependent traits. However, several methodological limitations and presentation errors must be addressed before publication.

Major Comments:

(1) Definition of 'Optimal' Dose (Figure 2D): The authors identify 8.0 W*cm-2 UV light for 300s as the optimal condition. However, this data point lies at the absolute boundary of the tested parameter space. In classical dose-response characterization, an optimum is defined by a local peak or a plateau followed by a decline in performance (typically due to rising off-target toxicity or scatter). Because the performance curve has not rolled over, this represents a boundary condition rather than a demonstrated mathematical optimum. The authors should either extend the parameter sweep to locate the true peak or soften their language to reflect that this is simply the highest performing condition tested.

(2) UV Exposure Time Gap: The exposure time sweep skips directly from 60s to 300s. While the closely spaced early timepoints are appropriate for capturing initial cell-death kinetics, the large gap to 300s leaves a significant engineering blind spot. Figure 3D demonstrates that off-target scattering damage scales linearly with cumulative light energy. If complete target cell arrest can be achieved at an intermediate exposure (e.g., 120s, 180s or 240s), operating the system at 300s unnecessarily subjects neighboring "surviving" cells to secondary global UV stress via device-wide scattering. An intermediate temporal sweep is recommended to optimize the selection window and properly balance target lethality with background library viability.

(3) Baseline Chemical Toxicity of Methylene Blue (MB): The photosensitizer workflow shows a clear improvement in contrast at lower power densities and exposure times. However, lines 151-153 note that the addition of 2 uM MB alone, even without light activation, stunts the baseline bacterial growth rate by ~40%. This is a major biological confounder. For applications like directed evolution or dynamic physiological screening, introducing a chemical stressor that nearly halves fitness imposes an unintended selective pressure. This baseline stress may activate pathways that mask or alter the phenotypes of interest. The authors must expand their discussion on how this baseline toxicity impacts multi-round iterative selections, and should ideally evaluate lower concentrations (e.g., 0.5uM or 1uM) or alternative photosensitizers to identify a more viable operational window.

(4) Negative Selection Framework and Search Space Scale: The MiPS platform relies entirely on negative selection by destroying unwanted variants. While effective for the demonstrated 1:1 binary proof-of-concept mixture, negative selection scales poorly when screening for rare variants within large libraries. For instance, isolating a single high performer from a library of 105 cells requires the system to successfully target and kill 99,999 individual cells; any statistical leak or failure in killing efficiency directly leads to heavy contamination of the recovered sample. The Discussion section requires a quantitative evaluation of these search space constraints, outlining how they limit the system's utility compared to positive selection mechanisms (such as optical tweezers or droplet sorters) when scaling to rare mutations (<1 in 104).

Significance:

This study presents a significant methodological advance in single-cell analysis and microfluidics by integrating long-term live-cell imaging, automated image analysis, and phenotype-guided cell recovery into a closed-loop platform. Existing approaches such as FACS and MACS are largely limited to endpoint or snapshot measurements, whereas MiPS enables selection based on dynamic and lineage-dependent cellular behaviors, thereby addressing an important gap in current single-cell screening technologies.

A key strength is the effective integration of mother machine microfluidics, custom optics, and deep-learning-based tracking into an automated and functional system. While the individual components are established, their combination into a phenotype-driven selection platform is innovative and expands the utility of live-cell microscopy from passive observation to active cell selection. The advance is therefore primarily methodological and technological, with potential to enable future conceptual discoveries in cellular heterogeneity and lineage dynamics.

However, limitations remain regarding scalability, robustness, selection accuracy, and generalizability across biological systems. Additional benchmarking and validation would strengthen the work further.

Overall, the study will be of interest to researchers in microfluidics, single-cell biology, microbial systems biology, bioengineering, quantitative imaging, and synthetic biology.

My expertise is in microfluidics, cell sorting and disease mechanobiology.

Reviewer #3 (Public review):

Summary:

The work describes an optofluidic automation setup to optically inhibit and enrich selected bacterial populations in confined microchannels through negative selection using light stimulation. The work is well described and the manuscript is well constructed.

Major comment:

The authors reported that methylene blue with 2uM incubation has superior performance than UV light. But it's also noted on line 152 there is an inhibition effect from the chemical affecting ~40% of the growth rate.

It will be noteworthy what is the growth curve or at least the MIC of methylene blue used on the MG1655 E. coli by the authors.

Significance:

The optics part of the work is well described, however the materials and methods details of the biological and microfluidic part can be extended.

Overall, the system demonstrated the practical use of combining microfluidics for enrichment of microbial population as a novel alternative method, despite that the efficiency is currently subpar to conventional methods.

But combining further with deep learning phenotype or growth rate monitoring, the technology represents a new path for phenotypic selection which is also novel that conventional methods cannot offer. The work will benefit readers in applied science seeking for new target enrichment based on optofluidics.

Reviewer #1 (Public review):

Summary:

The authors hypothesized that "RVM neurons operate across multiple temporal scales, integrating fast responses associated with reflex-linked control with slower fluctuations reflecting ongoing network or state-dependent modulation". The hypothesis was tested with the established ON/OFF-cell model and probabilistic modeling. The study is conceptually interesting and methodologically sophisticated. The findings build toward the conclusion that pain-control circuits operate across multiple timescales.

Strengths:

The use of Bayesian regression and Gaussian process modeling to quantify and characterize recovery dynamics and ongoing oscillatory activity.

The authors show that slow rhythmic activity appears preferentially in ON- and OFF-cells but not in NEUTRAL-cells, suggesting that the oscillations are related to pain-modulatory circuitry rather than being a generic feature of all recorded neurons.

The observation that some oscillatory activity is coherent with autonomic measures aligns with broader views of the RVM as a hub integrating nociceptive and homeostatic regulation.

Some pitfalls are appreciated and discussed by the authors, including the functional significance of slow fluctuations, the influence of anesthetics on global brain-state dynamics, the molecular profiles of the studied ON- and OFF-cells, and the heart rate as a covarying signal of RVM neuronal activity.

Weaknesses:

A general weakness is that the work is mostly descriptive and relies on anesthetized preparations. Whether the observed rhythms occur in awake animals and are linked to fluctuations in pain behavior needs to be confirmed in future studies.

The study measures limited autonomic variables. The causal relationship between "slow fluctuations" and "ongoing physiological state" is unclear and overstated, since the data presented appear correlational.

ON- and OFF-cells in the RVM are identified by their responses correlated with reflexive activity. The significance of the observed oscillations in spontaneous pain conditions is unclear.

It is uncertain whether the observed rhythms truly reflect intrinsic RVM organization rather than anesthesia-dependent phenomena; the authors appreciated this pitfall, though.

The Gaussian process analysis suggests predictability and quasi-periodicity, but predictability alone does not necessarily imply a true biological oscillator.

Conclusion:

The results support the authors' hypothesis. The findings provide a compelling conceptual message about the multiscale organization and dynamics of descending pain-control circuits and encourage further studies on the topic.

Reviewer #2 (Public review):

Using electrophysiological recordings in a well-characterized animal model of acute pain, and analytical and modeling methods, the authors show that descending pain-modulatory neurons in the rostral ventromedial medulla (RVM) operate across various timescales. They have both rapid multi-phase responses to noxious stimuli that unfold over tens of seconds, with distinct fast and slow recovery dynamics. Additionally, they generate slow quasi-periodic oscillations with approximately 5-minute periods during ongoing activity. These oscillations are statistically predictable and cell-type specific, demonstrating that descending pain control is organized through structured temporal dynamics that encompass immediate stimulus-evoked responses and slower fluctuations associated with physiological state.

A novel discovery is a ~5-minute quasi-periodic oscillation in ongoing ON- and OFF-cell activity. This oscillation, along with its coherence with heart rate, forms the basis for the claim that descending pain circuits exhibit intrinsic multi-timescale organization. However, it's crucial to demonstrate that this periodicity is independent of external experimental cycles such as methohexital infusion pharmacokinetics, servo-controlled temperature regulation, or slow autonomic feedback loops, all of which operate on similar timescales. For instance, the 300-second period closely matches typical drug infusion cycling and thermoregulatory feedback intervals. Therefore, heart-rate coherence peaks at multiples of this period could equally reflect a shared external driver rather than intrinsic RVM organization. Although the absence of this cyclic structure in Neutral cells argues against this possibility, the authors might want to explicitly discuss this potential confound.

The findings are important and novel in that they characterize an intriguing structure in the activity of ON and OFF neurons in the RVM. However, in the absence of a causal manipulation causality can only be inferred. That there is no phase-dependence of withdrawal latency argues against a causal role. The author are encouraged to qualify their conclusions (and their title) accordingly.

Because anesthesia can affect global dynamics, this might affect the oscillations reported. Without awake validation, it remains uncertain whether these rhythms reflect an intrinsic property or an anesthesia-induced regime. Again, the absence of oscillations in Neutral cells argues against this possibility, but it is still possible that ON/OFF cells are embedded in different circuits that are affected differently by anesthesia.

Analyses of many of the ON-cells had longer training windows (>1 sec) compared to those for the NEUTRAL cells. Could this have reduced the ability to fit and validate periodicity for the latter cell type?

Reviewer #3 (Public review):

Summary:

In this manuscript by Ashworth and colleagues, the authors investigate the temporal dynamics of the rostral ventromedial medulla (RVM), a key output node in a major descending pain-modulation circuit. Using data from extrasellar single-unit recordings of RVM ON, OFF, and NEUTRAL cells in lightly anesthetized rats, the authors' computational modeling yielded two major findings: (1) heat-evoked ON burst and OFF pause, followed by exponential recovery components in10s of seconds; and (2) ON and OFF cells exhibit periodic fluctuations in ~5-minute cycles that are statistically predictable.

Strengths:

The manuscript's concept is innovative, offering the first quantitative analysis of multi-timescale dynamics in physiologically characterized RVM pain-modulating neurons. This advances a field that has mostly depended on qualitative or single-timescale descriptions. The authors use contemporary Gaussian process and probabilistic models to capture statistically predictable slow dynamics. The study is further strengthened by identifying ON-, OFF-, and NEUTRAL-type cells using well-established criteria grounded in decades of RVM research. The combination of rapid reflex-related responses and slower ongoing rhythms supports a dual-timescale framework, providing a more integrated understanding of how these neurons may regulate reflex activity and state-dependent processes.

Weaknesses:

Several limitations are noted. Incomplete characterization of light anesthesia during recording sessions, such as methohexital stability and clear criteria for identifying "lightly anesthetized" states. While the NEUTRAL cell control is helpful, it does not fully address concerns about circuit specificity or systemic confounds. The findings are male-dominant, which may limit their generalizability. The synchrony between ON and OFF cells was suggested but not directly tested. The heart rate coherence with ON, OFF, and NEUTRAL cell activity results is intriguing but does not fully clarify how these neurons influence heart rate, particularly within the "lightly anesthetized" model.

Reviewer #1 (Public review):

Summary:

Liao et al. present SCOPE (Spatial reConstruction via Oligonucleotide Proximity Encoding), a method for reconstructing spatial organization from diffusion-defined DNA barcode interactions without the use of optical imaging. In SCOPE, hydrogel beads bearing unique DNA barcodes contain both "sender" and "receiver" oligonucleotides. Upon enzymatic release, sender oligos diffuse locally and hybridize to receiver oligos on neighboring beads, forming chimeric molecules that encode spatial proximity. Sequencing these products yields an interaction matrix, which is then used to reconstruct a spatial coordinate map.

The authors demonstrate reconstruction of synthetic two-dimensional shapes, a large multicolor Snellen eye chart, and the interior surface of three-dimensional molds. The work expands the conceptual and experimental landscape of optics-free spatial sequencing.

Strengths:

SCOPE employs bidirectional sender and receiver oligonucleotides on every bead, rather than using asymmetric transmitter-receiver architectures found in other diffusion-based methods. The symmetric design may improve detection sensitivity and reconstruction strategies, and represents a meaningful variation on optics-free spatial encoding.

A notable strength of this study is the physical scale achieved. The authors reconstruct a Snellen chart spanning approximately 704 mm² and demonstrate molded 3D structures on the order of 75-100 mm³. Although some larger-scale warping is evident, and is discussed as potentially due to non-uniform diffusion, the relative local positioning across these large areas appears impressively accurate.

The authors extend reconstruction beyond two-dimensional arrays to three-dimensional molded surfaces. This demonstrates that the assay and the computational methods for interpreting proximity graphs can support non-planar spatial relationships, expanding the scope of optics-free spatial inference.

The revised manuscript also strengthens the interpretation of these three-dimensional experiments by providing additional evidence that the limited recovery of interior regions primarily reflects technical constraints associated with molecular recovery from the hydrogel beads on the interior rather than an inherent limitation of the SCOPE framework.

Weaknesses:

Although the method is discussed in the context of spatial genomics and potential tissue applications, it is currently demonstrated only on engineered two-dimensional bead arrays and three-dimensional shapes fabricated in molds. The authors appropriately acknowledge that additional work will be required to establish performance in heterogeneous biological tissues, where diffusion and molecular recovery are likely to be more complex.

The revised manuscript substantially clarifies the limitations of the current three-dimensional implementation by providing additional discussion and control experiments supporting the interpretation that reduced recovery of interior beads is primarily a technical limitation of the present protocol. Although limited volumetric sampling remains a current constraint of the method, the authors appropriately discuss applications in which surface-resolved reconstruction may still be informative.

The computational reconstruction workflow is now described in greater detail, including automated parameter selection, fixed versus optimized hyperparameters, and explicit discussion of the manual flattening step required for the largest Snellen reconstruction. The revised manuscript also explains that many anticipated tissue-section applications present a more constrained reconstruction problem than the intentionally challenging proof-of-concept demonstrations presented here, providing additional context for the expected performance of the method in future biological applications.

Reviewer #1 (Public review):

Summary:

This study by Akhtar et al. aims to investigate the link between systemic metabolism and respiratory demands, and how sleep and circadian clock regulate metabolic states and respiratory dynamics. The authors leverage genetic mutants that are defective in sleep and circadian behavior in combination with indirect respirometry and steady-state LC-MS-based metabolomics to address this question in the Drosophila model.

First, the authors performed respirometry (on groups of 25 flies) to measure oxygen consumption (VO2) and carbon dioxide production (VCO2) to calculate the respiratory quotient (RQ) across the 24-hour day (12h:12h light-dark cycle) and assess metabolic fuel utilization. They observed that among all the genotypes tested, wild type (WT) flies and per0 flies in LD and WT flies in DD exhibit RQ >1. They concluded the >1 RQ is consistent with active lipogenesis. In contrast, the short-sleep mutants fumin (fmn) and sleepless (sss) showed significantly different RQ; the fmn exhibits a slight reduction in RQ values, suggesting increased reliance on carbohydrate metabolism, while sss exhibit even lower RQ (0.94), consistent with a shift toward lipid and protein catabolism.

The authors then proceeded to bin these measurements in 12-hour partitions, ZT0-12 and ZT12-24, to assess diurnal differences in average values of VO2, VCO2, and RQ. They observed significant day-night differences in metabolic rates in WT-LD flies, with higher rates during the day. The diurnal differences remain in the short-sleep mutants, but the overall metabolic rates are higher. WT-DD flies exhibit the lowest respiratory activity although the day-night differences remain in free-running conditions. Finally, per01 mutants exhibit no significant change in day-night respiratory rates, suggesting that a functional circadian clock is necessary for diurnal differences in metabolic rates.

They then performed finer resolution 24-hours rhythmic analysis (RAIN and JTK) to determine if VO2, VCO2, and RQ exhibit 24-hour rhythmic and if there are genotype-specific differences. Based on their criteria, VCO2 is rhythmic in all conditions tested while VO2 is rhythmic in all conditions except in fmn-LD. Finally, RQ is rhythmic in all 3 mutants but not in WT-LD and WT-DD. Peak phases for the rhythms were deduced using JTK lag values.

The authors proceeded to leverage a previously published steady-state metabolite datasets to investigate potential association of RQ with metabolite profiles. Spearman correlation was performed to identify metabolites that exhibit coupling to respiratory output. Positive and negative lag analysis were subsequently performed to further characterize these associations based on the timing of the metabolite peak changes relative to RQ fluctuations. The authors suggest that a positive lag indicates that metabolite changes occur after shifts in RQ, and a negative lag signifies that metabolite changes precede RQ changes. To visualize metabolic pathways that exhibit these temporal relationships, clustered heatmap and enrichment analysis were performed. Through these analyses, they concluded that both sleep and circadian systems are essential for aligning metabolic substrate selection with energy demands, and different metabolic pathways are misregulated in the different mutants with sleep and circadian defects.

Strength:

The research questions this study explore are significant given metabolism and respiratory demand are central to animal biology. The experimental methods used, including the well characterized fly genetic mutants, the newly developed method for indirect calorimetry measurements, and LC-MS based metabolomics, are all appropriate. This study provides insights into the impact of sleep and circadian rhythm disruption on metabolism and respiratory demand and serves as a foundation for future mechanistic investigations.

Comments on revised version.

The authors have thoughtfully revised the manuscript. They have now provided clarifications regarding perceived conceptual flaws in the original version. They have also performed additional data analysis to support their conclusions and provide clarifications on statistical methods when appropriate. Overall, the revised manuscript is much improved and the conclusions are generally well supported by their results.

Reviewer #2 (Public review):

This is an innovative and technically strong study that integrates dual-gas respirometry with LC-MS metabolomics to examine how sleep and circadian disruption shape metabolism in Drosophila. The combination of continuous O₂/CO₂ measurements with high-temporal-resolution metabolite profiling is novel and provides fresh insight into how wild-type flies maintain anticipatory fuel alignment, while mutants shift to reactive or misaligned metabolism. The use of lag-shift correlation analysis is particularly clever, as it highlights temporal coordination rather than static associations. Together, the findings advance our understanding of how circadian clocks and sleep contribute to metabolic efficiency and redox balance.

However, there are several areas where the manuscript could be strengthened. The authors should acknowledge that their findings may be gene-specific. Because sleep deprivation was not performed, it remains uncertain whether the observed metabolic shifts generalize to sleep loss broadly or are restricted to the fmn and sss mutants. This concern also connects to the finding of metabolic misalignment under constant darkness despite an intact clock. The conclusion that external entrainment is essential for maintaining energy homeostasis in flies may not translate to mammals. It would help to reference supporting data for the finding and discuss differences across species. Ideally, complementary circadian (light-dark cycle disruption) or sleep deprivation (for several hours) experiments, or citation of comparable studies, would strengthen the generality of the findings. Figures 1-4 are straightforward and clear, but when the manuscript transitions to the metabolite-respiration correlations, there is little description of the metabolomics methods or datasets, which should be clarified. The Discussion is at times repetitive and could be tightened, with the main message (i.e., wild-type flies align metabolism in advance, while mutants do not) kept front and center. Terms such as "anticipatory" and "reactive" should be defined early and used consistently throughout.

Overall, this is a strong and novel contribution. With clarification of scope, refinement of presentation, and a more focused Discussion, the paper will make a significant impact.

Comments on revised version.

The authors have satisfactorily addressed my concerns in the revised manuscript

Reviewer #3 (Public review):

Summary:

The authors investigate how sleep loss and circadian disruption affect whole-organism metabolism in Drosophila melanogaster. They used chamber-based flow-through respirometry to measure oxygen consumption, carbon dioxide production, in wild-type flies and in mutants with impaired sleep or circadian function. These measurements were then integrated with a previously published metabolomics dataset to explore how respiratory dynamics align with metabolic pathways. The central claim is that wild-type flies display anticipatory coordination of metabolic processes with circadian time, while mutants exhibit reactive shifts in substrate use, redox imbalance, and signs of mitochondrial stress.

Strengths:

The study has several strengths. Continuous high-resolution respirometry in flies is challenging, and its application across multiple genotypes provides good comparative insight. The conceptual framework distinguishing anticipatory from reactive metabolic regulation is interesting. The translational framing helps place the work in a broader context of sleep, circadian biology, and metabolic health.

Weaknesses:

At the same time, the evidence supporting the conclusions is somewhat limited. The metabolomics data were not newly generated but repurposed from prior work, reducing novelty. The biological replication in the respirometry assays is low, with only a small number of chambers per genotype. Importantly, respiratory parameters in flies are strongly influenced by locomotor activity, yet no direct measurements of activity were included, making it difficult to separate intrinsic metabolic changes from behavioral differences in mutants. In addition, repeated claims of "mitochondrial stress" are not directly substantiated by assays of mitochondrial function. The study also excluded female flies entirely, despite well-documented sex differences in metabolism, which narrows the generality of the findings.

Reviewer #1 (Public review):

Strengths:

Thorough reanalysis of the experimental results obtained in previous studies, which led to the publication of the PNAS paper in 2016.

New experimental evidence to confirm that enzymes previously considered as participating in the ED, actually are not catalyzing the ED biochemical reactions, but are involved in other metabolic pathways. Also, the authors completely discarded the occurrence of the GDH/GK shunt in Synechocystis PCC 6803. Generally speaking, the manuscript is very clearly written, with a precise description of the previous findings, the mistakes which took place in the 2016 paper, and the strategies they have used to address those issues, in order to reach a thoroughly revised vision of the glucose metabolic pathways in Synechocystis PCC 6803. In this regard, the drawings shown in Figures 1 and 7 are very helpful for the reader to follow the story and understand the possible metabolic transformations depending on the working hypothesis.

Also, I commend the authors for openly describing previous mistakes. In this paper, they reassess past observations under the light of more recent findings, and to integrate the information in this manuscript. The scientific conclusions are solid and very interesting, and besides they use the opportunity to offer valuable advice to researchers. This is especially focused on the importance of careful biochemical characterization of enzymes, which should always be carried out when studying proteins which have been identified as a specific enzyme on the basis of sequence homology. In a similar way, they found that an insertional mutant was the cause for the absence of specific metabolites, which had been attributed to particularities of a metabolic pathway in that mutant, when it was actually due to a nucleotide insertion; given that currently, genome sequencing is an affordable technique, this kind of mistakes can now be easily prevented by confirming the correct generation of the mutant by DNA sequencing, as proposed by the authors in a recently published preprint (Theune et al, bioRxiv 10.64898/2026.04.08.717167).

Weaknesses:

The authors propose that EDA might be involved in the PEP-pyruvate-OAA node, or in the proline metabolism, but this requires further experimental work for clarification; what their results indicate clearly is that this enzyme is not actually catalyzing the transformation of KDPG to GAP, which is the second specific enzyme of the ED pathway. But the real physiological function in this cyanobacterium is still unconfirmed.

Another aspect which could be improved is that the recombinant expression of some genes was carried out in E. coli; even if this is a useful and valid research strategy, in studies like this (where there is a strong focus on the physiological function of enzymes in the original organism, Synechocystis PCC 6803), I think it would have been more appropriate to express the 6803 genes in another cyanobacterium easily amenable for genetic transformation and gene expression, which would produce the protein in a physiological environment more similar to another cyanobacterium (compared to E. coli, which is an heterotrophic bacterium). I am not sure this would change any of the obtained results, but certainly would confer additional robustness to the enzymatic results.

Comments on revised version.

The authors have provided satisfactory replies to all my suggestions and corrections, and I have no further changes to suggest.

Reviewer #2 (Public review):

Summary:

The study presents novel results on the presence of the Entner Doudoroff pathway in Synechocystis sp. PCC 6803. In contrast to an earlier study, compelling evidence is given that this strain lacks both an ED pathway and a glucose dehydrogenase/glucokinase bypass but contains a promiscuous aldolase, which also decarboxylates oxaloacetate and cleaves 2-keto-4-hydroxyglutarate (as it occurs in proline degradation). The study concludes with successfully reconciling data of different studies and with lessons learned from the previous misconception.

Strengths:

Solid biochemical data is presented to reconcile contradicting data of earlier studies and to serve as basis for disclosing possible functions of a promiscuous aldolase. Earlier misconceptions and lessons to be learned are well discussed.

Weaknesses:

The materials and methods section is rather lengthy, suffering from a lack of conciseness and repetitions, and nevertheless misses some specifications.

Comments on revised version.

The materials and methods section has been significantly improved. The revised manuscript is now recommended for publication as it is.

Reviewer #1 (Public review):

Summary:

The authors test specific but related hypotheses regarding anti-predator responses of wild marmoset groups to predator and human playback sounds triggered to play via a motion sensor on camera-trap devices. The differential responses they observe to human noises and natural predator sounds are interesting, but greater inferences are limited due to a lack of clarity in the methods and analyses.

Strengths:

The authors create an excellent experimental design using a customised ABR system for testing the behavioural responses of wild, social-living, tiny, arboreal primates: pygmy marmosets. Much of the work is described with great transparency, and figures and tables are helpful in facilitating this.

Weaknesses:

The current study requires improvement in three areas, in my opinion, to permit readers to better evaluate the validity and importance of these results.

(1) Improve the framing of the paper:

The current title and justification for this study appear to point to a lack of previous studies testing specific hypotheses (line 51/52: "ABRs have not been applied to hypothesis testing". I find this a rather strange argument to make, given that a quick read through of other ABR papers, cited by the authors (e.g., Kasper et al., 2025, Epperly et al., 2021), are testing predictions set by ecological theory in the cascading effects of predator-prey dynamics. To me, even if these are not explicitly stating "X hypothesis" in their paper, they still appear to be studies guided by implicit hypotheses. To say that previous work with ABR did not test hypotheses is presumptuous, in my opinion. The entire paper would be much better appreciated if the authors could reframe the study for its importance to arboreal mammal/ tropical ecology, anthropogenic effects, and so on. Similarly, the authors should avoid use of phrasing such as "this study is the first direct test of .... " (lines 59/60) and should emphasize the true significance of their work, beyond it being the 'first' of something.

Similarly, on line 87, "demonstrating that the ABR system can be used to generate data for hypothesis testing" should be removed, as firstly sufficient sample size for any study depends on a number of study-specific parameters, and the authors do not actually demonstrate this in my opinion, given that many of their models end up suffering from singular fit. This is due to a lack of sample size, and also because they do not actually do any type of power analysis or something similar to demonstrate that they actually assessed sample size. So again, my suggestion is to reframe the paper to focus on the behavioural ecology and conservation-related impacts rather than this emphasis on methodology.

(2) Methods:

The authors generally do a great job providing sufficient detail on the ABR system and how each experiment was designed. Still, there is room for improvement, as I was confused a number of times. I also would recommend that the authors include a limitations section somewhere which considers the drawbacks of their study, in particular the lack of individual identity for behavioural responses of marmosets (especially given that they used focals, it seems), the groups being in close vicinity of one another/potentially related (?), the specific stimuli used, etc.

Points of confusion for me included what the control was for Experiment 1. Line 93 - 70 videos without playbacks are used (Table 1), but it is not clear how these videos were selected, and it is not a suitable control comparison for assessing the difference in behaviour associated with playbacks (playbacks with control sounds are). At most, these videos will give basal rates of behaviour (like vocalizations, etc.), but then it is not clear why these '70 videos' and how they were chosen to avoid bias. So, for example, in line 105 the authors write that focals were more likely to flee when hearing playback stimuli than in these "control" videos, but this is not convincing. If there was no fleeing after playback of control sounds (cicadas, macaws) - i.e., the true control in this experiment - then this should be the comparison that is emphasized.

Can the authors also clarify how they considered/assessed the sound playback level (normally done in Decibels) and if they did not normalize the sound level across the playback stimuli, why not, and what potential effect this could have on the results (i.e., something else to consider for the limitations section)?

Something else not discussed is the rate of exposure to predator and human noise for these wild monkeys. Are these rates within normal range/expectation for these monkeys? Thinking here of the number of videos captured for each group presumably means exposure to a playback unless 'control' videos were videos where no playback sound was emitted (see question above re: control videos). There were a lot more unsuccessful videos than successful ones that the authors could use, so trying to understand the potential impacts of this (see question re: trial/video # below as well).

(3) Analysis:

A few things are unclear and need more explanation in the way the authors conducted their analyses, although they do well to detail all steps of their statistical methods, which was great.

For assessing model fit, it is not clear what exactly was assessed with the 'performance package' line 467, as the authors do not go on to provide us with any results of the performance/fit. Instead, they tell us that the models did not fit well, with no parameter provided (e.g. lines 481-488). I'm familiar with overdispersion as a parameter that is reported for Poisson models (that does not seem to be provided here). Or by looking at changes in model estimates if one datapoint (and/or one group) is removed after another (with replacement, so keeps sample size static). On line 468/469, it says that model fit was assessed via conditional R2; could the authors provide a citation for this practice, and then provide the R2 parameter for the other models that were used/included in the end?

Also, please standardize how the GLMM results are presented. There should be the estimate, SE, Z or t, then p value. (line 99, 137).

Given the high rates of exposure to playbacks, I think the authors should test trial # (or video #) for a potential habituation effect, with earlier captures more likely to draw stronger responses than later video captures for each group.

Reviewer #2 (Public review):

Summary:

The article describes an interesting methodology to test hypotheses about the impact of anthropogenic noise on a small arboreal primate, the pygmy marmoset. The authors used a motion-triggered combination of camera traps and speakers to play back control sounds, avian predator calls, and anthropogenic noise to test the risk-disturbance hypothesis and the distracted prey hypothesis. In addition, the authors implemented a technique that is usually used for larger mammals and has not been used before for smaller arboreal animals. The authors are careful in their interpretation of the results and do not favor one hypothesis over the other. The authors also elaborate extensively in their discussion on how to improve this kind of data collection in the future.

Strengths:

This study provides a method for rapid data collection while minimizing observer impact. The sample size is comparatively large for a wild animal in a reserve, given the overall observation time. The article also benefits from a solid analysis of the data.

Weaknesses:

Though the authors tested two contrasting hypotheses, the discussion would benefit from more detail on the ecological relevance of the observed behaviors.

Reviewer #1 (Public review):

Summary:

In this manuscript, Du et al. identify a putative URS (nucleotides −709 to −229) that contributes to CY/MMS-induced DDI2/3 transcription in the promoter of S. cerevisiae DDI2 through promoter mapping. They further showed that CY/MMS leads to histone loss, and that genetic depletion of histone triggers DDI2/3 expression in an Fzf1-dependent manner. Using MNase-seq, the authors demonstrate that CY treatment leads to nucleosome loss at the DDI2/3 promoter and coding sequences, and that this chromatin remodeling process requires Fzf1. Based on these results, the authors propose that Fzf1 promotes CY-induced DDI2/3 expression through two distinct mechanisms: as a transcription factor and as a regulator of nucleosome occupancy. This dual mode of regulation may contribute to the exceptionally high induction of DDI2/3 relative to other Fzf1 target genes in response to CY.

Strengths:

This manuscript identifies the URS region at the DDI2 promoter that regulates CY/MMS-induced DDI2 expression. In addition, the authors revealed an important role of nucleosome occupancy in regulating DDI2/3 transcription, proposing the intriguing dual regulation model of Fzf1. Overall, this work furthers our understanding of how Fzf1 mediates the increase of DDI2/3 expression in response to CY/MMS treatment.

Weaknesses:

Overall, the study is of interest, and the data are generally convincing; however, several conclusions would benefit from further experimental validation. Certain controls are necessary for several experiments to improve the strength of evidence. Several major points are listed below:

(1) For Figure 6A and Figure 7A, the authors concluded that there are 'joint effects' of CY treatment and histone depletion. However, it is unclear whether CY treatment acts dependently or independently of histone depletion. As shown in Figure 2, both CY and MMS can cause histone reduction. In addition, the depletion system in the RMY102 strain only depletes about half of the H3 (based on the western blots in Figure 5D, E). It would be necessary to test whether H3 abundance is further depleted in CY-treated RMY102 by Western blot.

(2) Proper controls are missing in Figure 6A and Figure 7A. The authors compare gene expression levels in RMY102 + histone depletion + CY/MMS treatment with RMY102 + non-histone depletion. There are two variables here: histone depletion and CY/MMS treatment. It would be more convincing to include RMY102 YPGal+ CY/MMS treatment (5-40 mM), so that the impact of histone depletion and CY/MMS treatment on Fzf1 target gene expression levels would be clearer.

(3) In lines 242-249 and 269-272, the authors compared RMY102 versus BY4741 to conclude that histone depletion affects dose dependency of CY/MMS treatment. However, RMY102 and BY4741 might have different responses to CY/MMS due to strain background differences. Thus, in line with point 2, showing the expression level curves for non-histone depleting RMY102 treated with different doses of CY/MMS would be necessary.

(4) Figure 4 shows that CY and MMS have differential impacts on cell growth, which is intriguing. However, the rest of the data did not provide further insights in regard to this observation. It might be helpful to speculate possible underlying mechanisms in the Discussion session.

Reviewer #2 (Public review):

Summary:

Previous work established that FZF1 is both necessary and sufficient for activation of FZF1 target genes through the CS2 sequence motif, which is present upstream of FZF1-responsive targets. This study extends that model by demonstrating that, in addition to direct binding of FZF1 to CS2 elements, FZF1 can also promote reduced nucleosome-mediated repression, thereby contributing an additional layer of transcriptional regulation.

The authors investigate why FZF1-dependent transcriptional responses exhibit different magnitudes despite FZF1 binding to CS2 elements with similar affinity. Using promoter constructs derived from the DDI2-3 gene, the authors identify a region upstream of the CS2 element that functions as a repressive regulatory element. Based on this observation and publicly available datasets, the authors propose that this repression may be mediated through nucleosome occupancy.

Strengths:

The authors demonstrate that the DDI2-3 promoter contains positioned nucleosomes and show that chemical stress results in decreased histone protein levels and reduced histone-associated transcripts. They further examine whether histone depletion alone is sufficient to activate the DDI2-3 response and find that reduced histone levels increase expression, although chemical treatment produces an additional increase that remains dependent on FZF1. These findings suggest that FZF1 contributes to reductions in nucleosome occupancy at DDI2-3 and SSU1, revealing a second, potentially independent mechanism by which FZF1 regulates transcriptional responses to chemical stress.

Overall, the authors provide strong evidence that nucleosome occupancy influences the magnitude of FZF1-mediated DDI2-3 responses to chemical stress. This work has important implications for understanding how transcriptional networks evolve to generate highly tuned responses by combining multiple regulatory mechanisms acting on shared molecular components.

Weaknesses:

However, several additional considerations should be addressed. While histone depletion may contribute to differential FZF1-mediated responses, alternative mechanisms may also influence the observed transcriptional differences. For example, YHB1 exhibits basal expression that is independent of FZF1, and SSU1 contains the CS1 regulatory element, which can promote increased expression independently of FZF1 responsiveness. Therefore, differences in promoter architecture and the presence of alternative regulatory sequences may also contribute to differential FZF1 responses and should be discussed.

Additionally, the authors should clarify whether nucleosome depletion is directly mediated by the FZF1 ZF5 domain or occurs indirectly as a consequence of RNA polymerase II (Pol II) recruitment. Although the data presented in Figure 9 are consistent with a direct interaction model, the current evidence does not fully exclude the possibility that Pol II recruitment contributes to subsequent nucleosome/histone depletion. Unless there is direct experimental evidence demonstrating that FZF1 ZF5 independently promotes nucleosome remodeling, this alternative mechanism should be acknowledged and considered in the discussion.

Reviewer #3 (Public review):

Summary:

In the manuscript titled "Dual regulation of chemical stress-induced DDI2/1 3 expression by a transcription factor Fzf1 and nucleosome in Saccharomyces cerevisiae" Du et al have discovered a dual role of Fzf1 in transcriptional control of DDI2/3 during cyanamide (CY) or MMS treatment. While previous literature established that Fzf1 regulates multiple targets (DDI2/3, SSU1, YHB1, and YNR064C) by binding the CS2 consensus sequence, it remained unclear why DDI2/3 uniquely undergoes a massive 1,000-fold induction under cyanamide (CY) stress, whereas the others show only a 20- to 40-fold induction. In this work, the authors showed that Fzf1 functions beyond standard transcriptional activation. Using MNase-seq and a series of promoter truncation mutants, the authors mapped Upstream Repressing Sequences (URS) in the DDI2/3 promoter that are heavily occupied by nucleosomes. The authors showed that Fzf1 is essential for chromatin remodelling and nucleosome eviction (specifically at the -2 nucleosome position) to de-repress the DDI2/DDI3 expression.

Strengths:

The two-tier mechanism of action of Fzf1 in controlling the DDI2/3 expression during CY/MMS stress is compelling and novel.

Weaknesses:

While the authors presented the in vivo MNase-seq data that show Fzf1 is necessary for nucleosome displacement, the current study lacks any in vitro mechanistic proof. As the authors acknowledge, it remains unknown whether Fzf1 directly displaces nucleosomes on its own (perhaps through unmapped post-translational modifications induced by chemical stress) or whether its ZF5 activation domain merely acts as a scaffold to recruit separate chromatin remodelling complexes.

To test nucleosome repression, the authors utilised extreme global interventions, such as deleting the SPT10 gene or halting de novo histone synthesis using a galactose-to-glucose medium shift in the RMY102 strain. While these methods effectively deplete histones and induce DDI2/3 up to 30- to 350-fold, completely depleting cellular histones causes massive, pleiotropic secondary effects across the entire genome, which can obscure specific regulatory relationships.

Reviewer #1 (Public review):

Summary:

In this manuscript, Tuñí-Domínguez et al. present a large-scale, cross-study meta-analysis of 2,356 cell-free RNA sequencing (cfRNA-Seq) samples. The authors aimed to systematically evaluate the impact of pre-analytical variables and library preparation protocols on biological interpretation. By harmonizing publicly available and internally generated datasets through a uniform bioinformatics pipeline, the study seeks to establish standard quality control (QC) metrics and provide evidence-based guidelines for protocol selection in cfRNA-Seq biomarker discovery.

Strengths:

A major strength of the study is the scale and breadth of the harmonized dataset. The use of a common computational pipeline reduces variation arising from differences in bioinformatic processing and enables more direct comparisons among published datasets. The authors examine multiple complementary dimensions of data quality rather than relying on a single sequencing metric. The inclusion of variance-partition analyses, healthy-control-only analyses, and analyses restricted to samples with low gDNA contamination strengthens the evaluation of technical heterogeneity. The public availability of the analysis code and processing configurations further increases the reproducibility and potential utility of this work. The study convincingly demonstrates that technical and pre-analytical factors are major sources of variation across existing plasma cfRNA-seq datasets.

Weaknesses:

Several central conclusions are broader than the current cross-study design can fully support. Protocol category is strongly associated with dataset, laboratory, sample source, and collection procedure, making intrinsic protocol effects difficult to separate from study-specific effects, particularly for categories represented by only one or a few studies. The conclusion that technical variation generally overwhelms biological variation also requires qualification because diverse diseases and cancer types are combined into broad phenotype categories, and many phenotypes are concentrated within individual datasets. The interpretation and additional value of the proposed NG80 and NP80/NG80 metrics require further support, especially given their variable behavior across datasets. Most importantly, the thresholds used in the proposed universal QC framework are not independently validated and are strongly influenced by library-preparation strategy. The current findings therefore support protocol-dependent comparisons and identification of technical trade-offs more strongly than they support a universal definition of library quality.

Major concerns:

(1) Protocol effects remain difficult to distinguish from study-specific effects.

The manuscript interprets Broad Protocol Category as a major determinant of transcriptomic variation. However, protocol, dataset, laboratory, sample source, and collection procedure are strongly interconnected. Although both Dataset and BPC are included in the variance-partition model, several protocol categories are represented by only a limited number of studies.

This is particularly problematic for WRO, which is represented by a single study. Its apparent characteristics therefore cannot be separated from Reggiardo-specific laboratory, cohort, provider, or sample-processing effects. The authors should clarify the stability of the variance-partition results and, where feasible, provide sensitivity analyses. Alternatively, conclusions based on protocol categories represented by one or very few studies should be explicitly presented as study-specific observations rather than broadly validated protocol properties.

(2) The interpretation and robustness of the proposed library-diversity metrics require further support.

The manuscript attributes the high NG80 values in the Block and Sun datasets to gDNA contamination. However, other datasets with similarly low FSR values, including Wang and Giráldez, do not show comparably high NG80 values. This suggests that gDNA contamination alone is insufficient to explain library diversity and that sequencing depth, fragment length, mapping behavior, or library construction may also contribute.

The NP80/NG80 ratio is conceptually reasonable, but its additional value beyond the RNA-biotype composition shown in Figure 3C is unclear, particularly given the large variability observed in WRR datasets. The authors should further examine the relationships among FSR, NG80, sequencing depth, and protocol characteristics and assess the stability of NP80/NG80. If additional validation is not feasible, the interpretation and generality of these metrics should be moderated.

(3) The conclusion that technical variation generally overwhelms biological variation requires qualification.

The manuscript provides convincing evidence that technical heterogeneity is a major source of variation in the combined cross-study dataset. However, the conclusion that donor phenotype contributes only negligible variation may be broader than the analysis supports.

Phenotypes are reduced to healthy, cancer, and non-cancer disease categories despite substantial biological heterogeneity, and many disease groups are concentrated within particular studies. Consequently, disease-specific biological variation may partly be assigned to the Dataset term. A similar issue affects the cellular-origin analysis, where collection center and phenotype are substantially associated in the Chen dataset, making their individual contributions difficult to distinguish.

Where sample sizes permit, the authors should examine more specific disease categories or perform within-dataset analyses. Otherwise, the conclusions should be narrowed to state that technical variation dominates the present heterogeneous cross-study aggregation, rather than implying that phenotype-associated cfRNA signals are generally negligible.

(4) The proposed universal QC framework is insufficiently justified and protocol-dependent.

Figure 6 defines high-quality libraries using NG80 >1,000 together with FSR >20% or FER >75%. However, the manuscript does not explain how these thresholds were selected or validate them against an independent measure of reproducibility, analytical performance, or biomarker utility.

These criteria are also strongly affected by library-preparation strategy. FER and FSR favor libraries enriched for exonic or spliced RNA, whereas the NG80 cutoff disadvantages WRR libraries containing abundant noncoding transcripts. This is difficult to reconcile with the recommendation of WRR for exploratory transcriptomic and microbial analyses.

The authors should justify the threshold selection and assess its sensitivity and protocol dependence. Ideally, the criteria should be validated against an independent performance endpoint. Otherwise, Figure 6 should be reframed as a descriptive comparison, and protocol- or application-specific guidance should replace a universal binary definition of library quality.

Reviewer #2 (Public review):

Summary:

This manuscript systematically evaluates the impact of experimental workflows on plasma cell-free transcriptome sequencing (cfRNA-seq) data. The authors integrate a large number of cfRNA sequencing datasets from multiple publicly available studies and establish a unified bioinformatics framework to systematically assess the effects of experimental workflows, genomic DNA contamination, library diversity, and preanalytical factors on cfRNA transcriptomic profiles.

Strengths:

This study addresses the technical heterogeneity that may hinder cfRNA biomarker discovery and clinical translation and is of substantial value.

Weaknesses:

The effects of disease phenotype, technical confounding, criteria for library quality, and conclusions regarding DNase treatment require further clarification and validation.

Major Points:

(1) The conclusion that donor phenotype explains only a small fraction of transcriptomic variation requires further support from within-study analyses.

The authors conclude from variance partitioning across all studies that phenotype explains only a small fraction of cfRNA transcriptomic variation. However, the included studies encompass different diseases, while phenotype is simplified into healthy, cancer, and non-cancer disease categories, and the overall transcriptomic variation is strongly influenced by study-specific and experimental workflow batch effects. Therefore, the cross-study pooled analysis may underestimate genuine disease-associated cfRNA differences within individual studies conducted under the same experimental workflow.

Recommendation: The authors are encouraged to perform within-study phenotype analyses in datasets that include both healthy controls and disease samples and have sufficient sample size, and to quantitatively estimate the proportion of transcriptomic variance explained by phenotype. For example, the Zhu dataset includes healthy controls and liver cancer samples, and the authors have already observed relatively clear phenotype-associated clustering between the two groups. The contribution of healthy-versus-liver-cancer phenotype to transcriptomic variation could therefore be quantified within this dataset. If similar results are obtained across multiple independent cohorts, the findings could then be summarized across studies. The authors should also note that a low contribution of phenotype to global transcriptomic variance does not necessarily imply that disease-associated cfRNA signals lack biological or clinical relevance.

(2) Comparison of the relative contributions of technical factors and disease phenotype may be affected by confounding.

Figure 1C shows that phenotype is strongly or even completely confounded with technical variables such as collection center and centrifugation protocol in some cohorts. Nevertheless, the variance partitioning analysis across all samples is used to conclude that technical factors are the primary sources of variation, whereas phenotype contributes little. In the presence of such confounding, technical effects and disease-associated biological effects may not be reliably estimated independently, and this conclusion therefore requires more direct validation.

Recommendation: The authors are encouraged to perform an independent within-study variance analysis in cohorts in which technical variables and phenotype are relatively balanced. For example, in the Moufarrej cohort, phenotype is essentially unconfounded with collection center/centrifugation protocol (Cramer's V = 0). Phenotype and relevant technical variables could be included simultaneously in a within-cohort model to quantify their respective contributions to cfRNA transcriptomic variation. If technical factors still explain a larger fraction of variance in such relatively unconfounded cohorts, this would provide stronger support for the central conclusion of the manuscript.

(3) The use of NG80 as a criterion for defining "high-quality libraries" requires further validation.

The authors use NG80 as a metric of library diversity and further apply NG80 > 1,000 as one criterion for defining high-quality libraries in Figure 6. However, because NG80 is based on gene counts, it may be affected by sequencing depth. In addition, gDNA contamination can artificially increase NG80, whereas genuinely abundant non-coding RNAs in WRR libraries can lower NG80. Therefore, a higher NG80 does not necessarily indicate better overall library quality, and the metric may reflect both technical quality and genuine RNA composition.

Recommendation: The authors are encouraged to re-evaluate NG80 after downsampling samples to a common number of mapped fragments and to examine the relationship between NG80 and sequencing depth. The rationale for the NG80 > 1,000 threshold should also be further justified, and the impact of alternative NG80 thresholds on high-quality library classification and the main conclusions should be assessed. Unless there is evidence that this threshold reliably predicts library reproducibility or biomarker-related information content, library diversity and overall library quality should be clearly distinguished, and NG80 should not be presented as a universal criterion for high-quality libraries.

(4) Conclusions regarding DNase treatment should be interpreted more cautiously.

The Toden study did not explicitly report DNase treatment. The manuscript infers that DNase digestion was performed based on the fact that this study originated from the same laboratory as other studies and used a similar workflow; this inference should not be treated as an established experimental fact. In addition, the authors state that double DNase treatment is the most effective approach among non-EB workflows, but this conclusion is mainly based on cross-study comparisons, in which DNase strategy varies together with laboratory, sample handling, and cohort-specific factors. The current evidence is therefore insufficient to establish that double DNase treatment itself is superior.

Recommendation: The authors are encouraged to label the DNase status of the Toden study as "not reported" or "inferred", unless confirmation can be obtained from the original authors. The conclusion that double DNase treatment is the most effective approach should also be tempered, with explicit acknowledgment that it requires direct parallel validation using the same samples under different DNase treatment strategies.

Reviewer #1 (Public review):

Summary:

The authors are trying to characterize the sources of H. pylori in an island system. They find that, like the humans, the bacteria are admixed, but there is no correlation within the island between human ancestry and bacterial ancestry.

Strengths:

The study has taken particular care to characterize the humans from which isolates were obtained. Thus, it is a particularly convincing demonstration of a bacterial "melting pot".

Weaknesses:

The GWAS is highly confounded by population structure. In particular, there is a large group of strains that lack the cag pathogenicity island, and also differ in frequencies of other genes. So it's not clear that these differences are other than in cag status.

Figure 1 seems very inconclusive.

Reviewer #2 (Public review):

Summary:

This study investigates the population structure and ancestry of Helicobacter pylori in Cabo Verde, where the human population has mixed West African and European ancestry. The authors combine a population survey, serum markers, bacterial genome analysis, and paired human-bacterial ancestry data. They report high H. pylori seropositivity, several distinct bacterial groups, and limited correlation between human ancestry and bacterial ancestry. They also identify one European-derived bacterial group that appears to have undergone a recent expansion and carries fewer well-known virulence-related genes.

The study is interesting, and the dataset is valuable, especially because population-based H. pylori genomic data from Cabo Verde and West Africa are limited. The results provide useful information on bacterial diversity, historical migration, and host-bacterial ancestry. However, some of the main conclusions are stronger than the evidence currently supports, particularly the claims of host adaptation, increased transmission, and reduced virulence.

Strengths:

(1) A major strength is the study population. Participants were recruited from the general population and not only from patients with gastrointestinal disease. This gives a broader view of H. pylori diversity in Cabo Verde than studies based only on hospital patients.

(2) The number of participants tested for H. pylori antibodies is substantial, and the authors also obtained a relatively large number of bacterial genomes. The combination of human and bacterial genomic information is another important strength. This allows the authors to directly examine whether human ancestry is related to the ancestry of the colonising bacteria.

(3) The population genetic analyses are extensive. The authors use several different approaches, and these generally support the existence of African-derived and European-derived bacterial groups in Cabo Verde. The identification of two low-diversity European-derived groups is also interesting and suggests a relatively recent expansion.

(4) The addition of new strains from Ghana and Portugal improves the reference dataset. The results may help future studies of H. pylori population structure in Africa, Europe, Cabo Verde, and populations affected by historical Atlantic migration.

(5) The finding that human ancestry and bacterial ancestry are only weakly related in this population is potentially important. It suggests that the long-term relationship between human and bacterial ancestry may be less stable in recently admixed populations.

Weaknesses:

The main weakness is that several biological conclusions are based on indirect evidence. The genomic results support recent expansion of one bacterial group, but they do not directly show that this expansion was caused by adaptation to local hosts or by increased transmission. Founder effects, population history, geographic clustering, household transmission, or random expansion may also explain the pattern. The wording should therefore be more cautious.

The conclusion of reduced virulence is also not fully supported. The expanded lineage often lacks the cag pathogenicity island and carries less virulent forms of vacA, which suggests lower virulence potential. However, this does not prove that the strains cause less gastric damage or lower disease risk. There are no endoscopic or histological data, and serum pepsinogen values are only indirect markers.

The description of the study population as having limited gastric inflammation is too strong. Serum pepsinogen measurements are useful for estimating gastric atrophy, but they do not directly measure the degree of histological gastritis. In addition, participants were recruited independently of symptoms, but this does not mean that they were all asymptomatic.

The epidemiological estimate is based on antibody testing. This measures seropositivity and cannot clearly distinguish current from previous infection. Therefore, terms such as active infection or colonisation should be used carefully.

The proposed new West-Central African bacterial group is based on a small number of reference strains from Ghana and Nigeria. The result is interesting, but broader sampling from African countries is needed before this group can be considered firmly established.

The interpretation related to the trans-Atlantic slave trade is plausible, but the data mainly show patterns consistent with known historical migration. They do not directly demonstrate when or how the bacterial lineages moved.

The gastric cancer comparison may also be affected by bacterial population structure. Differences between the Cabo Verdean lineage and gastric cancer strains may reflect ancestry or lineage differences rather than disease association alone.

Overall, the study achieves its main aim of describing H. pylori diversity and ancestry in Cabo Verde. The evidence is strong for the population structure and ancestry findings, but less strong for the proposed mechanisms of adaptation, transmission, and reduced disease-causing potential. The work will be useful to the field, but the main conclusions should be stated more carefully.

Reviewer #1 (Public review):

Summary:

In this study, the authors use patient-specific induced pluripotent stem cell-derived cardiomyocytes (hiPSC-CMs) from six patients carrying three distinct pathogenic LMNA variants to investigate disease mechanisms underlying LMNA-associated dilated cardiomyopathy (DCM). The authors report shared abnormalities in nuclear morphology, electrophysiology, calcium handling, and contractility across all patient-derived lines and demonstrate that correction of representative LMNA variants by CRISPR/Cas9 rescues several of these phenotypes. They further develop a high-throughput phenotypic drug screening platform using calcium transient measurements and identify cyproheptadine as the only compound among 1,280 FDA-approved drugs that consistently improves calcium transient abnormalities across all patient-derived lines.

The study addresses an important clinical problem and establishes a technically sophisticated patient-derived screening platform. However, while the experimental work is generally well executed, several of the major biological and translational conclusions are not sufficiently supported by the presented data.

Strengths:

The major strength of this study is the development of a patient-derived functional screening platform using multiple LMNA mutations rather than focusing on a single pathogenic variant. The inclusion of six patient-derived iPSC lines representing three distinct mutations increases the generalizability of the observations and allows identification of disease features that appear reproducible across different genetic backgrounds.

