Reviewer #2 (Public review):

Summary:

In this work, the authors present a differentiable version of the widely-used Gillespie Algorithm. The Gillespie Algorithm has been used for decades to simulate the behavior of stochastic biochemical reaction networks. But while the Gillespie Algorithm is a powerful tool for the forward simulation of biochemical systems given some set of known reaction parameters, it cannot be used for reverse process, i.e. inferring reaction parameters given a set of measured system characteristics. The Differentiable Gillespie Algorithm ("DGA") overcomes this limitation by approximating two discontinuous steps in the Gillespie Algorithm with continuous functions. This makes it possible to calculate of gradients for each step in the simulation process which, in turn, allows the reaction parameters to be optimized via powerful backpropagation techniques. In addition to describing the theoretical underpinnings of DGA, the authors demonstrate different potential use-cases for the algorithm in the context of simple models of stochastic gene expression.

Overall, the DGA represents an important conceptual step forward for the field, and should lay the groundwork for exciting innovations in the analysis and design of stochastic reaction networks. At the same time, significantly more work is needed to establish when the approximations made by DGA are valid, and to demonstrate the viability of the algorithm in the context of complicated reaction networks.

Strengths:

This work makes an important conceptual leap by introducing a version of the Gillespie Algorithm that is end-to-end differentiable. This idea alone has the potential to drive a number of exciting innovations in the analysis, inference, and design of biochemical reaction networks. Beyond the theoretical adjustments, the authors also implement their algorithm in a Python-based codebase that combines DGA powerful optimization libraries like PyTorch. This codebase has the potential to be of interest to a wide range of researchers, even if the true scope of the method's applicability remains to be fully determined.

The authors also demonstrate how DGA can be used in practice both to infer reaction parameters from real experimental data (Figure 7) and to design networks with user-specified input-output characteristics (Figure 8). These illustrations should provide a nice roadmap for researchers interested in applying DGA to their own projects/systems.

Finally, although it does not stem directly from DGA, the exploration of pairwise parameter dependencies in different network architectures provides an interesting window into the design constraints (or lack thereof) that shape the architecture of biochemical reaction networks.

Weaknesses:

While it is clear that the DGA represents an important conceptual advancement, the authors do not do enough in the present manuscript to (i) validate the robustness of DGA inference and (ii) demonstrate that DGA inference works in the kinds of complex biochemical networks where it would actually be of legitimate use.

It is to the authors' credit that they are open and explicit about the potential limitations of DGA due to breakdowns in its continuous approximations. However they do not provide the reader with nearly enough empirical (i.e. simulation-based) or theoretical context to assess when, why, and to what extent DGA will fail in different situations. In Figure 2, they compare DGA to GA (i.e. ground-truth) in the context of a simple two state model of a stochastic transcription. Even in this minimal system, we see that DGA deviates notably from ground-truth both in the simulated mRNA distributions (Figure 2A) and in the ON/OFF state occupancy (Figure 2C). This begs the question of how DGA will scale to more complicated systems, or systems with non-steady state dynamics. Will the deviations become more severe? This is important because, in practice, there is really not much need for using DGA with a simple 2 state system-we have analytic solutions for this case. It is the more complex systems where DGA has the potential to move the needle.

A second concern is that the authors' present approach for parameter inference and error calculation does not seem to be reliable. For example, in Figure 5A, they show DGA inference results for the ON rate of a two-state system. We see substantial inference errors in this case, even though the inference problem should be non-degenerate in this case. One reason for this seems to be that the inference algorithm does not reliably find the global minimum of the loss function (Figure 2B). To turn DGA into a viable approach, it is paramount that the authors find some way to improve this behavior, perhaps by using multiple random initializations to better search the loss space.

Finally, the authors do a good job of illustrating how DGA might be used to infer biological parameters (Figure 7) and design reaction networks with desired input-output characteristics (Figure 8). However, analytic solutions exist for both of the systems they select for examples. This means that, in practice, there would be no need for DGA in these contexts, since one could directly optimize, e.g., the expressions for the mean and Fano Factor of the system in Figure 7A. I still believe that it is useful to have these examples, but it seems critical to add a use-case where DGA is the only option.

Reviewer #3 (Public review):

Summary:

This manuscript introduces a differentiable variant of the Gillespie algorithm (DGA) that allows gradient calculation using backpropagation. The most significant contribution of this work is the development of the DGA itself, a novel approach to making stochastic simulations differentiable. This is achieved by replacing discontinuous operations in the traditional Gillespie algorithm with smooth, differentiable approximations using sigmoid and Gaussian functions. This conceptual advance opens up new avenues for applying powerful gradient-based optimization techniques, prevalent in machine learning, to studying stochastic biological systems.

