Reviewer #1 (Public review):

Summary:

In this study, Diana et al. present a Monte Carlo-based method to perform spike inference from calcium imaging data. A particular strength of their approach is that they can estimate not only averages but also uncertainties of the modeled process. The authors focus on the quantification of spike time uncertainties in simulated data and in data recorded with high sampling rate in cebellar slices with GCaMP8f, and they demonstrate the high temporal precision that can be achieved with their method to estimate spike timing.

Strengths:

- The author provide a solid ground work for sequential Monte Carlo-based spike inference, which extends previous work of Pnevmatikakis et al., Greenberg et al. and others.

- The integration of two states (silence vs. burst firing) seems to improve the performance of the model.

- The acquisition of a GCaMP8f dataset in cerebellum is useful and helps make the point that high spike time inference precision is possible under certain conditions.

Weaknesses:

- Although the algorithm is compared (in the revised manuscript) to other models to infer individual spikes (e.g., MLSpike), these comparisons could be more comprehensive. Future work that benchmarks this and other algorithms under varying conditions (e.g., noise levels, temporal resolution, calcium indicators) would help assess and confirm robustness and useability of this algorithm.

- The mathematical complexity underlying the method may pose challenges for experimentalist who may want to use the methods for their analyses. While this is not a weakness of the approach itself, this highlights the need for further validation and benchmarking in future work, to build user confidence.

Comments on revisions:

Thank you for addressing the final comments, and congrats on this study!

Reviewer #2 (Public review):

Summary:

Methods to infer action potentials from fluorescence-based measurements of intracellular calcium dynamics are important for optical measurements of activity across large populations of neurons. The variety of existing methods can be separated into two broad classes: a) model-independent approaches that are trained on ground truth datasets (e.g., deep networks), and b) approaches based on a model of the processes that link action potentials to calcium signals. Models usually contains parameters describing biophysical variables, such as rate constants of the calcium dynamics and features of the calcium indicator. The method presented here, PGBAR, is model-based and uses a Bayesian approach. A novelty of PGBAR is that static parameters and state variables are jointly estimated using particle Gibbs sampling, a sequential Monte Carlo technique that can efficiently sample the latent embedding space.

Strengths:

A main strength of PGBAR is that it provides probability distributions rather than point estimates of spike times. This is different from most other methods and may be an important feature in cases when estimates of uncertainty are desired. Another important feature of PGBAR is that it estimates not only the state variable representing spiking activity, but also other variables such as baseline fluctuations and stationary model variables, in a joint process. PGBAR can therefore provide more information than various other methods. The information in the github repository is well-organized. The authors demonstrate convincingly that PGBAR can resolve inter-spike intervals in the range of 5 ms using fluorescence data obtained with a very fast genetically encoded calcium indicator at very high sampling rates (line scans at >= 1 kHz).

Weaknesses:

The accuracy of spike train reconstructions is not higher than that of other model-based approaches, and lower than the accuracy of a model-independent approach based on a deep network in a regime of commonly used acquisition rates.

Comments on revisions:

I have no further comments on the manuscript.

Reviewer #1 (Public review):

Summary:

The authors of Serantes et al. produced a well-designed set of experiments to address the mechanisms of olfactory disconnection during sleep. In contrast to other sensory modalities, olfaction is not filtered or potentially gated by the thalamus, potentially opening the door to unimodal sensory stimulation during sleep. Recent work (Schreck, 2022) used optogenetically activated Olfactory Sensory Neurons to show that local field potential and activity across the olfactory pathway, not only remained open during sleep but were potentially even accentuated under these brain states. However, their optogenetic manipulation is an artificial perturbation to the system that could override naturalistic early-gating mechanisms. In a set of careful experiments, Serantes et al. show that coupling between airflow and brain activity at the Olfactory Bulb is diminished under sleep and anesthetic brain states. In contrast to a peripheral gating mechanism proposed by Schreck, this lack of respiration-locked activity, measured with EEG and LFP, persists even in the presence of intense respiration and even when nasal airflow is artificially induced and controlled. Their results point to nonthalamic early sensory gating of olfactory information during sleep, which is independent of nasal airflow but dependent on internal brain states. Their work elicits questions about potentially undiscovered mechanisms at the level of the early sensory pathway.

Strengths:

The strengths of this paper lie in the level of control afforded by the multiple preps and the wide array of physiological recordings. Specifically, both their control of airflow with a dual tracheotomy and their control of internal states using both sleep and urethane anaesthesia have a cumulative impact on the results.

The paper is simple, well-written, well executed, has clear questions, describes the literature comprehensively, and points out conflicting results with precision and transparency. The same transparency and judgment should be used on their own results.

Another strength of the paper is the clear, unambiguous results. The effect sizes presented in the paper are sizable and convincing.

Weaknesses:

The paper's shortcomings include open questions and a lack of a full mechanistic understanding of the suggested internal gating process. There are some open questions about the relative importance of airflow sensing vs. odorant sensing. Recent work by Mahajan et al., Sci.Adv 2025 points to OSN as sensing both odorants and airflow to produce anemotaxis. Potentially, other cells could contribute to anemosensation as well, so that gated or non-gated information might depend on the ratio of airflow to odorant information. Perhaps, optogenetic stimulation of OSN acts as an unnatural sensory stimulation that can alter both olfaction and anemosensation.

Detailed ablation, pharmacological, and optogenetic experiments may be needed to elucidate the suggested mechanisms and determine the correct answer to the question posed by the authors.

Reviewer #2 (Public review):

Summary:

In this study, Serantes and colleagues analysed how sleep and anesthesia impact the processing of olfactory inputs, focusing on early sensory processing (occurring at the first or second synaptic contacts). First, they show that the transition to sleep has a major impact on breathing-dependent gamma activity. Second, they show that this decrease originates at the first synaptic contact and is independent of respiration itself. Third, they show a decrease in connectivity associated with neocortical slow waves. These results are very interesting and supported by a robust methodology. However, I have two major concerns regarding this work.

First, the authors fail to adequately contextualize their work. For example, the impact of sleep on respiration-locked gamma activity was reported several years ago and is, in fact, used in some laboratories to score sleep using data from the olfactory bulb.

Second, the authors should exercise much more caution when comparing the urethane anesthesia model with NREM/REM sleep cycles. There are very significant differences between the two. Yet, the title and abstract of the article mention only sleep and anesthesia. More concerningly, the results obtained under urethane anesthesia are uncritically generalized to sleep.

In conclusion, the first finding was already shown in previous studies, and the second and third results were obtained not during sleep but during an anesthetic state that only resembles certain aspects of sleep.

Strengths:

The authors deploy an interventional approach that allows them to determine with compelling evidence the relationship of the gamma activity time-locked to breathing and different aspects of breathing, proving in particular that the disconnection is independent of respiratory dynamics. They leveraged invasive recordings that allow them to pinpoint at which level the disconnection occurs.

Weaknesses:

(1) My first comment concerns how this work fits within the state of the art. The introduction of the article leaves out very important and highly relevant work.

(1a) First, "disconnection" is not a defining feature of sleep; "unresponsiveness" is. It is often assumed that this unresponsiveness (which can be directly measured, contrary to disconnection) is due to a form of disconnection, but there has been substantial work over the past decade showing that disconnection is not as extensive as initially expected. It is therefore incorrect, in my view, to state that "most models attribute sensory gating to thalamocortical mechanisms". Most models attribute sensory gating to a combination of thalamocortical and cortical mechanisms.

(1b) The rationale of the article appears unclear ("the olfactory system-bypassing the thalamus-offers a unique window into earlier stages of sensory disconnection"). If the idea is to investigate gating mechanisms before the thalamus, then any sensory modality would suffice, since even modalities that later relay through the thalamus involve pre-thalamic processing stages. I assume that the authors instead mean that, because olfactory information does not relay through the thalamus, gating mechanisms in the olfactory stream could occur very early. However, this also implies that focusing on olfactory processing would say little about other sensory modalities.

(1c) Key previous results have been completely overlooked. First, the impact of sleep on respiration-locked gamma activity was reported several years ago (Bagur et al., Plos Biology 2018). Second, important articles investigating olfactory processing during sleep have been overlooked (e.g., Arzi et al., Nature Neuroscience 2012; Arzi et al., Journal of Neuroscience 2014). I am not providing an exhaustive list here, but these articles are not only extremely relevant to the present study; they have also become classics in the sleep literature.

(2) For most of their findings (Figures 2 to 5), the authors used urethane anesthesia. They show that this pharmacological manipulation results in alternation between periods of high-amplitude delta waves (SWSt) and a desynchronized state (ASt). However, the parallel with NREM and REM sleep, respectively, is rough and insufficiently justified. Differences can already be noted by contrasting the short examples provided in the figures. While NREM and REM sleep differ in terms of muscle tone (EMG), no such difference is discernible between SWSt and ASt. In SWSt, the slow waves appear to overlap with fast activity at the cortical level (M1, S1), which is not typically the case during NREM sleep. In addition, because the time scale is not the same in Figures 1 and 2 (1 s vs 2 s), yet the slow waves appear to have similar durations, it is also possible that the slow waves generated during SWSt and NREM differ. To better support the proposed parallel between NREM and SWSt on the one hand, and ASt and REM on the other, the authors should provide a thorough comparison of these states (spectral features, properties of the slow waves, duration and frequency of each state, etc.). Without this, inferences from results obtained under urethane anesthesia to sleep are not warranted.

The authors acknowledge this issue in the Discussion ("These findings suggest that there is no functional equivalence between urethane-activated states and REM sleep"), but this caveat should be integrated from the very beginning (title, abstract, and introduction).

(3) In some graphs, the power spectrum is normalized. Under anesthesia, this normalization was performed "within each animal to the SWSt maximum for that signal". However, I could not find equivalent information for sleep. This is key information needed to correctly interpret the results shown in Figure 1.

(4) The authors should also clarify their criteria for concluding on the absence or presence of a given effect. For example, in the legend of Figure 1c, they write: "Note the presence of coherence during wakefulness, demonstrating the internalization of the respiratory signal, and its drop during sleep". Unless coherence is exactly zero, some degree of coherence is always "present". Figure 1 instead shows that coherence is modulated across frequencies during wakefulness, with peaks in the delta and theta ranges.

In Figure 2, they write: "PAC between respiration and OB gamma amplitude was present during ASt but disappeared during SWSt". Again, the authors should clarify what is meant by "disappeared", as they only tested for differences between ASt and SWSt.

Given that the authors implemented a strategy to test for above-chance coherence using surrogate datasets, they should consistently provide statistical tests showing which conditions or frequency bands exhibit coherence above chance in order to justify claims about the presence or absence of an effect.

(5) Likewise, comparisons across states should always be supported by statistical tests, for example, in Figure 4. In addition, despite the apparent absence of coherence during SWSt in Figures 4f and 4g (which again should be formally tested), Figure 4h shows an increase in coherence around 2 Hz, which suggests some degree of coherence between nasal airflow and the olfactory bulb.

(6) Figures should more clearly distinguish results based on a single "representative" animal from population averages. For example, were Figures 4g and 2h computed at the population level?

Reviewer #3 (Public review):

Summary:

Sleep is typified by a behavioural attenuation of responsiveness to external stimuli (higher arousal thresholds). There are various mechanisms through which sensory perception could be dampened, and while thalamic and cortical gate points have been well studied, the focus here is on peripheral ones - at the level of the olfactory bulb (OB). While something conceptually similar has been shown in insects, this paper represents an important contribution to understanding attenuation of sensory perception during rodent sleep and anaesthesia.

This paper shows that respiration-locked potentials and gamma activity in the olfactory bulb, which are important for olfactory coding, are diminished during sleep and when under anaesthesia compared to wake. Further, this state-dependent activity in OB is likely to be locally generated. Using a tracheotomy procedure aimed to dissociate nasal airflow from natural inhalations, authors demonstrate that local field potentials (LFPs) in the OB phase lock with artificially generated air pulses (delivered into the nasal cavity) during the active phase of anaesthesia but not during a more passive state. LFPs did not synchronise with respiratory signals during either anaesthesia state. Lastly, the authors showed that as delta power increased (typical of slow-wave-sleep), the coherence between nasal inhalation rhythms and OB LFP coherence decreased, indicating that as rats experienced something akin to slow-wave-sleep (during anaesthesia), disconnection from the external environment could be augmented. Taken together, the authors argue that the change in activity observed in the olfactory bulb during sleep and anaesthesia provides a non-permissive state for sensory processing and manifests as sensory dissociation

Strengths:

The manuscript is well-written, and the experiments are thorough. Experiments examining coupling of nasal respiration with OB potentials and delta activity are particularly interesting as they point to augmented sensory disconnection during a sleep phase typically associated with higher arousal thresholds.

Weaknesses:

(1) An experiment addressing the following points, is missing:

Does odour stimulation that wakes up a subject restore gamma activity and respiration-locked potentials?

Is OB/respiration desynchrony maintained when presented with a non-rousing stimulus?

Is waking upon stimulus delivery less likely as delta activity increases and coherence between OB/respiratory rhythms weakens?

(2) Many of the experiments are performed under anaesthesia, which I understand is for practical reasons. While authors are forthcoming about limitations of using anaesthesia in lieu of natural sleep states, I would have preferred to see more experiments performed on sleeping animals.

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:

Ever-improving techniques allow the detailed capture of brain morphology and function to the point where individual brain anatomy becomes an important factor. This study investigated detailed sulcal morphology in the parieto-occipital junction. Using cutting-edge methods, it provides important insights into local anatomy, individual variability, and local brain function. The presented work advances the field and will stimulate future research into this important area.

Strengths:

Detailed, very thorough methodology. Multiple raters mapped detailed sulci in a large cohort. The identified sulcal features and their functional and behavioural relevance are then studied using various complementary methods. The results provide compelling evidence for the importance of the described sulcal features and their proposed relationship to cortical brain function.

Reviewer #2 (Public Review):

Summary:

After manually labelling 144 human adult hemispheres in the lateral parieto-occipital junction (LPOJ), the authors 1) propose a nomenclature for 4 previously unnamed highly variable sulci located between the temporal and parietal or occipital lobes, 2) focus on one of these newly named sulci, namely the ventral supralateral occipital sulcus (slocs-v) and compare it to neighbouring sulci to demonstrate its specificity (in terms of depth, surface area, gray matter thickness, myelination, and connectivity), 3) relate the morphology of a subgroup of sulci from the region including the slocs-v to the performance in a spatial orientation task, demonstrating behavioural and morphological specificity. In addition to these results, the authors propose an extended reflection on the relationship between these newly named landmarks and previous anatomical studies, a reflection about the slocs-v related to functional and cytoarchitectonic parcellations as well as anatomic connectivity and an insight about potential anatomical mechanisms relating sulcation and behaviour.

Strengths:

- To my knowledge, this is the first study addressing the variable tertiary sulci located between the superior temporal sulcus (STS) and intra-parietal sulcus (IPS).

- This is a very comprehensive study addressing altogether anatomical, architectural, functional and cognitive aspects.

- The definition of highly variable yet highly reproductible sulci such as the slocs-v feeds the community with new anatomo-functional landmarks (which is emphasized by the provision of a probability map in supp. mat., which in my opinion should be proposed in the main body).

- The comparison of different features between the slocs-v and similar sulci is useful to demonstrate their difference.

- The detailed comparison of the present study with state of the art contextualises and strengthens the novel findings.

- The functional study complements the anatomical description and points towards cognitive specificity related to a subset of sulci from the LPOJ

- The discussion offers a proposition of theoretical interpretation of the findings

- The data and code are mostly available online (raw data made available upon request).

Reviewer #3 (Public Review):

Summary:

72 subjects, and 144 hemispheres, from the Human Connectome Project had their parietal sulci manually traced. This identified the presence of previous undescribed shallow sulci. One of these sulci, the ventral supralateral occipital sulcus (slocs-v), was then demonstrated to have functional specificity in spatial orientation. The discussion furthermore provides an eloquent overview of our understanding of the anatomy of the parietal cortex, situating their new work into the broader field. Finally, this paper stimulates further debate about the relative value of detailed manual anatomy, inherently limited in participant numbers and areas of the brain covered, against fully automated processing that can cover thousands of participants but easily misses the kinds of anatomical details described here.

Strengths:

- This is the first paper describing the tertiary sulci of the parietal cortex with this level of detail, identifying novel shallow sulci and mapping them to behaviour and function.

- It is a very elegantly written paper, situating the current work into the broader field.

- The combination of detailed anatomy and function and behaviour is superb.

Reviewer #1 (Public review):

The manuscript investigates how neuropeptidergic signaling affects sleep regulation in Drosophila larvae. The authors first conduct a screen of CRISPR knock-out lines of genes encoding enzymes or receptors for neuropeptides and monoamines. As a result of this screen, the authors follow up on one hit, the hugin receptor, PK2-R1. They use genetic approaches including mutants and targeted manipulations of PK2-R1 activity in insulin-producing cells (IPCs) to increase total sleep amounts in 2nd instar larvae. Similarly, dilp3 and dilp5 null mutants and genetic silencing of IPCs show increases in sleep. The authors also show that hugin mutants and thermogenetic/optogenetic activation of hugin-expressing neurons caused reductions in sleep. Furthermore, they show through imaging-based approaches that hugin-expressing neurons activate IPCs. A key finding is that wash on of hugin peptides, Hug-γ and PK-2, in ex vivo brain preparations activates larval IPCs, as assayed by CRTC::GFP imaging. The authors then examine how the PK2-R1, hugin, and IPC manipulations affect adult sleep. Finally, the authors examine how Ca2+ responses through CRTC::GFP imaging in adult IPCs are influenced by the wash on of hugin peptides.

Strengths:

(1) This paper builds on previously published studies that examine Drosophila larval sleep regulation. Through the power of Drosophila genetics, this study yields additional insights into what role neuropeptides play in regulation of Drosophila larval sleep.

(2) This study utilizes several diverse approaches to examine larval and adult sleep regulation, neural activity, and circuit connections. The impressive array of distinct analyses provides new understanding into how Drosophila sleep-wake circuitry in regulated across the lifespan.

(3) The imaging approaches used to examine IPC activation upon hugin manipulation (either thermogenetic activation or wash on of peptides) demonstrate a powerful approach for examining how changes in neuropeptidergic signaling affect downstream neurons. These experiments involve precise manipulations as the authors use both in vivo and ex vivo conditions to observe an effect on IPC activity.

Weaknesses:

(1) There is limited discussion of why statistically significant differences are observed in some genetic and temperature controls. This discussion would better support the authors' conclusions.

(2) The functional connectivity of the huginPC-IPC circuit in larvae could be better supported by chemogenetics using real-time calcium imaging (GCaMP).

Comments on revisions:

I would like to thank the authors for the revisions. The inclusion of all sleep metrics, more detailed descriptions in the methods, & a more thorough comparison to other published articles has addressed most of my concerns.

Reviewer #3 (Public review):

Summary:

Sleep affects cognition and metabolism, evolving throughout development. In mammals, infants have fast sleep-wake cycles that stabilize in adults via circadian regulation. In this study, the author performed a genetic screen for neurotransmitters/peptides regulating sleep and identified the neuropeptide Hugin and its receptor PK2-R1 as essential components for sleep in Drosophila larvae. They showed that IPCs express Pk2-R1 and silencing IPCs resulted in significant increase in the sleep amount, which was consistent with the effect they observed in PK2-R1 knock out mutants. They also showed that Hugin peptides, secreted by a subset of Hugin neurons (Hug-PC), activate IPCs through the PK2-R1 receptor. This activation prompts IPCs to release insulin-like peptides (Dilps), which are implicated in the modulation of sleep. They showed that Hugin peptides induce a PK2-R1 dependent calcium (Ca²⁺) increase in IPCs, which they linked to the release of Dilp3, showing a connection between Hugin signaling to IPCs, Dilp3 release and sleep regulation. Additionally, the activation of Hug-PC neurons reduced sleep amounts, while silencing them had the opposite effect. In contrast to the larval stage, the Hugin/PK2-R1 axis was not critical for sleep regulation in Drosophila adults, suggesting that this neuropeptidergic circuitry has divergent roles in sleep regulation across different stages of development.

Strengths:

This study used an updated system for sleep quantification in Drosophila larvae and this method allowed precise measurement of larval sleep patterns which is essential for the understanding of sleep regulation.

The authors performed unbiased genetics screening and successfully identified novel regulators for larval sleep, Hugin and its receptor PK2-R1, making a substantial contribution to the understanding of neuropeptidergic control of sleep regulation.

They clearly demonstrated the mechanism by which Hugin expressing neurons influence sleep through the activation of IPCs via PK2-R1 with Ca2+ responses and can modulate sleep.

Based on the demonstrated activation of PK2-R1 by the human Hugin orthologue Neuromedin U, research on human sleep disorders may benefit from the discoveries from Drosophila since sleep regulating mechanisms are conversed across species.

Weaknesses:

Previously identified weaknesses have been largely addressed by the authors.

Reviewer #1 (Public review):

Summary:

The authors aim to engineer a synthetic system for manipulating ATP homeostasis in budding yeast by expressing the microsporidian nucleotide transporter NTT1, thereby enabling ATP import from the extracellular environment. Using this system, they attempt to test whether intracellular ATP abundance causally regulates replicative lifespan and whether extracellular ATP sensing contributes independently to longevity pathways. The manuscript presents data from ATP biosensing, transcriptomics, mitochondrial perturbations, and microfluidic aging assays to build a dual-mechanism model linking ATP availability, MAPK signaling, mitochondrial function, and aging trajectories.

Strengths:

A major strength of the study is its creative application of xenotopic synthetic biology to directly manipulate ATP homeostasis-an ambitious approach that addresses an important and difficult question in aging biology. The use of complementary methods, including single-cell ATP reporters, microfluidic lifespan measurements, and RNA-seq, generates a rich experimental dataset with the potential to reveal multiple layers of ATP-dependent physiological regulation. The manuscript also raises interesting hypotheses regarding extracellular nucleotide sensing and HOG/MAPK pathway involvement, opening conceptual space for future exploration of ATP-based signaling in yeast.

Weaknesses:

Despite these strengths, the manuscript suffers from several critical weaknesses that undermine the central conclusions. Foremost, the intracellular ATP measurements contradict key interpretations: NTT1 expression lowers ATP levels, yet multiple sections assert or assume that NTT1 increases intracellular ATP via import. This unresolved contradiction propagates throughout the mechanistic model. The authors do not consider or experimentally address the more parsimonious explanation that NTT1 may be a bidirectional ATP transporter, which would unify many perplexing results. Several important analyses are missing (e.g., transcriptomic comparison of NTT1 cells with vs. without ATP), and key signaling claims lack proper validation (e.g., Hog1 quantification, AMPK controls). Additionally, inconsistencies in figures-such as incorrect scale bars, mismatched ATP measurements, and a conceptual model contradicted by the data-further detract from clarity. As a result, the manuscript does not yet convincingly achieve its stated aims, and the current evidence does not adequately support the proposed causal relationships between ATP homeostasis and lifespan.

Reviewer #2 (Public review):

Summary:

This work presents interesting findings where the addition of exogenous ATP extends the replicative lifespan of yeast cells in a way that seems uncorrelated with actual increased intracellular ATP levels or mitochondria. To be clear, the addition of ATP to yeast growth media increases the number of cell divisions per cell in yeast. Expression of the NTT1 ATP transporter gene increases intracellular ATP levels according to LCMS analysis, but the effect on replicative lifespan works without the NTT1 gene and without an intracellular increase in ATP (possibly with a decrease in intracellular ATP), so the effect appears to be independent of the effect on intracellular ATP levels or mitochondria, as mitochondria-less R0 yeast cells also have increased numbers of cell division when grown with extracellular ATP. The plots in Figure 5 make it seem like exogenous ATP addition lowers intracellular ATP for both the NTT1 cells and the wild-type cells, and that is not what the data in Figure 2d with LCMS shows.

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

Restated, the data suggest they were successful in increasing intracellular ATP by LCMS, but not by queen reporter, and that the seemingly likely increased intracellular ATP was not causative, as cells that did not have an increase in intracellular ATP, but had the same exogenous ATP addition, also gained an increase in replicative lifespan. There could also be two distinct mechanisms extending replicative lifespan to the same degree in these two different strains. More measurements, controls, and analyses are needed to accurately determine what is happening with intracellular ATP levels with age. It is currently unknown if there is any correlation between ATP levels and replicative aging (with properly controlled longitudinal measurements).

Strengths:

Longitudinal imaging of single cells. Analyzed ATP levels with two approaches. Creative approach to use NTT1 transporter to increase intracellular ATP levels. Solid replicative lifespan data.

Weaknesses:

Mostly unclear about ATP levels with age and the relationship, or lack thereo,f between intracellular ATP levels and replicative lifespan. No idea what this effect depends on, but some ideas what it does not depend on (mitochondria or increased intracellular ATP). Experiments seem to lack biological controls (cells without gfp) for age related changes in autofluorescence (and pH that can affect gfp signal) for the fluorescent microscopy quantifying ATP with age using the QUEEN reporter (seems that way as written); conflicting evidence on ATP levels; lack of LC-MS measurements in old cells; no apparent correlation between ATP levels and replicative lifespan, but that could be wrong - just not apparent from the longitudinal data plots. The LCMS data seems better than the microscopy data on ATP because the microscopy approach seems to lack proper biological controls, and the selection of only the top 40% of pixels to quantify signal seems unjustified as written, and possibly prone to technical artifacts. Figure 2 B&C plots of ATP levels should show what the cells were normalized to. The figures also seem too diluted and should probably be combined or put in the supplements (hog1 western) if they do not relate to the lifespan effect. There seem to be some technical scientific editorial errors, like in Figure 7.

Reviewer #1 (Public review):

Summary:

In this manuscript, Henning et al. examine the impact of GABAergic feedback inhibition on the motion-sensitive pathway of flies. Based on a previous behavioral screen, the authors determined that C2 and C3, two GABAergic inhibitory feedback neurons in the optic lobes of the fly, are required for the optomotor response. Through a series of calcium imaging and disruption experiments, connectomics analysis, and follow-up behavioral assays, the authors concluded that C2 and C3 play a role in temporally sharpening visual motion responses. While this study employs a comprehensive array of experimental approaches, I have some reservations about the interpretation of the results in their current form. I strongly encourage the authors to provide additional data to solidify their conclusions. This is particularly relevant in determining whether this is a general phenomenon affecting vision or a specific effect on motion vision. Knowing this is also important for any speculation on the mechanisms of the observed temporal deficiencies.

Strengths:

This study uses a variety of experiments to provide a functional, anatomical, and behavioral description of the role of GABAergic inhibition in the visual system. This comprehensive data is relevant for anyone interested in understanding the intricacies of visual processing in the fly.

Weaknesses:

The most fundamental criticism of this study is that the authors present a skewed view of the motion vision pathway in their results. While this issue is discussed, it is important to demonstrate that there are no temporal deficiencies in the lamina, which could be the case since C2 and C3, as noted in the connectomics analysis, project strongly to laminar interneurons. If the input dynamics are indeed disrupted, then the disruption seen in the motion vision pathway would reflect disruptions in temporal processing in general and suggest that these deficiencies are inherited downstream. A simple experiment could test this. Block C2, C3, and both together using Kir2.1 and shibiere independently, then record the ERG. Alternatively, one could image any other downstream neuron from the lamina that does not receive C2 or C3 input.

Figure 6c. More analysis is required here, since the authors claim to have found a loss in inhibition (ND). However, the difference in excitation appears similar, at least in absolute magnitude (see panel 6c), for PD direction for T4 C2 and C3 block. Also I predict that C2&C3 block statistically different from C3 only, why? In any case, it would be good to discuss the clear trend in the PD direction by showing the distribution of responses as violin plots to better understand the data. It would be also good to have some raw traces to be able to see the differences more clearly, not only polar plots and averages.

The behavioral experiments are done with a different disruptor than the physiological ones. One blocks chemical synapses, the other shunts the cells. While one would expect similar results in both, this is not a given. It would be great if the authors could test the behavioral experiments with kir2.1 too.

Comments on revisions:

I have no further comments.

Reviewer #2 (Public review):

The work by Henning et al. explores the role of feedback inhibition in motion vision circuits, providing the first identification of inhibitory inheritance in motion-selective T4 and T5 cells of Drosophila. Among the strengths of this work is the verification of the GABAergic nature of C2 and C3 with genetic and immunohistochemical approaches. In addition, double-silencing C2&C3 experiments help to establish a functional role for these cells. The authors holistically use the Drosophila toolbox to identify neural morphologies, synaptic locations, network connectivity, neuronal functions and the behavioral output.

A limitation of the study is that the mediating neural correlates from C2&C3 to T4&T5 are not clarified, rather Mi1 is found to be one of them. In the future, the same set of silencing experiments performed for C2-Mi1 could be extended to C2 &C3-Tm1 or Tm4 to find the T5 neural mediators of this feedback inhibition loop. Future experiments might also disentangle the parallel or separate function of C2 and C3 neurons.

In summary, this work advances our current knowledge in Drosophila motion vision and sets the way for further exploring the intricate details of direction selective computations.

Comments on revisions:

A label for T5 is missing from Figure 5b. Thank you for addressing our concerns and considering each of our suggestions.

Reviewer #1 (Public review):

Summary:

In this study, authors employed comprehensive proteomics and transcriptomics analysis to investigate the systemic and organ-specific adaptations to IF in male and they found that shared biological signaling processes were identified across tissues, suggesting unifying mechanisms linking metabolic changes to cellular communication, which reveal both conserved and tissue-specific responses by which IF may optimize energy utilization, enhance metabolic flexibility, and promote cellular.

Strengths:

This study detected multiple organs including liver, brain and muscle and revealed both conserved and tissue-specific responses to IF.

Weaknesses:

(1) Why did the authors choose liver, brain and muscle but not other organs such as heart and kidney? The latter are proven to be the large consumer of ketones, which is also changed in the IF treatment of this study.

(2) The proteomics and transcriptomics analysis were only performed at 4 months. However, a strong correlation between IF and the molecular adaptions should be time points-dependent.

(3) The context lack section of "discussion", which shows the significance and weakness of the study.

(4) There is no confirmation for the proteomic and transcriptomic profiling. For example, the important changes in proteomics could be further identified by a Western blot.

Reviewer #2 (Public review):

Summary:

Fan and colleagues measure proteomics and transcriptomics in 3 organs (liver, skeletal muscle, cerebral cortex) from male C57BL/6 mice to investigate whether intermittent fasting (IF; 16h daily fasting over 4 months) produces systemic and organ-specific adaptations.

They find shared signaling pathways, certain metabolic changes and organ-specific responses that suggest IF might affect energy utilization, metabolic flexibility while promoting resilience at the cellular level.

Strengths:

The fact that there are 3 organs and 2 -omics approaches is a strength of this study.

Weaknesses:

Poor figures presentation and knowledge of the literature. One sex (male).

On resubmission the Authors' decision to discriminate the organ-specific from the organ-shared effects of intermittent fasting (IF) also enabled them to more precisely determine the lack of correspondence between transcriptomics and proteomics, i.e., not all transcripts lead to protein translation.

Reviewer #3 (Public review):

Summary:

Fan et al utilize large omics data sets to give an overview of proteomic and gene expression changes after 4 moths of intermittent fasting (IF) in liver, muscle and brain tissue. They describe common and district pathways altered under IF across tissues using different analysis approaches. Main conclusions presented are the variability in responses across tissues with IF. Some common pathways were observed, but there were notable distinctions between tissues.

Strengths:

(1) The IF study was well conducted and ran out to 4 months which was a nice long-term design.

(2) The multi omics approach was solid and additional integrative analysis was complementary to the illustrate the differential pathways and interactions across tissues.

(3) The authors did not over-step their conclusions and imply an overreached mechanism.

Weaknesses:

The weaknesses, which are minor, include use of only male mice and the early start (6 weeks) of the IF treatment. However, the authors have provided justification on why they chose male mice and the time points used in the study.

Reviewer #1 (Public review):

Summary:

This study investigated the immunogenicity of a novel bivalent EABR mRNA vaccine for SARS-CoV-2 that expresses enveloped virus-like particles in pre-immune mice as a model for boosting the population that is already pre-immune to SARS-CoV-2. The study builds on promising data showing a monovalent EABR mRNA vaccine induced substantially higher antibody responses than a standard S mRNA vaccine in naïve mice. In pre-immune mice, the EABR booster increased the breadth and magnitude of the antibody response, but for Omicron, the effects were modest and often not statistically significant. The authors provide compelling evidence to support this may be due to immune imprinting.

This study also builds on prior work with additional experiments to elucidate the mechanisms that contributed to the EABR increased immunogenicity in naive mice including evidence that the vaccine is inducing responses to more RBD epitopes and a potential role for heterodimer formation as a mechanism whereby bivalent vaccines induce cross-reactive B cell responses.

Strengths:

Evaluating a novel SARS-CoV-2 vaccine that was substantially superior in naive mice in pre-immune mice as a model for its potential in the pre-immune population.

Providing insight into a possible role of immune imprinting in shaping immune responses to updated booster immunizations.

Minor weaknesses:

(1) Overall, immune responses against Omicron variants were substantially lower than against the ancestral Wu-1 strain that the mice were primed with. The authors speculate this is evidence of immune imprinting. While parallel controls (mice immunized 3 times with just the bivalent EABR vaccine) were not tested, the authors point to prior published work showing Omicron S antigen is a strong immunogen. This indicates the lower immune responses to Omicron are likely due to immune imprinting (or original antigenic sin) and not due to S immunogen being inherently less immunogenic than the S protein from the ancestral Wu-1 strain.

(2) The authors reported statistically significant increase in antibody responses with the bivalent EABR vaccine booster when compared to the monovalent S mRNA vaccine but consistently failed to show significantly higher responses when compared to the bi-valent S mRNA vaccine suggesting that in pre-immune mice, the EABR vaccine has no apparent advantage over the bivalent S mRNA vaccine which is the current standard. There were, however, some trends indicating the group sizes were insufficiently powered to see a difference. The discussion acknowledges these limitations of their studies and potential limited benefits of the EABR strategy in pre-immune mice vs standard bivalent mRNA vaccine.

(3) The EABR S mRNA vaccine was superior to the conventional mRNA S vaccine in naïve mice but not in pre-immune mice. The authors expanded the discussion to propose a possible role for immune imprinting in this result which is supported by the data.

Reviewer #3 (Public review):

Summary:

The authors evaluated a novel bivalent (Wu1/BA.5 based) mRNA platform that uses the EABR strategy to produce enveloped virus-like particles for vaccination. These were tested as boosters in the context of pre-existing immunity in mice that received two prior immunizations with conventional Wu1 mRNA vaccines. The animal experimental timeline aimed at mimicking the vaccinations/booster schedule implemented during the COVID-19 pandemia. The authors tested and compared different booster strategies: (1) conventional Wu1 S protein encoding mRNA vaccine, (2) EABR Wu1 S protein encoding mRNA vaccine that produces enveloped virus-like particles, (3) conventional Wu1/BA.5 S protein encoding mRNA vaccine, and (4) EABR Wu1/BA.5 S protein encoding mRNA vaccine that produces enveloped virus-like particles. The EABR approach (monovalent or bivalent) enhanced the antibody response against Wu1 and Omicron subvariants. Interestingly, the bivalent EABR Wu1/BA.5 mRNA (strategy 4) generated polyclonal sera targeting multiple receptor-binding domain epitopes: these sera were more diverse than those generated with the other tested booster strategies (1 to 3).

Strengths:

The monovalent Wu1 S-EABR mRNA booster led to increase in antibody binding to tested Omicron variants (BA.5, BQ.1.1, XBB.1), while the bivalent Wu1/BA.5 S-EABR mRNA booster led to the highest Ab response against Omicron variants (BA.5, BQ.1.1, XBB.1) in pre-vaccinated mice.

Neutralization assays showed that the monovalent Wu1 S-EABR mRNA booster had the highest Wu1 neutralization activity and to a lesser extent the early BA.1 early Omicron variant. The monovalent Wu1 S-EABR mRNA booster and bivalent Wu1/BA.5 S-EABR mRNA booster had similar BA.5 neutralizing activity. Neutralizing activity of the different boosters was less pronounced with later Omicron variants BQ.1.1 and XBB.1. However, of the different boosters tested, the bivalent Wu1/BA.5 S-EABR mRNA booster induced the highest neutralizing titers. These results support that the EABR mRNA vaccine strategy helps improve neutralizing activity against different tested Omicron subvariants: a few (1 or 2) mRNA constructs expressing major antigens in enveloped virus-like particles likely provide a novel strategy to elicit an immune response that has the potential to neutralize subsequent variants.

The EABR enveloped virus-like particle strategy induces a more diverse antibody response, including epitopes not recognized by the other booster strategies: these new epitopes could play a role in neutralizing activity against new future variants.

Moreover, the bivalent Wu1/BA.5 S-EABR mRNA booster could potentially produce heterotrimeric S proteins to help activation of cross-reactive B cells and increase polyclass antibody responses.

Weaknesses:

When it comes to later Omicron variants (BQ.1.1 and XBB.1), there is a discrepancy between epitope binding response and neutralization titers: only a few binding antibodies have neutralizing activity with these later variants, showing a limitation of the EABR strategy.

The authors showed that the EABR mRNA strategy represents a novel antigen exposing strategy where antigens are produced at the cell surface and also at the surface of enveloped virus-like particles. This allows the production of novel antigens in addition to those that would be typically generated against cell surface exposed antigens. These novel antigens targeting new epitopes could potentially have neutralizing activity.

Using a bivalent EABR mRNA booster led to higher antibody titers and higher neutralizing activity. The challenge is to select the best antigen target/variant to support neutralizing activity against later virus variants.

Reviewer #1 (Public review):

Summary:

This study delineates a highly specific role for the pPVT in unconditioned defensive responses. The authors use a novel, combined SEFL and SEFR paradigm to test both conditioned and unconditioned responses in the same animal. Next, a c-fos mapping experiment showed enhanced PVT activity in the stress group when exposed to the novel tone. No other regions showed differences. Fiber photometry measurements in pPVT showed enhancement in response to the novel tone in the stressed but not non-stressed groups. Importantly, there were also no effects when calcium measurements were taken during conditioning. Using DREADDS to bidirectionally manipulate global pPVT activity, inhibition of the PVT reduced tone freezing in stressed mice while stimulation increased tone freezing in non-stressed mice.

Strengths:

A major strength of this research is the use of a multi-dimensional behavioral assay that delineates behavior related to both learned and non-learned defensive responses. The research also incorporates high-resolution approaches to measure neuronal activity and provide causal evidence for a role for PVT in a very narrow band of defensive behavior. The data are compelling, and the manuscript is well-written overall.

Weaknesses:

Figure 1 shows a small, but looks to be, statistically significant, increase in freezing in response to the novel tone in the no-stress group relative to baseline freezing. This observation was also noticed in Figures 2 and 7. The tone presented is relatively high frequency (9 kHz) and high dB (90), making it a high-intensity stimulus. Is it possible that this stimulus is acting as an unconditioned stimulus? In addition, in the final experiment, the tone intensity was increased to 115 dB, and the freezing % in the non-stressed group was nearly identical (~20%) to the non-stressed groups in Figures 1-2 and Figure 7. It seems this manipulation was meant as a startle assay (Pantoni et al., 2020). Because the auditory perception of mice is better at high frequencies (best at ~16 kHz), would the effect seen be evident at a lower dB (50-55) at 9 kHz? If the tone was indeed perceived as "neutral," there should be no freezing in response to the tone. This complicates the interpretation of the results somewhat because while the authors do admit the stimulus is loud, would a less loud stimulus result in the same effect? Could the interaction observed in this set of studies require not a novel tone, but rather a high-intensity tone that elicits an unconditioned response? Along these same lines, it appears there may be an elevation in c-fos in the PVT in the non-stress tone test group versus the no-stress home cage control, and overall it appears that tone increases c-fos relative to homecage. Could PVT be sensitive to the tone outside of stress? Would there be the same results with a less intense stimulus? I would also be curious to know what mice in the non-stressed group were doing upon presentation of the tone besides freezing. Were any startle or orienting responses noticed?

Comments on revisions:

Following revision, this reviewer felt all of the above concerns were addressed.

Reviewer #2 (Public review):

Summary:

Nishimura and colleagues present findings of a behavioral and neurobiological dissociation of associative and nonassociative components of Stress Enhanced Fear Responding (SEFR).

Strengths:

This is a strong paper that identifies the PVT as a critical brain region for SEFR responses using a variety of approaches, including immunohistochemistry, fiber photometry, and bidirectional chemogenetics. In addition, there is a great deal of conceptual innovation. The authors identify a dissociable behavior to distinguish the effects of PVT function (among other brain regions).

Weaknesses:

(1) The authors find a lack of difference between the Stress and No Stress groups in pPVT activity during SEFL conditioning with fiber photometry but an increase in freezing with Gq DREADD stimulation. How do authors reconcile this difference in activity vs function?

(2) Because the PVT plays a role in defensive behaviors, it would be beneficial to show fiber photometry data during freezing bouts vs exclusively presented during tone a shock cue presentations.

(3) Similar to the above point, were other defensive behaviors expressed as a result of footshock stress or PVT manipulations?

(4) Tone attenuation in Figure 8 seems to be largely a result of minimal freezing to a 115-dB tone. While not a major point of the paper, a more robust fear response would be convincing.

(5) In the open field test, the authors measure total distance. It would be beneficial to also show defensive behavioral (escape, freezing, etc) bouts expressed.

(6) The authors, along with others, show a behavioral and neural dissociation of footshock stress on nonassociative vs associative components of stress; however, the nonassociative components as a direct consequence of the stress seem to be necessary for enhancement of associative aspects of fear. Can authors elaborate on how these systems converge to enhance or potentiate fear?

(7) In the discussion, authors should elaborate on/clarify the cell population heterogeneity of the PVT since authors later describe PVT neurons as exclusively glutamatergic.

Comments on revisions:

Following revision, this reviewer felt all of the above concerns were addressed.

Reviewer #3 (Public review):

Summary:

The manuscript by Nishimura et al. examines the behavioural and neural mechanisms of stress-enhanced fear responding (SEFR) and stress-enhanced fear learning (SEFL). Groups of stressed (4 x shock exposure in a context) vs non-stressed (context exposure only) animals are compared for their fear of an unconditioned tone, and context, as well as their learning of new context fear associations. Shock of higher intensity led to higher levels of unlearned stress-enhanced fear expression. Immediate early gene analysis uncovered the PVT as a critical neural locus, and this was confirmed using fiber photometry, with stressed animals showing an elevated neural signal to an unconditioned tone. Using a gain and loss of function DREADDs methodology, the authors provide convincing evidence for a causal role of the PVT in SEFR.

Strengths:

(1) The manuscript uses critical behavioural controls (no stress vs stress) and behavioural parameters (0.25mA, 0.5mA, 1mA shock). Findings are replicated across experiments.

(2) Dissociating the SEFR and SEFL is a critical distinction that has not been made previously. Moreover, this dissociation is essential in understanding the behavioural (and neural) processes that can go awry in fear.

(3) Neural methods use a multifaceted approach to convincingly link the PVT to SEFR: from Fos, fiber photometry, gain and loss of function using DREADDs.

Weaknesses:

No weaknesses were identified by this reviewer; however, I have the following comments:

A closer examination of the Test data across time would help determine if differences may be present early or later in the session that could otherwise be washed out when the data are averaged across time. If none are seen, then it may be worth noting this in the manuscript.

Given the sex/gender differences in PTSD in the human population, having the male and female data points distinguished in the figures would be helpful. I assume sex was run as a variable in the statistics, and nothing came as significant. Noting this would also be of value to other readers who may wonder about the presence of sex differences in the data.

Comments on revisions:

Following revision, this reviewer felt all of the above comments were addressed.

Reviewer #1 (Public review):

It is well established that many potivirids (viruses in the Potiviridae family) particularly potyviruses (viruses in the Potyvirus genus) recruit (selectively) either eIF4E or eIF(iso)4E, while some others can use both of them to ensure a successful infection. CBSD caused by two potyvirids, i.e., ipomoviruses CBSV and UCBSV severely impedes cassava production in West Africa. In a previous study (PBI, 2019), Gomez and Lin (co-first authors), et al. reported that cassava encodes five eIF4E proteins including eIF4E, eIF(iso)4E-1, eIF(iso)4E-2, nCBP-1 and nCBP-2, and CBSV VPg interacts with all of them (Co-IP data). Simultaneous CRISPR/Cas9-mediated editing of nCBp-1 and -2 in cassava significantly mitigate CBSD symptoms and incidence. In this study, Lin et al further generated all five eIF4E family single mutants as well as both eIF(iso)4E-1/-2 and nCBP-1/-2 double mutants in a farmer-preferred casava cultivar. They found that both eIF(iso)4E and nCBP double mutants show reduced symptom severity and the latter is of better performance. Analysis of mutant sequences revealed one important point mutation L51F of nCBP-2 that may be essential for the interaction with VPg. The authors suggest that introduction of L51F mutation into all five eIF4E family proteins may lead to strong resistance. Overall I believe this is an important study enriching knowledge about eIF4E as a host factor/susceptibility factor of potyvirids and proposing new information for the development of high CBSD resistance in cassava. I suggest the following two major comments for authors to consider for improvement:

(1) As eIF(iso)4e-1/-2 or nCBP-1/-2 double mutans show resistance, why not try to generate a quadruple mutant? I believe it is technically possible through conventional breeding.