The phenotypic characterization is comprehensive and includes nuclear morphology, transcriptomics, manual and automated electrophysiology, calcium imaging, and impedance-based contractility measurements. Importantly, CRISPR-mediated correction of representative LMNA variants provides convincing evidence that the observed cellular abnormalities are directly attributable to the pathogenic variants.

Finally, the implementation of an unbiased high-throughput drug screen using patient-derived cardiomyocytes represents a valuable technical advance that could facilitate therapeutic discovery in inherited cardiomyopathies.

Weaknesses:

The principal weakness of the manuscript is that the central conclusions substantially exceed what is directly demonstrated by the data.

The manuscript repeatedly concludes that dysregulated calcium handling represents a shared pathogenic mechanism underlying LMNA-associated cardiomyopathy. However, the presented experiments establish only that abnormal calcium handling is a shared cellular phenotype across the studied variants. The data do not distinguish whether calcium dysregulation is a primary disease mechanism or whether it is secondary to the numerous upstream abnormalities already known to result from LMNA dysfunction, including altered nuclear architecture, defective mechanotransduction, chromatin remodeling, and transcriptional dysregulation. This distinction is critical because the manuscript repeatedly interprets correction of calcium handling as correction of the underlying disease process without directly demonstrating this relationship.

A related concern is the interpretation of the drug screening results. The primary screen is entirely based on normalization of calcium transient parameters (CTD75, FWHM, and T75-25). Consequently, the screen identifies compounds capable of correcting calcium cycling rather than compounds that necessarily modify disease biology. Although cyproheptadine subsequently improves impedance-derived contractile parameters, it remains unknown whether treatment rescues other defining features of LMNA cardiomyopathy, including abnormal electrophysiology, nuclear defects, transcriptional alterations, or broader cellular stress responses. Thus, the conclusion that cyproheptadine represents a "novel treatment" for LMNA-associated cardiomyopathy is considerably stronger than the evidence presented.

The mechanistic studies are also insufficient to support the proposed mode of action. The manuscript proposes CHRM2 as the likely mediator of cyproheptadine activity primarily because it is the only appreciably expressed known target in the transcriptomic dataset. However, no functional experiments test this hypothesis. Without genetic or pharmacological interrogation of CHRM2, the proposed mechanism remains speculative. Likewise, alternative mechanisms of cyproheptadine action, including serotonergic signaling, histamine receptor antagonism, direct calcium channel modulation, or antioxidant effects, are not investigated.

Another conceptual weakness is that the manuscript promises to distinguish both shared and variant-specific disease mechanisms but ultimately focuses almost exclusively on shared phenotypes. The transcriptomic analyses remain largely descriptive and are not leveraged to identify mutation-specific biological pathways or explain differences among the three LMNA variants. Given the unique cohort assembled in this study, this represents a missed opportunity to generate broader biological insight into LMNA-associated disease.

The transcriptomic analyses themselves would also benefit from more rigorous interpretation. RNA from multiple independent differentiations was pooled prior to sequencing, limiting assessment of biological variability and reducing confidence in statistical inference. Similarly, many functional analyses emphasize the number of wells, recording sweeps, or individual cells while the number of independent biological differentiations is less prominently presented. Greater emphasis on biological replication would strengthen confidence in the robustness of the findings.

Finally, the translational implications of the work should be interpreted more cautiously. All therapeutic studies are performed in relatively immature two-dimensional iPSC-derived cardiomyocytes. No validation is presented in engineered heart tissues, multicellular cardiac organoids, animal models, or human tissue. The current evidence supports the conclusion that cyproheptadine is a promising in vitro phenotypic modifier rather than an established therapeutic candidate for LMNA-associated cardiomyopathy.

Overall, this study establishes a valuable patient-derived platform for investigating LMNA-associated cardiomyopathy and demonstrates the utility of functional high-throughput screening in identifying compounds that improve disease-associated cellular phenotypes. However, the manuscript currently overstates both the mechanistic significance of calcium dysregulation and the therapeutic implications of cyproheptadine. A more restrained interpretation of the findings together with additional mechanistic validation would substantially strengthen the impact of the work.

Reviewer #2 (Public review):

Summary:

The authors conducted a functional high-throughput drug screening using hiPSC-CMs derived from patients with LMNA-DCM. Cyproheptadine emerged as a therapeutic candidate.

Strengths:

The screen appears well designed.

Weaknesses:

The single candidate that emerged from the screen, cyproheptadine, raises issues with potency. In addition, validation studies that are both expected and necessary for a drug proposed as a novel therapeutic for human cardiomyopathy have not yet been performed. Rigor could be improved once the basic mechanistic and validation studies discussed below have been performed.

Reviewer #2 (Public review):

Summary:

This study addresses an important and timely question in colorectal cancer biology by systematically examining the effects of the common driver mutations APC, KRAS G12D, and TP53 in murine colorectal organoids, with particular emphasis on how the order of APC and TP53 acquisition influences tumor phenotype. These mutations are well known to be frequent, truncal, and often co-occurring in colorectal cancer. While it is increasingly appreciated that mutational order can shape tumor behavior, studies directly comparing the phenotypic consequences of alternative APC-TP53 mutation orders remain rare. This work therefore addresses a relevant and timely question.

Strengths:

A major strength of the study is its focus on previously unexplored biology, combined with the generation of multiple isogenic murine organoid models with controlled mutational sequences. The authors employ careful and robust quality control of the CRISPR-mediated alterations, and the inclusion of both in vitro and in vivo experiments strengthens the relevance of the work.

Weaknesses:

There are, however, several limitations that should be considered when interpreting the findings. First, KRAS G12D activation is used as the initiating alteration, whereas APC loss is generally believed to be the initiating event in most human colorectal cancers. Second, the analysis is restricted to comparing only two mutation orders (KAT versus KTA), which limits the breadth of conclusions that can be drawn about mutation ordering more generally. Finally, key RNA-sequencing and in vivo experiments rely on a limited number of isogenic lines, which constrains interpretability.

The study aimed to systematically investigate how the accumulation and sequence of driver mutations influence colorectal cancer initiation. The data provide intriguing evidence that the relative timing of APC and TP53 loss may impact tumor initiation and survival in a hostile microenvironment. However, given the limited number of biological replicates, these observations should be interpreted with caution and would benefit from further validation.

Reviewer #1 (Public review):

Summary:

The manuscript by Montenegro and colleagues reports a uniquely significant set of compelling results from a carefully designed study. The findings are fundamental and should substantially advance our understanding of whether prenatal exposure to high levels of alcohol produces neural changes that are precursors to the development of Alzheimer-like pathology in an animal model of Fetal Alcohol Spectrum Disorder (FASD). The quest was to test whether prenatal exposure to high-dose alcohol in the mouse would result in selective damage that would result in Alzheimer disease-like cellular disorder and mnemonic impairment. Both outcomes emerged and were exacerbated in relevant transgenic mice. The untoward effect on memory endured and even worsened with age.

Strengths:

The authors noted the importance of using a validated animal model to test their hypotheses related to AD-like outcomes because human postmortem data are unavailable and even in vivo data are limited to younger FASD cohorts. The authors further noted limitations, which also anticipate experiments that could chart the temporal course of the effect and windows of prenatal alcohol exposure that result in damage or resilience. In short, as the authors state on lines 435-7, "These data provide the first experimental evidence that developmental alcohol exposure impacts core proteolytic pathways central to AD/ADRD pathogenesis."

Weaknesses:

Addressing the following would clarify several points in an already well-written paper:

(1) It would be useful to have a timeline of the study, much like the one provided for the water maze protocol. On that timeline, please include the sample sizes examined, ages at exposure, and other pertinent procedures, indicating which animals remained alive for testing, etc.

(2) What were the attrition rates for each study group?

(3) What are the human age equivalents of the maternal mice?

(4) It would be helpful to see a graph of the BECs of each animal relative to the doses given. That would clarify how the alcohol exposure amount and timing are the same and where they are different for all exposed mice, given that the alcohol levels were somewhat different by group, as noted in the Methods. Were these BEC differences at all related to group differences in outcome measures or memory performance?

Reviewer #2 (Public review):

Summary:

In this study, the impact of prenatal alcohol (PAE) on amyloid precursor protein (APP) C-terminal fragments and notch intracellular domain (NICD) levels in adulthood is measured in 3xTg-AD mice.

Prenatal alcohol alters gamma secretase activity with development and aging. This could have implications for Alzheimer's disease risk in populations without inherited Alzheimer's risk genetics.

Strengths:

Strengths include the model, the use of orthogonal approaches, and the rigorous, high-quality data.

Weaknesses:

Some figures lack prenatal alcohol treatment in the 3xTg-AD mice.

Some overstatements should be tempered. For instance, one cannot conclude that the changes in CTFs are driving the changes in learning and memory (as suggested in the last line of the abstract) without a direct intervention testing this. For instance, though PAE caused a more robust learning deficit at 6 mo in WT, the impact on CTFs was less than it was at 3 mo. PAE did not significantly change CTFs or learning/memory in 3xTg-AD mice at 4 months, suggesting the genotype effect takes over at this point. The text should be adjusted to reflect this.

Conclusion:

In summary, this is a rigorous assessment of the long-term impacts of PAE on CTFs and learning/memory in adult WT and 3xTg-AD mice.

Reviewer #3 (Public review):

Summary:

The goal of this study was to test the hypothesis that prenatal alcohol exposure (PAE) can affect Alzheimer's disease (AD) pathogenesis using biochemical proxies, histology, and a behavioral paradigm sensitive to AD-related memory decline. Major strengths include the breadth of techniques used, consideration of different AD-related molecular markers, and the use of different ages as well as appropriate controls. The authors largely achieved their aims to show that PAE does affect amyloid precursor fragments (CTFs) and notch signaling very early on as well as long-term effects in adulthood, which may uncover a previously underappreciated mechanism that may contribute to AD-related neuropathology and behavioral outcomes during lifespan.

Strengths:

(1) Several techniques are used to address molecular, behavioral, and histological PAE-related changes.

(2) There is use of appropriate controls and an AD-relevant mouse model.

(3) Different ages are used to address age-related and long-term effects in AD and control mice.

(4) The novelty of results shows early changes in amyloid-related processes, affected by PAE.

Weaknesses:

(1) It is unclear as to whether there are sex differences, particularly in the adult cohort.

(2) More clarity is needed on sample size per cohort and whether mice that were used for anatomy and biochemical analyses were previously used for behavior. Including a table and noting any overlap would be useful.

(3) In many instances, two-way ANOVAs with treatment (PAE vs vehicle) and genotype as factors will be useful to report (e.g., Figure 1).

(4) In Figure 5 and line 253, it is stated that older mice have more severe deficits, but there are no direct statistical comparisons with younger AD mice.

(5 Lines 270-271 refer to mice as "presymptomatic", but these mice do have behavioral symptoms. Do the authors mean no neuropathology yet? Any data showing lack of robust neuropathology would be useful.

Reviewer #1 (Public review):

Vasilevskaya and Keller test different models of cortical function through the lens of predictive processing, a powerful framework for the brain to learn and predict the statistics of the world via generative internal models. The authors use a clever combination of behavioral perturbations in closed-loop and open-loop visuomotor virtual reality assays, a paradigm the Keller lab pioneered and used effectively in the past decade, in conjunction with two photon imaging of neuronal calcium responses and targeted optogenetic perturbations of activity. They specifically put to test proposed hierarchical vs. non-hierarchical circuit implementations of predictive processing by analyzing the logic of inter-lamina interactions (superficial vs. deep; L2/3 vs. L5/6).

The authors conclude that both versions of predictive processing architectures they analyze are likely invalid and instead formulate an alternative novel model of cortical function based on a recently developed machine learning algorithm for self-supervised learning (joint embeddings of predictive architectures, JEPA) and its further refinements. JEPA borrows elements from predictive processing engaging two encoder networks and training the output of one network to predict the output of the other. In their new model of cortical computations, prediction errors neurons in L2/3 compare the deep layers (L5/6) activity, which is taken as a teaching signal, to a local, L2/3 prediction of this latent representation.

Specifically, the authors build on their previous work and reports from other groups that different sets of L2/3 neurons compute positive prediction errors (fire when sensory stimuli appear unexpectedly with respect to the movements of the animal; e.g., grating onsets in the absence of locomotion) and respectively negative prediction errors (fire when sensory stimuli are absent, while the brain expected them to be present; e.g. mice locomote but visual flow is suddenly halted - visuomotor mismatches). These L2/3 positive and negative prediction error neurons exchange messages with neurons in the deeper cortical layers that, the authors propose, build an internal representation (R) of the sensory stimuli given the animals' movements.

In the hierarchical model, internal representation neurons (R) are supposed to act as a teaching signal for both types of prediction error neurons; the output of the positive prediction error neurons is assumed to suppress activity of R such that the error between the teaching signal and the prediction is minimized; similarly, in the non-hierarchical version, R serves as a prediction for the prediction error neurons, and in turn it receives excitatory drive from the positive prediction error neurons and negative input from the negative prediction error neurons.

The authors find that the functional impact of L5 neurons to L2/3 neurons is not compatible with the non-hierarchical architecture they and other groups proposed, but rather in accordance with the hierarchical model. At the same time, the functional impact of L2/3 neurons (positive vs. negative prediction error neurons) on L5 neurons (internal representation) appears not compatible with the hierarchical model, but rather in accordance with the non-hierarchical implementation.

They further hypothesize that L2/3 prediction error neurons don't use sensory input, but rather the L5 activity as a teaching signal, and test it using perturbations (halts) of optogenetic stimulation of L5 neurons coupled with locomotion (Fig.7).

All in all, the question is topical, and the new model addresses a decades-long quest to develop a unifying model of cortical function. The findings reported here transform our understanding of cortical computations, opening new exciting avenues for future investigation. The experimental design and execution are rigorous; the arguments are clearly laid out (in spite of ample potential for confusion given the numerous loops and sign flips). These include a discussion of why the non-hierarchical model proposed by the same group does not hold, as well as potential caveats in interpreting the results and novel testable proposed experiments emerging from the JEPA-like model.

Comments on revised version

I commend the authors for nicely provided answers and addressing my concerns and clarifying their points on the relationship of their findings to JEPA and current state of understanding.

In particular for Q5 -I meant if there is also a positive correlation between optomotor mismatch response and visuomotor mismatch response when looking only at neurons that the authors identify as PE-?<br /> The authors provided the answer on point.

Overall, I think this is a fundamental study and the strength of evidence for the claims is exceptional as an exemplary use of existing approaches.

Reviewer #2 (Public review):

This manuscript reveals functional connectivity of two different classed of cortical neurons that respond in opposite ways to mismatches between sensory and top-down inputs. These data are very valuable because different theories of information processing in the cortex make different predictions on the patterns of connectivity of these neurons. Therefore, these data strongly constrain possible theories of cortical processing.

Comments on revised version.

I thank the Authors for answering my questions and updating the manuscript.

Congratulations on this important work!

Reviewer #3 (Public review):

Vasilevskaya and Keller set out to experimentally distinguish between two variants of predictive processing: a hierarchical and a non-hierarchical variant. The hierarchical variant assumes a hierarchical organization in which internal representation neurons (believed to be a subset of layer 5 excitatory neurons) serve as a source of a teaching signal for local prediction error neurons as well as for the next higher level of the hierarchy, while simultaneously providing prediction signals to the preceding lower level. In contrast, the non-hierarchical variant posits that these layer 5 internal representation neurons provide local predictions to layer 2/3 prediction error neurons.

The interaction between internal representation neurons and prediction error neurons differs fundamentally between the two variants. In the hierarchical variant, internal representation neurons excite positive prediction error neurons and inhibit negative prediction error neurons, while at the same time being inhibited by positive prediction error neurons and excited by negative prediction error neurons. In the non-hierarchical variant, this pattern of connectivity is reversed.

This work is very exciting, timely, and carefully executed. The authors functionally, and later molecularly, identify layer 2/3 prediction error neurons in V1 and probe their interactions with genetically defined neuron types in cortical layers 5 and 6 using optogenetics. They demonstrate that the functional influence of putative prediction error neurons in layer 2/3 onto layer 5 is incompatible with the hierarchical variant, whereas the influence of layer 5 onto putative prediction error neurons in layer 2/3 is incompatible with the non-hierarchical variant. They then test an alternative hypothesis, in which layer 2/3 responses resemble prediction errors with respect to perturbations of artificial layer 5 activity patterns. To investigate this, they designed an experiment in which optogenetic activation of L5 IT neurons was closed-loop coupled to the mouse's locomotion speed in the absence of visual feedback, allowing them to probe the causal influence of L5 activity on layer 2/3 responses.

Finally, the authors hypothesize that their data are more consistent with a joint embedding predictive architecture (JEPA) and outline experimentally testable predictions arising from this framework.

While the work is overall convincing and provides important insights into the circuit-level implementation of predictive processing, I think the connection to JEPA networks would benefit from a more in-depth discussion of its relationship to recently proposed and implemented models. Below, I address the specific points raised by the authors (flanked by ' ... ' to make the author's statements stand out), in particular in relation to the model proposed by Nejad et al. (2025):

- 'The two proposals indeed share similarities in assuming that bottom-up input for both L2/3 and L5 arrives from thalamus, and that representations formed in L2/3 are used for predicting the activity of L5. However, there are a few important differences between the JEPA implementation proposal formulated here and the Nejad et al. model.

(1) There is no proposed mapping of computations in the Nejad et al. model onto different JEPA networks. We assume that the suggested mapping would be L4 and L5 as encoder networks, and L2/3 as a predictor network? In that case, it is different to our proposal, in which L2/3 is part of the encoder network.'

I think there is some confusion here. In Nejad et al., both L2/3 and L5 function as encoder networks. Each receives sensory input (with L2/3 receiving this input delayed via L4) and computes a latent representation of that input, denoted z_{L2/3} and z_{L5}, respectively. The prediction is obtained by comparing the output of L2/3 with L5 latent representations (via W_{L2/3->L5} * z_{L2/3}). In other words, L5 is the target in the learning objective.

Although, they did not explicitly state the mapping with JEPA, their model has the same fundamental property - predictive learning happens in the latent space. Also, this appears very similar to the roles assigned to L2/3 and L5 in your Figure 9B. The fact that you made this more explicit and the new data included, is in my view, a very interesting contribution. However, from an architectural perspective, it appears that your proposal and the model of Nejad et al. are conceptually very similar, and I do not see a substantial difference between the two. This should be made more clear in the Discussion.

- '2. Our proposal contains explicit prediction error neuron cell types within L2/3, while prediction errors in Nejad et al. are encoded in the gradients, and the layer origin of these signals is hypothesized to be L5 ('the learning-driving error signal originates in L5'). Hence, also the role of L5-L2/3 connection is distinct between the two proposals. In Nejad et al. this connection serves the role of error propagation and update for predictions in L2/3, while in our proposal this connection contains teaching signal (target representations) that are compared to predictions within L2/3. Similarly, the functional role of L2/3-L5 connection is also different, since in Nejad et al, it is supposed to carry predictions of L5 activity, whereas in our proposal we expect it to drive plasticity in L5 encoder.'

Indeed, in Nejad et al., the layer-dependent mismatch responses are modeled as gradients with respect to neuronal activity, and the model does not explicitly include prediction error neurons. However, this appears to be a modeling choice rather than a fundamental aspect of the proposal, and it does not preclude an implementation with explicit prediction error neurons. In fact, the authors explicitly acknowledge this possibility in the Discussion:

"The second approach would be to recast our model within a predictive coding framework... Predictive coding jointly optimizes both model parameters and neuronal activities, which could naturally lead to prediction errors observable in the activity of both L2/3 and L5 neurons. Note that these two views are not mutually exclusive."

While Nejad et al. hypothesize that the learning-driving error signals (that are distinct from their mismatch responses) originate in L5, the abstract loss function itself does not uniquely specify where the underlying comparison between the predicted representation (W_{L2/3 -> L5} z_{L2/3}) and the target representation (z_{L5}) must be implemented. The proposed biological implementation places this computation in L5, but from my understanding, the computational objective itself does not require this specific localization.

That said, I agree that your proposed model introduces a genuine difference. The functional roles assigned to the vertical projections are effectively reversed: in Nejad et al., the L2/3->L5 projection carries the prediction, whereas the L5->L2/3 projection conveys the error/gradient. In your architecture, by contrast, the L5->L2/3 projection carries the teaching signal (target). This is, in my view, a real and testable interpretational divergence that is worth stating clearly.

Therefore, I think the novelty lies less in the computational architecture itself and more in committing to a particular biological implementation-one that adds cell-type-specific detail to an implementation that Nejad et al. hypothesised as being compatible with their framework.

- '3. The difference outlined above also makes it evident that the two proposals should differ in how deep and superficial layers are expected to influence the activity of one another. Indeed, the proposal in Nejad et al. is based on the cortical column idea, and according to eq. 2 and 3 in the Methods, activity in L5 is a function of activity in L2/3, while activity in L2/3 is not a function of activity in L5. Our proposal is based on idea of layers forming parallel networks, where horizontal communication is the dominant mode of cortico-cortical interactions, and activity in deep layers serve as a teaching signal for L2/3. In our case, we expect the opposite - that activity in L2/3 depends on activity of L5, while activity of L5 is not immediately dependent on activity of L2/3 (only via plasticity route). This led us to propose one of direct tests for our framework - silencing L2/3 in a familiar setting should result in no immediate changes to L5 activity and behavior of the animal.'

My reading of Nejad et al. is consistent with your interpretation of the equations. Specifically, Eq. 3 makes L5 activity depend on L2/3 activity (albeit weakly, with a = 0.3), whereas Eq. 2 contains no L5 term, so L2/3 activity does not depend directly on L5 activity. In that model, the L5->L2/3 pathway carries the learning gradient rather than contributing to the activity dynamics. By contrast, in your proposed model, L2/3 activity depends on L5 activity, whereas L5 activity is not immediately dependent on L2/3 activity (except indirectly through learning/plasticity). So, you state that "silencing L2/3 in a familiar setting should result in no immediate changes in L5 activity.<br /> [...].

However, I am unsure how to reconcile this prediction with the results shown in Fig. 6. If I understand the figure correctly, optogenetic activation of Rrad-positive (positive prediction error) L2/3 neurons produces a small increase in L5 activity, whereas activation of Adamts2-positive (negative prediction error) L2/3 neurons produces a decrease in L5 activity. Although these experiments involve activation rather than silencing, they nevertheless suggest that perturbing L2/3 activity can have an immediate effect on L5 activity. Could you clarify how this is consistent with the proposed model? In other words, what aspect of the proposed circuitry makes activation effective while silencing is predicted to have no immediate consequence?

For comparison, Nejad et al. performed a related perturbation analysis in Fig. S15 by scaling the output of L2/3 neurons exhibiting positive mismatch signals (defined through the activity gradients), which increased L5 activity, whereas scaling neurons with negative mismatch signals produced the opposite effect. I am not entirely sure how directly these simulations map onto the experiments shown in your Fig. 6, since the Nejad simulations were performed during mismatch conditions, if I have understood them correctly.

- '4. The proposal in Nejad et al. relies on input reconstruction or variance maximization within the L5 autoencoder network to avoid collapse. Instead, our proposal has no reconstruction objective.'

Nejad et al. only require two encoders (like in JEPA), how these two are learnt can be done in several ways. While Nejad et al. focus on using a reconstruction loss to learn the L5 target, they also show that it works equally well with non-reconstruction objectives. Therefore, I do not think the presence or absence of a reconstruction objective constitutes a fundamental distinction between the two proposals.

As your current work presents a conceptual architecture rather than a fully implemented learning algorithm (in a model), the mechanism that would prevent representational collapse has not yet been defined. From my understanding, every joint-embedding approach must address this issue, whether through reconstruction, variance/covariance regularization, stop-gradient or EMA mechanisms, or other approaches. Thus, the absence of a reconstruction objective (or another anti-collapse mechanism) is not, in itself, a distinguishing feature of the proposed architecture, but rather an as-yet unspecified design choice within the learning objective.

- '5. Lastly, there is time-delay between inputs to L5 and L2/3 that is proposed in Nejad et al., while this is not something inherent to our proposal.'

I agree that the temporal delay introduced by L4 is a key component of the Nejad et al. model and is currently absent from your proposal. However, I would expect temporal delays to emerge naturally in your framework as well, given the multisynaptic and highly parallel organization of cortical circuits. More generally, implementing predictive learning over time (as in JEPA) requires comparing representations at times t and t+1, which seems to require some form of temporal delay. How else would you suggest this is done?

In general, I think the manuscript would benefit from a clearer discussion of its relationship to the model proposed by Nejad et al. (perhaps following the discussion above), including both the shared conceptual claims and the aspects that genuinely differ between the two frameworks. At present, some of the claims are presented as novel, although at least some of these core ideas have already been proposed in Nejad et al.

For example, the authors state: "Thus, we propose that layer 2/3 functions to predict layer 5 activity, not sensory input per se, hence making predictions in the internal representation space, not input space." This appears to be exactly what Nejad et al. proposed as discussed above - in their model L2/3 predicts L5 activity (purely in the latent space), as they state in the abstract.

That said, there are some interesting differences, and I think the community would greatly benefit from making these clear, including the roles assigned to interlaminar connections and the interpretation of the signals carried by these pathways. These differences are interesting and potentially testable, and I think the manuscript would be strengthened by explicitly distinguishing which aspects are in line with the ideas already present in Nejad et al. and which aspects represent new contributions.

Reviewer #1 (Public review):

Summary:

This work asks the question of how different organelles and structures in the apicomplexan parasite Toxoplasma gondii are recycled and/or segregated to the daughter cells during cell replication. In particular, they consider an unusual cell structure called the residual body that links replicating cells during the intracellular infection stage of this parasite. The residual body has historically been considered a 'dumping ground' for unnecessary relics of the mother cell during division, but this notion is increasingly being revised. Indeed, cell replication in Toxoplasma is often misinterpreted as cell division (cytokinesis), but in fact, the cell replicates its organelles and structures to multiple 10s of copies in seemingly distinctly formed daughter cells, but cytokinesis is delayed for many such cycles and typically only occurs simultaneously with parasite egress from its host cell. The residual body is, in fact, the connection between these pre-cytokinetic replicated daughters, and effectively, this is still a single cell at this stage. The authors have previously shown that an actin network extends through the residual body between these daughter cells, and ER and mitochondria common to all cells are also linked through this structure. This study examining the fates of organelles during cell replication is timely for continuing our understanding of how this fascinating component of the cell participates in these processes. The authors use Halo-tags as their principal tool to track discrete populations of proteins, labelling their organelle locations, and this provides beautiful insight into these processes.

Strengths:

Using dyes conjugated to Halo tags this work elegantly tracks the fates of proteins synthesised by an original 'mother' cell over several replication cycles of pre-cytokinetic 'daughters'. Using this tool, they show that some organelles are made intact just once and that some of these can be subsequently sorted to the daughters (micronemes and rhoptries) while others are dismantled (IMC) and the daughters must make their own. A third set of organelles (largely synthesis, sorting and metabolic compartments) are divided and inherited, and new daughter-synthesised proteins are added to the preexisting maternal proteins in these structures. A role for actin and myosin is clearly demonstrated for micronemes and rhoptries, and this correlates with their relatively late inheritance into the developing daughters. Overall, this work gives clarity to the behaviours of several cell structures during replication and paves the way to better understanding the mechanisms that drive the differences between structures and the universality of these processes in other apicomplexan parasites. In particular, this study shows that the residue body is a region of the cell syncytium that organelles can be actively transported from. Therefore, it is a space that can actively contribute to the segregation of the late segregating micronemes and rhoptries.

Weaknesses:

In addressing the question of residual body participation in sorting of organelles, a clear definition of this structure is required including when and where it is delineated from the posterior of a mother cell during the formation of daughter structures. The authors' definition is as follows: 'The RB originates from the collapse of the maternal parasite during daughter cell budding and occupies the space previously occupied by the mother cell.' As such, a clear marker of the mother cell 'collapse' is required, but such a marker is not identified or used in the study to separate what might be considered an active part of the mother cell during early daughter formation, and the residual body. This might seem like moot a point, but it would help to give clarity to notions of recycling and 'reservoirs'. Mother cells retain their active invasion apparatus until very late in daughter formation and the need for micronemes and rhoptries to be released from this service late in the process might explain why they are only then trafficked to the cell posterior and then into the daughters. So, is this a distinct 'residual body' body function/reservoir or just a spatial constraint of this sequence of daughter formation? The authors elegantly show that MyoF is necessary for segregation of micronemes and rhoptries into daughters, and that MyoF depletion leads to accumulation of these organelles within the residual body. Moreover, restored expression of MyoF can then recover these organelles. This clearly demonstrates the activity of the residual body as part of the syncytium space that participates in the maintenance of the vacuole. But does it imply that this space necessarily handles all inherited micronemes and rhoptries as a 'trafficking hub'? My concern with the lack of a clear definition could provide some misinterpretation or overinterpretation of the contribution residual body.

A further, remarkable conclusion is that maternal micronemes are evenly segregated into daughters through an active process for 'balanced microneme inheritance'. The proportion of maternal micronemes is quantified up to the 8-cell stage and shown to be not significantly different between cells. But would this result be expected with random assortment at this stage? The authors model the probability of a 32-cell stage vacuole occurring with each daughter having within 0-3 maternal micronemes and this is considered unlikely. However, the authors neither present the modelling for the 8-cell stage or show quantification of 32-cell vacuoles. They do show some images of large vacuoles, but it is not possible to determine the distribution of maternal micronemes in these images. A regulated process of segregation would require a complex mechanism where some form of microneme counting would be required to create the proposed balance. It is, therefore, important to have strong data supporting such a hypothesis, but this is not currently presented.

Reviewer #2 (Public review):

Summary:

Toxoplasma gondii is an obligate intracellular parasite and the causative agent of toxoplasmosis. Parasite invasion of host cells, intracellular replication, and subsequent egress, which results in destruction of the infected cell, are central to pathogenicity. This manuscript focuses on understanding how maternal resources, specifically cellular organelles, are shared between daughter parasites during cell division. Many organelles are present as a single copy, making their division and inheritance essential for successful replication. In T. gondii, our understanding of how organelles are divided during cell division remains limited, and this study helps address this important knowledge gap.

Strengths:

The major strength of this study is the use of a Halo-based pulse-chase assay to characterize patterns of organelle inheritance and to monitor protein synthesis, turnover, and movement. This approach will be of considerable interest to the field. Using this method, the authors identify three major modes of organelle inheritance:

(1) Organelles present in multiple copies (such as micronemes and rhoptries) are partitioned between daughter parasites, with additional contributions from newly formed vesicles. Newly synthesized and pre-existing material remain as distinct populations within the cell.

(2) Single-copy organelles, such as the Golgi and apicoplast, are expanded through the incorporation of newly synthesized material before division.

(3) Cytoskeletal structures are synthesized de novo during each round of cell division.

These findings provide a more refined understanding of organelle inheritance and demonstrate that secretory organelles are not generated entirely de novo during each round of division, as was previously thought.

The paper places particular emphasis on the fate of maternal micronemes and rhoptries during division. The data show that (1) during division in wild-type cells, maternal micronemes and rhoptries are detectable in the residual body (RB); however, the majority of these organelles are localized within the parasite body, either at the apical or basal ends of the daughter parasites (Fig. 6). (2) In the absence of the myosin motor MyoF, micronemes and rhoptries accumulate in the residual body and are not properly trafficked to the daughter cells. Upon restoration of MyoF protein levels, these organelles redistribute to the daughter cells, although in an uneven manner.

Weaknesses:

The second half of the paper focuses on a more detailed characterization of microneme and rhoptry recycling. The authors strongly argue that the RB is a central hub for recycling micronemes and rhoptries; however, this conclusion is not fully supported by the data. For example, the authors state:

Line 227:<br /> "Notably, after endodyogeny was completed, M-MIC2 was redistributed from the RB to the apical tip of the daughter cells (Figure 6A, 11:30, 16:00 h), confirming that the RB serves as a temporary reservoir during microneme recycling (Periz et al., 2019)."

Line 231:<br /> "In approximately 90% of parasites undergoing replication, M-RON2 was integrated into daughter rhoptries prior to mother cell collapse and formation of the RB (Figure 6B, 4:15-4:30 h and 10:30-10:45 h). Like M-MIC2, M-RON2 was occasionally detected in the RB, though less prominently, suggesting more rapid, tightly regulated, or more efficient recycling due to their lower number."

Line 326:<br /> "However, we show that the RB temporarily stores maternal secretory organelles, such as micronemes and rhoptries, which are later redistributed to daughter cells in a MyoF-dependent manner (Figure 9B)."

Thus, the model that all microneme and rhoptry trafficking is RB-dependent is based primarily on the MyoF depletion phenotype (which results in RB accumulation) together with the observation that a relatively small amount of maternal microneme and rhoptry material is detectable in the RB of wild-type parasites. Although the authors' interpretation-that recycling is RB-dependent-is one possible explanation, alternative models are not discussed.<br /> For example, an alternative possibility is that the majority of micronemes and rhoptries are trafficked directly from the apical end of the mother parasite to the daughter cells without passing through the RB. In this scenario, only a subset of the organelles would enter the residual body, perhaps reflecting imperfect trafficking efficiency rather than an obligatory recycling step. Loss of MyoF would impair this trafficking pathway, resulting in the accumulation of secretory organelles within the RB. In other words, RB accumulation could be a consequence of MyoF depletion rather than evidence that all trafficking in wild-type parasites normally proceeds through the RB.

This alternative interpretation seems particularly relevant for the rhoptries, given that the authors themselves state that "M-RON2 was integrated into daughter rhoptries prior to mother cell collapse and formation of the RB."

Other comments:

Figure S10C<br /> To determine whether microneme degradation occurs in the RB, the authors quantified the fluorescence intensity of individual micronemes in control parasites and following auxin washout, showing that after redistribution the fluorescence intensity of individual vesicles is unchanged. However, this is not the appropriate analysis to address the question being asked. To conclude that micronemes are not degraded, the authors would need to quantify the total fluorescence intensity within the entire vacuole. For example, if half of the micronemes were degraded, the remaining micronemes would be expected to retain the same fluorescence intensity as those in the control parasites. Thus, unchanged fluorescence intensity of individual vesicles does not exclude the possibility that degradation has occurred.

Reviewer #3 (Public review):

Summary:

Knoerzer-Suckow et al. explore the mechanisms of organelle inheritance during endodyogeny in Toxoplasma gondii using an innovative dual-labeling approach to track the distribution of maternal organelles into daughter parasites. They can clearly distinguish between maternal and daughter-derived organelles using their dual-labeling Halo Tag approach. They reveal that different organelles are trafficked to daughter parasites in three broad patterns they have binned into groups. Their findings reveal a role for MyoF in the inheritance of micronemes and rhoptries, and notably, they observe that the inner membrane complex (IMC) is not recycled. Instead, the IMC undergoes a pronounced relocalization to the posterior of the maternal cell, where it is likely targeted for degradation.

Strength:

The data surrounding their MyoF knockdown experiments, IMC degradation, and trafficking of MIC2 after auxin washout are convincing. These data add to the knowledge of how organelle inheritance occurs in T. gondii, increasing the field's understanding of endodyogeny.

Weakness:

The inability to achieve higher temporal resolution due to phototoxicity precluded tracking of single micronemes, thus it remains possible that some micronemes follow a path similar to rhoptries and enter daughter cells before development of the residual body while others are recycled via the residual body.

Reviewer #2 (Public review):

The authors use a library of influenza A viruses from different strains, classified in lab-adapted, human, avian, and swine according to the animal from which they were isolated. They propose that the cow mammary gland serves as a mixing vessel for influenza A viruses. As a first approach, the authors assess susceptibility to infection across different cell types, including continuous and primary cell lines, bovine mammary cells, and mammary explants. All these cells support polymerase activity. Then, they analyzed changes in the bovine virus's viral fitness relative to an avian precursor. The authors use single-gene replacement to study whether and which RNP segments improve viral transcription. As part of this section, they also test IFN-specific antagonism by NS1 to assess the input of segment 8. Quantitative glycomic analysis was performed on the continuous bovine mammary cell line to demonstrate the presence of both a2,3 and a2,6, which is consistent with their observation that these cells can be co-infected with human and avian IAVs simultaneously. The main question, however, is: what is the glycome in the explants, or directly from tissues?

Overall, the manuscript is clearly written and provides new insights into the behaviour of the cattle isolate, now compared with a representative group of model or precursor HAs of different origins.

It would be great if a consistent nomenclature for the IAV strains could be used in the study. There is a mix of origin (Texas), animal from which the virus was isolated (mallard), or abbreviations that do not follow guidelines (IAV07). Are the USSR and Udorn not lab-adapted?

The experimental setup includes bovine mammary primary and continuous cells, as well as mammary explants. Some of the most significant differences, for example, in viral fitness studies and co-infection experiments, are observed in these explants. Perhaps there could be some additional focus on this observation. The implications in comparison to the results obtained in cultured cells could be described. How will the human and other HA subtype viruses fare in the explants?

Comments on revised version.

The authors have satisfactorily addressed the reviewers' comments.

Reviewer #3 (Public review):

Summary:

This excellent manuscript by Pinto, Sharp, and colleagues examines bovine tissue tropism for influenza viruses. They find that bovine flu, as well as other strains, have strong replication in mammary tissue. They also map the genetic changes to influenza that improve replication in bovine cells. Overall, the study is well designed and executed and the results are very timely.

Strengths:

(1) The experiments are well-controlled.

(2) The figures are well-constructed and easy to follow.

(3) The Methods and legends are detailed, with sufficient information.

Comment on revised version.

The authors have strengthened the manuscript by addressing comments from the three reviewers and I have no additional concerns/suggestions.

Reviewer #1 (Public review):

In this article, the authors set out to understand how evolutionary selection could introduce structural priors into neural networks that act as an inductive bias to accelerate learning. To do so, the authors propose an evolutionary conditioning (ED) algorithm and analyse its properties. I find the conceptual framing of the paper very interesting, and it addresses an important question. Since the paper adopts a mostly theoretical approach with no comparison to empirical biological data, I do have a couple of concerns regarding the setup of the computational framework/method, which I think is incomplete and limits how much we can conclude from the current results.

Major Concerns:

(1) The evolutionary conditioning (EC) algorithm proposed works as fine-tuning training, plus propagation of the best parent network's weights to the next generation with added Gaussian noise. Conceptually, I find this to be a fairly implausible mechanism for evolution, since it requires carrying the entire set of network weights at some precision. The authors themselves point out that direct weight transfer could be problematic in the introduction.

(2) More importantly, I would like the authors to conduct a baseline / null model comparison, in which the "evolution" process consists simply of training a neural network for a small number of iterations, adding Gaussian noise, and repeating. The resulting network at each step serves as the "generations", which is then trained further. The same learning speed and dynamics analyses should be applied to this null model. What I am getting at is that I am not sure to what extent the EC algorithm can be thought of as "running a few iterations of SGD" and chaining them together; how much work is the selection process in the GA actually doing?

(3) I am also unclear on why the EC algorithm does not improve throughout learning. Is this behavior the result of applying only a small number of fine-tuning steps? Presumably, with longer fine-tuning, the individual networks in the middle generations would also improve in performance?

(4) The EC algorithm applied to a single problem seems somewhat artificial in its setup. I would conceptualize evolution as learning a prior that conditions the network for a range of survival-related tasks. A more realistic setup would apply EC to an ensemble of tasks and then examine its impact on learning a specific task afterwards.

Reviewer #2 (Public review):

Summary:

This paper studies the interplay of evolutionary and in-lifetime learning. The authors develop a neural network model in which initial weight configurations evolve under selective pressure, while fitness is determined by the network's performance after a learning period. They show that such a network displays very distinct learning dynamics from those trained by either gradient descent or genetic algorithms alone: in particular, they do not learn the task, but they show evidence of learning-to-learn and unusual representational structure.

Strengths:

(1) The writing, figures, and presentation of ideas were clear.

(2) The question of how evolution on initial weights combines with learning from within-lifetime experience to structure a learning trajectory seems interesting.

(3) The analysis of existing experiments was well-done, highlighting that though these networks did not really learn, they show latent learning structure that makes the network perform better from less data.

(4) The interplay between Baldwin & learning dynamics seemed novel and interesting, presenting many attractive puzzles.

Weaknesses:

First, the authors point to an important distinction between performing evolutionary selection on the weights pre- or post- lifetime training, the latter of which is Lamarckian. They argue, correctly, that their model is interesting because it selects on the weight initialisation, unlike, for example, Shuvaev et al. However, my understanding is that a long line of papers beginning perhaps with Hinton & Nowlan also do non-Lamarckian evolution: Hinton & Nowlan have unspecified weights (denoted '?' in the paper) that can be inherited and then learnt. Is this not exactly inheritance of initial conditions (in this case, whether learnable or not)? This novelty is a primary motivation of the paper, whereas to me it seems it was already apparent in Hinton & Nowlan, and developed further in what seems to be a long line of uncited literature (see next paragraph). As such, this paper's conclusions seem poorly positioned within the existing state of knowledge/literature.

Second, the algorithm is framed as novel, but I think it is a rediscovery. This framework is very close to MAML, in which an initial weight configuration is optimised by gradient descent to be good after a few steps of fine-tuning (Finn et al., 2017). The authors' approach differs in using a genetic algorithm to perform the training of the initial weights, avoiding some of the computational complexities of MAML, especially after long fine-tuning. In this, the authors have, I think, rediscovered ES-MAML, MAML where the inner optimisation loop is gradient descent, while the outer is genetic (Song et al., 2020). Other similar work is "Meta-Learning by the Baldwin Effect" (Fernando et al., 2018).

Further, within Fernando et al. there is a rich literature review, almost none of which are cited by the authors. I point especially to Keesing & Stork, 1990, which appears to show a strong dependence of Baldwin-like improvements on the amount of data, something this paper also shows but explores less thoroughly.

To summarise my critique thus far: I think the literature already answers the main concern of the motivation (i.e. non-Lamarckian neural network evolution and learning), I think it has already discovered this particular algorithm, and I think past work has more thoroughly analysed behaviours similar to those presented in this paper. Without positioning correctly within this literature, the more general contribution of the paper is hard to establish. The true novelty of the authors' analysis seems to be the emphasis on Saxe et al.-like learning dynamics and its interplay with the Baldwin effect, but I am not certain of this without knowing the literature better.

Regarding experiments, there was an interesting effect where the EC networks didn't learn but did show latent learning (Figure 2, Figure 3), which sped up later learning (Figure 4). There were a few details I was surprised by on which I would appreciate clarity:

(1) The main result has basically no headline learning under EC. This will clearly be very dependent on parameters (e.g. if you add or remove enough training steps, the algorithm becomes SGD/GA, which both show learning). It seems like a natural analysis would examine this (e.g. a plot of final performance of EC after 4000 generations with different per-generation learning budgets).

(2) It is then shown that after 4000 generations EC can learn very quickly to perform the semantic task perfectly, at least within 200 generations (Figure 4C, and perhaps much sooner, Figure 4D, Figure 4F last panel; it was hard to say. This and the previous point seem somewhat inconsistent; was it just that Figure 3 used only 100 fine-tuning steps while the perfect-task-performing networks in Figure 4 required somewhere between 100 and 200? This seems to point to extreme parameter dependence. More broadly, how should I square this inconsistency/near-inconsistency?

(3) Figure 3k, and especially Figure 4f bottom right panel, seem to show networks that correctly separate all stimuli but cannot classify them. Should I understand this as networks learning to just push apart all pairs of datapoints without structure?

(4) If I understood the genetic algorithm correctly, only three individuals from each population seeded the next generation. This seems another important parameter to tune, since I think it is far lower than standard evolutionary work, but I am not sure.

Finally, the paper most interested me as a neural network learning puzzle: how can the network perform so badly, yet lead to such different post-fine-tuning results? The paper pointed to these as 'distinct' learning phenomena without explaining what was causing those differences. The only way I could square these results in my head was as above: that the 4000 generations pushed the initial representation to represent all datapoints differntly, effectively changing the learning problem gradient descent faces from one with a lot of structure (the semantic task) that leads to stepwise learning, to one in which it was basically linear regression on a set of well separated stimuli without the structure necessary for stepwise learning. Since the paper focuses so much on learning dynamics, and studies a task where such things can be precisely probed, it would have been nice to pin down exactly what was happening slightly more.

Reviewer #1 (Public review):

Summary:

This work by Beaudet and colleagues aims at exploring the effect of phosphorylation on the formation of tau envelopes and consequently on axonal transport both in vitro on reconstituted microtubules and in human excitatory neurons derived from IPSCs.

The authors found that a relatively widely used construct in which 14 serine or threonine residues often hyperphosphorylated in Alzheimer's disease are mutated to alanines (phosphodeficient) increases the density of tau envelopes compared to wildtype tau whereas a phosphomimetic (same residues mutated to glutamic acid) reduces envelopes density both in vitro and in human excitatory neurons derived from IPSCs.

By analysing the trafficking of different kinesins (KIF1a and KIF5C), they observed different effects of tau phosphorylation status on the movement of these two motors.

They then analyse transport of lysosomes by employing live imaging of lysotracker in human excitatory neurons derived from IPSCs transfected with wildtype, phosphodeficient or phosphomimetic tau observing that phosphodeficient tau seems to reduce transport of lysosomes while phosphomimetic increases transport compared to wildtype tau.

Strengths:

(1) The work aims to study a novel and underexplored topic in the tau field, tau envelopes, and investigate their relevance to Alzheimer's disease pathology.

(2) Experiments are well conducted and of high quality.

Weaknesses:

Relying only on in vitro reconstituted microtubules and human neurons derived from IPSCs leaves some doubts about the relevance of these results for Alzheimer's disease considering the embryonic state of IPSCs-derived neurons, but the authors clearly discuss this point.

Reviewer #2 (Public review):

This manuscript examines how disease-associated hyperphosphorylation disrupts tau's role as a cooperative microtubule-binding regulator of intracellular transport. Using in vitro reconstitution assays and live-cell imaging in iPSC-derived neurons, the authors employ phosphomutant tau constructs (E14 to mimic hyperphosphorylation, AP to prevent phosphorylation) at 14 disease-associated residues to isolate phosphorylation effects independent of expression system-dependent PTM heterogeneity. The results show that hyperphosphorylated tau fails to form cooperative envelope-like structures on microtubules, instead binding diffusely and dissociating rapidly. In contrast, wild-type and phospho-resistant tau form cohesive envelopes that regulate motor protein access. At the single-molecule level, hyperphosphorylation reduces KIF5C inhibition while maintaining or enhancing KIF1A inhibition through altered processivity and detachment rates. In live neurons, hyperphosphorylated tau phenocopies tau knockout conditions, weakening tau-mediated inhibition of lysosome transport and increasing processive motility. The authors quantify tau binding using Gaussian mixture model-based image analysis and measure tau kinetics via FRAP, demonstrating that hyperphosphorylation-induced loss of cooperative binding correlates with dysregulated organelle transport. These findings establish a mechanism by which phosphorylation-driven disruption of tau's gatekeeper function on microtubules compromises axonal transport prior to aggregation in tauopathies.

Comments on revised version.

The authors did a good job responding to my comments and I support publication of the revised manuscript.

Reviewer #1 (Public review):

Summary:

This paper proposes a non-decision time (NDT)-informed approach to estimating time-varying decision thresholds in diffusion models of decision making. The manuscript motivates the method well, outlines the identifiability issues it is intended to address, and evaluates it using simulations and two empirical datasets. The aim is clear, the scope is deliberately focused, and the manuscript is well written. The core idea is interesting, technically grounded, and a meaningful contribution to ongoing work on collapsing thresholds.

Strengths:

The manuscript is logically structured and easy to follow. The emphasis on parameter recovery is appropriate and appreciated. The finding that the exponential NDT-informed function produces substantially better recovery than the hyperbolic form is useful, given the importance placed on identifiability earlier in the paper. The threshold visualisations are also helpful for interpreting what the models are doing. Overall, the work offers a well-defined, methodologically oriented contribution that will interest researchers working on time-varying thresholds.

Weaknesses / Areas for Clarification:

A few points would benefit from additional clarification following the previous revision:

Returning to one point from my original review. The applications to empirical data describe 6 models, including the FT-DDM with across-trial variability described as a benchmark. Yet the modelling results for both studies (Tables 2 and 3) show only 5 models, omitting the benchmark model. I acknowledge the comment about this in the response letter (no other FT-DDM models in the main text have across-trial variability). Nevertheless, for this to serve as a benchmark, the modelling results really should be reported in Tables 2 and 3 with the other 5 models, and the model goodness of fit figures currently shown in Appendix 7 incorporated into Figures 10 and 13 of the main text. Unfortunately, as it currently reads, it looks as if something is being obscured, which I don't believe is the intention. This won't change the primary conclusions, but it will increase transparency and ease of interpretation.

Many thanks for introducing Appendix 1 to the revised manuscript. Additional motivation for the central issue is always helpful. However, I'm not (yet) convinced the simulation study in Appendix 1 achieves the intended aim. The simulation study shows that NDT misspecification leads to poorer recovery of other CT parameters (i.e., if a generating value is perturbed and then held fixed at that perturbed value during estimation, recovery of the remaining parameters deteriorates). This demonstrates the consequences of fixing NDT incorrectly, but it does not seem to address the central claim of the manuscript: that NDT and the CT threshold parameters trade off when they are estimated simultaneously. I had expected the simulation study to estimate NDT alongside the remaining model parameters, mirroring the estimation procedure used in the empirical analyses. Such a simulation would directly test whether the two sets of parameters compensate for one another during estimation, and whether this results in poor recovery of the NDT parameters.

Reviewer #2 (Public review):

Summary:

The authors use simulations and empirical data fitting in order to demonstrate that informing a decision model using noisy single-trial estimates of an underlying fixed non-decision time can guide the model to more reliable parameter estimates, especially when the model has collapsing bounds.

Strengths:

The paper is well written and motivated, with clear depth of knowledge in the areas of neurophysiology of decision-making, sequential sampling models, and in particular, the phenomenon of collapsing decision bounds.

Two large-scale simulations are run to test parameter recovery, and two empirical datasets are fit and assessed; the fitting procedures themselves are state-of-the-art, and the study makes use of a very new and well-designed ERP decomposition algorithm that provides single-trial estimates of the duration of diffusion; the results provide inferences about the operation of decision bound collapse - all of this is impressive.

Weaknesses:

This is an interesting and promising idea, but a very important issue is not clear: it is an intuitive principle that information from an external empirical source can enhance the reliability of parameter estimates for a given model, but how can the overall BIC improve, unless it is in fact a different model?

Comment on revised version.

Thanks to the authors for their responses and inclusion of additional analyses and simulations. Thanks, in particular for clarifying a crucial detail, that the ndt-informed model actually assumes, like the uninformed model, that there is no variability in the non-decision time, and the idea is that the variable single-trial measurements of non-decision time are noisy estimates of an underlying, constant ndt. The revised paper itself has not made this clear - for example, throughout the Intro, there is no statement that the behavioural model assumes a trial-invariant ndt, and line 231 still calls tau the 'mean' non decision time, implying there is a distribution rather than an invariant single value in the behavioural model.

One implication of the above is that if the lognormal sigma is purely measurement noise that does not relate to actual variation in the underlying decision process generating behaviour, then the HMP latencies should not relate to behaviour, e.g. shorter latencies predicting shorter RT. I assume that even if the authors did find such a relationship, the principle still stands that a model with fixed ndt is more accurately fit when there are single-trial ndt estimates whose mean provides a constraint on that ndt value, than without such measurements. Still, given ndt variability is a core feature of many decision models, the authors could comment on whether the strategy would work in theory for a model with ndt variability (in the behavioural part), where the single trial estimates would then presumably reflect a mix of measurement noise and genuine ndt variability.

Another more important implication is that since it is in fact the same model being compared with and without the HMP data guiding the fixed ndt estimate, the reason the fit quality improves with HMP-information is not because it is a better model per se (it is the same model) but because without the HMP guidance, the search algorithm somehow gets lost and fails to find the 'optimal' parameter vector. That is, the parameter vector (just the parameters that relate to the behavioural model itself, not the HMP lognormally-distributed noise associated with VEP measurements) identified as optimal in the HMP-informed version of the model exists in the parameter space of the model without HMP information, but it is just not found? I raised this implication before, and it is still not clear whether it applies. I'm sorry to press on it, but it is critical for readers to understand why it is that neural information can improve overall model fit. Again, the enhancement of parameter recovery (like in Nunez 2025) makes sense, but the enhancement of the "model's fit to behavioural data" does not, without pointing to a deficiency in the search algorithm / fitting procedure.