The method was tested on a simple two-state promoter model of gene expression. The authors found that the DGA accurately captured the moments of the steady-state distribution and other major qualitative features. However, it was less accurate at capturing information about the distribution's tails, potentially because rare events result from frequent low-probability reaction events where the approximations made by the DGA have a greater impact. The authors could further use the DGA to design a four-state promoter model of gene regulation that exhibited a desired input-output relationship. The DGA could learn parameters that produced a sharper response curve, which was achieved by consuming more energy.

The authors conclude that the DGA is a powerful tool for analyzing and designing stochastic systems.

Strengths:

The DGA allows gradient-based optimization techniques to estimate parameters and design networks with desired properties.

The DGA efficacy in estimating kinetic parameters from both synthetic and experimental data. This capability highlights the DGA's potential to extract meaningful biophysical parameters from noisy biological data.

The DGA's ability to design a four-state promoter architecture exhibiting a desired input-output relationship. This success indicates the potential of the DGA as a valuable tool for synthetic biology, enabling researchers to engineer biological circuits with predefined behaviours.

Weaknesses:

The study primarily focuses on analysing the steady-state properties of stochastic systems. It is unclear how and if this framework can be used beyond the steady-state data presented in the case studies, where it is already quite computationally heavy.<br /> A more in-depth exploration of the DGA's performance in analysing dynamic trajectories, which capture the system's evolution over time, would provide a more comprehensive view of the algorithm's capabilities.<br /> Gradient computations in the DGA can be susceptible to numerical instability, particularly when the sharpness parameters of the sigmoid and Gaussian approximations are set to high values. This issue could lead to challenges in convergence during the optimization process.

Reviewer #1 (Public review):

Summary:

The authors provide a resource to the systems neuroscience community, by offering their Python-based CLoPy platform for closed-loop feedback training. In addition to using neural feedback, as is common in these experiments, they include a capability to use real-time movement extracted from DeepLabCut as the control signal. The methods and repository are detailed for those who wish to use this resource. Furthermore, they demonstrate the efficacy of their system through a series of mesoscale calcium imaging experiments. These experiments use a large number of cortical regions for the control signal in the neural feedback setup, while the movement feedback experiments are analyzed more extensively.

Strengths:

The primary strength of the paper is the availability of their CLoPy platform. Currently, most closed-loop operant conditioning experiments are custom built by each lab and carry a relatively large startup cost to get running. This platform lowers the barrier to entry for closed-loop operant conditioning experiments, in addition to making the experiments more accessible to those with less technical expertise.

Another strength of the paper is the use of many different cortical regions as control signals for the neurofeedback experiments. Rodent operant conditioning experiments typically record from the motor cortex and maybe one other region. Here, the authors demonstrate that mice can volitionally control many different cortical regions not limited to those previously studied, recording across many regions in the same experiment. This demonstrates the relative flexibility of modulating neural dynamics, including in non-motor regions.

Finally, adapting the closed-loop platform to use real-time movement as a control signal is a nice addition. Incorporating movement kinematics into operant conditioning experiments has been a challenge due to the increased technical difficulties of extracting real-time kinematic data from video data at a latency where it can be used as a control signal for operant conditioning. In this paper they demonstrate that the mice can learn the task using their forelimb position, at a rate that is quicker than the neurofeedback experiments.

Weaknesses:

There are several weaknesses in the paper that diminish the impact of its strengths. First, the value of the CLoPy platform is not clearly articulated to the systems neuroscience community. Similarly, the resource could be better positioned within the context of the broader open-source neuroscience community. For an example of how to better frame this resource in these contexts, I recommend consulting the pyControl paper. Improving this framing will likely increase the accessibility and interest of this paper to a less technical neuroscience audience, for instance by highlighting the types of experimental questions CLoPy can enable.

While the dataset contains an impressive amount of animals and cortical regions for the neurofeedback experiment, and an analysis of the movement-feedback experiments, my excitement for these experiments is tempered by the relative incompleteness of the dataset, as well as its description and analysis in the text. For instance, in the neurofeedback experiment, many of these regions only have data from a single mouse, limiting the conclusions that can be drawn. Additionally, there is a lack of reporting of the quantitative results in the text of the document, which is needed to better understand the degree of the results. Finally, the writing of the results section could use some work, as it currently reads more like a methods section.

Suggestions for improved or additional experiments, data or analyses:

Not necessary for this paper, but it would be interesting to see if the CLNF group could learn without auditory feedback.

There are no quantitative results in the results section. I would add important results to help the reader better interpret the data. For example, in: "Our results indicated that both training paradigms were able to lead mice to obtain a significantly larger number of rewards over time," You could show a number, with an appropriate comparison or statistical test, to demonstrate that learning was observed.

For: "Performing this analysis indicated that the Raspberry Pi system could provide reliable graded feedback within ~63 {plus minus} 15 ms for CLNF experiments." The LED test shows the sending of the signal, but the actual delay for the audio generation might be longer. This is also longer than the 50 ms mentioned in the abstract.