(2) I agree that L51F mutation may be important. But more evidence is needed to support this idea. For example. Authors may conduct quantitative Y2H assay on binding of VPg to each of eIF4E (L51F) mutants. Such data may

Comments on revisions:

(1) The authors explained it is technically challenging to generate quadruple mutant.<br /> (2) The authors have properly addressed my comment 2.<br /> I do not have more concerns.

Reviewer #2 (Public review):

Eukaryotic translation initiation factor 4E (eIF4E) acts as a key susceptibility factor for members of the Potyviridae family, and knockout of eIF4E family members enables the generation of corresponding virus-resistant germplasm. In this study, the authors performed systematic knockout experiments on the members of eIF(iso)4E and nCBP clades in cassava, which demonstrated that simultaneous knockout of the eIF4E-family genes nCBP-1 and nCBP-2 in the cultivar 60444 significantly attenuates Cassava Brown Streak Disease (CBSD) root symptoms and reduces viral titer. The authors further screened for CBP mutants without VPg-binding activity and identified the nCBP-2 L51F mutant, which loses the ability to interact with VPg. In the revised manuscript, the authors have addressed most of my previous questions and revised the relevant content accordingly. Overall, this study is a well-performed work, with extensive explorations carried out particularly in the gene knockout of members of eIF(iso)4E and nCBP. It provides an important value for investigating the functions of eIF(iso)4E and nCBP clade members in the development of disease-resistant germplasm, and the identified nCBP-2 L51F mutant also offers a crucial gene editing site target for the generation of virus-resistant cassava germplasm in future.

Reviewer #3 (Public review):

In the manuscript, the authors generated several mutant plants defective in the eIF4E family proteins and detected cassava brown streak viruses (CBSVs) infection in these mutant plants. They found that CBSVs induced significantly lower disease scores and virus accumulation in the double mutant plants. Furthermore, they identified important conserved amino acid for the interaction between eIF4E protein and the VPg of CBSVs by yeast two hybrid screening. The experiments are well designed, however, some points need to be clarified:

(1) The authors reported that the ncbp1 ncbp2 double mutant plants were less sensitive to CBSVs infection in their previous study, and all the eIF4E family proteins interact with VPg. In order to identify the redundancy function of eIF4E family proteins, they generated mutants for all eIF4E family genes, however, these mutants are defective in different eIF4E genes, they did not generate multiple mutants (such as triple, quadruple mutants or else) except several double mutant plants, it is hard to identify the redundant function eIF4E family genes.

(2) The authors identified some key amino acids for the interaction between eIF4E and VPg such as the L51, it is interesting to complement ncbp1 ncbp2 double mutant plants with L51F form of eIF4E and double check the infection by CBSVs.

Comments on revisions:

The reviewer understand Cassava is not a model plant, it is hard for the authors to generate multiple genetic mutant plants for experiments, so nothing was done to respond to the comments raised by the reviewer.

Reviewer #1 (Public review):

Summary:

The authors aimed to determine whether reward conditioning increases inhibitory regulation of Vglut1-expressing BLA→NAc neurons and whether this inhibition shapes motivated behaviors. They used whole-cell electrophysiology to measure conditioning-induced changes in synaptic inhibition and intrinsic excitability. Subsequently, they employed dual-recombinase chemogenetics to selectively inhibit this projection during behavioral tasks. The goal was to test whether suppressing the activity of Vglut1-expressing neurons would alter reward learning, valuation, and fear discrimination.

Strengths:

(1) The combination of electrophysical and behavioral assessments to dissect the function of Vglut1-expressing BLA→NAc neurons.

(2) The various behavioral assessments employed to determine the effect of silencing Vglut1-expressing BLA→NAc neurons.

Weaknesses:

(1) The introduction underscores the importance of molecular identity and population dynamics when studying the function of BLA→NAc neurons. Yet, the experiments and manuscript provide little to no information about the Slc17a7-expressing population under study. In fact, there is no evidence that the viral manipulations targeted this neuronal population (e.g., extent and specificity of viral transduction). Regarding population dynamics, evidence is meant to be provided by Experiment 1, but the results are difficult to interpret. The control mice were not exposed to the conditioning chambers, stimuli, or food rewards. These exposures may have been sufficient to produce the changes observed in the experimental mice (i.e., they may have had nothing to do with cue-reward learning). Further, the experiments provide no evidence that the observed effects result from prolonged conditioning, since there is no group receiving a single conditioning session.

(2) The dual-recombinase approach employed does not permit conclusions about the BLA→NAc pathway specifically, because the effects of silencing NAc-projecting BLA neurons could be driven by modulation of activity in other brain regions innervated by these same neurons through collateral projections. This limitation must be clearly acknowledged by the authors, and the manuscript should refrain from making definitive claims about the BLA→NAc pathway per se.

(3) The experimental parameters and measures used for cued-reward conditioning complicate any firm conclusions about the observed effects. The use of a 2-second cue provides a minimal temporal window to monitor cue-related behavior. This issue is masked in the data presented because what is labeled as "cued responses" includes responses that occur after the cue has terminated and overlap with those triggered by sucrose delivery itself. These post-cue responses cannot be classified as cue-reward responses since the cue is no longer present; they are reward-related responses. Perhaps the z-score calculation addresses this issue, but this is difficult to assess since the authors do not explain how this calculation was performed or what baseline period was used.

(4) Throughout the manuscript, there is conceptual confusion regarding the fundamental distinction between Pavlovian (cue-outcome) and instrumental (action-outcome) responses. It is unclear why the authors aimed to study both types of conditioning, but greater caution is necessary when interpreting the findings labeled as "instrumental conditioning." First, no evidence is provided that initiation port entries constitute an instrumental or goal-directed response rather than a Pavlovian approach behavior. Second, many of the conclusions are based on analyzing reward port entries-a Pavlovian conditioned response identical to that measured in the cued-reward conditioning task. This conflation undermines claims about instrumental learning.

(5) The data from the reward valuation and reversal learning experiments are difficult to interpret. The animals are not tested under extinction conditions (with the flavors present but without reward delivery), making it impossible to establish whether their behavior relies on learned associations or ongoing reinforcement. Further, the behavior generated by these procedures appears unreliable, with substantial inconsistencies across figures (compare Figure 4A with Figures 5B, C, G, H).

(6) The results from the auditory fear discrimination procedure are also difficult to interpret. No conditioning data are presented, and the "enhanced discrimination" could simply reflect reduced overall responding to the CS-. It is not clear how this selective impact on the CS- fits with the authors' conclusions about enhanced associative salience (noting that the meaning of the latter remains obscure).

(7) The manuscript contains several statements about behavioral outcomes that are not supported by statistical evidence. The list provided here is non-exhaustive, and the authors should carefully correct any conclusions that lack statistical support.<br /> a) Line 294 (Figure 2F): the control mice gradually reached a similar performance to the experimental mice.<br /> b) Lines 301-303 (Figures 3D-F): inhibition strengthened the temporal association between initiation and reward consumption.<br /> c) Lines 337-339 (Figure 4A): both groups increased their preference for 10% sucrose.

(8) The manuscript suffers from a lack of clarity and/or transparency about experimental parameters and data. Clarifications about the following would be necessary for the reader to confidently interpret the findings.<br /> a) Number of animals of each sex in each group.<br /> b) Number of animals excluded and justification.<br /> c) Analysis of sex differences.<br /> d) A clarification on the control group used in the electrophysiological experiment.<br /> e) Whether the same animals progress through multiple behavioral paradigms or if separate cohorts are used.<br /> f) All protocols should be described in the methods section.

Without clarifying the points made above, a reliable and fair assessment of the discussion is impossible.

Reviewer #2 (Public review):

Summary:

This study by Mercer et al. focused on Vglut1 neurons in the BLA that project to the NAc. They characterized reward conditioning-induced electrophysiological changes in these neurons, including a decrease in membrane excitability and an increase in inhibitory synaptic inputs onto them, and showed the consequences of reducing their activity in enhancing reward-seeking behaviors. Considering that Vglut1 neurons represent the majority of the BLA→NAc projecting neurons, the findings are important for potentially correcting some of the previous biases in understanding the role of BLA-to-NAc projection in reward processing, for example, the notion that this projection generally promotes reward seeking by conveying reward-associated cue information.

Strengths:

The paper is clearly written, with results strongly supporting the main conclusions for the most part.

There are a few weaknesses noted. For example:

(1) They used a retrograde recombinase strategy to drive DREADD expression in these cells; however, it is not known if they project exclusively to NAc or to other brain regions as well, and whether those other potential regions may mediate the DREADDs (Gi) effects on reward seeking. They also did not show which subregions of the NAc were innervated by these neurons.

(2) They did not assess potential changes in excitatory synaptic transmission onto these cells after reward conditioning, which leaves a gap in concluding a shift toward inhibition.

(3) They also did not report on whether the inhibition was specific to Vglut1 neurons.

(4) Some statistics appear missing (Figure 3D-F), not optimal (Figure 5CEF and HJK using separate t-tests rather than repeated measure ANOVA), not clear (Figure 2I on peak timing or port entry), or has low n number (Figure 1 Ephys, animal-based manipulations).

(5) They did not clarify why they used two different doses of the DREADDs ligand Compound 21 at 0.1 or 0.3 mg/kg for different experiments.

Reviewer #3 (Public review):

Summary:

This study by Mercer et al. investigates how inhibitory modulation of basolateral amygdala neurons expressing Vglut1 and projecting to the nucleus accumbens (Vglut1BLA→NAc) influences motivated behavior in both appetitive and aversive tasks. Using a combination of whole-cell electrophysiology, chemogenetic inhibition and behavioral tests, the authors demonstrate that (1) reward conditioning increases inhibitory synaptic input and reduces intrinsic excitability of Vglut1BLA→NAc neurons, (2) chemogenetic inhibition of these neurons enhances the number of conditioned approaches in a Pavlovian task and the number of nosepoke responses in an instrumental task, elevates reward valuation, and increases fear discrimination and (3) these effects are linked to salience assignment and associative strength, rather than altered learning or reversal flexibility. The work challenges the classical excitatory function usually reported about the BLA projection to the NAc and highlights an interesting and thought-provoking result. Nevertheless, the study does not address the potential effect of their manipulation on motoric impulsivity, nor did they provide a theoretical framework explaining this unorthodox yet interesting effect.

Strengths:

The study establishes the initial finding with a correlational approach that informs a causal study. They find convincingly that Pavlovian conditioning induces an increase in inhibitory inputs onto Vglut1BLA→NAc neurons that leads to reduced excitability. Causality is studied using a powerful dual recombinase chemogenetic strategy to selectively inhibit this population of Vglut1BLA→NAc neurons and determine the effect on different behavioral tasks. The use of different tasks provides convergence on their effect. This surprising finding provokes interest and will stimulate further investigation into the mechanisms underlying these effects.

Weaknesses:

Several important aspects of the evidence remain incomplete.

(1) First, an important aspect of the underlying processes at play remains to be investigated. In all behavioral tasks, the authors find that their manipulation increases responding that they interpret as a facilitation of learning. However, none of the appetitive tasks include a control stimulus that could address the specificity of their effect. Given that on the Pavlovian task, responding to the CS is almost 100%, I suspect that their manipulation may induce motoric impulsivity. This aspect would clearly benefit from additional controls.

(2) Second, I have several interrogations about the time-resolved probability of port entries (PSTHs).

a) There is a mismatch between the results presented in Figure 1. Panel D shows a peak of responses on the PSTH at ~2s on day 5 (my remark applies to all days), suggesting that the average should lie around this value. However, panel C reports a latency to respond at ~4sec. Could the authors double-check their PSTHs?

b) More generally, the fact that in the Pavlovian task all PSTHs show a peak at almost exactly 2 sec is quite surprising and raises questions about how they are constructed. Sure, the most salient event is the water drop occurring 2s after cue onset. Yet, if mice responded only to these drops, the peak response should occur at 2s+reaction time, which is not the case. Figure 2 shows that on the first acquisition day, responding is already centered around 2s and does not decrease with learning, except for treated animals.

(3) Several methodological flaws are present.

a) The authors need to report clearly the statistics. In most cases, the statistical test used is mentioned in the figure caption with a single P-value. Thus, on two-way ANOVAs, I do not know whether the P-value relates to the interaction, the main effects, or the post-hoc tests.

b) Another important issue is related to the average time-resolved z-score probability of port entries. The bin size used, the smoothing (that is much too strong), and the baseline period used to calculate the z-score are absent from the methods.

(4) This study reports that manipulating 70% of the glutamatergic projection to the NAc induces an effect opposed to what has been previously reported in many different studies. Such a surprising finding deserves a more elaborate discussion about the mechanism that could be at play.

Reviewer #1 (Public review):

This paper presents another excellent, sophisticated analysis from this group of brain-wide neural activity correlated with the tracking of belief about the generative state of a stochastic visual environment under volatile conditions. Whereas previous work focussed on the normative belief-updating dynamics mainly in brain areas related to motor planning, under conditions where the environmental state translates directly to a correct action, here, they abstract the belief-updating DV from a specific action by instead associating the environmental state to a stimulus-response mapping rule, to be used in a simple perceptual decision coming up after the environmental state cues. A decoding analysis shows that a remarkably large portion of the brain has activity correlated with the normatively evolving belief about environmental state and the evidence samples feeding into that belief. What the authors were trying to achieve, however, seems far more general than the above, namely, to study "the algorithmic and neural basis of higher-order internal decisions about behavioural context, formed under multiple sources of uncertainty", and I think that the loose implication of such grand notions (such phrasing brings to mind someone's choice to believe in God, to regulate their behaviour depending on whether they are on a rugby pitch or at church, etc, not how grating orientations link to left/right hand movements) muddies the value of the study. The authors thus may have overestimated the generality of the findings. I hope my impressions are a useful guide to focus the interpretations more.

Strengths:

One of the main strengths of the study is that it is a technical tour de force. As reflected in an unusually extensive methods section, the authors put an extraordinary amount of work into rigorous data collection and analysis, and all of it is described in excellent detail. The study also builds in a very valuable way on previous landmark studies on tracking of volatile environmental state linked to correct actions using MEG (Murphy et al 2021) and tracking of volatile stimulus-response mappings using fMRI (van den Brink et al 2023). Here, the environmental state is not directly linked to actions during the cues informing about the state, but instead linked to a stimulus-response mapping rule.

Weaknesses:

It is surprising, given this main innovation of abstracting the decision about visual position-distribution from particular actions, that the authors do not engage with the literature using EEG and fMRI to study such 'abstract,' 'motor-independent' or 'domain-general' (synonymous terms) decisions. The discussion, for example, mentions the curious lack of involvement of the frontal cortex, and the possibility of intermingled opposites being represented there; motor-independent EEG decision signals have been characterised by regressing against the absolute value of the differential belief-updating process for this very reason (e.g., see Pares-Pujolras et al 2025). Single-unit studies like Bennur & Gold (2011) have also found activity related to a decision about environmental state (non-volatile motion) even when that state does not yet translate directly to an action, and, like the current study, is instead specified in a later frame of the trial.

Another weakness, as mentioned above, is that of overgeneralisation. It is not clear how "higher-order, internal decisions" are generally defined, and terms more concretely grounded in the paradigm at hand (as in van den Brink et al (2023)), e.g., 'tracking of environmental state dictating a sensory-motor mapping rule,' would seem more useful. Since this task tracks a belief about a sensory feature and how it maps to motor actions, it may not be as surprising a revelation that a range of sensorimotor areas correlate with it, as compared to more general, truly internal decisions about behavioural context involving no sensory input (e.g., deciding one has become hungry). Similarly, the authors paint the belief-tracking process of Murphy et al (2021) as "lower-order" and the current one as higher-order, but both cases are the same in that a hidden binary generative state needs to be inferred on a continual basis from a series of discrete spatial positions presented visually. The only difference is that in the current case, the belief about the current binary state is not transformed directly into an immediate action choice but rather utilised to map a follow-up stimulus to its appropriate action. These decisions then happen one after the other in sequence, with a contingency, but I'm not sure this constitutes a 'high-level' and 'low-level' in the way implied by the authors.

The paper left me confused on the question of what these widespread decoding effects reflect - whether all areas directly compute and represent the normative DV in concert, or whether at least some areas reflect other processes that may correlate with the DV. Although the discussion mentions things like feedback modulation in V1, which seems to allow for the possibility that it is not directly involved in DV computation, the phrasing used ('encoding' and 'representation' and never 'secondary modulation') from Abstract to Results tends to imply direct involvement.

Related to this, it seems that the extensive model comparison was done for behaviour, but not for the activation in each area, which may have suggested some dissociations in role - for example, for areas that showed decoding of the evidence (LLR), at least some of them may more closely correspond to the related lower-level quantity of simply spatial position itself, or the higher-level quantity of the transformed belief update (the change in prior from before to after the current cue). There is a map of areas that correlate with the difference of new vs old prior (if I understand correctly - Figure 4D), but not of areas for which activity conforms better to this belief update than to the objective LLR or location. Aside from such model-defined quantities, a critical factor is spatial attention. The authors highlight that the correlated activation of visual regions may reflect feedback modulations akin to attention in nature, but it might actually reflect attention itself, since it is plausible that subjects would pay more attention to the upper field when it is more likely that the centre of the generative distribution is up there (i.e., belief leans upwards). It seems the data could provide insight into this: If the visual cortical effects reflect a spatial attention modulation towards the likely generative source (upper/lower), then the relationship with prior, coded so that upper and lower have opposite sign, should flip in ventral versus dorsal visual cortex. Figure 4A seems like it could be positioned to answer this, but I can't fully interpret it because the prior coding is not explicit in the methods - the relevant section (lines 989-1001) refers back to the normative model description (without pointing to specific equations), which does not say what states S1 and S2 mean (upper and lower? Correct and incorrect? The former is needed to test for this spatial-specificity expected of attention). Even if there are reasons not to perform extra analyses related to the above, the impressions could guide edits to clarify what the data can and cannot say about what these DV-decoding effects reflect. Finally, it could be acknowledged that because the environmental state (upper or lower field generative source) is directly linked to stimulus-response mapping, even decoding effects that are not spatially-specific could equally reflect a representation of either one of these.

The motivation for the decoding analysis running up to the response is not clear - what are the hypotheses here? Is the idea that if these areas truly represented the belief about the currently active context, then they should continue to do so during the response and beyond, since the next trial will begin in the same context as the previous ended? Or is this section tackling a different question? Is it that there is a potential confound in finding the significant decoding during the cue tokens, because it could be driven by the visual responses to the different spatial positions, and there are no such visual responses later at the response?

Reviewer #2 (Public review):

Summary:

Calder-Travis et al. investigate how people form decisions about abstract rules in environments that may change over time. They show that individuals adaptively accumulate information, adjusting how much weight they give new evidence depending on how surprising or uncertain the environment is. Using whole-brain recordings (MEG), they further report that signals reflecting beliefs about the current rule are broadly distributed, particularly in visual and parietal regions. They further argue that these belief-related signals cannot be reduced to representations of momentary sensory evidence alone.

Overall, the behavioral results convincingly demonstrate adaptive evidence accumulation consistent with the normative model. The neural data provide solid evidence for temporally structured belief-related signals that are broadly distributed across cortical regions. However, the evidence for sustained belief maintenance "across" cues and for full dissociation from gaze-related influences in visual cortex is less definitive. These issues temper, but do not undermine, the central conclusions.

Strengths:

A major strength of the study is the integration of normative modeling with temporally resolved neural data. The authors exploit the fine temporal scale of the recordings to examine belief updating across distinct task epochs, and they show that neural signals evolve in a manner consistent with the normative model that best captures behavior. This alignment between behavioral modeling and neural dynamics is carefully executed and conceptually coherent.<br /> Another strength is the authors' cautious interpretation of their findings. They explicitly acknowledge limitations in distinguishing between direct representation of a latent variable and neural modulation driven by that variable. This restraint strengthens the credibility of the conclusions and avoids overstatement.

Weaknesses:

(1) Evidence for sustained belief representation across cues

Behaviorally, the data clearly demonstrate accumulation across sequential cues. However, the neural analyses primarily focus on responses around individual samples (from pre-cue to late post-cue windows). While these analyses demonstrate belief updating following each sample, they do not fully establish whether belief representations are maintained continuously across cues.

Specifically, it remains unclear whether the neural representation of the prior belief is sustained from the late post-cue period of cue t-1 into the pre-cue period of cue t. Without explicit evidence of such continuity, it is difficult to conclude that the neural signals reflect a maintained belief state rather than repeated sample-locked updating processes. This distinction is important for interpreting the neural mechanism of accumulation.

(2) Interpretation of belief signals in the visual cortex

The claim that belief-related signals in the visual cortex cannot be explained by gaze position requires stronger support. The distribution of gaze positions across contexts appears largely non-overlapping, raising the possibility that context-related gaze biases could contribute to the observed neural effects.

In particular, the "gaze-inconsistent" analysis based on a median split may not fully dissociate belief from gaze if the absolute gaze positions remain systematically different between contexts. As currently presented, the evidence does not fully rule out the possibility that gaze-related modulation contributes to the belief-related signal in visual areas. This affects the strength of the interpretation regarding abstract belief representation in early sensory cortex.

(3) Clarity and transparency of task and model description

Several aspects of the task and modeling framework would benefit from clearer exposition. The description of the noise distribution in the context cue would be easier to interpret if the overlapping distributions were visualized explicitly, allowing readers to assess how much accumulation is required versus reliance on strong individual cues. Similarly, the main text would benefit from a clearer explanation of how change point probability and uncertainty are computed (not just in Methods), as these quantities are central to the analyses and interpretation.

In addition, temporal epochs (e.g., pre-cue, early post-cue, late post-cue) are not clearly defined with specific time ranges in the main text, making it difficult to compare across figures.

(4) Interpretation of neural dynamics

Several neural findings are intriguing but underinterpreted. For example, the absence of clear sensory evidence representation in early post-cue epochs in any regions (Figure 4B) is surprising and not discussed. The relative stability of belief-related signals in visual cortex compared to parietal regions (Figure 4E) is also unexpected and warrants interpretation. Additionally, the temporal dynamics of change point probability and uncertainty representations appear different from each other, but such a pattern was not described in detail.

Clarifying these points would strengthen the interpretability of the results and help readers understand the mechanistic implications.

Reviewer #3 (Public review):

Summary

In this study, the authors investigated how inference about the current task context is encoded in the cortex, using MEG measurements. Using the same behavioral task that was initially developed for an fMRI study to identify the loci of task context representation, the current results complement and extend the previous study by identifying the candidate regions that are important for the inference process, not just for encoding the end product. They reported widespread modulation of cortical activity by uncertainty in evidence and volatility of task context changes. In comparison, modulation correlated with the decision variable underlying the task context inference process was more restricted to the parietal and visual cortices, particularly in alpha-band activity.

Strengths:

(1) The normative model provides a solid computational foundation for disambiguating quantities related to decision variables from those related to task factors (e.g., uncertainty and volatility).

(2) The MEG technique allows examination of cortical activity that is modulated by the temporally evolving decision variable.

(3) Rigorous modeling efforts, including comparisons of well-reasoned alternative/reduced models and examinations of diagnostic features using participant-matched simulations.

Weaknesses:

(1) There are two major surprises in the results that raise concerns about how to interpret these data. The first is the absence of modulation of prefrontal cortical activities by prior or posterior. As the authors acknowledged, there are extensive single-neuron recording data (e.g., from the Miller group) demonstrating the presence of task rule modulation in the monkey PFC and prior representation in the PFC in the mouse study that they cited. The second surprise is that the strongest modulation of prior/posterior/evidence was almost always observed in the visual cortex, in contrast to the common embodied cognition assumption. A more elaborated discussion about these discrepancies would help contextualize the current results.

(2) It is not clear why the effects in Figures 2D and E dipped before responses, which is not expected from any of the models. This could potentially affect the interpretation of the MEG signals in late-post-cue or pre-response periods.

(3) The definitions of the different periods (e.g., early/late post-cue) are vague, making it hard to assess the functional relevance of the signals. For example, is the difference between the early pre-response map in Figure 5B and the late evidence map in Figure 4B due to completely non-overlapping time periods? A diagram of the timing definitions for different task periods would be helpful.

(4) Perhaps related to #2, it is puzzling that evidence encoding is absent in the visual cortex during the early post-cue period.

(5) The presentation and discussion of results related to correlated variability assume that the readers have already read their previous paper. A little more elaboration of the significance of this measurement would be helpful.

Reviewer #1 (Public review):

Summary:

The presented investigation aims to expand the sleep definition and its relationship with blood meal and/or circadian clock in the mosquito, Aedes aegypti. The authors exhausted the established sleep analytical paradigm and three behaviour toolkits: LAM10, EthoVision, and DART. They also investigated the potential underlying molecular mechanism by using dsRNA injection (LkR) and a KO mosquito (Cyc-/-).

Strengths:

The authors presented a very solid dataset showing posture changes and an increase in the arousal threshold of the mosquito after 10 minutes of immobility. This is a major clarification and extension to our understanding of insect sleep beyond Drosophila. Inclusion of analytical parameters such as bout length, waking activity and pDoze/Wake provide critical reminder for other investigators of the steps needed for defining sleep in a new species. The investigation, with its technical span in behaviour assays, therefore establishes a good standard for mosquito sleep analysis to the same quality seen in the landmark studies (Shaw et al 2000 and Hendricks et al 2000) for Drosophila sleep. The pioneering data showing a clear effect of blood meal and LkR reduction on locomotion and sleep provides an entry point for further investigations.

Weaknesses:

Despite the versatility of the behaviour and transgenic methods in this manuscript, there are two logical gaps in the conclusion, which are related to the effect of blood meal/BSA/LkR KD on A. aegypti sleep:<br /> (1) Conventionally, a coincidence of sleep increase and locomotion reduction would weaken the certainty of a sleep increase assessment. The authors implied this concurrence observed after blood meal is derived from internal "drowsy" neural state instead of physical "cripple", but they did not use their two high-resolution video tracking velocity or pDoze/Wake to clarify this.<br /> (2) The major molecular component underlying blood meal effect on sleep/locomotion is less certain, because the BSA solution used for feeding contains ATP, which itself is able to enter haemolymph and potentially exerts sleep/locomotion effect. Additionally, the basal or control sleep recording is done after sucrose feeding. It is, however, unclear from the method if this is 10% too? And if the observed sleep level increase after a blood meal is a result of sugar level reduction in the blood (~0.1%).

Reviewer #2 (Public review):

Zhang et al. investigate how blood feeding and dietary protein influence sleep in the mosquito Aedes aegypti. The authors first establish a behavioural definition of sleep using postural analysis and arousal threshold measurements, then demonstrate that both blood meals and a bovine serum albumin (BSA)-based protein diet increase sleep for several days. They further show that RNAi-mediated knockdown of the leucokinin receptor (Lkr) enhances sleep, implicating neuropeptide signalling in the regulation of postprandial sleep. The authors propose that elevated sleep persists well beyond the restoration of host-seeking behaviour, suggesting the existence of distinct "opportunistic" versus "determined" host-seeking phases.

Strengths

The central question is well-motivated, and the experimental approach is systematic. The use of multiple independent methods to characterise sleep - postural analysis, infrared activity monitoring, videography, and arousal threshold - provides converging evidence. The BSA feeding experiment is a particularly effective demonstration that dietary protein, rather than other blood components, is the key regulator of the sleep increase. The conservation of leucokinin signalling in sleep regulation between Drosophila and Ae. aegypti is a noteworthy finding that adds comparative depth.

Weaknesses

(1) Sleep definition.

The authors settle on a 10-minute immobility threshold, but their own data do not convincingly support this choice. The arousal threshold data (Figure 1G) show no significant difference between the 1-5 min and 6-10 min bins (P=0.246), with significance emerging only at the 11-15 min bin. The postural analysis likewise indicates that sleep-associated postures appear at ~20 min during the day and ~11 min at night. A 15-minute threshold would be better supported by the data as presented. The previous literature used 120 minutes for this species (Ajayi et al. 2022), making this a dramatic shift.

(2) Confound of reproduction and sleep.

The primary experimental paradigm measures sleep beginning at Day 4 post-blood feeding, immediately after oviposition. Animals have undergone gut distension, vitellogenesis, and oviposition, and what is being measured as "sleep" could reflect post-reproductive quiescence or recovery rather than diet-induced sleep per se. The BSA experiment partially addresses this, but since BSA also triggers vitellogenesis and egg production (as the authors note), the confound persists.

(3) Opportunistic vs. determined host-seeking hypothesis.

This framework is presented as a key conceptual contribution, but the paper contains no data on host-seeking behaviour. The authors infer two phases from the temporal mismatch between a 72-hour host-seeking suppression window (from prior studies) and elevated sleep through Day 5 (~120 hours). While this is an interesting hypothesis, it requires actual measurement of host-seeking alongside sleep to be substantiated, or at least the caveats need to be discussed more explicitly.

(4) Statistical approach.

The methods describe "one-way ANOVA, followed by Mann-Whitney tests with Welch's correction," which is an internally inconsistent combination: Mann-Whitney is non-parametric and does not use Welch's correction (which applies to t-tests). Throughout the figures, F-statistics (parametric) are reported alongside what appear to be non-parametric tests. The statistical framework needs to be clarified and made consistent. Exact sample sizes per group should also be stated explicitly in the methods for all experiments.

Reviewer #2 (Public review):

Summary:

Ito and Toyoizumi present a computational model of context-dependent action selection. They propose a "hippocampus" network that learns sequences based on which the agent chooses actions. The hippocampus network receives both stimulus and context information from an attractor network that learns new contexts based on experience. The model is consistent with a variety of experiments both from the rodent and the human literature such as splitter cells, lap cells, the dependence of sequence expression on behavioral statistics. Moreover, the authors suggest that psychiatric disorders can be interpreted in terms of over/under representation of context information.

My general assessment of the work is unchanged, and I still have some questions requesting methodological clarification

Strengths:

This ambitious work links diverse physiological and behavioral findings into a self-organizing neural network framework. All functional aspects of the network arise from plastic synaptic connections: Sequences, contexts, action selection. The model also nicely links ideas from reinforcement learning to a neuronally interpretable mechanisms, e.g. learning a value function from hippocampal activity.

Weaknesses:

The presentation, particularly of the methodological aspects, needs to be heavily improved. Judgment of generality and plausibility of the results is severely hampered but is essential, particularly for the conclusions related to psychiatric disorders. In its present form, it is impossible to judge whether the claims and conclusions made are justified. Also, the lack of clarity strongly reduces the impact of the work on the field.

Comments:

The authors have made strong efforts to improve on their description of the methods, however, it is still very hard to understand. As a result of some of their clarifications, new issues appeared that I was not able to extract in the previous version.

(1) Particularly I had problems figuring out how the individual dynamical systems are interrelated (sequences, attractor, action, learning). As I understand it now (and I still might be wrong) there is one discrete time dynamics, where in each time step one action takes place as well as the attractor and sequence dynamics are moved one step forward. Also, synaptic updates happen in every one of those time steps. The authors may verify or correct my interpretations and further improve on their description in the manuscript. It is also confusing that time in the figure panels is given in units of trials, where each trial may consist of (maybe different amounts of) multiple time steps. Are the thin horizontal red ad blue lines time steps?

(2) As a consequence of my new understanding of the model dynamics, I have become doubts about the interpretation of the attractor network as context encoding. Since the X population mainly serves to disambiguate sequence continuation, right before the action has to be taken (active for only two time steps in Figure 1C?) they could also be considered to encode task space (El-Gaby et al. 2024; doi: 10.1038/s41586-024-08145-x).

(3) Also technically, I wonder why the authors introduce the criterion of 50(!) time steps to allow the attractor to converge, if the state of the attractor network is only relevant in one time step to choose the appropriate continuation of the sequence of actions. Is attractor dynamics important at all? What would happen if just the input and output weights to the X population are kept and the recurrent weights are set 0?

(4) Figure 3E: How many time steps are the H cells active (red bars?) Figure 4J: What are the units of the time axis?

Reviewer #3 (Public review):

Summary:

This paper develops a model to account for flexible and context-dependent behaviors, such as where the same input must generate different responses or representations depending on context. The approach is anchored in the hippocampal place cell literature. The model consists of a module X, which represents context, and a module H (hippocampus), which generates "sequences". X is a binary attractor RNN, and H appears to be a discrete binary network, which is called recurrent but seems to operate primarily in a feedforward mode. H has two types of units (those that are directly activated by context, and transition/sequence units). An input from X drives a winner-take-all activation of a single unit H_context unit, which can trigger a sequence in the H_transition units. When a new/unpredicted context arises, a new stable context in X is generated, which in turn can trigger a new sequence in H. The authors use this model to account for some experimental findings, and on a more speculative note, propose to capture key aspects of contextual processing associated with schizophrenia and autism.

Strengths:

Context-dependency is an important problem. And for this reason, there are many papers that address context-dependency - some of this work is cited. To the best of my knowledge, the approach of using an attractor network to represent and detect changes in context is novel and potentially valuable.

Comments on revisions:

The authors have adequately addressed my concerns. Most importantly, the details of the implementation of the different components of the model are much more clearly described.

Reviewer #1 (Public review):

Summary:

The manuscript by Ito and Toyozumi proposes a new model for biologically plausible learning of context-dependent sequence generation, which aims to overcome the predefined contextual time horizon of previous proposals. The model includes two interacting models: an Amari-Hopfield network that infers context based on sensory cues, with new contexts stored whenever sensory predictions (generated by a second hippocampal module) deviate substantially from actual sensory experience, which then leads to hippocampal remapping. The hippocampal predictions themselves are context-dependent and sequential, relying on two functionally distinct neural subpopulations. On top of this state representation, a simple Rescola-Wagner-type rule is used to generate predictions for expected reward and to guide actions. A collection of different Hebbian learning rules at different synaptic subsets of this circuit (some reward-modulated, some purely associative, with occasional additional homeostatic competitive heterosynaptic plasticity) enables this circuit to learn state representations in a set of simple tasks known to elicit context-dependent effects.

Strengths:

The idea of developing a circuit-level model of model-based reinforcement learning, even if only for simple scenarios, is definitely of interest to the community. The model is novel and aims to explain a range of context-dependent effects in the remapping of hippocampal activity.

Weaknesses:

The link to model-based RL is formally imprecise, and the circuit-level description of the process is too algorithmic (and sometimes discrepant with known properties of hippocampus responses), so the model ends up falling in between in a way that does not fully satisfy either the computational or the biological promise. Some of the problems stem from the lack of detail and biological justification in the writing, but the loose link to biology is likely not fully addressable within the scope of the current results. The attempt at linking poor functioning of the context circuit to disease is particularly tenuous.

Reviewer #2 (Public review):

Summary:

Ito and Toyoizumi present a computational model of context-dependent action selection. They propose a "hippocampus" network that learns sequences based on which the agent chooses actions. The hippocampus network receives both stimulus and context information from an attractor network that learns new contexts based on experience. The model is consistent with a variety of experiments, both from the rodent and the human literature, such as splitter cells, lap cells, and the dependence of sequence expression on behavioral statistics. Moreover, the authors suggest that psychiatric disorders can be interpreted in terms of over-/under-representation of context information.

Strengths:

This ambitious work links diverse physiological and behavioral findings into a self-organizing neural network framework. All functional aspects of the network arise from plastic synaptic connections: Sequences, contexts, and action selection. The model also nicely links ideas from reinforcement learning to neuronally interpretable mechanisms, e.g., learning a value function from hippocampal activity.

Weaknesses:

The presentation, particularly of the methodological aspects, needs to be majorly improved. Judgment of generality and plausibility of the results is hampered, but is essential, particularly for the conclusions related to psychiatric disorders. In its present form, it is unclear whether the claims and conclusions made are justified. Also, the lack of clarity strongly reduces the impact of the work in the larger field.

More specifically:

(1) The methods section is impenetrable. The specific adaptations of the model to the individual use cases of the model, as well as the posthoc analyses of the simulations, did not become clear. Important concepts are only defined in passing and used before they are introduced. The authors may consider a more rigorous mathematical reporting style. They also may consider making the methods part self-contained and moving it in front of the results part.

(2) The description of results in the main text remains on a very abstract level. The authors may consider showing more simulated neural activity. It remains vague how the different stimuli and contexts are represented in the network. Particularly, the simulations and related statistical analyses underlying the paradigms in Figure 4 are incompletely described.

(3) The literature review can be improved (laid out in the specific recommendations).

(4) Given the large range of experimental phenomenology addressed by the manuscript, it would be helpful to add a Discussion paragraph on how much the results from mice and humans can be integrated, particularly regarding the nature of the context selection network.

(5) As a minor point, the hippocampus is pretty much treated as a premotor network. Also, a Discussion paragraph would be helpful.

Reviewer #3 (Public review):

Summary:

This paper develops a model to account for flexible and context-dependent behaviors, such as where the same input must generate different responses or representations depending on context. The approach is anchored in the hippocampal place cell literature. The model consists of a module X, which represents context, and a module H (hippocampus), which generates "sequences". X is a binary attractor RNN, and H appears to be a discrete binary network, which is called recurrent but seems to operate primarily in a feedforward mode. H has two types of units (those that are directly activated by context, and transition/sequence units). An input from X drives a winner-take-all activation of a single unit H_context unit, which can trigger a sequence in the H_transition units. When a new/unpredicted context arises, a new stable context in X is generated, which in turn can trigger a new sequence in H. The authors use this model to account for some experimental findings, and on a more speculative note, propose to capture key aspects of contextual processing associated with schizophrenia and autism.

Strengths:

Context-dependency is an important problem. And for this reason, there are many papers that address context-dependency - some of this work is cited. To the best of my knowledge, the approach of using an attractor network to represent and detect changes in context is novel and potentially valuable.

Weaknesses:

The paper would be stronger, however, if it were implemented in a more biologically plausible manner - e.g., in continuous rather than discrete time. Additionally, not enough information is provided to properly evaluate the paper, and most of the time, the network is treated as a black box, and we are not shown how the computations are actually being performed.

Reviewer #1 (Public review):

Summary:

In this compelling study, Howard et al. use deep mutational scanning to probe essentially all possible single amino acid substitutions in the TYK2 tyrosine kinase, and identify those that modulate signaling function and protein abundance. The methodological approach is elegant and thorough, and the results identify numerous examples of amino acid substitutions that have been previously reported to modulate TYK2 function, validating the approach.

Substitutions that are LOF with respect to IFN-a signaling but not protein abundance are particularly interesting and are widely dispersed across the protein. They include known functionally critical sites such as the active site and activation loop of the kinase domain, as well as the allosteric site within the regulatory pseudokinase domain, but also hundreds of other additional sites. The approach is then used to study the effects of substitutions on kinase inhibition using several JAK family inhibitors that target the pseudokinase domain. By assessing variant effects at both high and low drug concentrations, they are able to identify variants that mediate resistance or conversely potentiate inhibition, respectively. These map to distinct sites on the pseudokinase domain. Finally, the authors show that several TYK2 variants, most notably the P1104A substitution, previously shown to protect against autoimmune disease, correspond to substitutions that reduce protein abundance in their screen. Combining their DMS data with autoimmune phenotype and TYK2 genotype data uncovered a general dose relationship between autoimmunity and TYK2 abundance, and the authors propose that this might justify targeting TYK2 protein levels with degraders.

Strengths:

This is a nicely executed, well-written study with good figures and a clear presentation.

Weaknesses:

The only substantial critique I have is that while the paper makes a compelling case for the validity and power of the approach, the authors could perhaps go further in their interpretation of their data, particularly with regards to identifying functionally important sites and connecting them to putative allosteric sites and functionally relevant protein-protein interfaces in the context of what is known about JAK family kinase structure and function. An attempt is made to interpret the data in light of a composite structural model of full-length TYK2 engaged with the IFNAR1 receptor (Figure 2C), but much more could be said about this. Below, I list several examples where additional insight might be gleaned.

(1) The discussion of gain-of-function variants is limited. Given that tight regulation is a general theme of kinase signaling and gain-of-function mutations are a common disease mechanism, these mutations could be particularly interesting. Could the authors comment on patterns of gain versus loss? Are there gain-of-function signaling variants that work in a IFN-a dose dependent versus independent manner?

(2) The discussion of the signaling-specific variants (LOF in signaling but not abundance) is interesting but could be expanded. Can the authors comment on which regions of the pseudokinase/kinase interface, for instance, are affected, since this allosteric communication is a critical and unique aspect of JAK family protein function? Can something be said about what the 6 activation loop substitutions are doing?

(3) The cytokine signaling screen was performed at several different levels of IFN-α cytokine stimulation. The authors state that these data were used to identify quantitative variant effects (p7), but the cytokine dose response data are not widely discussed in the manuscript. Is it not possible that valuable information about the strength of substitution effects could be gleaned from this? One might expect that simple loss of function mutants that, e.g. completely destroy catalytic activity, will be LOF at all levels of stimulation, whereas mutations that have more nuanced "tuning" or allosteric effects on signaling might display LOF at low cytokine stimulation levels but be restored at high stimulation levels. Such information could be of potential functional importance and interest. Could the authors comment on this?

(4) In general, the variant data could be interpreted more specifically in light of the available detailed structural information about TYK2 and JAK kinases generally. For instance, could the resistance versus potentiation variants be interpreted in this context to hypothesize what they might be doing?

Reviewer #2 (Public review):

Howard et al. describe a set of deep mutational scanning (DMS) experiments applied to TYK2, which is a drug target implicated in autoimmune disease. By assaying protein abundance (stability) effects as well as immune signaling, the authors are able to disentangle variant effects that may be directly involved in protein activity (and therefore potentially druggable) from variant effects that are due to loss of protein or general structural instability. By performing these assays under multiple conditions, including the presence of various concentrations of small molecules, they develop a clear picture of which sites in TYK2 may be most relevant for intervention or targeting. Overall, the work represents a very compelling example of DMS for understanding protein biology and candidate drug mechanisms.

The work is very thorough, with multiple DMS assays described and compared/contrasted. This greatly enhances the impact and interpretability of any individual assay performed.

The authors have made improvements to the state of the art in terms of wet-lab assay design as well as the analysis of FACS-based deep mutational scans.

The potential mechanism of loss of protein abundance in TYK2 being protective for autoimmune disease is clear, but the estimates of the effect size in more physiologically relevant settings vary quite a bit and might be quite small. Are there examples that could be cited of other similar disease mechanisms where a 10% loss in abundance is associated with a clinical phenotype?

Reviewer #3 (Public review):

Summary:

In the paper "Deep mutational scanning reveals pharmacologically relevant insights into TYK2 signaling and disease", the authors perform a comprehensive deep mutational scan of the kinase TYK2, a protein of pharmacological interest due to its central role in multiple immune-related phenotypes. The study assesses two key functional phenotypes: protein abundance and IFN-α-dependent signaling. The signaling assays were conducted across a dose-response range under various inhibitor conditions, allowing for an in-depth characterization of TYK2 activity and regulation. Both the experimental design and data analysis were executed with rigor and transparency, yielding a dataset that appears highly reliable. The authors provide strong evidence and a scientifically grounded interpretation of their results.

The paper presents the results of a deep mutational scan based on two assays: an IFN-α-stimulated signaling assay and a protein abundance assay. These measurements are further supported by variant classifications from AlphaMissense and ClinVar, providing a framework for functional interpretation. Building on these data, the authors propose four potential pharmacological applications of their screening system at the end of the first results section.

First, they demonstrate that the combined analysis of abundance and IFN-α signaling identifies potential allosteric sites, focusing on variants with normal protein stability but reduced signaling activity. Through this approach, they detect two previously uncharacterized allosteric regions (Results Section 2).

Second, they explore how the screen can be used to predict variant-specific drug responses or resistance mechanisms (Results Section 3). This is achieved through assays involving two different inhibitors, which reveal both resistance- and potentiation-associated variants.

Third, they assess the relative functional consequences of ligand and inhibitor dosing by performing IFN-α and inhibitor dose-response experiments (1, 10, and 100 U/mL IFN-α; IC99 and IC75 inhibitor concentrations; Results Section 3).

Finally, the authors investigate how specific human variants, such as P1104A and I684S, may inform therapeutic modality selection (Results Section 4). Although these variants exhibit no detectable effect on IFN-α signaling within this experimental system, they substantially impact protein abundance. By integrating data from the UK Biobank, the authors further demonstrate that protective effects against autoimmune disease are associated with altered protein abundance rather than differences in IFN-α signaling, highlighting the distinct mechanistic basis of TYK2's clinical relevance.

Strengths:

Overall, we found this paper rigorous, well-written, and easy to follow. As such, we think this is an exceptional example of a deep mutational scanning manuscript, and this dataset will be invaluable to the field. We particularly appreciate that the authors could explore sensitivity to inhibitor concentration across multiple doses of the inhibitor.