The authors state in their replies that the onset of bound collapse is set at accumulation onset and imply that setting it instead at stimulus onset could "mathematically resolve the issue" but they don't do it because it is implausible. It is in fact not only plausible but clearly evidenced in empirical data - collapsing bounds are implemented neurally through urgency signals, and these can begin to dynamically build toward threshold well before, let alone at, stimulus onset. There is nothing bizarre about this - we can prepare movements without sensory input, and indeed even if choosing actions based on a sensory discrimination, motor preparation can launch well before the sensory evidence (e.g. Stanford, Salinas et al 2010) and this in effect collapses the bound on cumulative evidence for triggering action before any evidence actually arrives. So, Urgency/bound-collapse does not need to be triggered by a stimulus; it can start in anticipation of the stimulus. It seems critical, therefore, for the authors to clarify this point - does re-defining the onset of the collapse at stimulus onset remove the trade-off and render unnecessary the neurally-informed ndt estimation?

Related to this, it is still not clear how bias in the estimation of nondecision time would not be a problem. What if, for example, it is the end of the N2 rather than the peak of the N2 that marks accumulation onset, and/or there is an additional fixed motor time that adds to the N2-based marker to make the full nondecision time that applies in the underlying decision process. By definition (and I think this is essentially what the authors' new simulations verify), because of the trade-offs, this bias would simply be absorbed in shifted estimates of theta and lambda describing the bound collapse function. But wasn't the whole point of the exercise to more accurately estimate those parameters? The obvious implication is that the parameter-estimation accuracy of the ERP-informed model is determined by the accuracy with which the proposed ERP marker directly pinpoints the full nondecision time without bias, but this is not at all obvious in the paper as written. Importantly, in the example scenario I describe above where accumulation onsets when N2 ends, there may still be a perfect correlation of N2 peak latency with underlying ndt across trials - they could still be very strongly "linked" statistically, but we can't know what size offset might be involved.

Reviewer #3 (Public review):

The current paper addresses an important issue in evidence accumulation models: many modelers implement flat decision boundaries because the collapsing alternatives are hard to reliably estimate. Here, using simulations the authors demonstrate that parameter recovery can be drastically improved by providing the model with additional data (specifically, an EEG-informed estimate of non-decision time). Moreover, in two empirical datasets it is shown that those EEG-informed models provide a better fit to the data. The method seems sound and promising and might inform future work on the debate regarding flat vs collapsing choice boundaries. As an evidence-accumulation enthusiast, I am quite excited about this work, although for the more broader audience the immediate applicability of this approach seems limited because it does require EEG data (i.e. limiting widespread use of the method or e.g. answering questions about individual differences that require very large N).

Comments on revised version.

I thought the authors carefully addressed my concerns.

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:

Combining in vitro refolding, SEC-based assembly assays, peptide-library screening, MALDI-TOF, LC-MS/MS, structural analysis and immunopeptidomics, this manuscript investigates the peptide-binding principles of the promiscuous chicken MHC-I molecule BF2*21:01.

Strengths:

Although the peptide motif of BF2*21:01 is highly complex, this manuscript identified several principles, including a preference for 10-mer peptides, co-variation between P2 and Pc-2, effects of P3 and Pc-3, and a strong cellular preference for Leu at Pc. The results are important for avian MHC biology and poultry vaccine epitope prediction.

Reviewer #2 (Public review):

Summary:

The study presents an in-depth analysis of the peptide repertoire bound by a promiscuous chicken MHC molecule using mass spectrometry, x-ray crystallography and modelling. While the MHC can bind a very diverse set of peptides, the authors have found some new rules that govern peptide binding to this MHC that could help to build a predictive model to study the repertoire of pathogen-derived peptides.

Strengths:

The study uses a range of well performed experiment across multiple techniques and provides an in-depth analysis of the peptide repertoire, including peptide sequences, length, preferred residues, stability and MHC presentation.

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 reviewers' suggestions.]

Summary:

This paper presents a toolkit for the transformation of Blastocystis. The authors have screened a number of selectable agents, promoters and reporter genes and present their findings. This resource will be of immense use to those in Blastocystsis field, as well as those seeking to establish transformation tools in other species where such tools do not yet exist. Establishing new transformation tools is extremely challenging, and the authors have done an excellent job.

Strengths:

The authors have carried out a systematic screen of promoters, reporter genes and selectable agents. They have screened numerous for each, and all the data is presented. It is good to see when things did not work as well as when things did - so this data set is extremely useful indeed.

Comments on previous version.

The authors have revised their manuscript to clarify that molecular analyses have not yet occurred and have resolved the technical/publication issues with the figures. I look forward to seeing these tools used in future publications to answer important questions in Blastocystsis research.

Reviewer #3 (Public review):

Summary:

The primary objective of this study was to establish a practical and functional framework for propagation of stable transgenic cell lines of Blastocystis, a common animal gut microeukaryote. Although the work focused on Blastocystis ST7-B, a subtype with relatively low prevalence in humans, this choice is justified by its association with more frequent negative health effects. Beyond their relevance to the medical field, the methodological advances described here have the potential to also expand cell biology studies of this anaerobic organism, including its unusual mitochondria and redox metabolism.

Strengths:

Prior to this work, genetic tools for Blastocystis were very limited, relying on a single strong promoter-terminator combination. The authors successfully expanded the available promoter set across a range of expression strengths by testing two dozen variants in luciferase-based assays. Critically, they developed an integrated workflow from a modular transgenic construct design to an expanded inventory of molecular components (promoters, reporters), optimized DNA delivery, stepwise antibiotic resistance-mediated clonal selection and propagation, and to reporter validation. The evaluation of several anaerobiosis-compatible labeling strategies for live (and fixed) cell optical imaging will be particularly useful, with the SNAP-tag system appearing especially promising for Blastocystis.

Reviewer #1 (Public review):

This study by Vitar et al. probes the molecular identity and functional specialization of pH-sensing channels in cerebrospinal fluid-contacting neurons (CSFcNs). Combining patch-clamp electrophysiology, laser-based local acidification, immunohistochemistry, and confocal imaging, the authors propose that PKD2L1 channels localized to the apical protrusion (ApPr) function as the predominant dual-mode pH sensor in these cells.

The work establishes a compelling spatial-physiological link between channel localization and chemosensory behavior. The integration of optical and electrical approaches is technically strong, and the separation of phasic and sustained response modes offers a useful conceptual advance for understanding how CSF composition is monitored.

Comments on revised version:

I thank the authors for their extensive revisions and detailed responses to the reviewers' comments. The manuscript has been substantially improved, and most of the major concerns raised in the initial review have been adequately addressed. In particular, the additional analyses of PKD2L1 channel activity, the incorporation of physiologically relevant pH conditions, the clarification of ASIC involvement, and the expanded Discussion have significantly strengthened the study.

Major scientific concerns largely addressed:

Quantification of PKD2L1 channel activity<br /> The authors appropriately addressed my previous concerns regarding the use of Po as the sole measure of channel activity. The inclusion of additional parameters such as apparent Po, open time, nmax, holding current, and membrane charge provides a more robust assessment of PKD2L1 activity and substantially strengthens the conclusions.

Physiological relevance of pH modulation<br /> The inclusion of experiments at pH 6.5 and the additional analyses of holding current and resting membrane potential are valuable additions. These experiments considerably improve the physiological relevance of the study.

ASIC contribution<br /> The additional pharmacological experiments using ASIC blockers are helpful and support the conclusion that the photolysis-evoked response in the apical process is predominantly mediated by PKD2L1 channels.

Functional implications<br /> The expanded Discussion regarding Ca2+-dependent signaling, neurosecretion, and the potential physiological roles of CSFcNs considerably improves the manuscript.

Remaining concerns:<br /> Continued overstatement regarding "exclusive" localization and function:

Although the authors softened some statements in the revised manuscript, the term "exclusive" remains in several key locations, including the title.

For example:<br /> "PKD2L1 channels segregated to the apical compartment are the exclusive dual-mode pH sensor..."

The data clearly demonstrate strong enrichment of functional PKD2L1 channels in the apical process. However, the available evidence does not fully justify the term "exclusive," particularly because:

- PKD2L1 immunoreactivity is still detectable outside the apical process.<br /> - ASIC-mediated responses are present in CSFcNs.<br /> - The authors themselves use more appropriate terminology such as "predominantly located" in the Discussion.

Therefore, I recommend replacing "exclusive" with more conservative terminology such as:

- predominant<br /> - predominantly localized<br /> - enriched<br /> - functionally segregated

throughout the manuscript, including the title, Abstract, Introduction, Results, and Discussion.

Use of the term "tonic current"

The manuscript continues to use the term "PKD2L1 tonic current."

While the dibucaine-sensitive holding current is clearly present, the precise mechanism generating this current remains uncertain. Indeed, the authors themselves acknowledge in the Discussion that:

- an alternative conducting state may exist, or<br /> - unresolved brief channel openings may account for the current.

Therefore, the data support the existence of a sustained PKD2L1-associated current, but do not yet definitively establish a distinct tonic gating mode of the channel.

I therefore recommend replacing:

"tonic current"

with a more neutral expression such as:

- sustained current<br /> - PKD2L1-associated holding current<br /> - sustained PKD2L1-mediated current throughout the manuscript.

Continued use of "off-current" and "off-response":<br /> The revised manuscript has improved considerably in this regard. However, the terms "off-current" and "off-response" still remain in portions of the text and figure legends.

Because the manuscript itself demonstrates that the response reflects recovery from transient acidification rather than a separate OFF signaling mechanism, these terms remain potentially misleading.

I recommend replacing them with terminology such as:<br /> - photolysis-evoked PKD2L1 current<br /> - recovery current<br /> - proton-removal-induced current

throughout the manuscript, including figure legends.

Minor editorial corrections<br /> Figure 1Bd Please change: "po" to "Po" for consistency with standard channel physiology nomenclature.<br /> Figure 1Ca Please add units (mV) to the voltage labels shown on the left side of the traces.<br /> Figure 3E Please change: "Norm po" to "Norm Po".<br /> Figure 4Fb Please replace: "sec" with "s" to conform with SI unit conventions.

The authors have addressed the majority of my previous concerns and the manuscript has been substantially improved. The remaining issues are primarily related to terminology and overinterpretation rather than experimental deficiencies.

Reviewer #2 (Public review):

Summary:

Cerebrospinal fluid contacting neurons (CSF-cNs) are GABAergic cells surrounding the spinal cord central canal (CC). In mammals, their soma lies sub-ependymally, with a dendritic-like apical extension (AP) terminating as a bulb inside the CC.

How this anatomy-soma and AP in distinct extracellular environments-relates to their multimodal CSF-sensing function remains unclear.

The authors confirm in the GATA3:GFP mice where these cells are labeled that CSFcNs exhibit prominent spontaneous electrical activity mediated by PKD2L1 (TRPP2) channels, non-selective cation channels with ~200 pS conductance modulated by protons and mechanical forces.

They investigated PKD2L1 pH sensitivity and its effects on CSFcN excitability. They uncovered that PKD2L1 generates both phasic and tonic currents, bidirectionally modulated by pH with high sensitivity near physiological values.

Combining electrophysiology (intact and isolated AP recordings) with elegant laser-photolysis, they show functional PKD2L1 channels localize specifically to the apical extension (AP).

This spatial segregation, coupled with PKD2L1's biophysical properties (high conductance, pH sensitivity) and the AP's unique features (very high input resistance), renders CSFcN excitability highly sensitive to PKD2L1 modulation. Their findings reveal how the AP's properties are optimised for its sensory role.

Strengths:

This is a very convincing demonstration using elegant and challenging approaches (uncaging, outside out patch of the AP) together to form a complete understanding on how these sensory cells can detect so finely the changes of pH in the CSF.

Weaknesses:

Not weaknesses, there are only minor requests to complete the beautiful study.

(1) The apical extension's response to removal of acidification is nicely illustrated in Figure 4C,G. There's something puzzling there: while the response to Glutamate is immediate, the channel responses to H+ is extremely delayed by 100ms - 2s, and even sometimes came in bursts separated by few hundreds of ms. H+ diffuse even faster than glutamate. Why is that?

I don't quite understand how the response is so delayed & how to explain the recurring bursts of channel opening in the figure panel ?

- The authors should show in Fig 4C,G the traces for 1-2 s before uncaging occurs so we can appreciate whether such events occur as well in baseline and discuss this further in revisions.

- Could the authors use a fluorescent pH sensor to monitor pH in the extracellular space and in the cell ?

- Could the authors investigate whether in the apical extension, PKD2L1 channels are mainly at the outer membrane in the apical extension OR whether many channels are located in inner membranes ?

(2) Suppl Fig 4 is very cool and should be moved to main figure. The coupling of Soma and AP is very tight, yet there is a clear difference in targeting of channels that respond to cues in the CSF. In the context of an intact spinal cord, we can wonder how and when the contribution from ASIC in the some would be relevant to physiology. Can the authors think of experiments with an intact central canal to test the sensitivity and condition of recruitment of pH sensing in the soma (ASIC) versus the apical extension (PKD2L1)?

(3) The Reissner fiber is missing after slicing the spinal cord. From our observations in fish, the fiber being under tension triggers lots of activity in CSF-cNs (Bellegarda et al Elife 2023) that also relies on PKD2L1 (Bohm et al NC 2016; Sternberg et al NC 2019). Could the authors discuss the contribution of the Reissner fiber to the PKD2L1 mediated modulation of CSFcN excitability ? Could the authors conceive a way to slice along the anteroposterior axis (sagitally) the spinal cord to keep the Reissner fiber in the central canal when recording CSF-cN apical extension ?

Reviewer #1 (Public review):

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

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

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

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

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

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

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

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

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

Weaknesses:

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

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

Reviewer #1 (Public review):

Summary:

This interesting paper demonstrates that transgenic over-expression of sphingosine 1-phosphate receptor 1 (S1PR1) on neutrophils alters their phenotype, resulting in (1) accumulation of neutrophils in blood, spleen, lung, and liver; (2) a shift in homing receptor expression with reduced CXCR2 and elevated CXCR4; (3) altered transcriptional profile with an increase in "G5c" neutrophils and reduced "module scores" for apoptosis and inflammatory response; (4) reduced ROS production upon fLMP stimulation; and (5) altered responses to bacterial and viral infections of the lung. It raises many interesting questions about how S1P signaling regulates neutrophil biology, and hence will be the basis of future studies. These include: (1) What is the physiological role of S1PR1 signaling in neutrophils? Although there is no dramatic effect on numbers upon S1PR1 loss, is there an effect on any of the other parameters measured? (2) What is unique about the lung that S1PR1 over-expression is particularly impactful there? (3) What distinguishes the bacterial context in which S1PR1 over-expression is maladaptive from the viral context in which S1PR1 over-expression is protective? and (4) Can treatment with an S1PR1 agonist mimic S1PR1 over-expression? As a possibly related question, when in neutrophil development does S1PR1 signaling function to shift the phenotype?

Strengths:

(1) A comprehensive characterization of S1PR1-transgenic neutrophils.

(2) Opens many interesting areas of investigation.

Weaknesses:

Although some characterization of the neutrophil-specific Mrp8-Cre is done, most of the experiments use the more widely expressed LysM-Cre. The redistribution phenotype is much stronger with LysM-Cre than with Mrp8-Cre, so it is unclear what effects are attributable to a cell-intrinsic role of S1PR1, even in studies of neutrophils analyzed ex vivo.

Reviewer #2 (Public review):

The authors have utilised two main models to assess the function of S1PR1 in neutrophils in mice. The knockout of this receptor shows no conclusive effect on neutrophil numbers or functions; it was only the overexpression that resulted in significant alterations. Therefore, often the conclusions do not describe normal or disease physiology but could be useful in a bioengineering context.

Strengths:

From a bioengineering standpoint, this seems like an important study - showing enforced expression of S1PR1 in neutrophils has improved outcomes for influenza infection (Figures 6 and 7).

Weaknesses:

Although the strength is the influenza model, genetic modification of human neutrophils cannot be a strategy, and therefore, is there any way to increase this receptor for mouse, or more importantly, human neutrophils? This study only looks at mice with a non-physiological model of overexpression. It does not offer a real therapeutic option, which drastically hinders the importance of the study. I have other concerns with the data analysis and interpretation, which I detail on a figure-by-figure basis (and how it relates to conclusions) below:

Main specific issues:

(1) Figure 2A+B: This is unconvincing; in the surface staining there seem to be real cells positive for the receptor (high staining in the histogram), but none of the transgenic protein is getting there? This undermines the idea that the effects of the transgene are related to S1P signalling. In the 'Total S1PR1' this is both underwhelming and misleading, as an isotype control (or better S1PR1 knockout) is missing, which would give a better representation of actual expression (flow cytometry autofluorescence famously increases in the red laser channels with fix/perm). The Imagestream chosen images are showing best-case scenarios - and aren't representative. What does the isotype/ KO look like here? All in all, the conclusion on receptor internalization is not well supported, especially when theoretically the TG overexpression should overload S1P availability. This also highlights the lack of another control - does overexpression of another random/non-functional protein have the same effect? To play devil's advocate, perhaps overloading of the ubiquitin-proteasome system is responsible?

(2) Figures 2E-H: In the text, the authors should fix the statement 'Additionally, surface CXCR2 was downregulated and CXCR4 upregulated in LysM-S1pr1 TG neutrophils across bone marrow, spleen, and blood (Fig. 2, E and F)' to better reflect that there is no significant difference in the bone marrow regarding CXCR4. Of note, the total MFI from this data would also be informative, another noticeable absence being the gating strategies for much of the data. Also, alter the statement: 'CD62L expression was largely preserved across compartments, with only a modest reduction in bone marrow neutrophils (Fig. 2G)'. A 50% reduction in CD62L is not modest.

(3) Supplemental Figure 3. A common theme: the wrong statistics have been used here, which has led to a false conclusion. Megakaryocyte/erythrocyte progenitors (MEPs) were only elevated in 2/3 TG mice, and the numbers are so small that this is not significant by any measure of the word. This is certainly not statistically significant if the correct test of (log-normalized) two-way ANOVA is performed (with Sidak's post hoc test). Another acceptable test would be Kruskal-Wallis with Dunn's post-test just for MEPs.

(4) Starting at Figure 3, the authors refer to 'S1PR1hi neutrophil accumulation'. Crucially, the authors must here and throughout be explicitly clear in which cells they are referring to, as this can be misleading - particularly as there are real S1PR1-high cells identified in Figure 2A surface staining. It is my understanding that the authors here mean the transgenic artificially high mice - a very large distinction.

(5) Figure 3A: It is difficult to interpret the figure with the necessary details about the experiment. For instance, there is no mention that this is sterile inflammation or what caused it.

(6) Figure 3B and C: It should be made clear whether these splenic neutrophils are related to the time course of peritoneal inflammation in 3A. Why are there so many apoptotic neutrophils in the spleen? The low numbers here suggest a processing issue rather than real death in vivo (which usually is absent).

(7) Figure 3D: This can also be misleading - the wrong statistics are again used. This should be a log-transformed two-way ANOVA. Regardless of this, the data is not strong enough to be conclusive, a minor effect at best that could also just be related to the type of cell tracker used.

(8) Figure 5E: It is stated that 'LysM-S1pr1 TG mice exhibited a higher bacterial burden in the lungs than controls (Fig. 5E).' Again, misleading results, first the wrong statistical test was used (correct = log norm one-way ANOVA with Tukey's or Kruskal Wallis with Dunn's), secondly the only significance is between S1PR1(fsf) and the Mrp8-S1PR1, not with the LysM TG. 5F is also not strong, with only 2/7 values appearing outside the range of the control - P values can be misleading when poor statistics are used.

(9) Figure 6G: Some discussion should be given for why Neutrophils are lower in BALF in the IAV model - even though higher in the lung in the non-IAC mice in Figure 1. In general, rather than focusing on the non-physiological differences, the discussion could better reflect the inconsistencies and more fully address the difference between the TG and KO and what this means going forward.

Reviewer #3 (Public review):

Summary:

Using mice that overexpress S1PR1 in myeloid cells or specifically in neutrophils, the authors show that increased S1PR1 promotes neutrophil release from the bone marrow and accumulation in blood and peripheral tissues without causing baseline tissue injury. These cells acquire a CXCR4-high, CXCR2-low, CD101-low phenotype, survive longer, and display enhanced mitochondrial metabolism and mTOR signaling, together with reduced apoptotic, inflammatory, and ROS-related programs. Although phagocytosis is preserved, ROS production is markedly reduced. This is associated with impaired bacterial clearance in the lung but improved outcomes during influenza infection, including better survival, less weight loss, improved oxygenation, lower viral burden, and reduced lung inflammation. In contrast, myeloid S1PR1 deletion produces little detectable phenotype. The authors therefore propose that S1PR1 separates neutrophil persistence from inflammatory function, improving tolerance to viral lung injury at the expense of antibacterial defense.

Strengths:

This is a technically solid paper using novel mouse models to overexpress S1PR1 specifically in myeloid cells as well as neutrophils. The data are striking with respect to neutrophil expansion. The diverse roles of neutrophils and their population heterogeneity are an important scientific area that has led to many recent breakthroughs - PMC11785525; PMC12823425, thus this is a timely study.

Weaknesses:

The study mainly demonstrates what S1PR1 overexpression is sufficient to do, rather than establishing the physiological role of endogenous S1PR1. The conclusions should therefore be narrowed unless the authors provide stronger loss-of-function and physiological validation. As written, the abstract ("S1PR1 promotes mitochondrial fitness, enhances survival, and reduces inflammatory output") and the conclusion ("S1PR1 serves as a key regulatory axis") are sufficiency claims but should not be promoted as necessity claims. The honest sentence is: "Thus, a better conclusion would be that enforced S1PR1 expression is sufficient to reprogram neutrophils".

The authors do not confirm efficient S1pr1 deletion in neutrophils. Furthermore, the knockout is examined only under steady-state conditions and limited in vitro stimulation, but not in the bacterial or influenza models where the transgenic phenotype is observed. Without these experiments, the study cannot establish whether endogenous S1PR1 is necessary for the reported functions.

The degree of S1PR1 overexpression is not quantified relative to normal physiological levels. The authors should determine whether naturally occurring S1PR1-high neutrophils display the same survival, metabolic, trafficking, and inflammatory features observed in the transgenic cells.

Analysis of relevant human or mouse datasets, including sepsis, ARDS, viral infection, cancer, or aging, would also help establish whether this neutrophil state exists physiologically.

Surface S1PR1 expression appears similar between control and transgenic neutrophils, whereas total intracellular receptor is increased. This suggests that the phenotype may depend on receptor internalization or endosomal signaling. An internalization-deficient S1PR1 model, such as S1P1-S5A, would help distinguish sustained surface signaling from internalization-dependent signaling. The authors should also determine whether the phenotype requires ligand binding, Gi signaling, and mTOR activity.

The reduction in CXCR2 and decreased neutrophil accumulation in the airways could alone explain the protection from influenza-induced lung injury. The current experiments do not clearly distinguish neutrophil reprogramming from defective migration into the alveolar space.

Although this may be outside the scope of the current study, the authors should directly test whether CXCR2 inhibition reproduces the phenotype.

The reported reduction in viral load should also be confirmed using plaque assay or TCID50, and the possible contribution of NET formation should be examined.

Reviewer #1 (Public review):

Summary:

This article describes a new software package, HSSM, for simulating and fitting sequential sampling models. The package consists of three modules - one for simulating the models, one to train neural networks on mappings from behavior to parameter values, and one for combining these tools to fit particular models to users' data.

Strengths:

This is a very detailed description of a new package that is building on an already highly successful package. It promises to become a go-to software package for cognitive modelers, experimentalists, and practitioners.

Weaknesses:

I have only a few critiques of the article, and some are a matter of taste:

(1) I think it would be helpful for the authors to take the reader through one complete example at the end of the article, including loading in a dataset, fitting it with a regression model, checking model convergence, reading out parameter values, and doing posterior predictive checks (etc). It would be helpful to see it all in one place to get a sense of how much code is required to go through the whole process. One or two actual examples would help readers who are not already familiar with HDDM.

(2) The article assumes a certain level of computing and modeling expertise, which somewhat limits its reach. There are many abbreviations and references to other software tools that a reader might not be familiar with. Such readers might feel like HSSM is beyond their reach. Below is a non-exhaustive list of such undefined or unexplained terms:<br /> DDM, API, LBA, fMRI, EEG, JAX, PyTorch, ONNX, MCMC, VI, MAP, PyMC, PyTensor, NUTS, ArviZ, WAIC, LOO, KDE, CLI, YAML, GUI, LBA, RDM, QP.

(3) I found some of the figures/listings to be unpolished, unhelpful, and/or unnecessary. For instance, Figure 3 and Listing 3 seem to just be zoomed-in pieces of Figure 2. In Figure 4, what is the meaning of the little globe traveling between the within-trial and across-trial rows? Why is Figure 5 a figure and not a listing? Does HSSM not produce these plots directly? I have the same question for Figure 7. Figures 8 and 9 seem unnecessary to me, but perhaps they serve a function that I'm missing. Perhaps they could be turned into supplements for Figure 2.

Reviewer #2 (Public review):

Summary:

This manuscript introduces HSSM, a Python-based toolbox for fitting cognitive models, with a specific focus on sequential sampling models. The toolbox brings together several components: a model construction interface, surrogate likelihoods, sampling tools, an inference backend, formula-based regressions, and tools for validation and visualization.

One of the key advantages is that HSSM relies on well-established open-source packages. This ensures both a robust foundation and also opens a potential for future (community-driven) development. While HSSM is not the first publicly available toolbox for fitting sequential sampling models, it introduces several novel features that will be very valuable to researchers in the field.

Strengths:

The biggest strength of HSSM is its flexibility and ease of use for hierarchical modeling. Many existing toolboxes work as closed systems that are hard to modify. In contrast, HSSM's modular design allows it to be used either as a stand-alone tool or to pick out specific components to integrate into existing pipelines. In addition, the toolbox combines simulation-based inference, surrogate likelihoods, and formula-based regression. This opens up a lot of new modeling possibilities and makes it easy to incorporate trial-by-trial neural or physiological covariates alongside standard RT and choice data.

Weaknesses:

The paper provides a high-level overview of the toolbox, rather than a didactic walk-through that shows how to use it in practice. Additionally, despite being framed as a broad toolbox for "neurocognitive modeling", HSSM currently focuses on sequential sampling models. While these models are widely used, they represent only a small slice of neurocognitive modeling as a whole. Additionally, the toolbox is currently in beta phase, and lots of planned extensions are not implemented yet. Finally, there is currently no information on general performance benchmarks.

Reviewer #1 (Public review):

Summary:

The manuscript further explores the single-cell atlas of Clytia hemisphaerica by incorporating the planula larva. It compares the cell clusters with the previously established atlas of the medusa. It identifies similarities and differences between the two life stages.

Strengths:

The manuscript provides an important set of single-cell data that have not been assessed previously: the Clytia planula. The data is further supplemented with high-quality EM-based histology and an extensive in situ hybridisation of selected genes.

Weaknesses:

The detailed analysis does not go deep into the comparison between stages, nor does it provide an analysis of genes within the clusters; it could be described as remaining overall rather superficial.

Reviewer #2 (Public review):

Summary:

The generation of alternate stages in the life cycle of a single species requires vast remodeling of the cellular complement of the individual during metamorphosis from one stage to another. In this paper, the authors provide a detailed description of single-cell RNA-seq data derived from the planula stage of the hydrozoan model Clytia hemispherica and compare this to an expanded dataset from the medusa stage to assess changes in transcriptomic identity of cell types between these two phases of the life cycle. The paper further includes valuable TEM data illustrating fine anatomy of cell types present at both stages investigated, and documentation of the retention of epithelial polarity from the planula through to the polyp stage, using a reporter line.

Strengths:

The study provides a solid and convincing transcriptomic characterization of planula cell types (including in situ validations and a planula-to-polyp mapping of epithelial polarity), and introduces a potentially valuable method for evaluating cluster similarity.

Weaknesses:

The work suffers from insufficient documentation of methodological approaches and missing code, lack of clarity regarding clustering resolution and nomenclature (thereby hindering cross-referencing with prior papers), and unclear plans for public, fully annotated data release.

Full Review:

The single-cell transcriptomic data analyzed include both previously published and newly generated data: two additional medusa libraries and two additional planula libraries were generated and integrated with the data from https://doi.org/10.1126/sciadv.abh1683, and https://doi.org/10.1126/sciadv.adv1159. The original release of the planula dataset in their 2025 Science Advances paper did not include analyses of all cell types. Here the authors provide this analysis for the planula stage. However, as both the number of clusters and the nomenclature of the clusters changed, this leads to some confusion and inability to cross-reference the two papers. There is no explanation given for the re-processing of the planula dataset in the current paper, and the fact that only some of the data is new is buried in the supplement, which is not referenced in the main document, while the text within the main article suggests that the entire dataset is new. The fact that the dataset in the current analyses contains fewer cells than presented in their Science Advances paper further adds to this confusion. The current paper would benefit from greater transparency in the origin of the data analyzed.

The authors do try to apply the same nomenclature for the updated medusa dataset that is present in their 2021 Science paper. For example, the previously identified 'bioluminescent cells' are identified as 'gas-m8'. A look-up table that has all of the cluster id's cross-referenced would be useful (i.e. new: 8 = gas-m8 = previous: 28 = BC = "Tentacle GFP cells"). The inability to easily cross-compare with the published data is a major weakness of the current work and would benefit greatly from consistency between the three papers. Indeed, the clustering resolution is quite different across all three papers, and the current work does not adequately address how the clustering resolution was selected here. As an updated atlas, one would expect the entire transcriptomic diversity to be included here, so that the previous work can be transferred to the updated genomic mapping resource used in the current work. Nonetheless, presenting a unified nomenclature for moving forward would benefit the community as a whole and would increase the impact of the current work substantially.

The paper also includes new TEM data of the planula cell types. The authors attempt to correlate transcriptomic profiles with these anatomical data through in situ hybridizations that provide spatial distribution of the profiles. While the TEM data are valuable to catalog the presence of cells with different morphologies within the planula, the association with the transcriptomic profiles is somewhat speculative. These valuable anatomical data should be provided at a high enough resolution to zoom in and see the details, and further description could be provided. For example, the paper states that vacuolated cells are characteristic of the basal gastrodermal cells adjacent to the mesoglea; please identify the vacuoles in Figure 4f/h for the reader.

A novel method for reconstructing cluster similarity relationships is applied to grouping clusters into cell categories within the same life cycle stage, and also for matching cell types between stages. This is a valuable contribution to the field that is worthy of further evaluation. This is, however, difficult, as the methods for which DESeq2 was applied ("see code for details") are not present in the provided code, nor is it adequately described how the "binary matrix of marker gene presence/absence" was constructed. Similarly, there are additional details of other parts of the data analysis that are missing from the provided code, and the provided supplementary material is not referenced in the main document. More rigorous documentation of the methods is warranted.

The description of the transcriptomic profiles present in the planula is solid, and the attempt to associate these profiles with anatomic locations and putative morphology provides a foundation onto which further studies can be developed. Mapping of the planula ectoderm through to the polyp stage is also an important step forward in characterizing the life cycle, and the evidence for the retention of the oral/aboral ectodermal axis is convincing. The paper falls short in describing the updated medusa dataset and could benefit from a minor restructuring of the paper. Introducing the new medusa data only after the planula dataset is fully described would mediate the shallower treatment of the updated medusa dataset, where only 22 of the original 36 transcriptomic states are recovered. In this way, the focus will shift onto the cross-life cycle stage comparisons, and it could be argued that the lower resolution of the medusa dataset is justified in order to simplify the comparisons.

It will be essential that the datasets that are presented in this work be made available for public exploration in a fully annotated format. It is currently unclear how the authors intend to do this; however, there are many repositories available for this. The UCSC Cell Browser hosted at cells.ucsc.edu is one very good option if the authors do not wish to develop an interactive tool themselves. It is imperative that the gene annotations which correspond to the dataset, and the cluster annotations that are presented in this paper, are available and easily connected to the released dataset.

Reviewer #1 (Public review):

Summary:

Using cryofixation and serial block-face electron microscopy (SBEM), P. Vijayakumar and K. Cauwenberghs characterize extracellular vesicles (EVs) and non-vesicular extracellular particles (NVEPs) within native Drosophila olfactory sensilla. The study provides a unique and valuable dataset comprising approximately 7,800 extracellular particles, systematically describing their morphology, size, density, and distribution. The ultrastructural analysis across different sensillum classes offers insights into the potential biogenesis and functions of these extracellular particles.

Strengths:

Cryofixation preserves EVs and NVEPs within native tissue conditions. The detailed quantification of a very large dataset provides a unique source of information on extracellular particle number, categories, and distribution. The expertise of the group in the method and the tissue explored, as well as their detailed quantification, provide confidence in the dataset and observations.

Weaknesses:

Major comments

(1) As the authors state, the rare observation of EV budding or MVB release events suggests that these are transient processes, whereas EVs and NVEPs are retained for relatively long periods within the sensillum lumen. The current analyses may overinterpret steady-state vesicle abundance as differences in vesicle production.

(2) Given the above conclusion, differences between sensillum classes may be somewhat overstated.<br /> a) The absolute number of EVs and NVEPs per sensillum is highly variable, even within the same sensillum class (Figure 3D). For example, a substantial proportion of coeloconic sensilla have an empty lumen (Figure 3C). Consequently, expressing the data as ratios or proportions (Figures 3B, 4C, and 4E) may exaggerate differences between sensillum classes and should therefore be interpreted with caution.<br /> b) The rate of EV/NVEP production is unknown. For a similar rate of production across sensillum classes, Figure 3E suggests that the differences in lumen morphology and size may largely explain variation in EV density and distribution.

That said, I agree that ab1 sensilla display a striking enrichment of large cargo-filled EVs compared with the other sensillum classes, while coeloconic sensilla display enrichment in small dense filled EVs (Figure 4C). Together, large and cargo-filled EV observation provides strong support for differences in EV biogenesis between ab1 sensilla and the other sensillum classes. In that context, I also think the EV size distribution shown in Figure 4 - Figure Supplement 1 should be moved into the main figure, as it demonstrates that the majority of EVs in the ab1 lumen are relatively large and are therefore likely to represent microvesicles. Could you clarify why ab1 sensilla are only included in Figure 4 and not analysed in Figure 3?

(3) Approximately 10% of ORNs appear to be degenerating in 6-8-day-old flies, which seems unexpectedly high. This contrasts with the relatively infrequent occurrence of auxiliary cell apoptosis or complete sensillum degeneration. In these "degenerating ORNs", the authors state that the hallmarks of ORN apoptosis are restricted to the dendrites. As hallmarks, they state dendrite truncation, fragmentation and blebbing. Rather than apoptosis, I wonder whether these observations might instead represent ciliary truncation and ectosome shedding, followed by degradation of the shed ciliary membrane into EVs. Ciliary truncation and ectosome shedding, followed by ciliary regrowth, are dynamic processes that have been described across multiple species. This interpretation could explain large EVs that remain in the lumen long after the cilium has regenerated. It would reconcile this article with the general agreement that cilia are a prime site for the budding of EVs across species. Additional evidence supporting apoptosis of the ORNs would help distinguish between these possibilities. Otherwise, I believe the author should reconsider their interpretation.

Reviewer #2 (Public review):

Summary:

This paper presents a large structural survey of extracellular vesicles (EVs) and non-vesicular extracellular particles (NVEPs) in the olfactory sensilla of Drosophila melanogaster. Using high-pressure freezing and serial block-face SEM, the authors avoid many of the artifacts associated with conventional fixation and analyze more than 7,800 particles across 352 sensilla. The manuscript maps the distribution of these particles, describes their morphological heterogeneity, and examines their likely origins across different sensillum classes in both normal and degenerating tissue.

Strengths:

The strongest aspect of the paper is the imaging. Preservation is painstakingly controlled. The cryofixation appears to preserve the sensillum lymph in a more convincing native state than standard preparation methods, giving this work gravitas. Further, the authors characterized thousands of particles, further making this data strong.

The figures are strong. They are clear, easy to read, and generally well designed; I think people will use this paper as a model for how to present complex data in a concise and straightforward manner. The manuscript is careful in how it presents the dataset and does not overinterpret the descriptive observations. As an ultrastructural resource, this paper will be useful to the field. The identification of auxiliary support cells as major secretory sites, together with the striking accumulation of EVs in degenerating tissue, will provide a useful starting point for future work.

Weaknesses:

The main point that could use more clarification is the vesicle categorization. In particular, the distinction between "dense," "cargo-filled," and "double EVs" is not always easy to follow from a biological perspective. Some additional discussion of how the authors think these categories relate to one another, and whether they are intended as purely morphological groupings or as distinct biological classes, would strengthen the manuscript.

Reviewer #3 (Public review):

Using cryofixation-based serial block face electron microscopy of several subregions of the Drosophila antenna, the authors segment and assemble a high-resolution atlas of the anatomical structure, density, and spatial distribution of extracellular vesicles (EVs) and non-vesicular extracellular particles (NVEPs) in different Drosophila olfactory sensilla types. This systematic and thorough description is an important prerequisite to understanding the function of extracellular particles in intercellular signaling in the nervous system. Additionally, they describe examples of putative biogenesis events (budding/fusion), as well as neuronal and axonal cell degeneration events and measure the changes in particle accumulation in these altered microenvironments.

Overall, this is a significant and comprehensive analysis and represents an invaluable resource to this burgeoning field. The authors assemble an important dataset and their claims match the level of evidence provided.

Strengths:

(1) The authors use segmentations from four different patches of the antenna to provide a systematic ultrastructural survey of extracellular particles in native insect sensilla. The dataset captures the diversity of sensilla types and reconstructs ~7800 particles.

(2) We commend the authors for making the EM volumes available in the public Cell Image Library with accession numbers. It would be helpful to the community to also make the segmentations for this great resource easily accessible.

(3) The sample preparation technique appears to minimize typical artifacts associated with chemical fixation, as evidenced by the high reported sphericity of EVs.

Specific points:

(1) In Figure 3C, the authors should include a continuous measure of particle distribution in the sensilla. Currently, the authors define three categories of particle localization. In the five examples shown in Figure 3A, the spatial distribution of these particles appears quite distinct across classes. For example, EVs/NVEPs in large and small basoconic sensilla are largely restricted to the area proximal to the base, with a limited number located more distally. In contrast, intermediate sensilla show a marked concentration of particles more distally.

(2) The conclusion of different EV ratios across sensillum classes stems from a Kruskal-Wallis of p = 0.0476, with none surviving pairwise comparisons. This is not a strongly supported conclusion and is probably better characterized as a trend.

(3) The statement "selective enrichment of large, cargo-filled vesicles within the ab1 lumen suggests specialized EV-mediated communication adapted to the coordination demands of this neuronal population" seems speculative for a Results section without supporting functional evidence. It would seem better suited for the Discussion.

(4) Figure 4: Criteria for defining the classes of EVs.<br /> a) The authors should explain the rationale for classifying EVs using relative density rather than absolute density? We would expect EVs with similar contents to have similar electron density (similar darkness in the images). Would classifying them relative to the background, which itself might vary across sensilla or regions, create a possible confound, especially when comparing across sensillum classes?<br /> b) The two example images (in Figure 4A) of the cargo-filled EVs appear to have different densities themselves. Do the cargo-filled ones also display systematic differences in density and, if so, why is this another class instead of being a subcategory within the dense and lucent classes (i.e. dense with/without cargo, lucent with/without cargo)? The dense and lucent classes are defined by their density, whereas this is a more structural property.<br /> c) Regarding "Double" and "Ball-and-Socket" EVs, does the density vary between the two particles involved (e.g., does the inner structure consistently differ in density from the outer)?

(5) What was the rationale for the 200μm and 1000μm size cutoffs? A continuous distribution of maximum particle sizes would provide a clearer understanding of the data.

Reviewer #1 (Public review):

Summary

The authors present a valuable study of the gasdermins and caspases encoded by Callorhinchus milii, a shark that is one of the most basal members of the cartilaginous fishes. C. milii encodes GSDME and PJVK as well as another gene here called GSDMA/B (which has also been termed GSDMEc in other work). This latter gene is the ancestral gene for bird/reptile/amphibians GSDMA that, in turn, is the ancestral gene to mammal GSDMA, B, C, and D. Prior work had shown that more ancient animals have only GSDME and PJVK, and in these animals caspase-3 and caspase-1 can both independently cleave GSDME. Prior work had also shown that in birds/reptiles/amphibians, GSDMA is cleaved by caspase-1, and GSDME is only cleaved by caspase-3. Here, the authors demonstrate that the more ancient C. milii gene is similar to the bird/reptile/amphibian GSDMA in that it is cleaved by caspase-1. They further demonstrate that C. milii does not encode inflammasomes that would activate CmiCASP1, and instead this caspase is an LPS sensor through its CARD domain analogous to mammal caspase-4/5/11. The data supporting these conclusions are convincing, and could be strengthened by primary cell studies from C. milii in future studies. They further provide evidence that this gasdermin can kill bacteria directly, but the data supporting this conclusion are incomplete.

Strengths:

The data demonstrating that CmiCASP1 is an LPS sensor via its CARD domain is thorough and convincing.

The data demonstrating that CmiCASP1 cleaves and activates GSDMA/B and that this causes pyroptosis is also thorough and convincing.

Weaknesses:

I think that the gene/protein referred to in this paper as GSDMA/B was in prior publications called GSDMEc (doi 10.3389/fcell.2022.952015). Is this correct? If not, the relationship or lack thereof to GSDMEc needs to be described. If the authors wish to rename the gene, this needs to be justified and discussed clearly. Also, a gene name with a slash is not typical and was initially confusing to me as it made me think the authors were referring to two different genes.

The authors do not have data from primary cells from C. milii to demonstrate that the LPS sensing by CmiCASP1 and the pyroptosis induction by GSDMA/B is relevant in the native cell types. This is a common limitation in publications that seek to study diverse animals where tools may not be available. This issue can be studied in future publications.

The ability of gasdermins to kill bacteria is controversial.

This bactericidal effect was first shown by the cited article Liu et al. 2016 from Judy Lieberman's lab. I reviewed that manuscript at Nature, and I implored the authors to remove that data from the paper because the experimental design had a high risk of not being physiologically relevant. Indeed, my lab had previously published that bacteria survive the process of pyroptosis and they must be killed by secondary efferocytic phagocytes attracted to the pyroptotic corpse (doi 10.1084/jem.20151613). I have continued to consider whether gasdermins could kill bacteria over the decade since that 2016 paper, and wrote a detailed argument describing how this is unlikely to be physiologically relevant in a recent review article (see Box 3 in doi 10.1038/s41564-026-02272-z).

In the author's current manuscript, the experiments performed show a very mild effect in the linear range of a reduction of perhaps 20% of the control bacteria in Figure 5A. This is a minimal effect compared to antimicrobial peptides, which will reduce colony-forming units by 99.9%. Take a look at the magnitude of effect in Figure 1 of an example paper looking at polymyxin or colistin killing of Acinetobacter (doi: 10.1128/AAC.00756-12), where CFUs are reduced by about 3 logs (1000-fold) in 30 minutes. The magnitude of effect in Figure 5A is not even 2-fold. Further, it would be very challenging to determine whether the concentration of gasdermin protein used in the assay is equivalent to the concentration that exists in cells. The methods section needs to be clearer to explain how many effective cell lysates of 293T cells were exposed to how many bacteria, because these concentrated lysates are of unspecified concentration.

Regarding cardiolipin binding, this is a lipid that has a small head group attached to 4 lipid chains, resulting in a cone-like shape with the polar groups at the cone tip and the lipids forming the wide cone base. As such, it creates a larger lipid area than polar area, thus naturally creating a curved membrane shape such that cardiolipin is in the leaflet of the interior of a curvature. Thus, in the mitochondria, it exists in the inner membrane in the mitochondria and allows for the bends that form the cristae, where it faces the surface that is concave (nicely diagrammed in Figure 1 of doi 10.3390/biom16010071). Similarly, cardiolipin enriches in the inner leaflets of membranes at the poles of rod-shaped bacteria to allow for the curvature of the membrane at the poles. Therefore, cardiolipin is not exposed in the outer leaflet of the outer membrane of Gram-negative bacteria; instead, the primary lipid in the outer leaflet is LPS.

A competing mechanism that could explain the results is that the opening of gasdermin pores in eukaryotic cell plasma membranes occurs concomitant with the generation of ROS from mitochondria. This could occur by gasdermins inserting into mitochondria, as supported by DOI: 10.1038/s41419-025-07760-4. The resulting ROS production due to mitochondrial dysfunction could cause the bactericidal toxicity seen in the cell extracts.

Reviewer #2 (Public review):

The authors investigate the mechanism by which a gasdermin pore-forming effector of the cartilaginous fish Callorhinchus milii, GSDMA/B (CmiGSDMA/B), is activated. This potentially provides information on the ancestral function of gasdermins, a class of proteins broadly important in human health and disease. By reconstituting components of this system in vitro using transfection models, they show that GSDMA/B is activated by cleavage by the caspase-1 homolog CmiCASP1, which directly senses lipopolysaccharide. This mechanism is broadly similar to the non-canonical pathway in mammals, wherein caspase-4/5/11 cleaves GSDMD upon cytosolic LPS sensing. The conclusions of these interactions are mostly well supported by data, but some aspects need clarification, and based on the experimental approaches, some of the broader interpretations have limitations that should be considered and further discussed.

A more detailed analysis and discussion on the differences between caspases with regard to their LPS-binding capacity would be valuable for comparison. The analysis of Figure 4A and 4B effectively shows that there are similarities between CmiCASP1 and some of the studied mammalian caspases. However, part of this analysis is to make the point that some caspases do not bind LPS, and it would benefit from the inclusion of additional relevant LPS-insensitive caspases to show the connection between the chondrichthyan caspase residues highlighted and LPS-binding dependence. Modeling the LPS binding site (such as in Figure 1F) would further help clarify whether these are appropriately positioned for coordination, or for non-conserved residues, if there are alternate binding modes thought to have biological relevance.

The authors note that two different cleavage products are formed, with variable function, which is of interest. The results of Figure 2b suggest that the 241A mutation (blocking the 30 kDa product) increases processing to the larger 35 kDa product, while the 288A mutation decreases processing of the 30 kDa product (also blocking the 35 kDa form). Paired with the lysis data (Figures 2C-2E), its not clear that the 35 kDa product is anything but inactive, but this is quite different from the observations in the experiments with each form (Figure 3N-3Q). A more detailed kinetic and stoichiometric analysis between full-length, N241, and N288 would be important for clarifying the potentially interesting observation of N288 inhibition of N241.

The mechanism of bacteriocidal activity proposed in the final model and by the experiments of Figure 5 would benefit from further development to support the claim. The experiments do not adequately address whether, during pyroptosis, there is release of N241-like fragments that can kill bacteria. Figure 3G would indicate that it stays in the cell, either in the membrane or mitochondria, and it's not clear there would be circumstances where it could be extracted from it to then target bacteria. Figure 5B might require additional explanation and analysis, but the appearance of similar colonies between conditions would appear to support that there is not measurable antibacterial activity. More rigorous support would come from differences in bacterial killing by knockout Callorhinchus cells, but a minimal step to demonstrating the relevance would be MIC assays, and connecting the effective concentration with one that could naturally occur in Callorhinchus.

Broadly, the methods of reconstitution of components of this system demonstrate the sufficiency of LPS for activating Casp1, and Casp1 for activating GSMDA/B. However, in more established models, it is clear that there are inhibitors, feedback mechanisms, alternative pathways, and regulation that could render these interactions irrelevant in Callorhinchus. For example, it's not clear where Casp1 and GSMDA/B are ever expressed in the same cell, at quantities sufficient for this mechanism, or that Casp1 doesn't induce more rapid death by acting on something other than GSDMA/B, or that Casp1 is irrelevant because GSDMA/B can be activated more readily by another mechanism. Therefore, while the insights into the evolution of the individual factors of GSDMA/B and Casp1 are interesting and of potential value to the field, reconstituting choice components by transfection of human HeLa and HEK293 cells introduces limitations to how far these experiments can be interpreted as a system. The abstract, for example, states this is a "pyroptosis pathway in cartilaginous fish". However, for all the interest of these data in the evolution of these proteins, the evidence falls short of this. It establishes a biological potential, but it's not clear this is an active pathway in fish.

Reviewer #3 (Public review):

In this manuscript, the authors focused on Callorhinchus milii GSDMA/B (CmiGSDMA/B) and its upstream inflammatory caspase, CmiCASP1, and revealed that LPS directly engages the CARD domain of CmiCASP1, triggering its activation, which subsequently promotes the proteolytic cleavage of CmiGSDMA/B, yielding two N-terminal fragments with opposite functions. Moreover, consistent with GSDMD, the functional N241 of CmiGSDMA/B can mediate pyroptosis and exhibit bactericidal activity against Gram-negative bacteria in vitro. Based on these observations, the authors clarified that they uncovered an ancestral LPS-sensing CASP1-GSDMA/B axis in cartilaginous fish; however, several issues should be addressed.

(1) The evidence for direct and functional LPS sensing by CmiCASP1 remains insufficient. Although the authors propose that LPS directly binds the CARD domain of CmiCASP1 to trigger a non-canonical inflammasome-like pathway, the current support mainly comes from pull-down, competition, and in vitro cleavage/activity assays. These results are suggestive but do not yet establish a direct, specific, and physiologically relevant interaction. Additional quantitative binding and specificity analyses are needed to exclude indirect association, aggregation, or other assay artifacts. Therefore, the claim that CmiCASP1 functions as a bona fide direct LPS sensor appears overstated at this stage.

(2) The proposed antagonistic role of N288 is not yet convincingly supported. While the "dual-fragment antagonistic regulation" model is interesting, it currently relies mainly on overexpression/co-expression, co-IP, and localization analyses, which do not clearly distinguish a physiological inhibitory mechanism from a non-specific dosage or sequestration effect. Stronger support would require evidence for the relative generation and timing of N241 and N288, as well as quantitative data showing that N288 interferes with N241 membrane targeting, oligomerization, or pore formation. Testing the effect of selectively blocking D288 cleavage in the full-length protein would also strengthen this conclusion. At present, the antagonistic model remains premature.

(3) The physiological and evolutionary claims are stronger than the available evidence. Although the study shows that CmiCASP1 can cleave CmiGSDMA/B and that this module can be reconstituted in heterologous mammalian systems, these data do not demonstrate that such a pathway operates in elephant shark cells or tissues under physiological conditions. A similar concern applies to the antibacterial assays, which use HEK293T lysates rather than purified N241, making it difficult to exclude contributions from host-derived factors. The authors should either provide more direct evidence in a relevant chondrichthyan context or substantially tone down the evolutionary and physiological interpretations.

(4) The inhibitor data do not convincingly demonstrate suppression of CmiCASP1 activation. Although the authors state that Z-VAD-FMK blocks CmiGSDMA/B cleavage and pyroptotic phenotypes, Figure 1L and Figure 2H do not clearly show that CmiCASP1 activation or processing itself is inhibited. If CmiCASP1 remains processed in the presence of the inhibitor, it becomes unclear whether Z-VAD-FMK blocks CmiCASP1 activation, catalytic activity, or only downstream substrate cleavage. This point should be clarified with more direct biochemical evidence.

(5) The dosage control for GSDM-derived proteins in the antibacterial assays is unclear. In Figure 5, antibacterial activity is tested using HEK293T lysates or concentrated supernatants containing full-length CmiGSDMA/B, N241, or N288, but it is not clear how protein amounts were normalized across conditions. Differences in expression, stability, or recovery could substantially affect the apparent antibacterial activity. The authors should clarify how input was controlled and ideally provide quantitative normalization or matched-concentration assays to support the comparison.

Reviewer #1 (Public review):

Summary:

In this well-written and well-presented manuscript, Arafat and colleagues describe the proper use and advantages of multi-task batteries to understand the organization of the human brain. The authors present both simulation and empirical results suggesting a substantial advantage in using many short tasks vs a single localizer in identifying specific task-engaged regions. The natural question arises as to which tasks should be used within the battery, and how they should be organized. The authors address this question by demonstrating a data-driven strategy for task selection that outperforms random selection, and they further demonstrate the advantages of highly interspersed tasks over a more typical one-task-per-run strategy.

Strengths:

In general, I find this work highly compelling. The topic itself should be of high interest to the majority of researchers conducting human functional neuroimaging studies. The manuscript itself is comprehensive and sound. The analyses and data are truly excellent, with only a few, relatively minor issues that can be improved. The authors do an exceptional job of laying out the motivation and logic for almost every analysis and conclusion in the manuscript.

I want to point specifically to the potential impact of this work. While the claims made here are very appropriately constrained to the conclusions that can be drawn from the actual analyses, their impact is potentially far-reaching. By the end of this manuscript, we are left with a set of ideas that in effect overturns 2-3 decades of received knowledge about how functional neuroimaging tasks should be designed to optimally understand the organization of the human brain.