It could be helpful to visualize an individual trial for each experiment type, for instance how the audio frequency changes as movement speed / calcium activity changes.

The sample sizes are small (n=1) for a few groups. I am excited by the variety of regions recorded, so it could be beneficial for the authors to collect a few more animals to beef up the sample sizes.

I am curious as to why 60 trials sessions were used. Was it mostly for the convenience of a 30 min session, or were the animals getting satiated? If the former, would learning have occurred more rapidly with longer sessions?

Figure 4 E is interesting, it seems like the changes in the distribution of deltaF was in both positive and negative directions, instead of just positive. I'd be curious as to the author's thoughts as to why this is the case. Relatedly, I don't see Figure 4E, and a few other subplots, mentioned in the text. As a general comment, I would address each subplot in the text.

For: "In general, all ROIs assessed that encompassed sensory, pre-motor, and motor areas were capable of supporting increased reward rates over time," I would provide a visual summary showing the learning curves for the different types of regions.

Relatedly, I would further explain the fast vs slow learners, and if they mapped onto certain regions.

Also I would make the labels for these plots (e.g. Supp Fig3) more intuitive, versus the acronyms currently used.

The CLMF animals showed a decrease in latency across learning, what about the CLNF animals? There is currently no mention in the text or figures.

Reviewer #2 (Public review):

Summary:

In this work, Gupta & Murphy present several parallel efforts. On one side, they present the hardware and software they use to build a head-fixed mouse experimental setup that they use to track in "real-time" the calcium activity in one or two spots at the surface of the cortex. On the other side, the present another setup that they use to take advantage of the "real-time" version of DeepLabCut with their mice. The hardware and software that they used/develop is described at length, both in the article and in a companion GitHub repository. Next, they present experimental work that they have done with these two setups, training mice to max out a virtual cursor to obtain a reward, by taking advantage of auditory tone feedback that is provided to the mice as they modulate either (1) their local cortical calcium activity, or (2) their limb position.

Strengths:

This work illustrates the fact that thanks to readily available experimental building blocks, body movement and calcium imaging can be carried using readily available components, including imaging the brain using an incredibly cheap consumer electronics RGB camera (RGB Raspberry Pi Camera). It is a useful source of information for researchers that may be interested in building a similar setup, given the highly detailed overview of the system. Finally, it further confirms previous findings regarding the operant conditioning of the calcium dynamics at the surface of the cortex (Clancy et al. 2020) and suggests an alternative based on deeplabcut to the motor tasks that aim to image the brain at the mesoscale during forelimb movements (Quarta et al. 2022).

Weaknesses:

This work covers 3 separate research endeavors: (1) The development of two separate setups, their corresponding software. (2) A study that is highly inspired from the Clancy et al. 2020 paper on the modulation of the local cortical activity measured through a mesoscale calcium imaging setup. (3) A study of the mesoscale dynamics of the cortex during forelimb movements learning. Sadly, the analyses of the physiological data appears uncomplete, and more generally the paper tends to offer overstatements regarding several points:<br /> - In contrast to the introductory statements of the article, closed-loop physiology in rodents is a well-established research topic. Beyond auditory feedback, this includes optogenetic feedback (O'Connor et al. 2013, Abbasi et al. 2018, 2023), electrical feedback in hippocampus (Girardeau et al. 2009), and much more.<br /> - The behavioral setups that are presented are representative of the state of the art in the field of mesoscale imaging/head fixed behavior community, rather than a highly innovative design. In particular, the closed-loop latency that they achieve (>60 ms) may be perceived by the mice. This is in contrast with other available closed-loop setups.<br /> - Through the paper, there are several statements that point out how important it is to carry out this work in a closed-loop setting with an auditory feedback, but sadly there is no "no feedback" control in cortical conditioning experiments, while there is a no-feedback condition in the forelimb movement study, which shows that learning of the task can be achieved in the absence of feedback.<br /> - The analysis of the closed-loop neuronal data behavior lacks controls. Increased performance can be achieved by modulating actively only one of the two ROIs, this is not clearly analyzed (for instance looking at the timing of the calcium signal modulation across the two ROIs. It seems that overall ROIs1 and 2 covariate, in contrast to Clancy et al. 2020. How can this be explained?

Reviewer #3 (Public review):

Summary:

The study demonstrates the effectiveness of a cost-effective closed-loop feedback system for modulating brain activity and behavior in head-fixed mice. Authors have tested real-time closed-loop feedback system in head-fixed mice two types of graded feedback: 1) Closed-loop neurofeedback (CLNF), where feedback is derived from neuronal activity (calcium imaging), and 2) Closed-loop movement feedback (CLMF), where feedback is based on observed body movement. It is a python based opensource system, and authors call it CLoPy. The authors also claim to provide all software, hardware schematics, and protocols to adapt it to various experimental scenarios. This system is capable and can be adapted for a wide use case scenario.