Weaknesses:

Despite the authors' rigorous experimentation and thoughtful interpretation, the study leaves several important mechanistic questions unresolved, as is common in any study. While the data provide clear functional patterns, the underlying biophysical and biochemical explanations remain insufficiently explored. For instance, in point 1, the identification of two novel allosteric sites is intriguing, yet the paper does not elaborate on the structural basis or mechanistic rationale for their regulatory effects. In point 2, resistance and potentiation variants are described for two distinct inhibitors, but it remains unclear why certain variants respond specifically to one compound and not the other. In point 3, higher inhibitor concentrations appear to diminish allosteric interactions, though the reasons why some sites are affected while others are not are left unexplained. Finally, in point 4, the observation that protein abundance, but not IFN-α signaling, correlates with autoimmune protection is compelling but mechanistically ambiguous. These gaps do not detract from the technical excellence of the work; rather, they highlight opportunities for future studies to clarify the molecular and pharmacological mechanisms underlying TYK2 regulation and to deepen the translational insights drawn from this comprehensive mutational scan. We hope that the authors could provide more direction and mechanistic context in the discussion section to guide readers toward these next steps.

Joint Public Review:

Summary:

Inferring so-called "functional connectivity" between neurons or groups of neurons is important both for validating models and for inferring brain state. Under the assumption that brain dynamics is linear, the authors show that the error in estimating functional connectivity depends only on the eigenvalues of the covariance matrix of the observed data, and it is the small eigenvalues -corresponding to directions in which the variance of the brain activity is low - that lead to large estimation errors. Based on this, the authors show that to achieve low estimation error, it's important to excite the resonant frequencies and perturb well-connected hubs. The authors propose a practical iterative approach to estimate the functional connectivity and demonstrate faster convergence to the optimal estimate compared to passive observation.

Strengths:

The main contribution of the study is the derivation of an explicit expression for the error in functional connectivity that depends only on the covariance matrix of the observed data. If valid, this result can have a profound impact on the field. The study also motivates the current shift to closed-loop experiments by demonstrating the effectiveness of active learning in the system using perturbation, in comparison to passive estimation from resting-state activity. Finally, the relative simplicity of the model makes its practical applications straightforward, as the authors illustrate in the context of brain state classification and neural control.

Weaknesses:

The derivation of the main error term misses some important steps, which complicates peer review at this stage. In particular, factorisation of the covariance into noise and the inverse of the observation covariance matrix needs a more thorough justification. The cited sources do not contain the derivation for a noise term with full covariance, which is essential for deriving this error term.

The practical recommendation at the end of the paper also requires clearer guidance on how the design perturbations are constructed, and how many times and for how long the system is stimulated in each iteration of the experiment.

Finally, there is no analysis of model mis-specification. In particular, the true dynamics are unlikely to be linear; the noise is unlikely to be either Gaussian or uncorrelated across time; and the B matrix is unlikely to be known perfectly. We're not suggesting that the authors consider a more complex model, but it's important to know how sensitive their method is to model mismatch. If nothing can be done analytically, then simulations would at least provide some kind of guide.

Reviewer #1 (Public review):

Summary:

Using multi-region two-photon calcium imaging, the manuscript meticulously explores the structure of noise correlations (NCs) across mouse visual cortex and uses this information to make inferences about the organization of communication channels between primary visual cortex (V1) and higher visual areas (HVAs). Using visual responses to grating stimuli, the manuscript identifies 6 tuning groups of visual cortex neurons, and finds that NCs are highest among neurons belonging to the same tuning group whether or not they are found in the same cortical area. The NCs depend on the similarity of tuning of the neurons (their signal correlations) but are preserved across different stimulus sets - noise correlations recorded using drifting gratings are highly correlated with those measured using naturalistic videos. Based on these findings, the manuscript concludes that populations of neurons with high NCs constitute discrete communication channels that convey visual signals within and across cortical areas.

Strengths:

Experiments and analyses are conducted to a high standard and the robustness of noise correlation measurements is carefully validated. To control for potential influences of behaviour-related top-down modulation of noise correlations, the manuscript uses measurements of pupil dynamics as a proxy for behavioural state and shows that this top-down modulation cannot explain the stability of noise correlations across stimuli.

Weaknesses:

The interpretation of noise correlation measurements as a proxy from network connectivity is fraught with challenges. While the data clearly indicate the existence of distributed functional ensembles, the notion of communication channels implies the existence of direct anatomical connections between them, which noise correlations cannot measure.

The traditional view of noise correlations is that they reflect direct connectivity or shared inputs between neurons. While it is valid in a broad sense, noise correlations may reflect shared top-down input as well as local or feedforward connectivity. This is particularly important since mouse cortical neurons are strongly modulated by spontaneous behavior (e.g. Stringer et al, Science, 2019). Therefore, noise correlation between a pair of neurons may reflect whether they are similarly modulated by behavioral state and overt spontaneous behaviors. Consequently, noise correlation alone cannot determine whether neurons belong to discrete communication channels.

Reviewer #2 (Public review):

Summary:

This groundbreaking study characterizes the structure of activity correlations over millimeter scale in the mouse cortex with the goal of identifying visual channels, specialized conduits of visual information that show preferential connectivity. Examining the statistical structure of visual activity of L2/3 neurons, the study finds pairs of neurons located near each other or across distances of hundreds of micrometers with significantly correlated activity in response to visual stimuli. These highly correlated pairs have closely related visual tuning sharing orientation and/or spatial and/or temporal preference as would be expected from dedicated visual channels with specific connectivity.

Strengths:

The study presents best-in-class mesoscopic-scale 2-photon recordings from neuronal populations in pairs of visual areas (V1-LM, V1-PM, V1-AL, V1-LI). The study employs diverse visual stimuli that capture some of the specialization and heterogeneity of neuronal tuning in mouse visual areas. The rigorous data quantification takes into consideration functional cell groups as well as other variables that influence trial-to-trial correlations (similarity of tuning, neuronal distance, receptive field overlap, behavioral state). The paper demonstrates the robustness of the activity clustering analysis and of the activity correlation measurements. The paper shows convincingly that the correlation structure observed with grating stimuli is present in the responses to naturalistic stimuli. A simple simulation is provided that suggest that recurrent connectivity is required for the stimulus invariance of the results. The paper is well written and conceptually clear. The figures are beautiful and clear. The arguments are well laid out and the claims appear in large part supported by the data and analysis results (but see weaknesses).

Weaknesses:

An inherent limitation of the approach is that it cannot reveal which anatomical connectivity patterns are responsible for observed network structure. A methodological issue that does not seem completely addressed is whether the calcium imaging measurements with their limited sensitivity amplify the apparent dependence of noise correlations on the similarity of tuning. Although the paper shows that noise correlation measurements are robust to changes in firing rates / missing spikes, the effects of receptive field tuning dissimilarity are not addressed directly. The calcium responses of mouse visual cortical neurons are sharply tuned. Neurons with dissimilar receptive fields may show too little overlap in their estimated firing rates to infer noise correlations, which could lead to underestimation of correlations across groups of dissimilar neurons.

Reviewer #3 (Public review):

Summary:

Yu et al harness the capabilities of mesoscopic 2P imaging to record simultaneously from populations of neurons in several visual cortical areas and measure their correlated variability. They first divide neurons in 65 classes depending on their tuning to moving gratings. They found the pairs of neurons of the same tuning class show higher noise correlations (NCs) both within and across cortical areas. Based on these observations and a model they conclude that visual information is broadcast across areas through multiple, discrete channels with little mixing across them.<br /> NCs can reflect indirect or direct connectivity, or shared afferents between pairs of neurons, potentially providing insight on network organization. While NCs have been comprehensively studied in neurons pairs of the same area, the structure of these correlations across areas is much less known. Thus, the manuscripts present novel insights on the correlation structure of visual responses across multiple areas.

Strengths:

The measurements of shared variability across multiple areas are novel. The results are mostly well presented and many thorough controls for some metrics are included.

Weaknesses:

I have concerns that the observed large intra class/group NCs might not reflect connectivity but shared behaviorally driven multiplicative gain modulations of sensory evoked responses. In this case, the NC structure might not be due to the presence of discrete, multiple channels broadcasting visual information as concluded. I also find that the claim of multiple discrete broadcasting channels needs more support before discarding the alternative hypothesis that a continuum of tuning similarity explains the large NCs observed in groups of neurons.

Specifically:

Major concerns:

(1) Multiplicative gain modulation underlying correlated noise between similarly tuned neurons

(1a) The conclusion that visual information is broadcasted in discrete channels across visual areas relies on interpreting NC as reflecting, direct or indirect connectivity between pairs, or common inputs. However, a large fraction of the activity in the mouse visual system is known to reflect spontaneous and instructed movements, including locomotion and face movements, among others. Running activity and face movements are one of the largest contributors to visual cortex activity and exert a multiplicative gain on sensory evoked responses (Niell et al , Stringer et al, among others). Thus, trial-by-fluctuations of behavioral state would result in gain modulations that, due to their multiplicative nature, would result in more shared variability in cotuned neurons, as multiplication affects neurons that are responding to the stimulus over those that are not responding ( see Lin et al , Neuron 2015 for a similar point).

In the new version of the manuscript, behavioral modulations are explicitly considered in Figure S8. New analyses show that most of the variance of the neuronal responses is driven by the stimulus, rather than by behavioural variable. However, they new analyses still do not address if the shared noise correlation in cotuned neurons is also independent of behavioral modulations .

As behavioral modulations are not considered this confound affects the conclusions and the conclusion that activity in communicated unmixed across areas ( results in Figure 4), as it would result in larger NCs the more similar the tuning of the neurons is, independently of any connectivity feature. It seems that this alternative hypothesis can explain the results without the need of discrete broadcasting channels or any particular network architecture and should be addressed to support the main claims.

(2) Discrete vs continuous communication channels<br /> (2a) One of the author's main claims is that the mouse cortical network consists of discrete communication channels, as stated in teh title of the paper. This discreteness is based on an unbiased clustering approach on the tuning of neurons, followed by a manual grouping into six categories with relation to the stimulus space. I believe there are several problems with this claim. First, this clustering approach is inherently trying to group neurons and discretise neural populations. To make the claim that there are 'discrete communication channels' the null hypothesis should be a continuous model. An explicit test in favor of a discrete model is lacking, i.e. are the results better explained using discrete groups vs. when considering only tuning similarity? Second, the fact that 65 classes are recovered (out of 72 conditions) and that manual clustering is necessary to arrive at the six categories is far from convincing that we need to think about categorically different subsets of neurons. That we should think of discrete communication channels is especially surprising in this context as the relevant stimulus parameter axes seem inherently continuous: spatial and temporal frequency. It is hard to motivate the biological need for a discretely organized cortical network to process these continuous input spaces.

Finally, as stated in point 1, the larger NCs observed within groups than across groups might be due to the multiplicative gain of state modulations, due to the larger tuning similarity of the neurons within a class or group.

Reviewer #1 (Public review):

Summary:

The authors study criticality and drift in spontaneous activity observed in visual cortex of mice from existing data, and relate it to a model based on homeostatic plasticity. The main phenomena are power laws and an alignment across different neural representations that is maintained through drift.

Strengths:

The authors should be commended by making the effort of relating their model to experimental data. The mechanism that they propose has the advantage of being simple, and could unify various phenomena.

Weaknesses:

Introduction/abstract: General wording: the notion of reliability, which is key to the paper is not explicitly defined anywhere. The authors refer to some notion of information being preserved, but again, this is not clearly explained. A good example is the sentence "identical input signals exhibit significant variability but also share certain reliability across sessions". Depending on the definition of reliability, the sentence could be a contradiction. A similar issue appears when the authors talk about "restricted" representation. I get what they want to say, but it's not properly defined. "One example is the recent studies about stimulus-evoked..." The sentence explains that there are examples, but provides no citations! Also "One" and "exampleS"

Fig. 1: - The method to fit the power law is not detailed in the methods (just a vague reference to a package). This is a problem because some methods like least squares don't do well on power laws, and particularly for neuroscience due to low sampling (Wilting & Priesemann, Nat com.). - The "olive" curve is not "olive". Olive is dark green, and the color is purple. The problem appears in the subsequent figure.

Fig. 2: - The number of neurons is very small (19). This is very odd, since the original dataset has a lot of neurons. Also, the authors seem to pick age 97 and 102, but do not explain why those two points have any relevance. - If you run a correlation you need to explain what is the correlation (pearson, spearman?). It also matters where the variables are normalized or not, and there is no control for shuffling. - The authors mention "low dimensional", but don't explain what method they use (looks t-SNE to me). - The authors use the word "signal" while in the text they refer to the "mean activity". Are those the same? - "We reproduced previous results showing that low-dimensional embeddings of mean population response vectors for different signals remain similar across sessions" The blue and green clusters that the authors report as being close across sessions are not close. Red-green-grey seem to remain closer, but even that is quite a stretch. - Correlation across matrices is strange. Since the authors did not clarify the actual formula or method, the correlation of 0.5 in Fig. 2E could be simply due to the fact that all the variables are pre-selected to be positive (or above threshold). This would also have an important effect on the angle (Fig. G). In fact, it would explain how comes that the correlation does not decrease with Delta T (which is what would be expected from drift. - Whenever the authors run a statistical analysis, it would help to run a shuffled control.

Self-organised criticality emerges through homeostatic plasticity. - The authors refer a lot to reference 35, but it's not clear what is the difference between their work and that one. - The text provides a general overview and refers to the methods for details. Since most of the results are based on that mode, I suggest putting it in the main text (although this is an opinion, not a dealbreaker). - Especially, mention which populations are we talking about, what are the numbers of neurons in each, and how are they connected.

• Fig. 4 has a lot of the same weaknesses as Fig. 2. In fact, the results on E are very similar, despite the fact that the matrices in D are clearly not the same.

Enhanced Neural representation through self-organised criticality The phase transition seems to be an observation over a computational model, but I don't see much analysis. It would be nice to have some order parameter, although the plots are convincing without it. The authors do spend time talking about co-spiking and silent periods though, but don't actually plot this. The only reference is to S4, which actually only seems to cover the super-critical state.

Fig 6: - It might be true that the accuracy peaks at the critical point, but it's really hard to call it significant. The authors should run multiple models and assess significance. - I don't entirely see the point of C. What does it mean for the model? And although I assume it is on the same experimental data, the authors do not mention it.

Fig. 7: - Plot is squeezed, and has low resolution. - Since the authors didn't clarify whether they have II connections or not (some models use them, some don't), or whether their plasticity applies to inhibitory neurons, it is very hard to assess what are the differences between A and B.

References: There are a fair amount of works that studied computational models for criticality. I am particularly thinking of the works of Bruno del Papa "Criticality meets learning: Criticality signatures in a self-organizing recurrent neural network". Experimentally, there are works showing that the so-called spontaneous activity is actually very reliable (if you record enough neurons). Nghia et al. "Nguyen, Nghia D., et al. "Cortical reactivations predict future sensory responses." Nature 625.7993 (2024): 110-118."

An important point missing in this work is that it assumes that spontaneous activity is somehow intrinsically generated. This is not necessarily true of cortical areas (where it could easily come from hippocampus).

Reviewer #2 (Public review):

This work attempts to reconcile the concepts of critical neural dynamics with short-term reliable responses and long-term drifting responses. This is an important question, because critical dynamics are typically associated with unpredictable population responses to perturbations. Instead, this paper demonstrates that recordings from the mouse visual cortex include typical avalanche statistics in their spontaneous state as well as clustered within-session responses to natural movies. The authors find that a spiking neural network with homeostatic plasticity on inhibitory coupling captures the correlation-based metrics observed in experiments and that this network self-organizes into a critical state.

Strengths:

The structure of the manuscript is clear, and the line of argumentation is easy to follow. The question raised is valid, and the model employed to answer it is adequate. While I am unsure if representation should be equated with reliable responses, I find the framework of reliable responses well-suited to compare experimental and numerical data.

Weaknesses:

• The claim that the presented model "self-organizes to the critical spontaneous state" is incompatible with Fig. 6 showing that the inhibitory timescale is a control parameter of the transition from subcritical to supercritical avalanche statistics.

• The notion of "drift" implies to me a gradual change on long timescales. This is demonstrated in Ref. [47] for a model including two different types of plasticity. Also, such a drift over time was observed in Ref. [11] Fig.3C. In the present work, we can see from Fig. 2E that the correlation drops immediately to a plateau. Instead, the model actually shows some decay of correlations, expected from the ongoing plasticity. This challenges the claim that the "model successfully reproduce[s] both representational drift and [...]". Instead, the model of [47] does reproduce representation drift.

• The claim that "spontaneous self-organized criticality serves as [...] functional mechanism for maintaining reliable information representation under continuously changing networks" is not justified by the above-raised points.

• From the methods, I understand that the dimensionality reduction in Fig.2C and Fig.4C is a result of independent t-SNE. Since t-SNE to my knowledge starts with a random projection of data to then optimize the embedding, the resulting orientation of independent runs cannot be compared such that statements like "rotation of low-dimensional representations as in Fig. 2C, where nodes (centers of the same-color clusters) change their positions across sessions (top panel and bottom panel), but their relative positions remain stable" are not possible.

Reviewer #3 (Public review):

Summary:

This study uses computational modeling of a spiking network of E-I with homeostatic inhibitory plasticity and aims to show that self-organized criticality that arises from the homeostatic mechanism can result in representational drift as well as reliable stimulus representation, because the geometric representation of stimuli remains restricted.

Strengths:

This paper provides a framework to link critical spontaneous state, homeostatic inhibitory plasticity, representational drift, and stimulus population response reliability

Weaknesses:

The study does not show a causal (or necessary/ sufficient) relationship between criticality at the spontaneous state, representational drift, and reliable stimulus presentation. The study only reports an observation that these features could co-exist. However, it does not show how the criticality of the spontaneous state could restrict the manifold for stimulus response.

Reviewer #2 (Public review):

Summary:

This manuscript compares transcription and translation in the spinal cord during the acute and chronic phases of neuropathic pain induced by surgical nerve injury. The authors chose to focus their investigation on translation in the chronic phase due to its greater impact on gene expression in the spinal cord compared to transcription.

(1) The study is significant because the molecular mechanisms underlying chronic pain remain elusive. The role of translational regulation in the spinal cord has not been investigated in neuroplasticity and chronic pain mouse models. The manuscript is innovative and technically robust. The authors employed several cutting-edge techniques such as Rio-seq, TRAP-seq, slice electrophysiology, and viral approaches. Despite the technical complexity, the manuscript is well-written. The authors demonstrated that inhibition of eIF4E alleviates pain hypersensitivity, that de novo protein synthesis is more pronounced in inhibitory interneurons, and that manipulating mTOR-eIF4E pathways alters mechanical sensitivity and neuroplasticity.

(2) Strengths: innovation (conceptual and technical levels), data support the conclusions.

Comments on revisions:

The authors did a great job addressing my comments.

Reviewer #4 (Public review):

Summary:

The significance of this study lies in its focus on translational regulation in the late phase of neuropathic pain, using both genetic and pharmacological approaches, with specific emphasis on parvalbumin-positive (PV⁺) inhibitory interneurons in the spinal cord. The authors are very responsive to all the reviewers' comments.

Strengths:

I did not review this manuscript in the first round. However, the authors have been highly responsive to the reviewers' comments and have substantially strengthened the study. They conducted new behavioral experiments that yielded informative negative results (Fig. 6A and 6B). These findings demonstrate that targeting translational control in PV neurons is sufficient to reverse SNI-induced reductions in PV neuron excitability, but insufficient to ameliorate behavioral phenotypes. This suggests that additional cell types and pathways contribute to late-phase neuropathic pain.

Weaknesses:

Only the withdrawal threshold was measured to assess neuropathic pain. Some studies only used female mice. However, the authors appropriately discuss the study's limitations in the final two paragraphs and have added experimental details to improve clarity. Overall, the manuscript has been significantly improved.

Reviewer #5 (Public review):

Summary:

This study investigates the molecular mechanisms underlying the maintenance of neuropathic pain, specifically focusing on the role of mRNA translation in the spinal cord. Using the Spared Nerve Injury (SNI) model, the authors demonstrate that while both transcription and translation are active in the early phase, the chronic phase (day 63) is uniquely characterized by a shift toward translational control. They identify spinal inhibitory neurons, particularly parvalbumin-positive interneurons, as key sites of this translational regulation.

Strengths:

Technical Rigor: The use of Ribo-seq and TRAP-seq allows for a high-resolution view of the "translatome," which more accurately reflects the functional protein output than standard mRNA-seq.Novelty: The study uncovers that reducing a single translation initiation factor (eIF4E) specifically in the CNS is sufficient to provide long-lasting relief from established chronic pain.Addressing Disinhibition: The electrophysiological evidence showing that increased translation in PV+ neurons reduces their excitability provides a clear mechanism for the "spinal disinhibition" typically seen in chronic pain.

Weaknesses:

Cell-Type Sufficiency: New experiments in the revision show that while inhibiting translation in PV+neurons restores their individual excitability, it is not sufficient on its own to reverse behavioral pain hypersensitivity. This suggests that the maintenance of chronic pain likely involves translational changes across a broader network of cell types, including other inhibitory neurons or non-neuronal cells like microglia. -This does not have to be resolved in the current study, but providing some framework to account for potential mechanisms might help the audience.

Reviewer #1 (Public review):

In this manuscript, Wafer and Tandon et al. present a thoughtful and well-designed genetic screen for regulators of adipose remodeling using zebrafish as a model system. The authors cross-referenced several human adipocyte-related transcriptomic and genetic association datasets to identify candidate genes, which they then functionally tested in zebrafish. Importantly, the authors devised an unbiased microscopy-based screening platform to document quantitative adipose phenotypes with whole animal imaging, while also employing rigorous statistical methods. From their screen, the authors identified 3 genes that resulted in robust adipose phenotypes out of a total of 25 that were tested. Overall, this work will be an important resource for the field because of the genes identified from the screen, the quantitative screening pipeline, and the rigorous phenotypic analysis.

Comments on revisions:

The authors have far exceeded my expectations with their revised manuscript. All my questions and concerns from the original manuscript have been addressed by the authors. The additional data and analysis in Figure 6 and Supplementary Figure 8 are compelling and have greatly improved the manuscript.

Reviewer #2 (Public review):

This manuscript by Wafer, Tandon et al., presents exciting new approaches for using the zebrafish CRISPR screening and imaging system to identify genes that are associated with hyperplastic and hypertrophic adipose morphology. This paper established valuable screening pipelines in zebrafish to identify genetic regulators that affect adipose tissue morphology by combining CRISPR with an imaging-based, comprehensive adipose spatial analysis platform. Starting from a human transcriptomic dataset with differentially expressed genes that separate small and large adipocytes, they eventually identified 3 genes that induce hyperplastic or hypertrophic phenotypes in zebrafish. From which, they focused on foxp1 gene, a transcription factor known to regulate tissue development. They discovered that the foxp1 mutant displays basal hypertrophic morphology and failed to undergo hypertrophic remodeling in response to a high-fat diet, suggesting a link between adipose tissue development and diet-induced remodeling response. Overall, this manuscript is extremely well-written, the data presented is quite compelling, and the identified novel genes that are associated with adipose tissue hyperplastic and hypertrophic morphology and diet-induced remodeling are very exciting.

Strength:

(1) Obesity remains a worldwide public health concern. The mechanisms underlying adipose tissue hypertrophic and hyperplastic adaptation remain unclear.

(2) This manuscript combined multiple omic datasets to identify candidate genes and performed a CRISPR-based screening to identify genes underlying adipose tissue development and adaptation. This new method will open opportunities that will facilitate our understanding and testing of new genetic mechanisms underlying the development of obesity.

(3) Using the screening approach, this paper successfully identified new genes that are associated with adipose tissue LD size change. More importantly, the paper provided further validation using a stable CRISPR line to show the phenotype in basal and HFD conditions.

(4) The experiments are extremely well-designed. Sample sizes are large. Statistical analysis is rigorous. Overall, this is a very high-quality study.

Author's response to the previous comments/weakness:

(1) In this revised manuscript, the authors provided new comprehensive spatial analyses of foxp1a and foxp1 b mutants in basal conditions as well as responding to high-fat feeding. The new data confirmed their initial findings and beautifully illustrated the spatiotemporal dynamics of the adipocytes in response to High-fat diet feeding.

(2) The authors have addressed all my comments, and I do not have further comments.

Reviewer #1 (Public review):

Mutations in CDHR1, the human gene encoding an atypical cadherin-related protein expressed in photoreceptors, are thought to cause cone-rod dystrophy (CRD). However, the pathogenesis leading do this disease is unknown. Previous work has led to the hypothesis that CDHR1 is part of a cadherin-based junction that facilitates the development of new membranous discs at the base of the photoreceptor outer segments, without which photoreceptors malfunction and ultimately degenerate. CDHR1 is hypothesized to bind to a transmembrane partner to accomplish this function, but the putative partner protein has yet to be identified.

The manuscript by Patel et al. makes an important contribution toward improving our understanding of the cellular and molecular basis of CDHR1 associated CRD. Using gene editing, they generate a loss of function mutation in the zebrafish cdhr1a gene, an ortholog of human CDHR1, and show that this novel mutant model has a retinal dystrophy phenotype, specifically related to defective growth and organization of photoreceptor outer segments (OS) and calyceal processes (CP). This phenotype seems to be progressive with age. Importantly, Patel et al, present intriguing evidence that pcdh15b, also known for causing retinal dystrophy in previous Xenopus and zebrafish loss of function studies, is the putative cdhr1a partner protein mediating the function of the junctional complex that regulates photoreceptor OS growth and stability.

This research is significant in that it:

(1) provides evidence for a progressive, dystrophic photoreceptor phenotype in the cdhr1a mutant and, therefore, effectively models human CRD; and

(2) identifies pcdh15b as the putative, and long sought after, binding partner for cdhr1a, further supporting the theory of a cadherin-based junction complex that facilitates OS disc biogenesis.

Comments on the revised version of the manuscript:

The authors adequately addressed previous comments related to lack of details on quantitative and statistical analyses and methods. In this regard, I believe the revised manuscript presents a stronger analysis of the data. I also appreciated the revised discussion section, which better contextualizes their new data with previous observations in different animal models.

The authors provided additional evidence in Fig 1C-H for the co-localization of pcdh15b and actin within CPs using immunolabeling with super resolution imaging. This data firmly supports their other observations. A similar approach tends to also show co-localization of actin and cdhr1a, although the authors suggest that the pattern of expression is less overlapping, which would be expected if cdhr1a is predominately expressed in the OS membranes whereas pcdh15b is predominantly expressed in the CP membranes. In my opinion the data presented to support this separation is still not that convincing. Moreover, the authors show that both cdhr1a and pcdh15b are expressed in CPs using immuno-TEM (Fig 1I). This is a difficult question to address experimentally, and it is, of course, still plausible that pcdh15b within the CP membrane and cdhr1a within the OS membrane are interacting in trans. However, I just don't think that the data unequivocally support mutually exclusive localization of these proteins as suggested by the authors and depicted in the model in Fig 1J.

Reviewer #2 (Public review):

Summary:

The goal of this study was to develop a model for CDHR1-based Con-rod dystrophy and study the role of this cadherin in cone photoreceptors. Using genetic manipulation, a cell binging assay, and high- resolution microscopy the authors find that like rods, cones localize CDHR1 to the lateral edge of outer segment (OS) discs and closely opposes PCDH15b which is known to localize to calyceal processes (CPs). Ectopic expression of CDHR1 and PCDH15b in K652 cells indicate these cadherins promote cell aggregation as heterophilic interactants, but not through homophilic binding. This data suggests a model where CDHR1 and PCDH15b link OS and CPs and potential stabilize cone photoreceptor structure. Mutation analysis of each cadherin results in cone structural defects at late larval stages. While pcdh15b homozygous mutants are lethal, cdhr1 mutants are viable and subsequently show photoreceptor degeneration by 3-6 months.

Strengths:

A major strength of this research is the development of an animal model to study the cone specific phenotypes associate with CDHR1-based CRD. The data supporting CDHR1 (OS) and PCDH15 (CP) binding is also a strength, although this interaction could be better characterized in future studies. The quality of the high-resolution imaging (at the light and EM levels) is outstanding. In general, results support the conclusions of the authors.

Weaknesses:

While the cellular phenotyping is strong, the functional consequences of CDHR1 disruption is not addressed. While this is not the focus of the investigation, such analysis would raise the impact of the study overall. This is particularly important given some of the small changes observed in OS and CP structure. While statistically significant, are the subtle changes biologically significant? Examples include cone OS length (Fig 4F, 6E) as well as other morphometric data (Fig 7I in particular). Related, for quantitative data and analysis throughout the manuscript, more information regarding the number of fish/eyes analyzed as well as cells per sample would provide confidence in the rigor. The authors should also not whether analysis was done in an automated and/or masked manner.

Comments on revisions:

Most of my concerns were addressed in this revised version.

Reviewer #3 (Public review):

Summary:

The manuscript by Patel et al investigates the hypothesis that CDHR1a on photoreceptor outer segments is the binding partner for PCDH15 on the calyceal processes, and the absence of either adhesion molecule results in separation between the two structures, eventually leading to degeneration. PCDH15 mutations cause Usher syndrome, a disease of combined hearing and vision loss. In the ear, PCDH15 binds CDH23 to form tip links between stereocilia. The vision loss in less understood. Previous work suggested PCDH15 is localized to the calyceal processes, but the expression of CDH23 is inconsistent between species. Patel et al suggest that CDHR1a (formerly PCDH21) fulfills the role of CDH23 in the retina.

The experiments are mainly performed using the zebrafish model system. Expression of Pcdh15b and Cdhr1a protein is shown in the photoreceptor layer through standard confocal and structured illumination microscopy. The two proteins co-IP and can induce aggregation in vitro. Loss of either Cdhr1a or Pcdh15, or both, results in degeneration of photoreceptor outer segments over time, with cones affected primarily.

The idea of the study is logical given the photoreceptor diseases caused by mutations in either gene, the comparisons to stereocilia tip links, and the protein localization near the outer segments. The work here demonstrates that the two proteins interact in vitro and are both required for ongoing outer segment maintenance. The major novelty for this paper would be the demonstration that Pcdh15 localized to calyceal processes interacts with Cdhr1a on the outer segment, thereby connecting the two structures. Unfortunately, the data as presented are inadequate proof of this model.

Strengths:

The in vitro data to support the ability of of Pcdh15b and Cdhr1a to bind is well done. The use of pcdh15b and cdhr1a single and double mutants is also a strength of the study, especially being that this would be the first characterization of a zebrafish cdhr1a mutant.

This is a large body of data.

Weaknesses:

(1) I have serious concerns about the quality of the imaging here. The premise that cdhr1a/pcdh15 juxtaposition is evidence for the two proteins mediating the connection between outer segments and calyceal processes requires very careful microscopy. The SIM images have two major issues - one being that the red and green channels are misaligned and the other being evidence of bleed through between the channels. This is obvious in Fig 2A but likely true across all the panels in Fig 2, and possibly applies to confocal images in Fig 1 as well. The co-labelling with actin shows very uneven, punctate staining for actin bundles.

(2) The newly added TEM and transverse sections include colored regions that obscure the imaging.

(3) The quantification should be done with averages from individual fish. Counting individual measurements as single data points artificially inflates the significance. Also, the cone subtypes are still lumped together for analysis despite their variable sizes.

(4) I highlighted previously that the measurement of calyceal processes was incorrect. The redrawn labels in Fig 7 are now more accurate, although still difficult to interpret. However, the quantification in Fig 7O is exactly the same. How can that be if the measurement region is now different?

(5) Lower magnification views would provide context for the TEM data.

(6) The statement describing the separation between calyceal processes and the outer segment in the mutants is still not backed up by the data.

(7) The authors state "from the fact that rod CPs are inherently much smaller than cone CPs". This is now referenced, but incorrectly. Also, the issue of pigment interference was not addressed.

(8) The images in panels B-F of the Supplemental Figure are uncannily similar, possibly even of the same fish at different focal planes.

Reviewer #1 (Public review):

Summary:

The authors provide a simple yet elegant approach to identifying therapeutic targets that synergize to prevent therapeutic resistance using cell lines, data-independent acquisition proteomics, and bioinformatic analysis. The authors identify several combinations of pharmaceuticals that were able to overcome or prevent therapeutic resistance in culture models of ovarian cancer, a disease with an unmet diagnostic and therapeutic need.

Strengths:

The manuscript utilizes state-of-the-art proteomic analysis, entailing data-independent acquisition methods, an approach that maximizes the robustness of identified proteins across cell lines. The authors focus their analysis on several drugs under development for the treatment of ovarian cancer and utilize straightforward thresholds for identifying proteomic adaptations across several drugs on the OVSAHO cell line. The authors utilized three independent and complementary approaches to predicting drug synergy (NetBox, GSEA, and Manual Curation). The drug combination with the most robust synergy across multiple cell lines was the inhibition of MEK and CDK4/6 using PD-0325901+Palbociclib, respectively. Additional combinations, including PARPi (rucaparib) and the fatty acid synthase inhibitor (TVB-2640). Collectively, this study provides important insight and exemplifies a solid approach to identifying drug syngery without large drug library screens.

Weaknesses:

The manuscript supports their findings by describing the biological function(s) of targets using referenced literature. While this is valuable, the number of downstream targets for each initial target is extensive, thus, the current work does not attempt to elucidate the mechanism of their drug synergy. Responses to drugs are quantified 72 hours after treatment and exclusively focused on cell viability and protein expression levels. The discovery phase of experimentation was solely performed on OVSAHO cell line. An additional cell line(s) would increase the impact of how the authors went about identifying synergistic targets using bioinformatics. Ovarian cancer is elusive to treatment as primary cancer will form spheroids within ascites/peritoneal fluids in a state of pseudo-senescence to overcome environmental stress. The current manuscript is executed in 2D culture, which has been demonstrated to deviate from 3D, PDX, and primary tumours in terms of therapeutic resistance (DOI: 10.3390/cancers13164208). Collectively, the manuscript is insufficient in providing additional mechanistic insight beyond the literature, and its interpretation of data is limited to 2D culture until further validated.

Comments on revisions:

The reviewer has no further recommendations for the authors.

Reviewer #2 (Public review):

Summary:

Franz and colleagues combined proteomics analysis of OVSAHO cell lines treated with 6 individual drugs. The quantitative proteomics data was then used for computational analysis to identify candidates/modules that could be used to predict combination treatments for specific drugs.

Strengths:

The authors present solid proteomics data and computational analysis to effectively repeat at the proteomics level analysis that have previously been done predominately with transcriptional profiling. Since most drugs either target proteins and/or proteins are the functional units of cells, this makes intuitively sense.

Weaknesses:

Considering the available resources of the involved teams, preforming the initial analysis in a single HGSC cells is certainly a weakness/limitation. During the revision additional cell lines were used for verification.

The data also shows how challenging it is to correctly predict drug combinations. In Table 2 (if I read it correctly) the majority of the drug combinations predicted for the initial cell line OVSAHO did not result in the predicted effect. It also shows how variable response was in the different HGSC cell lines used for combination treatment. The success rate will most likely continue to drop as more sophisticated models are being used (i.e., PDX). Human patients are even more challenging.

It would most likely be useful to more directly mention/discuss these caveats in the manuscript. This was added to the discussion during the revision. Overall the authors have responded to previous suggestions.

Reviewer #1 (Public review):

Summary:

This study proposes a simple and universal reinforcement-learning framework for understanding learning in complex motor tasks. Central to the framework is a policy-gradient algorithm, in which motor commands are updated not via the gradient of the reward with respect to policy parameters, but via the gradient of the policy itself, scaled by reward information. The authors demonstrate that this scheme can reproduce learning dynamics that have been reported in previous empirical studies.

Strengths:

The key contribution of this study lies in its application of a policy-gradient algorithm to describe motor learning processes. This idea is biologically plausible, as computing the gradient of the policy with respect to its parameters is likely to be substantially easier for the nervous system than computing the gradient of the reward with respect to policy parameters. The authors present three representative examples showing that this scheme can capture several aspects of motor learning dynamics. Notably, providing such a unified description across different tasks has been difficult for conventionally proposed learning frameworks, such as supervised learning.

Weaknesses:

While this scheme is valuable in that it captures certain aspects of learning dynamics, I find that its overall significance is limited for the following reasons.

(1) The empirical results examined in this study primarily demonstrate that motor learning drives performance toward the spatial task goal while reducing variability. Given that the policies are expressed using Gaussian distributions and that their parameters (i.e., the mean and covariance matrix) are updated during learning, it is not surprising that the proposed scheme can reproduce these results by fitting the parameters to the data.

(2) The proposed framework assumes that the motor learning system relies on the gradient of the policy with respect to its parameters. However, I am not convinced that this assumption is always appropriate, because in all three empirical studies examined here, explicit spatial error information is available. In such cases, the motor learning system could, in principle, compute the gradient of the error with respect to the policy parameters directly, without relying on a policy-gradient mechanism.

(3) Most importantly, it remains unclear how the proposed scheme advances our understanding of the underlying learning mechanisms beyond providing a descriptive account of the learning process. While the framework offers a compact mathematical description of learning dynamics, it is uncertain how it can yield novel mechanistic insights or testable predictions that distinguish it from existing learning models.

Reviewer #2 (Public review):

Summary:

In this study, Haith applies, and to some extent extends, the theoretical framework of policy gradient (PG) and the derived REINFORCE learning rules to human motor learning. This approach is coherent because human motor skill learning is characterized by improvements in both accuracy and precision (the inverse of variance), and REINFORCE provides update rules for both the mean and the variance of the motor commands.

Weaknesses:

The mean update (equation 4) is given in task space (i.e., angle and velocity for the skittle task), but the covariance update (equation 5) is given in eigenvector space. This formulation appears to have been provided for computational convenience, as it ensures that the variances are always positive by exponentiating the eigenvalues. However, this eigenspace formulation is somewhat artificial and complex (notably the update rule for the orientation of the covariance matrix) and seems far from biological reality. A simpler alternative, suggested by the author, is to provide the full covariance matrix, including crossed terms, and derive equations to update the diagonal variance terms and the cross-terms (perhaps after a transformation to keep all elements positive if needed). This would provide a simpler and more biologically plausible update to the covariance matrix terms, in the spirit of the original REINFORCE algorithm. The author suggests that he has derived the update rule for the cross terms, so this should be relatively easy to write and update, especially for the skittle learning rules. If the author wishes to keep their rules in simulations, then the two mathematical rules could be presented in the methods or a supplementary material section.

The discussion about binary rewards and the increase in variance in previous experiments is potentially interesting. However, I do not understand why variance cannot increase with the policy-gradient RL update? Surely, equation 5 can lead to both an increase and a decrease in variance depending on the reward prediction error and the noise (for example, suppose the noise at trial i is small and leads to a smaller reward than the baseline; variance would increase). It would be interesting to see detailed simulation results for the skittle task showing changes in both mean and variance across a few consecutive trials, with both increases and decreases in reward prediction errors. These results could then be compared in simulations with those of a task with discrete binary rewards.

Generalization is a major feature of human learning, but it is not discussed or studied here. In fact, in the de novo task simulations, there can be no generalization because the values are modeled as running averages for each target rather than derived from a critic network. Can the author discuss this point and, ideally, show generalization results in simulations, say in the skittle task?

The application of the model to reproduce the Shmuelof et al. data is, at the same time, justified (because one of their main results is an improvement in precision, which Policy Gradient directly addresses) and somewhat "forced," as the author approximates curved movements with a series of straight-line movements. The author therefore needs to specify multiple via points with PG updating and a reward function that also enforces smoothness. The justification for the Guigon 2023 model seems somewhat artificial because it mainly applies to slow movements. Can the author comment and discuss alternatives that do not require via points, drawing from the robotics literature if needed (Schaal's Dynamic Movement Primitives come to mind, for example).

Policy Gradient requires both a "noisy" and a clean "pass", making it non-biological in its simplest form. Legenstein et al. (2010) and Miconi (2017) provided biologically plausible forms for the mean update. Since Policy Gradient is proposed as a model of human motor learning, can the author discuss the biological plausibility of the proposed learning rules and possible biologically plausible extensions?

Reviewer #1 (Public review):

The authors conducted a comprehensive benchmarking and evaluation of co-folding platforms, including AlphaFold3, Boltz-2, Chai-1, and the docking algorithm Dock3.7, which employs a physics-based scoring function that incorporates van der Waals interactions, electrostatics, and ligand desolvation energies. The system of interest was the SARS-CoV-2 NSP3 macrodomain (Mac1), an increasingly popular antiviral target, and the ligand sets comprised 557 unseen ligand poses (keeping the training for these co-folding platforms in mind). Additionally, the authors investigated whether the co-folding models could distinguish true ligands from non-binding small molecules. The study is thorough, with extensive statistical support and consensus across multiple metrics (chemoinformatics for quantifying ligand similarity and efficacy). The questions that the authors aim to address are whether the co-folding models struggle with memorization, whether they can distinguish between a true and a false binder, whether they replicate experimental binding affinities and efficacy, and how they compare to the physics-based docking algorithm (Dock3.7).

Strengths:

Overall, this is a scientifically solid paper. The work is highly detailed and well executed, featuring thorough data analysis and statistical assessment.

Weaknesses:

My main concern is that the study's aim is a bit unclear. Modern benchmarking studies comparing physics-based docking with deep learning-based co-folding approaches (e.g., AF3, Boltz-2, Chai-1, and others) are increasingly expected to go beyond aggregate performance metrics. In addition to rigorous dataset construction, transparent methodology, and appropriate statistical evaluation, high-impact benchmarks typically provide actionable guidance on when each method class is most appropriate, reflecting their distinct inductive biases and practical constraints. Failure-mode analyses that link performance differences to protein flexibility, ligand chemistry, or binding-site characteristics are particularly valuable, as they move comparisons beyond "scoreboard" assessments toward mechanistic understanding. While full biological validation is not expected, qualitative interpretation grounded in physical and biological principles strengthens conclusions. Providing reproducible workflows or reference pipelines is not mandatory, but it is increasingly viewed as a best practice because it facilitates adoption and helps contextualize results for practitioners.

Reviewer #2 (Public review):

Summary:

The manuscript by Kim et al. evaluates the performance of three modern AI-based methods in predicting complex structures and binding affinities between proteins and chemical compounds. An honest 'prospective' evaluation is achieved by studying benchmark structures and chemical compounds that did not exist in the PDB at the time the AI structure prediction models (AlphaFold3, Chai-1, Boltz-2) were trained.

Strengths:

(1) The study addresses an important question in modern computational biology and drug discovery, and establishes the strengths and limitations of the three tools in solving various computational chemistry tasks, including compound pose prediction, active-inactive discrimination, and potency ranking.

(2) The conclusions are based on examination of four separate targets and respective compound datasets, where for one of the targets, the authors also obtained numerous X-ray structures to serve as experimental answers for the binding pose prediction task.

(3) The study reports relationships between structure prediction confidence, predicted energies (DOCK3.7), and affinity predictions (Boltz-2) with the geometric accuracy of compound pose prediction as well as the experimentally measured potency.

(4) One of the key findings is the limited ability of co-folding methods to predict conformational rearrangements, which does not correlate with their ability to predict binding poses of the compounds inducing these rearrangements.

(5) The findings could serve as useful guidelines for computational chemists in selecting appropriate software and scoring schemes for each task.

Weaknesses:

While I consider this a solid study, several aspects would need to be addressed to make it really strong:

(1) DOCK3.7 docking and scoring experiments were performed using one experimental structure of Mac1, selected from dozens of structures based on a criterion that is not sufficiently well justified. For sigma2 receptor, dopamine D4 receptor, and AmpC β-lactamase, it is not clear which structures or models were selected for docking at all. It is well known that geometry predictions, scoring, and active-inactive ROC AUCs are all strongly influenced by the selected structure. It would be important to attempt Mac1 docking using all available experimental Mac1 structures, or at least against representative structures in various conformations; it would also be quite insightful to compare results to docking of the same compound sets to AF3, Boltz-2 and Chai-1 predicted structures of Mac1. Same goes for the docking studies of sigma2, D4, and AmpC β-lactamase.

(2) For binding affinity predictions, as a control, authors should consider compound co-folding with an unrelated protein, or even with a pseudo-peptide that consists of a few random single amino acids - this would provide an honest baseline for such predictions.

(3) ROC curves Figure 3 and elsewhere should be shown, and AUCs quantified/reported on a log or square-root scaled x-axis, to emphasize early enrichment, which is the area of practical significance for these predictions. For example, Figure 3A currently suggests that the pose prediction performance of AF3 exceeds that of Boltz-2 whereas the early enrichment is clearly better for Boltz-2.

(4) 'Trained set' in figures and text should probably be 'training set'? Or otherwise explain this new term the first time it is introduced.

(5) Figure 1 illustrates a projection onto the first two principal components of a space that apparently had only one (scalar) metric for each compound pair (% maximum common substructure or Tanimoto coefficient); the authors need to better explain the principle behind this analysis and visualization.

Reviewer #3 (Public review):

Summary:

This study's core conclusions are well-supported by data. It is shown that co-folding outperforms docking in known ligand pose/affinity prediction (validated by RMSD and IC₅₀ correlation), struggles with false-positive discrimination in virtual screens (lower AUC values), and is complementary to docking (non-correlated errors, distinct strengths in drug discovery stages).

Strengths:

(1) Unprecedented prospective design with 557 novel Mac1-ligand complexes ensures rigorous, independent evaluation of co-folding methods.

(2) Comprehensive comparison of 3 co-folding tools (AlphaFold3, Chai-1, Boltz-2) with DOCK3.7 across diverse targets and metrics enables nuanced performance assessment.

(3) The study clearly demonstrates complementary roles of co-folding (superior pose/affinity prediction for known ligands) and docking (better hit prioritization), and addresses deep learning memorization concerns via ligand similarity analysis.