Thanks to this paper, I personally will be rethinking how I design all of my fMRI studies in the future after reading this work. The authors are to be commended for this excellent contribution to the literature.

Weaknesses:

I struggled to understand the motivation and logic of the "connectivity modeling" section of the analyses.

Reviewer #2 (Public review):

Summary:

This paper presents theoretical and empirical insights into the use of multi-task batteries for precision functional brain mapping and offers practical guidelines for optimal task design. Specifically, the authors evaluate differences between single-contrast and multi-task localizers, explore data-driven strategies for battery selection, such as minimizing collinearity, and compare grouped and interspersed stimulus-presentation designs. Through a combination of simulations and analyses of empirical fMRI data, the study provides a systematic set of recommendations for improving the reliability and specificity of individualized functional mapping.

Strengths:

Traditional functional mapping has long relied on single-contrast localizers or resting-state fMRI. However, there is growing recognition that diverse batteries of general tasks can yield more detailed functional maps with higher signal-to-noise ratios (SNRs). This manuscript systematically evaluates these advantages using both simulations and empirical data. The contribution is timely and provides the community with not only a theoretical justification for multi-task designs but also practical tools, in the form of the MultiTaskBattery toolbox, for implementing them.

Weaknesses:

Although the results are robust, they are largely consistent with existing expectations in the field, and the conceptual novelty or "surprise" factor is therefore somewhat limited. Nevertheless, synthesizing these findings into a coherent set of design recommendations provides significant value to researchers.

Additionally, there appears to be a slight mismatch between the content of the manuscript and its designated article type. Although the manuscript was submitted as a "Tools and Resources" article, its extensive empirical analyses and theoretical evaluation make it read more like a "Research Article." I defer this categorization to the Editor's judgment.

Finally, the authors use inter-subject overlap as a primary metric for validating the accuracy of functional mapping (Figure 3). However, given that genuine inter-individual variability in brain organization is a central premise of precision mapping, greater overlap across subjects may not necessarily indicate more accurate individual-level localization. A more detailed analysis or discussion of how to distinguish measurement noise from genuine individual differences would make the paper more comprehensive and strengthen its overall contribution.

Reviewer #3 (Public review):

Summary:

This study introduces a principled framework for optimizing multi-task batteries for individualized functional brain mapping. Through simulations and empirical validation, the authors show that selecting tasks to maximize differences in regional response profiles can substantially improve the identification of functional brain regions. The work represents a valuable methodological advance for precision functional mapping, although some assumptions underlying the broader applicability of the framework would benefit from further discussion.

Strengths:

The manuscript addresses an important methodological challenge in precision functional mapping using a rigorous combination of theoretical analyses, simulations, and empirical validation. The framework is practical and well supported by open-source software and a publicly available task library, making it readily accessible for adoption and further development by the research community. The manuscript is well written, logically structured, and clearly presents both the methodological framework and its practical implementation.

Weaknesses:

(1) The abstract and introduction emphasize the application of the framework to individualized brain parcellation. While the presented analyses convincingly demonstrate improved prediction of held-out task responses using atlas-guided parcel assignments, they do not directly validate whether the optimized task batteries improve the estimation of an individual's true functional boundaries. The empirical validation relies on atlas-defined parcel identities as the reference standard, yet substantial inter-individual variability in the location and extent of functional regions - particularly within association cortex - has been well documented. Consequently, improved recovery of atlas-defined parcel labels does not necessarily imply more accurate recovery of an individual's functional organization. It would therefore be valuable to clarify this distinction in the abstract and discussion and to discuss how inter-individual variability may influence the interpretation and generalizability of the parcellation analyses.

(2) The framework assumes that informative task batteries can be designed to distinguish neighboring functional regions. While this is compelling for well-characterized systems with distinct functional response profiles, it is less clear how the approach generalizes to finer-scale subdivisions within association cortex (e.g., subnetworks), where neighboring regions may exhibit highly similar task-response profiles and their functional roles remain incompletely understood. In these settings, the relevant functional dimensions may not yet be known, making it difficult to design optimized task batteries a priori. It would therefore be valuable for the authors to discuss how the framework could be extended to such cases.

(3) More generally, the framework assumes that the sampled task space adequately captures the functional dimensions that differentiate cortical regions. However, particularly within the association cortex, neighboring regions may exhibit similar task-response profiles while differing in the information they represent, their interactions with other regions, the computations they perform, or their cortical layer-specific response patterns. In such cases, the dimensions that best distinguish cortical organization may not be fully reflected in task-response profiles alone, but instead become apparent through complementary approaches such as representational analyses, task-evoked or resting-state connectivity, computational modelling, or laminar response profiles. It would therefore be valuable to discuss how the proposed framework relates to these complementary perspectives.

(4) Many task batteries inherently contain tasks that vary substantially in cognitive demand. Given that task difficulty is itself a major organizational axis in association cortex, it would be helpful for the authors to discuss how the optimization framework accounts for this. Specifically, could differences in task difficulty drive regional differentiation, even when tasks probe similar underlying cognitive processes? If so, how does the framework distinguish between organizational differences arising from a common demand axis and those reflecting more specific functional specializations?

(5) The Discussion places the proposed framework in the broader context of precision functional mapping and refers readers to a companion paper demonstrating advantages over resting-state ("inside-out") approaches. Given that these comparisons motivate several of the broader recommendations made in the Discussion, it would be helpful to provide a brief summary of the main findings of the companion paper here. This would allow readers to better understand the basis for these conclusions without relying on a separate manuscript.

Reviewer #1 (Public review):

Summary:

This manuscript's major strength is the identification of Col20a1 as a novel marker for terminal Schwann cells (tSCs) and the generation of the Col20a1-CreERT2 knock-in mouse line, which represents a valuable new genetic tool for studying tSC biology at the neuromuscular junction. However, the central conclusion that terminal Schwann cells regulate presynaptic vesicle homeostasis is not sufficiently supported because the electrophysiological and ultrastructural analyses are based on limited sample sizes. Increasing the number of animals and NMJs analyzed would substantially strengthen the conclusions. In addition, further validation of Col20a1 expression using RNAscope or immunostaining, together with comparisons to established tSC markers such as Kir4.1 and NG2, would help establish its specificity. Finally, the developmental appearance of Col20a1-positive axonal Schwann cells is intriguing and warrants further investigation to determine whether these cells migrate and differentiate into terminal Schwann cells during postnatal development.

Strengths:

The authors identified Col20a1 as a specific marker of terminal Schwann cells (tSCs) at the neuromuscular junction (NMJ) in mice and generated a Col20a1-CreERT2 knock-in mouse line for in vivo labeling of tSCs. This represents a novel and significant technical advance for the NMJ field, providing a valuable genetic tool for studying the development, maintenance, and function of terminal Schwann cells in vivo.

Weaknesses:

The major weakness of this manuscript is that the sample sizes are too small to support the authors' conclusion that "Terminal Schwann Cells Regulate Presynaptic Vesicle Homeostasis but Not Neuromuscular Junction Integrity in Mice."

Although the authors state that "Quantification of the tdTomato-positive NMJ ratio showed an ablation efficiency of approximately 80%, with only ~20% of NMJs retaining escaper tSCs" (page 9), they do not provide the sample size or sufficient quantitative information for the Col20a1-tdTomato/DTA ablation experiment shown in Figure 4. This information is essential for evaluating the robustness and reproducibility of the ablation strategy.

The electrophysiological analyses are also based on very limited sample sizes. According to Figure 6, mEPP recordings were obtained from 10 NMJs from 3 control mice and 14 NMJs from 5 tSC-ablated mice. The EPP recordings were based on similarly small numbers (control, n = 10 NMJs from 3 mice; tSC-ablated, n = 14 NMJs from 5 mice). Thus, only approximately 2-3 NMJs were analyzed per tSC-ablated mouse on average. Given the inherent variability among individual NMJs and animals, these sample sizes are insufficient to support broad conclusions regarding the effects of terminal Schwann cell ablation on synaptic transmission.

In addition, the authors describe the phenotype as "leaky" presynaptic spontaneous release, but this terminology is not defined and lacks mechanistic explanation. It is therefore unclear what specific physiological alteration the authors intend to describe.

The sample sizes for the electron microscopy analyses (Figure 7) also appear to be limited, making it difficult to determine whether the reported changes in synaptic vesicle distribution are representative or statistically robust. Because the central conclusion relies heavily on these electrophysiological and ultrastructural data, the evidence presented is not sufficient to support the claim that terminal Schwann cells regulate presynaptic vesicle homeostasis. At present, this conclusion is overly broad and not adequately supported by the available data.

Minor comments:

(1) While several figures contain high-quality NMJ images (e.g., Figures 1B and 4), the image quality in other figures should be improved. For example, the S100B immunostaining appears overexposed in some panels, making it difficult to distinguish individual Schwann cells or visualize the boundaries between adjacent cells.

(2) Some neuromuscular junctions shown in Figure 2C appear to be partially denervated. The authors should clarify whether these represent normal variability, effects of the experimental manipulation, or imaging artifacts.

(3) The authors should specify the muscle preparation used in Figure 3, as this information is necessary for interpreting the results and comparing them with previous studies.

Reviewer #2 (Public review):

Summary:

Two types of Schwann cells (SCs) ensheath motor axons - myelinating SCs along the axonal length and terminal SCs (tSCs) that cover nerve terminals at the neuromuscular junction (NMJ). Therefore, the NMJ is, like other synapses, tripartite, with specialized presynaptic, postsynaptic, and glial cells. Many studies have shown that tSCs play roles in the development and function of the NMJ, but for some of these, interpretation is difficult because it is hard to manipulate tSCs without also manipulating myelinating SCs. To circumvent this problem, Kong et al. make use of a gene selectively expressed in tSCs, Col20a1 (Figure 1), to generate a knock-in mouse line, Col20a1-CreER, that gives them genetic access to tSCs. They cross this to Cre-dependent lines that mark tSCs with a red fluorescent protein (Figures 2 and 3) or ablate them by expression of diphtheria toxin along with the fluorescent protein (Figure 4). They show that ablation at postnatal day (P) 10 does not affect the overall structure or function of the NMJ (Figures 4 and 5). It does, however, affect some aspects of neuromuscular transmission over the following few weeks (Figures 6 and 7). Long-term effects cannot be studied by this method, however, because terminal SCs are replaced, presumably from the preterminal population (Figure 8).

Strengths:

The work is done to a high technical standard, including detailed characterization of the knock-in model. Results are presented clearly and illustrated beautifully. The finding that some early reports of synaptic alterations may result from concurrent loss of axonal SCs is important in rethinking the role of tSCs.

Weaknesses:

(1) The authors claim that tSCs are dispensable for some aspects of NMJ maturation, including synapse elimination (called pruning here), formation of "pretzel-like" postsynaptic topology, and generation of junctional folds in the postsynaptic membrane (lines 223 and 363). However, this conclusion is based on injection of tamoxifen to initiate tSC ablation at P10, which is necessary because Col20a1 is expressed in some preterminal SCs at earlier times. It presumably takes a few days for CreER to translocate to the nucleus and activate the toxin transgene, and some more time for the toxin to be generated and act. This is problematic because synapse elimination and other aspects of maturation mentioned occur during the first two postnatal weeks and are largely complete by P14. Therefore, one cannot conclude that these aspects "proceeded normally despite the loss of tSCs....".

(2) Effects on synaptic transmission are modest at best, being significant at a level of p<0.05 but not p<0.01 (Figure 6E, G, H and most of L). Effects on vesicle density are more robust (Figure 7).

(3) The authors use red fluorescent protein from the Col20a1 to label tSCs, and antibodies to S100b to label all SCs. This is appropriate in normal muscle and soon after tSC ablation. At later times, however, the NMJ is repopulated by S100+ Col20a1- SCs (Figure 8B). It is therefore important to show when this repopulation begins, because a modest recovery of SC coverage could have a big effect. For example, Figure 4C quantifies loss of NMJs with residual RFP+ cells but not S110+ cells; both should be quantified at this and slightly later stages.

Reviewer #3 (Public review):

Summary:

This manuscript reports a novel genetic model, Col20a1-CreERT2 knock-in mouse, to target terminal Schwann cells (tSCs) at mouse neuromuscular junctions in a cell-type-specific and temporal manner. The authors analyzed multiple publicly available single-cell transcriptome databases to identify Col20a1 as the tSC marker. The authors crossed Col20a1-CreERT2 and Rosa26-LSL-tdTomato to label tSCs successfully. In addition, the authors generated Col20a1-CreERT2; Rosa-tdT/ diphtheria toxin subunit A (DTA) to specifically ablate tSCs and analyze the role of tSCs in motor behavior, neuromuscular junction electrophysiological function, and the histology and ultrastructure of neuromuscular junctions.

Strengths:

The Col20a1-CreERT2 x Rosa26-LSL-tdTomato mice successfully labeled the tSCs at NMJs and reported the developmental distribution of the Col20a1-positive cell population. The Col20a1-CreERT2; Rosa-tdT/DTA mice successfully ablated tSCs, which did not cause changes in gross neuromuscular junction architecture, neuromuscular synapse physiology, or motor behavior.

Weaknesses:

The conclusion of this manuscript will be strengthened by additional analysis showing time-course data of tSC ablation and replacement by non-recombined Schwann Cells. Currently, it is not clear when and how long the tSCs are ablated, which makes it difficult to interpret the data and phenotype. Detailed review comments are provided to the authors in the "recommendations for the authors" section.

Reviewer #1 (Public review):

Summary:

The authors build a reusable, disease-agnostic pipeline that retrieves GWAS risk genes from the GWAS Catalog by ontology terms, filters them, and maps them onto Human Protein Atlas (HPA v24) co-expression modules at three biological scales (tissue/organ, brain region, cell type). Enrichment is assessed by a consensus of Fisher's exact test with Benjamini-Hochberg correction and 10⁶-iteration Monte Carlo simulation. Applied to AD, DLB/PD, and FTD/ALS, the analysis reports convergent neuronal-module enrichment across all three diseases, AD-specific enrichment in liver- and immune-associated modules, and DLB-specific enrichment in ciliary modules, followed by a DrugBank-based survey of compounds targeting module gene products.

Strengths:

(1) The core premise is sound and well-motivated: risk-gene lists are hard to interpret because most variants are low-penetrance and broadly expressed, and projecting them onto a multiscale expression atlas is a reasonable route from statistical association toward tissue/cell context.

(2) The pipeline is delivered as reusable, open code (GitHub) built entirely on public inputs (HPA, GWAS Catalog, DrugBank), which is a significant contribution to the field and provides opportunities for replication and expansion.

(3) The dual-enrichment design (fold enrichment with FDR correction plus a 10⁶-iteration Monte Carlo empirical null) is more defensible than any single test, and the "consensus" logic is sound.

(4) The multiscale framing (organ → brain region → cell type), with UMAP module projections, is genuinely helpful and makes the mapping legible to broad scientific backgrounds.

(5) The authors are commendably restrained on one key point: they explicitly report that most risk genes are broadly expressed and not brain-selective, rather than overstating neuronal specificity.

(6) The AD liver/immune convergence is nicely discussed and integrated, and the NAFLD-AD discussion (Kupffer-cell/hepatocyte Aβ clearance, locus coeruleus noradrenergic parallels, "type 3 diabetes") is thorough and well-referenced, even where it remains speculative.

Weaknesses:

(1) Gene-to-variant mapping via the author-reported gene field is unclear. The Methods assign genes using the GWAS Catalog author-reported gene field, which predominantly reflects the nearest gene to the lead SNP and may not be the effector gene; it is also inconsistent across studies and different time periods of publication (i.e., changing methodologies in genomics and GWAS procedures). Because every downstream result depends on the gene set, this choice likely introduces noise and bias into all enrichment, specificity, and drug claims. More modern practices link variants to genes via fine-mapping plus eQTL/pQTL colocalization, or integrative scores. At minimum, the sensitivity of the main signatures to nearest-gene versus colocalization-based assignment should be demonstrated.

(2) The suggestive threshold (p < 1×10⁻⁵) trades specificity for coverage in the analysis that requires specificity. Relaxing from 5×10⁻⁸ substantially raises the false-positive fraction of the gene set. This is defensible for exploratory coverage in under-powered DLB/FTD, but the headline claims concern disease specificity (limited gene-set overlap; distinct signatures). Non-overlap among partially false-positive lists can lead to biological specificity conclusions that may not actually exist. A genome-wide-threshold sensitivity analysis is needed to show the signatures persist. Also, see concerns below about the DLB designation.

(3) "Disease specificity" is confounded by GWAS power. AD GWAS (e.g., Bellenguez; Kunkle; Sherva ~205,500 cases) vastly outpower DLB and FTD discovery. The gene counts (453/278/219) and the minimal three-way overlap (only two genes) track sample size and locus density as much as biology. The claim of "disease-specific genetic architectures" should be tempered and ideally power-matched (e.g., subsampling AD, or restricting to comparable effective N) before specificity is asserted. Also, see concerns below about the DLB designation.

(4) Linkage disequilibrium structure at gene-dense loci is not addressed and may inflate the lipid/liver signal. The overlap genes named as driving the liver/lipid theme include APOC1, APOC2, and APOE, all of which reside within the same chromosome-19 linkage disequilibrium (along with TOMM40). Counting co-regulated, physically clustered genes from one association signal as independent risk genes risks inflation of enrichment for lipid/lipoprotein modules. The five "liver-enhanced" genes flagged in the text again lead with APOE. Evaluation of one gene per independent signal is essential before the liver/lipid signature can be interpreted as multi-gene convergence rather than a single strong gene driving the effect.

(5) The enrichment background is not clear. Risk genes are filtered to HPA brain-detected transcripts, but the Methods do not state whether the Fisher/Monte Carlo background (N_Total) is likewise restricted to brain-expressed/HPA-detected genes or reflects all protein-coding genes, which may introduce bias. Specific information on the Fisher/Monte Carlo should be provided to ensure that the enrichment background is the same. If they are not, additional analyses should be performed to ensure robustness of the findings when restricted to brain-expressed only or the broader background.

(6) Cross-scale "consensus" is not independent confirmation. The same genes reappear across tissue, brain, and cell modules, so agreement across scales is partly built-in rather than corroborating. The neuronal-signature counts (82 AD / 62 DLB / 53 FTD; 186 "unique" genes) should be accompanied by a clear statement of how much cross-scale evidence is non-redundant. Also, see concerns below about DLB designation.

(7) Temporal claims are overstated. Using control HPA tissue avoids end-stage confounds but, by construction, cannot capture disease-state programs central to AD. More importantly, framing these modules as "baseline vulnerability hotspots that precede clinical neurodegeneration" is not tested, as nothing here is longitudinal. This assumption is presented as a finding and should be reworded as a hypothesis.

(8) DLB and PD should not be merged, and the cilia-associated risk genes cannot be termed causal based on the study design. The supporting literature is almost entirely PD (Schmidt iPSC-NPCs from sporadic PD; LRRK2 PD striatum), yet DLB and PD are merged, and the signature is branded "DLB." These should not be merged, particularly as it relates to sporadic PD. Although there are similar genetic risk factors (i.e., GBA, SCNA), of which GBA is unfortunately not mentioned in the manuscript, there are major genetic differences in sporadic PD and even PD with dementia (PDD) and DLB. It is not clear why PDD was not incorporated.

Cross-sectional expression overlap with GWAS genes cannot establish that cilia-associated risk genes are "causative vulnerabilities rather than secondary effects." Please soften to association and rename to reflect the synucleinopathy grouping. Further, additional discussion of important differential genes in this category (i.e., APOE and GBA) is needed, and the pathological description of DLB is incomplete in the introduction (i.e., focuses only on synuclein).

(9) The drug/repurposing analysis rests on a weak targeting rationale. Most of the 1,777 drugs target co-expression-module neighbors of risk genes, not risk genes themselves, so "substantial repurposing reservoir" likely overstates the impact. The anesthetics example (sevoflurane/halothane/desflurane hitting GABA_A subunits and ATP2B2) is a near circular argument, as anesthetics necessarily engage neuronal ion channels. This finding does not independently confirm the neuronal signature.

Statin-dementia and hydroxychloroquine/amodiaquine links are pre-existing, and the Tirzepatide→cilia→DLB inference is highly speculative. This section should be labeled hypothesis-generating, with direct-risk-gene targets separated from module-neighbor targets.

(10) Interpretation leans heavily on nominal (p < 0.05) modules. Several of the most novel claims (parts of the liver and immune signatures) rest on nominally significant modules that do not survive FDR (itself set leniently at p_adj < 0.1). The text should make consistently explicit which claims are FDR/Monte-Carlo-supported versus nominal-only, and de-emphasize conclusions resting solely on the latter.

Reviewer #2 (Public review):

Summary:

Genes associated with risk for a specific disease commonly have widespread expression and functions across the body. Surveying patterns in these effects may reveal novel mechanisms, organs, and systems implicated in a disease, amongst other associations that are truly independent. In this work, Husen and coauthors use the Human Protein Atlas to explore such associations in Alzheimer's disease (AD), Lewy body dementia (DLB), and Frontotemporal dementia (FTD). Focusing on human non-disease tissue expression may avoid the effects of disease progression obscuring initial vulnerabilities. However, associations in non-diseased tissues do not necessarily reflect mechanisms causally related to the diseases themselves.

The work describes patterns of enrichment of genes across tissue types, brain regions, and cell types. A relatively small set of classes of each show enrichment for disease. While neural signatures are unsurprisingly prevalent, these classes are largely distinct across the three diseases. Alzheimer's disease is linked to liver and central and peripheral immune cells, while DLB shows interesting enrichments associated with cilia, which are linked to an existing literature. Results from the drug repurposing approach are then presented, with 1777 drugs linked to protein products of any of the modules enriched by the risk genes using DrugBank, categorised according to key signatures.

The authors developed R code (the HPA GeneSet Explorer) to automate the production of multi-system summaries of the organs, brain regions, cells and gene modules associated with traits and diseases and associated gene sets, within the HPA. Risk gene sets for the three dementia types were derived from the GWAS Catalog.

Strengths:

While many studies of how risk genes contribute to disease take a narrow approach focusing on organs, cell types, and processes already associated with a disease, it is a sensible approach to start with a system-agnostic approach that assesses tissues that are not ostensibly affected by disease. Here, this approach reveals a range of associations for 3 neurodegenerative diseases, identifying disease-associated modules and drug candidates that might be prioritized for subsequent confirmatory inference across biological scales. Results highlight key organs and cell types, most of which have established associations with the disease. Perhaps the most intriguing results are the links of DLB to cilia-related processes, which can be linked to some prior reports of DLB/PD but are not a core element of current theories of pathogenesis.

Weaknesses:

A difficulty with broad, multi-dataset surveys of disease associations is the need to distinguish novel and robust patterns - even if they lack causal evidence - from those that are unsurprising or do not stand out statistically. The work is exploratory in nature, but it is often hard to know how strong the evidence is for particular observations reported.

The work combines nominal, FDR<0.1, and Monte Carlo-based inference (with no apparent multiple assessment control across all tested modules) p-values throughout the paper, with patterns of effects of nominal significance. In some places, modules appear to be retained if they meet any of these criteria, muddying inference. This makes it difficult to weigh the different reported associations. Results report numbers of risk genes showing nominal p<0.05 enrichment across gene modules and biological scales - it is difficult for the reader to determine null expectations for false positives here. Similarly, it is unsurprising that thousands of drugs can be linked to the risk genes and their signatures using nominal significance.

The results have limited mechanistic specificity. The modules identified often reflect biological processes implicated in the diseases. This provides some validation of the approach, but the modules are often broadly defined, providing little mechanistic insight. For example, many aspects of ciliary biology may overlap with DLB, but can the HPA provide more specific insight? More generally, it is difficult to determine how much relevance that enrichment in non-disease tissue has for disease processes. Similarly, it is hard to determine whether overlap of drug targets from DrugBank with these modules realistically increases their prioritization.

Methodologically, there could be more detail. The paper - in particular the methods - is partially presented as a tool/pipeline paper, but thorough descriptions of the HPA models that are employed and modules reported for the analyses should still be presented in detail. The drug repurposing approach is described in a couple of sentences without a precise reference to the tool or statistical methods.

Reviewer #3 (Public review):

Summary:

The manuscript presents the development of a software tool and a computational workflow for the comparison and biological interpretation of GWAS results among three neurodegenerative diseases - AD, PD and FTD - using the data from the Human Protein Atlas. The multi-scale content analysis produces a representation of GWAS results highlighting enrichment at the level of brain regions, organ systems/tissues and cell types as well as in terms of molecular pathways. The manuscript argues that DLB, AD and FTD have differential 'modules' revealed by the procedure.

Strengths:

The system is leveraging vast knowledge sources including both the GWAS catalog and the HPA, and it is integrating these data. This synthesis of information is useful. It is making use of large investment in data generation and data warehouses in order to yield interpretation of epidemiologic results from GWAS in biological terms that may yield insight into disease processes and differences between diseases. The multiscale analysis recognizes the various biological lenses at which the implications of GWAS can be evaluated.

Weaknesses:

There is a lack of controls and/or disease comparators in the study. It is hard to assess that the workflow is performing 'as expected' without a set of positive or negative controls - or at least comparators - to gauge the performance of the tool. The statistical methods are simplistic and rely on Fisher's exact tests, UMAP analyses and clustering with little justification. There is a lack of power analysis and specification of the number of genes required for the procedure to 'work'. The mapping of GWAS hits to genes is simplistic and may in many cases be erroneous, and the implications of errors in these mappings are not considered. Many of the hits are not brain-specific - highlighting the complexity of gene function and the pleiotropic nature of gene activity. Moreover, the mapping between 'tissue enrichment' and 'tissue that is the functional driver of the GWAS signal' may be a logical flaw in the reasoning of the authors. Just because a tissue - such as liver enrichment in AD - is enriched in the GWAS gene-mapping analysis does not mean that that tissue found to be enriched is in fact the functional tissue that gave rise to the GWAS signal. Genes have different isoforms, functions, and regulatory mechanisms in different parts of the organism in different parts of development. In a phrase, the enrichment observed could be correlative and not causative, and in fact the enrichment could be driven by some hidden variable not considered. The etiologic tissue for neurodegenerative disease is the brain. The findings are not necessarily surprising or novel in the distinction between PD, AD, and FTD. Finally, the figures are perhaps not the best way to present results. There are many small pie charts that lack interesting results; the figures are in general hard to read and could use refinement in terms of fonts.

Reviewer #1 (Public review):

This study by Thapliyal and Glauser investigates the neural mechanisms that contribute to the progressive suppression of thermonociceptive behavior that is induced under conditions of starvation. Several previous studies have demonstrated that when starved, C. elegans alters its preferences for a variety of sensory cues, including CO2, temperature, and odors, in order to prioritize food seeking over other behavioral drives. The varied mechanisms that underlie the ability of internal states to alter behavioral responses are not fully understood, however there is growing evidence for a role by neuropeptidergic signaling as well as capacity for functionally distinct microcircuits, formed by distinct internal states, to trigger similar behavior outcomes.

Within the physiological range of C. elegans (~15-25C), starvation triggers a profound reduction in temperature-driven thermotaxis behaviors. This reduction involves the recruitment of the amphid sensory neuron pair AWC. The AWC neurons primarily act to sense appetitive chemosensory cues, however under starvation conditions begin to display temperature responses that previous studies have linked to the reduction in thermotaxis navigation. Here, Thapliyal and Glauser investigate the impact of starvation on thermonociceptive responses, innate escape behaviors that are triggered by exposure to noxious temperatures above 26C or rapid thermal stimuli below 26C. They compare the strength of thermonociceptive behaviors, specifically heat-triggered reversals, in worms experiencing either early food deprivation (1 hour off food) or prolonged starvation (6 hours off food). Their experiments demonstrate a progressive loss of heat-triggered reversals that is mediated by AWC and ASI neurons, as well as both glutamateric and neuropeptidergic signaling.

At the level of neural activity, this study reports that the transition from early food deprivation to prolonged starvation reconfigures the temperature-driven activity of AWC neurons from mostly excitatory to a heterogenous mix combining excitatory and inhibitory responses. This finding is interesting in light of previous work that reported the opposite transition in temperature-driven AWC responses when comparing well-fed worms to those kept from food for 3 hours. Specifically, these differences highlight the differences between temperature responses within the C. elegans physiological temperature range (previous studies) and their noxious temperature response (this study). This study also identifies neural and genetic mechanisms that contribute to differences in thermonociceptive responses at +1 versus +6 hours starvation; interestingly, these mechanisms are also partially distinct from those that contribute to differences in negative thermotaxis behaviors in well-fed and +3 hours starvation worms. A limitation of this manuscript is that these differences are not particularly acknowledged or addressed, other than the hypothesis that independent mechanisms underlie negative thermotaxis versus thermonociceptive stimuli.

In this revised article, the authors commanding knowledge of the distinction between thermotaxis navigation (especially negative thermotaxis) and thermonociceptive behaviors is communicated with an admirable depth and clarity to the readers; this study's new findings are helpfully contextualized within the previous literature.

This study represents an important addition to the growing evidence that C. elegans sensory behaviors are strongly impacted by internal states, and that neuropeptigergic signaling plays a key role in mediating behavioral plasticity. To that end, the authors have provided compelling evidence of their claims.

Reviewer #3 (Public review):

Thapliyal, Gopinath, and Glauser show that starvation alters how C. elegans respond to noxious thermal stimuli. Using targeted neural ablation, mutant analysis, and live-cell functional imaging the authors demonstrate that hunger changes the properties of AWC sensory neurons, which sense noxious heat. The authors further show that effects of hunger on nociception require ASI neurons, which are known to respond to hunger and mediate effects of food deprivation on behavior. Finally, the study uses mutant analysis to implicate glutamate and specific neuropeptides in thermal nociception and in modulation of nociceptors by hunger-responsive neurons.

The study clearly shows a strong effect of hunger on nociception and documents a striking effect of hunger on the intrinsic properties of AWC sensory neurons, which respond to noxious heat. The study also clearly and compellingly demonstrates that ablation of hunger-responsive ASI neurons blocks effects of hunger on nociceptive AWCs. These data, which constitute the kernel of the manuscript, are striking and exciting. This revised manuscript analyzes effects of starvation on AWC physiology and clearly shows that starvation alters the way AWCs respond to thermal stimuli by decreases the probability that AWCs will be activated and increases the probability that they will be inhibited. New data also identify ASI-derived neuropeptides that are required for modulation of AWCs by starvation. This study reveals a mechanistic link between an animal's metabolic state and sensory processing and establishes modulation of AWC function as a powerful model to study the molecular basis of this link.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers.]

The authors investigated the response of worms to the odorant 1-octanol (1-oct) using a combination of microfluidics-based behavioral analysis and whole-network calcium imaging. They hypothesized that 1-oct may be encoded through two simultaneous, opposing afferent pathways: a repulsive pathway driven by ASH, and an attractive pathway driven by AWC. And the ultimate chemotactic outcome is likely determined by the balance between these two pathways.

It is not surprising that 1-octanol is encoded as attractive at low concentrations and repulsive at higher concentrations. However, the novel aspect of this study is the discovery of the combinatorial coding of 1-oct in the periphery, where it serves as both an attractant and a repellent. Furthermore, the study uses this dual encoding as a model to explore the neural basis of sensory-driven behaviors at a whole-network scale in this organism. The basic conclusions of this study are well supported by the behavioral and imaging experiments, though there are certain aspects of the manuscript that would benefit from further clarification.

A key issue is that several previous studies have demonstrated a combinatorial and concentration-dependent coding of odorant sensing in the nematode peripheral nervous system. Specifically, ASH and AWC are the primary receptors for repellent and attractive responses, respectively. However, other neurons such as AWB, AWA, and ADL are also involved in the coding process. These neurons likely communicate with different interneurons to contribute to 1-oct-induced outputs. The authors' conclusion that loss of tax-4 reduces attractive responses and that osm-9 mutants reduce repulsive responses is not entirely convincing. TAX-4 is required for both AWC (an attractive neuron) and AWB (a repulsive neuron), and osm-9 is essential for ASH, ADL, and AWA (attraction-associated). Therefore, the observed effects on the attractive and repulsive responses could be more complex. Additionally, the interpretation of results involving the use of IAA to reduce the contribution of AWC at lower concentrations lacks clarity.

The authors did not observe any increased correlation between motor command interneurons and sensory neurons, which is consistent with the absence of a consistent relationship between state transitions and 1-oct application. Furthermore, they did not observe significant entrainment of AIB activity with the 2.2 mM 1-oct application. This might be due to the animals being anesthetized with 1 mM tetramisole hydrochloride, which could affect neural activity and/or feedback from locomotion.

Reviewer #2 (Public review):

Summary:

The authors used whole-network imaging to identify sensory neurons that responded to the repellant 1-octanol. While several olfactory neurons responded to the initial onset of odor pulses, two neurons consistently responded to all the pulses, ASH and AWC. ASH typically activates in response to repellants, and AWC typically activates in response to the removal of attractants. However, in this case, AWC activated in response to the removal of 1-octanol, which was unexpected because 1-octanol is a harmful repellant to the worm. The authors further investigated this phenomenon by testing different concentrations of 1-octanol in a chemotaxis assay and found that at lower (less harmful) concentrations the odor is actually an attractant, but becomes repulsive at higher concentrations. The amplitude of the ASH response appeared to be modulated by concentration, but this was not true for AWC. The authors propose a model where the behavioral response of the worm is the result of integrating these two opposing drives, where repulsion is a result of the increased ASH activity over-riding the positive drive from AWC. The authors further tested this theory by testing mutants that ablated the AWC response (tax-4 or AWC::HisCl) or ASH response (osm-9 or ASH::HisCl). The chemo-silencing (HisCl) and tax-4 experiments were consistent with their hypothesis, while the osm-9 mutation had a limited impact on chemotaxis behavior, highlighting the potential role of osm-9-independent signaling in ASH in response to 1-octanol. While the interneuron(s) that integrate these signals to influence behavior were not identified, the authors did find that increasing concentrations of 1-octanol did increase the likelihood of AVA activity, a neuron which drives reversals (and hence, behavioral repulsion).

Strengths:

This was simple and elegant work that identified specific neurons of interest which generated a hypothesis, which was further tested with mutants that altered neuronal activity. The authors performed both neuronal imaging and behavioral experiments to verify their claims.

Weaknesses:

The authors note that other sensory neurons likely contribute to 1-octanol chemotaxis. Given the NeuroPAL data, it would have been nice to identify these other neurons as well. However, the reviewer is aware that this is tangential to the primary focus of this study.

Reviewer #3 (Public review):

Summary:

This work describes how two chemosensory neurons in C. elegans drive opposite behaviors in response to a volatile cue. Because they have different concentration dependencies, this leads to different behavioral responses (attraction at low concentration and repulsion at high concentration). It has been known that many odorants that are attractive at low concentrations are aversive at high concentrations, and the implicated neurons (at least AWC for attraction and ASH for repulsion) have been well established. Nonetheless, by studying behavior and neural responses in a common context (odor pulses, as opposed to gradients) this provides a clear picture of how these sensory neurons may guide the dose dependent response by separately modulating odor entry and odor exit behaviors.

Strengths:

(1) This work provides good evidence that worms are attracted to low concentrations and repelled by high concentrations of 1-oct. Calcium imaging also makes it clear that dose-dependence of this response is stronger for ASH than AWC.

(2) This work presents calcium imaging and behavior with the same stimulus (sudden pulses in volatile odor concentration), while previous studies often focus on using neuronal responses to pulses to understand navigation of gentle gradients.

Weaknesses:

(1) As a whole it is not clear precisely how important AWC is (compared to other cells) for the attractive response (as the authors correctly acknowledge).

(2) The evidence that AIB minus AVA contains relevant information is weak. It appears the entrainment index in Fig. 6H for AIB-AVA could easily be explained by the negative entrainment between AVA and the stimulus (along with no effect or role for AIB). This is suggested by the similar p-values and similar distribution of random EIs (stretched and mirrored) between the first and last rows of this figure.

Reviewer #2 (Public review):

Summary

The authors aimed to investigate how microbial metabolites, including hydrogen and short-chain fatty acids, influence feeding behavior and clock-gene expression in mice. Specifically, they examined these effects across different microbial environments, including a reduced-community model, germ-free mice, and specific-pathogen-free mice. The study addresses an important and poorly understood question concerning how microbial metabolism may influence host daily rhythms and feeding patterns.

Strengths

The manuscript presents a thoughtful and innovative investigation into the relationship between microbial metabolism, feeding behavior, and host clock-gene expression. A major strength is the use of a reduced microbial community together with real-time measurements of hydrogen production, which provides a useful experimental framework for separating microbial metabolic activity from direct host nutrient intake. The inclusion of germ-free and specific-pathogen-free mice also allows the authors to examine how these effects depend on microbial complexity.

The revised manuscript has addressed several concerns raised in the original review. The authors have clarified aspects of stool collection, provided additional methodological information, refined their use of the terms "circadian" and "diurnal," and added experiments examining the osmotic effects of lactulose across different microbial environments. These revisions improve the clarity and interpretation of the work. The finding that lactulose-induced microbial activity is associated with altered feeding behavior and clock-gene expression in the reduced-community model, but not consistently in germ-free or specific-pathogen-free mice, remains intriguing and highlights the complexity of microbial-host interactions.

Weaknesses

Despite these improvements, several important concerns remain unresolved. Most notably, the response regarding excluded food-intake measurements is insufficient. The authors report that the probability of excluding measurements differed significantly between treatment and control groups in the key feeding experiment shown in Figure 4A/S5A. However, they do not provide the underlying number or percentage of excluded observations, the direction of the imbalance, how many animals were affected, whether the exclusions occurred before or after treatment, or which exclusion criteria accounted for the removed values. Because food-intake rate was calculated from repeated measurements of cumulative intake, differential exclusion of observations could influence both the estimated slope and the reported treatment effect. The authors should provide these details and demonstrate that the principal feeding result is robust to the exclusion procedure.

There is also ambiguity surrounding the analysis and presentation of the quantitative polymerase chain reaction data. Figure 3B-C and Supplementary Figure 4A-C use conflicting mathematical labels, the raw cycle-threshold and replicate-level delta cycle-threshold values are not provided, and the rebuttal appears to conflate logarithmic transformation with exponentiation. I suspect that this may primarily reflect terminology or figure-labeling errors rather than an incorrect underlying analysis. The negative values shown in Figure 3 suggest that the authors may have plotted negative delta-delta cycle-threshold values, corresponding to log2 fold change. Nevertheless, the current description makes the workflow difficult to verify.

Several mechanistic and interpretive issues were acknowledged but only partially addressed. The authors appropriately softened their interpretation of the clock-gene findings and clarified that hormone concentrations were measured at only one time point. However, they did not provide baseline evidence that the positive and negative limbs of the clock-gene network are normally in counterphase, did not discuss the possible involvement of AMP-activated protein kinase, and did not address the limitation of measuring total rather than active glucagon-like peptide 1. These issues should be explicitly discussed as limitations of the current study and as priorities for future work.

Overall assessment

The authors have mostly achieved their aims by providing novel evidence that acute changes in microbial metabolism may influence feeding behavior and clock-gene expression in a simplified microbial environment. The experimental approach is creative, and the study has the potential to contribute meaningfully to the fields of microbiome research and circadian biology. However, unresolved concerns regarding differential data exclusion and the transparency of the gene-expression analysis currently limit confidence in the strength of the evidence supporting the principal conclusions.

Addressing these reporting and analytical issues would substantially strengthen the manuscript and improve its value to researchers studying microbial metabolism, feeding behavior, and host biological rhythms.

Reviewer #3 (Public review):

Summary:

In the manuscript by Greter, et al., entitled "Targeted induction of gut-microbial metabolism acutely affects feeding patterns and clock gene expression in the host" the authors investigate whether acute exposure to a non-nutritive disaccharide (lactulose) promotes microbial metabolism that feeds back onto the host to impact circadian networks. The premise of the study is interesting, and the experiments are thoughtfully designed to dissect these relationships. The evidence presented generally supports the authors' conclusions regarding the impact of lactulose administration during the fasting period, which is intended to mimic a feeding-associated perturbation of the gut microbiota, and its comparison with lactulose administration during the fed state. The studies employ complementary model systems, including germ-free mice, mice colonized with a simplified three-member microbial community, and conventionally colonized animals. These approaches support the authors' conclusions regarding the relationship between diurnal rhythms of microbial fermentation and host circadian clock gene networks. Overall, the work provides a useful experimental framework for developing a deeper mechanistic understanding of how microbial fermentation products contribute to diurnal host-microbe interactions.

Strengths:

Attempting to disentangle nutrient acquisition from microbial fermentation and its impact on diurnal dynamics of gut microbes on host circadian rhythms is an important step for providing insights into these host-microbe interactions.

The authors utilize a novel approach in leveraging lactulose coupled with germ-free animals and metabolic cages fitted with detectors that can measure microbial byproducts of fermentation, particularly hydrogen, in real time.

The authors consider several interesting aspects of lactulose delivery, including how it shifts osmotic balance as well as providing calculations that attempt to explain the caloric contribution of fermentation to the animal in the context of reduced food intake. This provides interesting fundamental insights into the role of microbial outputs on host metabolism.

The authors employ complementary systems, including a simplified three-member microbial community, providing insight into the minimal set of functionally distinct community members necessary to promote the rhythmic production of fermentation products that can affect host physiology.

Residual limitations:<br /> Hypothesis and study framing: The manuscript still does not clearly articulate a specific, testable hypothesis. While the Introduction provides motivation and objectives (e.g., line 53 onward), it remains unclear what precise hypothesis was being evaluated. A more explicit statement would strengthen the conceptual framework of the study.

Interpretation of circadian gene expression changes: The authors have not fully reconciled the differing effects of lactulose treatment on circadian gene expression in the 3MM and SPF settings. In particular, it remains unclear how the increased expression of certain circadian genes observed in lactulose-treated 3MM mice, particularly Cry1, relates to the decreased expression seen in SPF mice, and how the reduction in Arntl expression observed in lactulose-treated SPF mice fits within the proposed model. The authors acknowledge that resolving these mechanistic differences is beyond the scope of the current study, but the limitation should be discussed more explicitly.

Reviewer #1 (Public review):

In this methods paper, the authors introduce a novel and innovative imaging approach for simultaneous in vivo multiphoton imaging of the mouse brain combined with DMD-based one-photon patterned photo-stimulation in different axial planes. This is a highly exciting technique that enables the axial decoupling of optical imaging of deep neural circuits from surface photo-stimulation of spatially precise (tens of micrometres) brain spots. This method builds on previous developments from the same laboratory, combining DMD-based patterned photo-stimulation with in vivo electrophysiological recordings. To my knowledge, this is the first instance in which patterned photo-stimulation has been combined and axially decoupled from two-photon (2P) imaging.

Beginning with a thorough characterisation of the optical resolution of the photo-stimulation system, the authors applied this method to the olfactory bulb (OB) network, in which sensory inputs are topographically organised at the surface of the OB and thus ideally suited to demonstrate the relevance of this approach. They first showed that this technique can be used to rapidly reveal connectivity patterns of OB output neurons and to identify sister mitral cells. In addition, they manipulated a specific glomerular inhibitory population and demonstrated that these neurons provide spatially heterogeneous long-range inhibition of OB output neurons, with differential effects on mitral and tufted cells (a result previously observed in a paper from the same lab: Banerjee et al., 2015, Neuron). Altogether, the data demonstrate that this technique is well-suited for high-throughput functional mapping of neural circuit properties. The results are compelling and illustrate both the significant advance represented by this method and its feasibility.

Despite my initial enthusiasm, there are several concerns in the present study that must be addressed in order to rule out confounding observations and to resolve remaining uncertainties regarding photo-stimulation resolution. These include the following:

(1) Spatial resolution: Although the authors provide convincing data on spatial resolution in vitro, several observations throughout the paper suggest that the effective photo-stimulation precision may be lower than initially reported. For instance, in Figure 2, the authors observe repeated responses in neighbouring glomeruli (e.g., glomeruli #3 & #5, #4 & #6). To what extent could light scattering along the X/Y/Z-axis above the targeted glomerulus recruit en passage axons, resulting in the inadvertent activation of multiple glomeruli?

A further observation concerns the presence of "inhibited" sister mitral cells (Figure 3). The authors claim this is reminiscent of the differential spike-timing reported between sister cells (Dwawale et al., 2010, Nat Neuro). However, observing both excitatory and inhibitory responses following stimulation of glutamatergic inputs is an altogether different matter, particularly given that sister mitral cells are reciprocally connected via gap junctions. This observation requires further clarification and raises serious questions about the effective resolution of the stimulation. Could the inhibited cell simply correspond to a non-sister mitral cell receiving disynaptic feed-forward inhibition? To verify sister cell identity, the authors could confirm that the predicted sister cells share a similar odour receptive field compared to randomly selected mitral cell pairs. In their previous study employing analogous DMD-based photo-stimulation (Dhawale et al., 2010, Nat. Neurosci.), sister mitral cells did not exhibit such opposite response profiles (firing rate correlation of ∼0.7 between sister cells). Could the authors verify that a comparable activity correlation is also observed among the sister cells identified using ADePT in the present study? In Figure S6, the authors show recordings and stimulation of the same neurons co-expressing GCaMP and ChR2. Applying this experimental design to the mitral/tufted cell population (using a Tbet-Cre mouse transduced in the OB with both GCaMP and Chrimson virus) would constitute a valuable control to clarify the nature of these "inhibited" sister cells.

An additional concern relates to the 21 out of 162 mitral cells that were activated by two distinct glomeruli - a finding that is incompatible with the established OB wiring diagram and that further challenges the claimed stimulation resolution.

A critical control experiment is also absent: in a Thy1-GCaMP6 mouse lacking any light-sensitive opsin, do the authors observe any unintended side effects of photo-stimulation?

Regarding sister cells (Figure 3), tufted cells are not analysed alongside mitral cells in this dataset, whereas this is elegantly performed in Figure 5 using the DAT+ model. Could the authors also demonstrate how the technique can reveal the complete family portrait of sister mitral and tufted cells?

(2) The authors have explored only a limited set of photo-stimulation parameters, primarily varying light intensity. They should present additional tests, such as varying the spot size (which appears to be arbitrarily fixed at 30-50 µm) and the z plane of stimulation. The level of activation can vary considerably: for example, in Figure 3a(iii), identical stimulations elicit responses of markedly different amplitudes (see glom#3 and #4). In Figure 2, 5 out of 15 glomeruli failed to respond - could the choice of z-plane account for this variability? The stimulation duration (50-150 ms) also appears somewhat arbitrary: can the authors demonstrate that the technique is compatible with finer temporal patterns (e.g., 10 Hz stimulation for 500 ms using 20 ms light pulses)? What are the spatiotemporal and axial scanning limits of this approach, and can two or three glomeruli be targeted simultaneously with temporally patterned stimulation?

(3) One particularly relevant application of this method would be to guide photo-stimulation based on prior functional measurements - for instance, by generating a photo-stimulation mask specifically targeting odour-responsive glomeruli. In the DAT-Cre × Thy1-GCaMP6 experiment shown in Figure 5e, which glomeruli are activated by a given odour, and how does this odor responsiveness influence the efficiency of DAT+ cell-mediated inhibition?

Reviewer #2 (Public review):

Summary:

In this manuscript, Koh and colleagues describe ADePT (Axially Decoupled Photo-stimulation and Two-photon Readout), a modular approach for combining patterned one-photon optogenetic stimulation with two-photon calcium imaging in independently controlled axial planes. The method relies on a digital micromirror device together with a motorized holographic diffuser to generate spatially confined stimulation patterns while imaging deeper neuronal populations. As proof-of-principle applications, the authors use the system to map excitatory and inhibitory functional connectivity in the mouse olfactory bulb by stimulating superficial glomerular circuits and recording responses from mitral and tufted cells in deeper layers.

This is a well-executed Tools and Resources manuscript. The technical implementation is described in considerable detail, the optical performance is systematically characterized, and the biological experiments provide convincing demonstrations of the types of circuit questions that can be addressed using the method.

Strengths:

The greatest strength of the manuscript is the comprehensive technical characterization of the optical system. The authors carefully benchmark the spatial resolution, axial confinement, registration accuracy, calibration procedure, and practical operating limits of the setup. I found the extensive optical benchmarking particularly helpful, as it gives readers a realistic sense of the operating regime and practical limitations of the approach.

Another strength is the high level of methodological transparency. The optical design, calibration procedures, stimulation strategies, and analysis pipeline are described in sufficient detail that an experienced laboratory could realistically evaluate whether the system is suitable for its own applications. This level of documentation is particularly appropriate for a Tools and Resources article.

A further strength is the clear positioning of ADePT relative to existing approaches. The authors are transparent about the trade-off between spatial resolution and implementation complexity: ADePT does not provide single-cell photostimulation, but offers flexible axial separation, a large stimulation field, and cellular-resolution two-photon readout in deeper planes without requiring a full holographic stimulation system. This defines a credible and potentially useful experimental niche.

The biological applications convincingly demonstrate the utility of ADePT. The experiments identifying sister mitral/tufted cells through selective glomerular stimulation and the mapping of heterogeneous inhibitory influences from DAT-positive interneurons illustrate the types of functional connectivity questions that become experimentally accessible with this approach. Importantly, the authors generally avoid overstating these biological findings and appropriately present them as proof-of-principle demonstrations of the technology.

Weaknesses:

The primary limitation is inherent to the method itself rather than the execution of the study. Because ADePT relies on one-photon patterned illumination, photo-stimulation remains restricted to relatively superficial structures and does not achieve single-cell spatial resolution. The authors appropriately acknowledge these constraints and clearly position the method within this operating regime. Consequently, ADePT occupies a useful niche for interrogating spatially organized functional units such as olfactory glomeruli or cortical barrels, rather than applications requiring single-cell precision or deeper tissue penetration.

Although the manuscript describes the approach as relatively simple and cost-effective, implementation still requires careful optical alignment, registration, calibration, and optimization. This does not diminish the value of the approach, but terms such as modular or accessible may better reflect the practical implementation than simple. Likewise, a brief bill of materials, approximate add-on cost, and indication of which components are essential versus substitutable would help prospective users assess the accessibility of the system.

Finally, the manuscript provides an impressive level of technical characterization, but much of the practical guidance for adopting the system is distributed across the Results and Discussion. Bringing together the principal limitations, recommended operating regime, expected calibration workflow, evidence for long-term alignment stability, and the circumstances in which ADePT is preferable to alternative approaches would further strengthen the manuscript as a community resource.

Reviewer #1 (Public review):

Summary:

This paper reports an important MEG study that is interesting from many different angles. By manipulating presentation rate (Fast vs. Slow) and "Structure" (word list vs. sentence list vs. story), the authors revealed the spatiotemporal dynamics of processing constituents at different speeds and semantic-conceptual scales. The methods are solid, and the results would be interesting to both researchers interested in the neural basis of structure building and researchers interested in the consequences of presentation rate, which, as the authors note, is understudied for visual sentence presentation. Overall, I enjoyed reading this paper and agree that it reports valuable findings for language processing, but there are a few points where clarity can be improved for readers to better evaluate and appreciate this work.

Strengths:

This paper studies the effects of presentation rate and linguistic structure building at different scales with MEG, which is perhaps one of the first MEG studies approaching these questions, and MEG is an appropriate technology to investigate spatiotemporal dynamics in the brain. The authors conducted a breadth of analysis, enabling us to fully understand what is shown by their data.

Weaknesses:

Here I would like to point out a few points where clarity can be improved (e.g., analytical details) for readers to better appreciate this paper.

(1) The "mean proficiency" was reported on page 5, but I did not see the details of the proficiency task, which also need to be reported.

(2) I was confused about the baseline correction part of the MEG analysis on page 10, and I would appreciate it if the authors laid out the rationale more clearly. From what I understand, the authors did not perform baseline correction, which is completely understandable, as word-lists, sentence-lists, and stories would have different baselines, and the baselines also keep building up as the trial evolves (which is a part of the study, instead of something to be parsed out). In this context, it becomes confusing why the authors singled out the Fast presentation condition to be unsuitable for baseline correction ("Since the prestimulus period cannot be analyzed during the Fast presentation..."). If the rationale is that the Fast condition did not have a long-enough blank screen between segments, this would not be a problem, as baselining is done in ERP RSVP studies anyway all the time. I am also curious what is meant by "The Fast and Slow presentation conditions were separated and demeaned independently". Would this make comparing the Fast and Slow conditions trickier? Overall, I think the analytical choices are potentially defensible, but more explanations of the rationale are needed.