Authors have shown that their system can control both positive (water drop) and negative reinforcement (buzzer-vibrator). This study also shows that using the close loop system mice have shown better performance, learnt arbitrary task and can adapt to change in the rule as well. By integrating real-time feedback based on cortical GCaMP imaging and behavior tracking authors have provided strong evidence that such closed-loop systems can be instrumental in exploring the dynamic interplay between brain activity and behavior.

Strengths:

Simplicity of feedback systems designed. Simplicity of implementation and potential adoption.

Weaknesses:

Long latencies, due to slow Ca2+ dynamics and slow imaging (15 FPS), may limit the application of the system.

Major comments:

(1) Page 5 paragraph 1: "We tested our CLNF system on Raspberry Pi for its compactness, general-purpose input/output (GPIO) programmability, and wide community support, while the CLMF system was tested on an Nvidia Jetson GPU device." Can these programs and hardware be integrated with windows-based system and a microcontroller (Arduino/ Tency). As for the broad adaptability that's what a lot of labs would already have (please comment/discuss)?

(2) Hardware Constraints: The reliance on Raspberry Pi and Nvidia Jetson (is expensive) for real-time processing could introduce latency issues (~63 ms for CLNF and ~67 ms for CLMF). This latency might limit precision for faster or more complex behaviors, which authors should discuss in the discussion section.

(3) Neurofeedback Specificity: The task focuses on mesoscale imaging and ignores finer spatiotemporal details. Sub-second events might be significant in more nuanced behaviors. Can this be discussed in the discussion section?

(4) The activity over 6s is being averaged to determine if the threshold is being crossed before the reward is delivered. This is a rather long duration of time during which the mice may be exhibiting stereotyped behaviors that may result in the changes in DFF that are being observed. It would be interesting for the authors to compare (if data is available) the behavior of the mice in trials where they successfully crossed the threshold for reward delivery and in those trials where the threshold was not breached. How is this different from spontaneous behavior and behaviors exhibited when they are performing the test with CLNF?

Reviewer #1 (Public review):

Summary:

Fluorescence imaging has become an increasingly popular technique for monitoring neuronal activity and neurotransmitter concentrations in the living brain. However, factors such as brain motion and changes in blood flow and oxygenation can introduce significant artifacts, particularly when activity-dependent signals are small. Yogesh et al. quantified these effects using GFP, an activity-independent marker, under two-photon and wide-field imaging conditions in awake behaving mice. They report significant GFP responses across various brain regions, layers, and behavioral contexts, with magnitudes comparable to those of commonly used activity sensors. These data highlight the need for robust control strategies and careful interpretation of fluorescence functional imaging data.

Strengths:

The effect of hemodynamic occlusion in two-photon imaging has been previously demonstrated in sparsely labeled neurons in V1 of anesthetized animals (see Shen and Kara et al., Nature Methods, 2012). The present study builds on these findings by imaging a substantially larger population of neurons in awake, behaving mice across multiple cortical regions, layers, and stimulus conditions. The experiments are extensive, the statistical analyses are rigorous, and the results convincingly demonstrate significant GFP responses that must be accounted for in functional imaging experiments. However, whether these GFP responses are driven by hemodynamic occlusion remains less clear, given the complexities associated with awake imaging and GFP's properties (see below).

Weaknesses:

(1) The authors primarily attribute the observed GFP responses to hemodynamic occlusion. While this explanation is plausible, other factors may also contribute to the observed signals. These include uncompensated brain movement (e.g., axial-direction movements), leakage of visual stimulation light into the microscope, and GFP's sensitivity to changes in intracellular pH (see e.g., Kneen and Verkman, 1998, Biophysical Journal). Although the correlation between GFP signals and blood vessel diameters supports a hemodynamic contribution, it does not rule out significant contributions from these (or other) factors. Consequently, whether GFP fluorescence can reliably quantify hemodynamic occlusion in two-photon microscopy remains uncertain.

(2) Regardless of the underlying mechanisms driving the GFP responses, these activity-independent signals must be accounted for in functional imaging experiments. However, the present manuscript does not explore potential strategies to mitigate these effects. Exploring and demonstrating even partial mitigation strategies could have significant implications for the field.

(3) Several methodology details are missing from the Methods section. These include: (a) signal extraction methods for two-photon imaging data (b) neuropil subtraction methods (whether they are performed and, if so, how) (c) methods used to prevent visual stimulation light from being detected by the two-photon imaging system (d) methods to measure blood vessel diameter/area in each frame. The authors should provide more details in their revision.