Weaknesses:

(1) Limited generalization to diverse protein families (e.g., no ion channels/transporters).

(2) Ambiguity in the mechanism underlying co-folding's failure to predict rare conformational changes.

(3) Virtual screen comparison is unbalanced (docking-prioritized hit lists bias results).

Reviewer #1 (Public review):

Summary:

In this study, the authors propose that HSV-1 infection degrades the class I histone deacetylases HDAC1 and HDAC2. The MDM2 E3 ubiquitin ligase from the DNA damage response pathway is responsible for ubiquitinating these HDACs that are subsequently degraded via proteasomes. The authors hypothesize that HDAC degradation will cause hyperacetylation of viral chromatin and enable viral gene transcription.

Strengths:

The ubiquitination of HDAC1 & HDAC2 by Mdm2 and the mapping studies are clear.

Weaknesses:

(1) Degradation of HDACs is observed late, at least 12-24 h post-infection (1 PFU/cell). Viral genes have been transcribed by that point, and the virus has replicated its genome. The kinetics do not match the proposed model.

(2) The authors need to connect these findings with their story. As of now, these findings are correlative. For example, what is the impact of MDM2 depletion on viral gene expression and progeny virus production? Leptomycin B is not specific to the HDAC cytoplasmic translocation, and its effect on the infection could be due to its effect on ICP27.

(3) The time point when the inhibitors were added to the cultures has not been stated in any experiment. If inhibitors were added with the virus, viral gene expression would be blocked.

(4) The authors need to present late gene expression data in all the experiments where drugs have been used.

(5) Figure 1A, ICP4 is not detected up to 12 hours post-infection of HeLa cells with 1 PFU/cell. This cannot be true.

(6) Leptomycin B blocks nuclear/cytoplasmic shuttling of ICP27 that brings viral mRNAs to the cytoplasm to be translated. So, the effect of LMB is not specific to the HDACs.

(7) The key experiment is to use the degradation-resistant form of HDAC1 to evaluate its impact on viral gene transcription.

(8) In the experiment where Mdm2 was depleted, the authors need to demonstrate the effect on the infection. ICP4 expression is not enough. How about growth curves? After Mdm2 depletion, ICP4 expression increases, which may contradict the authors' findings. An analysis of alpha and gamma gene expression is important.

(9) Why did the authors analyze a liver HSV-1 infection and not a more relevant skin infection?

Reviewer #2 (Public review):

Summary:

The authors discovered that HDAC1/2 are degraded in HSV-1 and PRV infections. They attempted to establish a new mechanism by which HDAC1/2 are translocated to the cytoplasm to be degraded in HSV-1 infection, and the degradation causes changes in histone acetylation to affect the DDR pathway.

Strength:

(1) Interesting findings of HDAC1/2 degradation during HSV-1 and PRV infection, and it may impact more than the virology field.

(2) Significant work to identify the ubiquitin site in HDAC1/2 and K63 linkage.

Weaknesses:

(1) Insufficient evidence to support the mechanism described by the authors.

(2) Expansion of the conclusion to alphaherpesvirus without studying the intended mechanism in PRV infection.

Overall, there may be a correlation between HDAC1/2 level, ATM/ATR phosphorylation, and HDAC1 translocation during the HSV-1 infection. However, core evidence supporting the mechanism that a) HDAC1 export causes its degradation, b) degradation of HDAC1 causes histone acetylation changes and DRR activation has not been sufficiently demonstrated.

Reviewer #3 (Public review):

The authors state that infection of cells by the alphaherpesviruses HSV-1 or PRV leads to a proteosome-dependent reduction in levels of HDAC1 and HDAC2 and that this leads to chromatin hyperacetylation, a DNA damage response, and greater replication of these viruses. Previously, other authors reported no change in levels of HDAC1 and HDAC2 after HSV-1 infection of human cells, but this paper is neither cited nor commented on in this new submission. The experiments are poorly designed. For instance, most of the time points analysed are way beyond the time needed for HSV-1 replication and are therefore not biologically relevant. The infections are done with a dose of virus that does not ensure that all cells are infected synchronously, but rather infection spreads from cell to cell with multiple rounds of replication. Some essential controls are missing. Additionally, this reviewer feels that the data presented do not support the conclusions drawn. Currently, links are not established between a reduction in HDAC1/ 2 and other phenomena such as hyperacetylation of histones, a DDR, and altered virus replication. The paper does not identify which HSV or PRV protein(s) induce reduction in HDACs, nor how the HDACs mediate antiviral activity; what are the HSV-1 or PRV protein targets? Lastly, the paper is not well prepared, and it does not adequately refer to prior literature.

Reviewer #1 (Public review):

Summary

The authors use reduced-representation sequencing (GBS) across samples from the quaking aspen clonal stand Pando to identify putative somatic mutations, which were used to estimate clone age, and evaluate whether somatic variation shows spatial structure across the grove. This is a compelling and charismatic system to look at somatic mutation in plants. They report little sharing of putative somatic mutations as a function of distance and interpret this as evidence for weak mutation transmission or homogenization over time, potentially driven by rapid root growth and clonal spread dynamics. They use mutations to estimate clone age. The authors are generally upfront and commendably transparent about limitations in sequencing depth and mutation calling. The paper addresses an interesting research system, but struggles to overcome limitations in the suitability of the data.

Strengths.

This is a fantastic system and an interesting set of questions. The authors' GBS data does a great job distinguishing Pando from its neighbors, which is an important first step in studying the history of this clone.

The manuscript is upfront and highlights the need for improved data to refine inference, for example: "Higher-coverage whole-genome sequencing, and ideally single-cell sequencing of defined meristem lineages, will be needed to refine mutational and evolutionary parameter estimates in this iconic organism."

It also states that "either we are missing roughly 80% of true somatic mutations or only 20% of the mutations we detect are true positives."

I appreciate that the authors report an age estimate range that considers the breadth of potential false negatives and positives.

Weaknesses

I am still not sure whether the paper overcomes issues with the use of GBS for somatic mutation calling.

I found it difficult to reconcile the manuscript's description of the call set as "conservative" with the reported validation tests (calibrated by looking at retained variants detected in 2 of 8 technical replicates). How was this threshold determined? A mutation with 2/8 has quite low reproducibility, which could reflect either substantial false negatives under low depth (true variants frequently dropping out) or false positives that recur sporadically due to library - or sequencing-specific artifacts. Without stronger internal diagnostics or external validation, it is hard to determine which applies here.

The GBS sequence space and genomic distribution could be more clearly explained. According to the methods, "The total number of base pairs sequenced(129,194,577) was estimated using angsd, and reduced following the proportion of base pairs that we filtered out because of low coverage (48%)." What does the 129M basepairs represent? Is that 129M/genome length, or is it the number of aligned basepairs (i.e., 1M genome covered x129 depth)? In addition, summarizing where GBS loci fall across the genome, genic vs intergenic vs TE; repetitive vs unique, since these can have substantially different somatic mutation rates (Meyer et al. 2025). Without additional summary/descriptive statistics, it is hard to interpret both missingness and "rate".

Statistical concerns about some results. In the Figure 3 legend, the authors state that the sample-level relationship between shared variants and distance is significant: "Pearson correlation coefficient ... is −0.02, 95% CI = [−0.05, 0.00], which is significantly different from a randomized distribution (P < 0.001) (B)." However, as plotted in Figure 3B, the observed correlation (−0.02) appears to fall well within the bulk of the randomized distribution of correlation coefficients. If the reported P value is intended to be permutation-based (i.e., the tail probability under the randomized null), it is unclear how P could be < 0.001 given that the observed value does not appear extreme relative to the null.

The developmental program of plant stem cell layers is essential, but not discussed much. In a root-spreading clone, expectations about mutation sharing depend strongly on how new ramets arise developmentally (root-derived meristem initiation) and how layered meristems partition mutations across tissues (e.g., L1/L2/L3). I was surprised there was not a substantial discussion of the details about the layer specificity of somatic development and mutation accumulation in plants. Especially relating to mutations that would be shared between roots/shoots around potential layer-specific growth of roots. The current analysis seems to focus on comparisons within tissue types (e.g., leaves between ramets), but did not report informative tests between tissue and within-ramet (e.g., in heavily sampled trees, whether a ramet's root, shoot, leaves, share a subset of variants; whether neighboring ramets share root-lineage variants more than shoot-lineage variants). It would help to articulate expectations and clarify what the data can and cannot test. Relatedly, for "mutation rates," in aging material, it would be good to discuss which meristem layer(s) each tissue is likely sampling and how layer-specific mutation dynamics (e.g., reported differences between L1 vs L2 lineages) could influence rate and therefore age estimates (Goel et al. 2024, Amundson et al. 2025).

Developmental mosaicism makes expected allele fractions lower than discussed in the paper. The supplement states, "However, because the Pando clone is triploid, it reduces our expectation for fixation of a mutation to 0.33", but this ignores layer-specific stem cells in plant development. True that if calls are made against a haploid reference, then a new somatic mutation in a triploid background is expected around ~1/3 allele fraction - but only if fixed in 100% of cells. Layer-specificity (e.g., L1 vs L2 vs L3 restriction) or polyclonal founding events will push expected allele fractions substantially lower. Therefore, at ~12-14× depth (or min of 4x), these allele fractions translate into only a handful (or even 0) of alternate reads (<<33% is expectation).

Within-tree replicate consistency was unclear. The manuscript hints at multiple samples/replicates per tree (e.g., Figure S2), but it is not clear how often the same putative somatic variants are recovered across samples from the same ramet and tissue. A simple reproducibility summary would be extremely helpful: for variants called in one sample, what fraction are recovered in other samples from the same tree (by tissue), what variant allele fractions, and how do their spectra compare to mutations unique to a single sample?

The manuscript did not provide supplemental tables or mutation calls. Supplemental tables containing pre-filter and/or post-filter calls (or some other structured data file with flags indicating various quality metrics, REF vs ALT depths at minimum, REF call, and ALT call) would substantially improve transparency and ability to evaluate the work.

Reviewer #2 (Public review):

Summary:

The topic of the paper is intriguing as it sets out to age one of the potentially largest living organisms, a tree clone (Pando), using shallow genome resequencing of a large number of replicate samples. The key result is that the Pando clone is several tens of thousands of years old, which is of high-interest to plant genomics and evolutionary ecology.

Weaknesses:

Unfortunately, the claims are not matched by the available data and their analysis. Probably, the results can also not be resurrected using modified analyses, as the available data are not suited to reliably detect somatic genetic variation as a means to age-clonal plants.

In order to reliably age clones, one needs to consider the full process by which clone mates genetically diverge from one another over time, which starts with a plant's apical meristem (SAM). From this, all above-ground tissues such as twigs and branches, as well as leaves, are derived, which has been beautifully worked out now in oaks and many fruit trees (e.g., doi: 10.1101/2023.01.10.523380 ; 10.1101/2024.01.04.573414). For the accumulation and propagation of fixed somatic genetic variation, only the processes in the SAM matter. Hence, it does make little sense to look at tissue-specific mutations unless one is invoking non-cell division induced mutations through UV light. Those, however, would remain undetected with the present low-coverage sequencing as they cannot leave the mosaic status any more, as that tissue is essentially non-dividing.

Somatic genetic drift (https://www.nature.com/articles/s41559-020-1196-4) is the foundation for the fixation of somatic genetic variation and hence, for ageing (plant) clones. It requires quantitative modeling of the processes at the cell-line level when new modules, here, aspen trees are formed, in particular N (cell population size) and N0 (founder cell size).

Calibrations have to be made using the mutation and fixation rate at the somatic cell lineage level, ideally also with some empirical data. In trees such as aspen, it would be very easy to obtain calibration points of branch tips that have physically and thus genetically diverged upon a defined TCA to directly determine the rate of accumulation of somatic genetic variation by direct dendrochronology (i.e., counting tree rings).

Instead, in the present work, a mutation rate from another tree species is taken, which will introduce a lot of uncertainty into the estimates, given that tree SAMs divide at a very different pace (see doi 10.1093/evolut/qpae150). It is clear that a small difference in the assumed mutation rate, e.g., a higher one, would conversely reduce the age estimate considerably.

I am doubtful that a conventional phylogenetic model based on coalescence, such as the one employed here, can be utilized, as it assumes a sexually recombining population and hence variable sites. A model simulation on an asexually evolving population would be needed to check this.

In order to reliably call somatic genetic variation, a decent coverage of short-read sequences is needed, definitely > 15x, which was achieved in the present dataset. This is particularly relevant as a fixation in one of the three haploid chromosome sets would just amount to a read frequency of only 0.33. A coverage of only 4x reads per called site seems very low to me; in other words, the filtering steps do not seem to be very rigorous to me. It is also difficult to follow the logic of several ad hoc adjustments that were made to compensate for the low coverage of sequencing, in particular, the common panel and the replicate identical samples. Why chose 80% in the latter?

There are alternative, non-sequencing-based ways to double-check the accuracy of somatic SNP calls (e.g., described here https://www.nature.com/articles/s41559-020-1196-4), which could have been employed at least once to evaluate the error rates for the specific sequencing strategy.

I also suggest that for any future study, reference to mutation callers developed for cancer somatic mutation detection should be employed, which are now increasingly used both in clonal plants and trees for that purpose.

What worries me is that there is a poor correlation between physical and genetic distance. This lack of correlation among spatial and genetic structure, for example, the star-like phylogeny presented in Figure 6d, indicates a large fraction of false positives rather than some special, as yet unexplained processes of local mutation accumulation that the authors claim to have discovered.

Finally, the work is not properly embedded into the current literature. For example, recent developments of molecular clocks were not considered, such as the development of a dedicated somatic genetic clock that precisely addresses this question (https://www.nature.com/articles/s41559-024-02439-z). Also, older but nevertheless significant work that aged aspen clones using microsatellite markers is not mentioned (http://dx.doi.org/10.1111/j.1365-294X.2008.03962.x).

Reviewer #1 (Public review):

Summary:

The manuscript by Vasquez-Correa and colleagues describes the expression pattern of the ocelli (simple eye) gene regulatory network in ants. They correlate the expression pattern of these genes with the presence and absence of ocelli in different classes and species of ants. The presence of ocelli is a polyphenic trait in ants - understanding the molecular and developmental underpinnings of polyphenic traits is of significant interest to evolutionary biologists, developmental biologists, and ecologists. The authors propose that the presence of the latent expression of the ocellar network in classes of ants that do not display ocelli in the adults may underlie the re-evolution of ocelli within the ant lineage.

Strengths:

The strengths of the manuscript are that it is well written, the images are of the highest quality, and the data support the conclusions of the authors.

Weaknesses:

One improvement that could be made is to include imaginal discs of the queen ants as well as scanning electron images of the ocelli of the queen ant to match the pupal stage images of the worker and soldier ants. A second improvement is to attempt a gene knockdown using RNAi or similar methods to ensure that the genes that are being studied are, in fact, responsible for ocelli development in the ant.

Reviewer #2 (Public review):

Summary:

The manuscript titled "Latent gene network expression underlies partial re-evolution of a polyphenic trait in the worker caste of ants" by Vasquez-Correa et al. aimed to study genetic mechanisms underlying developmental plasticity, especially binary polyphenism in queen vs worker ant castes. This is an interesting question regarding the extent to which phenotypic traits were altered, lost or regained, and how molecular pathways (upstream vs. downstream) can facilitate this process.

In ants, reproductive castes (queens and males) develop wings as well as 3 ocelli for mating flights and other activities, while worker castes are wingless, and in some species, they have either no or a reduced number of ocelli. The phylogenetic analysis showed that in the Camponotini ant clade, the one-ocellus phenotype re-evolved in three species independently. The authors analyzed the conserved developmental pathways between Drosophila (well-established) and ants using HCR (a high-quality in situ hybridization technique). They found that although upstream genes for the development of ocelli (otd and hh) showed similar expression between castes, downstream genes (toy, eya, and so) had reduced or no expression in workers of C. floridanus, and this differential expression may lead to partial or complete loss of ocelli. Consistently, workers develop rudimentary tissues, suggesting that they initiate the ocellus developmental process but somehow stop it before adulthood.

Strengths:

Evo-devo approaches to reveal conserved molecular pathways of ocellus development. High-quality HCR provided convincing evidence of the expression of key genes in ocelli, eyes and antenna throughout larval development.

Using HCR, the authors showed differential expression of downstream genes in males vs. soldiers vs. minor workers of C. floridanus, which might explain phenotypic differences between castes.

Weaknesses:

Although the molecular pathway is conserved, the mechanism underlying the lack of ocelli in workers remains unclear. In C. floridanus, it could be explained by the evidence of no expression of certain developmental genes, but in other species, e.g. Polyrachis rastellata, is their expression intact, or reduced? There is no control male.

In addition, HCR in species with partial re-evolution (if their genomes have been sequenced) would be useful to understand the mechanism. For example, there might be differential spatial expression between medial and lateral ocelli.

Reviewer #3 (Public review):

Summary:

This paper examines the loss and re-evolution of specific organs during the evolution of ants. The authors show that these organs, the ocelli, disappear and are re-evolved in different ant species and in different ant castes within these species. The authors show that this is linked to dto a conserved GRN discovered in Drosophila, that appears to underlie the development of the ocelli, and demonstrate that this GRN appears to remain active in the developing heads of ants that have no ocelli- implying that it is the evolutionary latency of this GRN that allows loss and subsequent evolution.

Strengths:

This manuscript has outstanding imaging of a very difficult developing organ, and the key data, fluorescence in situ hybridisation, is done well and clearly shows what the authors wish to demonstrate. The methods are well described and underpin the whole work.

The authors convincing demonstatrate that gene expression patterns imply the conservation of the ocellus gene regulatory network from Drosophila to ants. They further show that this network is present even in ants that don't produce an adult ocellus, but do show that in those species, loss of a developing nascent ocellus (which they identify) occurs at the same time as an interruption in the expression of the key genes in the GRN. All of this data is beautifully presented and explained.

Weaknesses:

There is one key weakness in that there are no functional students that indicate that the GRN actually does make the ocellus, though the expression patterns are convincing. This applies to loss of the ocellus as well. It would be nice to see that transient loss of the ocelli GRN might lead to loss of ocelli in ant species that have them. These are very difficult things to achieve, as the key genes have earlier developmental roles, such that CRISPR knockouts would not be interpretable, and transient RNAi in the head capsules of developing pupal ants would be challenging.

Reviewer #1 (Public review):

Summary:

This manuscript identifies the orphan kinesin KIN-G as a substrate of Polo-like kinase (TbPLK) in Trypanosoma brucei and demonstrates that phosphorylation of Thr301 inhibits KIN-G microtubule binding and disrupts its cellular function. Using a combination of in vitro kinase assays, phosphosite mapping, microtubule binding and gliding assays, and in vivo complementation with phosphomimetic and phosphodeficient mutants, the authors link TbPLK-mediated regulation of KIN-G to defects in centrin arm integrity, FAZ elongation, Golgi organization, flagellum positioning, and division plane placement. The study provides a mechanistic advance in understanding how TbPLK regulates centrin arm biogenesis and integrates KIN-G into the growing regulatory network controlling hook complex and FAZ assembly. Overall, the work is technically strong, internally consistent, and builds logically on previous studies from this group and others.

Strengths:

A major strength of the manuscript is the clear mechanistic link between phosphoryltion of Thr301 and loss of microtubule binding activity. The use of phosphomimetic (T301D) and phosphodeficient (T301A) mutants in an RNAi-rescue framework provides a clean and convincing demonstration of functional relevance in vivo. The integration of biochemical assays with detailed cell biological phenotyping (centrin arm length, FAZ elongation, basal body segregation, and cytokinesis markers) is particularly effective and makes the central conclusion robust. The observed phenotypic cascade from centrin arm defects to FAZ and division plane abnormalities is also well aligned with existing models of trypanosome morphogenesis.

Weaknesses:

My (more or less main) concern relates to the interpretation of the Golgi phenotype. The conclusion that phosphorylation of KIN-G "impairs Golgi biogenesis" is currently based on fluorescence microscopy using TbGRASP and Sec13 markers and on quantification of the number and distribution of Golgi/ERES puncta in binucleated cells. While these data convincingly demonstrate altered Golgi/ERES number and spatial organization, they do not distinguish between true defects in Golgi biogenesis or duplication and alternative possibilities such as fragmentation, vesiculation, or mislocalization of Golgi membranes. Given the central role of Golgi-centrin arm organization in the proposed model, ultrastructural analysis (for example, by EM or electron tomography) would greatly strengthen this aspect of the study by providing direct evidence for structural alterations of the Golgi and its association with the centrin arm and ERES. Such data would elevate this part of the manuscript from a descriptive fluorescence phenotype to a true structural cell biological insight. I appreciate that this experiment goes beyond the current dataset, but it would substantially enhance the mechanistic depth of the Golgi-related conclusions and strengthen the causal chain linking centrin arm defects to Golgi abnormalities. However, I have to confess, the inclusion of such data would make this reviewer particularly enthusiastic about the work. If this is not feasible, I would recommend tempering the wording of "Golgi biogenesis" to a more conservative description, such as altered Golgi organization or duplication, and explicitly acknowledging the limitations of fluorescence-based analysis for this conclusion.

An additional conceptual point concerns the dual role of TbPLK in centrin arm regulation. TbPLK is known to promote centrin arm biogenesis through phosphorylation of TbCentrin2, yet in this study, TbPLK phosphorylation of KIN-G negatively regulates centrin arm assembly. This dual positive and negative regulatory role is intriguing but could be discussed more explicitly. The manuscript would benefit from a clearer conceptual framework addressing how phosphorylation of KIN-G might serve as a temporal or spatial switch to restrain KIN-G activity at specific stages of centrin arm assembly.

Finally, a schematic model summarizing the proposed regulatory pathway from TbPLK phosphorylation of KIN-G to centrin arm assembly, FAZ elongation, division plane placement, and Golgi organization would aid the reader.

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 a 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, as detailed below.

Weaknesses:

Overall, I find this work to be solid and to provide an important addition to our understanding of mechanisms controlling cell division in T. brucei. The biochemistry, in particular, is rigorous and convincingly demonstrates PLK can P-ate KIN-G, altering its MT-binding ability. Analysis of phospho-mutants of KIN-G in live T. brucei supports the conclusion that P-ation of KIN-G at T301 negatively affects KIN-G function in vivo. I think, however, that the results fall short of supporting the title, because, although the data convincingly show that PLK can phosphorylate KIN-G at T301 in vitro, and that T301 is P-ated in vivo, they do not formally demonstrate (nor even test) whether PLK is the kinase responsible for this phosphorylation in vivo (experiments to address this seem quite feasible). I also do not see where the authors try to reconcile the absence of phenotype for KIN-G-T301A with the implied importance of KIN-G phosphorylation by PLK in cell division, which calls into question the need for P-ation of KIN-G-T301 in cell division. Suggestions for addressing these concerns are provided below.

My two main questions are:

(1) What is the biological relevance of KIN-G P-ation at T301?

a) The authors report no defect for the KIN-G-T301A mutant, so what then is the need for T301 P-ation, if the cell gets along fine without it? One step toward addressing this would be to ask what fraction of KIN-G shows P-ation at T301. Although published studies indicate P-ation at T301, it isn't known what percentage of KIN-G in the cell is P-ated. One might anticipate, for example, that T301-P is a small minority of the population in asynchronous cultures and that T301 P-ation increases at specific cell cycle stages.

b) Published work links PLK to cell division, FAZ elongation, etc... The current work suggests that one role of PLK is to P-ate KIN-G at T301. In contrast, however, the current work also indicates that P-ation of KIN-G at T301 is unnecessary for normal cell division, FAZ elongation, etc....

c) Some experiments or at least commentary on points a and b above would strengthen the paper.

(2) Is PLK the kinase that P-ates Kin-G T301 in vivo?

a) The authors show PLK P-ates T301 (and other residues) in vitro, and that T-301 is P-ated in vivo. To bring the analysis full circle, it would be informative to examine KIN-G P-ation in a PLK mutant or upon inhibition of PLK with published inhibitors. This seems to be a very doable experiment with the tools available.

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. Using immunofluorescence-based imaging approaches, they also show that TbPLK colocalizes with KIN-G at centrin arms during the early S-phase of the cell cycle. Centrin 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 immunofluorescence 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.

Weaknesses:

Some of the broader conclusions are not directly supported by the data. For example, the title states "Polo-like kinase phosphorylation of the orphan kinesin KIN-G negatively regulates centrin arm biogenesis in Trypanosoma brucei," but the data do not directly address the specific role of TbPLK in phosphorylating KIN-G in cells. Moreover, some of the more specific conclusions in the paper, for example, that "phosphorylation of KIN-G" causes various cellular defects, are a bit of an overstatement. The supporting data rely on the expression of a phospho-mimetic mutant of KIN-G. Presumably, phosphorylation in cells is a normal part of KIN-G regulation, and it is not just phosphorylation, but rather hyperphosphorylation that is being mimicked by the mutant. Some rewording of the specific conclusions is warranted, and the broader conclusion would be better supported with additional experimental evidence.

Reviewer #1 (Public review):

Summary:

Severe childhood malaria is associated with three main overlapping syndromes: impaired consciousness (IC), respiratory distress (RD), and severe malaria anaemia (SMA). One central feature of severe malaria, driven by host and parasite factors, is the sequestration of parasitized red blood cells in vascular beds, leading to impaired tissue perfusion and lactic acidosis. The causing agent, the parasite ligand PfEMP1, is expressed on the surface of infected red blood cells, where it binds to a broad range of different endothelial receptors. Accumulation of parasite-infected erythrocytes in the host's microvasculature has been repeatedly confirmed for cerebral malaria, but there are scarce data on the extent of sequestration in the other severe malaria syndromes. However, the absence of effective adjunctive therapies for severe malaria implies that our understanding of its pathogenesis remains incomplete. Thus, by comparing var gene expression from a large Kenyan cohort (n=372 severe cases; n=340 non-severe cases), this study addresses a critical knowledge gap regarding the role of PfEMP1 across distinct severe malaria syndromes. The substantial sample size, phenotypic stratification, and use of two complementary methods (DBLa-tag sequencing and RT-qPCR), along with data about the parasite's ability to form rosettes and antibody level assessments, provide a strong setup. Var gene expression data - either proportions of different DBLa-tags classified by the number of cysteine residues and presence of particular motifs or relative expression RT-qPCR data from a set of primer pairs targeting conserved regions of var groups or particular domains - is associated with (a) severe malaria syndromes, (b) variant expression homogeneity, (c) rosetting ability, and (d) mortality using independent linear regression models, spearman ranks correlations, or logistic regression models. In summary, the study confirms that A-type and DC8-containing gene expression correlate with IC, that RD is associated with rosetting, and that SMA is linked to a high variant expression homogeneity (VEH) of var-A expression, which may indicate a longer infection duration. However, some findings remain inconclusive. For example, when analyzing pure syndromes, several associations changed: DC8 expression was also found to be significantly enriched in SMA (with multiple primer pairs) and RD, not exclusively with IC. Additionally, rosetting was associated with DC8 expression but not with IC, even though IC itself is linked to DC8 expression. Overall, the findings are significant and supported by a large dataset, though the reported evidence remains largely associative rather than mechanistic.

Strengths:

As the authors stated themselves, one of the key unresolved questions is whether severity-causing parasites are biologically different from parasites responsible for asymptomatic infections. This study is among the first to address this question using data from a large, phenotypically stratified cohort. The use of two complementary methods (DBLa-tag sequencing and RT-qPCR), together with data on the parasites' ability to form rosettes and assessments of antibody levels, provides an excellent experimental framework.

Weaknesses:

Even when assessing var gene expression using two different approaches - DBLα-tag sequencing and RT-qPCR targeting pre-defined variants - only a glimpse of the parasites' actual biology is captured. Moreover, a well-known confounder in gene expression studies of P. falciparum field isolates is variation in parasite age (hours post-invasion) or synchronicity, both of which significantly influence var gene expression. The methods employed in this study, unfortunately, do not allow for controlling or correcting for these factors. Then, the old classification system of DBLa-tag data developed by Bull et al is certainly still valid; however, more recent advances in bioinformatic tool development now allow for a more in-depth exploration of DBLa-tag datasets. Tools such as Varia (doi: 10.1186/s12859-022-04573-6), cUPS (https://doi.org/10.1371/journal.ppat.1012813), and upsML (doi: https://doi.org/10.1101/2025.05.19.654848) enable the prediction of DBLa-tag-connected PfEMP1 domains and the var group affiliations.

As A-type var gene expression has already been associated with severity, most expression studies (including this one) have a selection bias towards A- and B/A-type var genes. Here, A- and B/A-types are covered by 8 primer pairs (gpA1, gpA2, 4x DC8, DC13, DC4), whereas high polymorphic B-types are targeted by only 2 primer pairs (b1, DC9) and C-types only by a single primer (c2). Thus, any association with A-type expression is more likely to be observed, although evidence is accumulating that parasites are preferably expressing B-type var genes at the onset of blood stage infection in naïve/less immune individuals; this is also consistent with the observation of the authors that VEH is positively associated with immunity (measured as anti-IE) and negatively associated with temperature.<br /> I am not an expert in biostatistics, but to my understanding, independently performed regressions should be corrected for multiple testing.

Overall, the authors largely achieved their aims, identifying specific var groups associated with different severity syndromes. However, due to the complexity of var gene data and the interdependence of parameters, the resulting picture is not entirely clear. Some opposite results between different analyses may also be difficult for the reader to interpret. Nevertheless, this study can be considered a pioneering effort, providing valuable insights into the complex interplay of var gene expression across different severity syndromes and offering useful data for the field. Follow-up studies will be important to validate these findings and further dissect the mechanisms linking parasites gene expression to clinical outcomes.

Reviewer #2 (Public review):

Summary:

The manuscript presents results of a study using two complementary approaches (RT-qPCR and DBL) to analyze the putative relationship between var gene transcription (and hence, PfEMP1 expression) and clinical presentation among Kenyan children with Plasmodium falciparum malaria. Binary rosetting (yes/no) data are used in a similar way. The study includes samples collected over a period of almost 20 years from about 700 children presenting with either severe (impaired consciousness [IC], respiratory distress [RD], severe anemia [SA]) or non-severe malaria. During the study period, the study area experienced a remarkable drop in P. falciparum transmission intensity.

Strengths:

The study stands on the shoulders of many similar studies of this kind, both by the authors and by other research teams, and the inferences made largely confirm those made previously. The current study has analytical rigor and a large sample size. Disentangling the multiple parameters of the above-mentioned relationship is of obvious and crucial importance to an improved understanding of P. falciparum malaria pathogenesis and of the targets and mechanisms of protective immunity to the disease. The present study is a valuable effort towards that. The study is well-structured, and the figures are clear.

Weaknesses:

It is somewhat unclear to this reviewer to what extent the samples and data analyzed and reported here are new (i.e., not used/analyzed in previous studies). If there is substantial overlap with earlier studies, this is a weakness because of the risk of circular inferences. The Discussion section would benefit from less repetition of the results section and a more in-depth discussion of the findings obtained relative to the existing literature. Better inclusion of key primary references is recommended.

Reviewer #3 (Public review):

Summary:

In this manuscript, Ndugwa et al. attempt to link specific severe malaria manifestations with particular var gene expression patterns. This is an important question, and the dataset the authors have assembled over decades is impressive. However, greater clarity in the descriptions and statistics would, in my view, help this reviewers, and readers in general develop a more precise understanding of the significance of the findings.

Strengths:

The study addresses a critically important question in malaria pathogenesis, and the dataset is extensive and represents a significant long-term effort by the authors.

Weaknesses:

The Results section often lacks clarity: clinical group definitions (NS, non-IC, non-SMA, mild vs. moderate) are sometimes ambiguous, and key methodological details, including the VEH index calculation, RT-qPCR quantification, antibody detection methods, and rosetting assays, are either missing from the results text or poorly explained in the figure legends. Additionally, figure presentation requires improvement, with inconsistent reporting of sample sizes, undefined colors, and p-values that overlap with data points rather than being clearly displayed above them.

Reviewer #1 (Public review):

Summary:

The authors aimed to overcome the limitations of whole-tumor-cell vaccines, specifically the weak immunogenicity and rapid clearance often associated with them. They leveraged the unique properties of senescent tumor cells (STCs), which remain metabolically active and secrete chemokines, as a source of antigens. However, to counteract the secretion of the immunosuppressive lipid prostaglandin E2 (PGE2), which is part of the senescence-associated secretory phenotype (SASP), they engineered a hydrogel vaccine formulation (STCs+CLX-Lipo@Gel) containing STCs and liposomal celecoxib (a COX2 inhibitor).

Strengths:

(1) The study is conceptually strong in its approach to leveraging the SASP to improve immunotherapy responses. By selectively inhibiting COX2/PGE2 while preserving the secretion of recruitment chemokines (like CCL2 and CCL5) in the SASP, the authors successfully turn a potentially deleterious cellular state into a therapeutic asset.

(2) Mechanistic Insight: The manuscript provides detailed evidence regarding the mechanism of action. The authors convincingly show that the vaccine restores activity in the NK-DC axis. Specifically, they demonstrate that reducing PGE2 levels enhances NK cell activation (upregulation of NKG2D and NKp46) and promotes the secretion of CCL5 and XCL1 by NK cells, which subsequently recruits cDC1 dendritic cells.

(3) The therapeutic potential is tested across multiple models, including a subcutaneous melanoma model, a difficult-to-treat melanoma brain metastasis model, and an orthotopic pancreatic cancer model. The consistent efficacy across these distinct physiological contexts suggests broad applicability.

Weaknesses:

(1) While the authors successfully inhibit PGE2, the SASP is a complex cocktail of factors. The discussion regarding the long-term presence of these "live" senescent cells is somewhat limited. Although the hydrogel retains cells locally, the potential for other chronic inflammatory factors to eventually promote tumorigenesis or tissue damage in the surrounding niche warrants careful consideration when translating this approach to patients and may require additional preclinical testing.

(2) The study posits that STCs serve as an antigen reservoir. However, the manuscript would benefit from a clearer distinction between whether the immune system is recognizing senescence-specific neoantigens or simply shared tumor antigens that are being presented more effectively due to the adjuvant effect. The authors briefly touch upon neoantigens in the discussion, but the experimental data primarily measure general anti-tumor responses.

Impact:

This work bridges material science and immunology, offering a practical solution to the immunosuppressive barriers of cell-based vaccines. It provides a platform that could potentially be adapted for various solid tumors.

Reviewer #2 (Public review):

Summary:

Wang et al. examined an engineered whole-tumor-cell vaccine based on senescent tumor cells co-encapsulated with liposomal celecoxib in a chitosan hydrogel. The authors propose that prolonged persistence of senescent cells, combined with COX2/PGE2 inhibition, restores NK-DC crosstalk, enhances cDC1 recruitment, and ultimately drives robust CD8⁺ T-cell-mediated antitumor immunity. The study is nicely executed and clearly presented, with extensive in vitro and in vivo validation across multiple tumor models, including melanoma brain metastases and orthotopic PDAC. While the overall concept is timely and of potential interest, several mechanistic conclusions are based primarily on correlative evidence and would benefit from additional functional experiments to strengthen causal interpretation and translational relevance.

Strengths:

(1) Strong conceptual framework

(2) Impressive breadth of in vivo models.

(3) Clear immunological readouts.

(4) Innovative combination of senescence biology and biomaterials.

Weaknesses:

(1) Mechanistic conclusions rely heavily on correlation.

(2) Lack of functional immune cell depletion studies.

(3) Limited exploration of long-term safety and antigenic specificity.

Major Critiques:

(1) The authors emphasize the expansion and activation of cDC1 as a key mechanism linking innate and adaptive immunity, yet it does not directly test whether cDC1 is required for the observed CD8⁺ T-cell responses and tumor control.

The authors should perform experiments using Batf3-deficient mice or any other cDC1-depletion strategies to provide important mechanistic validation. If such experiments are not feasible, this limitation should be more clearly acknowledged and discussed.

(2) The authors note that senescence may generate neoantigens distinct from those present in proliferating tumor cells, but the extent to which STC-induced immunity cross-reacts with non-senescent tumor cells is not fully addressed. While it is appreciated that tumor challenge experiments are included, the author should perform a more explicit analysis of antigenic overlap that would strengthen the translational relevance of the approach. For example, they can compare senescence induced by different stimuli or directly assess immune recognition of non-senescent tumor targets, which would help clarify whether the vaccine primarily exploits senescence-specific antigens or broadly shared tumor antigens.

(3) Hydrogel encapsulation clearly extends STC persistence in vivo; however, the study provides limited information on the eventual clearance of these cells and the potential implications of prolonged SASP exposure. Given general concerns regarding chronic inflammation associated with senescent cells, additional discussion of long-term local and systemic responses would be helpful. If extended safety analyses are beyond the scope of the current study, the authors should acknowledge the limitation.

(4) The immunological effects are attributed to COX2/PGE2 inhibition, but it remains unclear whether these effects are specific to celecoxib or could reflect formulation-dependent or off-target mechanisms. The authors may perform additional experiments employing an alternative COX2 inhibitor, genetic COX2 suppression, or PGE2 rescue, which could further support the specificity of the COX2/PGE2-dependent mechanism.

Reviewer #1 (Public review):

Summary:

In the work from Qiu et al. a workflow aimed at obtaining the stabilization of a simple small protein against mechanical and chemical stressors is presented.

Strengths:

The workflow makes use of state-of-the-art AI-driven structure generation and couples it with more classical computational and experimental characterizations in order to measure its efficacy.

The work is well presented and results are thorough and convincing.

The Methods description is quite precise, and some important details were added during review.

Weaknesses:

The pulling velocity is quite high but in accordance with this observation the results were only used for comparative analyses.

Following the review process the authors have shown that the minimum distance between each protein from its periodic images was consistently above 1 nm, yet towards the end of some simulations the value crosses the non-bonded interaction cut-off distance.

Comments on revisions:

The authors did a good job in addressing the reviews.

Reviewer #2 (Public review):

Summary:

Qiu, Jun et. al., developed and validated a computational pipeline aimed at stabilizing α-helical bundles into very stable folds. The computational pipeline is a hierarchical computational methodology tasked to generate and filter a pool of candidates, ultimately producing a manageable number of high-confidence candidates for experimental evaluation. The pipeline is split into two stages. In stage I, a large pool of candidate designs is generated by RFdiffusion and ProteinMPNN, filtered down by a series of filters (hydropathy score, foldability assessed by ESMFold and AlphaFold). The final set is chosen by running a series of steered MD simulations. This stage reached unfolding forces above 100pN. In stage II, targeted tweaks are introduced - such as salt bridges and metal ion coordination - to further enhance the stability of the α-helical bundle. The constructs undergo validation through a series of biophysical experiments. Thermal stability is assessed by CD, chemical stability by chemical denaturation, and mechanical stability by AFM.

Strengths:

A hierarchical computational approach that begins with high-throughput generation of candidates, followed by a series of filters based on specific goal-oriented constraints, is a powerful approach for a rapid exploration of the sequence space. This type of approach breaks down the multi-objective optimization into manageable chunks and has been successfully applied for protein design purposes (e.g., the design of protein binders). Here, the authors nicely demonstrate how this design strategy can be applied to successfully redesign a moderately stable α-helical bundle into an ultrastable fold. This approach is highly modular, allowing the filtering methods to be easily swapped based on the specific optimization goals or the desired level of filtering.

Weaknesses:

Assessing the change in stability relative to the WT α-helical bundle is challenging because an additional helix has been introduced, resulting in a comparison between a three-helix bundle and a four-helix bundle. Consequently, the appropriate reference point for comparison is unclear. A more direct and informative approach would have been to redesign the sequence of the original α-helical bundle of the human spectrin repeat R15, allowing for a more straightforward stability comparison.

The three constructs chosen are 60-70% identical to each other, either suggesting over-constrained optimization of the sequence, or a physical constraint inherent to designing ultrastable α-helical bundles. It would be interesting to explore whether choosing a different combination of filters would enable ultrastable α-helical bundles constructs with a more varied sequence content.

While the use of steered MD is an elegant approach to picking the top N most stable designs, its computational cost may become prohibitive as the number of designs increases or as the protein size grows, especially since it requires simulating a water box that can accommodate a fully denatured protein.

Comments on revisions:

The authors have done a good job of addressing the comments.

Reviewer #3 (Public review):

Summary:

Qiu et al., present a hierarchical framework that combine AI and molecular dynamic simulation to design α-helical protein with enhanced thermal, chemical and mechanical stability. Strategically chemical modification by incorporating additional α-helix, site-specific salt bridges and metal coordination further enhanced the stability. The experimental validation using single-molecule force spectroscopy and CD melting measurements provide fundamental physical chemical insights into the stabilization of α-helices. Together with the group's prior work on super-stable β strands (https://www.nature.com/articles/s41557-025-01998-3), this research provides a comprehensive toolkit for protein stabilization. This framework has broad implications for designing stable proteins capable of functioning under extreme conditions.

Strengths:

The study represents a complete frame work for stabilizing the fundamental protein elements, α-helices. A key strength of this work is the integration of AI tools with chemical knowledge of protein stability.<br /> The experimental validation in this study is exceptional. The single-molecule AFM analysis provided a high-resolution look at the energy landscape of these designed scaffolds. This approach allows for the direct observation of mechanical unfolding forces (exceeding 200 pN) and the precise contribution of individual chemical modifications to global stability. These measurements offer new, fundamental insights into the physicochemical principles that govern α-helix stabilization.

Weaknesses:

(1) While the initial manuscript lacked a detailed explanation for the stabilizing effect of the additional helix, the revised version now includes a clear structural basis for this improvement. The authors successfully attribute the increased unfolding force threshold to the reinforcement of the hydrophobic core and enhanced cooperative interactions, supported by relevant literature correlations between helix bundle size and stability.

(2) The author analyzed both thermal stability and mechanical stability. It would be helpful for the author to discuss the relationship between these two parameters in the context of their design. Since thermal melting probes equilibrium stability (ΔG), while mechanical stability probes the unfolding energy barriers along pulling coordinate. While the integrative design approach successfully improved both stability types, a deeper exploration of how the specific structural modifications influence the unfolding energy barrier relative to the overall equilibrium stability would further strengthen the mechanistic impact of the work.

(3) While the current study demonstrates a dramatic increase in global stability, the analysis focuses almost exclusively on the unfolding (melting) process. However, thermodynamic stability is a function of both folding (kf) and unfolding (ku) rates. The author have clarified that the observed ultrastability likely originates from a significantly reduced unfolding rates, a hypothesis consistent with the unfolding force. Direct measurements of the kinetics would provide deeper insights.

(4) The authors chose the spectrin repeat R15 as the starting scaffold for their design. R15 is a well-established model known for its "ultra-fast" folding kinetics, with folding rates (kf ~105s), near three orders of magnitude faster than its homologues like R17 (Scott et.al., Journal of molecular biology 344.1 (2004): 195-205). Measuring the folding rates of newly designed proteins would provide additional insights into the design.

Comments on revisions:

I think the author have addressed comments.

Reviewer #1 (Public review):

Summary:

The authors present a novel investigation of movement vigor of individuals completing a synchronous extension-flexion task. Participants were placed into groups of two (so-called "dyads") and asked to complete shared movements (connected via a virtual loaded spring) to targets placed at varying amplitudes. The authors attempted to quantify what, if any, adjustments in movement vigor individual participants made during the dyadic movements, given the combined or co-dependent nature of the task. This is a novel, timely question of interest within the broader field of human sensorimotor control.

Participants from each dyad were labeled as "slow" (low vigor) or "fast" (high vigor), and their respective contributions to the combined movement metrics assessed. The authors presented four candidate models for dyad interactions: (a) independent motor plans (i.e., co-activity hypothesis), (b) individual-led motor plans (i.e., leader-follower hypothesis), (c) generalization to a weighted average motor plan (i.e., weighted adaptation hypothesis), and (d) an uncertainty-based model of dynamic partner-partner interaction (i.e., interactive adaptation hypothesis). The final model allowed for dynamic changes in individual motor plans (and therefore, movement vigor) based on partner-partner interactions and observations. After detailed observations of interaction torque and movement duration (or, vigor), the authors concluded that the interactive adaptation model provided the best explanation of human-human interaction during self-paced dyadic movements.

Strengths:

The experimental setup (simultaneous wrist extension-flexion movements) has been thoroughly vetted. The task was designed particularly well, with adequate block pseudo-randomization to ensure general validity of the results. The analyses of torque interaction, movement kinematics, and vigor are sound, as are the statistical measures used to assess significance. The authors structured the work via a helpful comparison of several candidate models of human-human interaction dynamics, and how well said models explained variance in the vigor of solo and combined movements.

The authors adequately addressed several concerns that I raised in my initial review of the work, including clarity regarding analyses of movement vigor and inclusion of additional analyses of reaction time. The results are supported by both parametric and non-parametric statistical methods.

The research question is timely and extends current neuroscientific understanding of sensorimotor control, particularly in social contexts. This work answers several new, important questions about control of vigor during volitional movements, and in doing so it motivates future research into the topic.

Weaknesses:

My chief concern about the study is the relatively low number of dyad data points (n=10). The authors recruited 20 participants, but the primary conclusions are based on dyad-specific interactions (i.e., analyses of "fast" vs "slow" participants in each pair). However, it is important to note that most of the effects upon which the conclusions rest are associated with relatively large effect sizes.