(3) For the Results section, the authors should check the text again to increase clarity for statistical reporting for readers. For example, on page 14, the p-values were not always reported, and the dfs for t-values were also not always reported. For "pairwise comparisons", one would expect a reporting like "ps < ..." instead of a singular "p < 0.001".

(4) For behavioral results, was the analysis of RT directed at all trials or correct trials only? It would be worth checking whether the RT results hold true when analyzing only correct trials, or whether they were primarily driven by incorrect trials. Note that I don't find it a problem to include all trials for the MEG analyses (which the authors did), as we would believe that the participants were doing the task anyway despite it being challenging, and task difficulty was an inherent component of the research goal instead of something to be parsed out.

Reviewer #2 (Public review):

Summary:

The main contribution of this study is that brain activations related to linguistic context varied as a result of presentation speed, with the main finding that increased activity for coherent stories relative to other conditions was reduced in fast presentation relative to slow. The results thus challenge certain assumptions about the nature of the brain dynamics of language processing, with certain effects even disappearing under faster presentations, which may be related to the processing mode of the participant. The results continue to establish the viability of a parallel presentation design, which generally produces results congruent with those of the literature.

Strengths:

The study contains a somewhat novel presentation method, illustrating its viability. The results are bolstered by a strong sample size (N=33) and robust analytic techniques. The conclusions are measured and appropriate to the results, and the manuscript is exceedingly clearly written and accessible to readers.

Weaknesses:

The spatial specificity of the effects is hampered by the use of MEG, particularly with minimal structural MRIs for participants. Thus, the conclusions of the study in the spatial domain are tentative and more general than might result from other studies.

In addition, the general finding that faster presentation speed reduced activity overall (and eliminated it in the frontal cortex) appears to be somewhat contradictory to existing literature, which finds that sentences which are complex or difficult to process generally produce greater activation, particularly in the frontal cortex. These studies might be reviewed, and this (seeming) contradiction could be addressed.

Reviewer #1 (Public review):

Summary:

Chen and colleagues utilize in vivo electrophysiology to characterize distance-encoding neurons in the retrosplenial cortex of rats during both random foraging and goal-oriented navigation. They observe a subset of RSC neurons that encode distance to a hidden goal location and that HD coding is enhanced during goal-directed navigation when compared to foraging. They also demonstrate that goal distance coding is preserved in the dark. Distance encoding has been shown in RSC in prior publications, but examining it with respect to a behaviorally relevant location will be of interest to the field. That said, the manuscript needs substantially more methodological detail before I am convinced that goal-distance-to-goal (DTG) coding is not an artifact of self-motion or of other spatial tuning already known to exist in the area. The authors also introduce several new machine-learning approaches that are hard to interpret without clearer justification or a demonstrated need. Addressing the points below would provide more convincing evidence for DTG coding and enhance readability.

Strengths:

The task is useful for determining whether the goal distance is encoded in neural populations.

Retrosplenial cortex is an excellent candidate region for examining representations related to goal distance.

The analytical framework is state-of-the-art and is useful for determining the contribution of goal distance to complex activation in retrosplenial cortex that possesses mixed selectivity.

Weaknesses:

The analyses/simulations intended to ascertain the relationship between other known spatial/self-motion codes in RSC and DTG coding are insufficient. I struggle with how DTG and speed can be convincingly disentangled given task structure. I suspect many DTG cells are in fact speed-modulated, and that if the task was flipped such that the animal had to run through the goal location rather than stop, DTG tuning curves would be mirrored. There are a couple of simple things that could help:

(1) Show significantly more examples of DTG neurons (perhaps all of them) alongside their corresponding spatial (e.g., EBC and HD) and self-motion tuning curves (e.g., speed and angular speed) for multiple goal locations.

(2) The relationship between the DTG tuning curve and the speed tuning curve should be presented.

(3) Report what fraction of DTG cells are tuned to a random, non-goal location, what fraction qualify as DTG by chance, and how much better goal decoding is than decoding to a random location (Figure 2a).

(4) We need visualizations of DTG reliability both within and across goal locations (see below).

The GLM analyses are meant to address the unique contribution of distance to goal, but there are issues with this approach.

(1) The five behavioral variables included in the analysis are not independent and will covary strongly. Forward selection is greedy, so once one member of a correlated set is admitted, the remaining members' unique contribution to held-out log-likelihood may fall below the 0.01 bits/spike threshold even if they are genuinely encoded. The pairwise correlation (or mutual information) structure among the five variables should be reported for all sessions, as well as the Δllh values of the variables rejected at each step, so readers can judge how close the near-misses were.

(2) What is the L1 penalty and how was it selected? L1 shrinkage lowers each candidate's Δllh, so a stronger penalty yields smaller selected models. This is also important when considering that the basis sets for each variable have different dimensionality. Is a single L1 penalty shared across candidate models?

Reliability of DTG responses.

(1) The 1D DTG tuning curves lack error bars, which should be presented to convey reliability. These should be shown for individual DTG neurons for multiple goal locations.

(2) The 2D DTG ratemaps in Figure 1 are not especially compelling; it would be helpful to see all examples in the supplement.

Several observations suggest that some DTG neurons may actually be encoding boundaries.

(1) The distribution of DTG peaks is strongly bimodal, with peaks either at the goal or at the boundary. Together with the mixed-selectivity results, this suggests that some DTG cells may show a boundary response or activity at the goal related to speed or acceleration. The manuscript at present does not effectively rule out this possibility. This could be addressed by showing that DTG coding is preserved across different goal locations.

(2) An arena-expansion condition would clearly distinguish DTG responses from boundary responses.

(3) It would be useful to see the peak sorted plot (1E) cross-validated within and across goal locations. I suspect that DTGs with intermediate-distance peaks shift with goal location while the others do not. If they remain fixed, it would solidify the presence of the phenomenon.

More characterization of the neurons that are 'important' for goal distance decoding that are not DTG cells is needed (i.e., the IMP population). As I understand it, IMP and DTG cells were grouped for decoding analyses, but the two populations do not overlap. The IMP population is much larger than the DTG cells, and it is unclear what these neurons are doing. Moreover, it seems that the IMP sub-class could alone be used to decode distance to goal. This is difficult to reconcile with the framing of DTG cells as the substrate of goal-distance coding and deserves comment. Decoding should be conducted with the IMP cells alone to show what the DTG cells actually add.

Reviewer #2 (Public review):

Summary:

Chen et al. consider the activity of retrosplenial cortex (RS) neurons during performance of an open-field navigation task in mice. Using a Ca-++ transient imaging approach to examine activity, the authors claim to find tuning to distance of the animal to a hidden reward location. The question of tuning to distance in RS is of much interest of late, with other works making claims. In this respect, the present work is interesting in that it utilizes an actual navigational task that does not explicitly demand encoding of distance and does consider an open-field environment. I do have reservations concerning the robustness of distance tuning.

Strengths:

Testing of distance coding in open fields during performance of an actual navigational task.

Weaknesses:

Lack of robust evidence for distance coding and head direction coding.

Reviewer #1 (Public review):

Summary:

The authors have achieved an excellent, thorough anatomical characterization of all spinal projecting neurons in the larval zebrafish. The comprehensive nature of their labeling approach and their quantification will make this work an instant reference benchmark for a wide number of zebrafish researchers. In addition, the scholarly approach in comparisons with other work in and outside of fish makes the manuscript valuable to researchers outside the field who would like to know how to translate between zebrafish and mouse terminologies.

Strengths:

The figures are clear and easy to follow. The literature review is impressive. The authors are careful to note the few limitations of their approach (eg the absence of Mauthner cell labeling and associated large neuron weak label). The manuscript does the whole field a major service.

Weaknesses:

No weaknesses were identified by this reviewer.

Reviewer #2 (Public review):

Summary:

The 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 the 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 whole approach could be enhanced by counter-staining their preparation to profile brain structures, including many nuclei more precisely.

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

Reviewer #3 (Public review):

In this study, the authors aim to provide the most comprehensive and detailed topographic map to date of spinal projection neurons in the larval zebrafish brain. They achieve this by retrogradely photoactivating, in the rostral spinal cord, a photoconvertible GFP expressed pan-neuronally, and by constructing a template larval zebrafish brain atlas to regionalize the location of all labeled somata across the brain. The labeling strategy, together with the chosen animal model, provides strong support for the completeness of the dataset. The generation of a standardized anatomical atlas establishes a rigorous framework for analysis. Molecular and anatomical evidence suggesting evolutionary conservation of selected regions of interest appears solid.

Overall, the authors successfully achieve their aim. By generating this atlas of spinal projection neurons, they provide not only an anatomical framework of the regions involved, but also an important reference for improving the orientation and regionalization of the zebrafish brain, which has historically been difficult to define. This work may serve as a valuable resource for future evolutionary, developmental, and comparative studies of spinally projecting neuronal populations implicated in diverse functions.

Reviewer #1 (Public review):

Summary:

This manuscript presents a new foundation model, EvoDiff, for designing primary protein sequences. By leveraging an evolutionary-scale dataset, the model can be applied to evolution-guided sequence generation, sequence inpainting, and functional scaffolding.

Strengths:

The model provides an efficient approach for designing protein sequences and could be useful for developing protein therapeutics, engineering enzymes, designing biomaterials, and many other applications. The manuscript presents solid results showing that proteins designed by EvoDiff can achieve the same biological functions as their wild-type counterparts.

Weaknesses:

Compared with other sequence-generation models, EvoDiff does not substantially improve the success rate, suggesting that significant experimental effort is still required to screen and identify successful hits.

Reviewer #2 (Public review):

In this work, Alamdari et al. present EvoDiff, which provides the capability to generate protein sequences directly in sequence space, using a discrete diffusion model. There are several versions. EvoDiff-seq is trained on UniRef50 sequences (~42 million), and EvoDiff-MSDA operates instead by using sequence alignment methods to generate new members of protein families. The authors demonstrate many modes of sequence generation, including unconditional and conditional, inpainting of disordered regions, and also generating scaffolding of functional motifs. Their evaluation is also multifaceted, covering foldability, folding self-consistency, language embeddings, secondary structure distributions, and experiments for a set of different scenarios.

The paper has many notable strengths. It is comprehensive in breadth, and the experimental component is distinctive, although I am not personally suited to review the rigor of that element.

I would suggest that the paper's results certainly support the conclusion that order-agnostic sequence generation can yield useful candidates for multiple conditional design tasks. I am not totally convinced that it necessarily establishes diffusion as a generally superior approach to other competitors, like the conventional protein language models- EvoDiff is certainly competitive, and I think that the demonstration of diffusion is nice. I also am not sure that it is fair to say that sequence alone is sufficient for the broad design capabilities claimed (other than the "in principle" statement).

I am overall quite supportive of the work and its demonstration, but I have a few comments for consideration in any revision.

(1) I did not work through all dates of everything, but it appears to me that there are several recent conceptual and methodological competitors. These include DPLM and ProtBFN - both of these seem to be after the first preprint of EvoDiff, but given the time gap, there probably deserves to be some additional discussion or comparison. I would say, ideally, they should offer direct benchmarking. If the authors are disinclined, then I would think they should just temper their claims of contemporary SOTA performance or general superiority. Instead, the paper would still remain valuable as an early and experimentally demonstrated sequence diffusion framework. I don't think it needs to be more than that.

(2) Related to the above, the manuscript should more carefully distinguish the demonstrated advantage of order-agnostic generation from the quality of unconditional generation. Regarding Figure 3, the authors argue that Evodiff's diffusion objective is necessary, but this does not seem to account for or address the LRAR baselines in Tables S1 and S3. Unless I am misunderstanding, the 640M LRAR model exhibits several better scores. The authors later suggest that EvoDiff's principal advantage is conditioning on arbitrary positions, which is valid, but that's a little different that what is being claimed. I suggest that the LRAR results should be shown or discussed alongside Figure 3, and then the authors revise to say that they have flexible conditional generation as the principal empirical benefit.

(3) I really like the IDR experiment, but I'm not sure it demonstrates that Evodiff can design functional IDRS generally. Cox15 is a favorable target because its mature sequence strongly identifies a conserved mitochondrial protein, and EvoDiff-MSA is supplied directly with its orthologous family. The eight tested sequences were also selected from hundreds of candidates using both DR-BERT and MitoFates, making the experiment a test of the full generation-and-prediction pipeline rather than of EvoDiff alone. Moreover, mitochondrial targeting is tested, but the disordered character of the generated sequences is not experimentally established. In any case, I think it would certainly be more convincing if there were other examples, with unrelated proteins or IDR functions. I would appreciate that this is again a step beyond what the authors might be compelled to do, but their claim could be simply more calibrated.

(4) The authors might benefit from explaining the advantages or complementarity of EvoDiff to other property-directed approaches for exploring sequence space. This has been done, for example, by using Bayesian optimization and genetic algorithms to tune properties of IDP condensates (DOI: 10.1021/acs.jpcb.8b03822). In my understanding, these are addressing a different problem from EvoDiff by optimizing sequences explicitly towards physical targets, while EvoDiff is a generative framework that can be used for sampling/inpainting/ etc. Is it clear how these strategies might be plausibly integrated? If so, that would be a relevant point of discussion and a potential advantage for EvoDiff.

Reviewer #1 (Public review):

Summary:

In the manuscript by Francis-Oliveira et al., the authors investigated whether mild adolescent social isolation in female mice produces a latent vulnerability that emerges during the postpartum period as impaired maternal caregiving. They further tested the hypothesis that maternal deficits alter offspring social development. Based on their findings, the authors propose that adolescent psychosocial adversity disrupts maternal behavior and that resulting alterations in offspring social function are mediated through dysfunction of the midcingulate cortex (mCg) to prelimbic cortex (PrL) pathway. They further suggest that exposure to experienced parous females during the postpartum period can rescue maternal behavior and normalize offspring outcomes through restoration of activity in this circuit.

To test these hypotheses, the authors exposed female mice to mild social isolation during late adolescence and subsequently bred those females. Maternal behaviors were assessed postpartum, and offspring were evaluated in adulthood using assays of sociability, social novelty recognition, social odor recognition, anxiety-like behavior, locomotion, and non-social memory. The authors also measured corticosterone levels in control and stress-reared offspring. To test circuit-specific effects, the authors employed chemogenetic activation and inhibition of the mCg→PrL pathway using DREADDs and performed electrophysiological recordings from identified projection neurons. Finally, stressed dams were co-housed with experienced parous females during the postpartum period to determine whether maternal and offspring phenotypes could be rescued, as well as the social deficits previously observed in offspring.

The authors found that adolescent isolation selectively impaired pup-directed maternal behaviors, including nursing, licking, nest building, and pup retrieval, while leaving self-directed behaviors intact. Adult offspring of stressed dams exhibited deficits in sociability, social novelty recognition, and social odor discrimination, but showed no impairments in locomotor activity, anxiety-like behavior, or novel object recognition. Chemogenetic activation of the mCg→PrL pathway restored social behavior in stressed offspring, whereas inhibition of the pathway induced social impairments in controls. Co-housing stressed dams with experienced parous females restored maternal caregiving, normalized offspring social behavior, and rescued reduced firing of mCg→PrL neurons observed in offspring of stressed dams. Collectively, these findings support the authors' model that adolescent psychosocial adversity disrupts maternal caregiving and contributes to offspring social deficits through dysfunction of the mCg→PrL circuit.

Strengths:

The study includes multiple levels of assessment, including behavioral measures, behavioral intervention, the use of DREADDs for circuit manipulation to both test effects of activation versus inhibition on behavioral outcomes as well as physiology experiments. The multilevel approach is a strength.

Weaknesses:

(1) Interpretation of the parous co-housing experiment:

The principal limitation of the study is that the communal housing paradigm does not distinguish rescue of maternal behavior in the stressed dam from direct caregiving provided by the experienced parous female. The authors interpret the rescue experiment as evidence that social support and/or social learning from experienced mothers restores maternal behavior in stressed dams, which in turn normalizes social behavior in offspring. However, pups were continuously housed with both the stressed dam and the parous female from P0-P7, and the parous female had unrestricted access to the pups throughout the intervention period. The parous female was removed only briefly during maternal behavior testing. This design raises an important alternative interpretation. The experienced parous female may have directly provided substantial maternal care to the pups, supplementing or compensating for deficits in the stressed dam. The rescue of offspring phenotypes may reflect care received from the parous female rather than improved caregiving by the stressed dam.

Were caregiving behaviors of the stressed dam and parous female quantified separately during the co-housing period? What proportion of licking, nursing, retrieval, and nest maintenance was performed by each animal? Can the authors exclude the possibility that direct maternal care from the parous female, rather than social learning or social support, accounted for the rescue of offspring outcomes? Without such controls, the central claim that restoration of maternal behavior in the stressed dam mediates normalization of offspring phenotypes is not fully supported.

(2) Specificity of the behavioral phenotype and rescue:

The manuscript repeatedly frames the findings as restoration of offspring outcomes and intergenerational vulnerability. However, the behavioral phenotype appears highly selective and restricted primarily to social behaviors. Offspring exhibited impairments in sociability, social novelty recognition, and social odor discrimination, but showed normal locomotion, anxiety-related behavior, and non-social memory. Thus, the authors should more explicitly acknowledge that maternal adversity produced a domain-specific social phenotype rather than broad behavioral dysfunction. Interestingly, the rescue studies only evaluated a subset of the affected behaviors, making it unclear whether co-housing with parous females restored broader aspects of offspring neural or behavioral function or selectively improved specific social behaviors.

Why was social olfactory recognition not included in the rescue experiments? Why were additional behavioral measures not reported following circuit activation or parous co-housing (e.g., anxiety-like behavior and novel object test) - were these improved in controls by enriched early parenting? Did manipulation of the mCg→PrL pathway or co-housing with parous females influence anxiety-like or depressive-like behaviors despite the absence of baseline group differences?

(3) Strength of the DREADD-mediated causal claims:

The DREADD experiments implicate the mCg→PrL pathway in regulating social behavior; however, several aspects limit the strength of the causal conclusions. Sample sizes were relatively small (n = 6/group). In addition, the variance observed in the DREADD cohorts appears substantially reduced relative to that observed in the non-surgical cohorts. For example, vehicle-treated groups appear more clearly separated than would be expected based on the original behavioral data presented in Figure 2. Can the authors comment on potential reasons for this discrepancy?

Second, although activation and inhibition experiments support involvement of the mCg→PrL pathway in social behavior, the manipulations do not fully recapitulate the broader phenotype observed in stressed offspring. Thus, the data support a role for this pathway but may not justify the stronger conclusion that dysfunction of this circuit alone accounts for the entirety of the offspring phenotype.

The authors argue that altered maternal behavior is causal for social deficits in offspring. However, in the absence of a cross-fostering experiment, the study cannot fully exclude alternative explanations, including direct influences of caregiving by the co-housed parous female, gestational effects, altered maternal physiology during pregnancy, or germline-mediated influences. A cross-fostering design would substantially strengthen the causal interpretation of the findings.

Additionally, clarification of litter effects is important: For example, how many litters contributed to each experimental group? Was litter treated as a random effect in statistical analyses? Were multiple offspring from the same litter analyzed as independent observations? Because maternal behavior is manipulated at the litter level, litter rather than individual offspring may represent the appropriate experimental unit for many analyses.

(4) Integration of corticosterone findings into the mechanistic model:

The corticosterone findings appear somewhat disconnected from the central mechanistic narrative. The authors report elevated corticosterone levels in stressed offspring and suggest that HPA-axis dysregulation may contribute to the observed behavioral phenotype. However, the manuscript does not establish whether corticosterone plays a causal role in the social deficits or instead represents a parallel physiological consequence of altered maternal care.

Were corticosterone levels normalized by co-housing with parous females? Did DREADD-mediated activation of the mCg→PrL pathway normalize corticosterone levels? Could corticosterone manipulation alone drive aspects of the behavioral phenotype independent of circuit manipulation? Do corticosterone levels correlate with the severity of social behavioral impairments? It is difficult to determine whether corticosterone is mechanistically relevant or simply serves as an associated physiological marker. The authors should either more directly integrate the endocrine findings into their mechanistic framework or temper discussion suggesting a causal role for HPA-axis dysfunction.

In summary, this manuscript addresses an important and understudied question concerning how adolescent adversity influences maternal caregiving and offspring social development. The behavioral, circuit, and electrophysiological findings are generally coherent and support a role for the mCg→PrL pathway in mediating offspring social outcomes. However, the strongest mechanistic claim, that social support rescues offspring phenotypes by restoring maternal behavior in stressed dams, is weakened by the communal rearing design, which allows direct caregiving by parous females. Additional clarification regarding caregiver-specific behaviors, litter effects, the role of corticosterone, and the specificity of the DREADD-mediated phenocopy would strengthen the causal interpretation of the findings. Overall, the study is potentially impactful, but several conclusions currently extend beyond what is directly supported by the data.

Reviewer #2 (Public review):

Summary:

Studies in rodents have demonstrated that early life adversity (ELA) impacts many aspects of the exposed offspring's brain and behavior. Work in this field has traditionally focused on how<br /> stress in very early life can impact cognitive and emotion-related behaviors in the ELA-exposed offspring. By contrast, this manuscript focuses on how stress in a slightly later adolescent period can produce latent and intergenerational effects by impacting maternal caregiving from female offspring, as well as social outcomes of the next generation of animals born to ELA-exposed females. Specifically, the manuscript describes that female mice exposed to ELA in the form of social isolation in late adolescence show reduced pup-directed maternal behaviors, while self-directed behaviors remain intact. Offspring reared by these dams in turn show deficits in social behavior, which are linked to reduced activity in an excitatory connection between the medial cingulate cortex (mCg) and prelimbic cortex (PrL). Further, the authors find that social behavior can be rescued by chemogenetic activation of the mCg-PrL pathway in the offspring of ELA-exposed/stressed mice or recapitulated in control mice by chemogenetic inhibition of this connection. Importantly, co-housing ELA-exposed/stressed dams with experienced parous females during the early postpartum period restores pup-directed maternal behaviors in these mice and normalizes offspring social outcomes as well as mCg-PrL activity.

Strengths:

Strengths of the manuscript include the focus on an important and novel question about intergenerational effects of adolescent ELA transmitted via subsequent maternal care, and the use of multiple techniques to link circuit function to behavior, including slice electrophysiology and chemogenetics. While the findings that maternal care can influence offspring behavior and that experienced females can instruct and improve maternal care of less experienced mice are not novel, they add support to this important area of literature.

Weaknesses:

Weaknesses of the paper include the lack of validation that the viral chemogenetic paradigm was appropriately targeted in the brain and impacted the excitability of mCg to PrL projections as anticipated, the use of inappropriate statistical tests that do not account for non-independence of pups from the same litter or cells measured from the same pup or categorical versus continuous data, and the lack of important descriptions of methods or experimental paradigms in several places that altogether make it difficult to judge the rigor of the findings in its current state.

If these weaknesses are addressed, these findings will provide important information about circuit mechanisms underlying intergenerational effects of adolescent stress on social behavior in next-generation offspring.

Reviewer #1 (Public review):

Summary:

The authors addressed how viral-mediated expression of amyloid in medial septum (MS) cholinergic neurons, or broadband amyloid expression, affects the integrity of MS cholinergic neurons in aging mice, as well as cognition, sleep, and hyperexcitability. Using fiber photometry and viral tracing, they show that MS cholinergic neurons are active during wakefulness and REM sleep and that they also project to many different areas. Next, they show that when they express a viral vector carrying APP to encode amyloid beta in MS cholinergic neurons, these neurons express amyloid as they do in a globally expressing APP model (APP-NLGF). They find that amyloid may spread largely following MS projections and that MS die over time presumably due to amyloid expression. They also describe the emergence of memory deficits and reduced REM sleep attributable to loss of MS cholinergic neurons. Lastly, they report a higher burden of epileptiform activity in mice with broadband amyloid expression and the emergence of neuroinflammation in MS, which may be contributing to cell loss and network dysfunction.

Strengths:

(1) New insights on a potential role of MS cholinergic neurons in spreading amyloid.

(2) Use of several different methods to address effects of MS dysfunction in aging mice (AAV, global, lesioning).

(3) Combination of activity-related readouts including fiber photometry, EEG coupled to histological, behavioral, tracing, and neuropathology measures.

(4) Consideration of potential confounds to behavioral measures using proxies of anxiety-related behavior.

Weaknesses:

(1) The authors aim to model the prodromal phase of Alzheimer's disease (AD) neuropathology, which is a very promising area to target therapeutic intervention. While reduction in basal forebrain volume has been reported early in AD, presumably functional changes may be happening much earlier, i.e., even before MS start to degenerate or before REM sleep is reduced. This view has been proposed by human studies showing increased ChAT reactivity in MCI (PMID: 11835370) and evidence in mouse models showing that MS cholinergic neurons may be hyperactive early and degenerate late with distinct implications for memory (PMID: 41717904). Thus, functional changes could be considered before structural changes could be discussed, as earlier ages in this model could reveal such early changes.

(2) One limitation of the tracing methodology (Figure 1) that could be improved is sample size, as only 2 mice have been used. Moreover, it would be interesting to conduct the same tracing experiments in APP mice to see how these projections are affected by amyloid pathology.

(3) Figure 3 measurements included the whole hippocampal formation, but a region-specific analysis would be warranted as the authors discuss specific accumulation areas.

(4) Figure 5 novel object recognition comparisons use a group of 10 sec exploration, which is unclear why. Novel vs familiar comparisons and reporting of discrimination indexes are considered more robust measurements to report.

(5) Interictal spike detection would benefit from more methodological detail and examples of spikes detected. Reference 72 does not seem to detail interictal spike detection. Moreover, when during sleep do these spikes happen? It has been shown that they occur primarily during REM sleep when mice show cholinergic hyperactivity (PMID: 37714307). From panel 7B, it seems they occur during NREM, which may be explained by a diminished drive of cholinergic circuits to drive spikes in these mice (vs REM in younger mice). Thus, a NREM vs REM vs Wake analysis will be insightful.

Reviewer #2 (Public review):

Summary:

In this study, Nollet and colleagues sought to determine whether selective amyloid pathology confined to medial septal (MS) cholinergic neurons is sufficient to recapitulate the prodromal Alzheimer's disease-like phenotypes observed in global AppNL-G-F knock-in mice. To this end, the authors employed a cell-type-specific AAV-mediated approach to selectively express the familial AppNL-G-F allele in MS-ChAT neurons, and subsequently characterized sleep-wake architecture, EEG spectral features, cognitive function, emotional behavior, and histological changes over 13-14 months. By comparing these mice with global AppNL-G-F knock-in mice and with mice in which MS-ChAT neurons were selectively ablated via caspase expression, the authors found that cholinergic cell lesioning recapitulated most disease phenotypes, suggesting that cholinergic loss, rather than amyloid deposition, is a likely driver of these phenotypes.

Strengths:

The study has several notable strengths. First, the experimental design is rigorous and well-controlled, employing three complementary mouse models that enable elegant causal inference. The use of cell-type-specific APP expression is a powerful approach for distinguishing the contributions of MS-ChAT neurons and amyloid deposition. Second, the combination of multiple behavioral assessments, EEG spectral analysis using FOOOF parameterization, and detailed histological quantification strengthens the validity of the conclusions. Third, the finding that caspase-induced cholinergic lesions largely recapitulate the cognitive and REM sleep phenotypes, while amyloid pathology contributes additional features such as epileptiform spikes and astrogliosis, represents an important mechanistic dissection.

Weaknesses:

Despite the overall strength of the study, several limitations warrant consideration. First, the mechanism by which amyloid is "broadcast" from MS-ChAT terminals to distant brain regions remains unclear. The authors do not definitively determine whether the amyloid detected in hippocampal and cortical regions represents released soluble Aβ, transported APP fragments, or amyloid derived from degenerating axons. Second, while the authors demonstrate that MS-ChAT cell loss correlates with cognitive, emotional, and REMS deficits, the causal relationship among these phenomena and the specific circuits involved remains unresolved.

Reviewer #3 (Public review):

Summary:

The central idea of the study is strong and potentially important: that the vulnerability of the cholinergic medial-septal population can account for a substantial fraction of prodromal-like AD phenotypes, thereby shifting part of the mechanistic focus from cortex-centered pathology to subcortical neuromodulatory circuit failure. The work has several notable strengths. The authors combine circuit mapping, calcium photometry, longitudinal EEG/EMG sleep phenotyping, histology, behavior, and a caspase-based lesion comparison to build a multi-level case for medial septal cholinergic involvement in REM Sleep and memory phenotypes. The inclusion of both a focal amyloid model and a partial cholinergic ablation model is especially valuable because it attempts to separate effects of Ch-neuronal loss from effects of amyloid itself.

However, the manuscript has several issues, from manuscript formatting to experimental design, overarching statements, insufficient exclusion of alternative explanations, incomplete quantification details for key histological results, a discussion that often moves beyond the actual data into speculative translational framing, and a discussion that completely ignores the early presence of p-tau in human AD patients and even lacks supplementary materials.

Strengths:

(1) The conceptual premise is compelling: cholinergic basal forebrain vulnerability is a real and important feature of AD, and testing whether selective medial septal cholinergic pathology can drive REM sleep and cognitive phenotypes is mechanistically interesting and clinically relevant.

(2) The experimental framework is broad and generally thoughtful, spanning anatomy, function, sleep architecture, EEG spectral parameterization, behavior, and histopathology.

(3) The projection mapping and photometry provide a useful systems-level introduction, establishing that MSChAT neurons are Wake/REM sleep-active and project strongly to hippocampal and cortical targets before the disease manipulations are introduced.

(4) The MSΔChAT comparison group is valuable because it allows the authors to argue that some phenotypes track with cholinergic loss rather than amyloid per se.

(5) The longitudinal sleep analysis is one of the strongest parts of the study, especially the emphasis on REM sleep quantity and bout architecture over time rather than relying only on an endpoint comparison.

Weaknesses:

(1) The title overreaches in its use of "prodromal phase." In the clinic, "prodromal AD" denotes a biomarker‑positive, pre‑dementia phase with subtle, progressive cognitive decline before widespread neurodegeneration, whereas here the authors demonstrate substantial cholinergic degeneration alongside cognitive impairment, which corresponds to advanced pathology within these models rather than a clinically prodromal stage. Moreover, APP knock‑in mice are amyloid‑centric, lack tau pathology, and don't recapitulate human disease staging; therefore, it would be better to avoid terms used for AD staging in the clinic. A more accurate framing of the title would be "Modeling the prodromal-like phase in an Alzheimer's disease mouse model".

(2) The opening statement in the abstract (line no 22) is overstated. Current evidence supports that changes in REM sleep, slow‑wave sleep disruption, and excessive daytime sleepiness are associated with a higher risk of AD and reflect early involvement of brain regions vulnerable to AD proteinopathy. No study indicates that REM sleep changes per se are a strong predictor on their own. For example, Jin et 2025 studied REM latency in AD and concluded that prolonged REM latency may be a marker of early neurodegeneration (PMID: 39868572). Thus, the opening statements need to be modified.

(3) Line 63: The current phrasing of neuromodulators being also essential for orchestrating sleep/wake states is very simplistic. Sleep/wake regulation is a highly complex process involving several interacting neurotransmitters and neuromodulatory systems. I recommend revising this sentence to reflect the broader, multi‑system nature of sleep/wake control.

(4) Line 64: "ACh is required for the generation of REMS" is incomplete. The sentence implies REM sleep generation depends exclusively on ACh. Instead, the sentence must emphasize that ACh is a crucial component of a broader REM sleep circuitry and explain why it is critical for REM sleep.

(5) Line 65: The sentence "Importantly, reductions and alterations in REMS have emerged as strong predictors of clinical AD onset" (Reference 37) is an overstatement of the evidence; Peas et al. 2017 analyzed a dementia cohort that included AD cases and concluded: "Despite contemporary interest in slow-wave sleep and dementia pathology, our findings implicate REM sleep mechanisms as predictors of clinical dementia." The authors should rephrase this to reflect that the study examined REM sleep changes in a mixed dementia population with AD, rather than to establish REM alterations as strong, standalone predictors of AD onset.

(6) Lines 73-75 address human Alzheimer's studies and state that basal BF-Ch neurons are vulnerable to Aβ but largely omit the well-established contribution of early tau pathology. In human AD patients, p-tau accumulation in BF is an early event (Braak I-II) and is closely associated with BF-Ch neuronal loss and BF atrophy and has been documented extensively. By relying almost exclusively on Aβ-centric framing, the current text risks implying that BF-Ch degeneration is solely amyloid-driven, which is not accurate. Even though the mouse model used here is "amyloid-heavy" and lacks tau pathology, the introduction should acknowledge the role of p-tau (especially when the paragraph contextualizes human studies) and clarify that in humans, BF-Ch vulnerability reflects converging amyloid and tau insults, so that readers do not infer a purely amyloid-dependent mechanism from the way the background is presented.

(7) Line 92: and elsewhere in the manuscript, I recommend avoiding the term "prodromal phase" and instead using the phrase "prodromal-like phase in an AD mouse model". The authors should be more precise in describing the disease stage in animal models that don't recapitulate human disease staging and ensure that clinical staging terminology is specific to human studies.

(8) Age and duration of pathology are major concerns. The different models are not adequately matched for amyloid exposure duration and age at testing. Age is the strongest risk factor for AD, and varying both chronological age and time under pathology across groups is a major design flaw. In MSChAT-AppNL-G-F/GFP mice, AAV injection was delivered at 11-13 weeks of age, and animals were sacrificed at 13-14 months post-injection (roughly 15-16 months old), whereas AppNL-G-F/NL-G-F knock-in mice and APPWT were 13-14 months old at the time of termination. Thereby, there is a difference in the duration of Aβ exposure across models. This mismatch directly weakens comparisons such as the lower epileptiform spike counts in MSChAT-AppNL-G-F versus AppNL-G-F/NL-G-F mice, because differences could simply reflect shorter cumulative pathology exposure rather than a genuinely weaker circuit-specific effect.

The same issue affects the internal control logic of the MSΔChAT model, which is intended to isolate cholinergic neuron loss from amyloid aggregation. For this comparison to be clean, ages and exposure durations should be aligned as closely as possible. Instead, MSΔChAT mice are tested earlier than the AppNL-G-F/NL-G-F and MSChAT-AppNL-G-F/MSChAT-GFP cohorts, introducing a 4 to 7-month age gap that complicates attribution of phenotypic differences solely to cholinergic loss versus amyloid pathology.

Finally, the absence of sham-operated controls is a concern, as it prevents separating the effects of the surgical procedure and AAV delivery from those of amyloid expression or cholinergic ablation.

(9) Line 115 through 117: The text cites Figure 2D, but does not refer to Figure 2C for the statement "their phenotypes were then compared in detail with MSChAT-AppNL-G-F and AppNL-G-F/NL-G-F global knock-in mice that were aged at the same time". Figure 2C depicts D54D2 amyloid staining in MSChAT-GFP vs MSChAT-AppNL-G-F mice. For clarity and consistency, I suggest adding a Figure 2C notation to this sentence (e.g., "Figures 2A, 2C").

(10) In Figure 1C-D, the authors map MSChAT projection targets across a wide range of brain areas, including hippocampal subfields, mPFC, primary cortices, entorhinal cortex, olfactory bulb, thalamus, anterior hypothalamus, amygdala, and medial habenula, and identify several of these as substrates through which MSChAT activity could influence REM sleep and cognition. However, the lateral hypothalamic area (LHA) is conspicuously absent from both the listed projection targets and the tracing panels shown in Figure 1D, despite the anterior hypothalamus being reported as an innervated region.

This omission is notable given that LHA-MCH neurons are among the best-established REM-sleep-promoting neurons, and the authors themselves cite prior work implicating LHA-MCH neurons in the AppNL-G-F REM sleep phenotype (ref. 49, 107; line 403) as an alternative cell-circuit candidate, a claim they explicitly try to weigh against their own MSChAT-centered model in the discussion.

a) The MSChAT neurons are reported to be REM sleep- and wake-active (Figure 1A-B), the same vigilance-state profile as LHA-MCH neurons,<br /> b) The Discussion directly engages with LHA-MCH neurons as a competing/complementary REM sleep-generating mechanism, and<br /> c) The reported anterior hypothalamus innervation (Figure 3C) raises the question of whether MSChAT axons specifically innervate LHA, and whether any projections specifically to LHA or LHA-specific amyloid deposition were examined. Clarifying this would help position the proposed MSChAT-hippocampal circuit mechanism relative to the well-established LHA-MCH REM sleep node.

(11) Line 125: "13- to 14-month-old MSChAT-AppNL-G-F mice immunohistochemical analyses employing the amyloid-specific antibodies....", in the methods section (Line 652) the authors mention MSChAT-AppNL-G-F and MSChAT-GFP mice were perfused 13-14 months after AAV injection (age at the time of injection was 11-13 weeks of age). This leaves the question of how they have 13- to 14-month-old MSChAT-AppNL-G-F mice available to study Amyloid-β load.

(12) Line 174-175: As currently written, the sentence could be read as both wild-type and homozygous AppNL-G-F/NL-G-F mice received AAV injections and were then aged 13-14 months post‑injection. In fact, the Methods clearly state that knock‑in mice are simply aged from birth without any AAV manipulation. The sentence should be rephrased to avoid suggesting that global APP knock‑in animals are part of the AAV‑injected cohorts.

(13) Lines 182-183, 196-197, and 209 refer to "Supplementary information" and imply that detailed behavioral data and analyses are provided in that section. However, in the current submission, the supplementary material consists only of Figures S1-S7 (Amyloid marker and cerebral vasculature, Aβ in hippocampus, GABA and glutamatergic neurotransmission, and sleep/wake parameters) and does not include supplementary figures or tables for the behavioral assays described in the main text. This discrepancy makes it impossible to verify the full behavioral dataset and the analyses referred to in the results section. The authors should carefully check the submission package and ensure that all referenced supplementary figures, tables, and detailed behavioral results are included and appropriately labeled.

(14) The lack of details for histological quantification is a major concern for a manuscript in which major conclusions hinge on Aβ load and MS-Ch neuronal counts. The histological quantification section is severely under-specified. The authors describe a 23% MSChAT loss, differences in regional Aβ burden, and a vascular association; however, the methods section is strangely silent about the quantification pipeline. For Aβ quantification, it is not clear whether "load" reflects percent positive area, plaque counts, or another metric; which Fiji thresholding algorithm(s) were used; how ROIs were defined; how staining batch effects were controlled; and how autofluorescence was normalized. For neuronal counts, the strategy for identifying and counting ChAT-positive neurons, normalization, and blinding are not described. There are no details on section spacing, axis of counting, the number of sections counted per animal, or whether both hemispheres were analyzed. Given that the reported differences are modest and central to the main claims, a more detailed and rigorous description of the image-analysis pipeline is essential.

(15) Statistical annotations in figures: There is inconsistency in how statistical significance is indicated across the figures. For example, in Figure 5C, the significance between MSΔChAT and AAV‑Aβ⁻ is indicated by a connecting bracket (**), whereas the comparison between AAV‑Aβ⁻ and AAV‑Aβ⁺ is marked by asterisks (***) placed above AAV‑Aβ⁺. In addition, the single asterisk above KI-Aβ⁺ does not clearly specify which pairwise comparison it refers to (e.g., AAV‑Aβ⁻ vs WT‑Aβ⁻ or another contrast). This heterogeneity makes it difficult to decipher exactly which group comparisons have been tested and found significant. The notation should be standardized and explicitly linked to the corresponding pairwise comparisons (for example, by using consistent brackets/lines and specifying all contrasts in the figure legend). Figures must be self-explanatory.

(16) Figure 5D statistical notation and group comparisons: The statistical markings in Figure 5D do not seem to match the results text and are difficult to interpret. The authors state that both MSΔChAT and AAV‑Aβ⁺ mice lack a preference for the novel object compared with AAV‑Aβ⁻ controls, yet the figure does not clearly indicate significance for MSΔChAT versus AAV‑Aβ⁻, and the notation over AAV‑Aβ⁺ is ambiguous. As a result, it is unclear which group differences are being tested and reported. It would be preferable to use the standard convention of placing significance annotations directly over the experimental groups (e.g., AAV‑Aβ⁺, KI-Aβ⁺⁺, MSΔChAT) or use notation above brackets to ensure that the figure labels are fully consistent with the statistical statements in the results.

(17) The discussion contains many compelling ideas, but it needs pruning and recalibration. The best discussion points are those linking the lesion comparison to REM sleep/cognitive outcomes and those situating MS cholinergic neurons within broader REM sleep circuitry. The least convincing sections are those implying disease-stage equivalence, prion-like spread, and direct therapeutic implications without sufficient evidentiary support.

(18) Line 448: The authors discussing reduced anxiety-like behavior in their model corroborates with the 3xTg mouse model (Ref: 116). Interestingly, they don't consider or include reports of anxiety-like disorders from human cohort studies that indicate the prevalence of higher anxiety and its association with preclinical and prodromal AD stages (SCD, MCI) and progression of AD. This apparent contradiction with the human literature is not discussed in the discussion section. The authors should explicitly address how their anxiolytic-like phenotype fits with clinical data (e.g., species differences, task specificity, disease stage, or model limitations) and clarify whether they view this as a limitation of the model or as evidence for a more complex relationship between amyloid, cholinergic dysfunction, and emotional behavior.

(19) Line 654 states, "Comparable durations of amyloid pathology," but this is not fully substantiated, as the onset and progression of amyloid in the AAV-driven MSChAT-AppNL-G-F model versus the global AppNL-G-F knock-in model are not described. The data support comparison at a similar late-stage amyloid burden, but not necessarily equal duration of pathology.

Reviewer #1 (Public review):

Summary:

This paper from Bardossy et al. explores whether viral macrodomains in dual-host viruses contribute to infection in the mosquito vector. Using the CHIKV Caribbean strain, the authors generated nsP3 macrodomain catalytic site mutants (N24A or N24D) and identified a compensatory mutation site at position 31 during virus propagation in Vero cells. They then assessed the impact of these mutations on viral growth kinetics in A549 (human) and U4.4 (Ae albopictus cells), as well as on infectivity and dissemination in vivo in Ae. aegypti and Ae. albopictus. Biochemical and structural analyses of recombinant macrodomain proteins (alone or in combination) revealed effects on stability, catalytic activity, and ADP-ribose binding. Overall, the study demonstrates that CHIKV macrodomain catalytic activity plays an important role in virus infectivity and dissemination within the mosquito vector.

Strengths:

A complete set of experimental approaches spanning generation of recombinant viruses, in vitro characterization, in vivo studies in mosquitoes, and detailed biochemical and structural characterization.

Weaknesses:

(1) The sequence analysis of the generated stocks revealed the emergence of a second-site mutation at position 31 of the nsP3 macrodomain when (N24A or N24D) CHIKV mutants were generated on Vero cells. However, it is not clear from the text or the experimental design how many independent replicates were performed. Based on the current description, it appears this was done only once, which raises the question of whether mutations at position 31 represent a reproducible outcome of infection. This is particularly important because experiments in A549 cells did not reveal emergence of mutations at position 31. To strengthen this finding, the experiment should be performed at least three independent times.

(2) Based on the primer information used to generate amplicons for sequencing, the amplicons evaluated do not span the full nsP3 gene as stated in the text (Line 105). Instead, they cover only the first 119 amino acids of the macrodomain (160 aa long). Thus, the current data do not rule out the emergence of other compensatory mutations elsewhere in the nsP3 macrodomain or in the full-length protein. Additional sequencing is recommended, or the text should clearly state that only a portion of the macrodomain was sequenced.

(3) Another key question is whether this is a specific feature of the Caribbean strain or a feature conserved across different CHIKV lineages.

(4) The use of A549 cells (interferon-competent) to study CHIKV infection is somewhat surprising, as the current literature indicates that this cell line is not efficiently infected by Asian or ECSA lineages of CHIKV (PMID: 17604450) unless the Mxra8 receptor is overexpressed (PMID: 29769725) or IFN signaling is inhibited (PMID: 31682641). The data presented here are compelling and suggest specific features of the Caribbean strain that enable efficient infection of this cell line (Do the authors observe detectable cytopathic effect (CPE) in CHIKV-infected A549 cells?).

However, to further support the authors' claim related to human immunocompetent cells, it would be important to demonstrate the phenotype in an additional interferon-competent cell line that is well-established as highly permissive to CHIKV, such as human fibroblasts.

(5) To fully support the conclusion stated in lines 234- 237, the authors should fully sequence the virus stock used to demonstrate that no additional mutations (beyond N24D-D31H/N) are present that could contribute to the enhanced dissemination phenotype. This is especially important if the experiment was performed with only one stock of virus, given justified gain-of-function concerns.

(6) The authors did not assess transmission but transmission potential (only viral dissemination to heads was measured). The sentence at line 360 should be modified to accurately reflect the data-supported conclusion.

Reviewer #2 (Public review):

Summary:

To address how the CHIKV macrodomain contributes to replication dynamics in mammalian and insect hosts, the authors initially created two separate mutations in the highly conserved N24 residue, which is known to be critical for the CHIKV macrodomain's ability to erase ADP-ribose from target proteins. Interestingly, they could not produce a virus with a mutation in this residue without second-site mutations in an aspartic acid residue nearby (D31). However, when tested biochemically, these second-site mutations did not enhance the enzymatic activity of the protein, indicating that other enzyme dynamics, such as substrate binding, may be impacting these mutations. Mutations at this residue allowed the CHIKV to replicate in Vero cells and in mosquito cells, but they replicated poorly in IFN-competent human cells, indicating clear IFN-specific impacts on these viruses. Interestingly, they found unique impacts on virus dissemination and replication in live mosquitoes. While the N24A/D31N virus did poorly in vivo in all accounts, the N24D/D31H/N virus tended to infect both the bodies and heads of the mosquitoes better than the WT virus, though titers were reduced. The authors claimed, based on a DSF assay, that there were no real differences in ADP-ribose binding and thus suggested that these differences could be due to changes in substrate specificity, as the D31 residue resides in the substrate exit path, potentially tuning the virus to unique substrates in different species. The authors also produced crystal structures of the mutants to demonstrate the changes in the binding pocket caused by these mutations.

Strengths:

The authors have done a rigorous job of evaluating CHIKV macrodomain mutant viruses and the proteins' biochemical activities. The use of live mosquitoes is highly unique and provides important insights into the importance of the macrodomain in different species.

Weaknesses:

It is not clear if the interpretation of the ADP-ribose binding data is correct. It appears there are notable differences that could explain the results, though the authors chose to minimize the impact that these differences had on the results. The N24D-D31H/N proteins had at least a 1C degree difference in the thermal shift assay when compared to the N24A/D31N, single D31 mutants, and WT proteins, which is likely significant and could explain the dichotomous results between the two viruses in mosquito cells. Even the single N24D mutant had enhanced binding compared to the WT protein. Furthermore, as this virus has no enzymatic activity, one could hypothesize that enhanced binding to a substrate that is normally cleaved by the protein could certainly lead to alterations in phenotypic effects, whether good or bad. The authors should test the binding activity in a separate assay, such as an ITC assay, to determine if there are, in fact, binding differences or not. Having said this, it is likely that the impacts of these mutations on replication and transmission in human and mosquito cells are multi-factorial and could include both enhanced binding with altered substrate specificity amongst other activities.

Additionally, as both mutants had no detectable enzymatic activity but had quite different phenotypes in mosquitoes, I don't agree with the title stating that catalytic activity modulates dissemination and transmission potential in mosquitoes. It seems more likely that alterations in binding activity or substrate recognition (even suggested by the authors) impact these phenotypes in mosquitoes.

Reviewer #3 (Public review):

Summary:

The authors investigated the role of the nsP3 macrodomain catalytic activity in the replication and transmission of CHIKV in mosquito vectors. The conserved dual-host alphavirus catalytic site N24 has previously been shown to be essential for ADP-ribosylhydrolase activity. Despite this, mosquito-specific alphaviruses do not share this catalytic site. To assess whether the macrodomain catalytic activity of a dual-host virus was essential in insect hosts, the authors targeted the N24 site to abolish catalysis while maintaining binding capacity. The loss of ADP-ribosylation led to the emergence of compensatory mutations at site D31 that impact viral infectivity, dissemination, and transmission in Aedes sp. mosquitoes in vivo. The conclusions are well supported by the results and provide insight into the importance of nsP3 macrodomain activity in the mosquito vector, which hasn't been explored before.

Strengths:

The main strength of this study is the use of Aedes sp. mosquito models to investigate the selective pressure of macrodomain mutations in vivo. The functional characterization as well as the structural analysis of the mutants provide supporting evidence of a potential role of the compensatory mutations at site D31 in substrate recognition.

Weaknesses:

A considerable part of this study relies on the use of N24 mutant viral stocks generated in Vero cells, which yields an additional mutation at site 31 and consequently doesn't allow the authors to properly dissect the effect of mutation of N24 and D31 independently. It would be recommended to generate stocks with individual mutations in both A549 and U4.4 cells, pooling and concentrating them if needed. Replication of the N24A mutant in A549 cells does not lead to mutation at residue 31. Yet surprisingly, there is no reversion from N back to D at site 31 when the double mutant Vero stocks are passaged in A549. Since they are double mutants, it isn't possible to assess whether the defects in the growth of mutants N24A/T-D31N and N24D-D31H/N compared to WT are due to site 24 or 31, or both (Figure 2, panel c). Even though the authors emphasize that the compensatory mutation could have additional roles that impact viral infectivity and transmission in mosquito cells, it would strengthen the work to show that these mutations would spontaneously appear in stocks generated directly in mosquito cells. As a corollary, is it known whether insect-specific alphaviruses that lack macrodomain catalytic activity have corresponding mutations at site 31?

Additionally, there is a lack of consistency in the prevalence of WT virus at days 5 and 7 in in vivo experiments with Ae. albopictus and Ae. aegypti (Figure 3 and Supplementary Figure 2). This raises concern about the reproducibility of these experiments.

The inability to tease apart the roles of N24 and D31 in mosquito hosts partially prevented the authors from fully achieving their aims, but the work is nonetheless of interest to the field and suggests that more work is necessary to fully understand the role of the nsP3 macrodomain and its catalytic activity in the two disparate but obligate hosts for CHIKV and other dual-host alphaviruses.

Reviewer #1 (Public review):

Summary:

The study identifies and characterizes a set of amino acid states that make the protein robust to other mutations, to the point of being able to compensate mutations that render wildtype proteins entirely non-functional. The study uses a previously published dataset and uses it to find and study such super-compensators. It then analyzes the biophysics and fitness landscape structure of what may be behind the compensation, identifying stability as an important parameter that, nevertheless, is not sufficient to explain all of the compensatory effect. These findings have important implications for our understanding of protein evolution, with these super-compensators possibly acting in a role of "permissive mutations" and opening up evolutionary trajectories that may be closed without them. Perhaps the identification of such super-compensator substitutions can be incorporated into various protein design approaches.

Strengths:

The paper presents a compelling case with a rigorous analysis of the expected error rates of observation. While not unique, the current state-of-the-art in the field typically does include experimental error rate estimation like this work. The paper also does a good job in exploring the issue, including looking at plausible biophysical basis of super-compensators.

Weaknesses:

The paper lacks rigor in talking about evolutionary-related issues of the state of the fitness landscape. As an example, the paper mentions that these super-compensators flatten the landscape. While I understand where this is coming from, I think that the fitness landscape in this context is a static entity and cannot be flattened or otherwise altered. A much more accurate description is that a sequence with a super-compensator is located in a flatter-than-expected segment of the fitness landscape, or on a flat fitness ridge. These issues are more semantic in nature, and while the manuscript would benefit from it being shown to an expert in molecular evolution or fitness landscapes, this issue does not take away from the importance of the results.

Reviewer #2 (Public review):

Summary:

This manuscript presents an interesting and conceptually valuable analysis of compensatory evolution using a large combinatorial deep-mutational-scanning dataset for yeast His3p.

Strengths:

I particularly like the identification of "super compensatory" substitutions that improve fitness across diverse genetic backgrounds and apparently reduce the sensitivity of the local fitness landscape to subsequent mutations. The work connects epistasis, protein stability, mutational robustness, and evolvability in a clear and potentially broadly relevant manner.<br /> The authors provide several complementary lines of evidence in support of this central conclusion. In particular, the new experimental validation of S189A is an important strength because it directly demonstrates that a predicted super compensator can buffer the effects of diverse deleterious substitutions, while analyses of additional DMS datasets from other proteins and assay systems suggest that the phenomenon is not restricted to the original His3p landscape.