Reviewer #2 (Public review):

Approach

In this study, Yogesh et al. aimed at characterizing hemodynamic occlusion in two photon imaging, where its effects on signal fluctuations are underappreciated compared to that in wide field imaging and fiber photometry. The authors used activity-independent GFP fluorescence, GCaMP and GRAB sensors for various neuromodulators in two-photon and widefield imaging during a visuomotor context to evaluate the extent of hemodynamic occlusion in V1 and ACC. They found that the GFP responses were comparable in amplitude to smaller GCaMP responses, though exhibiting context-, cortical region-, and depth-specific effects. After quantifying blood vessel diameter change and surrounding GFP responses, they argued that GFP responses were highly correlated with changes in local blood vessel size. Furthermore, when imaging with GRAB sensors for different neuromodulators, they found that sensors with lower dynamic ranges such as GRAB-DA1m, GRAB-5HT1.0, and GRAB-NE1m exhibited responses most likely masked by the hemodynamic occlusion, while a sensor with larger SNR, GRAB-ACh3.0, showed much more distinguishable responses from blood vessel change.

Strengths

This work is of broad interest to two photon imaging users and GRAB developers and users. It thoroughly quantifies the hemodynamic driven GFP response and compares it to previously published GCaMP data in a similar context, and illustrates the contribution of hemodynamic occlusion to GFP and GRAB responses by characterizing the local blood vessel diameter and fluorescence change. These findings provide important considerations for the imaging community and a sobering look at the utility of these sensors for cortical imaging.

Importantly, they draw clear distinctions between the temporal dynamics and amplitude of hemodynamic artifacts across cortical regions and layers. Moreover, they show context dependent (Dark versus during visual stimuli) effects on locomotion and optogenetic light-triggered hemodynamic signals.

Most of the first generation neuromodulator GRAB sensors showed relatively small responses, comparable to blood vessel changes in two photon imaging, which emphasizes a need for improved the dynamic range and response magnitude for future sensors and encourages the sensor users to consider removing hemodynamic artifacts when analyzing GRAB imaging data.

Weaknesses

The largest weakness of the paper is that, while they convincingly quantify hemodynamic artifacts across a range of conditions, they do not quantify any methods of correcting for them. The utility of the paper could have been greatly enhanced had they tested hemodynamic correction methods (e.g. from Ocana-Santero et al., 2024) and applied them to their datasets. This would serve both to verify their findings-proving that hemodynamic correction removes the hemodynamic signal-and to act as a guide to the field for how to address the problem they highlight.

The paper attributes the source of 'hemodynamic occlusion' primarily to blood vessel dilation, but leaves unanswered how much may be due to shifts in blood oxygenation. Figure 4 directly addresses the question of how much of the signal can be attributed to occlusion by measuring the blood vessel dilation, but notably fails to reproduce any of the positive transients associated with locomotion in Figure 2. Thus, an investigation into or at least a discussion of what other factors (movement? Hb oxygenation?) may drive these distinct signals would be helpful.

Along these lines, the authors carefully quantified the correlation between local blood vessel diameter and GFP response (or neuropil fluorescence vs blood vessel fluorescence with GRAB sensors). To what extent does this effect depend on proximity to the vessels? Do GFP/ GRAB responses decorrelate from blood vessel activity in neurons further from vessels (refer to Figure 5A and B in Neyhart et al., Cell Reports 2024)?

Raw traces are shown in Figure 2 but we are never presented with the unaveraged data for locomotion of stimulus presentation times, which limits the reader's ability to independently assess variability in the data. Inclusion of heatmaps comparing event aligned GFP to GCaMP6f may be of value to the reader.

More detailed analysis of differences between the kinds of dynamics observed in GFP vs GCaMP6f expressing neurons could aid in identifying artifacts in otherwise clean data. The example neurons in Figure 2A hint at this as each display unique waveforms and the question of whether certain properties of their dynamics can reveal the hemodynamic rather than indicator driven nature of the signal is left open. Eg. do the decay rate and rise times differ significantly from GCaMP6f signals?

The authors suggest that signal to noise ratio of an indicator likely affects the ability to separate hemodynamic response from the underlying fluorescence signal. Does the degree of background fluorescence affect the size of the artifact? If there was variation in background and overall expression level in the data this could potentially be used to answer this question. Could lower (or higher!) expression levels increase the effects of hemodynamic occlusion?<br /> The choice of the phrase 'hemodynamic occlusion' may cause some confusion as the authors address both positive and negative responses in the GFP expressing neurons, and there may be additional contributions from changes in blood oxygenation state.

The choice of ACC as the frontal region provides a substantial contrast in location, brain movement, and vascular architecture as compared to V1. As the authors note, ACC is close to the superior sagittal sinus and thus is the region where the largest vascular effects are likely to occur. The reader is left to wonder how much of the ROI may or may not have included vasculature in the ACC vs V1 recordings as the only images of the recording sites provided are for V1. We are left unable to conclude whether the differences observed between these regions are due to the presence of visible vasculature, capillary blood flow or differences in neurovasculature coupling between regions. A less medial portion of M2 may have been a more appropriate comparison. At least, inclusion of more example imaging fields for ACC in the supplementary figures would be of value.