Reviewer #2 (Public review):

Summary:

This study examines how individual movement vigor is integrated into a shared, dyadic vigor when two individuals are physically coupled. Participants performed wrist-reaching movements toward targets at different distances while mechanically linked via a virtual elastic band, and dyads were formed by pairing participants with different baseline vigor profiles. Under interaction conditions, movements converged to coordinated patterns that could not be explained by simple averaging, indicating that each dyad behaved as a single functional unit. Notably, under coupling, movement durations for both partners were shorter than in the solo condition, arguing against the view that each individual simply executed an independent movement plan. Furthermore, dyadic vigor was primarily predicted by the slower partner's vigor rather than by the faster partner's, suggesting that neither a leader-follower strategy nor a weighted averaging account fully explains the observed behavior. The authors propose a computational model in which both partners adapt to the emerging interaction dynamics ("interactive adaptation strategy"), providing a coherent explanation of the behavioral observations.

Strengths:

The study is carefully designed and addresses an important question about how individual movement vigor is integrated during joint action. The experimental paradigm allows systematic manipulation of interaction strength and partner asymmetry. The behavioral results show clear and robust patterns, particularly the shortening of movement durations under elastic coupling (KL and KH condition) and the asymmetrical contribution of the slower partner's vigor to dyadic vigor. The computational model captures the main behavioral patterns well and provides a principled framework for interpreting dyadic vigor not as a simple combination of two independent motor plans, but as an emergent property arising from mutual adaptation. Conceptually, the study is notable in extending the notion of vigor from an individual attribute to a dyad-level construct, opening a new perspective on coordinated movement and motor decision-making.

Weaknesses:

The revised manuscript now clearly explains why the proposed computational model successfully accounts for the observed dyadic behavior. In particular, the mechanisms by which uncertainty associated with the slower partner and time-related costs of the faster partner jointly shape dyadic vigor are now clear. I have no further comments to add.

Reviewer #3 (Public review):

Summary:

This study provides novel insights into how individuals regulate the speed of their movements both alone and in pairs, highlighting consistent differences in movement vigor across people and showing that these differences can adapt in dyadic contexts. The findings are significant because they reveal stable individual patterns of action that are flexible when interacting with others, and they suggest that multiple factors, beyond reward sensitivity, may contribute to these idiosyncrasies. The evidence is generally strong, supported by careful behavioral measurements and appropriate modeling.

The authors have addressed all of my previous comments. I appreciate the clarification of abbreviations, terminology, and key concepts, the expansion of the discussion, and the adjustments to some of the statistical analyses in response to both my earlier comments and those of Reviewer 1.

Reviewer #1 (Public review):

Summary:

The authors aimed to extend a prior fiber photometry analysis process they developed by incorporating the new ability to determine instantaneous, within trial, relationships between the photometry signal and continuously changing variables. They present solid evidence via simulations and example use cases from published datasets highlighting that their approach can capture instantaneous relationships. Overall, while they make a compelling case that this approach is less biased and more insightful, the implementation for many experimentalists remains challenging enough and may limit widespread adoption by the community.

Strengths:

This work builds on prior efforts to analyze photometry signals in a less biased and more statistically sound way. This work incorporates a very important aspect by avoiding the need to summarize individual trials with singular behavioral variables and instead allows for interactions with continuously changing variables to be investigated. The knowledge and expertise of the authors and the presentation provide strong validity and strength to the work. Examples from prior studies in the field are a necessary and important component of the work.

Weaknesses:

While use cases are provided from prior data, a clearer presentation of how common implementations in the field are performed (i.e. GLM) and how one could alternatively use the cFLMM approach would help. Otherwise, most may continue using common approaches of Pearson's correlations and GLMs.

Reviewer #2 (Public review):

The paper presents a regression-based approach for analysing fiber photometry data termed Concurrent Functional Mixed Models (cFLMMs). The approach works by fitting linear mixed effect models separately to each time point in trial aligned data, then applying smoothing to the model coefficients (betas), and computing confidence intervals. The method extends the authors previous work on using FLMMs for photometry data analysis by allowing for the inclusion of predictors whose value changes across timepoints within a trial, rather than just from trial to trial. As fiber photometry is a rapidly expanding field, developing principled methods to analyse photometry data is valuable, particularly as the authors have released an R package that implements their method to facilitate their use by other groups. The basic FLMM approach for using mixed effects models to analyse trial aligned photometry data, detailed by the authors in their previous manuscript (Loewinger et al. 2025, doi: 10.7554/eLife.95802) appears valuable. The aim of incorporating variables that change within trial into this framework is interesting, and the technical implementation appears to be rigorous. However, I have some reservations as to whether the way in which variables that change within trial have been integrated into the analysis framework is likely to be widely useful, and hence how impactful the additional functionality of cFLMM relative to the previously published FLMM will be.

In the original FLMM approach, where predictors change only from trial-to-trial, fitting separate regressions at each timepoint generates a timeseries of betas is for each predictor, indicating when and how the predictor explained variance across the trial. This makes a lot of sense and is widely used in neuroscience data analysis. In extending this approach to incorporate variables that change within trial, the authors have used the same method of fitting separate regression models at each timepoint, to obtain a timeseries of betas for each predictor. It is less clear that this approach makes sense for variables that change within trial. This is because the resulting betas only capture how variation in the predictor across trials at a given timepoint explains variance in the signal, but does not capture effects of variation in the predictor across timepoints within trials. This partitioning of variance in the predictor into a between-trial component whose effect on the signal is modelled, and a within-trial component whose effect on the signal is not, is artificial in many experiment designs, and may yield hard to interpret results.

Consider e.g. the experimental condition considered in Figure 3, taken from Machen et al. 2025 (doi: 10.1101/2025.03.10.642469) in which mice ran down a linear track to collect rewards. In analysing such data, one might want to know how neural activity covaried with the animal's position, but as this variable changes strongly within trial but will have a similar time-course across trials, the cFLMM analysis approach will not work to quantify these effects. This is because variance attributed to position would not capture how neural activity covaried with changes in the animals position within trial, but rather how neural activity covaried with changes in the animals position from trial-to-trial at a given timepoint, which could occur due to e.g. trial-to-trial differences in latency to start moving or running speed. As such, although significant effects of 'position' might be observed, they would not capture covariation between position and neural activity in a straightforwardly interpretable way.

It is therefore not obvious to me that incorporating variables that change within trial into an analysis framework that runs separate regressions at each timepoint in trial aligned data is likely to be widely useful. If scientific questions require understanding how neural activity covaries as a function of variables that change both within and across trials, an alternative approach would be to run a single regression analysis across all timepoints, and capture the extended temporal responses to discrete behavioural events by using temporal basis functions convolved with the event timeseries. This provides a very flexible framework for capturing covariation of neural activity both with variables that change continuously such as position, and discrete behavioural events such as choices or outcomes, while also handling variable event timing from trial-to-trial.

One way that cFLMM is used in the manuscript is to handle variable timing of trial events in trial aligned data. In the Machen et al. data, the time when the animal reaches the reward varies from trial to trial, and this is represented in the cFLMM analysis by a binary variable which changes value at this timepoint. From the resulting beta coefficient timeseries (Figure 3C) it is not straightforward to understand how neural activity changed as the subject approached and then received the reward. A simpler approach to quantify this, which I think would have yielded more interpretable coefficient timeseries would have been to align activity across trials on when the subject obtained the reward, rather than on the start of the trial, allowing e.g. the effect of reward type to be visualised as a function of time relative to reward delivery, and hence to see the differential effects during approach vs consumption. More broadly, handling variable trial timing in analyses like FLMM which use trial aligned data, can be achieved either by separately aligning the data to different trial events of interest or by time warping the signal to align multiple important timepoints across trials. It is not obvious that using cFLMM with binary indicator variables that indicate when task states changed will yield a clearer picture of neural activity than these methods.

It may be that I am missing some key strengths of cFLMM relative to the other approaches I have outlined, or that there are applications where this approach to implementing within-trial variable changes is a natural formalism. However my impression is that while cFLMM represent a technical advance, it is not clear how widely useful the model formalism will be.

Reviewer #3 (Public review):

Summary:

This work is an extension of their previous study (Loewinger et al 2025) describing a statistical framework for the analysis of photometry data using functional linear mixed models with joint confidence intervals, together with an open-source tool implemented in R. The present study extends it by adding the possibility of using 'concurrent' variables (variables that change within a trial) as regressors, for example, capturing the change of speed at each timepoint in the trial. The main claim is that using 'concurrent' regressors can identify associations between signal and behavior that could not be captured by 'non-concurrent' regressors (the value for a regressor on a specific trial is the same for each timepoint), which could lead to misleading conclusions. While the motivation for using time-varying covariates is useful and supported by previous literature (using fixed-effects models, although not cited in this manuscript), the reanalysis of previous studies does not clearly prove the benefit of using concurrent regressors as opposed to non-concurrent, and some of the results are difficult to interpret.

Strengths:

• The motivation for using time-varying covariates is well supported by previous literature using them on fixed-effects models, and here the authors are extending it to mixed-effects models.<br /> • The authors have included this new functionality in their previous open-source R package.

Weaknesses:

• The main weakness of this study is that it is not clear what the conceptual or methodological advance of this work is. As it is written, the manuscript focuses on showing how concurrent regressors offer interpretation advantages over non-concurrent regressors. While the benefit of such time-varying regressors is supported by previous literature (e.g., Engelhard et al., 2020), it is not clear whether the examples provided in the current study clearly support the advantage of one over the other, especially in the reanalysis of Machen et al. (2025), where the choice of regressors is confusing. In this specific example, if the question is about speed and reward type, why variables such as latency to reward or a binary 'reward zone vs corridor' (RZ) regressors are used instead of concurrent velocity (or peak velocity - in the case of the non-concurrent model)? Furthermore, if timing from trial start to reward collection is variable, why not align to reward collection, which would help in the interpretation of the signal and comparison between methods? Furthermore, while for the non-concurrent method, the regressors' coefficients are shown, for the concurrent one, what seems to be plotted are contrasts rather than the coefficients. The authors further acknowledge the interpretational difficulties of their analysis.<br /> • Because the relation between behavioral variables and neuronal signal is not instantaneous, previous literature using fixed effects uses, for example, different temporal lags, splines, and convolutional kernels; however, these are not discussed in the manuscript.<br /> • From the methods, it seems that in the concurrent version of fastFMM, both concurrent and non-concurrent regressors can be included, but this is not discussed in the manuscript.<br /> • The methodological advance is not clearly stated, apart from inputting into fastFMM a 3D matrix of regressors x trial x timepoint, instead of a 2D matrix of regressors x trial.<br /> • This manuscript is neither a clear demonstration of the need for concurrent variables, nor a 'tutorial' of how to use fastFMM with the added extension.

Reviewer #1 (Public review):

This study examines how two types of RNA polymerases organize themselves within the nucleus of C. elegans cells, building directly on the same group's prior publication and largely functioning as a companion to that earlier work. While the observation that the two polymerases occupy distinct but neighboring locations at the same genomic region adds nuance to our understanding of gene cluster regulation, the manuscript would benefit from more clearly delineating which findings are new versus continuations of previously published work. Protein localization, gene expression effects, and genomic mapping data appear to overlap substantially with the earlier paper.

The condensate claims would also benefit from additional experimental support. Demonstrating fusion events and concentration-dependent assembly are now standard expectations in the field. Additionally, one measurement reported appears inconsistent with a condensate model, warranting further discussion.

Some findings would benefit from more interpretive context. Why does polymerase clustering fluctuate with the cell cycle? What are the functional implications of ATTF-6 being required for one polymerase's foci but not the others?

The elevated-temperature experiments are intriguing but difficult to interpret, as the temperature used is well-established as a broad stress trigger in this organism. Acknowledging this and considering additional controls would help clarify whether the observed effects are specific to foci behavior.

Finally, the manuscript would be strengthened by adding quantification to some figures and revising the model diagram to better reflect what the current data support.

Reviewer #2 (Public review):

Summary:

The researchers analyzed GFP-tagged RNA Pol II and RNA Pol III catalytic subunits RPB-1 and RPC-1, and showed that they form foci in early embryo nuclei that overlap with the 5S rDNA loci and foci by ATTF-6-RFP. They showed foci are round, dissolve upon hexanediol incubation, and are detected during S phase, removed during, and re-established after mitosis. The researchers performed FRAP and showed fast exchange of polymerases, unlike ATTF-6. They show that, unlike RNA Pol III, RNA Pol II foci are dependent on ATTF-6 and temperature sensitive. The researchers propose that the two polymerases form distinct foci with different biochemical dependencies. This study shows that, although closely located within a gene cluster, the regulation of RNA Pol II and RNA Pol III is independent.

Strengths:

The researchers provide high-quality images that support the main results. The researchers' use of auxin-inducible and RNAi depletion work is validated in the same embryos by fluorescent analysis of the target protein.

Weaknesses:

Although the researchers propose the hypothesis that the RNA Pol II and RNA Pol III form distinct condensates, alternative hypotheses are not presented, and the criteria by which the other possibilities are ruled out are not discussed.

Reviewer #3 (Public review):

Wang et al demonstrate that RNA polymerase II and RNA polymerase III form distinct nuclear foci at the 5S rDNA-SL1 gene cluster in C. elegans. By ChIP, Pol II is highly enriched at the SL1 gene, whereas Pol III is enriched at the 5S rRNA gene. Both polymerase foci are spherical, show rapid exchange in FRAP experiments, and assemble in a cell-cycle-dependent manner, predominantly during S phase. The transcription factors ATTF-6 and SNPC-4 are required for the formation of Pol II foci but are dispensable for Pol III foci. Pol II foci, but not Pol III foci, are temperature-sensitive and dissolve upon heat stress; dissolution correlates with a strong reduction of SL1 transcription, whereas 5S rRNA levels remain largely unaffected.

Overall, this is a clean, well-organized, and well-controlled study, and I only have two comments.

(1) Roundness measurements, FRAP, and sensitivity to 1,6-hexanediol are indicative but not sufficient to show that these foci are condensates. They could, for example, also be scaffolded /chromatin-anchored assemblies (see https://pubmed.ncbi.nlm.nih.gov/36526633/). Please either provide better evidence or rephrase/tone down the condensate statements.

(2) Image quantification is only provided for Figure 5, but should also be reported for Figures 6 and 7. In addition to the foci number, also, e.g., intensity over background (similar to partition coefficient) should be quantified.

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 a broad impact by linking lysosomal integrity to ferroptosis and iron homeostasis, both of which are relevant to cancer biology and therapeutic targeting.

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.

Areas for improvement:

While the study is strong, several issues should be addressed for mechanistic depth and general relevance.

(1) Although NINJ2 is shown to interact with LAMP1 and LAMP1 knockdown rescues ferritin levels, it remains unclear whether the NINJ2-LAMP1 interaction is required for lysosomal protection. The authors could:<br /> a) Map the NINJ2 domain required for LAMP1 interaction and test whether an interaction-deficient mutant fails to protect against LMP and ferroptosis.<br /> b) Rescue NINJ2 KO cells with wild-type versus mutant NINJ2 to establish causality.

(2) The conclusion that NINJ2 suppresses ferroptosis relies primarily on RSL3 and Erastin sensitivity. A direct assessment of ferroptosis would hence the study, such as:<br /> a) Include ferroptosis rescue experiments using ferrostatin 1 or liproxstatin 1.<br /> b) Assess lipid peroxidation directly (e.g., C11 BODIPY staining) to strengthen the ferroptosis claim.

(3) The manuscript discusses lysosomal ferritin degradation but does not directly examine NCOA4, a central mediator of ferritinophagy. It would be good to:<br /> a) Test whether NCOA4 knockdown rescues ferritin loss and ferroptosis sensitivity in NINJ2 KO cells.<br /> b) This would clarify whether NINJ2 acts upstream of canonical ferritinophagy pathways or via an alternative mechanism.

(4) The study is entirely cell-based, despite references to inflammatory and tumor phenotypes in Ninj2-deficient mice. While not strictly required, even limited in vivo validation (e.g., ferroptosis markers or iron accumulation in existing Ninj2 KO tissues) would substantially strengthen the manuscript.

(5) Finally, most imaging data (e.g., Galectin 3/LAMP1 colocalization, PLA signals) and immunoblot data are presented qualitatively. The authors should provide the qualifications of Western blots and other measurements.

Reviewer #1 (Public review):

Summary:

This study aims to test whether human mate choice is influenced by HLA similarity while accounting for genome-wide relatedness, using the Himba as an evolutionarily relevant small-scale society population, unique among most HLA-mate choice studies. By comparing self-chosen ("love") and arranged marriages and using NGS-based 8-locus HLA class I and II sequences and genome-wide SNP data, the authors ask whether partners who freely choose each other are more HLA-dissimilar than those paired through social arrangements or random pairs. They further extend their work by examining functional differences in peptide-binding divergence among pairs and predicted pathogen recognition in potential offspring.

Strengths:

This study has many strengths. The most obvious is their ability to test for HLA-based mate choice in the Himba, a non-European, non-admixed, small-scale society population, the type of population that has been missing, in my opinion, from the majority of HLA mate choice studies. While Hedrick and Black (1997) used a similarly evolutionarily relevant remote tribe of native South Americans, they only considered 2 class I loci (HLA-A and HLA-B) at the first typing field (serological allele group) and did not have data for genome-wide relatedness. The Himba are also unique among previously studied populations because they have both socially arranged and self-chosen partnerships, so the authors could test if freely-chosen partners had lower MHC-similarity than assigned or randomly chosen partners.

Another key strength of the study was the relatively large sample size (HLA allele calls from 366 individuals, 102 unrelated) and 219 individuals with HLA data, whole genome SNP data, and involved in a partnership.

The study was also unique among HLA-mate choice studies for comparing peptide binding region protein divergence (calculated as the Grantham distance between amino acid sequences) among partner types and randomly generated pairs. This was also the first time I have seen a study use peptide binding prediction analysis of relevant human pathogens for potential offspring among partners to test if there would be a pathogen-relevant fitness benefit of partner selection.

Weaknesses:

My main concerns relate to the reliance on imputed HLA haplotypes and on IBD-based metrics in a region of the genome where both approaches are known to be problematic.

First, several key results depend on HLA haplotypes inferred through imputation rather than directly observed sequence data. The authors trained HIBAG imputation models on Himba SNP data across the full 5 Mb HLA region using paired HLA allele calls from target capture sequencing (L251-253). However, the underlying SNP data were generated by mapping reads to a 1000 Genomes Yoruba reference, meaning that both SNP discovery and subsequent imputation depend on the haplotypes represented in that reference panel. As a result, the imputation framework is likely biased toward common haplotypes shared between the Himba and Yoruba populations, while rare or Himba-specific HLA alleles are less likely to be imputed accurately or at all. This limitation has been noted previously for HLA imputation, particularly for novel or low-frequency variants and for populations that are poorly represented in reference panels. While the authors compare (first-field) imputed alleles to sequenced alleles to assess imputation accuracy, this validation step itself may be biased toward the same common haplotypes that are easiest to impute. This becomes especially problematic if IBD is inferred using imputed haplotypes, because haplotype sharing would then primarily reflect common, reference-supported haplotypes, while true population-specific variation would be effectively invisible. In this scenario, downstream estimates of IBD sharing may be inflated for common haplotypes and deflated for rare ones, potentially biasing conclusions about haplotype sharing, selection, and mate choice at the HLA region.

Second, the interpretation of excess identity-by-descent (IBD) sharing in the HLA region is difficult given the well-documented genomic properties of this locus. The classical HLA region is highly gene-dense, structurally complex, and characterized by extreme heterogeneity in recombination rates, with pronounced hot- and cold-spots (Miretti et al. 2005; de Bakker et al. 2006, reviewed in Radwan et al. 2020). Elevated IBD in such regions can arise from low recombination, background selection, or demographic processes such as bottlenecks, all of which can mimic signals of recent positive selection. While the authors suggest fluctuating or directional selection, extensive haplotype sharing is also consistent with long-term balancing selection at the MHC (Albrechtsen et al. 2010) or recent demographic history in this population.

Beyond these main issues, there are several additional concerns that affect interpretation. Sample sizes and partnership counts are sometimes unclear; some figures would benefit from clearer scaling (Figure 1) and annotation (Figures S6 and S7), and key methodological choices (e.g., treatment of DRB copy number variation, no recombination correction in IBD calling) require further explanation. Finally, some conclusions, particularly those invoking optimality or specific selective mechanisms, are not directly tested by the analyses presented and would benefit from more cautious framing.

Reviewer #2 (Public review):

Summary:

Evidence for the influence of MHC on mate choice in humans is challenging, as social structures and norms often confound the power of studying populations. This study uses an unusual, diverse, but relatively isolated population that allows a direct comparison of arranged and chosen partners to determine if MHC diversity is increased when choice drives mate choice. Overall, the authors use a range of genetic analyses to determine individual relationships alongside different measures of MHC diversity and potential selection pressures. The overall finding that there is no heterozygous dissimilarity difference between arranged and chosen partners. There is evidence of positive selection that may be a stronger driver, or at least it may mask other selection forces.

Strengths:

A rare opportunity to study human mate choice and genetic diversity. An excellent range of data and analysis that is well applied, and all results point to the same conclusion.

Overall, this is a very well-written and concise paper when considering the significant amount of data and excellent analysis that has been undertaken.

Weaknesses:

(1) For the type of samples and data available, none are obvious.

(2) Although this paper is clearly focused on humans, I was expecting more discussion around the studies that have been undertaken in animals. It is likely that between populations and species, there are different pressures that have driven the MHC evolution, but also mate choice.

(3) The peptide presentation based on pathogen genomes is interesting but usually not significant. I wondered if another measure of MHC haplotype diversity to complement this would be the overall repertoire of peptides that could be presented, pathogen-based or otherwise. There is usually significant overlap in the peptides that can be presented, for example, between HLA-A and HLA-B, and this may reveal more significant differences between the alleles and haplotype frequencies.

Reviewer #3 (Public review):

The study investigates MHC-related mate choice in humans using a sample of couples from a small-scale sub-Saharan society. This is an important endeavour, as the vast majority of previous studies have been based on samples from complex, highly structured societies that are unlikely to reflect most of human evolutionary history. Moreover, the study controls for genome-wide diversity, allowing for a test of the specificity of the MHC region, as theoretically predicted. Finally, the authors examine potential fitness benefits by analysing predicted pathogen-binding affinities. Across all analyses, no deviations from random pairing are detected, suggesting a limited role for MHC-related mate choice in a relatively homogeneous society. Overall, I find the study to be carefully executed, and the paper clearly written. Nevertheless, I believe the paper would benefit if the following points were considered:

(1) The authors claim (p. 2, l. 85) that their study is the first to employ a non-European small-scale society. I believe this claim is incorrect, as Hendrick and Black (1997) investigated MHC similarity among couples from South American indigenous populations.

(2) Regarding the argument that in complex societies, mating with a random individual would already result in sufficient MHC dissimilarity (p. 2, 78), see the paper from Croy et al. 2020, which used the largest sample to date in this research area.

(3) Dataset. As some relationships are parallel, I assume that certain individuals entered the dataset multiple times. This should be explicitly reported in the Methods. If I understand the analyses correctly, this non-independence was addressed by including individual identity as a random effect in the model - the authors should confirm whether this is the case. I am also wondering to what extent so-called "discovered partnerships" may affect the results. Shared offspring may be the outcome of short or transient affairs and could have a different social status compared with other informal relationships. Would the observed patterns change if these partnerships were excluded from the analyses?

(4) How many pairs were due to relatedness closer than 3rd degree? In addition, why was 4th degree relatedness used as a threshold in some of the other analyses?

(5) I was surprised by the exclusion of HIV, given that Namibia has a very high prevalence of HIV in the general population (e.g., Low et al. 2021).

(6) It appears that age criteria were applied when generating random pairs (p. 8, l. 350). Could the authors please specify what they consider a realistic age gap, and on what basis this threshold was chosen? As these are virtual couples used solely to estimate random variation within the population, it is not entirely clear why age constraints are necessary. Would the observed patterns change if no age criteria were applied?

(7) I think it would be helpful for readers if the Results section explicitly stated that real couples did not differ from randomly generated pairs. At present, only the comparison between chosen and arranged pairs is reported.

(8) I appreciate the separate analyses of pathogen-binding properties for MHC class I and class II, given their functional distinctiveness. For the same reason, I would welcome a parallel analysis of MHC sharing conducted separately for class I and class II loci.

(9) I think the Discussion would benefit from a more detailed comparison with previous studies. In addition, the manuscript does not explicitly address limitations of the current study, including the relatively limited sample size given the extensive polymorphism in the MHC region.

References:

Hedrick, P. W., & Black, F. L. (1997). HLA and mate selection: no evidence in South Amerindians. The American Journal of Human Genetics, 61(3), 505-511.

Croy, I., Ritschel, G., Kreßner-Kiel, D., Schäfer, L., Hummel, T., Havlíček, J., ... & Schmidt, A. H. (2020). Marriage does not relate to major histocompatibility complex: A genetic analysis based on 3691 couples. Proceedings of the Royal Society B, 287(1936), 20201800.

Low, A., Sachathep, K., Rutherford, G., Nitschke, A. M., Wolkon, A., Banda, K., ... & Mutenda, N. (2021). Migration in Namibia and its association with HIV acquisition and treatment outcomes. PLoS One, 16(9), e0256865.

Reviewer #1 (Public review):

Summary:

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

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

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

Strengths:

The primary strength of this work lies in its systematic and comprehensive approach to dissecting how experimental variables influence the outcome of autophagy-lifespan epistasis tests. The compilation of prior data alongside the authors' own multi-condition dataset is a genuinely useful resource for the field. The study raises a timely and important point about condition selection bias, which is relevant not only to autophagy research but to C. elegans aging studies more broadly. The finding that atg-18 behaves distinctly from other autophagy genes across all conditions is noteworthy and opens avenues for future mechanistic work.

Weaknesses:

Despite its breadth, the study has several weaknesses that limit the strength of some conclusions.

(1) Variability in control lifespan data. The N2 lifespan values under ostensibly identical conditions (e.g., GFP RNAi at 20{degree sign}C) differ substantially across experiments (compare Tables S2, S5, S6, S7, and S9). Since N2 serves as the baseline for calculating whether the effect is greater in long-lived mutants via Cox proportional hazard (CPH) analysis, this variability in controls directly affects the reliability of those comparisons.

(2) Limited biological replication. Most experiments were performed with only two biological replicates. In several cases, the two replicates yield contradictory outcomes: one showing significant lifespan suppression and the other showing no effect or even extension. The authors combine these into cumulative datasets for analysis, which, while not incorrect in principle, may obscure genuine irreproducibility. Given that the central message of the paper concerns variability and condition dependence, additional replication would have substantially strengthened confidence in the reported results.

(3) Low sample sizes in individual trials. A number of lifespan assays were conducted with only 40-50 worms per replicate, and in some cases, as few as 30. Such sample sizes are below the standard commonly used in the C. elegans aging field and are likely to contribute to the variability observed.

(4) RNAi efficacy measured only in N2 at 20{degree sign}C. The authors demonstrated that atg-2 and atg-4.1 RNAi did not significantly reduce target mRNA levels, which may explain their weaker lifespan effects. However, these same RNAi treatments significantly affected lifespan in several other conditions (e.g., daf-2(e1368) at 20{degree sign}C, glp-1 at 20{degree sign}C and 25{degree sign}C, and N2 with 15 µM FUDR). Measuring RNAi efficacy across different genetic backgrounds and conditions would be needed to properly interpret these variable results.

(5) Incomplete mechanistic exploration. The investigation of why atg-18 knockdown has uniquely strong effects was limited to DAF-16. Given published evidence that atg-18 may regulate HLH-30/TFEB, a master transcriptional regulator of autophagy and lysosomal biogenesis, testing whether atg-18 specifically affects HLH-30 nuclear localisation or activity could have provided valuable mechanistic insight and would distinguish atg-18 from the other genes tested.

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

Additional functional validation would further strengthen the conclusions.

Reviewer #1 (Public review):

Summary:

The current study by Xing et al. establishes the methodology (machine vision and gaze pose estimation) and behavioral apparatus for examining social interactions between pairs of marmoset monkeys. Their results enable unrestrained social interactions under more rigorous conditions with detailed quantification of position and gaze. It has been difficult to study social interactions using artificial stimuli, as opposed to genuine interactions between unrestrained animals. This study makes an important contribution for studying social neuroscience within a laboratory setting that will be valuable to the field.

Strengths:

Marmosets are an ideal species for studying primate social interactions due to their prosocial behavior and the ease of group housing within laboratory environments. They also predominantly orient their gaze through head-movements during social monitoring. Recent advances in machine vision pose estimation set the stage for estimating 3D gaze position in marmosets but requires additional innovation beyond DeepLabCut or equivalent methods. A six point facial frame is designed to accurately fit marmoset head gaze. A key assumption in the study is that head-gaze is a reliable indicator of the marmoset's gaze direction, which will also depend on the eye position. Overall, this assumption has been well supported by recent studies in head-free marmosets. Thus the current work introduces an important methodology for leveraging machine vision to track head-gaze and demonstrates its utility for use with interacting marmoset dyads as a first step in that study.

Comments on revisions:

I thank the authors for their careful revisions of the manuscript. It has addressed all of my comments.

One final suggestion would be to add a scale bar in Supplemental Figure 2A so the size of the video/image stimuli is clear (in cm of monitor size) and also to report a range for how far away was the marmoset in viewing these stimuli (in cm). This will enable calculation of the rough accuracy in visual degrees.

Reviewer #2 (Public review):

Summary:

The manuscript describes novel technique development and experiments to track the social gaze of marmosets. The authors used video tracking of multiple cameras in pairs of marmoset to infer head orientation and gaze, and then studied gaze direction as a function of distance between animals, relationships, and social conditions/stimuli.

Strengths:

Overall the work is interesting and well done. It addresses an area of growing interest in animal social behavior, an area that has largely been dominated by research in rodents and other non-primate species. In particular, this work addresses something that is uniquely primate (perhaps not unique, but not studied much in other laboratory model organisms), which is that primates, like humans, look at each other, and this gaze is an important social cue of their interactions. As such, the presented work is an important advance and addition to the literature that will allow more sophisticated quantification of animal behaviors. I am particularly enthusiastic about how the authors approach the cone of uncertainty in gaze, which can be both due to some error in head orientation measurements as well as variable eye position

Weaknesses:

While there remains some degree of uncertainty in the precise accuracy of the gaze measure, the authors have done an excellent job accounting for these as well as they can, and appropriately acknowledge the limitations of their approach.

Comments on revisions:

I have no further recommendations. The authors addressed my previous suggestions or acknowledged them as topics for future investigation. This is excellent work.

Reviewer #1 (Public review):

The authors show experimentally that, in 2D, bacteria swim up a chemotactic gradient much more effectively when they are in the presence of lateral walls. Systematic experiments identify an optimum for chemotaxis for a channel width of ~8µm, a value close to the average radius of the circle trajectories of the unconfined bacteria in 2D. These chiral circles impose that the bacteria swim preferentially along the right-side wall, which indeed yields chemotaxis in the presence of a chemotactic gradient. These observations are backed by numerical simulations and a geometrical analysis.

Reviewer #3 (Public review):

This paper addresses, through experiment and simulation, the combined effects of bacterial circular swimming near no-slip surfaces and chemotaxis in simple linear gradients. The authors have constructed a microfluidic device in which a gradient of L-aspartate is established, to which bacteria respond while swimming while confined in channels of different widths. There is a clear effect that the chemotactic drift velocity reaches a maximum in channel widths of about 8 microns, similar in size to the circular orbits that would prevail in the absence of side walls. Numerical studies of simplified models confirm this connection.

The experimental aspects of this study are well executed. The design of the microfluidic system is clever in that it allows a kind of "multiplexing" in which all the different channel widths are available to a given sample of bacteria.

The authors have included a useful intuitive explanation of their results via a geometric model of the trajectories. In future work it would be interesting to analyze further the voluminous data on the trajectories of cells by formulating the mathematical problem in terms of a suitable Fokker-Planck equation for the probability distribution of swimming directions. In particular, this might help understand how incipient circular trajectories are interrupted by collisions with the walls and how this relates to enhanced chemotaxis.

The authors argue that these findings may have relevance to a number of physiological and ecological contexts. As these would be characterized by significant heterogeneity in pore sizes and geometries, further work will be necessary to translate the present results to those situations.

Reviewer #2 (Public review):

Summary:

Dr Lenz and colleagues report on their in vitro studies comparing gene transcription and epigenetic modifications in Plasmodium falciparum NF54 parasites selected or not selected for adhesion of the infected erythrocytes (IEs) to the placental IE adhesion receptor chondroitin sulfate A (CSA).

The authors report that selection led to preferential transcription of var2csa, the gene that encodes the VAR2CSA-type PfEMP1 well-established as the PfEMP1 mediating IE adhesion to CSA. They confirm that transcriptional activation of var2csa is associated with distinct depletion of H3K9me3 marks and that transcriptional activation is linked to repositioning of var2csa. Finally, they provide preliminary evidence potentially implicating 5mC in transcriptional regulation of var2csa.

Strengths:

The study confirms previously reported features of gene transcription and epigenetic modifications in Plasmodium falciparum.

Weaknesses:

No major new finding is reported.

Comments on revisions:

I suggest replacing the term "pregnancy-associated malaria (PAM)" with the more current and more precise term "placental malaria (PM)" throughout the manuscript.

L. 59-60: "... shielding of the parasite antigens expressed on pRBC surfaces by leukocytes...". It is unclear to me what this means - I suggest a rephrasing for improved clarity.

L. 144-6: Please provide a reference for the primary antibody reagent used.

Reviewer #3 (Public review):

Summary:

The manuscript by Lenz et al. seeks to investigate molecular mechanisms directing virulence gene expression in the malaria parasite Plasmodium falciparum. The report provides a detailed characterization of the phenotypic and epigenetic features of a var2csa expressing parasite population, the key virulence gene causing the clinical syndrome of placental malaria. Novel evidence supporting the concept that active expression of this gene is associated with nuclear repositioning away from suppressive regions of chromatin is presented. In addition, the authors conducted a preliminary characterization of different forms of DNA methylation, suggesting that 5-methylcytosine is enriched in virulence genes, but does not correlate with their activation or repression. However, a trend towards higher enrichment of 5-methylcytosine in highly active as opposed to inactive genes from the core genome was reported, although this observation requires further validation.

Strengths:

The concise study provides a well documented and controlled set of experiments utilizing state-of-the-art OMICs methodologies including ChIPseq, RNAseq, chromatin-conformation capture (Hi-C) and DNA methylation (MeDIPseq) to generate deep insight into the epigenetic regulation of the key virulence factor of P. falciparum. The study unifies different lines of evidence and thereby contributes to a clearer understanding of the mechanisms underlying active expression of var2csa.

Weaknesses:

Although all experiments appear to have been rigorously conducted and documented with appropriate replicates and controls, the study is overall lacking statistical support from individual analyses of the biological replicates. In particular, the key novel result suggesting increased distance of the active var2csa gene from regions of heterochromatin as assessed by chromatin conformation capture would benefit from further analysis by comparison with other genetic loci. This also applies to the differential DNA methylation patterns, which should be dissected in more detail to support any association with gene expression or intron function.

Reviewer #3 (Public review):

Summary:

This work investigates whether human imprecision in numeric perception is a fixed structural constraint or an endogenous property that adapts to environmental statistics and task objectives. By measuring behavioral variability across different uniform prior distributions in both estimation and discrimination tasks, the authors show that perceptual imprecision increases sublinearly with prior width. They demonstrate that the specific exponents of this scaling (1/2 for estimation and 3/4 for discrimination) can be derived from an efficient-coding model, wherein decision-makers optimally balance task-specific expected rewards against the metabolic costs of neural coding. The revised manuscript expands this framework to accommodate logarithmic representations and validates the core model against an independent dataset of risky choices.

Strengths:

The authors have effectively addressed my previous concerns with rigorous additions:

(1) The mathematical formulation has been revised into a discrete signal accumulation framework, making the objective function and resource trade-offs much more transparent and mathematically tractable.

(2) The incorporation of the logarithmic representation resolves prior ambiguities regarding structural constraints.

(3) The new split-half analysis effectively addresses the temporal dynamics of adaptation. The stability of the sublinear scaling across the experiment provides solid evidence that human subjects utilize rapid, top-down modulation to adjust their encoding strategy when explicitly informed about the environment.

(4) Validating the derived scaling exponents on an independent risky-choice dataset robustly supports the generalizability of the theoretical framework beyond a single cognitive domain.

Comments on revisions:

The authors have addressed my remaining theoretical concern regarding the model's predictions for mean estimation bias. I have no further comments.

Reviewer #1 (Public review):

Summary:

The integration of single-cell datasets across species is a powerful approach to understanding how cell types and patterns of gene expression have evolved. Current methods to perform such integrations require multiple steps: clustering, the integration itself, and downstream differential expression analysis. In this study, the authors describe a new approach, called ANTIPODE, that combines these steps by integrating deep learning with interpretable decoding and linear modeling. This method builds on previous deep learning approaches to dataset integration, namely SCVI and scANVI, that employ a variational autoencoder to model single-cell RNA-sequencing datasets. However, gene expression estimates from these previous methods are challenging to interpret due to non-linear decoding from the modeled latent space. ANTIPODE seeks to address this issue by using a single-layer decoder coupled to a linear model to estimate patterns of differential expression, e.g. differential expression by coexpression module, across cell types, etc.

The authors apply their framework to a large single-cell RNA-seq dataset (~1.8M cells) containing cells from the central nervous systems of humans, macaques, and mice spanning in utero developmental time points. They identify a consensus set of cell clusters across each species. They find that ANTIPODE performs at least as well as SCVI in terms of species integration and batch correction. The authors demonstrate several use cases of this integrated approach by analyzing differential expression that correlates with gene structure, the evolution of expression differences in neuropeptide systems, and the anatomical and phylogenetic variation in neurodevelopmental timing.

Strengths:

ANTIPODE is a welcome addition to techniques that integrate large single-cell RNA-seq datasets across multiple species. The approach's simultaneous inference of cell clusters, integration manifolds, and differential expression should streamline analysis pipelines whose elements are often disjointed and sometimes work at cross purposes.

Weaknesses:

The authors note several limitations to their method that will be targets for future development. First, clustering "resolution" is inferred from the data and cannot be tuned as with other approaches. Second, because of the linear decoding, ANTIPODE does not accommodate combining datasets obtained from different modalities (e.g. single-cell with single-nucleus RNA-seq). Third, as currently implemented, ANTIPODE does not explicitly model phylogenetic relationships. However, the authors describe an extension that could enable this, enhancing the power of multiple species integrations. A weakness with the current manuscript is the organization and readability of the figures. The supplemental figures in particular need to be restructured and reformatted to increase their interpretability.

Reviewer #2 (Public review):

Summary:

This work presents ANTIPODE, a bilinear generative model developed for the simultaneous integration and identification of cell types across species and developmental stages using single-cell RNA-seq data. ANTIPODE is inspired by scANVI, a well-established semi-supervised framework for single-cell transcriptomics. After describing its implementation, the authors use ANTIPODE to integrate data from 15 species comprising 1,854,767 cells. Then, the authors benchmark ANTIPODE against commonly used methods (scVI, Harmony, and Scanorama) using two snRNAseq datasets and report comparable or superior performance. They then return to the initial integrated dataset and analyse patterns of gene expression evolution. Finally, they leverage the model to study the "later-is-larger" concept, evaluating the relationship between gene expression, developmental timing and structure size and finding gene expression signatures of this concept.

Strengths:

A major strength of the paper is that ANTIPODE employs a bilinear decoding architecture, which produces more interpretable model parameters while performing at least as well as existing, more opaque nonlinear integration approaches.

The authors demonstrate the utility of ANTIPODE by integrating single-cell mRNA sequencing data from mouse, macaque, and human brains and confirming general principles regarding developmental timing and cell-type-specific gene expression divergence.

They also propose a conceptually interesting framework for studying gene expression evolution: instead of focusing solely on differentially expressed genes between homologous cell types, they jointly model gene expression across developmental states and species-specific divergence, allowing them to define and analyse four categories of differential expression.

Finally, the authors' conclusions are well supported by the analyses presented, although these conclusions remain relatively conservative and reinforce already established principles.

Weaknesses:

A central weakness of the paper is its limited accessibility to a broad audience. Despite attempting to keep computational details in the supplement, the main text still uses substantial jargon, undermining the goal of providing an intuitive explanation of the model. The figures are also insufficiently annotated (e.g., colour schemes in Figure 2 heatmap, bubble plot details in Figure 3, entropy definition in Figure 3), and the figure legends are overly brief and lack essential information. I strongly recommend that the authors revise both text and figures to improve clarity and readability.

Similarly, the materials and methods lack a lot of information about the implementation of the model, the statistical tests used, the calculations of entropy, etc.

The study sits between tool development and biological discovery but does not fully commit to either. As a result, it cannot be evaluated as a full benchmarking study, yet it also does not provide new biological insights that are validated experimentally.

Finally, the GitHub repository for ANTIPODE is not yet functional and lacks documentation or tutorials, making it impossible to assess usability or reproducibility.

Reviewer #1 (Public review):

This manuscript by Niño-González and collaborators shows that PIF4 undergoes alternative splicing in response to elevated temperature, generating distinct isoforms that may contribute to early seedling responses of Arabidopsis thaliana to heat stress (37 {degree sign}C). This work provides an intriguing perspective on how PIF activity may be modulated under stress conditions.

The authors report rapid heat-induced changes in seedling morphology, with cotyledon angle and hypocotyl length altered as early as 3 hours after transfer to 37 {degree sign}C. These responses correlate with a transient increase in PIF4 transcript levels, followed by a return to control values at later time points. Notably, heat induces preferential production of an exon 5-skipping isoform of PIF4. The resulting short protein variant (PIF4-S) lacks part of the bHLH domain and is therefore unlikely to be transcriptionally active.

To explore functional consequences, the authors expressed the exon 5 inclusion (functional) isoform, PIF4-L, in the pif4-101 mutant background. Some heat-induced phenotypes, such as protochlorophyllide accumulation and subsequent photobleaching, were reduced or absent in these lines. Interestingly, pif4-101 mutants themselves largely resemble WT plants for most heat-responsive traits, with the exception of hypocotyl length. PIF4-L expression specifically attenuates the cotyledon angle response to heat, without strongly affecting hypocotyl elongation.

An important point is that PIF4 itself is not essential for the observed heat responses, as pif4 mutants respond largely like wild-type plants. This implies that the phenotypes described are likely controlled by multiple PIFs acting redundantly. In this context, the generation of the PIF4-S isoform may represent one of several mechanisms by which heat stress reduces overall functional PIF levels, rather than a PIF4-specific regulatory switch.

Other caveats should be considered when interpreting the work. The functional relevance of the PIF4-S isoform under heat stress is not tested, as heat responses of these transgenic lines were not examined. Transcriptome analysis of heat-stressed WT, pif4-101 mutant, and PIF4-L-expressing plants revealed an enrichment of PIF-regulated genes, supporting a possible role for this family of transcription factors in the heat stress response. Notably, the heat responsiveness of the mutant and of the transgenic lines differs only marginally from that of WT plants. In addition, the study relies primarily on total transcript-level analyses, without quantitative assessment of individual PIF isoforms or direct measurement of PIF protein abundance. Given that other PIFs are also expressed and may be subject to alternative RNA processing, it needs to be determined whether PIF4-S alone could exert a dominant effect, counteracting all the other functional PIFs by itself, under heat stress. Hence, the proposed model is a plausible but still incomplete framework that requires further experimental validation and analysis.

Altogether, the results presented in this manuscript could also be interpreted as follows: multiple PIFs contribute to the observed phenotypes in response to heat, with overlapping (redundant) functions. Heat stress may reduce functional PIF levels through different mechanisms, one of which is the regulation of alternative splicing, as shown here for PIF4, leading to the production of non-functional proteins or protein variants that could act as negative competitors (such as PIF4-S). Restoring PIF levels to values of control conditions could therefore reverse heat-induced phenotypes, as observed in the PIF4-L expression lines.

Main concerns:

(1) The existence of a shorter isoform of PIF4 and PIF6 is relevant, and PIF4 could indeed play a role in the context of heat stress, as it does in thermomorphogenesis. In this sense, the interplay between PIF4-S and PIF4-L might be linked to plant morphological responses to heat; however, the present work requires further investigation to determine whether this is indeed the case. It is important to note that pif4 mutants behave similarly to WT plants, indicating that PIF4 is not necessary for the observed responses. These phenotypes are therefore most likely related to several PIFs rather than to one specific family member. The results obtained with the transgenic lines expressing PIF4-L or PIF4-S support this interpretation, as increasing a functional PIF (PIF4-L) reduces some phenotypes, while expressing a dominant-negative version mimics heat-induced phenotypes under control conditions. Thus, it is reasonable to interpret that under heat stress, functional PIF levels are reduced through multiple mechanisms, alternative splicing and PIF4-S generation being one of them in the case of PIF4, but likely with additional effects on other family members. This clearly requires further study.