Weaknesses:

The structural analysis currently relies primarily on correlations with RSA, weighted contact number, conservation, and Rosetta-predicted changes in folding or binding energy. For super compensators, the mechanistic evidence is largely limited to predicted stabilization and individual examples, such as the proposed salt bridge between 110D and R112. I believe that the newly developed structure-aware deep-learning approaches could provide useful information on the mechanism of super compensators. For example, an inverse-folding model such as ESM-IF1 could score complete multi-mutant sequences conditioned on the His3p backbone and test whether adding a super compensator restores sequence-structure compatibility across backgrounds. More recent multimodal mutation-effect or stability models could similarly be used to cross-check the Rosetta results, including models that explicitly support combinatorial mutations. I would not recommend simply comparing AlphaFold confidence scores between mutants, because current structure predictors are not necessarily sensitive to subtle mutation-induced energetic or conformational changes.

The manuscript states that the pipeline was applied to 217 ProteinGym datasets and concludes that super compensators are broadly distributed across proteins and assays. However, this central generalization is described in only a few sentences and is largely relegated to Figure S7. The Methods do not explain which datasets contained sufficient combinatorial mutants to calculate compensatory ability or buffering, how many genotype pairs or quadruplets were available per substitution, or how differences in assay scale and library design were handled. This point requires clarification because supercompensation is inherently a background-dependent property and cannot be established from single-mutant measurements alone. ProteinGym is widely used as a substitution-effect benchmark, and many of its constituent assays primarily contain single substitutions; for example, an analysis of an earlier ProteinGym collection reported that 76 of 87 assays contained only single substitutions. It is therefore unclear how the same compensatory-interaction pipeline could be applied uniformly to all 217 datasets.

The analysis of 335 His3p orthologs in Discussion is potentially very interesting, but co-occurrence between super compensators and putatively deleterious amino-acid states does not by itself demonstrate evolutionary compensation. Closely related species share substitutions through common ancestry, and both states could be associated with a particular lineage or ecological context. A tree-aware analysis would considerably strengthen this result. The authors could reconstruct ancestral states and ask whether acquisition of a super compensator tends to precede or accompany otherwise deleterious substitutions. Alternatively, they could use phylogenetically informed permutations that preserve substitution frequencies and shared ancestry.

Reviewer #3 (Public review):

The manuscript by Jiang and co-authors presents an analysis of experimental measurements (about 400k variants) from a deep mutational scan of the HIS3 enzyme. The authors assess the ability of a genotype to be "rescued" and show that this depends on mutation sites (in particular their solvent accessibility) and mutation effects (should be mild on folding stability or binding affinity). They further identify a set of super-compensatory mutations, and their results suggest that these mutations flatten the fitness landscape.

This finding is interesting and likely of interest to a broad community. The analysis seems sound.

However, I have a number of major concerns regarding the presentation and positioning of the work.

(1) It would improve the manuscript to clarify the present contribution with respect to a previous study by the same authors, namely Pokusaeva et al. 2019. Did the authors apply the same protocol to generate a new library of mutants, or did they re-analyse an already published library? If the library is not new, ambiguous sentences like "Nevertheless, to our knowledge, the His3p library remains one of the largest and most comprehensive resources that contains multi-site mutants" should be reformulated.

(2) Pokusaeva et al. 2019 is cited for the library and also for the deep neural network. It would be beneficial to briefly describe the architecture, the inputs and outputs, and the training procedure. Was the network trained on the current library? What is the purpose of this network? It looks more like an additive linear model (except for the global sigmoid) than a deep neural network. How does it relate to global epistasis models? The sigmoid function is designed to capture plateauing effects; doesn't that introduce some circularity issue in the reasoning?

(3) Are the super-compensatory mutations observed (conserved) across evolution? Beyond the fact that they are accompanied by mildly deleterious mutations in natural sequences. Can we predict them with variant effect predictors?

(4) The AAindex mention should be accompanied by a citation.

(5) Equations should be numbered. WCN formula seems to contain misformatting issues.

(6) A more explicit description of the structural data analysed (which PDB entry?) should be provided.

(7) I believe the citation Van Cleve and Weissman 2015 for the ProteinGym benchmark is incorrect. Additionally, is the Rosetta citation adequate?

(8) How is the definition of rescueability sensitive to the threshold choice?

Reviewer #1 (Public review):

A previous study from the same team (McDougle & Taylor, 2019) demonstrated that explicit strategies during visuomotor adaptation can be dissociated into retrieval-based and algorithmic strategies. However, whether these distinct forms of explicit processing differentially influence implicit recalibration has remained unresolved, with previous studies providing evidence both for relatively independent explicit and implicit processes and for interactions between them. This study addresses this question through a series of experiments that used Critical and Non-Critical targets to induce distinct strategic modes while maintaining comparable adaptation at the Critical target.

Experiment 1 replicated previous findings showing broader implicit generalization under algorithmic strategies. However, this broader generalization could be explained by spillover effects arising from adaptation at the Non-Critical targets. Experiment 2 was designed to reduce such spillover effects by increasing the spatial separation between the Critical and Non-Critical targets. Although broader generalization was still observed in the algorithmic condition, this effect was interpreted as reflecting greater variability in reaching behavior at the Critical target. Finally, Experiment 3 introduced additional controls using an error-clamp paradigm, and the difference in generalization width between the two strategies largely disappeared.

Together, these findings led the authors to conclude that implicit recalibration is relatively insensitive to the type of explicit strategy employed and is primarily shaped by the statistics of the movement plans on which learning occurs.

The experimental design using Critical and Non-Critical targets is particularly interesting and represents a creative approach to manipulating strategy use. Reaction times were generally longer in the algorithmic group, even at the Critical target, suggesting that the manipulation was at least partially successful in biasing participants toward algorithmic versus retrieval-based strategies. The results that the implicit recalibration is independent of the explicit strategy (how you aim) but depends on the aiming point by the explicit strategies (where you aim) are basically reasonable.

I would like the authors to clarify two points.

First, how reasonable is it to infer the use of distinct explicit strategies primarily from reaction time differences? While longer reaction times in the algorithmic group are consistent with greater computational demands, it remains unclear whether the longer reaction times observed at the Critical target necessarily reflect different strategy implementations at that location. In particular, could the increased cognitive demands associated with the Non-Critical targets in the algorithmic condition have carried over to the Critical target, thereby prolonging reaction times without implying qualitatively different strategies at the Critical target itself?

Second, the interpretation of Experiment 3 is not entirely clear to me. The manuscript argues that the algorithmic group continued to exhibit greater reaching variability than the retrieval group. If this variability indeed reflects greater variability in movement plans, one might expect a broader implicit generalization function in the algorithmic group. However, the generalization widths were comparable between groups. Could this result instead suggest that the implicit recalibration process itself generalized more narrowly in the algorithmic group, thereby offsetting the broader distribution of movement plans? More generally, I would appreciate further clarification regarding the relationship between reaching variability, movement-plan variability, and the resulting width of the implicit generalization function.

Reviewer #2 (Public review):

This study addresses an important question in motor learning: whether algorithmic versus retrieval-based explicit strategies differentially shape implicit recalibration. The progressive experimental logic across three experiments is commendable, and the plan-based generalization account is a plausible and interesting interpretation. However, several methodological concerns limit the strength of the conclusions. I recommend the authors temper their claims accordingly, in the results/discussion section.

Concerns

(1) The retrieval group received 5 pre-exposure trials before main training began, which the algorithmic group did not. Faster RTs in the retrieval group could therefore reflect task familiarity from extra practice rather than efficient memory retrieval per se. I might have missed this, but I did not see performance data from these pre-exposure trials. The early training advantage in the retrieval group might be confounded with the 5 pre-exposure trials they received. Unless there is a direct comparison between the pre-exposure trials for the caching group and the first 5 trials of the algorithmic group, the claim that "storing and retrieving a memory from a short-term memory cache confers more rapid performance improvements than executing an algorithmic strategy" seems somewhat unwarranted.

The algorithmic group also visited the critical target approximately 40% of trials across 356 trials (about 140 trials?). McDougle & Taylor (2019) showed that 300 trials of practice with 2 targets is enough transition from algorithmic to caching strategies. It seems likely that the number of visits to the critical target here was sufficient for caching to develop in the algorithmic condition. This concern about caching in the algorithmic group has implications for the implicit recalibration measurements. As I understand it, the 7 exclusion blocks were distributed throughout training, and so, implicit recalibration was measured across both early and late practice. If caching emerged in the algorithmic group during late practice, then the generalization functions - averaged across all 7 exclusion blocks - conflate early algorithmic strategy and later caching. The broader generalization function observed in the algorithmic group may therefore be driven primarily by early exclusion blocks, while later exclusion blocks may increasingly resemble the retrieval group as caching develops. This is testable in the data: if generalization breadth in the algorithmic group narrows across the 7 exclusion blocks while remaining stable in the retrieval group, that would be consistent with a strategy transition occurring during training. The authors should either report exclusion block-by-block generalization functions separately for each group, or acknowledge that the averaged generalization functions may obscure a strategy transition in the algorithmic group.

(2) The error-clamp paradigm in Experiment 3 introduces two problems. First, it breaks the relationship between planned movement direction and feedback of movement direction, likely reducing the sense of agency over movement feedback (indeed, typical error clamp study instructions tell participants to ignore the movement feedback).

Reduced agency may itself suppress differences between algorithmic and caching conditions. First, if strategy type exerts its influence on implicit recalibration via the explicit plan - as the plan-based generalization account predicts - then severing the link between intended movement and feedback might close off the channel through which strategy could shape the implicit system, regardless of which strategy is used. Second, reduced agency could modify the explicit strategies themselves. For caching, the stimulus-response association might be reinforced by a consistent relationship between intended movement and observed outcome; the clamped feedback may make it more difficult to reinforce the cached response, weakening the stimulus-response association. For the algorithmic strategy, effortful mental rotation may depend on the perception that the computation meaningfully determines the outcome; as participants understand that clamped feedback does not depend on their behavior (although yes, the text-based "Excellent/Good Move feedback) does depend on their behavior, they may engage in somewhat less complete mental rotation. Both possibilities could contribute to convergence between groups in generalization. It is noted that the preserved RT difference between groups in Experiment 3 partially argues against a loss of effort under the algorithmic condition, but it does not rule out weakened formation of stimulation-response associations during caching.

Reviewer #3 (Public review):

Summary:

This manuscript asks whether two forms of explicit strategy use in visuomotor adaptation, i.e., algorithmic mental rotation and retrieval of a cached aiming solution, differentially influence implicit recalibration. The question is relevant because much prior work treats explicit strategy as a unitary process, whereas the algorithmic/retrieval distinction is theoretically meaningful and grounded in cognitive theory. Across three experiments, the authors report that algorithmic strategy conditions initially produced broader fitted implicit generalization functions than retrieval conditions, but that this difference was reduced or eliminated when reach variability and sensory prediction errors were more tightly controlled.

Strengths:

The paper is clearly written, theoretically well-motivated, and employs a commendably transparent and progressive experimental logic. The three-experiment structure, in which confounds are systematically identified and addressed, represents a strong model of cumulative experimental design (I will certainly use it in teaching courses on experimental methods):

Experiment 1 establishes an apparent difference in implicit generalization breadth. Experiment 2 attempts to reduce error spillover from Non-Critical targets by increasing angular separation and using delayed endpoint feedback. Experiment 3 uses an error-clamp design to decouple variable reaching from error feedback. This sequence is appropriate for testing whether the initial difference reflects a strategy-dependent change in implicit recalibration or instead follows from the distribution of movement plans and error exposure. The authors also provide reaction-time and performance data that are broadly consistent with the intended distinction between algorithmic and retrieval-like task performance.

Weaknesses:

The evidence does not support the strongest claims made in the manuscript, namely that algorithmic and retrieval strategies generally do not reshape implicit recalibration.

In general, I am skeptical of the authors' interpretation of null results. Several central conclusions depend on non-significant group differences, especially in Experiment 3. Non-significant tests are repeatedly treated as evidence that groups are equivalent or that confounds are absent (e.g., implicit recalibration magnitude (Algorithmic: 11.43 {plus minus} 6.43{degree sign}; Retrieval: 15.49 {plus minus} 8.99{degree sign}; t(38) = −1.65, p = .11), adaptation level before Exclusion probes (F(1,256) = 3.04, p = .08) and Exclusion RT differences (F(1,266) = 3.15, p = .08), whereas a modest model-dependent breadth effect (bootstrap p = .02) is treated as meaningful (for more on the model-dependent breadth effect, see below).

Without confidence intervals, equivalence tests, or Bayesian analyses, I think that the authors' interpretations comprise an inferential gap. A failure to find a significant difference is not equivalent to evidence of equivalence, particularly given that the implicit recalibration signal gets progressively attenuated across experiments (Experiment 1: ~16-17{degree sign}; Experiment 2: ~11-15{degree sign}; Experiment 3: ~7-8{degree sign}). With a substantially diminished signal in Experiment 3, the null result could partly reflect reduced statistical sensitivity rather than true equivalence.

My main technical concern is the analysis of generalization breadth already alluded to. The central claims rely on group-level Gaussian fits to only seven Exclusion probe locations spanning −45{degree sign} to +45{degree sign} around the Critical target. In several cases, the fitted centers and widths are poorly constrained by the sampled range. For example, in Experiment 2 the algorithmic group's fitted center is shifted to approximately 29{degree sign}, meaning that the probe range samples the function asymmetrically relative to its own peak. In Experiment 3, fitted centers are near or outside the sampled range, while estimated widths are very broad. Under these conditions, the width parameter may partly reflect extrapolation or parameter trade-offs between center, amplitude, and width rather than a genuine difference in generalization breadth.

Lastly, I think that the authors' use of an error-clamp paradigm is, from an experimental point of view, quite elegant. By controlling the sensory prediction error independently of reach direction, they can isolate implicit recalibration from the confounds identified in Experiments 1 and 2. However, I see a fundamental problem or question concerning construct validity here: In Experiments 1 and 2, the algorithmic strategy was operationalized as participants computing a counterrotated aiming direction in response to a visible cursor rotation. This is a naturalistic context where mental rotation is both required and meaningfully connected to task success. In Experiment 3, however, there is no visuomotor rotation to compensate for. The error-clamp renders the cursor feedback task-irrelevant. Instead, participants are instructed via text commands (e.g., "move towards 45{degree sign}") to reach invisible locations, rendering the "algorithmic strategy" in this context essentially an instructed spatial navigation toward arbitrary angular locations, not genuine visuomotor mental rotation driven by an error signal.

To put it differently, are we sure that the cognitive process engaged by the algorithmic group in Experiment 3 is the same as the algorithmic mental rotation strategy in Experiments 1 and 2? If not, then the null result in Experiment 3 may not speak to the original question about how algorithmic strategies interact with implicit recalibration after all. Instead, it may reflect the absence of a genuine strategy manipulation.

To their credit, the authors report a compelling RT dissociation that mirrors Experiments 1 and 2: The algorithmic group shows slower RT, which is decreasing over training (0.98s → 0.76s), whereas the retrieval group exhibits faster, stable RT (0.52s → 0.45s). While this pattern is consistent with genuine strategy differences persisting in Experiment 3, it could also reflect the greater spatial precision demands of reaching to invisible targets from text instructions, rather than genuine mental rotation per se. Reaching to an invisible location defined by a verbal angular label is inherently more demanding than reaching to a visible target, regardless of strategy type, and this demand is asymmetrically present in the two groups, since Non-Critical targets are invisible for the algorithmic group but visible for the retrieval group.

Thus, from my point of view, experiment 3 should not be used as definitive evidence that algorithmic and retrieval strategies during standard visuomotor adaptation cannot differentially influence implicit recalibration.

Overall, the manuscript addresses a meaningful question and the multi-experiment structure is useful. The evidence is incomplete for the broad claim that implicit recalibration is insensitive to strategy type. The study would make a clearer contribution if the authors narrowed the claims, strengthened the generalization analyses, and treated null effects with appropriate inferential tools.

Reviewer #1 (Public review):

Summary:

The authors characterize the phospholipid scramblase Xkr in Drosophila. They generate null mutants in both S2 cells and flies and find that phosphatidylserine (PS) exposure is reduced during apoptosis; they show reduced engulfment of apoptotic cells, and that the protein is localized partially within the cytoplasm, overlapping with the ER. They go on to identify Xkr binding partners and show that they overlap with plasma membrane-ER contact sites, suggesting that Xkr facilitates PS transfer from the ER to PM. Overall, this reveals a new role for Xkr and identifies new binding partners, which are valuable contributions to the field.

Strengths:

(1) The generation of new Xkr reagents in both S2 cells and flies to analyze its function. Tools are used to quantify both PS exposure and efferocytosis, and the effects of Xkr knockout are significant.

(2) The discovery of new binding partners of Xkr which also affect PS exposure and efferocytosis.

(3) The authors demonstrate that the binding partners are conserved in mammalian cells.

Weaknesses:

(1) Throughout the manuscript (e.g, lines 105, 165, 274 and discussion), the authors describe Xkr as being activated in a caspase-independent manner, and use this as the rationale for identifying binding partners. However, this is never shown in the manuscript or clearly referenced. Interestingly, there is a TEVDA sequence in the fly ortholog at the same location as the caspase cleavage site in C. elegans Ced-8 (Figure S1), suggesting the caspase cleavage site is conserved. This should be further investigated, or the statements regarding caspase independence should be modified. I don't think the N- and C-terminal GFP fusions indicate caspase independence, especially since apoptosis was not induced in Figure 1A, B. If cleavage occurred at the TEVDA site in Figure S1A, it would not lead to a noticeable change on the Western blot, although the size does look a bit smaller in Figure S2B at the 8 h time point.

(2) The authors examine overlap between tagged Xkr and cellular compartment markers and find substantial overlap with Lamp (and other vesicle markers to a lesser extent) (Figure S2). This is not addressed in the paper and could indicate engulfment of other cells since S2 cells are macrophages. To test this, the staining could be tested on the mixed cells (vesicle-GFP tagged S2 + apoptotic xkr-mcherry). Similarly, calreticulin is an eatme signal that gets translocated to the PM of apoptotic cells. This could affect interpretation of colocalization (Figure 2J), and ideally another ER marker should be used.

(3) There are some places where there is over- or incorrect interpretation, and these instances should be corrected.

Specific examples:

a) Line 342 "Relative expression analysis by RT-qPCR showed that all three mutants were likely null alleles." This does not make sense since there is still mRNA present. In Figure S7A, the tm9sf4 allele is expressed at 75% of the control. The others show a greater reduction, but this is not proof of a null allele.

b) Figure S3I - It looks like mCherry-Lact:C2 does get localized to the PM with AcD treatment in the xkr[ko], although the authors conclude "this disrupted PS localization to the PM could not be restored by apoptosis induction". However, the PM localization does look disrupted in the tm9sf4 and sac1 knockdowns.

c) Figure 3I. The control Lact:C2 staining looks very different from the staining in Figure 2J, with abundant Lact:C2 outside the cell. Given the variability in the staining, were the contact sites quantified? On lines 287-288, it is stated that "fewer ER-PM MCSs were detected in xkrko cells than in WT", but no quantification is provided.

d) Line 299-300 - "the interaction between Xkr and dORP9 was enhanced after apoptosis induction". The interaction does not look enhanced in Figure S5F, so this statement should be removed or data supporting the statement should be provided. The interaction between Xkr and dORP2 looks enhanced upon apoptosis induction, but also paradoxically looks even more enhanced when apoptosis is blocked.

e) The data in Figure S6 are highlighted in the abstract. If this is a major conclusion, it would be best to move it to the main text and provide quantification.

f) Lines 392-4. The concluding statement seems overstated given that there was only a modest inhibition of PS exposure in the osbpl5 knockdown (Figure 6A) and no defects in efferocytosis (Figure 6C). The osbpl8 showed a stronger effect on PS exposure but still a very modest effect on efferocytosis.

Reviewer #2 (Public review):

In this study, the authors investigate the mechanisms underlying phosphatidylserine (PS) exposure during efferocytosis in Drosophila. They first show that Xkr promotes PS exposure and apoptotic cell clearance in both S2 cells and Drosophila embryos. As Drosophila Xkr lacks the canonical caspase cleavage site found in mammalian XKR proteins, the authors further explore the underlying mechanism by which Xkr regulates PS externalization. Through protein interaction studies, they identify TM9SF4 as an interacting partner of Xkr that regulates PS distribution and show that non-vesicular PS transport contributes to apoptotic PS exposure and efferocytosis. Using protein interaction studies, they further demonstrate that Xkr interacts with the lipid transfer protein dORP9 at ER-PM contact sites to facilitate non-vesicular PS transport to the plasma membrane. Loss of these proteins affects PS externalization and efferocytosis in Drosophila. Finally, using human cells, they demonstrate that human OSBPL8 interacts with XKR8 to regulate apoptotic PS exposure. Overall, the study supports a model in which Xkr promotes efferocytosis by facilitating lipid transport in addition to its role as a phospholipid scramblase.

Reviewer #3 (Public review):

Summary:

The manuscript investigates the function of the Drosophila Xkr protein, a homolog of mammalian Xkr8 that lacks the canonical caspase-cleavage motif. The authors show that apoptotic stimuli increase Xkr protein abundance through a post-transcriptional mechanism and that Xkr promotes phosphatidylserine (PS) exposure during apoptosis. Using immunoprecipitation coupled with mass spectrometry, they identify TM9SF4 as an Xkr-interacting protein and further implicate TM9SF4, Sac1, dORP2, dORP9, and Vap33 in regulating apoptotic PS exposure and efferocytosis. Based on these findings, the authors propose that Xkr regulates PS transport at ER-PM contact sites. Similar observations are also presented in human cells.

Strengths:

Overall, this is an interesting study. The authors provide convincing evidence that Drosophila Xkr participates in apoptotic PS exposure and employ multiple complementary approaches to support the involvement of several proteins in this pathway. The identification of TM9SF4 as a potential regulator of Xkr-mediated PS exposure is likely to be of broad interest.

Weaknesses:

I am less convinced by the evidence supporting the proposed role of ER-PM contact sites, and several mechanistic conclusions appear to extend beyond the data presented. Addressing the following points would substantially strengthen the manuscript.

Major concerns:

(1) In Figure 2A and related text, it is unclear whether the mass spectrometry analysis was performed using untreated cells or AcD-treated cells. If the objective was to identify apoptosis-associated Xkr interactors, it would be helpful to clarify the experimental condition and explain whether apoptosis-specific interactors were analyzed separately.

(2) In Figure 2B, 2E, and several other co-IP results, a negative control of Flag tag only is required to exclude experimental errors like insufficient washing, etc.

(3) In Figure S3B, S3F, and several other BiFC results, an mVC-only negative control would be important to exclude nonspecific fluorescence complementation.

(4) In Figure 2G, the quantitative values appear inconsistent with the flow cytometry histograms. The peak shift following Sac1 knockdown appears smaller than that of TM9SF4 knockdown, whereas the quantified values suggest the opposite. Please clarify this apparent discrepancy.

(5) I find the interpretation in Lines 223-227 difficult to reconcile with the data. Knockdown of both tm9sf4 and sac1 impaired apoptotic PS exposure to a similar extent as xkr knockout. However, while xkr deficiency significantly reduced efferocytosis, sac1 knockdown produced only a modest, statistically insignificant effect. These observations suggest that impaired PS exposure alone may not fully account for the efferocytosis phenotype observed in xkr-deficient cells. These results appear difficult to reconcile with the proposed model, which needs careful discussion.

(6) In Lines 274-275, the authors state that 'increased Xkr may accelerate non-vesicular PS transport for efficient apoptotic PS exposure'. However, Xkr protein levels increase only ~8 h after AcD treatment, whereas PS exposure occurs much earlier. Thus, alternative explanations like Xkr relocalization (Figure S5C), rather than increased abundance, may also explain how Xkr mediates PS transport. An Xkr overexpression experiment could be helpful to support this statement.

(7) The interpretation of the MAPPER experiments requires further clarification. In Line 283, the authors refer to "the intracellular proportion of the signal for each protein overlapping with MAPPER." Since MAPPER is designed to label ER-PM contact sites, which are located on the plasma membrane, intracellular MAPPER fluorescence likely represents the ER network rather than bona fide ER-PM contacts. Throughout the manuscript (including Figure S6, etc.), intracellular MAPPER puncta appear to be interpreted as ER-PM contacts, which may not be appropriate. In contrast, the peripheral MAPPER puncta observed along the cell cortex (e.g., Figure S5C after AcD treatment) are more consistent with authentic ER-PM contact sites. It is also not obvious that these cortical MAPPER signals colocalize with Xkr(Figure S5C). Thus, while the data support a role for the ER, they do not yet convincingly demonstrate Xkr clustering at ER-PM contact sites.

(8) In the Xkr knockout cells, all fluorescence signals appear substantially low in intensity. Differences in protein distribution are difficult to interpret when overall probe expression also appears altered. It would be helpful to demonstrate that probe expression levels are comparable between conditions. Furthermore, as noted above, intracellular MAPPER signal may primarily represent ER rather than ER-PM contacts. Finally, despite the reduced signal intensity, the remaining MAPPER and PS signals still appear well colocalized in the knockout cells, similar to the observations in Figure 2J. The interpretation in Lines 285-288 should therefore be reconsidered.

Reviewer #1 (Public review):

Summary and Strengths:

Shin et al deepen our understanding of high frequency oscillations in the frontal cortex during REM in a manner that sheds important light on the roles of these events. In particular, they reveal that cortical HFOs are modulated by theta oscillations, occur in chains and recruit cortical neuronal activation patterns in a manner that is distinct from other high frequency events during nonREM or in hippocampus. They also show that these events occur during increased oscillatory cross-talk between hippocampus and cortex and may protect cortical neurons from down regulation of firing during sleep. Overall, this is important work with several novel observations pointing towards an important role for these events that will open become increasingly understood over time.

I also wanted to comment that 2D is a beautiful illustration of separate and essentially exclusive communication channels used during HF events in NREM vs REM. They almost perfectly complement each other's frequencies.

Weaknesses:

I have only one major scientific critique, I believe we need to see quantification of how phasic REM theta waves with versus without HFOs differ. What do REM HFOs add to the "normal" theta oscillation? Without this, comparison it is more difficult to interpret the meaning of these events. Given that HFO chains have IEIs around the time of a theta cycle duration, are the repeating spiking activities stronger during HFO repeats than during adjacent theta waves without HFOs? What percentage of theta waves contain HFOs and what is the firing rate during those theta waves with vs without HFOs? Is there differential firing rate modulation? The authors may even consider that all REM-HFO-specific quantifications should be shown as differential from phasic theta cycles without HFOs.

As a non-scientific comment on the manuscript itself: unfortunately, the paper is difficult to read and understand at times, requiring great effort by the reader. This is to an extent that communication is hindered. The paper is dense with changing methods often from panel to panel. Unfortunately, the panel quantifications are not explained in the results section in a manner that readers can understand without going to read the methods for often each individual panel. These measures should be explained in a way that lets readers understand the conclusions of each panel and grossly what calculations were used to reach those. Instead, too much jargon is used rather than clear descriptions of overall calculations being done for each panel.

The authors mention in discussion that they see increased functional connectivity between mPFC and CA1, but most data suggesting that seems to be based on LFP rather than spiking. Functional connectivity is defined best by spiking-spiking relationships. And these authors have spiking data. So I believe either the descriptive language should be pulled back to something like "oscillatory coupling" or more analyses should be dedicated to showing spike-spike coordination across regions. 


Comments on revised version.

Previously raised concerns are addressed.

Reviewer #2 (Public review):

Summary:

In this study, the authors investigate high-frequency oscillations (HFOs) in the prefrontal cortex during REM sleep. They identify a specific pattern where these HFOs occur in "chains" that are phase-locked to theta oscillations, primarily during the "phasic" periods of REM. The study contrasts these events with isolated HFOs and NREM ripples, suggesting a unique role for these chains in coordinating activity between the prefrontal cortex and the hippocampus. Most notably, the authors report that a specific subset of hippocampal cells-those that co-fire with the prefrontal cortex during these HFOs-increase their firing rates over the course of sleep, suggesting a potential mechanism for selective memory consolidation.

Strengths:

The study addresses an under-explored area of sleep physiology: the fine-grained temporal coordination between the cortex and hippocampus during REM sleep. The identification of HFO "chains" and their association with higher theta power provides an interesting framework for understanding how the brain might organize information transfer outside of NREM sleep. The observation that specific hippocampal populations show differential firing rate changes based on their participation in these HFO events is a striking finding that warrants further investigation.

Comments on revised version.

I do have one remaining concern, which is about their continued use of the term "reactivation" during REM sleep, whereas it still seems "activation" is more appropriate. The only place they show more Post vs. Pre activation is in Figure 6F/6G which includes NREM sleep where indeed reactivation is robust (but not the main focus of this paper). There is no evidence offered that the REM ensembles are not already "pre-configured" and active at similar levels (with similar activation patterns) during Pre sleep. Notably Louie and Wilson 2001 found greater "replay" during Pre than Post during REM. Also, the first half vs. second half comparisons (e.g. Fig 6C) could be more effectively performed in Figure 6A, showing that the same ordering persists across the periods. If this point were addressed, the significance of the findings could potentially increase.

Reviewer #3 (Public review):

Summary:

Shin et al. examine hippocampal-prefrontal interactions during sleep using simultaneous CA1 and prefrontal cortex recordings in rats performing a spatial memory task. They identify high-frequency oscillation (HFO) events in PFC during REM sleep that occur in theta-modulated chains and are associated with increased CA1-PFC coherence and sequential, sparse reactivation of cortical ensembles. This pattern contrasts with the synchronous reactivation observed during NREM cortical ripples. Together with a simple cholinergic network model, the authors propose that REM HFO chains represent a distinct mechanism for hippocampal-cortical coordination that complements NREM ripple-mediated processing during sleep.

Strengths:

A major strength of the work is the extensive electrophysiological dataset, which includes simultaneous recordings of large neuronal populations in both hippocampus and prefrontal cortex across behaviour and subsequent sleep. The analyses linking high-frequency events to population dynamics, interregional coherence, and ensemble reactivation are technically sophisticated and provide an incredibly detailed description of REM-associated cortical activity patterns. In particular, the demonstration that REM HFOs occur in chains aligned to theta phase and organise sequential activation of cortical assemblies represents a potentially important advance in understanding the neural structure of REM sleep activity. The integration of experimental data with a computational model further provides a useful framework for interpreting the observed differences between REM and NREM network states in terms of neuromodulatory influences.

Weaknesses:

While overall this study provides a highly valuable body of work, there are two primary limitations, which if overcome, would provide substantially more significance to the overall characterisation of REM HFOs. Specifically:

Distinction from wake HFOs<br /> The results largely support the authors' claim that REM HFO chains represent a distinct pattern of neural coordination compared to NREM cortical ripples. The analyses consistently show differences between REM and NREM events in terms of neuronal modulation, ensemble structure, and interregional coupling. However, similar high-frequency events during wake are not examined. Since REM sleep shares several network features with wakefulness, including strong theta oscillations, evaluating whether comparable PFC HFOs occur during wake would provide clarity on whether these events are specific to REM sleep (and its associated functions) or represent more general theta-associated phenomenon.

Link to memory consolidation<br /> The manuscript proposes throughout that REM HFO chains may contribute to memory consolidation by coordinating hippocampal-cortical reactivation, but the evidence for this functional role remains indirect. The authors do highlight this as a limitation of the study - the inability to link their findings to learning - but it is not clear why. Further details of the behaviour results should be included. If no learning occurred across the eight behavioural sessions, this should be reported. If learning did occur, but could not be linked to HFO events, this should also be reported.

Comments on revised version.

The authors have since addressed these weaknesses. In supplementary figure S11 the authors now show that while HFOs were detectable during wake, they were not associated with gamma/theta oscillations or theta modulation of unit activity. This suggests that HFOs during REM are a distinct feature of REM sleep and not comparable to HFOs during NREM or wake. It would be interesting for future work to identify the significance of wake PFC HFOs, whether there are differences between HFOs during running compared to stationary behaviour, and their relationship to hippocampal sharp-wave ripples and memory consolidation.

Regarding the link between REM HFOs and memory consolidation, the authors have further acknowledged this as a limitation of the study and requirement for a more specific experimental design to test related hypotheses. Nevertheless, they do show a clear trajectory of learning in the rats and corresponding increase in reactivation of task-related activity which could be associated with REM sleep HFOs. This study paves the way for future experiments to more directly test this link.

Reviewer #1 (Public review):

Summary:

The manuscript investigates value-based decision-making under risk and ambiguity using a combination of behavioral, pupillometric, and EEG data. Participants are stratified into three "decision styles" (ideal, aggressive, conservative) based on how their choices under known risk align with expected-value optimality. The central claim is that ambiguity aversion is not a uniform bias but reflects heterogeneous internal belief models, and that physiology tracks subjective belief rather than objective task structure. While this is an interesting conceptual question, the evidence is underwhelming given that differences between groups are not tested statistically (but just described), there are clear problems with how the computational models are implemented, and there are serious issues with sampling of participants.

Strengths:

The multimodal design (behavior, pupillometry, EEG) and the attempt to link a latent belief parameter to physiological signatures address a question of clear interest.

Weaknesses:

Framing and motivation

(1) The framing conflates two questions that appear distinct. The motivation centers on "ambiguity aversion," but the study's actual aim - how individuals internally represent ambiguous outcomes - seems like a different question. The relationship between these two framings needs to be made explicit, because as written the motivating phenomenon and the studied phenomenon are not obviously the same thing.

(2) Several of the contrasts the paper sets up against prior literature read as strawmen. The claim that ambiguity aversion is treated as "a single bias or fixed trait that applies uniformly" is presented as the view being overturned, but it is not clear this is a position the field actually holds - it reads as a strawman. Relatedly, the central objective-versus-subjective valuation distinction that the results are built around also reads as a strawman dichotomy rather than a genuine competing account.

(3) The motivation for the physiological measures is overly broad. The statement linking EEG to control, attention, valuation, uncertainty, conflict, effort, and engagement is so general as to be uninformative - EEG signals have been linked to essentially everything, so this does not constrain the hypotheses or predictions. A more specific, falsifiable rationale is needed.<br /> Design, sample, and grouping.

(4) The inclusion of the collaborative spacecraft/Apollo task is unclear. It is not explained why this task is included, and its role relative to the core ambiguity question needs justification (this also bears on the leadership analyses; see below).

(5) The participant numbers do not add up and must be reconciled. The text reports 57 participants, yet the analyses describe three groups of roughly 32 + 32 + 31. The relationship between participants, sessions, and group n's needs to be stated clearly and consistently, because at present the sample description is internally contradictory.

(6) The rationale for categorizing participants into three discrete groups is not established, and the approach is statistically questionable. Decision tendency appears to be a continuous variable; dichotomizing/trichotomizing a continuous measure is generally discouraged and can manufacture or distort group differences. The authors should justify why discrete groups are needed at all, and ideally show whether there are genuine group differences (e.g., evidence of discontinuity/clustering) rather than an arbitrary split of a continuum.

Statistics

(7) Key claims about how ambiguity affects groups differently are made without the appropriate test. To support a claim that the effect of ambiguity differs across groups, the interaction (group × ambiguity) must be shown - group-wise effects reported separately are not sufficient. This is really a key limitation of the current work.

(8) The methods mentioned that some participants performed multiple sessions, but their data were treated as if coming from separate participants. This is incorrect for several reasons, particularly given the focus on individual differences.

Belief parameter and terminology

(9) The term "ideal" is not justified. It is unclear why this group is labelled "ideal" - are they Bayes-optimal, or optimal in some defined sense? If the label implies normativity, that needs to be demonstrated; otherwise it should be renamed.

Drift-diffusion modelling

(10) The boundary parameter is fixed (a detail which is hidden in the methods), but this is highly problematic. By enforcing the same boundary value for all participants, the model is forced to capture any variation as drift rate effects. As such, all conclusions about drift rate are not interpretable as they might reflect boundary effects in disguise.

(11) The DDMs are fit separately per group of participants, which again precludes testing interactions. As with the behavioral analyses, fitting separate models means group differences cannot be properly compared within a single statistical framework, and interactions cannot be assessed. The paper does mention some comparison between groups, but comparing DDM parameter estimates across separately fit models is not valid.

(12) Overall, the DDM is very complex, and the manuscript does not yet provide enough validation to make the model trustworthy. Given the number of trial-wise covariates entering the drift rate and the per-participant fitting, stronger evidence that the model is identifiable and that its parameters are recoverable/reliable is needed before the conclusions drawn from it can be accepted.

Methods - EEG and analysis details

(13) The high-pass filter setting appears very aggressive. The authors should confirm whether this risks removing genuine low-frequency signal of interest, particularly given that delta-band effects are later interpreted.

(14) There is an apparent inconsistency in the epoching/time-locking. The time-frequency analysis appears to be computed on choice-locked data, yet elsewhere the epochs are described as stimulus-locked. This needs to be clarified and made consistent, as it affects interpretation of the pre- versus post-decision EEG clusters.

(15) The mixed-effects modelling appears to omit random slopes. The authors should justify the random-effects structure (e.g., why only random intercepts), as this affects the validity of the inference.

Reviewer #2 (Public review):

Summary:

The manuscript by Qin and colleagues entitled "Pupil and Neural Dynamics Reveal Belief-Dependent Decision Making Under Ambiguity" examines decision-making under risk and ambiguity using pupillometry and EEG. The study employs a lottery choice task with three levels of ambiguity (zero, low, high). Participants were classified into three groups based on their choice behavior in a condition with risk and no ambiguity: ideal (choosing in line with objective expected values), aggressive (preference for investments), and conservative (preference against investments). The authors then compared behavior, pupil, and EEG results across these groups. The study concludes that individual beliefs about ambiguity are reflected in different behavioral strategies and neural correlates.

Strengths:

The combination of behavior, computational modeling, pupillometry, and EEG.

Weaknesses:

(1) It is unclear whether group definition is theoretically justified.

One general concern is that the strategy to form three distinct groups is not clearly motivated. The authors created the three groups, "aggressive", "ideal", and "conservative", based on the zero-ambiguity trials. However, as the authors state: "Ambiguity differs fundamentally from risk at both the physiological level (34; 6) and the behavioral level" (page 4). Under this assumption, it is questionable whether forming groups based on risk preferences is a useful strategy for studying ambiguity. What do we learn about ambiguity processing when group differences are primarily based on risk preferences? Might the present results partly be driven by risk preferences rather than ambiguity preferences? I recommend the following two points: (a) Clearly justify the reasoning behind the group approach; (b) Add an additional continuous analysis approach indicating whether the key results hold independent of the group definition based on risky decision-making.

(2) k-parameter.

The authors use the k-parameter that infers the expected high-payoff probability (e.g., page 11). On page 22, this is explained as: "the subjective value term K was assigned according to each participant's internal belief of the high-payoff rate under ambiguity, yielding a participant-specific estimate of expected value under uncertainty." I hope I have not missed anything, but I neither understood the role of this parameter nor how it was computed.

(3) How were individual beliefs and models computed?

A related but more general point is that it remained unclear how the authors computed internal beliefs and internal models in the study. The study contains many statements suggesting that the authors measured internal beliefs. For example:

a) Abstract: "We show that individuals adopt distinct decision strategies that reflect different internal beliefs about unknown outcomes."<br /> b) Page 3: "We then inferred subjective belief parameters that captured how individuals internally interpreted the ambiguous probability mass and examined how these beliefs related to choice behavior, arousal dynamics, and neural activity."<br /> c) Page 16: "Together, these findings show that ambiguity does not evoke a uniform behavioral or physiological response across participants with different decision-making styles; instead, individuals rely on distinct internal models and computational strategies when forming decisions under ambiguity."<br /> d) Page 16: "Taken together, these results show that ambiguity aversion is not a uniform psychological bias, but a set of heterogeneous belief-driven strategies that shape how ambiguity is represented and acted upon."<br /> e) Page 18: "Ambiguity processing, therefore, reflects distinct belief-driven pathways rather than a single canonical mechanism."

Based on the present data, analyses, and results, I don't think that the authors can draw these conclusions. Which analyses in the manuscript identify these internal beliefs, models, or strategies? How can we dissociate a unified strategy from a heterogeneous set of strategies based on the present results? My feeling is that the k-parameter might be related to this, but as explained above, I did not understand how it was computed and what it is supposed to reflect. The DDM analyses might also be targeted at this. However, it remains elusive how the DDM captures internal beliefs about ambiguity itself. My recommendation is that the authors more clearly explain (a) why the DDM is a useful model to study ambiguity, (b) what the different parameters exactly reflect about ambiguity processing, and (c) how the DDM captures internal beliefs and distinct belief-driven strategies in this context.

(4) Statistical tests.

4.1. Figure 2B: The authors summarize the number of participants with significant effects of ambiguity on choice behavior for each group. I recommend a statistical test at the second level that properly assesses the effects of ambiguity and group within a common statistical model. In my opinion, it is not enough to simply count the number of significant tests (from the first level) for each group.

4.2. Figure 2C: For the analysis of response times, the authors might want to consider reporting the main effects of group and ambiguity.

4.3. Figure 2D: The text on page 8 states that Figure 2D indicates that "aggressive investors showed no significant pupil modulation by ambiguity...". However, the figure and its caption indicate significant differences between ambiguous and non-ambiguous trials across all groups. Moreover, if the authors want to compare the groups, it is necessary to compare the groups to each other; a test against zero within each group would not be enough to demonstrate any group differences. In my mind, this would also be important for analyses in Figure 3C and D.

4.4. Strictly speaking, for the statistical tests, it would be necessary to take into account that participants completed multiple sessions (within-subject variance is different from between-subject variance). Currently, each session is treated independently (page 19: "Each individual completed one to three experimental sessions. For data analysis, each session was treated as an independent participant, yielding a total of 108 sessions.")

(5) Necessary quality control for pupillometry and EEG data.

The task was performed in a virtual reality environment with a head-mounted display. The task was not isoluminant, and, to the best of my knowledge, participants were not instructed to avoid eye movements. The authors applied a GLM to control for luminance effects in the pupil data. For EEG, they used ICA to remove ocular and muscular artifacts. While these methods are established, they are usually applied to more controlled paradigms optimized for EEG and pupillometry. To demonstrate high data quality despite these issues, it is necessary to present quality-control analyses. Can the authors please indicate how many blinks had to be removed from the data? Could the authors please indicate how many blinks were removed from the data? Can the authors please show trial-level data (after preprocessing) for a few subjects?

(6) Quality control for the DDM.

The manuscript lacks systematic posterior predictive checks and parameter recovery for the DDM results. It is important to validate that the model accurately captures the data. Currently, we only see the model parameters, but it remains unclear whether the model performs well on the current data set. Moreover, if the authors aimed to test different strategies using the DDM, it might be useful to perform systematic model comparison.

(7) Implications of the second experiment with collaborative task remain unclear.

To me, the link between the main study and the second experiment on leadership and team performance is not obvious. In my opinion, this topic is beyond the scope of the present paper. Linking the two studies more comprehensively based on deeper theoretical grounds would likely be better suited for an independent manuscript.

Reviewer #1 (Public review):

Summary:

This article purports to show that ML-SA8, a synthetic activator of the lysosomal TRPML1 channel, results in AMPK activation and glucose uptake in hepatocytes, and that this action has therapeutic potential for metabolic disease. The final figure shows that glucose levels are improved in db/db mice, although it is not entirely clear whether this is due to an effect on the liver, on other tissues, or on glucose production or uptake. The earlier figures try to make the case that SA8 causes activation and GLUT4 translocation and glucose uptake in liver cells; however, these data are not convincing. GLUT4 is expressed at such low levels in liver that it is likely not physiologically important. The authors use a fluorescent glucose analog to measure glucose uptake, and this molecule has been shown to enter cells largely by fluid phase endocytosis. Overall, this reviewer finds the premise misguided and the data unconvincing.

Strengths and Weaknesses:

The initial figures show phosphorylation of AMPK on Thr172, but no downstream effects are shown. Usually, to convincingly show that AMPK activity is increased, it would be appropriate to immunoblot phospho-ACC or some other substrate. This is minor.

Lines 135-148: GLUT4 is not expressed at levels that are significant for physiology in liver cells, and its function in liver is not particularly relevant. The authors cite references 38-40 to support that it may be expressed at low levels in liver, but no knockout studies have been done to show that this expression is physiologically important.

Figure 1e is not convincing. No controls are included to show the specificity of the antibody for immunofluorescent staining. No intracellular GLUT4 is visible in the unstimulated samples.

In Figure 1f, again, the data are not convincing. The bands seem too sharp for GLUT4, which has 12 membrane-spanning domains as well as an N-linked glycosylation, so that it usually runs as a smear.

Figure 1h. Data are not convincing. 2-NBDG is not a valid approach to measure glucose uptake. 2-NBDG enters cells largely via fluid phase endocytosis, and its accumulation is independent of known GLUT inhibitors such as cytochalasin B (Yazdani et al., MBoC 2022; PMID: 35921166; see also PMID: 42287154). The idea that such a bulky derivative of glucose could enter the transporter channel is not compatible with known structural data.

Supplementary Figure 5 uses 2-NBDG glucose uptake again. This reviewer is not convinced that the data reflect transporter-mediated glucose uptake, as suggested by the authors. As well, although palmitate treatment of cells can cause an insulin-resistant-like phenotype in some cell types, this is not characterized in the present work. Finally, as noted, one would not expect hepatocytes to exhibit insulin-responsive glucose transport. Glycogen synthesis is the main insulin-regulated step that might be affected.

The data in Figures 2b,c,f,g,k,l are not convincing. Again, 2-NBDG is used.

For the glucose consumption measurements in other panels of Figure 2, the methods section states that cells were cultured in 10 mM glucose. What volume was used? It is difficult to believe that a monolayer of cells would consume very much of the glucose that is present in the culture medium. Data are shown as a percent of controls, and look reasonable, but it would be helpful to include absolute as well as relative units.

In Figure 2, in experiments using the TRPML1 KO cells, no panel is shown to demonstrate knockout. The authors cite a previous paper for the construction of these cells, but the control immunoblot should still be shown here.

In Figure 3, controls are missing in the BAPTA experiment in Figure 3a (only SA8-treated cells were treated with BAPTA and with EGTA). Again, it would be helpful to have p-ACC or some other readout of AMPK activity, and not just AMPK phosphorylation. 2NBDG is again used in this figure.

Line 212-213 the text states "considering our finding that TRPML1-mediated Ca2+ release is essential for AMPK activation." This has not been shown. The work uses chelators and does not necessarily indicate a role for TRPML1. The drug may be specific, as suggested by the authors, but the way this phrase is worded is too strong. As well, AMPK was shown to be phosphorylated, but full activation towards its various substrates has not been shown.

Figure 4cd suggests that GLUT4 expression is increased by 2 or 3-fold in the liver of DB+SA8-treated mice, compared to controls. This may be the case, but its abundance is still likely ~1000-fold less in liver compared to skeletal muscle or adipose tissue. This reviewer is still not convinced that this is physiologically relevant. The images in Supplementary Figure 8 suggest a larger increase, but it remains uncertain whether the staining really represents GLUT4.

Data showing that blood glucose and HbA1c are reduced in SA8-treated mice are reasonable, and GTTs and ITTs are shown. Unfortunately, there are no insulin concentrations, and it remains uncertain whether glucose production is reduced or uptake is increased (or if both effects are present).

In the discussion, the authors again state that GLUT4 is present in the liver and that it regulates hepatic glucose homeostasis, and they cite reference 63. This review article does not argue that GLUT4 acts in the liver to regulate hepatic glucose homeostasis, but that its actions in muscle and fat have secondary effects on the liver.

Reviewer #2 (Public review):

Summary:

The manuscript contains interesting studies suggesting that pharmacological activation of TRPML1 could be useful to treat T2D by increasing glucose uptake via activation of AMPK. Preclinical studies suggest the inhibitor improved blood glucose in Db/Db mice. Ex vivo studies in cell lines examine both pharmacologic and genetic manipulations, both to activate and to inactivate TRPML1, and the results consistently suggest that TRPML1 activates AMPK and increases glucose uptake.

Strengths:

The manuscript is well written, and the studies are carefully performed.

Weaknesses:

All mechanistic studies were performed in transformed cell lines; conclusions would be stronger if performed in primary cells. The in vivo studies were only performed in male mice. Performing metabolic studies in both sexes is standard practice now. Whether the findings would extend to females was not tested and remains uncertain. Some controls are missing, such as plasma membrane loading controls for fractionation studies. The GLUT4 staining was performed after fixation and permeabilization, yet control cells appear to be devoid of intracellular (and all) staining, a confusing result that doesn't reflect the expected biology.

Reviewer #3 (Public review):

Summary:

Zhu et al. present a proof-of-concept for targeting the lysosomal calcium channel MCOLN1/TRPML1endolysosomal ion channels to restore type 2 diabetes mellitus (T2DM). Using synthetic TRPML1 agonists (ML-SA8) and genetic manipulation, the authors demonstrate that TRPML1 stimulation triggers localized lysosomal calcium release. This calcium efflux sequentially activates CaMKKβ and phosphorylates AMPK at Thr172 in various cell models, including palmitic acid-induced insulin-resistant HepG2 cells. This signaling pathway promotes GLUT4 translocation to the plasma membrane and increases intracellular glucose uptake. When administered daily to diabetic db/db mice over six weeks, ML-SA8 lowers fasting and random blood glucose, improves oral glucose and insulin tolerance tests, reduces hepatic steatosis, and lowers serum ALT and AST levels.

Strengths:

Based on the TFEB-independent pathway activated by TRPML1 and the experimental approaches described by Medina's group (PMID: 31822666), the authors use a combination of pharmacological and genetic tools to dissect such an intracellular signaling pathway. Additionally, the animal experiments show consistent phenotypic improvements across independent metabolic parameters. The ability of ML-SA8 to restore glycogen deposition and clear hepatic lipid accumulation in db/db mice without causing weight loss or overt toxicity provides a strong rationale for exploring lysosomal targets in metabolic disease.

Weaknesses:

(1) The authors focus almost exclusively on hepatic GLUT4 to explain the observed glucose disposal. However, other glucose transporter isoforms such as GLUT2 dominate basal glucose transport. While the authors show increased AMPK phosphorylation in skeletal muscle and adipose tissue, they do not measure GLUT4 translocation or glucose uptake in these primary disposal organs. As a result, attributing systemic glycemic recovery primarily to hepatic GLUT4 translocation overlooks the major physiological roles of peripheral tissues.

(2) In both HepG2 cells and mouse liver tissues, ML-SA8 treatment increases total GLUT4 protein expression in addition to plasma membrane localization. Because total protein pools expand, the enrichment of GLUT4 in plasma membrane fractions cannot be cleanly attributed to acute vesicular translocation alone. The manuscript does not explain the timescale or mechanism behind this rapid total protein upregulation, leaving a mechanistic gap between acute ion channel gating and protein expression.

(3) While the in vitro specificity of ML-SA8 is well-controlled, the systemic animal experiments lack a specific rescue or knockout control. Small-molecule agonists administered intraperitoneally over six weeks can exert off-target effects. Without demonstrating that co-administering the TRPML1 inhibitor ML-SI5 blunts the therapeutic effect in vivo, or showing that ML-SA8 lacks efficacy in TRPML1-null mice, the definitive link between in vivo glycemic recovery and TRPML1 activation remains incomplete.

Reviewer #1 (Public review):

Summary:

This study investigated the formation of mitochondrial-derived compartments (MDCs) under metabolic adaptations. They hypothesized that MDCs may play a role in regulating the mitochondrial proteome under these conditions by removing excess and superfluous membrane proteins that may challenge mitochondrial proteostasis. They found that glucose restriction, carbon-source switching, and osmotic stress can stimulate MDC formation. Underlying these stressors is a common signaling pathway that involves Snf1-dependent derepression of mitochondrial biogenesis and rapid synthesis and trafficking of nuclear-encoded proteins into mitochondria. They then showed that MDC formation is attenuated in tom70/tom71 mutants, suggesting that the delivery of these proteins to mitochondria is critical. Data also suggested that HAP4-stimulated mitochondrial biogenesis promotes MDC formation, which is further enhanced by glucose restriction and is suppressed after prolonged adaptation.

Strengths:

The genetically amenable yeast system allowed the authors to generate convincing data showing the rapid formation of MDCs under physiologically relevant conditions where the mitochondrial proteome needs to be expanded to accommodate increasing metabolic function. MDCs therefore function to buffer spillovers of outer membrane proteins upon an abrupt protein influx. Overall, the data presented are of high quality. The conclusion is strongly supported by the data.

I think this is a significant study as (1) it supported MDCs as a physiologically relevant mechanism of mitochondrial proteostasis; and (2) it offers a common mechanistic framework explaining the MDC phenomenon under many other conditions such as TOR inhibition and hydrophobic protein overloading previously published by this group. Although the precise mechanism of MDC formation and how MDC formation contributes to the overall proteostasis of mitochondria remain unknown, as the authors stated in the manuscript, the current work is a clearly identifiable milestone in this specific area of investigation.