In Figure 3, How do the proportions of responsive GFP neurons compare to GCaMP6f neurons?

How is variance explained calculated in Figure 4? Is this from a linear model and R^2 value? Is this variance estimate for separate predictors by using single variable models? The methods should describe the construction of the model including the design matrix and how the model was fit and if and how cross validation was run.

Cortical depth is coarsely defined as L2/3 or L5, without numerical ranges in depth from pia.

Overall Assessment:

This paper is an important contribution to our understanding of how hemodynamic artifacts may corrupt GRAB and calcium imaging, even in two-photon imaging modes. Certain useful control experiments, such as intrinsic optical imaging in the same paradigms, were not reported, nor were any hemodynamic correction methods investigated. Thus, this limits both mechanistic conclusions and the overall utility with respect to immediate applications by end users. Nevertheless, the paper is of significant importance to anyone conducting two-photon or widefield imaging with calcium and GRAB sensors and deserves the attention of the broader neuroscience and in-vivo imaging community.

Reviewer #3 (Public review):

Summary:

In this study, the authors aimed to investigate if hemodynamic occlusion contributes to fluorescent signals measured with two-photon microscopy. For this, they image the activity-independent fluorophore GFP in 2 different cortical areas, at different cortical depths and in different behavioral conditions. They compare the evoked fluorescent signals with those obtained with calcium sensors and neuromodulator sensors and evaluate their relationship to vessel diameter as a readout of blood flow.<br /> They find that GFP fluorescence transients are comparable to GCaMP6f stimuli-evoked signals in amplitude, although they are generally smaller. Yet, they are significant even at the single neuronal level. They show that GFP fluorescence transients resemble those measured with the dopamine sensor GRAB-DA1m and the serotonin sensor GRAB-5HT1.0 in amplitude an nature, suggesting that signals with these sensors are dominated by hemodynamic occlusion. 
Moreover, the authors perform similar experiments with wide-field microscopy which reveals the similarity between the two methods in generating the hemodynamic signals. Together the evidence presented calls for the development and use of high dynamic range sensors to avoid measuring signals that have another origin from the one intended to measure. In the meantime, the evidence highlights the need to control for those artifacts such as with the parallel use of activity independent fluorophores.

Strengths:

- Comprehensive study comparing different cortical regions in diverse behavioral settings in controlled conditions.<br /> - Comparison to the state-of-the-art, i.e. what has been demonstrated with wide-field microscopy.<br /> - Comparison to diverse activity-dependent sensors, including the widely used GCaMP.

Weaknesses:

- The kinetics of GCaMP is stereotypic. An analysis/comment on if and how the kinetics of the signals could be used to distinguish the hemodynamic occlusion artefacts from calcium signals would be useful.<br /> - Is it possible that motion is affecting the signals in a certain degree? This issue is not made clear.<br /> - The causal relationship with blood flow remains open. Hemodynamic occlusion seems a good candidate causing changes in GFP fluorescence, but this remains to be well addressed in further research.

Reviewer #1 (Public review):

Summary:

This study aims to investigate the links between social behaviors observed in free-moving situations and behavioral performances measured in well-controlled, laboratory settings. The authors assessed general social tendencies and dyadic relationships among four monkeys in a group by scoring agonistic (aggression) and affiliative (grooming and proximity) behaviors in each pair. By measuring the saccadic reaction time in a classic social interference task, the authors reported that the monkeys with higher SEIs (i.e., more social individuals) were less distracted by the faces of other monkeys. These effects were enhanced when the distractors were out-group monkey faces rather than in-group ones. Lastly, oxytocin administration increased the impact of the out-group monkey faces in the social interference task, while reducing the magnitude of general social tendencies measured with SEI.

Strengths:

(1) The combination of behavioral data obtained in a colony room and in a laboratory environment is rare and important.<br /> (2) The evaluation of social interactions were successfully performed based on an automated target detection algorithm. The resulting multi-dimensional, complicated social interactions were summarized into simple indices (SEI and IEI). These indices provide a good measure for the social tendencies of each monkey.<br /> (3) Well-designed and robust experiments in the laboratory environment that are linked nicely with the general social tendencies observed in spontaneous behaviors.

Weaknesses:

(1) While the overall results are interesting, I am somewhat left confused about how to interpret the difference in the scores derived from different conditions. For example, the authors stated "Comparing the weights for in-group and out-group distractors, the effect of proximity was larger than that of aggression and grooming" in p.8. Does this mean that the proximity is indeed the type of behavior most affected in the out-group condition compared to the in-group condition? The out-group effects are difficult to examine with actual behavioral data, but some in-group effects such as those involving OT can be tested, which possibly provides good insights into interpreting the differences of the weights observed across the experimental conditions.