(2) RT-qPCR quantification of total PIF4 transcripts, as well as the long and short isoforms under the tested conditions, is necessary. While we agree with the authors that PIF4-S could act as a dominant-negative factor, demonstrating this requires comparison of phenotypes under heat versus control conditions using the PIF4-S transgenic lines. Importantly, for the authors' hypothesis to be valid, PIF4-S must be able to outcompete other PIFs; therefore, accurate quantification of its expression levels across conditions is crucial. Combining the results shown in Figures 2A and Figure 2G suggests that the levels of the functional PIF4-L isoform are unchanged or even reduced after 3 h of heat treatment, as the increase in total PIF4 does not fully compensate for the diversion toward PIF4-S. Additionally, it would be equally relevant to quantify the expression of other PIFs (or at least those shown in Suppl. Fig. 6) to determine whether PIF4-S could exert such a strong effect even when expressed at relatively low levels. By "proper quantification", we refer specifically to functional protein-coding variants, as in the PIF4-L case. Supplemental Figure 6 shows that PIF3 and PIF5 appear unaffected by heat, while PIF1 expression is increased. However, JBrowse data for dark-grown seedlings indicate that PIF1 is subject to alternative transcription initiation, alternative splicing, and alternative polyadenylation at its 3′ end. A similar situation occurs for PIF3, at least at the 5′ end of the transcriptional unit. Therefore, alternative RNA processing mechanisms may play a key role in modulating functional PIF protein levels in response to heat. Without considering diverted isoforms of other PIFs, the interpretation becomes problematic, as PIF1 is upregulated by heat, and PIF4-S would therefore need to overcome its activity as well. This is particularly relevant given that the cotyledon angle phenotype at 37 {degree sign}C appears even stronger than in the pif1pif3pif5 triple mutant, if such a comparison is feasible.

(3) In addition, PP2A is a well-established housekeeping gene for normalization across different light regimes, as its expression is not affected by light. However, we are not convinced this holds true under heat stress conditions (see Li et al., Plant Cell 2019 Jul 29;31(10):2353-2369. doi:10.1105/tpc.19.00519).

(4) Furthermore, the mechanistic conclusions would be strengthened by directly assessing PIF protein levels, for example, by western blot analysis, to determine whether changes in transcript isoform abundance translate into corresponding changes in protein accumulation under heat stress.

(5) Importantly, the authors' interpretation that "PIF4-L.1 expresses the long isoform at levels similar to those of WT plants (Supplemental Figure 9A), ruling out the possibility that the suppression of heat-induced phenotypes (cotyledon opening and Pchlide accumulation) is due to elevated PIF4 expression levels" is not correct. The RT-qPCR assay quantifies all isoforms containing exon 6, which include both long and short variants with respect to exon 5 inclusion. Since WT plants at 37 {degree sign}C express both isoforms (L/S ≈ 60/40), the PIF4-L lines actually express 2-4-fold higher levels of the functional PIF4 isoform, based on the values shown in the figures.

(6) Figure 3B should include a statistical analysis, as it appears that PIF4-L expression does not significantly reduce photobleaching. Cotyledon angle is not affected by either the pif4 mutation or PIF4-L expression under 22 {degree sign}C conditions (Figure 3C). However, after 24 h at 37 {degree sign}C, there is a clear effect, with cotyledon angles closer to those observed in WT plants at 22 {degree sign}C. Regarding hypocotyl length, although statistical testing was not performed, it is evident that pif4-101 affects this parameter, while PIF4-L expression in this background does not substantially alter the mutant response.

Other comments:

(1) We do not believe that Figure 3E is an optimal way to demonstrate attenuation of transcriptional changes by PIF4-L expression in pif4 mutants. A heat map representation would likely be more direct and informative.<br /> The authors should consider expressing another functional PIF in the pif4 mutant background to determine whether the observed effects are specific to PIF4, as proposed, or whether they reflect a general PIF function.

(2) It would also be informative to examine the response under Light + 37 {degree sign}C conditions. Since PIF4 mRNA accumulation is induced by light, the authors should test whether plants incubated in light show a similar response to heat or whether it is attenuated. Potential cross-regulation between light and heat responses would be worth exploring.

(3) As the authors acknowledge in the introduction, most of our knowledge regarding PIFs in temperature signalling has focused on thermomorphogenesis. Therefore, we believe it is important to place these new findings (exon 5 skipping) within that framework, as they could help explain observations made under better-characterized conditions. In addition, would be interesting to see the phenotypes of the pifq mutant under heat stress. Even though this mutant line displays a heat-stress-like phenotype under control conditions, it may still respond to heat treatment. If so, this would indicate that PIFs are not fully determinative of this response.

(4) The authors should clearly state the genetic background of the PIF4-S expression lines, which appear to be in the pif4-101 background but are not explicitly described as such in the manuscript.

Reviewer #2 (Public review):

The manuscript "Alternative splicing of PIF4 regulates plant development under heat stress" by Niño-González et al. describes a heat-responsive alternative splicing (AS) event in PIF4 in Arabidopsis and its potential impact on seedling development. The authors observe that etiolated ings exposed to heat respond with a more photomorphogenic developmental behaviour, as reflected, for example, by increased cotyledon opening and reduced hypocotyl elongation. They propose that the AS event in PIF4 may contribute to this response, due to reduced formation of the full-length PIF4 protein and an increase in the shorter PIF4 protein with potentially dominant negative functions.

Expressing the individual variants in a pif4 mutant background was used to further examine their function. In the case of the full-length PIF4 variant, some of the heat-induced phenotypes were suppressed. For the lines overexpressing the shorter PIF4 variant, heat responses were not examined.

The authors describe an interesting phenotype and present an appealing model of how AS of PIF4, a well-known key regulator of developmental processes including light- and temperature responses, might be involved. However, I don't think that the authors provide strong evidence for their model, and the unaltered heat response of pif4 mutants argues against a major role of this gene and its AS event under these conditions. Regarding the heat responses, it remains open how distinct those are from thermomorphogenesis.

Weaknesses:

(1) In the manuscript, it is emphasized that previous studies on PIFs' role in temperature responses have mainly focused on thermomorphogenesis under high ambient temperature and not under hot temperatures causing heat stress. How do the authors know that the effects they are looking at are specific to hot temperatures and do not also occur at more moderate temperature increases? So, what would PIF4 splicing look like upon a shift from 22{degree sign}C to 28{degree sign}C (instead of 37{degree sign}C as used in the manuscript)?

(2) The potential role of PIF4 and its AS event in the heat response is the key point of this manuscript, as also reflected by the title. As summarized above, I don't see direct evidence for this and a functional characterization of the AS event is lacking. First, the pif4 mutant doesn't show an altered response, which argues against its requirement under these conditions, and in particular against the proposed model that a shortened version of PIF4 acts in a dominant negative manner. Second, the impact of AS on PIF4 protein levels remains open. Antibodies against PIF4 exist and have been used before, e.g. in Lee et al. (2021), Nat Comm, and Fan et al. (2025), Nat Comm - both studies address the role of PIF4 in thermomorphogenesis and should also be discussed in this manuscript. Detecting PIF4 proteins would allow testing if indeed both PIF4 protein variants are detectable and whether, upon heat stress, the longer variant decreases while the shorter variant increases. This could be expected based on transcript data; however, due to regulation at multiple steps, a correlation between transcript and protein levels might not exist. Third, the transgenic lines expressing either the short or long PIF4 variant do not really reflect the situation in the wild type and might be/are overexpression lines. Specifically, constructs for both variants lack the UTRs according to the description in the method section. Furthermore, is the short version expressed as GFP fusion, as I understood from the method description? The PIF4-L mutants have similar PIF levels as the WT (SFig. 9); however, this refers to total transcripts, which makes a difference in the wild type, in particular under heat stress. Comparing here only the PIF4-L levels would be more informative. Accordingly, the transgenic lines may overexpress PIF4-L compared to the wild type. All the PIF4-S lines show 4 to 5-fold overexpression (again for total transcripts) compared to WT. Including lines with lower overexpression levels would be needed for a direct comparison to the wild type. Moreover, immunoblot analysis of the PIF4 protein would be needed for a direct comparison between the wild type and the two types of mutants.

(3) Apart from the question of what level of (over)expression the transgenic lines have, several aspects of the phenotyping experiments are not in line with a simple model of PIF4 regulation or have not been addressed. Expressing the long PIF4 variant in the pif4 mutant background suppresses some of the heat-induced changes, but not the hypocotyl shortening, suggesting that the hypocotyl effect is not caused by a heat-induced lack of PIF4.

When expressing the short variant, the authors observe increased cotyledon opening in darkness, consistent with a suppression of skotomorphogenesis due to a negative function of PIF4-S, at least when it is overexpressed. For hypocotyl length, no consistent difference between wild type and PIF4-S lines was observed: seedlings grown for 3 d in darkness had identical lengths, for 4-d-old seedlings, the PIF4-S lines did not give consistent results: PIF4S.1 (which has highest transgene expression) had same length as wild type; a pronounced difference was only seen for PIF4-S.3, which is the line with lowest expression. Have the experiments been reproduced with independent seed badges? I'm also wondering why the authors haven't performed the heat stress experiments with these PIF4-S lines, as they did for the PIF4-L mutants. According to the authors' model, the PIF4-S lines might show an opposite response compared to the PIF4-L lines, i.e. an even more pronounced heat effect compared to the wild type.

(4) Why was the heat effect on AS of PIF6 not further analysed? Previous work showed the role of PIF6 in seed development and germination; in line with this, PIF6 expression is particularly high in embryos and seeds, but it is also expressed and alternatively spliced in other tissues and conditions, as shown in Figure 1 and SFigure 2. From the data in Figure 1, it looks like the AS pattern in heat might also be different from other conditions. So, it would be interesting to see how AS of PIF6 changes in the control and heat samples that the authors analysed for PIF4 AS, in particular, if this response is distinct for PIF4 versus PIF6.

(5) The presentation of the RNA-seq data is incomplete. According to the method section, WT, pif4-101, PIF4-L.1 and PIF4-L.2 seedlings upon 3 h heat/control treatment were analysed. Why are DE and DAS genes and comparisons of different genotypes not shown? The FC data displayed in Figure 2E and the overlap between heat-regulated genes (Fig. 3D; only in WT) and PIF regulation show only some aspects of the data.

Reviewer #3 (Public review):

Summary:

PIFs play a pivotal role not only in light and temperature signaling pathways, but in many other signaling pathways regulating plant development by modulating transcription of a large number of genes both directly and indirectly. Similarly, alternative splicing (AS) plays a critical role in shaping the splice isoforms of thousands of genes under different environmental conditions to regulate plant development. In fact, AS of PIF6 has been shown to be involved in seed development. PIF4 is a central transcription factor integrating light and temperature signaling pathways. However, AS of PIF4 has not been involved in any pathways. This story first describes how AS of PIF4 is regulated by heat stress, and this regulation is involved in heat stress signaling to regulate plant development. This is an important finding of general interest.

Strengths:

The authors first describe AS of PIF4 is regulated by heat stress, and this regulation is involved in heat stress signaling to regulate plant development.

Weaknesses:

There are many loose ends in this story that need to be tied up.

Major points:

(1) The authors are showing only the AS transcripts by PCR, but no protein data. Given that the hypothesis is that the short form of PIF4 is functioning in a dominant negative fashion, the authors need to show that this short isoform expresses a protein. In addition, they need to show that this form is functioning in a dominant negative fashion with other PIFs, either by showing that this form reduces the DNA binding and/or transcriptional responses of other PIFs.

(2) The two mutant alleles used for this study (pif4-100 and pif4-2) have T-DNA insertion after the AS exon. Do these alleles express any short version of the protein? The previous studies showed no protein production, and thus, they may not function as a dominant negative form. Usually, the T-DNA insertion alleles may express truncated transcripts, but many do not express any protein due to a lack of stop codon and/or degradation of the transcripts. But in this case, the mutants are behaving like WT. The authors need to show that these alleles are expressing a truncated version of the PIF4 protein.

(3) Figure 4 shows phenotypes of independent lines expressing the PIF4 short version. The authors analyzed only the cotyledon and hypocotyl phenotypes, but not Pchlide or bleaching assays. The authors need to do a thorough phenotype analysis, including heat-stress phenotypes of these lines, to test if the data make sense with their hypothesis.

Reviewer #1 (Public review):

The authors aim to interrogate the sets of intramolecular interactions that cause kinesin-1 hetero-tetramer autoinhibition and the mechanism by which cargo interactions via the light chain tetratricopeptide repeat domains can initiate motor activation. The molecular mechanisms of kinesin regulation remain a key question with respect to intracellular transport and this study adds important perspectives to our understanding. It has implications for the accuracy and efficiency of motor transport by different motor families, for example the direction of cargos in one or other direction on microtubules.

The authors focus on the response of inactivated kinesin-1 to peptides found in cargos and the cascade of conformational changes that are induced. They also test the effects of the known activator of kinesin-1 - MAP7 - in the context of their model. The study benefits from multiple complementary, albeit relatively low-resolution, methods - structural prediction using AlphaFold3, 2D and 3D analysis of (mainly negative stain) TEM images of several engineered kinesin constructs, biophysical characterisation of the complexes, peptide design, hydrogen/deuterium-exchange mass spectrometry and simple cell-based imaging. Each set of experiments is carefully designed and the intrinsic limitations of each method are offset by other approaches, such that the assembled data convincingly supports the authors' regulatory model of kinesin activation.

This study benefits from prior work by the authors on this system and the tools and constructs they previously accrued, as well as from other recent contributions to the field. This work will be of broad interest to cell and structural biologists, especially those seeking to tackle small and flexible macromolecular complexes, as well as biophysicists and those interested in protein engineering.

Reviewer #2 (Public review):

Summary:

In this paper, Shukla, Cross, Kish, and colleagues investigate how binding of a cargo-adaptor mimic (KinTag) to the TPR domains of the kinesin-1 light chain, or disruption of the TPR docking site (TDS) on the kinesin-1 heavy chain, triggers release of the TPR domains from the holoenzyme. This dislocation provides a plausible mechanism for transition out of the autoinhibited lambda-particle toward the open and active conformation of kinesin-1. Using a combination of negative-stain electron microscopy, AlphaFold modeling, biochemical assays, hydrogen-deuterium exchange mass spectrometry (HDX-MS) and other methods, the authors show how TPR undocking propagates conformational changes through the coiled-coil stalk to the motor domains, increasing their mobility, and enhances interactions with the microtubule-bound cofactor MAP7. Together, they propose a model in which the TDS on CC1 of the heavy chain forms a "shoulder" in the compact, autoinhibited state. Cargo-adaptor binding, mimicked here by KinTag, dislodges this shoulder, liberating the motor domains and promoting MAP7 association, driving kinesin-1 activation.

Strengths:

Throughout the study, the authors use clever construct design - e.g. delta-Elbow, ElbowLock, CC-Di and the high-affinity KinTag - to test specific mechanisms by directly perturbing structural contacts or effecting interactions. The proposed mechanism of releasing autoinhibition via adaptor-induced TPR undocking is also interrogated with a number of complementary techniques that converge on a convincing model for activation that can be further tested in future studies.

Weaknesses:

These reflect limits of what the current data can establish rather than flaws in execution. It remains to be tested if the open state of kinesin-1 initiated by TPR undocking is indeed an active state of kinesin-1 capable of processive movement and/or cargo transport. It also remains to be determined what the mechanism of motor domain undocking from the autoinhibited conformation is. But this important study provides the groundwork for testing these open questions.

Comments on revisions:

My original minor concerns have been addressed in the revision.

Reviewer #3 (Public review):

Summary:

The manuscript by Shukla and colleagues presents a comprehensive study that addresses a central question in kinesin-1 regulation-how cargo binding to the kinesin light chain (KLC) tetratricopeptide repeat (TPR) domains triggers activation of full-length kinesin-1 (KHC). The authors combine AlphaFold3 modeling, biophysical analysis (fluorescence polarization, hydrogen-deuterium exchange), and electron microscopy to derive a mechanistic model in which the KLC-TPR domains dock onto coiled-coil 1 (CC1) of the KHC to form the "TPR shoulder," stabilizing the autoinhibited (λ-particle) conformation. Binding of a W/Y-acidic cargo motif (KinTag) or deletion of the CC1 docking site (TDS) dislocates this shoulder, liberating the motor domains and enhancing accessibility to cofactors such as MAP7. The results link cargo recognition to allosteric structural transitions and present a unified model of kinesin-1 activation. I recommend acceptance of the manuscript subject to the following additions:

Strengths:

(1) The study addresses a fundamental and long-standing question in kinesin-1 regulation using a multidisciplinary approach that combines structural modeling, quantitative biophysics, and electron microscopy.

(2) The mechanistic model linking cargo-induced dislocation of the TPR shoulder to activation of the motor complex is well supported by both structural and biochemical evidence.

(3) The authors employ elegant protein-engineering strategies (e.g., ElbowLock and ΔTDS constructs) that enable direct testing of model predictions, providing clear mechanistic insight rather than purely correlative data.

(4) The data are internally consistent and align well with previous studies on kinesin-1 regulation and MAP7-mediated activation, strengthening the overall conclusion.

Weaknesses:

(1) While the EM and HDX-MS analyses are informative, the conformational heterogeneity of the complex limits structural resolution, making some aspects of the model (e.g., stoichiometry or symmetry of TPR docking) indirect rather than directly visualized.

(2) The dynamics of KLC-TPR docking and undocking remain incompletely defined; it is unclear whether both TPR domains engage CC1 simultaneously or in an alternating fashion.

(3) The interplay between cargo adaptors and MAP7 is discussed but not experimentally explored, leaving open questions about the sequence and exclusivity of their interactions with CC1.

Comments on revisions:

The authors have addressed my comments satisfactorily.

Reviewer #1 (Public review):

Barré et al. investigated the role of Shp1 and Shp2 in megakaryocytes (MKs) and platelets by conditional knock-out of Shp1, Shp2, or both under the control of the Gp1ba promoter. Deletion of Shp1 and Shp2 in MKs and platelets was almost complete. The Shp1/Shp2 double knock-out mice displayed macrothrombocytopenia and increased bleeding, whereas the single knock-outs did not show significant defects. Platelet function was aberrant in DKOs, but not in single knock-outs, and so was ligand-induced signaling, particularly Syk phosphorylation.

Megakaryocyte maturation was impaired in Shp1/Shp2 DKO mice. Ligand-induced signaling was impaired in Shp2 knock-out and DKO. Ex vivo formation of platelets and in vivo maturation of MKs were impaired in DKO mice. Pharmacological inhibitors of Shp1 and Shp2 had largely similar effects as observed in the single knock-outs. The authors conclude that Shp1 and Shp2 have synergistic functions in the MK/platelet lineage, and that Shp2 may be a potential therapeutic target in myeloproliferative neoplasms.

Strengths:

The data clearly show effects of the Shp1/Shp2 double knock-out on MKs and platelets.

Weaknesses:

There appears to be a discrepancy between the results with the Shp2 single knock-out and the Shp2 inhibitor: the Shp2 knock-out does not affect MKs and platelets, except Erk1/2 signaling, whereas the Shp2 inhibitors appear to affect MK function.

This work is interesting and may have potential from a therapeutic point of view.

Reviewer #2 (Public review):

Summary:

In this manuscript, Barré et al. investigate the roles of the phosphatases Shp1 and Shp2 in the megakaryocyte and platelet lineage using genetic depletion in mice. By employing Gp1ba-Cre-based models, the study builds on the authors' previous work and addresses some limitations associated with earlier Pf4-Cre approaches. The authors report relatively mild alterations in megakaryocyte and platelet parameters in mice lacking either Shp1 or Shp2 alone, whereas combined deletion of both phosphatases results in macrothrombocytopenia, mild bleeding, and impaired GPVI-dependent platelet aggregation accompanied by reduced Syk phosphorylation. The functional platelet defects are linked to reduced expression of GPVI and integrin α2, while thrombocytopenia is associated with impaired megakaryocyte maturation, reduced ploidy, defective proplatelet formation, and altered TPO-dependent Ras/MAPK signaling. Similar effects on megakaryopoiesis are also observed in vitro following treatment with newly developed Shp2 inhibitors.

Strengths and Weaknesses:

The study addresses an important biological question and presents a substantial dataset that could contribute to a better understanding of Shp1 and Shp2 function in platelet biology. However, several aspects of data presentation and interpretation would benefit from additional clarification. In particular, while the authors conclude that single genetic deletion or pharmacological inhibition of Shp1 has a limited impact and that the major phenotypes are specific to combined Shp1/2 deletion or Shp2 inhibition, some of the data suggest more nuanced effects that may warrant further discussion.

Reviewer #3 (Public review):

Summary:

In this manuscript, Barré et al utilize the Gp1ba-Cre transgenic mouse model to build upon previous findings in a Pf4-Cre system to investigate the effects of individual and combined Shp1 and Shp2 deletion in megakaryocytes and platelets. They report decreased megakaryocyte maturation, macrothrombocytopenia, and increased bleeding primarily in association with the Shp1/Shp2 double-knockout condition. The authors further show that this phenotype appears to be driven primarily by Shp2 and implicate dysregulation of Mpl signaling and downstream Ras/MAPK pathways, including ERK1/2. Given the key role of these pathways in human diseases such as myeloproliferative neoplasms and the challenges associated with modulating such a central pathway, identification of a specific regulator of Mpl signaling poses intriguing questions for future studies on clinical applicability.

Strengths:

Overall, the experiments combine in vitro, in vivo, and ex vivo approaches and appear to have been carefully designed and carried out, with multiple technical and biological replicates where relevant. The authors make a compelling argument for using the Gp1ba-Cre as opposed to the Pf4-Cre system and demonstrate both the dose- and stage-dependent effects of Shp1 and Shp2 on megakaryopoiesis and thrombopoiesis. They find that Shp1 and Shp2 are required in late-stage megakaryocyte maturation and that even low levels of expression compared to baseline are likely sufficient to yield generally normal megakaryocytes. Their findings also lead to specific future directions, such as the mechanism by which Shp1 regulates megakaryopoiesis and thrombopoiesis that is distinct from TPO-mediated signaling.

Weaknesses:

While the experiments have been thoughtfully designed and carried out, there is limited background explanation on relatively complex or niche pathways/mechanisms, such as the relationship between P-selectin, CRP, and PAR4p; the interactions between SFK, Syk, GPVI, and CLEC-2; and TPO, MPL, ERK1/2, AKT, and STAT3, which, while likely intuitive to experts in their respective fields, may be less obvious to a reader approaching this manuscript with a global interest in megakaryopoiesis/thrombopoiesis and thus detract from the impact of the findings.

With regard to the science itself, some of the conclusions feel premature based on the available data.

(1) The section "Aberrant ITAM signaling in Shp1- and Shp2-deficient platelets" is challenging to follow for those not well-versed in ITAM signaling and associated pathways, and may take additional outside reading to follow the conclusion that Syk-dependent signaling is modulated downstream of GPVI and CLEC-2 based on lack of change in Src p-Tyr418, especially considering that Src p-Tyr418 was previously introduced as a measure of SFK rather than Syk. In the introduction, Shp1 is specifically mentioned as a negative regulator of the ITAM/Syk/phospholipase pathway. However, in Figure 4Ai and Bi, Syk phosphorylation/activation in Shp1 knockout cells did not appear to be different from Shp2 knockout cells, and is lower than the control, which is surprising for a negative regulator. It is also not clear why, in the section (Figure 4A-B), there is reduced Syk activation in Shp1 and Shp2 single knockout cells upon CLEC2 stimulation (but apparently not with CRP) when there was no difference in response to CLEC2 (but a difference in response to CRP) in the previous section (Figure 3A, C).

(2) In the section "Reduced Tpo signaling in Shp1/2-deficient MKs," only Western blot data for (p)ERK1/2, AKT, and STAT3 are presented before concluding that decreased ERK1/2 activity is a mechanistic explanation for thrombocytopenia seen in the Shp1/2 double-knockout condition. Such a statement would benefit from additional experiments, such as protein or transcriptional levels of ERK1/2 targets specifically relevant to megakaryopoiesis, such as ETS, FOS, and JUN, to assess the consequences of decreased phosphorylated ERK1/2.

(3) Suggesting that "inhibiting Shp2 will not hav[e] any bleeding consequence in patients" and that Shp2 may be a therapeutic target in myeloproliferative neoplasms when none of these studies have been carried out in a human model is a bold conclusion. There are no data presented on, for example, whether Shp2 inhibition can help reverse the MPL/JAK/STAT pathway in the setting of gain-of-function mutations specifically associated with myeloproliferative neoplasms.

Reviewer #1 (Public review):

Summary:

Jackman et al report the analysis of a cis-regulatory region upstream of the dlx2b gene in zebrafish, that is hypothesised to control gene expression in the developing tooth. To demonstrate this, the authors performed solid promoter bashing analysis to assess the gene expression driven by the regulatory region, and validated the expression against a GFP-reporter knock-in. They narrowed down the tooth-specific enhancer activity to the MTE, which was sufficient to drive gene expression. Interestingly, they have identified a vertebrate conserved region which contained four predicted transcription factor binding sites, which when mutated individually, did not alter the reported gene expression. However, in combination, the expression was disrupted. The authors propose a putative upstream regulator cebpa binding one of the predicted TFBS, using in situ hybridisation to show overlapping gene expression domains.

Strengths:

The experiments presented in this paper were rigorously executed and the authors' effort to systematically dissect the different elements of the enhancer are commendable. The discussion and limitations of the study were very well-balanced.

First, the results represent important findings first for the enhancer biology field to sustain evidence of the role of redundant TFBSs. Too often, only TFBS mutations that are sufficient and necessary to drive gene expression patterns are reported, but work providing evidence that some TFBS are necessary but not sufficient by themselves to drive expression is rarer. TFBS redundancy is a crucial concept in enhancer biology but also a difficult concept to prove that hinders the accurate prediction of enhancer function. In an era where increasingly more powerful machine learning models are developed to predict enhancer function, this work is a reminder of the complexity of enhancer biology and provides ground truths for experimental validation.

Second, the results present valuable findings for the field of tooth development. While the authors have comprehensively described work performed in this space, there are still not many tooth-specific enhancers identified and accurately described. The work also presents further avenues for studying upstream regulators.

Weaknesses:

It seems to me that one of the greatest outcomes of this work is demonstrating the collective action of mutated TFBSs where individual mutations are not affecting gene expression. These findings fall into the realm of enhancer redundancy but this concept was not thoroughly discussed in the introduction of the paper.

The claimed results are generally well-supported by the experiments performed, and hypothesis and speculations have been clearly stated. However, some speculative statements remain that should be addressed, for example in the abstract line 33 "These findings suggest that loss of MTE function permits alternative cis-regulatory elements to gain control of the promoter". There is no data indicating what these cis-regulatory elements could be, hence this sentence might be better suited in the discussion.

The manuscript could be strengthened by further exploration of the wider region upstream of dlx2b to support the recruitment of other TFBSs: Were there any other vertebrate-conserved regulatory regions just outside of the MTE? Were there any other family members of the predicted TFs expressed in the tooth? Transcription factor binding sites identity remains a prediction; it could be expanded to other TFs within the same family.

Reviewer #2 (Public review):

The manuscript by Jackman et al. explores the role of a candidate enhancer of dlx2b in zebrafish tooth formation.

They have mapped the dental epithelium and mesenchyme activity of a 4kb promoter proximal region previously identified as a candidate enhancer region. They identified candidate TFBS and candidate transcription factors regulating this enhancer and proposed that their findings reveal principles of enhancer function during vertebrate organogenesis (tooth development) and the power of dissecting cis regulatory architecture. The study offer valuable genetic tagging resource for studying tooth development while further experiments and analyses would be needed to support the suggestion for novel findings on in cis-regulatory principles of tooth development. In the lack of functional evidence on endogenous target gene pr tooth development, some of the claims of the paper may need rephrasing.

(1) The candidate enhancer region has previously been published, this study narrows the enhancer effect to a well-conserved region within. To what degree the element is unique in the locus for tooth development and to what degree this element is required for tooth morphogenesis, is not addressed.

(2) The knock-in approach is convenient for reporter activity based analyses, however it lacks the precision that would be necessary to conclude on enhancer- autonomous effects or enhancer effects on the endogenous target promoter. The HSP promoter inserted in within a 5kb(?) insert in the UTR region of dlx2b creates an chimeric E-P context. The expression profile of the knock-in reporter is substantially different from the endogenous gene (Figure 1B and C) suggesting E-P interaction dependent expression profile, which may confuse what in the expression comes solely from the enhancer and not as a result of the HSP promoter interaction with the enhancer. An alternative heterologous promoter would help in defining the enhancer specific effects.

(3) Function of the candidate enhancer: The MTE enhancer effect is measured by gain of function towards dlx2b regulation. The deletion assays are limited to plasmids designed to test the enhancer in isolation from the endogenous enhancer architecture, or to a deletion in the knock-in, which may be impacted by the chimeric regulatory interaction with a heterologous HSP promoter. As a result we do not learn whether the enhancer targets or needs for endogenous target gene activity. This design allows a conclusion on tissue activity of the enhancer but not the requirement for tooth development.

(4) Since the locus is scattered by candidate enhancers (see genome annotation resources) it is feasible that additional E-P interactions lead to potential enhancer redundancies with the MTE. For a conclusive functional test/requirement of the MTE enhancer, the authors would need to delete it in the endogenous locus context. The knock-in could theoretically be used for an enhancer function on dlx2b activity, if the authors show that there is interaction with the endgogenous promoter (3C type experiment); and that the MTE enhancer-driven GFP activity was identical to the endogenous tagged dlx2b activity. This does not appear to be the case, as ectopic expression in Fig 1C as compared to B is shown. Of note, RNA detection by WISH would be more precise for comparisons. The figure likely compares protein (legend is unclear, but text suggests protein) to mRNA, which is imprecise.

(5) There is an experimental design question arising with generating the MTE deletion in the knock-in (line 391): the authors describe generating the transgenic lines by screening for reduced reporter activity first. This suggests the authors pre-emptively looked for an effect as result they predicted when generating the transgenic lines, which would create a circular argument. All transgenic lines carrying the deletion (tested by sequencing first) would need to be assayed for activity change and then can conclusion could be made on effect of MTE loss by statistical analyses of reporter activities in the generated lines.

(6) Most transgenic work described are based on single transgenic lines. Enhancer promoter contexts may be affected either by position effects (in case of the reporter constructs) or by the heterologous promoter context of the knock which may be affected by unexpected recombination events. Such unintended confound effects can be excluded by replicates.

(7) GFP protein detection does not allow precise spatio-temporal resolution due to varying protein stability in tissues, which potentially impacts endogenous gene activity comparison, and accurate determination of activity dynamics towards conclusions on lineage determining/maintenance roles of the dlx2b enhancer.

(8) The expression pattern change upon MTE loss (retention of mesenchyme, loss of epithelium) is an interesting observation, which would benefit from more comprehensive analysis of the grammar (TFBS contributions) to the pattern variation by dissection of the combination of TFBS contributions. Without such, enhancer grammar remains mostly unclear, thus, principles of morphogenesis may not have been uncovered.

(9) The diagrammatic models of the conclusions are illustrating simple logic which does not add to the text.

(10) Author contributions need to be explained in more detail to be sufficiently granular for fair credit.

Reviewer #3 (Public review):

In the manuscript entitled "A Minimal tooth Enhancer Regulates dlx2b Expression During Zebrafish Tooth 1 Formation: Insights into Cis-Regulatory Logic in Organogenesis", the authors explore the cis-regulatory logic of a dlx2b minimal enhancer capable of directing dlx2b gene expression to the developing tooth germs. The study combines (1) CRISPR-mediated GFP knock-in to track endogenous gene expression; (2) a promoter-bashing approach to identify a minimal tooth enhancer (MTE); (3) site-directed mutagenesis coupoled with transgenesis to assess the individual role of conserved TF binding sites; and (4) in vivo deletgion of the MTE to examine the consequences for gene expression. Overall, this is a technically solid study that provides some novel insights into tooth development and extends previous observations by the authors (Jackman & Stock, 2006; PNAS). However, the added value of the manuscript is limited by both the narrow experimental scope and the relatively modest impact of the findings for the broader field of developmental biology.

Main concerns:

(1) My main concern is that the study restricts the search for cis-regulatory information to the 5' region 4kb upstream of the TSS of the gene, rather than encompassing the full genomic locus. This is particularly limiting given that a knock-in allele was generated, which in principle allows interrogation of regulatory elements across the entire locus, and that the authors acknowledge the availability of genome-wide regulatory datasets (e.g. DANIO-CODE) in the Discussion. Despite this, no systematic effort is made to test additional regulatory elements beyond the proximal promoter/enhancers.<br /> This has important implications for the interpretation of the current work as: (a) dlx2b, as many developmental genes, resides in a gene desert enriched in open chromatin regions that may function as distal enhancers, and (b) the deletion of the MTE unmasked a cis-regulatory activity which nature cannot be explained with the information provided, and that may seem relevant for the expression of the gene in the dental mesenchyme.

(2) A second concern is the absence of information on the functional consequences of deleting the gene or the MTE on tooth primordium development. From the description of the KI strategy, it is unclear whether the GFP insertion results in a functional fusion protein. The cytoplasmic GFP distribution and the schematic in Figure S1 instead suggest the presence of a terminal stop codon in the GFP sequence, which would result in a dlx2b loss-of-function allele. If this interpretation is correct, the manuscript does not describe the developmental consequences in homozygous embryos. Similar concerns apply to the MTE deletion: it remains unclear whether loss of this enhancer results in any detectable morphological or developmental defects.

[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.]

Reviewer #1 (Public review):

Summary:

The manuscript by Ma et al. provides robust and novel evidence that the noctuid moth Spodoptera frugiperda (Fall Armyworm) possesses a complex compass mechanism for seasonal migration that integrates visual horizon cues with Earth's magnetic field (likely its horizontal component). This is an important and timely study: apart from the Bogong moth, no other nocturnal Lepidoptera has yet been shown to rely on such a dual-compass system. The research therefore expands our understanding of magnetic orientation in insects with both theoretical (evolution and sensory biology) and applied (agricultural pest management, a new model of magnetoreception) significance.

The study uses state-of-the-art methods and presents convincing behavioural evidence for a multimodal compass. It also establishes the Fall Armyworm as a tractable new insect model for exploring the sensory mechanisms of magnetoreception, given the experimental challenges of working with migratory birds. Overall, the experiments are well designed, the analyses are appropriate, and the conclusions are generally well supported by the data.

Strengths:

• Novelty and significance: First strong demonstration of a magnetic-visual compass in a globally relevant migratory moth species, extending previous findings from the Bogong moth and opening new research avenues in comparative magnetoreception.<br /> • Methodological robustness: Use of validated and sophisticated behavioural paradigms and magnetic manipulations consistent with best practices in the field. The use of 5 min bins to study a dynamic nature of magnetic compass which is anchored to a visual cue but updated with latency of several minutes is an important finding and a new methodological aspect in insect orientation studies.<br /> • Clarity of experimental logic: The cue-conflict and visual cue manipulations are conceptually sound and capable of addressing clear mechanistic questions.<br /> • Ecological and applied relevance: Results have implications for understanding migration in an invasive agricultural pest with expanding global range.<br /> • Potential model system: Provides a new, experimentally accessible species for dissecting the sensory and neural bases of magnetic orientation.

Weaknesses:

Overall, this is a strong study, and the authors have completed an excellent major revision.

Reviewer #2 (Public review):

Summary:

The work titled "Geomagnetic and visual cues guide seasonal migratory orientation in the nocturnal fall armyworm, the world's most invasive insect" provided experimental evidence on how geomagnetic and visual cues are integrated, and visual cues are indispensable for magnetic orientation in the nocturnal fall armyworm.

Strengths:

It has been demonstrated that the Australian Bogon moth could integrate global stellar cues with the geomagnetic field for long distance navigation. However, data are lacking for other insects. This study suggested that the integration of geomagnetic and visual cues may represent a conserved navigational mechanism broadly employed across migratory insects.

Weaknesses:

The visual cues used in the indoor experimental system designed by the authors may have some limitations in ecological relevance. The author may need more explanations on this experimental system.

In the revised manuscript, the authors have added explanations in the discussion section. I am fine with the revision.

Reviewer #1 (Public review):

Summary:

The researchers aimed to identify which neurotransmitter pathways are required for animals to withstand chronic oxidative stress. This work thus has important implications for disease processes that are caused/linked to oxidative stress. This work identified specific neurotransmitters and receptors that coordinate stress resilience, both prior to and during stress exposure. Further, the authors identified specific transcriptional programs coordinated by neurotransmission that may provide stress resistance.

Strengths:

The manuscript is very clearly written with a well-formulated rationale. Standard C. elegans genetic analysis and rescue experiments were performed to identify key regulators of the chronic oxidative stress response. These findings were enhanced by transcriptional profiling that identified differentially expressed genes that likely affect survival when animals are exposed to stress.

Weaknesses:

Where the gar-3 promoter drives expression was not discussed in the context of the rescue experiments in Fig 7.

Comments on revisions:

This issue has now been appropriately addressed in the revision.

Reviewer #2 (Public review):

In this paper, Biswas et al. describe the role of acetylcholine (ACh) signaling in protection against chronic oxidative stress in C. elegans. They showed that disruption of ACh signaling in either unc-17 mutant or gar-3 mutants led to sensitivity to toxicity caused by chronic paraquat (PQ) treatment. Using RNA seq, they found that approximately 70% of the genes induced by chronic PQ exposure in wild type failed to upregulate in these mutants. The overexpression of gar-3 selectively in cholinergic neurons was sufficient to promote protection against chronic PQ exposure in an ACh-dependent manner. The study points to a previously undescribed role for ACh signaling in providing organism-wide protection from chronic oxidative stress likely through the transcriptional regulation of numerous oxidative stress-response genes. The paper is well-written, and the data are robust, though some conclusions seem preliminary and are not fully support the current data (see below). While the study identifies the muscarinic ACh receptor gar-3 as an important regulator of the response to PQ, the specific neurons in which gar-3 functions were not unambiguously identified, and the sources of ACh that regulate GAR-3 signaling and the identities of the tissues targeted by gar-3 were not addressed.

Comments on revisions:

The authors addressed my comments adequately in their revised submission. Please include representative images to accompany the quantification of the new results presented in Fig S4A.

Reviewer #1 (Public review):

This study makes a fundamental contribution to our understanding of interocular suppression, particularly continuous flash suppression (CFS). Using neuroimaging data from two macaque monkeys, the study provides compelling evidence that CFS suppresses orientation responses in neurons within V1. These findings enrich the CFS literature by demonstrating that neural activity under CFS may prevent high-level visual and cognitive processing.

Comments on revisions:

The authors have addressed all my previous comments.

Reviewer #2 (Public review):

Summary:

The goal of this study was to investigate the degree to which low-level stimulus features (i.e., grating orientation) are processed in V1 when stimuli are not consciously perceived under conditions of continuous flash suppression (CFS). The authors measured the activity of a population of V1 neurons at single neuron resolution in awake fixating monkeys while they viewed dichoptic stimuli that consisted of an oriented grating presented to one eye and a noise stimulus to the other eye. Under such conditions, the mask stimulus can prevent conscious perception of the grating stimulus. By measuring the activity of neurons (with Ca2+ imaging) that preferred one or the other eye, the authors tested the degree of orientation processing that occurs during CFS.

Strengths:

The greatest strength of this study is the spatial resolution of the measurement and the ability to quantify stimulus representations during CSF in populations of neurons preferring the eye stimulated by either the grating or the mask. There have been a number of prominent fMRI studies of CFS, but all of them have had the limitation of pooling responses across neurons preferring either eye, effectively measuring the summed response across ocular dominance columns. The ability to isolate separate populations offers an exciting opportunity to study the precise neural mechanisms that give rise to CFS, and potentially provide insights into nonconscious stimulus processing.

Weaknesses:

However, while this is an impressive experimental setup, the major weakness of this study is that the experiments don't advance any theoretical account of why CFS occurs or what CFS implies for conscious visual perception. There are two broad camps of thinking with regard to CFS. On the one hand, Watanabe et al., 2011 reported that V1 activity remained intact during CFS, implying that CFS interrupts stimulus processing downstream of V1. On the other hand, Yuval-Greenberg and Heeger (2013) showed that V1 activity is in fact reduced during CFS. By using a parametric experimental design, they measured the impact of the mask on the stimulus response as a function of contrast, and concluded that the mask reduces the gain of neural responses to the grating stimulus. They presented a theoretical model in which the mask effectively reduced the SNR of the grating, making it invisible in the same way that reducing contrast makes a stimulus invisible.

In the first submission of the manuscript, the authors incorrectly described the Yuval-Greenberg & Heeger (2013) paper and Watanabe et al. (2011) papers, suggesting that they had observed the same or similar effects of CFS on V1 activity, when in fact they had described opposite results. Reviewer 1 also observed that the authors appeared to be confused in their reading of these highly relevant papers. In the revision, the authors have reworked this paragraph, now correctly describing these sets of opposing results. However, I still do not understand what the authors are trying to argue: "...these studies were not designed to quantify the pure effect of CFS on stimulus-evoked V1 responses." I do not understand what is meant by "pure" in this case. Regardless, it is clear that the measurements in the present study strongly support the interpretation of Yuval-Greenberg & Heeger (i.e., that V1 activity is degraded by CFS, 'akin' to a loss in the contrast-to-noise ratio of neural activity). It would be appropriate for the authors to communicate this clearly.

I continue to be of the opinion that this study is lacking an adequate model of interocular interactions that might explain the Ca2+ imaging. The machine learning results are not terribly surprising - multivariate methods, such as SVMs, are more sensitive than univariate approaches. So it is plausible that an SVM can support decoding of the coarse orientation information, even when no tuning is evident in the univariate analyses. However, the link between this result and the underlying neurophysiology is opaque. The failure to model the neural data with an explicit model is a missed opportunity.

Reviewer #3 (Public review):

Summary:

In this study, Tang, Yu & colleagues investigate the impact of continuous flash suppression (CFS) on the responses of V1 neurons using 2-photon calcium imaging. The report that CFS substantially suppressed V1 orientation responses. This suppression happens in a graded fashion depending on the binocular preference of the neuron: neurons preferring the eye that was presented with the marker stimuli were most suppressed, while the neurons preferring the eye to which the grating stimuli were presented were least suppressed. Binocular neuron exhibited an intermediate level of suppression.

Strengths:

The imaging techniques are cutting-edge.

Weaknesses:

The strength of CFS suppression varies across animals, but the authors attribute this to comparable heterogeneity in the human psychophysics literature.

Comments on revisions:

The authors have addressed my comments from the previous round of review, and I have no further comments

Reviewer #1 (Public review):

This study by Li and colleagues examines how defensive responses to visual threats during foraging are modulated by both reward level and social hierarchy. Using a naturalistic paradigm, the authors test how the availability of water or sucrose, with sucrose being more rewarding than water, shapes escape behavior in mice exposed to looming stimuli of different intensities, which are used to probe perceived threat level and defensive responses. In parallel, the study compares dominant and subordinate animals to assess how social rank biases the trade off between reward seeking and threat avoidance. By combining detailed behavioral analyses with computational modeling, the work addresses how reward level and social context jointly influence escape decisions in an ethologically relevant setting.

Across the different experimental conditions, perceived threat level is the main determinant of behavior. The authors show that looming stimuli associated with higher threat (contrast) consistently elicit faster and more robust escape responses than lower threat stimuli. This effect is particularly evident during early exposures, when animals are highly vigilant and have not yet habituated to the looming stimulus (learned that it is not dangerous). Later they described that as animals gain experience and habituate, behavior becomes more flexible, and reward level begins to exert a graded modulation of the escape response. Importantly, the authors show that under high threat conditions increasing reward value leads to more frequent and faster escape rather than greater reward pursuit. This finding is particularly relevant, as it suggests that highly valued rewards can heighten vigilance and thereby enhance responsiveness to threat, highlighting that reward does not simply compete with defensive behavior but can also reshape it depending on the perceived level of danger, in contrast to low threat conditions, where threat can be more easily outweighed by reward. Thus, an important conceptual contribution of the study is the introduction of vigilance as a useful framework to interpret these effects. Vigilance is treated as a behavioral state reflecting heightened attention to potential danger. In line with what is known from natural foraging, mice initially maintain high vigilance when confronted with an innate threat. This perspective helps clarify a finding that might otherwise appear counterintuitive. One might expect higher rewards to motivate animals to tolerate risk, explore more, and habituate faster in any scenario. Instead, the data suggest that highly rewarding outcomes can elevate vigilance, making animals more responsive to threat and leading to faster or more frequent escape under high threat conditions. In this sense, reward does not simply compete with threat but can also amplify sensitivity to it, depending on the internal state of the animal.

The social results are particularly interesting in this context as well. Dominant mice consistently prioritize avoidance over reward, showing stronger escape responses and slower habituation than subordinates. This behavior is well captured by the vigilance framework proposed by the authors: dominant animals appear to maintain higher vigilance, which biases decisions toward threat avoidance. The authors further suggest that stable social relationships sustain high vigilance and slow habituation, framing this as an evolutionarily conserved strategy that may enhance survival. This interpretation provides a valuable perspective on how social structure shapes defensive behavior beyond immediate physical interactions. At the same time, there are important limitations to this interpretation. All experiments were conducted in male mice, and it is possible that the relationship between social hierarchy, vigilance, and defensive behavior would differ substantially in females. In addition, the idea that stable social relationships maintain elevated vigilance does not straightforwardly align with broader views of social stability as protective for mental health and as a buffer against anxiety and stress. These points do not undermine the findings but suggest that the social effects described here should be interpreted with caution and within the specific context of the task and sex studied.