Weaknesses:

Although the data are overall strong, weaknesses are mainly related to potential misinterpretation of the data.

(1) I have reservations regarding the interpretation of some results. First, the authors concluded that MDC biogenesis is activated when glycolytic metabolism is altered. I disagree with this. The authors should distinguish between "loss of glycolysis" and "loss of glucose repression". The yeast S288C strains are GAL2 and can ferment galactose. Likewise, glycolysis is also supported by raffinose and sucrose. In a broad sense, these carbon sources do support glycolysis as long as sugar influx is maintained at a high level. However, these alternative carbons do not repress mitochondrial respiration like glucose. It is likely the derepression of mitochondrial respiration (which is stated in some sections of the manuscript) instead of loss of glycolytic metabolism that stimulates MDC formation. This needs to be made clear throughout the manuscript. As such, the statement that "Carbon-source switching" stimulates MDCs is not accurate and needs to be re-interpreted.

(2) The explanation for the requirement of low glucose levels could be misleading. A complete lack of carbon sources and high concentrations of 2-DG may shut down global protein synthesis, cell cycle progression, and many other processes, including mitochondrial biogenesis. Glucose at 0.02% is not sufficient to cause glucose repression, as only the high-affinity but low-influx transporters are functioning. Under the low glucose conditions, mitochondrial respiration is also derepressed. In this scenario, low glucose simply plays a role in supporting cell growth without causing the repression of mitochondrial biogenesis.

(3) The idea that MDCs are formed when protein load exceeds the capacity the organelle can accommodate is attractive. Early studies have shown that the mitochondrial compartment is expanded by several folds in volume when yeast cells are switched from fermentative to oxidative metabolism. Perhaps, space expansion takes longer than protein influx increase. It would be interesting to see whether there is a correlation between MDC frequencies and the delay in volume expansion. Long-term adaptation would solve this challenge, as it allows the cell to complete volume expansion.

(4) HAP4 may primarily activate OXPHOS genes but not some MDC cargo proteins. The requirement for "metabolic remodeling" for full induction of MDC formation may be an overstatement. The authors should either reexamine the proteomic data to see whether known MDC cargos are not subject to HAP4 activation or have this discussed in the manuscript.

Reviewer #2 (Public review):

Summary:

Price et al. present new work providing insight into the function and mechanisms of mitochondrial-derived compartments (MDCs) in yeast. The Hughes lab previously established that these large ~micron-sized structures are formed under a variety of conditions including amino acid stress (rapamycin, conA, cycloheximide), alterations in mitochondrial metabolites and lipids, or acute expression of specific outer membrane proteins. These stressors lead to the sequestration of outer membrane proteins (that can include mistargeted inner membrane proteins) that extend or tubulate into large multilamellar structures that ultimately target the vacuole in an ATG5/Dnm1 dependent autophagy related pathway for degradation. Initially reported in aging yeast a decade ago, it has now been accepted as a mechanism to remove excess mitochondrial proteins as a pathway distinct from mitophagy or the extraction of stalled precursors from the import translocon.

In this study, the authors examined additional metabolic transitions they suspected would drive increased mitochondrial protein expression and promote MDC formation. Indeed, they show that glucose-restricted conditions (or a switch to galactose or incubation with 2DG) induced MDCs within 2 hours. This correlated with increased transcription/translation of mitochondrial precursors porin and OM45. Similar results were seen with osmotic shock, a process previously shown to induce mitochondrial gene expression. The metabolic or osmotic shift was shown to activate a yeast AMPK-type kinase called Snf1, which phosphorylates a key substrate Mig1 - an established repressor of mitochondrial gene expression. Loss of these pathways abolished the generation of MDCs under these conditions. As the key novel finding in the study, the authors explored the relationship/requirement for Snf1 and Mig1 using multiple approaches in different backgrounds and employing auxin-inducible degron tools for acute depletion. These data further support the hypothesis that excess mitochondrial outer membrane proteins result in MDC formation to facilitate their removal, at least transiently until the import machinery can adapt to the increased import demand. To test this more directly, they generated an inducible yeast strain to express a canonical transcription factor Hap4 that induces mitochondrial gene expression. In this system, induction of Hap4 expression also resulted in MDC formation. While not all previously reported MDC inducers act through Snf1/Mig1, the common feature is the transcriptional induction of mitochondrial protein expression.

Strengths:

The important aspect of this work is that the authors dissected the transcriptional signaling pathway that induces MDCs in a much more physiological metabolic transition, which complements the more common use of chemical compounds. They had previously shown that overexpression of individual outer membrane proteins could lead to MDCs, but here the Hap4 expression offers a new condition to show that the canonical induction of mitochondrial biogenesis leads to MDC shedding. Overall, the data are of high quality, the findings are clear, and the work provides important new insights into the regulation of MDC formation.

Weaknesses:

There are a few points that should be addressed.

(1) MDCs are almost exclusively monitored through GFP-tagged TOM70, and the authors do not show the inclusion of any endogenous cargo. The evidence for their fate in the vacuole is through the appearance of cleaved, free GFP after 6 hours that is dependent on ATG5, Dnm1, Pep4, etc. Can the authors demonstrate the appearance of MDCs without expressing any GFP tags and instead monitor known outer membrane cargoes? In the case of Hap4 expression, the proteomics identifies some very highly induced mitochondrial proteins, and there surely must be some with antibodies that can detect the protein by IF and Western blot.

(2) There is a very unexpected ~10X increased in a sporulation factor SPO21 upon induction of Hap4. I see no evidence of sporulation, and it's not long enough for stationary phase. Is the increased mitochondrial biogenesis driving a specific metabolic state of these cells that is signaling to other biology?

(3) It is important to understand the kinetics and stoichiometry of outer membrane loading that drives MDCs, and their transit to the vacuole. This is why it would be highly informative to monitor some endogenous cargoes (previous point). In the review the authors cite (NRMBC, Pfanner lab 2019), it was stated that the import machinery is not generally increased upon metabolic induction of mitochondrial gene expression. Therefore, (pre-MDCs) the field concluded that the import machinery has a very high capacity for the rapid biogenesis of newly synthesized proteins, along with regulation through the phosphorylation of import receptors (ie; the work of Meisenger). Consistent with this, the Hap1 proteomics did not show any increases in the core import machinery, while ETC subunits and a large swath of mitochondrial proteins were elevated over 2-fold (I looked carefully through the Excel sheet). Since MDCs are induced transiently about 2 hours after glucose deprivation, and fully dependent on de-repression of Mig1, the authors are right to imply that this is coupled to the import of newly synthesized proteins.

However, it seems to me that MDCs are being formed at very early stages of mitochondrial protein expression, not after they have necessarily "overloaded" the outer membrane. The Hap4 proteomics after 3.5hr of induction would suggest that the bulk of the mitochondrial proteins have been successfully inserted (no import failure) and are likely already functional (metabolizing). I'm trying to understand the percentage of the proteins that would be incorporated within MDCs, as the mitochondria appear to handle the bulk of their newly inserted proteins without issue. How can the authors adapt their "free GFP" assay to understand the stoichiometry of the transport of endogenous, newly imported outer membrane proteins to the vacuole?

(4) As a last theoretical point for discussion: Can the authors exclude that MDCs are not functional or play a signaling role? Given the emerging work on SPOTs (Lena Pernas), and from the new evidence from Craig Thompson's lab that there can be very specific functional mitochondria (oxidizing vs reducing), it is possible that MDCs are not simply there to be degraded. They last at least 3 hours, which is a long time for yeast (budding cycle 90 min, 3 hours in glucose deprivation). Taking the data presented here very objectively, there is no direct evidence that the cargoes within MDVs reflect any failure to import, or that they are damaged in any way. The deletions of Tom70/71 have way too many pleotropic effects and essentially demonstrate only that the MDC cargoes came from the mitochondria. It could be helpful if the discussion also positioned these MDC mechanisms within the context of other aspects of selective mitochondrial-related compartments that have been emerging in the literature.

Reviewer #3 (Public review):

Summary:

In this manuscript, Price et al. report the physiological conditions and proteins involved in the formation of mitochondria-derived compartments (MDCs), specialized domains exclusively containing outer mitochondrial membrane (OMM) proteins, in budding yeast. Hughes and his colleagues have previously established MDCs as unique multilamellar membrane structures derived from the OMM that arise with both mitochondrial metabolic perturbation and hydrophobic OMM protein load. Whether cells undergo MDC formation in response to physiological changes in mitochondrial biogenesis remains to be explored. In this study, the authors sought to test if glucose restriction, carbon-source switching, and salt stress can induce MDC formation, and found that these situations, which naturally promote acute mitochondrial biogenesis concomitantly with metabolic transitions, trigger MDC induction. Under these conditions, loss of Snf1, an AMP-activated protein kinase that facilitates mitochondrial biogenesis under metabolic stress, almost completely abolished MDC formation. Snf1 induces MDC induction under metabolic stress via phosphorylating (suppressing) Mig1, a transcriptional repressor of mitochondrial biogenesis. Consistent with this idea, loss of Mig1 mostly rescues MDC formation under glucose restriction or salt stress in cells lacking Snf1. The authors further found that acute induction of Hap4, a core activator of mitochondrial biogenesis, is sufficient to trigger MDC formation even without metabolic stress. Finally, cells lacking Tom70 and Tom71, protein receptors of the TOM (translocase of the outer membrane) complex that mediate targeting of hydrophobic mitochondrial proteins, almost failed to form MDCs under glucose restriction. Correctively, the authors propose that MDCs act in the reduction of OMM protein load upon metabolic stress-induced acute mitochondrial biogenesis.

Strengths:

The experiments for this study are well-designed, and the resulting data are mostly convincing, with proper controls and significant statistics to support their conclusions. The paper potentially provides new insights into the physiology of MDC formation.

Weaknesses:

There are only a few new mechanistic advancements in this paper.

Reviewer #1 (Public review):

Summary:

Escalante et al. employ super-resolution microscopy to achieve a clearer, nanoscale view of how trans-sialidases and mucins are organized on the Trypanosoma cruzi parasite membrane. Comparing the experimental data using clustering analysis with model-based simulations, they report two kinds of organizational states describing the non-uniform distribution of these two proteins: a segregated state where mucins and trans-sialidases form spatially distinct nano-clusters, and a non-clustered state where they share a proposed fibrillar network with more ordered, shorter-than-random separation distances. They also look at the oligomerization states of the two proteins to try and propose a mechanistic basis for the observed distributions.

Strengths:

The in-depth analysis of the distributions of both proteins coupled with model-based simulations brings out new insights into organizational principles underlying protein distribution on the membrane surface. The ability to resolve shorter-than-random separation distances even in the non-clustered state is to be highlighted and is a key take-away from this manuscript.

Weaknesses:

The authors propose the oligomeric state of mucins compared to the non-oligomeric trans-sialidases as a basis for explaining the distinct organization of these proteins. Although this hints at how segregation may occur, it does not inform us of how the more ordered non-clustered state could co-exist with the clustered segregated state and warrants further investigation.

Overall, the analytical framework applied in this study to elucidate organizational principles for the non-uniform distribution of proteins can potentially be used in a wide-range of contexts across different organisms and systems. This study also lays the groundwork to understand mechanisms that spatially regulate how trans-sialidases act on their substrates. Going forward, it could be very interesting to look at how different kinds of mucins and trans-sialidases are organized with respect to one-another and amongst themselves. Also, the development of tools to observe the dynamics of these proteins live will likely provide further insights into the mechanism.

Reviewer #2 (Public review):

The manuscript describes a numerical analysis of the domains of the T. cruzi cell surface containing different proteins. It has the potential to be of great interest.

I do not have the expertise necessary to comment on the image collection or analysis.

I have one concern: the amount of manipulation of the cells prior to fixation; these were clearly stated in the methods, which is good.

My concern is whether these manipulations prior to fixation alter the observations. The 'Labelling sialic acid acceptors' involves >6 centrifugations and >90 minutes incubation in PBS prior to fixation, and the 'immunostaining' protocol involves cells 'extensively washed with PBS' prior to fixation. I would like to suggest that the authors do controls in which they compare the pattern of anti-SAPA staining under four conditions.

(1) Cells fixed in culture by the addition of paraformaldehyde to 4%, followed by blocking and PBS washes.

(2) Cells fixed in culture by the addition of paraformaldehyde to 4% and glutaraldehyde to 0.2% followed by blocking and PBS washes.

(3) Cells fixed by the 'labelling sialic acid acceptors' protocol.

(4) Cells fixed by the 'immunostaining protocol'.

Reviewer #3 (Public review):

Summary:

The authors present an innovative approach to tackle the lateral organization of mucins and trans-sialidases (TS) on the cell membrane of the organism Trypanosoma cruzi. By applying dual-color super-resolution microscopy (STORM), the authors report on a differential nanoscale distribution between mucins and TS on the cell membrane. Moreover, they find that 60% of mucins and TS are organized in nanoclusters with an inter-nanocluster distance following a random distribution. The remaining 40% of both proteins are organized in a non-random manner, and, using simulations, the authors claim that they are organized in rectilinear fibers.

Strengths:

The authors use dual-color STORM microscopy to unravel the protein nanoscale organization of mucins and TS on the cell membrane of Trypanosoma cruzi for the first time. They perform a dedicated analysis of the localizations and clustering of both proteins. Moreover, they perform, for every type of analysis on real data, simulations to compare their results for random organization. They also use an analysis approach together with simulations to propose that the lateral organization of both non-clustered proteins are within rectilinear fibers. They also complement their microscopy findings with BN-PAGE. Overall, the use of advanced microscopy techniques, corresponding data analysis and simulations is very solid and remarkable.

Weaknesses:

As the authors point out, they do not provide a molecular/biophysical mechanism explaining the non-random lateral organization of mucins and TS (both clustered and individual proteins).

Reviewer #1 (Public review):

Summary:

This report seeks to understand the mechanisms whereby the ferroptosis inducers ML162 and erastin cause cell death in several tumor cell lines. They present evidence that caspase-5 is activated and required for ferroptosis, but other caspases, including caspase-1 and -4, are not important. Surprisingly, caspase-5 cleaved and activated GSDME, instead of the expected gasdermin target GSDMD

Strengths:

The magnitude of effect for triggering ferroptosis by ML162 and erastin is strong, and the strength of inhibition by YVAD is also very strong, making these effects convincing. The lack of effect of DEVD, which inhibits apoptotic caspases, is also convincing. Also, the lack of effect of necrostatin is convincing. These negative results strengthen the positive results seen with YVAD.

Inhibition by disulfiram is convincing.

Caspase-5 knockout single-cell clones and the ability to complement these with caspase-5, but not catalytically inactive caspase-5 in Figure 5, is strong data.

Weaknesses:

(1) Prior publications have asserted that ferroptosis is caspase-independent. Can the authors repeat some of these experiments directly to reveal whether there was an error in the published work that resulted in missing the phenotype for a caspase in ferroptosis? In my experience, caspase inhibitors sometimes only delay cell death because they are not 100% effective, especially over hours of time. Can the authors repeat the prior experiments to reveal whether this caveat affected previously published data? At the least, the authors should use the z-VAD-fmk and Boc-D-FMK inhibitors to determine whether they give the same effects as YVAD to rule out a very unlikely possibility that these "pan-caspase" inhibitors do not inhibit caspase-5.

a) The original report describing ferroptosis by Dixon and Stockwell, doi: 10.1016/j.cell.2012.03.042, shows that erastin treatment-induced ferroptosis is not affected by z-VAD-fmk in 3 cell lines.<br /> b) A later report from Dr. Stockwell states in data not shown that a different pan-caspase inhibitor (Boc-D-Fmk) does not block erastin-driven ferroptosis. Doi 10.1016/S1535-6108(03)00050-3<br /> c) An earlier 2008 report from Dr. Stockwell shows that z-VAD-fmk and Boc-D-fmk do not rescue cells treated with RSL-3 or RSL-5 treated cell lines derived from BJ cells. doi 10.1016/j.chembiol.2008.02.010<br /> d) A recent paper shows a delay of ferroptosis after RSL3 treatment by pan-caspase inhibitor Q-VD-OPh. Doi 10.1038/s41418-025-01514-7. The delay was about 8 hours in time, so cells were still dying.<br /> e) Gpx4 knockout cells or erastin or RSL3 treatment are unaffected by z-VAD-FMK. Doi 10.1038/ncb3064<br /> f) I encourage the authors to do more thorough searching of the literature to find more publications that have used caspase inhibitors.

(2) The authors should discuss how mouse cells can undergo ferroptosis while they do not encode caspase-5, and the evolutionary conservation of caspase-5 in general. If caspase-5 is not encoded by an animal (as is the case with mice), can their cells undergo ferroptosis?

(3) Disulfiram is not a specific inhibitor. It is a nonspecific inhibitor that modifies cysteine residues of many proteins. This should be described in more detail so the reader can appreciate the strengths and weaknesses of the inhibitor.

(4) I encourage the authors to assess IL-1β processing by Western blot and show that this is inhibited by YVAD. Because ELISA can detect release of the pro form after lytic cell death by other mechanisms.

(5) ASC knockdown in Supplementary Figure 3a for two cell lines is not sufficient to draw any conclusions in Figure 3a.

(6) Caspase-5 can be more specifically inhibited by LEVD inhibitors. Can the authors show that these work as well?

(7) I would like to see a positive control in Figure 5a to show what a strong caspase signal activity looks like.

(8) Since caspase-3 is known to cleave GSDME, the authors need to assess whether caspase-3 is also activated, and whether other caspase-3 target proteins are also cleaved. There are many to choose from. Caspase-3 western blots, including with the cleaved caspase-3-specific antibody, are critical. This is in addition to the blot shown in Supplementary Figure 10. Positive controls should be included. It is important to continue to add controls to rule out caspase-3, with more than just negative data with DEVD inhibitors and the western blot in Figure S10.

(9) The data in Figure 6c are not strong.

(10) One would expect that any mode of activation of caspase-5 should lead to its proteolytic activity upon its preferred substrates, so LPS should cause caspase-5 to cleave GSDME and not GSDMD. Additional data to strongly activate caspase-5 with LPS should be investigated to see if this leads to GSDME cleavage and pyroptosis via GSDME and not GSDMD.

Reviewer #2 (Public review):

Summary:

In the submitted manuscript, Akter et al use a series of ferroptosis inhibitors in mesenchymal-like ovarian cancer cells and discover that the ferroptosis inducers induce cell death that is inhibited by pyroptosis inhibitors, namely YVAD-fmk and disulfiram, which inhibit pore formation by gasdermin D (GSDMD). Remarkably, the authors also saw the release of IL-1β in response to ferroptosis inducers. Unexpectedly, they did not observe the involvement of caspase-1 but rather observed that caspase-5 was activated in response to the ferroptosis inducers. Moreover, they found that caspase-5 directly cleaves GSDME in response to the ferroptosis inducers, establishing CASP5/GSDME as downstream executors of ferroptosis.

Strengths:

These findings are interesting because only CASP1 is known to induce IL-1β maturation, and their data suggest that CASP5 rather than CASP1, is responsible for IL-1β activation in the context of ferroptosis inducers. Notably, CASP3 is the only caspase reported to be able to cleave GSDME, so the identification of CASP5 as a driver of ferroptosis in this context is a significant finding. They genetically show that loss of CASP5 and GSDME knockdown inhibits cell death in response to the ferroptosis inducers ML162 and Erastin, which is evidence that they play a role in this context.

Weaknesses:

The major findings in this paper are interesting, but the data presented do not robustly support the claims made in this paper. For example, they claim that CASP5 is responsible for the activation of GSDME by cleaving it directly to induce cell death. They try to rule out the involvement of CASP1, ASC, and CASP4 using siRNA targeting these genes, but the knockdowns are incomplete, and the loading controls are inconsistent. They also claim they do not see GSDMD or CASP3 cleavage and activation but use negative data to make that claim. It is unclear if the antibodies used can detect cleaved GSDMD or CASP3 as they do not include a positive control to show that they can indeed detect these activation events if they were occurring. This needs to happen in the same experiment - they need to show in the same experiment with the same lysates that they can detect CASP5, GSDME and IL-1β activation but not CASP1, GSDMD, CASP4, or CASP3 activation. Of course, they should include agonists for positive controls of CASP1, CASP4 and GSDMD activation, which are lacking in the current manuscript.

Notably, the major evidence supporting a direct role for CASP5 cleavage of GSDME is one Coomassie gel using recombinant CASP5 and GSDME, but there were too many non-specific bands, and the full-length uncleaved protein could not be detected even in the untreated lanes. The authors need to show a gel where the protein can easily be identified and should also include a positive control protein like GSDMD to show the relative cleavage efficiency of GSDME compared to a known substrate. It would also be great to compare this to CASP3-mediated cleavage of GSDME. With recombinant proteins, calculating the catalytic efficiencies would be the best way to ascertain if this is biologically similar to other known substrates.

The way that ferroptosis is defined, it is caspase-independent, and pyroptosis is defined as gasdermin-mediated cell death. Given that these agents lead to activation of CASP5/GSDME, it would be more accurate to say that these ferroptosis inducers also induce CASP5/GSDME-dependent pyroptosis, as opposed to them being the executors of ferroptosis. This can be a distinct mechanism/pathway from the ferroptosis pathway, as multiple cell death pathways can be initiated in cells. Consistent with this, ferrostatin-1 also inhibited cell death, likely due to inhibition of the ferroptosis signaling cascade. It is unclear if this pathway is upstream of the caspases. How these ferroptosis triggers selectively activate CASP5 and not CASP4 to induce GSDME cleavage is a major unresolved question. Notably, it is also unclear if this biology is specific to the mesenchymal-like cells used in this study or if it expands to other cells.

Reviewer #3 (Public review):

Summary:

Akter et al. identify caspase 5 activation and Gasdermin E cleavage as a novel downstream executioner of ferroptotic cell lysis induced by erastin and ML162. These data are novel and very interesting to the wider cell death community.

Strengths:

Strengths of the study include the use and validation of findings in several mesenchymal ovarian cancer cell lines, the rigorous validation using small molecule approaches, siRNA-mediated silencing and CRISPR/Cas9-mediated knockouts with re-expression.

Weaknesses:

A weakness of the study is the fact that ferroptosis was not induced genetically (GPX4 ko) and, hence, off-targets of the mode of induction cannot be ruled out at this point (e.g. ML162 also targets TrxR1). Moreover, it would be vital to understand at which point in ferroptosis execution caspase 5 is activated in a time-resolved kinetic together with lipid ROS tracing to also obtain hints as to its possible activation.

Conclusion:

Despite the weaknesses described, this is a very interesting, timely, and well-executed study with the described limitations. The work provides important mechanistic insights into the interplay between ferroptosis and pyroptosis with possible consequences for inflammatory responses.

Reviewer #1 (Public review):

Summary:

The authors conducted a comparative acoustic analysis of primate vocal repertoires, focusing on the assumption that speech and language evolution required and involved an expansion in the acoustic space of voiced vocalizations from non-human primates to humans. Results challenge this idea. The study compiles and analyzes a large dataset of calls to quantify differences in vocal production space.

Strengths:

The study is technically sound, with a solid implementation of acoustic measurements and a valuable new dataset that brings empirical rigor to test a dominant, yet hitherto strictly theoretical, notion about what speech and language evolution entailed. It provides concrete comparative acoustic data across species to disprove that speech and language required an increase in the range of voiced calls, and thus, by extension, of vowels. The approach is methodologically rigorous and directly engages with the relevant data, rather than relying on untested presumptions of what great apes "ought" to be able to do or not.

Weaknesses:

The theoretical contextualization should be strengthened and updated, as several aspects contain inaccuracies, most notably by equating voiced calls or vocalizations with speech (overlooking the critical role of consonants, as human languages typically show vowel:consonant ratios of 1:4 or greater) and misrepresenting the premises and current status of the neural (Kuypers-Jürgens) hypothesis.

The discussion drifts into speculative territory on features like syntax and co-articulation that fall outside the paper's scope and data, and it does not sufficiently engage recent evidence on vocal learning and consonant-like capacities in great apes.

Minor issues include incomplete sampling justifications, imprecise terminology, and reliance on references that have been critiqued in more recent work.

Reviewer #2 (Public review):

This study examines the evolutionary context of the emergence of human speech. The authors address the widely held hypothesis that the expansion of the human vocal space, resulting from modifications of the vocal tract, was a key prerequisite for the evolution of spoken language.

To test this hypothesis, the authors quantified the acoustic space of human speech, non-linguistic vocalizations, and musical vocalizations and compared it with that of nonhuman primates, chimpanzees, bonobos, and chacma baboons.

The authors found that speech and song occupied significantly less volume in the acoustic space than human non-linguistic vocalizations. In addition, the acoustic-feature volume of speech and song was not statistically distinct from that of non-human primates. Accordingly, the authors conclude that the evolution of human speech did not depend on an expansion of the human vocal acoustic space.

I find the analysis presented in this manuscript highly convincing. It is conducted at a contemporary scientific standard, and the results provide strong support for the authors' conclusions. I particularly appreciate that the authors explicitly discuss the limitations of their approach. For example, they acknowledge that MFCCs cannot capture all aspects of acoustic structure.

I have only three minor comments:

First, the authors may wish to briefly summarize the main findings of the study by Anikin et al., as it represents the central reference for the present work. A concise summary in two or three sentences would help readers who are not familiar with that study.

Second, I would appreciate a brief explanation of why the authors chose this particular statistical approach.

Third, the authors could briefly mention that the Chacma baboon dataset provides a very comprehensive representation of the vocal repertoire of this species, although a small number of rare vocalizations are not included. I am not sure whether a similar limitation also applies to the chimpanzee and bonobo datasets, but if so, it would be useful to mention this as well.

Reviewer #1 (Public review):

Summary:

The authors develop a GFP-LC3-RFP autophagy reporter under the control of the Rosa26 locus to measure autophagic flux in mouse embryos as well as adult tissues. While image quantification is consistently used, the authors also develop a semi-high-throughput assay for measuring autophagic flux using a microplate reader. Additionally, the authors cross these mice with a Cre-inducible Atg5-deletion mouse model, allowing the investigation of how autophagy flux is affected upon loss of Atg5. With this model, they demonstrate that loss of Atg5 leads to an increased ratio of GFP/RFP intensity in multiple tissues, including the brain, revealing that the brain undergoes basal autophagy. They further go on to show that the increase in GFP/RFP intensity upon Atg5 loss is greater in adult tissues compared to their embryonic counterparts. The development of an animal model, along with quantitative tools to measure the model, will have a high impact on the field. However, the analyses from the data presented do not fully justify the conclusions.

Strengths:

(1) A mouse model to better measure autophagy.

(2) The plate-reader-based method to quantify autophagy across tissues.

(3) Assessment of autophagy in many different tissues.

(4) Crossing the reporter mouse with the Atg5f/f mouse to assess basal autophagy.

Weaknesses:

(1) While the tool is of high impact, there is little new biological or mechanistic insight provided in these studies.

(2) The quantification and normalization method is unclear, making it difficult to compare across tissues accurately.

(3) Differential expression across cell types is not well documented or taken into account for comparisons.

(4) There is no consideration for sex as a biological variable.

Reviewer #2 (Public review):

Summary:

The aim of the authors was to measure starvation-induced and basal autophagy in vivo across several tissues and developmental stages. For this, they developed a novel mouse model expressing the GFP-LC3-RFP reporter. They also aimed to provide a more high-throughput method for autophagy flux measurements than assessment by imaging and developed an assay based on a microplate reader.

Strengths:

(1) Good validation of the mouse model. The knock-in strategy is well explained and illustrated.

(2) The model has potential to be applied to a wide range of research questions. The Cre-dependent expression allows for customization of KO timing, which will be beneficial in developmental studies.

(3) The authors presented consistent findings using two different methods to quantify autophagy, strengthening the robustness of their results.

(4) The authors demonstrated the validity of the high-throughput method (microplate reader).

Weaknesses:

(1) The comparison of neuronal populations in different areas of the brain is not ideal. In the cerebellum, Purkinje cells were chosen, which are rare and not representative of this tissue, as well as functionally very different from the neurons in the hippocampus and cortex that they were compared to.

(2) The explanation of the GFP-LC3-RFP construct and specifically if/how autophagosome formation can be measured and distinguished from flux could be clearer.

Conclusion:

The work presented is thorough, and the authors achieved their goals for this study. The effort used to further investigate unexpectedly high basal levels of autophagy in the brain is well appreciated and adds value to this paper. The conclusions of the authors are mostly very well supported by the data provided. The well-structured description of the results, along with clear figures, allows the reader to comprehend the authors' reasoning in reaching their conclusions.

The presented mouse model has great potential for a lasting positive impact on the research field of in vivo study of autophagy. The method of utilizing a microplate reader will also benefit future research where semi-high throughput is an advantage. Together, the information provided in this study not only presents new methodology that will allow the investigation of new research questions, but also provides novel information about in vivo autophagy flux at the selected developmental stages that opens up new follow-up research questions.

Reviewer #1 (Public review):

We appreciate the authors have provided answers to many of the points we raised, and the changes made to their manuscript, which we think strengthen the overall evidence presented. However, we find that some important controls are still missing across experiments.

Major comments:

(1) Shortcomings in Immunofluorescence experiments:

a. Antibody cross-reactivity was only tested against CK1ɛ, but should also be tested against CK1α, which is abundant in U2OS cells, and is also known to be involved in cell-cycle regulation.

b. Fig. 1: Statistical analyses are missing from the analysis.

c. Fig. 2: No colocalisation analysis shown for figure 2, only some arrowheads pointing to puncta. Appropriate colocalisation statistics are important since for practical reasons, only a few representative images can be shown on the figure.

d. Fig. 6: Even if the figure is illustrative, it is important to show centrosome staining to visualise CK1ẟ's recruitment to the centrosome in G2/prophase, especially since this information is used to propose the model in figure 7.

e. For all figures: Please mention the number of independent biological replicates in the figure legends (1, 2, 6). For figure 1, if there are 3 independent biological replicates, the quantification should take all of them into account (as opposed to the data points corresponding to 10 cells), and statistics must be done appropriately, taking those independent replicates into account. Same for the colocalisation analysis in figure 2 once you include it.

(2) Shortcomings in biochemistry experiments:

On CalA control, this is not a matter of confirming that CalA treatment works in principle, but rather to confirm that CalA treatment worked in this specific replicate. Aliquots may lose potency (e.g. with freeze-thaw cycles / exposure to light), hence checking for enrichment of phospho-proteins is essential to confirm the treatment was successful in this particular instance. In the worst-case scenario, the company may have sent the wrong compound altogether! A positive and a negative control is the basis for every experiment to make meaningful interpretation. On a separate note, many experiments have control and siRNA or compound treatments on two different gels - this should be rectified as they are meaningless if different exposures have been selected for different immunoblots.

(4) As the authors mention, the kinase is not fully inactive when tail phosphorylated. Recent research has also suggested that tail-phosphorylated CK1ẟ may show increased catalytic activity for a few select, specific substrates, in the co-occurrence of pT220 (Cullati et al., 2022; Cullati et al., 2024). It is thus tricky to directly infer that phosphorylated CK1ẟ is inhibited, when no positive control for CK1ẟ inhibition was shown in the evidence presented. It would be necessary to either nuance your claim or include a positive control for CK1ẟ inhibition. Please revise statements in the manuscript accordingly.

(5) It would be important to include statistical analyses for the immunofluorescence data in Fig. 1 and 2.

(9) The authors mentioned "In the eLife study, we show that inhibition of kinase activity by PF670462 stabilizes CK1δ and that the overexpressed kinase-dead mutant CK1δ-K38R is stable." Unfortunately, the data from biochemical analyses presented in the eLife publication is uninterpretable due to a lack of loading controls.

(10) While the data presented in Penas et al. strongly suggests a link between CK1ẟ stabilisation and the APC/C-Cdh1 complex, it is the only study to have shown it. Given that (1) science relies on data reproducibility and (2) your proposed model relies heavily on the relationship between CK1ẟ stabilisation and the APC/CCdh1 complex, it would be appropriate to include the investigations mentioned in our original comment.

Reviewer #2 (Public review):

In this study, Serrano et al. employed a combination of cell biological and molecular approaches to investigate the localization and regulation of Casein Kinase CK1 during the cell cycle using U20S cells. They show that CK1 dynamically localizes between the centrosomes and the nucleus but can be sequestered away from the centrosomes upon overexpression of its binding partner PER2. They provide evidence that CK1 WT but not a phospho-null mutant strongly accumulates in a hyperphosphorylated form upon inhibition of phosphatases (using Calyculin and Okadaic Acid) and thus conclude that CK1 tail phosphorylation protects the kinase from degradation. Using synchronized cells, they show that CK1 accumulates unphosphorylated in S-phase (APC/Cdh1 inactive) but phosphorylated at the G2-M transition. Immunostaining shows that CK1 localizes to the centrosomes during mitosis.

The manuscript has improved overall, but some sections are still inconclusive and require clarification.

Major comments:

Figure 1 is inconclusive. CK1 nuclear staining is highly similar in untreated cells and in cells treated with CHX + PF670462. The reduction in centrosomal staining in these cells is barely significant. However, the authors draw very strong conclusions from these data sets. In panel B, the cells appear to have been fixed incorrectly, and the anti-PCNT shows a strong background signal. Not convinced that immunofluorescence is the best approach to look at protein dynamics in vivo.

In Figure 2, panel B, the authors should co-stain the centrosomes of cells that co-express CRY1 and CK1, as some of these dots may represent the centrosomes.

Figures 3B, please provide information on the non-phosphorylable CK1a mutant (it is mentioned as a variant in which all serine and threonine residues in the C-terminal tail were replaced by alanine). Specify the number of sites mutated and their exact position. Is this non-phosphorylable CK1a version catalytically active? Treatment of samples with inactivated PPase should be used as a control.

Strengths:

The authors reveal that the activity and abundance of dephosphorylated and phosphorylated CK1δ are regulated in a cell cycle-dependent manner. This suggests that these different pools are associated with distinct physiological functions.

Weaknesses:

Unfortunately, some of the data are inconclusive, and there is no data/information linking the cell cycle regulation of CK1δ to its function during the cell cycle.

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.]

This study provides evidence that the apicoplast-locaized isoform of acyl-carrier protein (ACP) has acquired important non-enzymatic functions in the malaria parasite. Previous studies have shown that the apicoplast-located FASII-dependent pathway of fatty acid synthesis is not essential in Plasmodium blood stages. In contrast, genome-wide knockout studies suggested that ACP, a key protein in this pathway, is essential in these stages, indicating that it may have additional non-canonical functions. In this study, the authors confirm that ACP is essential in Pf blood stages (using both apicoplast IPP rescue and conditional knockdown); show that this essential function requires modification with 4-phosphopantetheine and use proximity biotinylation and complementary immunoprecipitation pull-down approaches to provide compelling evidence that ACP binds to and stabilizes the apicoplast-located isoform of pyruvate kinase II. Notably, these interactions appear to differ from those associated with the binding of mitochondrial isoforms of ACP to proteins involved in Fe-S biosynthesis. Loss of ACP was shown to lead to a decrease in PKII levels and apicoplast DNA/RNA synthesis, consistent with loss of NTP synthesis in this organelle. The data are clear and very well described, and the findings represent a significant advance in our understanding of metabolic regulatory mechanisms in apicomplexan apicoplast studies.

Strengths:

The study uses a variety of complementary genetic approaches to demonstrate the essentiality of ACP and the enzyme involved in its activation with 4-PP in Pf blood stages, demonstrating that the ascribed non-enzymatic function is mediated by holo-ACP. Similarly, a number of complementary biochemical approaches, including proximity biotinylation, immunoprecipitation, and co-expression of PfACP and PK-II in a heterologous bacterial expression system, are used to confirm the physiological significance of the PfACP and PK-II interaction. The study also reports additional findings, such as the independence of P. faciparum blood stages on exogenous (media) fatty acids, indicating that intracellular stages can salvage all of their requirements from the red blood cell.

Weaknesses:

Overall, this is a very strong study. While questions remain around the function of other apicoplast ACP-interacting proteins detected in this study, I don't have any suggestions for significant improvements.

Reviewer #2 (Public review):

This study focuses on revealing the essential divergent function of the Acyl Carrier protein (ACP) in the deadliest human malaria parasite, Plasmodium falciparum. More precisely, using inducible KO, cellular and biochemical approaches, the authors determined that instead of a canonical role for ACP allowing the de novo synthesis of fatty acids in the apicoplast (essential relict plastid) of the parasite, the enzyme couples with pyruvate kinase II to generate nucleoside triphosphate to maintain parasite survival during blood stages. The study is novel, well-designed, providing interesting new data on Plasmodium and apicomplexa biology. The results convincingly support the major claim of the study. However, it is currently incomplete to support some claims on the essentiality of some apicoplast pathways.

In this study, Geher et al. focused on deciphering the role of the Acyl Carrier Protein (ACP) present in the relict non-photosynthetic plastid, i.e. the apicoplast of the most lethal human malaria parasite, Plasmodium falciparum. More particularly, they determined an essential function of ACP independent of its usual/typical function as the central protein for the normal function of the apicoplast Type II fatty acid synthesis (FASII) pathway. Rather, the protein seems to associate with the apicoplast Pyruvate Kinase II, together generating an essential nucleoside triphosphate (NTPs) source to fuel the apicoplast and parasite survival instead.

By generating a TetR-DOZY-based inducible KD line for ACP, they confirmed that the protein is indeed essential to maintain apicoplast integrity and parasite survival during asexual blood stages, as previously predicted and experimentally shown. They showed that ACP requires a biochemical modification, typically activating the protein for its function in the FASII pathway, i.e. binding of the 4-PP group by holoACP synthase. Then, they showed that the other enzymes of the FASII pathway are likely dispensable during the blood stage, as they were able to generate a KO line of the first enzyme of the pathway, FabD (which was predicted to be essential in P. falciparum). Based on a cell culture approach in a controlled culture medium, they further claimed that, unlike current evidence-based hypotheses, the FASII pathway (and thus a potentially FASII-linked ACP) has no role/activity during blood stages. Using a proximity biotinylation approach, they determined that ACP associates with the apicoplast pyruvate Kinase II (PKII), previously shown to generate NTPs in the apicoplast for energy and DNA/RNA maintenance (Xia et al. 2019), and not to fuel the FASII pathway as its main function in blood stages. Finally, they showed that the disruption of ACP induces the reduction of the presence/content in PKII in the parasite, as well as the drastic reduction of the apicoplast DNA and RNA content. Together, they concluded that the main function of ACP is indeed the NTP formation via its association with PKII, rather than its canonical role for the generation of fatty acids in the apicoplast.

This study is novel and focuses on a topic of particular interest in malaria biology, but also for most of the apicomplexa-related diseases, and beyond for plastid bearing orgnaisms and this unusual role for ACP. The study is well thought out with proper biochemical approaches that convincingly point to this association of ACP with PKII for NTP synthesis as a major function during P. falciparum blood stages.

Reviewer #1 (Public review):

Summary:

This manuscript addresses an important question in cardiac biology: whether distinct cardiomyocyte (CM) subpopulations play specialized roles during heart development and regeneration. Using single-cell RNA sequencing and newly generated genetic tools, the authors identify phlda2 as a specific marker of primordial cardiomyocytes in the adult zebrafish heart. They further show that these primordial CMs function are essential for myocardial morphogenesis and coronary vascularization but are dispensable for myocardial regeneration or revascularization after injury. These findings indicate that heart regeneration doesn't simply recapitulate developmental processes.

Strengths:

A major strength of the study is the generation of a phlda2 BAC reporter, which provides a specific and reliable marker for primordial cardiomyocytes. The lack of genetic tools has previously limited functional analysis of this CM population. By using phlda2 regulatory elements to generate reporter and NTR-based ablation lines, the authors can visualize and selectively manipulate primordial CMs in vivo. This enables a direct functional interrogation rather than relying on lineage tracing or correlative evidence. Through genetic ablation, the authors convincingly demonstrate that primordial CMs are essential for myocardial morphogenesis and coronary vascular organization during development but are not necessary for heart regeneration.

Weaknesses:

(1) The manuscript would benefit from clarifying whether the primordial cardiomyocytes ablation affects epicardial cell behaviors during heart development, given that the well-established role of the epicardium in supporting coronary vessel growth, it is possible that the vascular phenotypes observed after primordial CM ablation may be affected, at least in part, by altered epicardial cells.

(2) Because primordial cardiomyocytes form a dense, single-cell-thick layer covering the ventricular surface, it would be informative to determine whether their loss alters the spatial distribution or inward migration of coronary endothelial cells or epicardial cells.

(3) The manuscript carefully examines the relationship between primordial CMs and gata4⁺ cardiomyocytes during regeneration. However, their relationship during heart development should be more fully addressed.

(4) As loss of cardiomyocytes is known to induce gata4:GFP activation during regeneration, it would be important to determine whether ablation of primordial cardiomyocytes alone triggers gata4:GFP expression in neighboring cardiomyocytes. This analysis would further support the conclusion that primordial cardiomyocytes are not required for regenerative responses.

Reviewer #2 (Public review):

Summary:

In the manuscript "Primordial Cardiomyocytes orchestrate myocardial morphogenesis and vascularization but are dispensable for regeneration", Sun et al. identify a novel marker of primordial cardiomyocytes and use it to visualize and ablate the population during development and regeneration. The role of the primordial layer has not been investigated because the tools to manipulate this population have not existed. The manuscript is straightforward, easy to understand, and addresses an important question that has not been explored.

While the manuscript provides important insights into the role of primordial CMs, backed by a convincing methodology, the authors should clarify their requirements for heart development and maturation. Specifically, is the primordial layer required for the fish to survive? Do primordial CMs regenerate when ablated during development, and do the defects observed (in trabecular and compact CMs and coronary vessels) resolve after 10 days post-treatment when they were detected?

Strengths:

The major strengths are the identification of a marker that enables manipulation of primordial cardiomyocytes and the tools generated by the team.

Weaknesses:

The major weakness is not considering the longer-term consequences of primordial layer ablation during development, as it is unclear whether the animals succumb to the acute cardiac defects observed or fully recover.

Reviewer #3 (Public review):

Summary:

The authors performed single-cell RNA sequencing of adult zebrafish hearts and identified markers for distinct cardiomyocyte subpopulations. One marker, phlda2, marks primordial cardiomyocytes. They generated transgenic reporter lines to characterize phlda2 expression patterns and a phlda2-NTR ablation line to determine the functional requirement of primordial cardiomyocytes during heart regeneration. They found that phlda2+ primordial cardiomyocytes are essential for myocardial morphogenesis and coronary vessel development. Interestingly, when phlda2+ primordial cardiomyocytes are ablated during heart regeneration, gata4+ cortical cardiomyocytes, coronary vessel revascularization, and scar tissue formation are not affected.

Strengths:

The authors identified a new primordial cardiomyocyte marker, phlda2. They further demonstrated that primordial cardiomyocytes are important for heart morphogenesis but dispensable for heart regeneration. Their findings reveal a potential difference between heart development and regeneration programs.

Weakness:

Despite the interesting findings, the authors did not provide supplemental data for their scRNAseq to demonstrate the data quality and support their conclusions, and some results are not well described.

Reviewer #1 (Public review):

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

Summary:

The manuscript by Lu and colleagues demonstrate convincingly that PRRT2 interacts with brain voltage-gated sodium channels to enhance slow inactivation in vitro and in vivo. The work is interesting and rigorously conducted. The relevance to normal physiology and disease pathophysiology (e.g., PRRT2-related genetic neurodevelopmental disorders) seems high. Some simple additional experiments could elevate the impact and make the study more complete.

Strengths:

Experiments are conducted rigorously including experimenter blinding and appropriate controls. Data presentation is excellent and logical. The paper is well written for a general scientific audience.

Comments on revised version.

The manuscript by Lu and colleagues has been revised sufficiently to address all my prior concerns.

Experiments are conducted rigorously including experimenter blinding and appropriate controls. Data presentation is excellent and logical. The paper is well written for a general scientific audience.

Reviewer #2 (Public review):

Summary:

As a member of DspB subfamily, PRRT2 is predominantly expressed in CNS and has been associated with various paroxysmal neurological disorders. Previous studies have shown that PRRT2 interacts with Nav and Cav channels, modulating channel properties and neuronal excitability.

In this manuscript, Lu et al. demonstrate that PRRT2 is a potent regulator of Nav channel slow inactivation, promoting the development of Nav slow inactivation and impeding the recovery from slow inactivation. This effect is highly conserved in PRRT2s across species as well as among DspB family members (TRARG1 and TMEM233). The authors further confirmed the interaction between Nav channels and PRRT2 in heterologous expression systems as well as in Prrt2-V5 knock-in mice. Prrt2-mutant mice, which lack PRRT2 expression, require lower stimulation thresholds for evoking after-discharges when compared with WT mice.

Overall, this is a well-executed and methodologically comprehensive study. This work offers valuable insight into the physiological functions of PRRT2 and reveals a potential pathogenic mechanism underlying PRRT2-associated neurological disorders.

The revised manuscript has addressed most of the concerns raised by the reviewers and has been substantially strengthened, although I still have several concerns regarding the discussion section.

Strengths:

(1) Overall, this is a well-executed and methodologically comprehensive study. The electrophysiological data strongly support the conclusion that PRRT2 is a potent regulator of Nav channel slow inactivation. The observation that this regulation is conserved in PRRT2 across species and among DspB family members raises the possibility that altered regulation of Nav channels may also contribute to the pathogenesis of TRARG1- or TMEM233-associated disorders.

(2) Co-immunoprecipitation assay performed using brain tissue from genetically modified Prrt2-V5 knock-in mice provides convincing in vivo evidence for the interaction between PRRT2 and Nav1.2 channels.

(3) Prrt2-V5 KI mice show markedly reduced PRRT2 protein expression and display phenotypes similar to those observed in Prrt2-mutant mice, supporting an important role of PRRT2 in regulating neuronal and network excitability.

Weaknesses:

(1) Nav1.6 is also highly expressed in cortical neurons and is widely regarded as a major contributor to action potential initiation and sustained high-frequency firing. Given that PRRT2 similarly regulates the fast and slow inactivation of Nav1.6 and Nav1.2 channels, the potential contribution of Nav1.6 regulation to neuronal and network excitability should be discussed.

(2) Slow inactivation is generally considered to develop over timescales ranging from hundreds of milliseconds to seconds or longer. Therefore, the statement in Discussion (Page 13, line 381-382) that "slow inactivation develops on a timescale of tens of milliseconds to seconds" may not accurately reflect the conventional kinetic definition of slow inactivation and should be clarified.

(3) Page 14, line 417-430: "question about how Nav channel slow inactivation is regulated in cells that do not express PRRT2".<br /> PRRT2 is unlikely to be the sole regulator of Nav channel slow inactivation. Other molecules and signaling pathways may regulate Nav channel and contribute to neuronal excitability. In addition, neuronal excitability can also be regulated through modulating other Nav properties, such as long-term inactivation or slow recovery from inactivation, as well as through modulating the activity of other ion channels, for example, Kv7.2 and Kv7.3 channels. Therefore, PRRT2-negative cells may utilize alternative mechanisms to fine-tune neuronal excitability. In its current form, this paragraph somewhat overstates the role of PRRT2 and would benefit from a more balanced discussion.

(4) Page 50, Figure 7-figure supplement 2: It would be helpful to include representative traces of the 1st and the last (20th) compound APs in panels B and C.

Reviewer #3 (Public review):

This paper reveals that the neuronal protein PRRT2, previously known for its association with paroxysmal dyskinesia and infantile seizures, modulates the slow inactivation of voltage-gated sodium ion (Nav) channels, a gating process that limits excitability during prolonged activity. Using electrophysiology, molecular biology, and mouse models, the authors show that PRRT2 accelerates entry of Nav channels into the slow-inactivated state and slows their recovery, effectively dampening excessive excitability. The effect seems evolutionarily conserved, requires the C-terminal region of PRRT2, and is recapitulated in cortical neurons, where PRRT2 deficiency leads to hyper-responsiveness and reduced cortical resilience in vivo. These findings extend the functional repertoire of PRRT2, identifying it as a physiological brake on neuronal excitability. The work provides a mechanistic link between PRRT2 mutations and episodic neurological phenotypes.

Comments:

(1) The precise structural interface and the molecular basis of gating modulation remain inferred rather than demonstrated.

(2) The in vivo phenotype reflects a complex circuit outcome and does not isolate slow-inactivation defects per se.

(3) Expression of PRRT2 in muscle or heart is low, so the cross-isoform claims are likely of limited physiological significance.

(4) The mechanistic separation between trafficking of PRRT2 and its gating effects is not clearly resolved.

(5) Additional studies with Nav1.6 should be carried out.

Comments on revised version.

These comments have been addressed in the revised version.

Reviewer #1 (Public review):

Summary:

The study investigates the role of asymptomatic pertussis carriage in transmission between mothers and their infants in particular. The authors use a longitudinal cohort study that involved 1,315 mother-infant dyads in Lusaka Zambia and they utilized qPCR based detection of IS481 to track Bordetella pertussis transmission over time. Insights from the study suggest that minimally symptomatic or asymptomatic mothers may act as a reservoir for B. pertussis transmission in the infants thus challenging the traditional surveillance methods that focus on symptomatic cases. Additionally, the study also identified a subgroup of persistently colonized individuals where mothers were majorly asymptomatic despite sustained bacterial presence.

The authors aimed to improve comprehension of pertussis transmission dynamics in high burden low resource settings and they advocated for an enhanced molecular surveillance strategies to capture full pertussis infection including those that might have gone undetected.

Strengths:

The strength are the use of innovative study design especially the longitudinal approach and routine sampling rather than symptom driven testing that minimizes bias in the study. The methodology were also rigorous and transparent by evaluating IS481 signal strength to classify pertussis detection and conducts retesting to assess qPCR reliability. There was also important epidemiological insights and the findings challenge the traditional wisdom by suggesting that pertussis transmission may frequently occur outside of symptomatic cases. The findings also showed its relevance to global health and policy by arguing for the incorporation of molecular tools like qPCR for surveillance of pertussis in low resource setting.

Weaknesses:

These includes reliability on qPCR based detection without additional validation measures like confirmatory culture or serology. There are also potential alternate explanation for transmission patterns observed in the study such as shared environmental exposure or household transmission. Additionally, there are limited generalizability as the study was done in a single urban site in Zambia. There is also lack of functional immune data.

Reviewer #2 (Public review):

Summary:

In this paper, the authors describe the results of a longitudinal study of pertussis infection in mother/infant dyads in Lusaka, Zambia. Unlike many past studies, the authors assessed the infection status of individuals independently of whether they were symptomatic for a respiratory infection. As a result, this work represents one of the first studies specifically designed to assess asymptomatic transmission of pertussis. Using qPCR, the authors find strong evidence for the role of asymptomatic transmission from mothers to infants and also evidence for long-term bacterial carriage. This work represents an important contribution to our understanding of the global burden of pertussis. Also, it highlights the still under-appreciated role of asymptomatic transmission across many infectious diseases (including vaccine-preventable ones).

Strengths:

Unlike many past studies, the authors assessed the infection status of individuals independently of whether they were symptomatic for a respiratory infection. As a result, this work represents one of the first studies specifically designed to assess asymptomatic transmission of pertussis. Using qPCR, the authors find strong evidence for the role of asymptomatic transmission from mothers to infants and also evidence for long-term bacterial carriage.

Comments on revised version:

I appreciate the authors' attention to my comments during the revision process and still believe that their work represents an important contribution to our understanding of pertussis epidemiology. In most cases, the authors have done a thorough job of either addressing or responding to my comments. However, I do not believe the authors engaged sufficiently with two of the queries raised in my previous round of comments. The two queries were about the vaccination status of the mothers and engagement with literature on asymptomatic transmission. I still think they matter and ask the authors to consider them again.

I do not think the authors can rule out two alternative explanations: (1) recent introduction of pertussis and low vaccination coverage amongst study mothers, or (2) recent introduction of a breakthrough strain (either w.r.t. the vaccine or prior infection) and higher vaccination coverage/infection-derived immunity amongst study mothers. Depending on which mechanism was mostly driving the observed patterns in Zambia, i.e.,

a. long-running, widespread, unreported transmission;<br /> b. transmission started recently, and vaccination was low amongst study mothers;<br /> c. a breakthrough strain is causing the current rise (here we'd still want to know about vaccination status); and<br /> d. something else that I have not considered

would have implications for how the results are interpreted, and potentially far-reaching implications for the broader pertussis community. All of that is to say, I think the authors were too quick to dismiss these concerns (even if they disagree with my assertions).