(2) I think it is important to provide how variable spontaneous social interactions were across sessions and how impactful the variability of the interactions is on the SEI and IEI, as it helps to understand how meaningful the differences of weights are across the conditions, but such data are missing. In line with this point, although the conclusions still hold as those data were obtained during the same experimental periods, shouldn't the weights in Fig. 3f and Figs. 4g and 4h (saline) be expected to be similar, if not the same?

Reviewer #2 (Public review):

Summary:

The study presents significant findings that elucidate the relationship between multi-dimensional social relationships and social attention in rhesus macaques. By integrating advanced computational methods, behavioral analyses, and neuroendocrine manipulation, the authors provide strong evidence for how oxytocin modulates attention within social networks. The results are robust and address critical gaps in understanding the dynamics of social attention in primates.

Strengths:

(1) The use of YOLOv5 for automatic behavioral detection is an exceptional methodological advance. The combination of automated analyses with manual validation enhances confidence in the data.<br /> (2) The study's focus on three distinct dimensions of social interaction (aggression, grooming, and proximity) is comprehensive and provides nuanced insights into the complexity of primate social networks.<br /> (3) The investigation of oxytocin's role adds a compelling neuroendocrine dimension to the findings, providing a bridge between behavioral and neural mechanisms.

Weaknesses:

(1) The study's conclusions are based on observations of only four monkeys, which limits the generalizability of the findings. Larger sample sizes could strengthen the validity of the results.<br /> (2) The limited set of stimulus images (in-group and out-group faces) may introduce unintended biases. This could be addressed by increasing the diversity of stimuli or incorporating a broader range of out-group members.

Reviewer #1 (Public review):

Summary:

In this manuscript, Kondo et al. developed a method to suppress somatic action potentials while recording spine calcium signals using two-photon imaging in the L2/3 visual cortex in response to visual stimuli. The authors identified different patterns of dendritic spine activation by visual stimuli and analyzed how the different patterns of spine responses may contribute to somatic visual responses. Their analysis results suggest that spines on dendrites with a clustered arrangement can potentially generate sharply tuned output.

Strengths:

This is an interesting study addressing a standing question of how previously reported pepper-and-salt-like distributed sensory inputs on individual spines may give rise to somatic sensory selectivity. The method of somatic inhibition to prevent bAPs appears new and effective. The measurements of spine activity are carefully done. The finding that a small number of spines located in the same branch with similar tuning properties would predict the somatic tuning is consistent with local dendritic nonlinear integration mechanisms.

Weaknesses:

(1) The demonstration of the effectiveness of soma-specific inhibition is inadequate. Figure 1 only provides a single example trace showing the inhibition of somatic visual responses. The authors should provide statistical analysis over grouped data. For the effect of soma-specific inhibition on spine activity, the authors provided mostly negative results, lacking effects on spine responses for both soma inhibition and bAP subtraction. This is confusing. One possible explanation is that bAPs normally have little influence on spine activity. However, this would conflict with the known fact that somatic APs can easily invade spines in L2/3 neurons (e.g., Chen et al., Nature 2011). Another possibility is that under the current experimental conditions, somatic APs were rarely evoked by the visual stimulus. The authors should also rule out the possibility that the spines they imaged are from different neurons than the ones with somatic inhibition. The authors may consider identifying those cases where somatic APs have a significant impact on spine activity or spine tuning and show how bAP inhibition influences the dendritic and spine responses.

(2) Figure 4 shows that the proportion of spines with a preferred orientation similar to the soma (ΔOri {less than or equal to} 30{degree sign}) was 60%, which is surprisingly high. It is intriguing that without somatic AP invasion, there could be such a high degree of similarity between spine activity and somatic tuning. What is the ratio without soma inhibition? One could reason that with bAP invasion, there should be even more spines showing visual responses similar to those of the soma. Moreover, with such a high proportion of spines showing similar sensory tuning to the soma, it is inevitable that many branches contain more spines with similar tuning as the soma, exhibiting an apparent branch-specific clustering. While such apparent clustering may well predict somatic tuning, it primarily reflects a correlational relationship rather than a causal synaptic integration mechanism.

(3) There has been extensive work studying how the integration of spine activity or sub-branch activity gives rise to somatic output. The proposed main contribution of this study is to use an improved method to inhibit somatic activity in order to more confidently measure spine-specific activity and examine the integration mechanisms. However, the results showed that the measured spine-specific activity under soma inhibition was not significantly different from that measured under normal conditions (see point 1). It becomes unclear how this new method contributes to obtaining new insights into the synaptic integration mechanism.

(4) Figure 6 shows how the tuning similarity between spines depends on the distance between them. It is unclear what new information was acquired regarding the functional clustering of spines. This result can be largely explained by the overall higher proportion of similarly tuned spines (60%) compared to the soma's preferred orientations. Moreover, the authors did not demonstrate how such clustering may contribute to nonlinear synaptic integration.