Another important limitation is that the neural mechanisms underlying these effects remain speculative. The manuscript includes an extensive discussion of candidate circuits, particularly involving the superior colliculus and downstream structures, but this section is necessarily based on prior literature rather than on data presented in the study. Given the complexity of the circuits involved in integrating internal state, reward, social context, and vigilance, the current work should be viewed as providing a strong behavioral and conceptual framework rather than direct insight into underlying neural mechanisms.

Methodologically, the behavioral paradigm is well suited for studying escape decisions in socially housed animals, and the machine learning based classification of defensive responses is a clear strength. The computational model provides a useful formalization of how threat level, reward level, and vigilance interact and may be valuable for other laboratories studying escape, approach avoidance, or conflict situations, particularly as a way to classify behavioral outcomes after pose estimation. More generally, the work will be of interest to the neuroethology community for its detailed characterization of escape behavior under naturalistic conditions.

Given the ethological nature of the study and the high inter individual variability reported by the authors, clarity and precision in the methods are especially important for reproducibility. While the revised manuscript addresses many earlier concerns, some aspects remain slightly difficult to follow. For example, the main text states that animals were not water deprived to avoid differences in internal state, whereas parts of the methods describe conditions in which animals were water deprived, suggesting that internal state manipulation may differ across experiments. Clearer separation and explanation of these conditions would further strengthen confidence in the work.

Overall, this study provides a rich and thoughtful analysis of how reward level and social hierarchy modulate defensive behavior through changes in vigilance. It offers a useful conceptual advance for thinking about escape behavior in naturalistic settings and lays a solid foundation for future work aimed at linking these behavioral states to underlying neural circuits.

Reviewer #2 (Public review):

Zhe Li and colleagues investigate how mice exposed to visual threats and rewards balance their decisions in favour of consuming rewards or engaging in defensive actions. By varying threat intensity and reward value, they first confirm previous findings showing that defensive responses increase with threat intensity and that there is habituation to the threat stimulus. They then find that water-deprived mice have a reduced probability of escaping from low contrast visual looming stimuli when water or sucrose are offered in the environment, but that when the stimulus contrast is high, the presence of sucrose or water increases the probability of escape. By analysing behaviour metrics such as the latency to flee from the threat stimulus, they suggest that this increase in threat sensitivity is due to increased vigilance. Analysis of this behaviour as a function of social hierarchy shows that dominant mice have higher threat sensitivity, which is also interpreted as being due to increased vigilance. These results are captured by a drift diffusion model variant that incorporates threat intensity and reward value.

The main contribution of this work is quantifying how the presence of water or sucrose in water-deprived mice affects escape behaviour. The differential effects of reward between the low and high contrast conditions are intriguing, but I find the interpretation that vigilance plays a major in this process not supported by the data. The idea that reward value exerts some form of graded modulation of the escape response is also not supported by the data. In addition, there is very limited methodological information, which makes assessing the quality of some of the analyses difficult, and there is no quantification on the quality of the model fits.

(1) The main measure of vigilance in this work is reaction time. While reaction time can indeed be affected by vigilance, reaction times can vary as a function of many variables, and be different for the same level of vigilance. For example, a primate performing the random dot motion task exhibits differences in reaction times that can be explained entirely by the stimulus strength. Reaction time is therefore not a sound measure of vigilance, and if a goal of this work is to investigate this parameter, then it should be measured. There is some attempt at doing this for a subset of the data in Figure 3H, by looking at differences in the action of monitoring the visual field (presumably a rearing motion, though this is not described) between the first and second trials in the presence of sucrose. I find this an extremely contrived measure. What is the rationale for analysing only the difference between the first and second trials? Also, the results are only statistically significant because the first trial in the sucrose condition happens to have zero up action bouts, in contrast to all other conditions. I am afraid that the statistics are not solid here. When analysing the effects of dominance, a vigilance metric is the time spent in the reward zone. Why is this a measure of vigilance? More generally, measuring vigilance of threats in mice requires monitoring the position of the eyes, which previous work has shown is biased to the upper visual field, consistent with the threat ecology of rodents.

(2) In both low and high contrast conditions, there are differences in escape behaviour between no reward and water or sucrose presence, but no statistically significant differences between water and sucrose (eg: Figure 3B). I therefore find that statements about reward value are not supported by the data, which only show differences between the presence or absence of reward. Furthermore, there is a confound in these experiments, because according to the methods, mice in the no-reward condition were not water-deprived. It is thus possible that the differences in behaviour arise from differences in the underlying state.

(3) There is very little methodological information on behavioural quantification. For example, what is hiding latency? Is this the same are reaction time? Time to reach the safe zone? What exactly is distance fled? I don't understand how this can vary between 20 and 100cm. Presumably, the 20cm flights don't reach the safe place, since the threat is roughly at the same location for each trial? How is the end of a flight determined? How is duration measured in reward zone measures, e.g., from when to when? How is fleeing onset determined?

(4) There is little methodological information on how the model was fit (for example, it is surprising that in the no reward condition, the r parameter is exactly 0. What this constrained in any way), and none of the fit parameters have uncertainty measures so it is not possible to assess whether there are actually any differences in parameters that are statistically significant.

Comments on the revised manuscript:

The manuscript has been revised and improved significantly by the addition of methodological details and new analysis. I remain, however, unconvinced by the argument that increased vigilance in the presence of reward leads to heightened escape behaviour.

In response to my criticism that the work does not measure vigilance directly, the authors have included measures of foraging interval and foraging speed, which they state are "two direct behavioral analyses of vigilance". I disagree - like reaction time, foraging speed and foraging interval can be modulated, for example, by changes in threat sensitivity. Increased threat sensitivity comes with diverse behavioral changes that may well include increased vigilance, but foraging interval and foraging speed can certainly change without the animal expressing increased vigilance behaviors. A bigger issue I still have though, is with the conclusion that the presence of reward increases "direct escape behaviors". Comparing the no reward, water and sucrose groups indeed shows a difference (which is now clear after the split into early and late phases), but the issue is that these are different mice. As the text is written, is sounds like introducing reward will acutely increase escape. But if we look at the raw data show in Figure 2C, what I think is happening is that the presence of reward is decreasing habituation to the stimulus. The data for trials 1 and 10 in the three conditions show this - there is habituation with no reward (reaction times are all shifting to the right), a bit less with water and very little with sucrose. This is interesting in its own right and we can speculate why it might be happening, but I think this is conceptually different from what the authors are proposing.

Reviewer #3 (Public review):

Male mice were tested in a classic behavioral "flee the looming stimulus" paradigm. This is a purely behavioral study; no neural analyses were done. Mice were housed socially, but faced the looming stimulus individually, using an elegant automated tunnel (see videos for clarity).

The additional changes made to the paper clarify the work done. While there are some limitations (male mice, weird stimulus), the general results are interesting and a valuable addition to the experimental literature. The main claim of the paper is that the different rewards (none, water, sucrose) did not change the escape properties early in learning, but did late, particularly that in the late (already experienced) conditions, reward value (assuming sucrose > water > no reward) interacted with the salience of the looming stimulus (light gray, dark gray). (Panels 3D, 3G, 3K, 3N).

For readers, I want to note that one of the most interesting results is actually in Figure S2, where they find that a looming stimulus behind the mouse still makes a mouse run to the nest. In these conditions, the mouse runs past the looming stimulus to get to safety! (I also do love the video of the mouse running around the barriers like a snake to get home.)

I have a few minor clarification questions and a few notes that I think would be useful additions for authors and readers to think about.

Dominance: What does the mouse social science literature say about the "test tube" test? What can we conclude from this test? This would be useful when trying to understand what is causing the dominance/submissive difference in responses. Figure 4 shows that the dominant mice are more risk-averse than the submissive mice. Is "dominance" in the test-tube actually a measure of risk-seeking? Is the issue that the submissive mice don't think they can get back to the food-site easily, so they are less willing to sacrifice the current (if dangerous) foraging opportunity? Is the issue that the submissive mice can't get back to the nest? As I understand it, the nest was always available to all the mice, so I suspect inability to get to the nest is an unlikely hypotheses. Is the issue that the submissive mice also don't feel safe in the nest?

Limitations of the study: There is an acknowledged limitation to male mice, and the limitations of the small data sets that are typical of such experiments. In addition, however, it is also worth noting the strangeness of the looming stimulus, which is revealed clearly in the videos. The stimulus is a repeating growing circle, growing in a single location within the environment. The stimulus repeats 10 times, once per second. This is not what an attacking hawk or owl would look like. (I now have this image of an owl diving down, and then teleporting up and diving down again.) Note - I am fine with this stimulus. It produces an interesting experiment and interesting results. I do not think the authors need to change anything in their paper, but readers need to recognize that this is not a "looming predator".

These "limitations" are better seen as "caveats" when folding these results in with the rest of the literature that has gone before and the literature to come. (Generally, I do not believe that science works by studies making discoveries that change how we think about problems - instead, science works by studies adding to the literature that we integrate in with the rest of the literature.) Thus, these caveats should not be taken as problems with the study or as fixes that need to be done. Instead, they are notes for future researchers to notice if differences are found in any future studies.

Thus, my only suggestion is that I think authors could write a more careful paper by using the past and subjunctive tense appropriately. Experimental observations should be in past tense, as in "the influence of reward was context-dependent and emerged in the late phase" instead of "the influence of reward is context-dependent and emerges in the late phase" - it emerged in the late phase this once - it might not in future experiments, not due to any fault in this experiment nor due to replicability problems, but rather due to unexpected differences between this and those future experiments. At which point, it will be up to those future experiments to determine the difference. Similarly, large conclusions should be in the subjunctive tense, as in "these data suggest that threat intensity is likely to be the primary determinant of decision making" rather than "threat intensity is the primary determinant of decision making", because those are hypotheses not facts.

Reviewer #1 (Public review):

In this manuscript, the authors report that GPR55 activation in presynaptic terminals of Purkinje cells decrease GABA release at the PC-DCN synapse. The authors use an impressive array of techniques (including highly challenging presynaptic recordings) to show that GPR55 activation reduces the readily releasable pool of vesicle without affecting presynaptic AP waveform and presynaptic Ca2+ influx. This is an interesting study, which is seemingly well-executed and proposes a novel mechanism for the control of neurotransmitter release. However, the authors' main conclusions are heavily, if not solely, based on pharmacological agents that most often than not demonstrate affinity at multiple targets. Below are points that the authors should consider in a revised version.

Major points:

(1) There is no clear evidence that GPR55 is specifically expressed in presynaptic terminals at the PC-DCN synapse. The authors cited Ryberg 2007 and Wu 2013 in the introduction, mentioning that GPR55 is potentially expressed in PCs. Ryberg (2007) offers no such evidence, and the expression in PC suggested by Wu (2013) does not necessarily correlate with presynaptic expression. The authors should perform additional experiments to demonstrate presynaptic expression of GPR55 at PC-DCN synapse.

(2) The authors' conclusions rest heavily on pharmacological experiments, with compounds that are sometimes not selective for single targets. Genetic deletion of GPR55 would be a more appropriate control. The authors should also expand their experiments with occlusion experiments, showing if the effects of LPI are absent after AM251 or O-1602 treatment. In addition, the authors may want to consider AM281 as a CB1R antagonist without reported effects at GPR55.

(3) It is not clear how long the different drugs were applied, and at what time the recording were performed during or following drug application. It appears that GPR55 agonists can have transient effects (Sylantyev, 2013; Rosenberg, 2023), possibly due to receptor internalization. The timeline of drug application should be reported, where IPSC amplitude is shown as a function of time and drug application windows are illustrated.

(4) A previous investigation on the role of GPR55 in the control of neurotransmitter release is not cited nor discussed Sylantyev et al., (2013, PNAS, Cannabinoid- and lysophosphatidylinositol-sensitive receptor GPR55 boosts neurotransmitter release at central synapses). Similarities and differences should be discussed.

Minor point:

(1) What is the source of LPI? What isoform was used? The multiple isoforms of LPI have different affinities for GPR55.

Comments on revisions:

In this revised version, the authors have addressed my major concerns. Notably, they used CRISPR/Cas9 genetic knockdown of GPR55 to independently validate their original findings. The main conclusions are now well supported and represent an important contribution to the field.

Reviewer #2 (Public review):

Summary:

This paper investigates the mode of action of GPR55, a relatively understudied type of cannabinoid receptors, in presynaptic terminals of Purkinje cells. The authors use demanding techniques of patch clamp recording of the terminals, sometimes coupled with another recording of the postsynaptic cell. They find a lower release probability of synaptic vesicles after activation of GPR55 receptors, while presynaptic voltage-dependent calcium currents are unaffected. They propose that the size of a specific pool of synaptic vesicles supplying release sites is decreased upon activation of GPR55 receptors.

Strengths:

The paper uses cutting edge techniques to shed light on a little studied, potentially important type of cannabinoid receptors. The results are clearly presented, and the conclusions are sound.

Weaknesses:

The nature of the vesicular pool that is modified following activation of GPR55 is not definitively characterized.

Comments on revisions:

The authors have done a good job in answering the criticisms of reviewers. Consequently, the revised version offers a substantial improvement over the first version.

Reviewer #3 (Public review):

Inoshita and Kawaguchi investigated the effects of GPR55 activation on synaptic transmission in vitro. To address this question, they performed direct patch-clamp recordings from axon terminals of cerebellar Purkinje cells and fluorescent imaging of vesicular exocytosis utilizing synapto-pHluorin. They found that exogenous activation of GPR55 suppresses GABA release at Purkinje cell to deep cerebellar nuclei (PC-DCN) synapses by reducing the readily releasable pool (RRP) of vesicles. This mechanism may also operate at other synapses.

Strengths:

The main strength of this study lies in combining patch-clamp recordings from axon terminals with imaging of presynaptic vesicular exocytosis to reveal a novel mechanism by which activation of GPR55 suppresses inhibitory synaptic strength. The results strongly suggest that GPR55 activation reduces the RRP size without altering presynaptic calcium influx.

Weaknesses:

The study relies on the exogenous application of GPR55 agonists. It remains unclear whether endogenous ligands released by physiological or pathological processes would have similar effects. There is also little evidence that GPR55 is expressed in Purkinje cell axon boutons. This study would benefit from the use of GPR55 knockout (KO) mice. The downstream mechanism by which GPR55 mediates the suppression of GABA release remains unknown.

Comments on revisions:

The authors have addressed all my concerns effectively. I have no further comments and want to commend their comprehensive study.

Reviewer #1 (Public review):

Summary:

The "number sense" refers to an imprecise and noisy representation of number. Many researchers propose that the number sense confers a fixed (exogenous) subjective representation of number that adheres to scalar variability, whereby the variance of the representation of number is linear in the number.

This manuscript investigates whether the representation of number is fixed, as usually assumed in the literature, or whether it is endogenous. The two dimensions on which the authors investigate this endogeneity are the subject's prior beliefs about stimuli values and the task objective. Using two experimental tasks, the authors collect data that are shown to violate scalar variability and are instead consistent with a model of optimal encoding and decoding, where the encoding phase depends endogenously on prior and task objectives. I believe the paper asks a critically important question. The literature in cognitive science, psychology, and increasingly in economics, has provided growing empirical evidence of decision-making consistent with efficient coding. However, the precise model mechanics can differ substantially across studies. This point was made forcefully in a paper by Ma and Woodford (2020, Behavioral & Brain Sciences), who argue that different researchers make different assumptions about the objective function and resource constraints across efficient coding models, leading to a proliferation of different models with ad-hoc assumptions. Thus, the possibility that optimal coding depends endogenously on the prior and the objective of the task, opens the door to a more parsimonious framework in which assumptions of the model can be constrained by environmental features. Along these lines, one of the authors' conclusions is that the degree of variability in subjective responses increases sublinearly in the width of the prior. And importantly, the degree of this sublinearity differs across the two tasks, in a manner that is consistent with a unified efficient coding model.

Comments on revisions:

The authors have done an excellent job addressing my main concerns from the previous round. The new analyses that address the alternative model of "no cognitive noise and only motor noise" are compelling and provide quantitative evidence that bolsters the paper's overall contribution. The authors also went above and beyond by reanalyzing the Frydman and Jin (2022) dataset to provide new and very interesting analyses that provide an additional out of sample test of the model proposed in the current paper.

Reviewer #2 (Public review):

Summary:

This paper provides an ingenious experimental test of an efficient coding objective based on optimization as a task success. The key idea is that different tasks (estimation vs discrimination) will, under the proposed model, lead to a different scaling between the encoding precision and the width of the prior distribution. Empirical evidence in two tasks involving number perception supports this idea.

Strengths:

- The paper provides an elegant test of a prediction made by a certain class of efficient coding models previously investigated theoretically by the authors.<br /> The results in experiments and modeling suggest that competing efficient coding models, optimizing mutual information alone, may be incomplete by missing the role of the task.

- The paper carefully considers how the novel predictions of the model interact with the Weber/Fechner law.

Weaknesses:

- The claims would be even more strongly validated if data were present at more than two widths in the discrimination experiment (also noted in Discussion).

Reviewer #3 (Public review):

Summary:

This work investigates whether human imprecision in numeric perception is a fixed structural constraint or an endogenous property that adapts to environmental statistics and task objectives. By measuring behavioral variability across different uniform prior distributions in both estimation and discrimination tasks, the authors show that perceptual imprecision increases sublinearly with prior width. They demonstrate that the specific exponents of this scaling (1/2 for estimation and 3/4 for discrimination) can be derived from an efficient-coding model, wherein decision-makers optimally balance task-specific expected rewards against the metabolic costs of neural coding. The revised manuscript expands this framework to accommodate logarithmic representations and validates the core model against an independent dataset of risky choices.

Strengths:

The authors have effectively addressed my previous concerns with rigorous additions:

(1) The mathematical formulation has been revised into a discrete signal accumulation framework, making the objective function and resource trade-offs much more transparent and mathematically tractable.

(2) The incorporation of the logarithmic representation resolves prior ambiguities regarding structural constraints.

(3) The new split-half analysis effectively addresses the temporal dynamics of adaptation. The stability of the sublinear scaling across the experiment provides solid evidence that human subjects utilize rapid, top-down modulation to adjust their encoding strategy when explicitly informed about the environment.

(4) Validating the derived scaling exponents on an independent risky-choice dataset robustly supports the generalizability of the theoretical framework beyond a single cognitive domain.

Weaknesses:

The methodological and theoretical issues raised in the first round have been thoroughly resolved, and the evidence supporting the claims regarding response variance is convincing.

There is one remaining theoretical point that warrants discussion to provide a complete picture of the proposed generative model. The manuscript exquisitely models and predicts response variance (imprecision), but it remains largely silent on the closed-form predictions for the mean estimation (i.e., bias). Under the assumption of optimal Bayesian decoding combined with specific encoding schemes (e.g., linear vs. logarithmic), the model implicitly generates mathematical predictions for the subjects' mean estimates. Specifically, varying the scaling exponent (α) and the prior width (w) should systematically alter the predicted bias in different conditions.

While fitting or explicitly explaining this mean bias is not strictly necessary for the core claims regarding variance scaling, acknowledging what the optimal decoder analytically predicts for the mean estimation-and how it aligns or contrasts with typical empirical observations-would strengthen the theoretical transparency of the paper.

Reviewer #1 (Public review):

Summary:

The authors aimed to assess the variability in expression of surface protein multigene families between amastigote and trypomastigote Trypanosoma cruzi, as well as between individuals within each population. The analysis presented shows higher expression of multigene family transcripts in trypomastigotes compared to amastigotes and that there is variation in which copies are expressed between individual parasites. Notably, they find no clear subpopulations expressing previously characterised trans-sialidase groups and that no patterns of coexpressed TcS genes were evident within individual cells or subpopulations. They also note that TcS encoded in the core genome are more often expressed, compared to TcS genes encoded in other genome compartments.

Strengths:

Additionally, the authors successfully process methanol fixed parasites with the 10x Genomics platform. This approach is valuable for other studies where using live parasites for these methods is logistically challenging.

In this second submission the authors show the kallisto mapping approach used is as robust as possible, and that this approach outperforms STAR mapping.

Weaknesses:

The authors describe a single experiment, which lacks repeats, controls or complementation with other approaches and the investigation is limited to the trans-sialidase transcripts.

Comments on revised version:

Thank you to the authors for taking the time to thoroughly address the peer review. The main concerns have now been addressed, and the manuscript edited to make points of confusion clearer.

Reviewer #2 (Public review):

Summary:

This manuscript presents a valuable single-cell RNA-seq study on Trypanosoma cruzi, an important human parasite. It investigates the expression heterogeneity of surface proteins, particularly those from the trans-sialidase-like (TcS) superfamily, within amastigote and trypomastigote populations. The findings suggest a previously underappreciated level of diversity in TcS expression, which could have implications for understanding parasite-host interactions and immune evasion strategies. The use of single cell approaches to delve into population heterogeneity is strong. However, the study does have some limitations that need to be addressed.

The focus on single-cell transcriptional heterogeneity in surface proteins, especially the TcS family, in T. cruzi is novel. Given the important role of these proteins in parasite biology and host interaction, the findings have potential significance.

Strengths:

The key finding of heterogeneous TcS expression in trypomastigotes is well-supported. The analysis comparing multigene families, single-copy genes, and ribosomal proteins highlights the unusual nature of the variation in surface protein coding genes.

Weaknesses:

While the manuscript identifies TcS heterogeneity, the functional implications of the different expression profiles remain speculative. The authors state it may reflect differences in infectivity, but no direct experimental evidence supports this.

The manuscript lacks any functional validation of the single-cell findings. For instance, do the trypomastigote subpopulations identified based on TcS expression exhibit differences in infectivity, host cell tropism, or immune evasion? Such experiments would greatly strengthen the study.

The authors identify a subpopulation of TcS genes that are highly expressed in many cells. However, it is unclear if these correspond to previously characterized TcS members with specific functions.

The authors hypothesize that observed heterogeneity may relate to chromatin regulation. However, the study does not directly address these mechanisms. There are interesting connections to be made with what they identify as colocalization of genes within chromatin folding domains, but the authors do not fully explore this. It would be insightful to address these mechanisms in future work. [...]

Comments on revisions:

The novel version of the manuscript has improved and satisfied this reviewer.

Reviewer #3 (Public review):

The study aimed to address a fundamental question in T. cruzi and Chagas disease biology - how much variation is there in gene expression between individual parasites? This is particularly important with respect to the surface protein-encoding genes, which are mainly from massive repetitive gene families with 100s to 1000s of variant sequences in the genome. There is very little direct evidence for how expression of these genes is controlled. The authors conducted a single cell RNAseq experiment of in vitro cultured parasites with a mixture of amastigotes and trypomastigotes. Most of the analysis focused on the heterogeneity of gene expression patterns amongst trypomastigotes. They show that heterogeneity was very high for all gene classes, but surface-protein encoding genes were the most variable. Interestingly, in the case of the trans-sialidase genes, many sequence variants were detected in fewer than 5% of parasites while a subset of 31 others was detected in >40% if parasites, hinting at compartmentalised expression control within the gene family. The biology of the parasite (e.g. extensive post-transcriptional regulation) and potential technical caveats (e.g. high dropout rates across the genome) make it difficult to infer connections to actual protein expression on the parasite surface, but the results are a significant advance for the field.

(1) Limit of detection and gene dropouts.

An average of ~1100 genes are detected per parasite which indicates a dropout rate of over 90%. It appears that RNA for the "average" single copy 'core' gene is only detected in around 3% of the parasites sampled (Figure 2c: ~100 / 3192). While comparable with some other trypanosome scRNAseq studies, this remains a caveat to the interpretation that high cell-to-cell variability in gene expression is explained by biological factors. The argument would be more convincing if the dropout rates and expression heterogeneity were minimal for highly expressed housekeeping genes. The authors are appropriately cautious in their interpretation and acknowledge the need for further validation.

(2) Heterogeneity across the board.

The authors focus on the relative heterogeneity in RNA abundance for surface proteins from the multicopy gene families vs core genes. While multicopy gene sequences do show significantly more cell-to-cell variability, there is still surprisingly high inequality of expression amongst genes in other classes including single copy housekeeping and ribosomal genes. Again the biological relevance of the comparison is uncertain and the authors acknowledge the need for further investigation.

This study provides some tantalising evidence that the expression of surface genes may vary substantially between individual parasites in a single clonal population. The study is also amongst the very first to apply scRNAseq to T. cruzi, so the broader data set will be an important resource for researchers in the field.

Comment on revised version:

The manuscript is significantly improved. The revised explanations and figures make several aspects of the data analysis and interpretation much clearer to me now. Thanks to the authors.

Reviewer #1 (Public review):

Summary:

In this manuscript, Rupasinghe and co-authors introduce a new statistical model for spiking neurons. Building on earlier work, they propose to model spikes as arising from a Poisson process whereby the firing rate is the product of stimulus drive and a stimulus-independent gain signal. The critical innovation of this work is that the gain signal is modeled in continuous time. Earlier explorations of this statistical construction treated the gain-signal as constant within a trial. This innovation is elegant and important. It makes the model richer, more plausible, and more broadly applicable. The authors show that the model parameters are recoverable from realistic amounts of data and then apply the framework to previously studied datasets. They show that the new model outperforms earlier models and alternative candidates in capturing spiking data across four visual areas of the macaque monkey. Analysis of the model parameters replicates some earlier findings and uncovers several new insights. The model and fitting methods can be broadly applied to partition different types of signals and noise from spiking data and are likely to be widely adopted in the systems neuroscience community.

Strengths:

(1) Through clever use of advanced statistical techniques, the authors manage to infer critical information from single-trial single-cell data.

(2) The question of which aspect of a spike train is signal and which is noise is omnipresent in neuroscience. By improving our ability to characterize the distinct factors that shape spiking activity, this work makes a fundamental contribution to the literature.

Weaknesses:

Overall, I find the work impressive and important. I have a couple of questions and suggestions.

(1) The work is entirely focused on single-cell data. While this is a great starting point, expanding the approach to spiking activity in neural populations is an important future goal.

(2) Line 49-53: These statements seem incorrect to me. The modulated Poisson model, as introduced in Goris et al (2014), is a process model that can perfectly be used to generate spike trains (within a trial, spiking emerges from a Poisson process, which can be homogeneous or inhomogeneous). Moreover, the model contains a parameter that represents the duration of the counting window (delta t). The dependency of over-dispersion on the size of the time bins for real neurons is shown in Figure 1b (inset plot) of that paper (and shown to resemble the model prediction). This time-dependency was further explored by the same authors in Goris et al (2018 - Journal of Vision) and also in Hénaff et al (2020 - Nature Communications ). I suggest that the authors rephrase this argument (here and at some later points in the paper). They could just say that the Goris model makes the simplistic and implausible assumption that, within a given trial, gain does not fluctuate. This is clearly an important limitation and the key difference with the continuous model introduced here.

(3) Line 54-55: I think the first part of the claim is a bit misleading. There is nothing in the Goris model that would inherently limit it to homogeneous Poisson processes, as seems to be implied by this description. The model is built on the assumption that spike generation within a trial arises from a Poisson process. This may very well be an inhomogeneous Poisson process (i.e., a stimulus-dependent time-varying firing rate). Homogeneous and inhomogeneous Poisson processes both give rise to Poisson distributed spike counts (and thus a mixture of Poisson distributions across trials in the Goris model). I suggest the authors clarify this description a bit. Note that the two model variants illustrated in Figure 1b and c were also explored in Hénaff et al (2020 - Nature Communications).

(4) The extension to the continuous case is very elegant!

(5) I find the result shown in Appendix 3 critically important. The recoverability of the model for realistic amounts of data is foundational for the rest of the paper. I would consider including this analysis in the main results section. Not all readers may check Appendix 3, but they should know about this result.

(6) Figure 3: I am wondering whether the inferred gain is capturing some response fluctuations that originate from the cell's phase-selectivity. Could the authors compute the trial-averaged inferred gain (ideally, aligned to stimulus-phase at the start of the trial if this experimental parameter varied across repeats)? If they have successfully partitioned the response variance, the trial-averaged gain should have no systematic temporal structure. If it has a sinusoidal modulation, it may partially capture stimulus-drive. This could be an interesting test to run on all model fits to further validate that the partitioning into a signal and noise component succeeded as intended.

(7) One common observation that is currently not explored is the quenching of neuronal response variability following stimulus onset (Churchland et al 2010 - Nature Neuroscience), which was suggested to reflect a quenching of gain variability in Goris et al (2024 - Nature Reviews Neuroscience). Building on the previous suggestion, the authors could compute the temporal evolution of cross-trial gain variability from the inferred gain traces. Do they recognize a reduction in gain variability following stimulus onset? If so, it would be worthwhile to show this.

(8) Line 543-565: I want to make sure I understand the Baseline Poisson model and Poisson-GP correctly. For the baseline model, I had imagined that the authors would simply use the stimulus-conditioned PSTH as an estimate of the time-dependent firing rate, coupled with an inhomogeneous Poisson process assumption. But they additionally assume a Gamma prior on the firing rate to compensate for the sparseness of the data (sometimes only 5 repeats per condition). The Poisson-GP includes exactly the same model components, but now the time-dependent firing rate is modeled by a Gaussian process. Doing this massively improves the goodness-of-fit (Fig 4A). Do I understand this correctly?

Reviewer #2 (Public review):

Summary:

Neurons have varied responses to external stimuli that cannot be explained by naive Poisson models. Previous work has quantified and partitioned higher-than-Poisson variability in the brain into different components. The authors improve on these methods to infer how both the stimulus drive and internal gain dynamics impact neuronal variability continuously in time. The clean and well-reasoned model is rigorously developed and then applied to neural data across the visual hierarchy. This lends new insights into how variability is partitioned, agreeing with and extending previous work on how that variability changes from early visual areas (LGN, V1) through to higher, motion-sensitive areas (area MT). Another key contribution is that this partitioning can be fully addressed as a continuous-time process, which allows for the dissection of how the timescale of fluctuations in these two components changes across the brain's processing arc.

Strengths:

(1) The model is cleanly derived and thoroughly documented, including usable code shared in a GitHub repo. This makes the method immediately portable to other neural systems.

(2) This is a clear and well-presented piece of work. The figures and writing are clear and understandable, and all pieces of the derivations are included in the main text and supplementary information.

(3) Comparisons to other models, particularly the one from Goris et al., 2014 shows how this Continuous Modulated Poisson (CMP) model outperforms previous work.

(4) New insights about how variability partitioning changes across the visual stream from LGN to MT are revealed, including how the gain fluctuates on longer timescales in higher visual areas. Another key result about the anticorrelation between the variance in stimulus drive and gain fluctuations comports with theories about how neurons maintain efficient, reliable encoding.

(5) In addition to the results reported here, this work will serve as an excellent tutorial for students and postdocs first delving into the sources of variability in the brain.

Weaknesses:

The work is somewhat incremental, building on previous studies of the partitioning of variability in the brain, but it provides important new extensions, as noted above.

The only major gap I would suggest addressing in the Discussion is the observation of sub-Poisson variability in the brain. It seems clear that this model can extend to sub-Poisson variability and its partitioning and perhaps even show how that varies in real time, with an animal's attentional state. That is, of course, beyond the scope of the current work, but could be mentioned in the Discussion.

Reviewer #1 (Public review):

Summary:

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

Strengths:

The authors collected high-resolution behavioral data from the same animals across multiple days, allowing for a detailed characterization of individual variation in taste preferences. They then performed recordings from the same set of animals in response to the same stimuli, allowing them to draw parallels between behavioral and neural responses. They convincingly show that preference ranks for a variety of basic tastes change over time and that the correlation between neural responses and preferences is not stable, correlating more strongly with more recent measures of preference.

Weaknesses:

Behavioral analysis: Data presentation does not show how preferences change over the course of testing. In particular, it is unclear whether there are any systematic changes in preferences over the course of testing that could explain the observed changes in correlation with neural responses, such as changes due to learning (e.g., flavor nutrient conditioning, relief of neophobia), changes in deprivation state, or habituation to/proficiency with the BAT setup. A secondary point is whether any changes in preference are attributed to internal individual versus external contextual factors. Both types of variation (i.e., across individuals and across time within an individual) are mentioned in the introduction, but it is not clear what the authors believe about the nature or neural representation of these sources of variation.

With respect to neural data analysis, no individual animal/day data are shown, making it difficult to assess the extent to which differences in correlation match individual differences in preferences and/or changes in preference with time within individuals. The correlation analysis is also lacking control for the fact that there is a certain degree of "chance" associated with behavioral and neural measures having matching ranks.

Finally, the conclusion that correlations between final day preferences and neural responses obtained from the second recording session are the result of experience needs more justification; it is unclear to what extent changes in correlation may be attributed to overall changes in responsiveness of the neural population.

Reviewer #2 (Public review):

Summary:

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

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

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

Strengths:

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

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

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

Weaknesses:

(1) The manuscript could use additional corollary analyses to provide a more complete picture of the phenomenon. For instance, how many neurons (per animal and in total) have significant correlations with the final BAT patterns? And with the first BAT? Can a time course of such counts be provided? Can some decoding analyses be performed at a single session level to reconstruct a rat's behavioral preference pattern from its neural activity?

(2) The manuscript could benefit from additional polishing, both in the text as well as in the figures.

Reviewer #3 (Public review):

Summary:

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

Strengths:

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

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

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

Weaknesses:

Experiments require further clarification. The interpretations would be strengthened by reorganizing the experimental design.

(1) Figures 5-6 show shifts in palatability-related GC responses from recording day 1 to recording day 2. The authors propose that this drift is due to the taste experience during recording day 1, but the study, as designed, does not directly test this idea. Without a behavioral measure collected after recording day 1 intraoral exposure, it is not possible to determine whether taste preference was altered by that experience, nor whether the neural responses collected on recording day 2 represent current or most recent palatability expression vs something else. The authors' conclusion would be strengthened by adding an intervening brief access test between recording days 1 and 2. The authors could then determine whether the behavioral preferences changed after intraoral taste exposure on recording day 1, as well as whether the new set of taste-related palatability responses correlates with the updated taste preferences.

(2) The current experimental design exposes animals to 3 distinct sets of substances. These substances differ in identity (some rats never experienced sweet, while others did not experience bitter during the recording sessions) and concentration (ranging from very aversive to slightly aversive or possibly even neutral). Because palatability is known to be comparative depending on the other substances available and concentration-dependent, this introduces challenges to interpretation.

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

(3) Responses to sweet tastes are not reported in the electrophysiology data. This is seemingly the case because rats given set 1 received no sweet stimulus while rats given set 2 received to 2 distinct sweet tastes. Finally, rats given set 3 did not receive quinine, yet quinine is reported in electrophysiology data.

(4) The choice of reporting average lick cluster size is problematic because the authors use thirsty rats with 10-second-long trials. Thirsty rats are likely to lick in relatively long clusters, especially for neutral and palatable tastes. If the rat is mid-cluster when the trial ends, the final cluster would be cut off prematurely, resulting in shorter overall average lick cluster size, disproportionately affecting neutral and palatable tastes over aversive tastes.

(5) Canonical palatability rankings may not apply to the concentrations selected in every stimulus set. This is particularly true for set 1, which included two concentrations of citric acid and quinine for the behavior. It is also not clear which concentrations are reported in Figures 3A2 and 3B2. Meanwhile, the concentrations of quinine and citric acid used for electrophysiology are quite low.

Reviewer #1 (Public review):

Summary:

The authors provide extensive immunoreactivity and expression data to map monoaminergic neurotransmitter production sites in Pristionchus pacificus. This nematode is relatively distantly related to the popular model nematode Caenorhabditis elegans, for which such information is already available. They find that dopamine, tyramine, and octopamine are present in the same neurons in both species, but differences are observed for serotonin. This forms the basis for a comparison of serotonergic neurons across 22 nematode species. In addition, they evaluate monoaminergic effects on egg-laying, head movement during reversals, and nictation behavior, to find that monoaminergic control over the latter differs between C. elegans and P. pacificus. This shows that some anatomical flexibility supports similar outcomes, whereas in other cases it is the basis of evolved regulatory differences.

Strengths:

The comparative efforts are laudable and valuable, including a thorough revisiting of old data and corrections of what is judged as a historic misannotation. The expected continued value of this work is also appreciated, because nematodes have similar anatomies and behaviors, cellular-resolution data of different species permits the study of functional evolution of neurotransmitter usage in homologous neurons.

Despite the strong experimental approach, there are some points that require addressing:

(1) Not all the concepts of the introduction ('feeding behaviors', to a lesser extent also 'evolution of neurotransmitter usage in homologous neurons') are followed up upon in the results or discussion sections.

(2) The choice of nematodes ('only' 13 species) may affect what is perceived as ancestral. Also, identifying their cells based on comparisons with Ce or Ppa identifications only is understandable but mildly risky: there are many cells in the head, and mistakes would go unnoticed until detailed analysis in each species can provide conclusive evidence.

(3) It is not reported whether the nictation-defective mutants have general locomotion defects; therefore, whether the reported problem is specific to this host-finding behavior or not.

(4) The section on RIP neurons makes sense for Ppa, but not for Ce (dauers in fact have weakened IL2-to-RIP connections), and should be revised. The nictation data also do not support the breadth of the conclusions, which should either be toned down or rephrased as hypothetical.

(5) The discussion mostly reiterates the results, leaving little room for the author's interpretations and opinions. I would suggest reworking in favor of conceptual discussion.

Reviewer #2 (Public review):

Summary:

This paper makes important contributions to our understanding of how nervous systems evolve, with a particular focus on whether changes in neurotransmitter usage within homologous neurons represent a mechanism for evolutionary adaptation without large-scale changes to circuitry. Comparing the predatory nematode P. pacificus with C. elegans, this study systematically examines monoamine-producing neurons, assesses how their neurotransmitter identities differ between homologous neural types, and determines how these differences relate to behavior.

Strengths:

The major strength of this work is its breadth, rigor, and data quality. It combines multiple, independent lines of evidence to assign neurotransmitter identity for neurons with homology grounded in lineage, morphology, and connectomics, which is essential for meaningful cross-species comparisons. Additionally, by extending the analysis beyond P. pacificus and C. elegans to other nematodes, the authors convincingly argue that features observed in P. pacificus likely reflect an ancestral state. This depth greatly enhances the significance of the conclusions.

This work is likely to have a significant impact on the fields of comparative neurobiology and nervous system evolution. It demonstrates a powerful system and approach for linking molecular identity, cell-type homology, circuit context, and behavior across species. The data generated here will be a valuable resource for the community and provide a strong foundation for future mechanistic studies.

More broadly, the study reinforces the idea that evolutionary change in nervous systems can occur through modulation of chemical signaling within conserved circuits, rather than through complete rewiring. This conceptual framework is likely to influence how researchers think about neural evolution in other systems.

Weaknesses:

Given the availability of detailed connectivity information for both species, a more explicit comparison of the local circuit context of key neurons would further strengthen the link between molecular identity and circuit function.

Reviewer #3 (Public review):

Summary:

The study by Hong, Loer, Hobert, and colleagues is a comprehensive description of monoaminergic neurons in the nematode Pristionchus pacificus. The work used multiple, complementary approaches, including immunostaining and expression of genes involved in neurotransmitter synthesis or transport, to identify neurons that express a monoamine neurotransmitter. Moreover, this study characterized the phenotypes of various mutants to study their organismal function. Extensive comparisons are made to C. elegans, the nematode model that, in a way, anchors the model studied here, and new outgroup species were examined for some features so that the polarity of their evolution could be inferred. Although there is no simple or groundbreaking punchline to distill from the manuscript (i.e., other than some things are the same as in C. elegans, and some things are different), and while the study is basically descriptive in nature, the scope of the project warrants broad attention.

Strengths:

This manuscript offers a tremendous resource for those who use this species as a model, which, based on the author list alone, includes many labs. This study sets the bar for what can be done in a "satellite" model system.

Given the complementarity of approaches used, such as the position of cell bodies, the connectivity and morphology of dendrites, and a previously published atlas of the connectome for this species, the identification of specific neurons (which, as the authors point out, can be easily mistaken) is convincing throughout. Likewise, appropriate caution is observed where neuron identities are ambiguous, e.g., unlabelled cells in Figure 5, or ambiguous identities in other species, as shown in Figure 10. There was a lot of data to unpack in this manuscript, but I could not find any obvious flaws in neuron identification.

Also, the phenotypic assays were straightforward and informative.

Weaknesses:

No serious weaknesses were noted. One minor comment is that in general, I think the Methods could use some additional text to describe what the goal of any given technique was. For example, although there is a description of the HCR protocol in the methods, nowhere does it say what genes this method would be used for. In addition to what is shown in Figure 4, this information should be given in the Methods.

Reviewer #1 (Public review):

Summary:

This manuscript examines whether retrieval practice protects memory-based inference from acute stress and proposes rapid neural reactivation of a bridging memory element as the underlying mechanism. Using a two-day associative inference paradigm combined with EEG decoding, the authors report that stress impairs inference accuracy and speed, while retrieval practice eliminates these deficits and restores neural signatures associated with bridge-element reactivation. The study addresses an important and timely question by integrating research on retrieval-based learning, stress effects on memory, and neural dynamics of inference. While the work provides promising multi-level evidence linking behavioral and neural findings, limitations in experimental design, causal interpretation, and decoding specificity weaken the strength of the mechanistic claims and suggest that further work is needed to disentangle strengthened associative memory from inference-specific protection effects

Strengths:

(1) Strong theoretical integration<br /> The study integrates three influential frameworks: memory integration through associative inference, stress-induced retrieval impairment, and the testing effect. The authors present a clear theoretical narrative linking these domains and derive testable hypotheses that retrieval practice protects inference by strengthening neural reactivation of a bridge element. The conceptual framing is well-grounded in prior literature and addresses an important gap regarding neural dynamics during inference.

(2) Multi-level evidence<br /> The study provides converging behavioral and neural evidence. The authors demonstrate that stress reduces inference accuracy and speed, while retrieval practice eliminates these deficits. EEG decoding further suggests that bridge element reactivation predicts successful inference. The combination of behavioral performance and neural decoding strengthens the overall argument.

(3) Transparent experimental implementation<br /> The procedures are described in substantial detail, including stimulus construction, stress manipulation, and decoding pipelines. Data and code availability are also strengths, facilitating reproducibility.

Weaknesses:

(1) Insufficient evidence that retrieval practice specifically protects inference rather than strengthening associative memories

A central claim of the manuscript is that retrieval practice specifically protects inference ability rather than simply strengthening underlying associative memories. However, the current data do not convincingly distinguish between these possibilities. Although the authors limited analyses to trials in which AB and BC pairs were correctly retrieved in the subsequent memory test, this procedure does not fully rule out the possibility that improved inference performance reflects stronger base associative memories rather than enhanced integrative processes.

Importantly, the direct memory retrieval test used a two-alternative forced-choice (2AFC) format, which inherently allows a substantial proportion of correct responses to arise from guessing. Consequently, trials classified as "successfully retrieved" may still include weak associative memory traces, making it difficult to conclude that failures in inference reflect deficits in integration rather than incomplete associative learning.

The authors further argue that retrieval practice does not improve inference in the absence of stress, suggesting independence between inference and associative memory strength. However, this null effect does not sufficiently rule out mediation through strengthened premise memory. A factorial design and/or mediation analysis would be necessary to determine whether inference resilience emerges independently of premise memory strength.

(2) Apparent below-chance inference performance raises interpretational concerns

One surprising aspect of the results is that inference performance across experiments and groups appears to fall below the theoretical chance level (0.33) in Figure 4A. This is particularly unexpected because analyses were restricted to trials in which participants correctly retrieved both AB and BC associations.

If performance is indeed below chance, this raises concerns regarding whether participants fully understood the task instructions or whether other methodological factors influenced performance. Additionally, below-chance performance complicates the interpretation of subsequent behavioral and neural analyses. It is possible that this reflects my misunderstanding of the figure; therefore, clarification from the authors regarding how inference accuracy is calculated and presented would be helpful.

(3) Between-experiment implementation of retrieval practice weakens causal inference

The retrieval practice manipulation was implemented as a separate experiment rather than as part of a factorial design. Experiment 2 was conducted after results from Experiment 1 were known, and the authors acknowledge this post hoc decision. This design introduces several potential confounds, including cohort differences between experiments, possible differences in participant motivation or task familiarity, and reduced ability to rigorously test interaction effects.

Although the authors combined data across experiments to test interactions between stress and retrieval practice, such post hoc aggregation cannot fully substitute for a factorial design. A within-experiment 2 × 2 design (Stress × Retrieval Practice) would provide substantially stronger causal evidence and reduce confounding influences.

(4) Lack of an appropriate comparison condition for retrieval practice limits the interpretation of the mechanism

Although acknowledged briefly in the discussion, the absence of an appropriate comparison condition for retrieval practice represents a critical limitation. Without a matched re-exposure or restudy control condition, it remains unclear whether observed benefits are attributable specifically to retrieval practice or to additional exposure to AB and BC associations.

Furthermore, it is unclear whether retrieval practice operates at the trial level or the participant level. Retrieval practice could enhance memory representations for specific practiced items, making those trials more resistant to stress, or it could induce a more global change in cognitive strategy or stress resilience across participants. One way to address this issue would be to analyze inference performance separately for trials that were successfully retrieved during the retrieval practice phase versus those that were not.