In their reply, the authors largely dismissed concerns about not knowing the mother's vaccination status, stating in their reply that, "our findings strongly suggest ongoing pertussis transmission in this population. Based on this, we expect that mothers in our study who were not vaccinated would likely have some degree of infection-derived immunity."

However, they also stated that, "Zambia offers an evocative example of pertussis surveillance, where no cases have appeared in official WHO reports since 2009" and "As we noted above (and now address in our Discussion), widespread genomic surveillance and microbiological characterization of pertussis are sorely lacking across Africa."

I don't disagree with the authors' conclusion that pertussis is clearly spreading in Zambia. I also don't disagree that there's clearly evidence for minimally symptomatic, infectious mothers spreading infections to children. Both of these findings matter for Zambia and for our broader understanding of pertussis. However, I don't see how the authors can so confidently conclude that low vaccination rates, coupled with a recent introduction, high vaccination rates, coupled with a breakthrough strain, or high infection-derived immunity, coupled with a breakthrough strain, couldn't be what's driving the increase. The authors do hedge in places and also state in the discussion that their findings don't line up with expectations related to WP/infection-derived immunity, "This corresponds to a mean return frequency of one infection per 14.8 years, which is much shorter than the presumed duration of immunity from natural infection or the whole-cell pertussis vaccination used in Zambia (70, 71)." But, my read of the paper is that the authors are pushing way to ward for a preferred hypothesis that is not more favored than other alternatives.

Secondly, I asked about placing this work in the context of other studies on asymptomatic transmission, but realize that I did not list any specific papers. Two worth considering are Warfel et al. 2014 and Althouse and Scarpino 2015. Restating for the editor, the Warfel study found that WP facilitated rapid clearance in a non-human primate experimental infection study (admittedly with small sample sizes and many other caveats). Many took that as evidence that WP would also block transmission (admittedly experiments Warfel did not run). If the mechanism underlying the results in Zambia is that either WP or natural infection does not block transmission (in the absence of a breakthrough strain), that would upend many of the assumptions in pertussis research. While not incompatible with the Warfel et al. results, it would negate most of the importance of their finding that WP blocked transmission. From what I can see, the authors do not even cite Warfel et al. 2014, which is a serious gap regardless of whether the authors agree or disagree with the findings. A quick sidebar, the authors seem to duplicate Craig et al. 2020 10.1093/cid/ciz531, listing it as both citation 9 and 38.

In Althouse and Scarpino, they found evidence of a rise in asymptomatic/underreported/subclinical transmission following the switch from WP to AP. While not as directly relevant to the current study as the Warfel paper (so I leave it to the authors to decide whether citing this paper is important), Althouse and Scarpino discuss asymptomatic transmission at length and also assume that WP conferred strong protection against transmission, so their results (along with dozens and dozens of other studies assuming similar WP/infection-induced immunity protection and durability) would also need to be reinterpreted in the context of this study. The authors should engage with the implication of their results in the context of past modeling studies and what we think we know about vaccine-/infection-derived immunity.

Going back to my earlier points, unvaccinated mothers and the recent introduction of pertussis, or vaccinated/infection-induced immune mothers with a breakthrough strain, would both explain the current results and be compatible with Warfel et al., Althouse and Scarpino, and a sizable number of other studies. Instead, if transmission from WP- or naturally infected mothers is common (in the absence of a breakthrough strain), that would really change the landscape of pertussis epidemiology. The authors have not convinced me that they can make this conclusion. Hence, why I think it's important that the authors engage more actively with those hypotheses and with relevant debates in the pertussis literature on asymptomatic transmission. I think it's appropriate for the authors to present their preferred hypothesis, but, absent other data, they should also present plausible alternatives that are consistent with past publications.

References:

Althouse, B. M., & Scarpino, S. V. (2015). Asymptomatic transmission and the resurgence of Bordetella pertussis. BMC medicine, 13, 1-12.

Warfel, J. M., Zimmerman, L. I., & Merkel, T. J. (2014). Acellular pertussis vaccines protect against disease but fail to prevent infection and transmission in a nonhuman primate model. Proceedings of the National Academy of Sciences, 111(2), 787-792.

Reviewer #1 (Public review):

Summary:

This manuscript presents a genome-wide investigation of the genetic architecture underlying adaptation to prolonged starvation in Drosophila melanogaster, using an E&R experimental design maintained across 60 generations. Four starvation-selected (SS) and four matched control (C) populations were whole-genome resequenced, and two complementary analytical frameworks, selective sweep inference combined with low-heterozygosity mapping, and a diffusion-based drift-filtering approach, were applied to identify genomic regions under selection. As a result, the authors report (1) 62 high-confidence sweep-low-heterozygosity regions encompassing 255 genes, and (2) 3,578 SNPs with allele-frequency shifts exceeding neutral drift expectations shared across all four SS replicates, mapping to 578 genes. Mitochondrial pathways are identified as prominent targets, with a 13.9-fold enrichment of nuclear-encoded mitochondrial genes among candidates and differentiation at the mitochondrial origin of replication. Finally, the authors demonstrate that human orthologs of starvation-responsive fly genes are enriched for highly differentiated variants in four human populations from the 1000 Genomes Project.

Strengths:

(1) The experimental design with four evolution replicates provides proper control for false discovery.

(2) The phenotypic characterisation is thorough. The approximately 3-fold increase in starvation survival and 1.5-fold increase in TAG content provide a clear physiological basis for interpreting the genomic findings, and the observation of increased adult longevity adds a meaningful life-history dimension to the results.

(3) The mito-nuclear analysis is one of the more novel contributions of this paper. The implicated picture of coordinated mito-nuclear remodelling under sustained nutrient deprivation is compelling.

(4) The comparative analysis connecting fly selection candidates to human population differentiation is ambitious and adds evolutionary breadth to the study.

Weaknesses:

(1) Ne estimation is derived from controls only, not from selected populations

The entire drift-filtering framework rests on estimates of effective population size obtained from allele-frequency variance among the four control replicates (Ne = 530 for autosomes, Ne = 461 for the X chromosome). This is justified by assuming that divergence among control populations reflects neutral drift alone, a reasonable assumption for C populations maintained on standard food.

However, the starvation-selected populations experienced 75-80% mortality per generation as an explicit design feature of the selection regime. This severe, recurrent demographic bottleneck would substantially reduce the effective population size within SS lines relative to controls. The authors do not acknowledge this discrepancy, nor do they attempt to estimate Ne within SS replicates or assess the sensitivity of their drift thresholds to plausible reductions in Ne. If Ne in SS populations is appreciably lower than in controls, the drift thresholds derived from the control-based Ne will underestimate the amount of neutral drift occurring in SS lines. Consequently, some allele-frequency shifts that are driven by the repeated bottleneck could be misclassified as candidate loci, inflating the apparent number of selection targets. This is the most consequential methodological concern in the paper. The authors should either estimate Ne separately for SS populations, implement a sensitivity analysis varying Ne over a biologically plausible range, or, at a minimum, provide a thorough discussion of how downward bias in SS Ne would affect their results and conclusions.

(2) Lack of consideration about binomial sampling noise due to the pool size in the modeling

With only 100 individuals pooled per population, binomial sampling from the pool contributes a non-trivial additional source of variance to allele-frequency estimates, on top of genetic drift and sequencing error. This is a well-documented issue in Pool-seq data. Critically, the Kimura diffusion framework used for drift modeling does not appear to explicitly incorporate this binomial sampling noise component, an omission that could affect the calibration of drift thresholds, particularly for low-frequency alleles. The authors should discuss whether and how pool-size-induced sampling variance is accounted for in their drift model.

(3) No benchmarking against established Pool-seq analysis tools

The authors use Pool-HMM for sweep detection and a custom diffusion-based drift framework for allele-frequency analysis, with PoPoolation (v1) used only for Tajima's D calculations. However, the study does not benchmark its candidate SNP sets or sweep regions against well-established Pool-seq analysis frameworks such as PoPoolation2, which provides CMH tests and FST estimation specifically designed for replicated Pool-seq E&R data, or R/poolSeq, which implements drift-aware testing purpose-built for this experimental design. The authors should either benchmark their approach against at least one established alternative or provide explicit justification for why their custom framework is preferable and how it compares in sensitivity and specificity.

(4) Absence of negative controls in the human PBS comparative analysis

A critical missing element in this comparative analysis is a negative control: the authors do not test whether equivalent enrichment is observed in populations with no particular history of famine or nutritional stress, such as European or East Asian populations from the 1000 Genomes Project. The inclusion of at least one negative-control population triplet is necessary to support the cross-species interpretation as stated.

Reviewer #2 (Public review):

Summary:

The authors use an Evolve-and-Resequence approach in Drosophila to study the genomic basis of adaptation to long-term starvation. Replicated selection lines and control populations are sequenced and analyzed to identify signals of selection, which are then related to starvation-related phenotypes. The general experimental design is appropriate, and the combination of genomic and phenotypic data is a clear strength of the study.

Strengths:

The strongest aspect of the work is the experimental evolution framework combined with population genomic inference across replicate populations. The observed parallelism across replicates supports the robustness of at least a subset of the detected selection signals. However, several key methodological details are either unclear or insufficiently justified. In particular, both the maintenance of control populations and demographic assumptions are not fully described, and the treatment of structural variation (e.g., segregating inversions) is not sufficiently addressed. The phenotypic analyses are broadly appropriate and replicated but would benefit from access to raw data.

Weaknesses:

The human ortholog enrichment analysis is an interesting component of the study, but it should be interpreted more cautiously. As currently presented, it is based on correlational signals of differentiation and is therefore sensitive to potential confounding factors. While the analysis may point to intriguing patterns consistent with conserved genetic architecture, the evidence is not sufficient to support strong claims of conserved starvation/malnutrition-related polygenic adaptation in humans. Framing this component more explicitly as exploratory would strengthen the manuscript. In its current form, this analysis is somewhat less conclusive than the experimental evolution results in flies.

Overall, the study provides a useful dataset and a reasonably solid analysis of starvation adaptation in experimental Drosophila populations, but several methodological clarifications and a more balanced framing of the cross-species comparisons would strengthen the manuscript.

Reviewer #3 (Public review):

Summary:

This study tries to identify the genetic signatures of adaptation to starvation conditions. For this, outbred populations of Drosophila melanogaster were selected for starvation resistance by using the 20% surviving adults after starvation to start the next generation. This was done for 60 generations while parallel populations were kept under control conditions. At the end of the experiment, starvation-selected flies showed increased survival, longevity, and TGA storage. DNA poolseq data from control and starvation populations were compared to identify genomic regions with low heterozygosity and signatures of selective sweeps, and SNPs with differences in allele frequency. The candidate regions point to mitochondrial and metabolic pathways as the targets of selection for starvation resistance.

The authors replicate the experimental design, selection approach, data collection, and analyses from Hardy et al 2018 (https://doi.org/10.1093/molbev/msx254), which also investigated adaptation to starvation conditions but used a different Drosophila melanogaster population. In this sense, the current study recapitulates most of the findings from Hardy et al. (2018). The analyses of the mitochondrial results, including the overlap with human data, are the novelty of this paper. However, those analyses are not very well justified. The fact that this study is almost identical to Hardy et al is not clearly stated nor discussed in the manuscript.

Strengths:

The authors made use of an experimental evolution approach to identify the genetic basis underlying adaptation. This is a powerful approach that has proven very successful in the past. They used a good number of replicates (four per condition), an appropriate depth of sequencing, and quantified higher-order phenotypes to validate the claim that the populations had evolved increased starvation resistance.

Weaknesses :

Although the findings of this study seem credible based on the known biology of starvation resistance, there are several aspects of the experimental design that weaken my confidence in the results. The points below should be clarified, and the limitations of the experimental design and analyses need to be included in the discussion.

(1) Pooled genomic data were collected for the four replicates at the end of 60 generations of selection, and four replicates were kept under control conditions. No data were collected at the beginning of the experiment, which is the current standard in Evolve and Resequence experiments. To infer the genomic regions underlying adaptation to starvation, evolved control and starved cages are compared. Although this will identify regions that are possibly truly caused by adaptation to starvation stress, the available data doesn't allow to determine, for example: a) whether the differences between control and starvation regimes are due to changes in control cages relative to the starting population, combined with no changes in starvation cages relative to the starting population; b) whether the differences across replicates are due to different genomic composition at the start of the experiment that could have been amplified by drift.

(2) Selection was applied by starving flies until ~80% of the population died. The 20% surviving flies were used to seed the next generation. The control populations, on the other hand, were propagated using the whole population. Given that only the starvation populations were subject to such a strong bottleneck, it is not possible to disentangle whether the genomic signatures at the end of the experiment are due to this, and not necessarily to starvation resistance. For example, the low heterozygosity blocks and the very great changes in allele frequency could be a natural result of such a bottleneck. A proper comparison would have been to select a random 20% of the control individuals to seed every generation.

(3) The analyses that involve human populations are poorly justified, and the enrichment tests are not clearly explained. There is no evidence of signatures of selection for starvation resistance in human datasets (as mentioned in the text, line 112), and yet the authors claim that their analyses that identify branch-specific alleles for a set of four human populations serve as a dataset for it. I don't think the results of this analysis and further overlap with candidate genes identified in the Drosophila experiment support the conclusion that polygenic adaptation of metabolic pathways is conserved across species (line 303).

(4) The conclusion that adaptation to starvation conditions is repeatable is not justified by the data. The overlap across replicates is very low in every metric.

(5) The methods are poorly described. In most of the sections, there is not enough information to be able to replicate the experiments or the analyses. Several of the analyses presented in the results are not described in the methods. Without this information, it is very difficult to assess whether the analyses were correctly done or whether the results are robust.

Reviewer #1 (Public review):

Summary:

This is an interesting paper on an important topic, the taxonomic and conservation status of some unusual salmonid populations in Taiwan.

Strengths:

The first part of the manuscript is quite strong: the authors sequence and build a reference genome and conduct a phylogenomic analysis. They examine chromosome structure and rearrangements, test for loss-of-function mutations, and do a proteomic analysis. As a stand-alone, this could serve as its own manuscript, perhaps for a more specialized journal.

Weaknesses:

I find this manuscript rather disjointed. The first part of the manuscript is related to phylogenomics of the taxon in question, compared to other nearby species from Japan. The authors go on to describe chromosomal rearrangements, sex-chromosome location, and proteomics. All of these fit within a paper about taxon-level issues. I do find the proteomic analysis perhaps unnecessary. I'm not sure we learn much of substance through this analysis, which is highly speculative.

PSMC analysis seems highly questionable for taxa with such strong genetic structure. If historical Ne and past changes in structure are confounded, what does this analysis provide? I recommend deletion of the analysis included in Figure 1e.

The second portion of the manuscript deals with population structure of three O. formosanus populations, based on RADSeq data. This part reads as a separate manuscript, in my opinion. I think the authors are trying to squeeze too much into one manuscript.

For the second part on population genomics, not enough detail is provided to evaluate the methods, results, and interpretations. For example, not enough detail is provided about each of the three Taiwan populations, the stocking history, and the demographic data collection. The only information available is a brief paragraph in the introduction. Was the Luoyewei (L) population stocked from a brook derived from this population or from Qijiawan (Q)? Why do three L fish have such different levels of MLH? Are these stocked from somewhere else? Are the rest of the fish from one pool, and maybe one family (this would also explain the extremely low contemporary Ne)? Only 17 fish were examined from L, and apparently from one site in the stream; more detail is needed. Are L, Q, and H currently isolated? What is the stocking history? The authors conclude that the Hehuan (H) population has more genetic variation and is likely the result of an unknown native population that bred with stocked fish (which arise from Q). This story does align with the genetic results, but again, more detail is needed. Are there alternative explanations? A more careful treatment would be helpful.

The demographic modeling is not convincing. Not enough detail is provided, and the lack of individual identification of fish makes it so the modeling is very general. It is hard to place too much stock in these vital rate estimates. The methods were fishing, snorkeling, and some electrofishing. Scales were used for ageing, and catch curve analysis was employed. Overall, this is an underdeveloped portion of the paper that is important, but not convincing as written.

Reviewer #2 (Public review):

Summary:

Lee et al. is a comprehensive conservation genomics study that combines a chromosome-level genome assembly (sex-specific, too), population resequencing, coalescent species delimitation, and simulations to reassess the evolutionary status and conservation outlook of the Formosan landlocked salmon, Oncorhynchus formosanus. The authors showed a distinctive genome structure, replete with chromosome fusions and an unusual placement of the sex-determining gene sdY. Across sampling sites, they observed variable levels of genetic diversity, but in a way that was surprising given previous census numbers and conservation history. In particular, the authors report a previously unrecognised native population in Hehuan Creek, and conclude that Hehuan is more resilient to typhoon disturbance than the long-protected Qijiawan population - motivating stream-specific rather than range-wide conservation.

Overall, this is a well-written paper that combines a number of elements that are timely and relevant. It uses state-of-the-art techniques to reach its conclusions and is generally performed to a high standard. It describes a critically endangered species that poses its unique conservation challenges. There are a number of things to like, as well as some substantial shortcomings in this paper.

Strengths:

The genomic resource is excellent. The assembly is well validated (97.3% anchored to 25 scaffolds, 95.7% BUSCO), and the authors generated a separate male assembly specifically to resolve the sex-determining region, allowing XY-shared and Y-specific contigs to be distinguished on coverage rather than inference. This is truly well done, and at a high standard. The synteny evidence for telomere-to-telomere fusions involving at least 14 ancestral chromosomes, against two in O. m. masou, is convincing.

The Hehuan Creek result is the paper's most valuable contribution. Elevated heterozygosity, short and infrequent runs of homozygosity, and private alleles absent from the Qijiawan broodstock are difficult to reconcile with a purely reintroduced origin. The contrast with Luoyewei is a clean and useful cautionary case for hatchery supplementation.

Weaknesses:

(1) The species-rank claim is featured in the abstract, but it is made with any level of rigour in the paper. "New species" appears once, in the abstract (l. 32). The Results conclude only that O. formosanus is a distinct evolutionarily significant unit (ll. 188-191), which itself can be well-justified, but it's far from a taxonomic rank (see author's own ref 10). No species concept is explicitly named anywhere, and the taxon is referred to across the manuscript as a subspecies (l. 68), a "new species" (l. 32), and an ESU (l. 189) in turn.

(2) Gene flow is asserted, not tested, and two divergence estimates disagree twentyfold. The abstract reports "no detectable gene flow for ~50,000 years." That figure is a divergence time from BPP under the A00 model, which contains no migration parameter; a model that cannot fit gene flow cannot report its absence. Separately, Figure 1b shows a split at 1.15-5.09 Mya (Figure 1b), while the ddRAD coalescent places the same split at ~50 kya (Figure 1d). The explanation offered (ll. 417-421, "differing temporal sensitivity of genomic markers") is not a mechanism.

(3) The placement of sdY is unresolved, and the paper's own figures conflict with its text. Figure S10 and Table S6 both make O. formosanus chr13 homologous to O. m. masou chr32, whereas reference 28 - on which the authors rely - places the sdY contig on O. m. masou chr7, whose O. formosanus homologue is chr5 (Table S6). These cannot both be correct, and Figure S10's caption compounds the confusion by attributing chr13 to masou and omitting the chr32 track entirely.

(4) The population-viability model's stated mechanisms are contradicted by the authors' own supplementary tables. The Discussion attributes Qijiawan's vulnerability to "lower juvenile survival, decreased fecundity, and narrower terminal age class representation" (ll. 522-525). Table S10 gives Qijiawan higher age-0 survival (0.202/0.616 vs 0.184/0.615); Table S11 gives it higher fecundity at every reproductive age (7.68/19.27/7.86 vs 6.10/8.95/4.14); Table S9 gives it a broader terminal age class (5.0% vs 0.8% age-3 in November). The only parameter favouring Hehuan is age-1 survival - 0.087 (95% CI 0.000-0.180) versus 0.131 (0.093-0.187) under typhoon, and 0.054 (0.000-0.167) versus 0.087 (0.047-0.149) at baseline. Both Qijiawan intervals include zero and overlap Hehuan's, yet a reported extinction odds ratio of 4.48 rests on this difference.

(5) The two streams were not measured equivalently, and every asymmetry favours the conclusion.

Reviewer #1 (Public review):

The manuscript by Fisher et al describes the molecular mechanism underlying how G beta gamma subunits engage with the beta 3 isoform of PLC. The paper used a combination of cryo EM, BRET assays, and biochemical assays of PLC beta activity. A key discovery is that G beta gamma is not sufficient to drive membrane binding by itself and instead promotes G alpha activation. The work is important, but suffers slightly from some ambiguity in the actual interface that is present in their cryo EM model, as crosslinkers could stabilise a transient and non-native complex. This is somewhat abrogated by the careful mutational analysis, which shows that mutation of any of these three sites does somewhat block PLC beta G beta gamma activation. However, there could be some improvement in the presentation of this data, as well as possible mutant selection. Overall, this paper is a nice complement to the Falzone et al paper showing the membrane bound complex of PLCB3 on membranes, with this work building on this work, highlighting the importance this will have in our full understanding of PLC beta activation.

Major concerns

My most major concern is the potential that this interface is artefactual based on the crosslinking strategy utilised. Here are thoughts on how this could be better validated, presented in a more convincing way.

(1) The authors main claim is that there is a degree of plasticity of G beta gamma binding to the PLC beta 3 isoform, with three possible binding sites. The main complication of this is of course the possibility that the crosslinking stabilises a non-native complex, driven by a mutated cysteine.

Because of this any other additional details about this interface are going to be critical for the scientific audience to judge if this is accurate.

What would greatly help figure 1, is an evolutionarily conservation analysis of the novel Gbg interface in PLC, to see how well this is conserved, and compare this to the conservation of the previously annotated sites. Conservation of these sites on both the G beta gamma and PLC side would help justify this as a native complex.

This also will help orient the reader to the identity of the mutated residues assayed in figure 3.

(2) The g beta gamma orientation is also different than what I have observed in previous g beta gamma effector structures. Is there any precedent for this as an effector interface? A supplemental figure comparing this structure to other g beta gamma interfaces from other enzymes, for example recent tesmer structure with PI3K.

(3) The mutational analysis in Figure 2D-G seems to give some strange results, and I have some question why certain residues were chosen rather than others. Mutation of the Gbg side will be more complicated as of course that can effect any of the three surfaces. My main question is that from the way fig 2A is oriented that the main salt bridge in their novel interface to me looks like R199-D228, with K183 being in the wrong orientation to E226, and D167 being far from any charged residues. Why did the authors not make the corresponding R199 to D or E mutation?

(4) To help reader interpretation of Figure 2A, I would recommend a supplemental figure showing the density for interfacial residues, as that also would increase confidence in the interface.

Comment on revised version.

After revision the authors have addressed all of my concerns.

Reviewer #2 (Public review):

In this manuscript, the authors dissect how Gβγ potentiates PLCβ3 signaling in cells. Using engineered crosslinking to stabilize a Gβγ-PLCβ3 complex, single particle cryo-EM, and cell-based functional assays, they identify map multiple putative Gβγ interaction surfaces on PLCβ3, including a previously unrecognized binding mode. Structure-guided mutagenesis supports the functional relevance of these interactions and suggests that Gβγ potentiation is not primarily mediated by PLCβ3 membrane recruitment, but instead enhances PLCβ3 activity after the lipase is already at the membrane.

Previous reconstitution work on membrane surface (Falzone & MacKinnon, 2023) proposed a recruitment/partitioning-centric model in which Gβγ increases PLCβ3 output largely by elevating its membrane surface concentration, whereas Gαq primarily increases catalytic turnover; under those reconstitution conditions, the two inputs can combine approximately multiplicatively. In receptor-driven cellular signaling, however, PLCβ3 is robustly recruited to the plasma membrane upon Gαq activation, which raises the question of whether Gβγ contributes mainly through additional recruitment or through a post-recruitment mechanism once PLCβ3 is already at the membrane.

This manuscript helps address that gap by using membrane-anchored PLCβ3 and complementary cellular readouts to separate "getting PLCβ3 to the membrane" from "boosting activity once PLCβ3 is already there." Their results argue that, in cells, membrane recruitment is largely dominated by Gαq·GTP, while Gβγ can further potentiate PIP2 hydrolysis after membrane association, consistent with a modulatory role at the membrane rather than primary recruitment.

Overall, the work provides a structural and mechanistic framework for Gβγ-PLCβ3 cooperation and helps clarify the basis of Gq pathway amplification.

Comments on revised version.

The authors have reasonably addressed my comments.

Reviewer #3 (Public review):

Summary:

PLCβ3 is activated by both Gαq and Gβγ subunits. This paper follows previous solution and cryoEM studies of the PLCβ3 / Gβγ complex to delineate the molecular details of activation using cellular BRET assays and cryoEM.

Strengths:

The authors find evidence for multiple binding sites on PLCβ3 for Gβγ and suggest that Gβγ is not bone fide activator per se but enhances Gαq activation by positioning the catalytic site towards substrate. The authors also find that this activation is not through recruitment of the enzyme to the membrane by Gβγ released upon G protein activation in accord with other PLCβ enzymes.

Weaknesses:

(1) The main issue is that the author's mechanism does not fully explain how Gβγ activation occurs for PLCβ2 in reconstituted systems in the absence of Gαq subunits but will be investigating this in future studies.

Reviewer #1 (Public review):

Summary:

This study reports a novel and potentially impactful role for NINJ2 in maintaining lysosomal integrity and regulating cellular susceptibility to ferroptosis. The authors demonstrate that NINJ2 localizes to lysosomes and interacts with LAMP1, a key lysosomal membrane glycoprotein involved in sensing lysosomal stress. Loss of NINJ2 increases lysosomal membrane permeabilization (LMP), resulting in selective leakage of lysosomal contents, including labile iron, into the cytosol. The authors further show that NINJ2 deficiency reduces the expression of ferritin storage proteins, thereby sensitizing cells to ferroptosis induced by RSL3 and erastin. Collectively, the work proposes a mechanistic link between NINJ2-mediated control of LMP, iron homeostasis, and ferroptotic vulnerability, with potential relevance to cancer biology.

Strengths:

This study identifies a novel role for NINJ2 in regulating lysosomal integrity and ferroptosis and establishes a mechanistic link between lysosomal membrane permeabilization, iron homeostasis, and ferroptotic sensitivity, with potential translational relevance in cancer.

Weaknesses:

The results overall support the authors' conclusions and provide a plausible mechanistic framework; however, additional quantification of western blot data and further discussion of mechanistic questions would strengthen the study.

The findings are likely to have broad impact by linking lysosomal integrity to ferroptosis and iron homeostasis, both of which are relevant to cancer biology and therapeutic targeting.

Comments on revised version.

The authors have addressed all of my comments and questions. I have no further concerns.

Reviewer #2 (Public review):

This manuscript, "Nerve Injury-Induced Protein 2 preserves lysosomal membrane integrity to suppress ferroptosis", identifies a previously unrecognized function of NINJ2 as a regulator of lysosomal membrane integrity and iron homeostasis, thereby suppressing ferroptosis. The authors demonstrate that NINJ2 localizes to lysosomes, interacts with LAMP1, limits lysosomal membrane permeabilization (LMP), stabilizes ferritin, and protects cells from ferroptotic cell death. They further extend these mechanistic findings to human cancer datasets, showing co overexpression and positive correlation of NINJ2 with ferritin genes in iron addicted cancers.

Overall, the study is conceptually interesting, technically solid, and integrates cell biology, iron metabolism, and ferroptosis in a coherent framework. The work expands the functional repertoire of the Ninjurin family beyond plasma membrane rupture and inflammation, which will be of interest to researchers in cell death, lysosome biology, and cancer metabolism.

Strengths:

(1) The identification of NINJ2 as a lysosome-associated protein that suppresses ferroptosis represents a meaningful advance beyond its previously described roles in inflammation, pyroptosis, and tumorigenesis.

(2) The work distinguishes NINJ2 functionally from NINJ1, reinforcing the idea that structurally related Ninjurins have divergent membrane-related roles.

(3) The study presents a logically connected pathway:<br /> NINJ2 loss → LMP → labile iron increase → ferritin degradation → ferroptosis sensitization, which is well supported by the data.

(4) The link between LAMP1, ferritin turnover, and ferroptosis is particularly compelling and timely given recent interest in lysosomal contributions to ferroptotic signaling.

(5) The authors use confocal microscopy, proximity ligation assays, biochemical IPs, iron measurements, protein half-life analyses, ferroptosis assays, and TCGA-based analyses, providing convergent evidence for their model.

(6) Use of two distinct cell lines (MCF7 and Molt4) strengthens generalizability.

(7) The integration of cancer expression datasets linking NINJ2 with ferritin expression in hepatocellular and breast carcinomas enhances translational relevance.

(8) Assigning NINJ2 a lysosomal protective function, distinct from NINJ1-mediated plasma membrane rupture is novel.

(9) Linking NINJ2 to ferroptosis regulation via lysosomal iron handling, rather than canonical GPX4 or system Xc⁻ pathways is also novel, along with proposing a NINJ2-LAMP1-ferritin axis as a buffering mechanism against iron-driven lipid peroxidation.

(10) These insights are not incremental; they reframe how NINJ2 may function at the intersection of membrane biology, iron metabolism, and regulated cell death.

Reviewer #1 (Public review):

Summary:

The authors investigated the function of a Drosophila chemosensory receptor, IR20a, using genetics, neuronal histology, calcium imaging (in vivo and in cultured cells), and behavioral approaches. They provide evidence that this receptor functions in the detection of the amino acid arginine and of low salt (NaCl) concentrations, functioning in different combinations with "co-receptor" IRs, IR25a and IR76b.

Strengths:

The experiments are generally very well-performed and clearly presented, using established methodology. While, unsurprisingly, some puzzles remain (mentioned below), the work provides one of the clearest lines of evidence for the combinatorial coding of sensory information at the periphery through the combined action of distinct sets of chemosensory IRs.

As taste neurons have long been recognized to express many different combinations of IRs and Gustatory Receptors (GRs), this study will be of interest to chemosensory biologists in general, particularly those studying invertebrate model systems (though co-expression of different families of taste receptors is a feature of mammalian taste cells).

The precise molecular mechanisms remain unclear: there is no direct evidence here for protein complex formation (though this is likely), the stoichiometry of such complexes, or how subunits interact to confer or suppress sensory sensitivity. Nevertheless, these receptors, and the authors' success in reconstituting functionality in cultured cells, might make these a powerful model to explore such questions in the future.

Weaknesses:

Given the particular interest of the data from the heterologous reconstitution in cultured cells, the authors should be quite explicit about the nature of the quantification of the S2 cell responses. It is unclear whether the cited "n" refers to numbers of cells or something else, and whether all or only a fraction of (transfected) cells gave responses.

There has been some prior work on the context-specific role of IR76b in amino acid-sensing and salt sensing by Ganguly and colleagues (Cell Reports 2017), who also implicated (weakly) a contribution of IR20a in contributing to the amino acid-sensing role. In that work, the authors focussed principally on the labellum and used electrophysiology rather than calcium imaging. The present manuscript appears rather dismissive of the earlier results (only mentioning them in the Discussion), and the authors could be a bit more generous about what was previously determined, where they have confirmed previous findings, where their results diverge, and why this might be. Similarly, the original functional analysis of IR76b (Zhang Science 2013) argued this was a low-salt sensor by itself, which is at least partially corroborated here; it remains unclear how this role relates to the low-salt detecting function of a potential complex of IR20a/IR25a/IR76b. It would be useful to have a summary model of the possible variety of complexes of IRs in different types of sensory neurons, as supported by the results in this and previous studies.

The discord between the lack of requirement for IR20a for physiological responses to arginine in tarsi versus the necessity for behavioral responses is puzzling (though might reflect a labellar role for IR20a). There appears to be a trend of a decrease in calcium signal in tarsi to 100 mM arginine, which is the highest concentration tested (Figure 2A, C). Would a statistically significant decrease be observed with lower arginine concentrations? (A more substantial experiment would be to perform calcium imaging in the labellar IR20a neurons, or their axonal projections in the SEZ; this is not necessary, but the authors should at least acknowledge that their imaging of tarsal responses, while convenient, only examines a tiny fraction of the entire IR20a neuron population.

The authors argue for synergistic responses to arginine and NaCl mediated by IR20a/IR25a. It's not clear to me to what extent there is synergism. In Figure 5A, 10 mM arginine or 10 mM NaCl individually lead to c.30-40% PER, and then when both are presented together in the "Mix" (presumably both compounds at 10 mM?), PER rises to c.60%. Is this really synergism, or rather simple additivity of behavioral responses to two attractive compounds? The authors could discuss this more thoroughly. Similarly, in Figure 5G the authors show that 50 mM arginine does not evoke a significant response in S2 cells expressing IR25a/IR20a, but in Figure 4 it would seem likely that a 50 mM dose would produce a significant response (the response to 25 mM arginine in Figure 4F is already elevated above the control, albeit not statistically significant). Is this just a batch effect of the experiments performed at different times (so they are not directly comparable)?

The legend title to Figure 6 implies cooperation between tonic and state-modulated pathways, but I don't see specific evidence for "cooperation". Rather, as in the results text, they seem to work in parallel, so this analysis seems slightly peripheral to the main focus of the manuscript. It's ultimately unclear how the IR20a/IR76b/IR25a low salt sensor and the sensor containing IR56b functionally interact at the behavioral level. Here, a graphical summary, as mentioned above, of the different salt sensing neurons, the receptors they use, and the behaviors they control could be useful to establish the current knowledge and highlight open questions for the future.

Reviewer #2 (Public review):

Summary:

This study identifies IR20a-expressing gustatory neurons in Drosophila as a multimodal sensory population integrating amino acid (arginine) and low-salt signals through combinatorial IR20a/IR25a/IR76b receptor assemblies. The proposed model of peripheral-level signal integration and synergistic enhancement of feeding preference is potentially significant, as it expands current understanding of gustatory coding beyond single-modality labeled lines.

Strengths:

Overall, the findings are conceptually interesting and suggest a novel framework for multimodal taste integration, but some mechanistic interpretations remain incompletely supported by direct evidence.

Weaknesses:

(1) Although the authors demonstrate co-expression of IR20a, IR25a, and IR76b in the same GRN population, this evidence is insufficient to support the proposed model of distinct receptors coexisting within individual neurons. Additional molecular or structural data would be required to distinguish whether these subunits assemble into complexes.

(2) Given that IR76b has already been established as a sodium/salt sensing channel, the novelty of this study relies on the proposed role of IR20a in conferring multimodal integration and synergy. However, it remains unclear whether this represents a fundamentally new sensory mechanism or a re-interpretation of known IR76b-dependent salt responses in a different neuronal context.

(3) Line 127:<br /> -The statement that there is no overlap between IR20a-GAL4 and GR64f-LexA or GR66a-LexA is not sufficiently supported by the presented imaging data. In particular, the resolution and clarity of the confocal images in Figure 1 appear suboptimal, making it difficult to confidently assess co-localization. The authors are encouraged to provide higher-resolution images or additional quantitative co-localization analysis to substantiate this conclusion.<br /> -In addition, the images shown in Figure 1 F1-F2 suggest possible partial overlap between IR20a and GR66a signals, which appears inconsistent with the authors' statement of no co-expression. This discrepancy should be clarified.

(4) Lines 138-141:<br /> There appears to be a discrepancy between imaging and behavioral data: IR20a is reported as dispensable for arginine-evoked neural responses, yet IR20a mutants show significantly reduced attraction to arginine in behavioral assays. The authors should clarify how behavioral deficits arise in the absence of detectable changes in calcium imaging,

(5) The manuscript proposes that IR20a functions in combination with IR25a to mediate multimodal detection of arginine and low NaCl. However, the specific role of IR25a in this context remains unclear.

(6) The authors report that co-expression of IR20a and IR25a confers synergistic responses to combined arginine and NaCl stimulation, whereas the inclusion of IR76b abolishes this response (Figures 5E-K). This is an intriguing and potentially important finding; however, the mechanistic basis for this suppression is not clearly explained.

(7) The authors propose that IR56b mediates state-dependent modulation of low-salt preference. However, the current data do not clearly distinguish whether IR56b acts as a real nutrient state sensor or just functions as a downstream modulatory component within a broader feeding circuit. Additional evidence linking IR56b activity changes to upstream metabolic state signals would be necessary to support the interpretation that IR56b functions as a primary state sensor.

(8) The manuscript suggests that IR20a and IR56b define two parallel and functionally independent pathways mediating nutrient detection and state-dependent preference, respectively. However, this conclusion is not fully supported by the current dataset. While the two receptors are shown to be expressed in distinct neuronal populations, the possibility of indirect interactions or convergence at downstream circuit nodes has not been excluded. Given that both pathways ultimately influence feeding behavior, it remains possible that they converge at higher-order interneurons or shared neuromodulatory circuits.

(9) In the state-dependent feeding assays (Figure 6), using H2O as a control introduces a severe masking effect. Salt-deprived flies actively suppress pure water intake to avoid osmotic shock, which artificially inflates the Preference Index (P.I.) for salt due to the denominator effect. To cleanly isolate salt preference from the thirst/osmotic drive, the authors will need to utilize an "isosmotic sucrose vs. isosmotic sucrose + salt" paradigm (Jaeger et al., 2018, eLife; Puri et al., 2026, PNAS).

Reviewer #3 (Public review):

Summary:

Drosophila, like other animals, use sophisticated taste systems with specialized chemoreceptors to identify gustatory cues in their environment. Multiple gustatory cues associated with a food source are often encountered simultaneously, but our understanding of how this sensory information is detected and integrated remains incompletely understood. This valuable study investigates how salt, amino acids, or their combination are detected by specific combinations of peripheral Ionotropic Receptors, leading to behavioral attraction. The authors show that distinct combinations of IR76b, IR25a, and IR20a confer sensitivity to salt, arginine, or both. They also show striking evidence that cells co-expressing IR25a/IR20a display a synergistic response to a mixture of sub-activating concentrations of these tastants. Together, these experiments lead to the conclusion that combinatorial expression of different subunits and synergistic responses to taste mixtures facilitates integration of taste cues beginning in the periphery. However, in its current form, key methodological details are missing or inadequately described, which complicates interpretation. Additionally, characterization is heavily focused on the population of IR20a+ neurons in the tarsi, while the response properties of the newly-identified, functionally distinct population in the labellum are investigated only through behavioral analysis, limiting the description of potentially additional IR20a complexes. Ultimately, more in-depth biochemical characterization of the IR complexes described will be required to fully support the conclusion that combinatorial assembly of distinct IR20a receptors enables peripheral integration of taste mixtures.

Strengths:

The authors characterize the expression pattern of IR20a in the tarsi as well as in the labellum, a tissue for which IR20a expression has been a point of debate. Multiple levels of analysis, including behavioral assays, physiological recordings, as well as ectopic and heterologous expression systems, are used to characterize the response properties of different combinations of IR subunits, demonstrating remarkably consistent behavior of the IR-complexes across cell types. Well-controlled genetic analysis and the use of multiple behavioral assays provide additional support for their results, including the surprising demonstration of synergistic responses to mixtures of tastants that supports the idea of peripheral integration of gustatory inputs. This report also identifies a distinct IR, IR56b, required for starvation-enhanced responses to salt.

Weaknesses:

(1) The title states that IR20a integrates L-arginine and salt signals via distinct subunit assemblies, though the paper lacks direct evidence that IR20a serves as a multimodal tuning receptor in distinct functional assemblies. Heterologous expression shows that co-expression of IR20a/IR25a confers sensitivity to Arg, IR76b confers sensitivity to NaCl, and IR20a/IR25a/IR76b co-expression confers sensitivity to both Arg and NaCl. This seems to be interpreted to mean that all three subunits are assembling into a single complex. However, current results do not show any difference in salt response when IR76b is expressed alone compared to alongside IR25a+IR20a. Without more direct evidence for co-assembly of all three subunits, it is equally plausible that the responses observed represent activity of distinct IR25a/IR20a and IR76b receptors for Arg and salt, respectively. In this model, genetic disruption resulting in expression of either IR25a or IR20a alone with IR76b could disrupt its activity or membrane trafficking (as seen here and in previous studies) while co-expression of both IR20a and IR25a relieves this inhibition by sequestering IR20a/IR25a into a distinct complex from IR76b. Direct biochemical characterization, for instance in the form of co-immunoprecipitation or FRET, will be required to differentiate between these possibilities.

(2) Key methodological details are missing throughout the manuscript. For instance, incomplete genotype and staining information is provided for images in Figure 1, making it difficult to interpret what is being shown. Additionally, for the calcium imaging methods, what is the imaging speed? How are max values calculated (is this the average of several images or just a single maximum)? How are ligands diluted and delivered to cells, and were they applied in a manner that allowed for subsequent washout?

(3) The composition of the S2 imaging bath buffer requires clarification. As described, the bath buffer appears to lack any Ca2+ or other IR-permeable cations. If this is indeed the case, more detail should be provided about why this bath buffer was selected and what this means for the source and mechanism of calcium responses observed, since it would not reflect direct IR-mediated transduction. It is also notable that addition of water gives such a detectable change in the tarsal preps.

(4) Visualization of IR20a driver activity in the labellum is interesting. Previous descriptions of labellar expression of IR20a range from no expression to expression in bitter neurons, so the current data linking IR20a to a different population of IR76b+ neurons warrants careful analysis in light of this discrepancy. However, some of the strongest presented evidence for expression is found in Figure 1, where the images are quite small, making it difficult to distinguish the morphology and sensillar innervation pattern of the cells labeled by the IR20a driver. In Figure 1A, several of the arrows do not appear to be associated with any visible fluorescence. It is similarly difficult to assess overlap. Including higher-resolution images and/or validating labellar expression, using antibodies, in situ hybridization, RT-PCR, or transcriptomics would strengthen these claims.

(5) Similarly, Figure 2 shows that IR20a is not required for Ca2+ responses to AAs or KCl in the legs, but is required for behavioral preferences and PER responses in the labellum. This suggests that IR20a receptors may function differently in different tissues, though direct evidence is lacking. Calcium imaging from a weakly expressed driver may be difficult, but electrophysiological recordings from relevant labellar sensilla or ectopic/heterologous reconstitution of the molecular receptors found there would give important insights into the response properties of these other IR20a receptor type(s) and could provide evidence for additional IR20a-containing complexes. The current paper focuses exclusively on IR25a/IR20a/IR76b, which do seem to reliably reproduce the Arg/NaCl responses observed in the tarsi, but even for the tarsal neurons it is unclear that this represents an exhaustive list of all the relevant IR20a-interacting subunits coexpressed in these cells. For instance, Koh et al., 2014 (PMID: 25123314) found several additional IR driver lines, including IR56b, were active in the 5v/s tarsal sensilla.

Reviewer #1 (Public review):

Summary:

This Perspective proposes a conceptual model in which incomplete age-related lobular involution (ARLI) in the breast reflects an actively maintained senescent-immune "reserve niche," rather than simply passive failure of lobular regression after menopause. The authors aim to integrate breast cancer epidemiology, mammary gland biology, cellular senescence, immune surveillance, and comparative reserve-tissue systems to explain why persistent postmenopausal lobules are associated with increased breast cancer risk. The manuscript is ambitious, creative, and potentially useful in shifting attention from residual epithelial quantity alone toward the microenvironmental state of persistent lobules.

Strengths:

A major strength of the manuscript is its forward-looking synthesis. The authors bring together several areas that are often considered separately: ARLI as a tissue-level risk marker, inflammatory features of incompletely involuted breast tissue, senescence biology, macrophage-mediated remodeling, and the menopausal transition as a potential window of biological plasticity. The model is conceptually interesting and, if supported by future evidence, could stimulate new approaches to risk stratification and prevention focused on the perimenopausal period.

Weaknesses:

However, the current manuscript often presents the proposed model with more certainty than the available evidence supports. The evidence clearly supports associations among incomplete ARLI, inflammatory or immune features, and breast cancer risk, but it does not yet demonstrate that senescent cells maintain persistent lobules, that immune clearance failure causes incomplete involution, or that a self-sustaining senescent-immune "niche lock" exists in human breast tissue. Much of the mechanistic framework is extrapolated from other tissues, postpartum involution, or general senescence biology. These are reasonable sources for hypothesis generation, but the manuscript would be stronger if it more clearly distinguished established observations from inference and speculation.

The senescence component of the model requires stronger and more direct support. Several claims about senescent burden in the aging breast appear to rely on general senescence literature or mammary aging studies that do not directly demonstrate senescence in persistent human TDLUs. This distinction is important because the manuscript's central model depends on senescent cells being spatially and functionally linked to incomplete ARLI.

The epidemiologic evidence also requires a more balanced treatment. Although several studies support incomplete ARLI as a breast cancer risk-associated phenotype, other cohorts and quantitative approaches have reported attenuated or null associations. This mixed evidence is acknowledged, but it is treated largely as a caveat rather than incorporated into the central argument. For readers, this uncertainty is important for interpreting the strength and generalizability of the proposed model.

Reviewer #2 (Public review):

Summary:

This review constructs a novel theoretical framework to elucidate incomplete postmenopausal age-related lobular involution (ARLI) in the breast. Differing from the conventional view of persistent lobules as passive residual structures, the work innovatively defines them as an actively maintained senescence-immune reserve niche. It comprehensively integrates multidisciplinary evidence from breast epidemiology, stromal biology, cellular senescence and immune surveillance, as well as cross-tissue research findings, and identifies menopause as a core biological turning point regulating ARLI and relevant breast cancer risk, providing a new theoretical perspective for subsequent breast cancer risk assessment and preventive intervention research.

Strengths:

This study presents an original, logically rigorous, and well-organized research hypothesis. It innovatively breaks through the traditional cognitive perspective of ARLI and adopts a multidisciplinary and cross-tissue analytical approach to sort out relevant biological mechanisms systematically. The proposed theoretical framework is insightful, with good theoretical innovation and potential translational value for guiding breast cancer risk evaluation and targeted prevention strategies.

Weaknesses:

The manuscript currently serves primarily as a conceptual framework rather than a rigorously evidenced synthesis. Its central argument relies heavily on cross-sectional correlations and theoretical analogies to other organ systems, lacking operational definitions for the reserve state in human breast tissue.

Reviewer #3 (Public review):

Summary:

Here the authors investigate the role of the Trypanosoma brucei polo-like kinase TbPLK in the function of flagellum-associated cellular structures in trypanosomes. They set out to test the hypothesis that a key substrate of TbPLK is the kinesin protein KIN-G, and that TbPLK phosphorylation of KIN-G regulates its functions in cells.

Strengths:

Using in vitro biochemistry with purified proteins, the authors convincingly demonstrate that TbPLK phosphorylates KIN-G at 29 sites. Moreover, they convincingly show that phosphorylation at one site, T301, impairs the binding of purified KIN-G to purified microtubules. They further confirm that inhibition of TbPLK in cells reduces KIN-G phosphorylation at T301 (and S569). Using immunofluorescence-based imaging approaches, they also show that TbPLK colocalizes with KIN-G at centrin arms during early S-phase of the cell cycle. Centin arms are structures that are located near the basal body and flagellum and are important for new flagellum biogenesis, Golgi positioning, and cell division. To evaluate the function of KIN-G phosphorylation in cells, they depleted KIN-G by RNAi, simultaneously expressed phospho-mimetic (T301D) and phospho-ablative mutant proteins, and used immunofluorescene to examine the impact on flagellum-associated cellular structures. They show that expression of the phospho-mimetic mutant KIN-G-T301D causes the following defects: reduced cell proliferation, disruption of centrin arm and Golgi biogenesis, impairment of FAZ elongation and flagellum positioning, and misplacement of the cell division plane. The data convincingly support the conclusion that KIN-G phosphorylation on T301 plays an important role in regulating the cellular functions of this kinesin motor protein.

Reviewer #2 (Public review):

Summary:

The authors identify KIN-G as an in vitro substrate for phosphorylation by TbPLK and show that several of the in vitro P-ated sites, including T310, overlap with P-ation sites seen in live cells. The authors further show that PLK-mediated P-ation inhibits KIN-G binding to microtubules in vitro, as does a KIN-G-T301D mutant, and that expression of a KIN-G-T301D Phospho-mimic in T. brucei phenocopies KIN-G RNAi knockdowns, producing defects in cell division, morphogenesis of the centrin arm, FAZ and other cellular structures, as well as misplaced cytokinesis furrow.

Understanding cytoskeletal rearrangements that drive cell division in T. brucei is an important and unresolved problem, so the work addresses important questions that are of great interest. PLK and KIN-G have previously been shown to be important for cell division and morphogenesis of cytoskeletal structures that drive cell division in T. brucei. The current work advances our understanding by suggesting a potential mechanism by which PLK and KIN-G might participate, namely through PLK-dependent P-ation to control KIN-G MT binding activity.

Strengths:

The authors use a rigorous combination of biochemistry, phosphoproteomics, cell biology, and mutant analysis to support their conclusion that PLK-mediated P-ation of KIN-G negatively regulates KIN-G microtubule binding and this may explain the observation that a KIN-G T301 phosphomimic mutant blocks cell division and perturbs biogenesis of cytoskeletal structures that drive cell division and morphogenesis. Combining rigorous and informative in vitro studies with mutant analysis in live cells is a great strength. The work is solid and important, though a few pieces are needed to fully connect the in vitro findings with the in vivo observations.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers.]

I think the main points raised in the review have now been addressed. In particular, the new experiment with TbPLK inhibition and mass spectrometry is an important addition, as it provides direct evidence that phosphorylation of KIN-G at Thr301 and Ser569 depends on TbPLK activity in cells.

I also appreciate that the authors have toned down the interpretation of the Golgi phenotype. The revised text now makes clear that the fluorescence data show altered Golgi/ERES organization or duplication, but do not prove a structural defect in Golgi biogenesis.

The added discussion of the T301A result is also helpful. The finding that only a small fraction of KIN-G is phosphorylated at Thr301 in asynchronous cells makes the lack of a strong T301A phenotype more understandable.

Overall, I am happy with the revision of the beautiful manuscript.

Reviewer #1 (Public review):

Summary:

In this study, the authors identified transcription factor combinations capable of inducing retinal neuronal programs in cultured fetal human retinal pigment epithelial (RPE) cells. Using a pooled screening strategy, single-cell RNA sequencing, lineage barcoding, and immunohistochemical analyses, they identified ASCL1 and NEUROD1 as an effective combination for inducing retinal neuron-associated transcriptional states. This work aims to advance the development of therapeutic approaches for retinal regeneration by exploring the plasticity of RPE cells.

Strengths:

A major strength of the study is the comprehensive experimental design. The combination of transcription factor screening, lineage tracing, single-cell transcriptomics, and molecular validation provides a detailed characterization of the cellular responses to reprogramming factor expression.

Weaknesses:

All experiments were performed using fetal human RPE cells. Because fetal RPE remains relatively immature and retains proliferative capacity, it remains unclear to what extent the observed responses reflect true reprogramming of differentiated RPE cells versus activation of developmental plasticity already present in fetal tissue. The absence of adult human RPE controls limits assessment of the generality and translational relevance of the findings.

Reviewer #2 (Public review):

Summary:

This is an interesting study that explores how human RPE could be used as a source for new retinal neurons. This is a welcome addition to the field of retinal regeneration, which is currently focused almost exclusively on the regenerative capacity of Müller glia cells. The line of inquiry is firmly rooted in findings from amphibian and embryonic chick model systems and advances a fetal human retina RPE-based screening system as a rich resource for insights into human RPE biology, including as a potential stem cell source.

The authors investigate the potential of fetal human RPE cells to be reprogrammed into retinal neurons using overexpression of pro-neural factors. While this is a critical knowledge gap in the field of retinal regeneration with significant promise for developing regenerative therapies, several methodological concerns impact the interpretation of results. Firstly, while the authors sought to evaluate factors that enhance RPE reprogramming when co-expressed with ASCL1, nearly all co-expression constructs tested failed to achieve appreciable expression of ASCL1, leaving a central hypothesis of this study largely untested (Major concern 1). Second, although the authors were able to detect a cluster of photoreceptor-like cells in their screen, they were unable to identify which reprogramming construct generated this cluster (Major concern 2). Finally, an essential control that definitively demonstrates the value of combinatorial transcription factor reprogramming is missing (Major concern 3).

In summary, the authors establish a valuable new paradigm for culturing and reprogramming fetal human RPE, and even more importantly, demonstrate successful reprogramming to neural fates. However, the discussion and interpretation of results needs to be modified significantly to make it clear that (i) the outcome of many co-expression paradigms remains effectively unknown/untested due to failed over-expression of ASCL1, and that (ii) the reprogramming construct giving rise to photoreceptor-like cells could not be conclusively identified from their initial screen.

Strengths:

(1) Powerful new screening system advanced for exploring the regenerative potential of human fetal RPE cells.