(5) Interpretation of EEG decoding as bridge-element reactivation may be overstated

The neural decoding results form the mechanistic foundation of the manuscript; however, the interpretation that decoding reflects reactivation of specific bridging memories may be overstated. The classifier distinguishes between face and building categories, and because the bridging element belongs to one of these categories, successful decoding may reflect category-level semantic activation rather than reinstatement of item-specific episodic representations.

Alternative explanations include category-level retrieval, strategic task differences, or even attentional biases. Because only two categories were used, the decoding analysis lacks the specificity necessary to distinguish between category-level and item-level reactivation. As such, conclusions regarding the reinstatement of specific bridging memories should be tempered or supported with additional analyses.

Reviewer #2 (Public review):

Summary:

Guo et al. investigate the neural and behavioral mechanisms of stress-induced impairments in memory-based inference. Across two well-powered experiments (N=136), the authors demonstrate that acute stress disrupts the rapid neural reactivation of "bridge" elements necessary for novel inferences. Crucially, they identify retrieval practice as a robust behavioral buffer that restores both inferential performance and the underlying neural signatures of memory reactivation.

Strengths:

(1) The use of two independent experiments provides high confidence in the behavioral findings.

(2) Utilizing time-resolved EEG decoding allows the authors to pinpoint the "online" moment of inferential failure, a significant advancement over the lower temporal resolution of fMRI.

Weaknesses:

(1) The authors correctly timed the inference task to begin approximately 20 minutes after the onset of the stressor. While this window aligns with the expected peak of the glucocorticoid (HPA) response, it also represents a period where the rapid adrenergic (SAM) response, confirmed by heart rate elevation, is still highly influential. As the authors acknowledge, because they did not collect saliva samples due to safety protocols, they cannot definitively separate the influence of peak cortisol from the tail-end of the adrenergic surge on the observed memory impairments.

(2) Figures 4 and 6: Without asterisks is really difficult to compare the significant group differences.

Appraisal and Impact:

This study provides high-quality evidence that acute stress impairs the rapid neural reactivation of "bridge" elements necessary for novel memory-based inferences. By leveraging the high temporal resolution of EEG decoding, the authors identify the specific neural "chokepoint" where inferential failure occurs. The research is strengthened by two independent experiments and the identification of retrieval practice as a powerful buffer that not only preserves but also enhances neural reactivation under pressure. The findings have significant implications for both cognitive neuroscience and applied learning science.

Reviewer #3 (Public review):

Summary:

In this study, Guo and colleagues investigated the effects of stress and retrieval practice on memory inference. In the first experiment, they found that memory inference was significantly worse after induced stress. Conversely, when participants received retrieval practice in the second experiment, they found no significant differences between these conditions. They monitored EEG during the inference phase and applied multivariate decoding analysis to examine evidence of neural reactivation. Complementing the behavioural findings of the first experiment, they found that they were able to decode the stimulus category of the inference item with more fidelity in the no stress condition. Surprisingly, they found the opposite direction when participants had retrieval practice, with stronger evidence of reactivation in the stress condition than in the control condition.

Strengths:

(1) The authors have carefully designed two studies investigating the effects of stress and memory retrieval on memory inference.

(2) The use of multivariate decoding on the inference phase data sheds new light on how stress and retrieval may impact the neural signatures of inference processing.

Weaknesses:

(1) There are some key gaps in the reporting of the data. In particular, data is missing on how many trials were included in the inference phase and how many were retrieved in the direct memory task. This is important to know as the main conclusions are based on inference trials proportional to the direct retrieval trials. Considering that the direct retrieval performance differs significantly between the experiments, there could be issues with floor/ceiling effects (in the behaviour) and statistical power (in the EEG results) that confound the comparisons between experiments. Without the data, it is difficult to draw conclusions.

(2) There are some relatively strong conclusions drawn without the data to support them. An important example is the title suggesting a mechanistic role of memory reactivation for these effects; however, the data instead suggest a relationship between successful inference and evidence of reactivation. Additionally, one-tailed t-tests have been used in follow-up tests, and, as I understand it, no multiple comparisons corrections have been applied to the post-hoc tests, suggesting that these findings should be interpreted with caution.

(3) In places, the structure is unclear, making the narrative difficult to follow, often making it necessary for the reader to go back and forth between the sections to understand the study and analyses. I have made some recommendations for how to improve this.

Reviewer #1 (Public review):

Summary:

The authors report a novel binding partner of the TolC channel protein that forms complexes with the two principal classes of transporter-based tripartite assemblies (both ABC- and RND-transporter based) and appears to modulate their function, while also anchoring TolC into the outer membrane, compensating for the lack of direct lipidation seen in other members of the OMF family.

The newly identified protein, YbjP, is comprehensively characterized from both phylogenetic and structural perspectives. Two independent cryo-EM structures (MacAB-TolC-YbjP and AcrABZ-TolC-YbjP) provide strong structural evidence for its role and are generated using peptidiscs, mimicking the membrane environment. These findings are further supported by pull-down experiments (including state-of-the-art in vivo photo crosslinking) and functional assays for a well-rounded characterisation of the protein, and a significant amount of modelling and phylogenetic analysis. This work sheds light on the function of the members of the DUF3828-containing protein family, which appear to anchor TolC to the outer membrane and influence the expression of the TnaB and YojI transporters.

Strengths:

The strengths of the manuscript are numerous, and it presents a well-rounded package of structural biology complemented by functional and computational studies.

The full assemblies of both MacAB-TolC-YbjP and AcrABZ-TolC-YbjP are reconstituted and resolved to near-atomic resolution using cryo-EM for unambiguous assignment of binding interfaces, which are then validated using a number of techniques, including ITC, in vitro and in vivo binding assays and cross-linking.

The evolutionary analysis is particularly notable, and provides genuine insight into the DUF3828-containing proteins, the function of which remains enigmatic till now. Similarly, the involvement of YbjP in trafficking of TolC and the analysis of the impact of YbjP deletion of the full E. coli proteome is commendable.

Overall, this is a very solid piece of work, competently executed and presented, which significantly advances the field.

Weaknesses:

None obvious, however the presentation and especially main-text illustrative material seems to focus disproportionately on MacAB-TolC-YbjP complex, and the AcrABZ-TolC-YbjP is relegated to supplementary data which is somewhat confusing. There is no high-resolution side view of the AcrABZ-TolC-YbjP side-by-side to MacAB-TolC-YbjP which may be helpful to spot parallels and differences in the organisation of the two systems.

Supplementary Figure 2 may also be better presented in the main text, as it shows specific displacements of residues upon binding of the YbjP relative to the apo-complexes, although this can be left at the authors' discretion.

Reviewer #2 (Public review):

This article focuses on the study of two E. coli tripartite efflux pumps both using TolC as partner in the outer membrane, namely MacAB-TolC and AcrABZ-TolC.

By preparing MacAB-TolC in Peptidiscs rather than in detergent for cryo-EM structure determination, they visualized an extra protein localized around TolC. The resolution was sufficient to build part of the structure, and using the AlphaFold2 database and DALI topology recognition program, they identified it as the lipoprotein YbjP. This protein has an anchorage in the outer membrane, and it was suggested that it could act as a support for TolC that is the only OMF that does not have an N-terminal extension anchored in the outer membrane, which is very puzzling for the community working in this field of research.

Authors used a large number of different approaches to evaluate the importance of YbjP (structure, genomic evolution, microbiology, photocrosslink in vivo, proteomic profile), but did not succeed in finding it a clear role so far, even if it could be important depending on environmental stress. Nevertheless, their results are of main interest for the comprehension of the complexity of such systems and deserve publication.

The different analyses are properly performed and presented, and support the conclusions.

My only concern is for the photocrosslink presented in Figures 3 and S3. My impression is that the bands do not migrate at the proper size after the crosslink.

A second point that could be discussed further is the comparison of the structure of the pump in the presence of the peptidoglycan with the images previously obtained by tomography. It is not totally clear to me if YbjP could have been positioned in these maps.

Reviewer #1 (Public review):

Summary:

The authors introduce EMUsort, an open-source algorithm for the automatic decomposition of high-resolution intramuscular EMG recordings. The method builds upon the Kilosort4 framework and incorporates modifications designed to better handle the spatial and temporal characteristics of intramuscular signals. The performance of EMUsort is evaluated on openly available datasets and compared against KS4 and MUEdit, demonstrating improved motor unit accuracy.

Strengths:

(1) The manuscript is clearly written, technically detailed, and well structured.

(2) The open-source software is thoroughly documented, both within the manuscript and in the accompanying repository README, facilitating adoption by the community.

(3) The availability of both code and datasets is a major strength, enabling reproducibility and independent validation.

(4) The authors provide quantitative comparisons with existing decomposition algorithms, which is essential for contextualizing the proposed method.

(5) The methodological details are sufficiently described to allow replication and further development by other researchers.

Weaknesses:

While the manuscript is strong overall, I have several suggestions that could further strengthen its impact and clarity.

(1) Benchmarking and community integration

A recent work has proposed standardized datasets and benchmarking pipelines for high-density surface EMG decomposition ("MUniverse: A Simulation and Benchmarking Suite for Motor Unit Decomposition", Mamidanna*, Klotz*, Halatsis* et al, NeurIPS 2025). A similar effort for intramuscular EMG would be highly valuable to the field. The authors may consider discussing how their dataset and algorithm could be integrated into broader benchmarking initiatives (e.g., platforms such as MUniverse), enabling systematic comparisons across multiple datasets and decomposition methods.

(2) Comparison with additional decomposition algorithms

Since the manuscript compares EMUsort with MUEdit, it would be appropriate to also include a comparison with Swarm-Contrastive Decomposition (SCD), which has been proposed for both surface and intramuscular EMG signals. Including this comparison, or explicitly discussing why it was not feasible, would strengthen the positioning of EMUsort relative to the current state of the art.

(3) Manual editing and post-processing

In practical EMG decomposition workflows, manual inspection and editing of motor units are often required after automatic decomposition. It would be useful for readers to know whether EMUsort provides (or is compatible with) a graphical interface or workflow for manual refinement, or how the authors envision this step being handled.

(4) Ablation analysis of algorithmic modifications

EMUsort is described as an extension of Kilosort4. An ablation analysis examining the impact of the main modifications introduced relative to KS4 would help clarify which changes contribute most to the observed performance improvements and under which conditions.

(5) Failure modes and limitations

A more explicit discussion of when EMUsort is likely to fail or degrade in performance would be valuable. For example, sensitivity to the number of channels, recording duration, signal quality, or motor unit density could be discussed to guide users.

(6) Generalisability to surface EMG

Given the shared methodological foundations between surface and intramuscular EMG decomposition, it would be helpful to know whether EMUsort has been tested on high-density surface EMG datasets or whether the authors expect limitations when applied outside the intramuscular domain.

(7) Applicability to human intramuscular recordings

The authors could clarify whether EMUsort has been tested on human intramuscular EMG, and discuss any expected differences in performance due to anatomical or physiological factors.

(8) Parameter sensitivity

Clustering-based methods can be sensitive to parameter choices. Reporting a parameter sensitivity analysis, or at least discussing the robustness of EMUsort to parameter variations, would increase confidence in the method's reliability and ease of use.

(9) Differences between template matching and BSS methods

Since the manuscript proposes a new template matching algorithm, but it compares its performance with a BSS one (MUedit), BSS algorithms should be described in the introduction. The differences between the methodologies should be highlighted, and the pros and cons of each described.

Conclusion:

The authors largely achieve their stated aims, and the results mostly support the main conclusions. EMUsort represents a meaningful contribution to the EMG decomposition literature, particularly for researchers working with high-resolution intramuscular recordings. With additional clarification regarding benchmarking, algorithmic ablations, and limitations, the manuscript would be further strengthened and likely to have a substantial impact on the field.

Reviewer #2 (Public review):

Summary:

This work presents a new spike sorter, EMUsort, to target the challenging task of spike sorting Motor Unit Action Potentials (MUAP). EMUsort is essentially a modified version of Kilosort, with some key extensions to target EMG data: correct for large delays due to propagation across channels, spike detection of highly overlapping and large units via multiple thresholds, an increased number of waveform templates for spike detection, and an extended representation of waveforms to grasp complex MUAP spike shapes. The results on simulated data show solid evidence that the applied modifications make a difference for EMG recordings. All in all, I believe that EMUsort will greatly improve spike sorting performance for high-density EMG data.

Strengths:

The manuscript is well written, and the methods and modifications to the Kilosort pipeline are well-motivated, well-explained, and clear. The simulation results provide strong evidence that the presented modifications make spike sorting of high-density EMG data more accurate.

Weaknesses:

The method is overall only validated on 15 simulated motor units. The monkey dataset, in particular, seems too "easy" and not challenging enough to highlight weaknesses of any of the spike sorters. A second weakness is in the distribution of the code, which is shipped with submodules for Kilosort and SpikeInterface, and makes it hard to maintain long-term, and pins to old versions of these key dependencies.

Reviewer #3 (Public review):

Summary

This paper introduces EMUsort, an extension of Kilosort4 designed to sort motor unit action potentials from high-density intramuscular EMG recordings. Using rat and monkey forelimb recordings, the authors generate realistic simulated datasets with known ground truth and demonstrate that EMUsort substantially outperforms Kilosort4 and MUedit, particularly during periods of high motor unit overlap.

Strengths

This is a timely study in light of recent advances in intramuscular muscle recording technologies and the growing interest in automated methods for decoding neural and neuromuscular signals. The work leverages state-of-the-art electrode arrays and combines them with advanced signal processing tools to address a challenging and relevant problem in motor unit analysis.

Weaknesses

There are several aspects of the study that substantially limit the interpretation of the main results and conclusions. The following major points should be carefully considered by the authors.

(1) Choice of experimental model and validation framework: The study aims to validate a new methodology for EMG decomposition, yet the rationale for the chosen experimental models is unclear. Specifically, it is not evident why the authors focused on intramuscular recordings from two animal models performing dynamic tasks. Given the extensive literature on the development and validation of EMG decomposition methods, the choice of an experimental design that substantially deviates from established approaches is insufficiently justified. In particular, it is unclear why the authors did not consider more standard validation paradigms based on (i) isometric contractions, (ii) human data, (iii) surface EMG recordings, or (iv) combinations of their recording technologies with previously validated motor unit identification methods. This methodological divergence makes it difficult to interpret the findings in the context of existing evidence.

(2) Lack of manual EMG decomposition as reference: Related to the previous point, it is unclear why standard manual EMG decomposition methods were not used to generate reference datasets for validation. Manual decomposition has been shown to be reliable under specific conditions (low contraction levels, slow dynamics, etc.) and would have substantially strengthened the validation of the proposed algorithm.

(3) Neglect of muscle deformation effects: While the manuscript discusses several factors that complicate EMG decomposition relative to brain recordings, it does not address the well-known effects of muscle deformation during contractions on motor unit action potential shapes. There is extensive literature demonstrating that dynamic muscle contractions lead to systematic changes in action potential morphology, representing a major challenge for EMG decomposition and a fundamental difference from brain recordings. Additionally, even small relative movements of intramuscular electrodes can produce waveform changes that are large relative to muscle fiber dimensions. These issues are particularly relevant given the highly dynamic tasks studied here (e.g., treadmill walking in rats), yet they are not discussed or incorporated into the analysis.

(4) Exclusive reliance on simulated data for validation: The primary validation of EMUsort is based on simulated data, which represents a major limitation of the study. This reliance should be clearly and explicitly stated in the abstract, introduction, and discussion. Moreover, the simulation approach itself raises concerns. The simulated EMG signals are generated using templates derived from the same sorting framework being validated, which introduces a potential methodological bias. The linear combination of components used to synthesize waveforms constitutes an unjustified modeling assumption that may favor template-based approaches such as EMUsort. Additionally, the spike time generation procedure appears unnecessarily complex and insufficiently justified. Previous validation studies typically modeled motor units as firing at relatively stable levels along their recruitment curves, producing long spike trains with pseudo-random relative timing and diverse overlap conditions. This framework would likely provide a more robust and interpretable validation. If the authors believe their simulation approach is superior, a stronger justification is required. Finally, the limited number of simulated motor units is difficult to reconcile with the expected level of motor unit recruitment during the studied behaviors, and this choice is not adequately justified.

(5) Incomplete reporting and visualization of experimental data: The manuscript would benefit from a clearer description of the number of rats and monkeys used, which should be reported explicitly in the abstract. In addition, visualizations of the raw multichannel EMG data across different task phases and activation levels would substantially improve transparency. Providing comprehensive visualizations of motor unit action potential shapes across all channels and identified units (for both rats and monkeys) would also help readers assess the spatiotemporal features that underpin unit identification and sorting reliability.

(6) Physiological limitations of conduction delay correction: The proposed method for correcting conduction delays across channels is physiologically suboptimal. First, motor unit conduction velocities differ substantially across units, implying that delay correction should be applied at the unit level rather than uniformly across channels. Second, conduction delays depend on fiber orientation and distance relative to electrode geometry; if fibers are oriented at different angles with respect to the array, a single delay correction becomes invalid. Additionally, the schematic in Figure 2A appears to contradict the proposed correction approach: if electrode threads are arranged perpendicular to muscle fibers, conduction delays across channels within a single thread should be minimal.

(7) Clarity issues in Figure 4: Figure 4 (panels A-D) is potentially misleading. It should be clearly stated whether the signals shown are artificial examples or derived from real recordings; ideally, real data should be used to illustrate the advantages of dynamic thresholds. In panels B-D, the depiction of overlapping action potentials is difficult to interpret due to the thickness of the traces, and it is unclear whether overlaps with neighboring action potentials are absent by design or expected to occur in real data. If overlaps are expected, one would also expect to observe contamination in the extracted waveforms, which is not evident in the figure.

(8) Concerns regarding method comparisons: The comparison with existing methods raises methodological concerns. It appears that EMUsort was carefully optimized, whereas the competing algorithms were not equivalently fine-tuned. The literature clearly shows that EMG decomposition performance depends strongly on adapting algorithms to the signal type (intramuscular vs. surface, species, electrode geometry). Furthermore, it is surprising that MUedit is reported to perform particularly poorly during periods of motor unit overlap, as blind source separation methods were explicitly developed to handle convolutive mixtures and overlapping sources, especially in surface EMG (which is an extreme case of motor unit overlapping). This discrepancy requires further explanation.

(9) Insufficient characterization of motor unit firing properties: The study does not provide sufficient information about the firing characteristics of the identified motor units in experimental data. Relevant metrics that should be reported include average, minimum, and maximum firing rates; coefficients of variation of discharge rate; signal-to-noise ratios of motor unit action potentials; potential evidence of motor unit rotation over time; and stability of firing behavior across recording intervals.

(10) Lack of theoretical framing: Given the scope and claims of the paper, it would be valuable to include a more theory-driven introduction explaining why different sorting approaches (e.g., template matching vs. blind source separation) may be more or less suitable depending on the nature of the recorded signals. A clearer conceptual rationale for why the proposed approach is expected to outperform existing methods would substantially strengthen the manuscript.

(11) Limitations of validation metrics: Some of the metrics used to evaluate performance are not ideal. For example, reporting 0% accuracy for a unit is misleading and should instead be described as a failure to identify that unit. Similarly, comparisons of total spike counts are of limited interpretive value and may be misleading, as correct spike counts do not necessarily imply correct spike identities.

(12) Clarification of computational performance claims: Finally, the discussion of computation times should clarify that some existing methods require substantial time for offline estimation of projection vectors but can operate in near real time once these vectors are learned and remain stable. This distinction is important for a fair comparison of practical usability.

Reviewer #1 (Public review):

Summary:

Freas and Wystrach present a computational model of steering in insects. In this model, the central complex provides an error signal indicating the animal should turn left or right; this error signal biases the function of an oscillator composed of two mutually inhibiting self-exciting units. The output of these units generates a "steering signal" that is used both to set the direction and speed of the ant. Additionally, a separate module induces pauses, and an inverse relation between forward speed and turning speed is externally imposed. Statistics of the trajectories generated by the model are compared to the measured behaviors of ants.

Strengths:

While the model is very simple compared to state-of-the-art models, that simplicity makes it a potentially useful guide to researchers studying insect navigation. Some predictions that emerge from the model appear to be experimentally testable, although a more complete description of the model and its parameters, as well as an analysis of how this model's predictions differ from previous models' predictions, would be required to design these experiments.

Weaknesses:

I found it difficult to identify evidence in the paper supporting central elements of the abstract. Hopefully, these difficulties can be resolved with a clearer presentation and the addition of supporting detail, especially in the methods.

(1) The model is not clearly described

In the Materials and Methods, there is no description of the model, just "The computational model is presented in Figure 1." (This is probably a typo and may refer to Figure 2A-C), and a link to Matlab source code. It is inappropriate to ask readers or reviewers to examine source code in lieu of providing a method, but I attempted to do so anyway. To my eye, the source code does not match the model presented in 2A-C. For instance, in 2C, "Steering signal" inhibits "Freeze", but I couldn't find this in the source. "Freeze" is shown to inhibit "steering signal," but as "steering signal" is a signed quantity, it's not clear what this means. Literally, since "ang_speed_raw = L-R," it would seem to indicate the "freeze" would bias towards right turns. In the code, "freeze" appears to be implemented through the boolean variable "speed_inhibition_time." The logic controlled by this variable doesn't appear to inhibit the "steering signal" but instead (depending on control parameters) either reduces the movement speed and amplifies the turning rate, or it turns the angular speed output into a temporal integral of the control signal.

There are a number of parameters in the source code that aren't described at all in the paper, including the internal oscillator parameters.

Together, these limitations make it difficult to understand what is being simulated, what parts of the model are tied to biology, and where the model improves on or departs from previous work.

It is absolutely essential that authors fully describe the computational model, that they explain the meaning of all parameters of the model, and that they explain how the particular values of these parameters were chosen.

(2) The biological inspiration is unclear

A central claim of the paper is that the model is "biologically grounded." But some elements, for instance, using a signed quantity to represent left-right steering drive, are not biologically possible; at best, these are shorthand for biologically possible implementations, e.g., opposing groups of left-right driving neurons.

The mechanism that produces fixations and saccades - the "freeze" module - is not tied to any particular anatomy of the insect brain. Initiation of a freeze occurs at a specific time coded into the model by the authors; it is not generated by an internal model signal. Release of a freeze is by drawing a random variable; there is no neural mechanism proposed to generate this signal.

In some versions of the model, instead of directly controlling the signal, during fixations, the angular drive signal is integrated into a variable "cumul_drive." No neural substrate is proposed for this integrator. In the code, if cumul_drive passes a threshold, the angular heading of the ant changes (saccades), but only if this threshold is passed before the Poisson process ends the fixation. No neural substrate is proposed for any of this logic.

The model steps forward in time by a fixed increment - the actual duration (in seconds) of this time step is not specified. From Figure 4F, G, it appears a simulation time step is meant to be about 10ms. This would imply an oscillator frequency of about 2 Hz (Fig 2B), that the heading oscillates at a similar frequency (2G), and that a forward crawling ant stops moving every 500 ms (2I). Are these plausible? Can they be compared to an experiment?

Model parameters, including the ones that control the frequency of the oscillator, are non-dimensionalized. It is not possible to evaluate whether these parameters are biologically plausible or match experimental results.

(3) Claims that behaviors emerge from the model may be overstated

The abstract claims that steering correction and fixations/saccades emerge naturally from the same model. But it appears to me that fixations/saccades are externally imposed by the specification of specific times for a "freeze." Faster angular rotation during saccades than during course correction is imposed and does not emerge naturally from neural simulations.

(4) Citations to previous literature are difficult to follow, and modeling results are presented as though they are experimental data

I would ask the authors to be much clearer in their description and citation of previous work. It should be clear whether the cited work was experimental or computational. To the extent possible, the actual measurement should be described succinctly. Instead of grouping references together to support a sentence with multiple claims, references should be cited for each claim. Studies of computational models should not be presented as proving a biological result.

For example:

a) Lines 141-146:<br /> "Previous studies have established many key components of insect navigation, including .... the intrinsic oscillatory dynamics in the lateral accessory lobes (LALs) that support continuous zigzagging locomotion (Clément et al., 2023; Kanzaki, 2005; Namiki and Kanzaki, 2016; Steinbeck et al., 2020)."

The first reference is to one author's previous modeling work - it hypothesizes that oscillations in the LAL support zigzagging but includes no data that would "establish" the fact. Kanzaki et al. 2005 describes numerical modeling and simulation with a physical robot. Namiki and Kanzaki, 2016 is a review article that links the LAL to zigzagging behavior. It describes the LAL as a winner-take-all bistable network but does not describe or hypothesize that the LAL has intrinsic oscillatory dynamics. Steinbeck et al. 2020 is a more comprehensive review; it reinforces that the LAL is a winner-take-all bistable network that drives left-right steering, including during zig-zagging behavior. But in my reading, I could not find a statement that the LAL has intrinsic oscillatory dynamics (the closest is Steinbeck et al. saying the activity pattern switches regularly, as does the behavior; this doesn't imply that the LAL is intrinsically oscillatory.)

b) Lines 701-703:<br /> "In plume-tracking moths, CX output has been shown to modulate LAL flip-flop neurons driving zigzagging (Adden et al., 2022)."

This reads as though an experimental measurement was made, but in fact, this is modeling work.

c) Lines 703-706:<br /> "In ants, strong goal signals in the CX - whether elicited by the path integrator or visual familiarity (Wehner et al., 2016; Wystrach et al., 2020b, 2015) do not only sharpen directional accuracy but also increase oscillation frequency (Clément et al., 2023)."

Here again, modeling results are presented as though they were experimental data.

Reviewer #2 (Public review):

Summary:

The paper by Freas and Wystrach is an interesting computational study, exploring the detailed mechanisms of how simple neural circuits could explain complex behavioral patterns observed in navigating ants. The authors compare detailed, high-speed video recordings of Australian desert ants (Melophorus bagoti) with predictions made by their new computational model and find convincing similarities between the model and the behavioral data, at a level of detail not previously studied. Particularly interesting are emerging properties of the model, yielding behavioral motifs it was not designed to reproduce, but which occur in natural ant behavior.

Strengths:

A strength of the study is that the model is based on previous models, without making major novel explicit assumptions. It combines existing models of the insect central complex with a model of the lateral accessory lobe and adds a stochastic inhibition of forward velocity to the interaction of central complex and lateral accessory lobes. The central complex provides corrective steering signals when the goal direction and the current heading of an insect are not aligned, while the lateral accessory lobes provide an intrinsic oscillator underlying the behavioral oscillations shown by walking ants at all times. These background oscillations are modulated by the steering signals from the central complex. Depending on which phase of the intrinsic oscillations coincides with the corrective signals, and how fast the ant is moving forward during this time, a complex set of behaviors emerges. Most prominently, scanning behaviors, which are regularly carried out by the ants, are recapitulated in great detail by the model. Additionally, other behaviors, such as full loops, emerge naturally from the model. While computational models are not to be seen as definite evidence for any biological reality, they can provide strong support for particular neural implementations. The current study is an excellent example in that it provides evidence for a serial arrangement of central complex circuits upstream of the lateral accessory lobe circuits, modulated by speed-regulating input. While the latter is hypothetical, it yields a clear hypothesis that can be validated by connectomics studies and functional work in the future.

The study shows that even complex behavioral motifs do not require dedicated neural modules, but can rather emerge from the interplay of already known circuits - highlighting the efficiency of insect brains and possibly providing the path towards embodied hardware solutions of such circuits in autonomous agents.

Weaknesses:

There are several weaknesses in the paper as it is.

Firstly, the model is not described in the methods, but only found when following the link to the authors' GitHub repository. This is clearly not sufficient and prevents readers from evaluating the model's assumptions directly. Most importantly, how natural do the emerging properties indeed emerge from the model? What parameters need to be tuned to generate a match between data and model?

Second, it is often not entirely clear what is biological data and what is a computational model. This relates to figures, text, and references. As a reader, this makes it difficult to clearly judge what is new in the current paper, how it adds to previous models, and what the predictions and assumptions are for biology.

Third, while neural data from bees and flies are taken to motivate and design the computational model, the discussion and interpretation revolve almost exclusively around ants. For the most part, this is justified, as the behavioral data used to benchmark the model are taken from ants. Nevertheless, more broadly discussing the newly defined circuit in the context of flying insects would give a better idea of the broad relevance of the neural circuits predicted by the model.

Reviewer #1 (Public review):

Summary:

D. Fuller et al. set out to study the molecular partners that cooperate with ATG2A, a lipid transfer protein essential for phagophore elongation, during the process of autophagy. Through a series of experiments combining microscopy and biochemistry, the authors identify ARFGAP1 and Rab1A as components of early autophagic membranes, which accumulate at the periphery of aberrant pre-autophagosomal structures induced by loss of ATG2. While ARFGAP1 has no apparent function in autophagy, the authors show that RAB1A is implicated in autophagy, although the precise mechanisms are not explored in the manuscript.

Strengths:

The work presented by Fuller et al. provides new insights into the composition of early autophagic membranes. The authors provide a series of MS experiments identifying proteins in close proximity to ATG2A, which is a valuable dataset for the field. Furthermore, they show for the first time the interaction between ATG2A and RAB1A both in fed and starved conditions, which extends the characterisation of the pre-autophagosomal structures observed in ATG2 DKO cells.

Weaknesses / Specific comments:

(1) The authors claim that Rab1A/B knockdown phenocopies the LC3-II accumulation observed in ATG2 DKO cells. While LC3-II accumulation is consistent with this interpretation, depletion of many autophagy-related proteins can give rise to a similar phenotype, even when they function at distinct stages of the autophagic cascade. Therefore, LC3-II accumulation alone is insufficient to support phenocopying in my vew. Immunofluorescence analyses demonstrating comparable cellular phenotypes-such as membrane accumulation of pre-autophagosomal structures-following Rab1 knockdown should be provided. Moreover, p62 does not accumulate upon Rab1 depletion, suggesting that loss of Rab1 does not fully phenocopy ATG2 deficiency. Consequently, it remains unclear whether Rab1A depletion truly phenocopies ATG2A depletion with respect to autophagy progression or the accumulation of pre-autophagosomal structures.

(2) Interpretation of the significance of the data

(2.1) The significance statement asserts that "this study elucidates the role of early secretory membranes in autophagosome biogenesis." While the data convincingly demonstrate an association between the RAB1A GTPase and ATG2A, the study does not provide mechanistic insight into how this interaction functionally contributes to autophagy. As presented, the findings support a correlative relationship rather than a defined role in autophagosome biogenesis.

(2.2) The title states that ATG2A "engages" Rab1A- and ARFGAP1-positive membranes during autophagosome formation. However, both Rab1A and ARFGAP1 are shown to localize to pre-autophagosomal structures independently of ATG2A. In the absence of evidence demonstrating a functional or causal dependency, the term "engages" appears overstated. A more descriptive term, such as "associates," would more accurately reflect the data.

(2.3) In the Discussion, the authors state that previous studies have reported increased LC3-II levels following knockdown of Rab1 proteins (refs. 38 and 49). However, it is unclear where this observation is documented in the cited references.

(3) Some concerns remain in specific figures, as outlined below:<br /> • Quantification is missing in Fig S2D.<br /> • The authors claim: "siRNA against ARFGAP1 had very little effect" but the quantification and blots show actually no effect.<br /> • Conclusions drawn from KD experiments in Fig. S2 should be interpreted with caution, as knockdown efficiency is very low, particularly for ARFGAP1/3 in the triple knockdown.<br /> • In New Fig. 4, the representative blot is not representative of the results showed in the quantification as previously noted.

Reviewer #2 (Public review):

The mechanisms governing autophagic membrane expansion remain incompletely understood. ATG2 is known to function as a lipid transfer protein critical for this process; however, how ATG2 is coordinated with the broader autophagic machinery and endomembrane systems has remained elusive. In this study, the authors employ an elegant proximity labeling approach and identify two ER-Golgi intermediate compartment (ERGIC)-localized proteins-Rab1 and ARFGAP1-as novel regulators of ATG2 during autophagic membrane expansion.

Their findings support a model in which autophagosome formation occurs within a specialized subdomain of the ER that is enriched in both ER exit sites (ERES) and ERGIC, providing valuable mechanistic insight. The overall study is well executed and offers an important contribution to our understanding of autophagy. I support its publication in eLife and offer the following minor comments for clarification and improvement.

Specific Comments

(1) Integration with Prior Literature<br /> The data convincingly implicate the ERES-ERGIC interface in autophagosome biogenesis. It would strengthen the manuscript to discuss previous studies reporting ERES and ERGIC remodeling and formation of ERERS-ERGIC contact sites (PMID: 34561617; PMID: 28754694) in the context of the current findings.

(2) Figure Labeling<br /> The font size in Figure 1A and Supplementary Figure S1G is too small for comfortable reading. Please consider enlarging the labels to improve clarity.

(3) Experimental Conditions<br /> In Figures 2A-C and Figure 4, it is unclear how the cells were treated. Were they starved in EBSS? Please include this information in the corresponding figure legends.

(4) LC3 Lipidation vs. Cleavage<br /> In Figure 2A, ARFGAP1 knockdown appears to reduce LC3 lipidation without affecting Halo-LC3 cleavage. Clarifying this observation would help readers better understand the functional specificity of ARFGAP1 in the pathway.

(5) Use of HT-mGFP in Figure 2C<br /> Please clarify why the assay in Figure 2C was performed in the presence of HT-mGFP. Explaining the rationale would aid interpretation of the results.

(6) FIB-SEM Imaging<br /> For the FIB-SEM images in Figures 3 and S3, directly labeling the cellular structures in the images would greatly facilitate interpretation for the reader.

(7) Supplementary Figures<br /> Many of the supplemental figures are high quality and contain key data. If space permits, I suggest moving these into the main figures. In particular, the FLASH-PAINT experiment could be presented as part of Figure 1.

(8) Text Revision for Clarity<br /> In line 242, the phrase "but protein-protein interactions appear to be limited to RAB1" would benefit from clarification. A more precise formulation could be: "but stable protein-protein interactions appear to be limited to RAB1."

(9) COPII Inhibition Strategy<br /> The authors used the dominant-active SAR1(H79G) mutant to inhibit COPII function. While this is effective in in vitro budding assays, the GDP-locked mutant SAR1(T39N) has been shown to be more effective in blocking COPII-mediated trafficking in cells. Including SAR1(T39N) in the analysis would provide stronger support for the conclusions.

Reviewer #3 (Public review):

The manuscript by Fuller et al describes a crosstalk between ARTG2A with components of the early secretory pathway, namely RAB1A and ARFGAP1. They show that ATG2A is recruited to membranes positive for RAB1A, which they also show to interact with ATG2A. In agreement with earlier findings by other groups, silencing RAB1A negatively affects autophagy. While ARFGAP1 was also found on ATG2A positive membranes, silencing ARFGAP1 had no impact autophagy. Notably, these ARFGAP1 positive membranes are not Golgi membranes.

The findings are interesting and the data are in general of good quality. I think the story is good enough to be published in eLife and I have the following questions, which the authors may attend to:

(1) Are the membranes to which ATG2A is recruited a form of ERGIC?

(2) Figure 3A/B: Is it possible to show a better example? The difference is barely detectable by eye. Since Immunoblotting is not really a quantitative method, I think that such a weak effect is prone to be wrong. Is there another tool/assay to validate this result?

(3) Is the curvature-sensitive region of ARFGAP1 required for its co-localization with ATG2A?

(4) What does Rab1A do? What is its effector? Or does the GTPase itself remodel the membrane?

(5) What about Arf1? It appears that this role of ARFGAP1 is unrelated to Arf1 and COPI? Thus, one would predict that Arf1 does not localize to these structures and does not affect ATG2A function

(6) Does ARFGAP1 promote fission of the membrane from its donor compartment?

(7) What are ARFGAP1 and Rab1A recruited to? What is the lipid composition, or protein that recruits these two players to regulate autophagy?

Comments on the latest version:

The revisions carried out by the authors are fine. The new data on ArfGAP1 and about the indirectness of the ATG2A and Rab1A interaction improve both clarity and strength of the manuscript. I have no further comments.

Reviewer #1 (Public review):

Summary:

Participants learned a graph-based representation, but, contrary to the hypotheses, failed to show neural replay shortly after. This prompted a critical inquiry into temporally delayed linear modeling (TDLM)--the algorithm used to find replay. First, it was found that TDLM detects replay only at implausible numbers of replay events per second. Second, it detects replay-to-cognition correlations only at implausible densities. Third, there are concerning baseline shifts in sequenceness across participants. Fourth, spurious sequences arise in control conditions without a ground truth signal. Fifth, the revised manuscript adapts a previously published synthetic simulation to show that previous validations/support of TDLM may have overestimated TDLM sensitivity because synthetic assumptions can produce unrealistically high pattern separability and reduced baseline confounds.

Strengths:

- This work is meticulous and meets a high standard of transparency and open science, with preregistration, code and data sharing, external resources such as a GUI with the task and material for the public.

- The writing is clear, balanced, and matter-of-fact.

- By injecting visually evoked empirical data into the simulation, many surface-level problems are avoided, such as biological plausibility and questions of signal-to-noise ratio.

- The investigation of sequenceness-to-cognition correlations is an especially useful add-on because much of the previous work uses this to make key claims about replay as a mechanism.

- In the revised version, the authors foreshadow ways to improve sequenceness detection by introducing a sign-flipping analysis.

Weaknesses:

Many of the weaknesses are not so much flaws in the analyses, but shortcomings when it comes to interpretation and a lack of making these findings as useful as they could be. Furthermore, as I will explain below, some weaknesses have been partially improved in the last round of revisions.

- I found the bigger picture analysis to be lacking, though improved in the latest version. Let us take stock: in other work during active cognition, including at least one study from the Authors, TDLM shows significant sequenceness. But the evidence provided here suggests that even very strong localizer patterns injected into the data cannot be detected as replay except at implausible speeds. How can both of these things be true? Assuming these analyses are cogent, do these findings not imply something more destructive about all studies that found positive results with TDLM? In the revisions, the manuscript concentrates a bit more on criteria that influence detection of sequences, though it is still not entirely clear what consequences there are for previous work.

- All things considered, TDLM seems like a fairly vanilla and low assumption algorithm for finding event sequences. Although the authors have improved their discussion of "boundary conditions" or factors for why TDLM might fail, it remains not fully clear to what extent the core problem is TDLM on an algorithmic/mathematical level (intrinsic factor), vs data quality, power, window size (extrinsic factors).

- The new sign-flip analysis underscores the authors' goal of being solution-oriented, though it is important to emphasize that a comprehensive way forward is not yet provided. This is fine, but the manuscript could be improved further through a concrete alternative or a revised version of the original approach.

Reviewer #2 (Public review):

Summary:

Kern et al. investigated whether temporally delayed linear modeling (TDLM) can uncover sequential memory replay from a graph-learning task in human MEG during an 8 minute post-learning rest period. After failing to detect replay events, they conduct a simulation study in which they insert synthetic replay events, derived from each participants' localizer data, into a control rest period prior to learning. The simulations suggest that TDLM only reveals sequences when replay occurs at very high densities (> 80 per minute) and that individual differences in baseline sequenceness may lead to spurious and/or lacklustre correlations between replay strength and behavior.

Strengths:

The approach is extremely well documented and rigorous. The authors have done an excellent job re-creating the TDLM methodology that is most commonly used, reporting the different approaches and parameters that they used, and reporting their preregistrations. The hybrid simulation study is creative and provides a new way to assess the efficacy of replay decoding methods, and its comparison to earlier published TDLM simulations is particularly useful. The authors remain measured in the scope/applicability of their conclusions, constructive in their discussion, and end with a useful set of recommendations for how to best apply TDLM in future studies. I also want to commend this work for not only presenting a null result, but thoroughly exploring the conditions under which such a null result is expected. I think this paper is interesting and will be generally quite useful for the field.

In the revised version, the authors have adequately addressed each of the weaknesses I raised previously. In brief, they:

(i) Added new power analyses of sequenceness for bootstrapped sample sizes, along with a new permutation test (Supplemental Fig 11),

(ii) Qualified their conclusions with added limitations and clarified several points that I found previously unclear,

(iii) Added several new analyses to the Appendices

(iv) Demonstrated that previous simulations validating TDLM overestimated TDLM sensitivity relative to the hybrid simulation.

(v) Added a new and extensive appendix on the relationship between TDLM and replay characteristics.

Weaknesses:

The remaining weaknesses of the work relate primarily to explaining the cause of measured non-random fluctuations in the simulated correlations between replay detection and performance at different time lags, as well as a lack of general recommendations of parameter choices for applying TDLM in future work. But these are minor weaknesses that can be left to future work.

Reviewer #3 (Public review):

Summary:

Kern et al. critically assess the sensitivity of temporally delayed linear modelling (TDLM), a relatively new method used to detect memory replay in humans via MEG. While TDLM has recently gained traction and been used to report many exciting links between replay and behavior in humans, Kern et al. were unable to detect replay during a post-learning rest period. To determine whether this null result reflected an actual absence of replay or sensitivity of the method, the authors ran a simulation: synthetic replay events were inserted into a control dataset, and TDLM was used to decode them, varying both replay density and its correlation with behavior. The results revealed that TDLM could only reliably detect replay at unrealistically (not-physiological) high replay densities, and the authors were unable to induce strong behavior correlations. These findings highlight important limitations of TDLM, particularly for detecting replay over extended, minutes long time periods.

Strengths:

Overall, I think this is an extremely important paper, given the growing use of TDLM to report exciting relationships between replay and behavior in humans. I found the text clear, the results compelling, and the critique of TDLM quite fair: it is not that this method can never be applied, but just that it has limits in its sensitivity to detect replay during minutes long periods. Further, I greatly appreciated the authors efforts to describe ways to improve TDLM: developing better decoders and applying them to smaller time windows.

The power of this paper comes from the simulation whereby the authors inserted replay events and attempted to detect them using TDLM. Regarding their first study, there are many alternative explanations or possible analysis strategies that the authors do not discuss; however, none of these are relevant if replayed, under conditions where it is synthetically inserted, cannot be detected.

Further, the authors provide a simulation and series of analyses aimed at replicating previous TDLM-based replay studies. They demonstrate methodological flaws, and show that previous simulations greatly overestimated the sensitivity of TDLM. This work emphasizes the need to cast a critical eye over both past and future studies applying TDLM to detect replay.

Finally, the authors are relatively clear about which parameters they chose, why they chose them, and how well they match previous literature (they seem well matched); and provide suggestions for how others can determine the best parameters for TDLM within their own experimental contexts.

Comments on revisions:

The authors thoroughly addressed my previous comments; the added analyses and discussion significantly strengthen the paper's clarity, utility, and impact.

Reviewer #1 (Public Review):

Summary:

Zeng et al. have investigated the impact of inhibiting lactate dehydrogenase (LDH) on glycolysis and the tricarboxylic acid cycle. LDH is the terminal enzyme of aerobic glycolysis or fermentation that converts pyruvate and NADH to lactate and NAD+ and is essential for the fermentation pathway as it recycles NAD+ needed by upstream glyceraldehyde-3-phosphate dehydrogenase. As the authors point out in the introduction, multiple published reports have shown that inhibition of LDH in cancer cells typically leads to a switch from fermentative ATP production to respiratory ATP production (i.e., glucose uptake and lactate secretion are decreased, and oxygen consumption is increased). The presumed logic of this metabolic rearrangement is that when glycolytic ATP production is inhibited due to LDH inhibition, the cell switches to producing more ATP using respiration. This observation is similar to the well-established Crabtree and Pasteur effects, where cells switch between fermentation and respiration due to the availability of glucose and oxygen. Unexpectedly, the authors observed that inhibition of LDH led to inhibition of respiration and not activation as previously observed. The authors perform rigorous measurements of glycolysis and TCA cycle activity, demonstrating that under their experimental conditions, respiration is indeed inhibited. Given the large body of work reporting the opposite result, it is difficult to reconcile the reasons for the discrepancy. In this reviewer's opinion, a reason for the discrepancy may be that the authors performed their measurements 6 hours after inhibiting LDH. Six hours is a very long time for assessing the direct impact of a perturbation on metabolic pathway activity, which is regulated on a timescale of seconds to minutes. The observed effects are likely the result of a combination of many downstream responses that happen within 6 hours of inhibiting LDH that causes a large decrease in ATP production, inhibition of cell proliferation, and likely a range of stress responses, including gene expression changes.

Strengths:

The regulation of metabolic pathways is incompletely understood, and more research is needed, such as the one conducted here. The authors performed an impressive set of measurements of metabolite levels in response to inhibition of LDH using a combination of rigorous approaches.

Weaknesses:

Glycolysis, TCA cycle, and respiration are regulated on a timescale of seconds to minutes. The main weakness of this study is the long drug treatment time of 6 hours, which was chosen for all the experiments. In this reviewer's opinion, if the goal was to investigate the direct impact of LDH inhibition on glycolysis and the TCA cycle, most of the experiments should have been performed immediately after or within minutes of LDH inhibition. After 6 hours of inhibiting LDH and ATP production, cells undergo a whole range of responses, and most of the observed effects are likely indirect due to the many downstream effects of LDH and ATP production inhibition, such as decreased cell proliferation, decreased energy demand, activation of stress response pathways, etc.

Comments on revisions:

Based on the response to comments that the authors have submitted, I do not think I need to make any changes to my review, as the time course experiment that could have explained the difference between reported results and extensive prior literature has not been performed.