(5) The results shown in Figure 7 can again be largely explained by the static property of a higher proportion of spines tuned similarly to the soma. These results do not reveal any active dendritic integration mechanisms.

Reviewer #2 (Public review):

Summary:

The paper from Kondo et al., addresses how the functional organization of synaptic inputs in 2/3 pyramidal neurons contributes to their output firing. Expressing GCamp6s to monitor calcium activity and the bi-stable inhibitory opsin SwiChR++ to inhibit the somatic activity of the imaged neurons, the authors were able to image up to ~5700 spines in basal dendrites from 6 neurons. Mapping the functional responses of such a large number of dendritic spines and relating it to the output firing of the parent neuron is a remarkable feat. The authors studied the clustering of similarly tuned spines within individual dendrites and found that while some dendrites are similarly tuned to the same orientation of the parent neuron, other dendrites exhibit tuning to other orientations and moreover a significant proportion of dendrites exhibit no tuning. Modelling work suggests that the clustering of spines in a small proportion of dendrites should suffice to give rise to the tuning of the parent cell.

Strengths:

(1) Removal of the potential confound of somatic firing via optogenetic inhibition is convincing and validates a useful tool for the neuroscientific community. As discussed by the authors the tool would be most valuable for the study of excitatory inputs in inhibitory neurons.

(2) The comparison of optogenetic inhibition of somatic responses and isolation of spine-specific signals using the removal of backpropagating action potential by robust regression is an important control and constitutes an important affirmation of previously published work.

(3) The large dataset size provides enough statistical power to test for clustering of similarly tuned spines in basal dendrites.

(4) The study provides a useful replication of previously published results.

(5) Modelling work in the study shows that as in the ferret visual cortex (Wilson et al., 2016), a combination of dendritic nonlinearity and spike thresholding contribute to the sharpness of orientation tuning in the mouse visual cortex.

Weaknesses:

(1) One of the main conclusions of the study, the classification of dendrites according to the presence or absence of visual responses, lacks quantification.

(2) Some of the statistics employed in combination with shuffling controls are not adequate.

(3) All the neurons imaged are very highly tuned (with a very high orientation selectivity index (OSI)). The performance of the models is evaluated by the correlation coefficient between the predicted and the measured somatic tuning curve. The high OSI of the neurons reduces the sensitivity of the evaluation of the models, as it results in extremely high or low correlation coefficients (Figure 8a). It would be important to recapitulate the results from the model for neurons with lower OSI, given that not all L2/3 neurons are so highly tuned.

(4) It is very hard to understand how the modelling results relate to the experimental data, as the definitions of what constitutes a clustered dendrite in the model or in the experimental data are unclear.

Reviewer #1 (Public review):

In this manuscript, Chang et al. investigated the cell type-specific role of the integrin activator Shv in activity-dependent synaptic remodeling. Using the Drosophila larval neuromuscular junction as a model, they show that glial-secreted Shv modulates synaptic plasticity by maintaining the extracellular balance of neuronal Shv proteins and regulating ambient extracellular glutamate concentrations, which in turn affects postsynaptic glutamate receptor abundance. Furthermore, they report that genetic perturbation of glial morphogenesis phenocopies the defects observed with the loss of glial Shv. Altogether, their findings propose a role for glia in activity-induced synaptic remodeling through Shv secretion. While the conclusions are intriguing, several issues related to experimental design and data interpretation merit further discussion.

Reviewer #2 (Public review):

In this paper Chang et al follow up on their lab's previous findings about the secreted protein Shv and its role in activity-induced synaptic remodeling at the fly NMJ. Previously they reported that shv mutants have impaired synaptic plasticity. Normally a high stimulation paradigm should increase bouton size and GluR expression at synapses but this does not happen in shv mutants. The phenotypes relating to activity dependent plasticity were completely recapitulated when Shv was knocked down only in neurons and could be completely rescued by incubation in exogenously applied Shv protein. The authors also showed that Shv activation of integrin signaling on both the pre- and post- synapse was the molecular mechanism underlying its function. Here they extend their study to consider the role of Shv derived from glia in modulating synaptic features at baseline and remodeling conditions. This study is important to understand if and how glia contribute to these processes. Using cell-type specific knockdown of Shv only in glia causes abnormally high baseline GluR expression and prevents activity-dependent increases in bouton size or GluR expression post-stimulation. This does not appear to be a developmental defect as the authors show that knocking down Shv in glia after basic development has the same effects as life long knockdown, so Shv is acting in real time. Restoring Shv in ONLY glia in mutant animals is sufficient to completely rescue the plasticity phenotypes and baseline GluR expression, but glial-Shv does not appear to activate integrin signaling which was shown to be the mechanism for neuronally derived Shv to control plasticity. This led the authors to hypothesize that glial Shv works by controlling the levels of neuronal Shv and extracellular glutamate. They provide evidence that in the absence of glial Shv, synaptic levels of Shv go up overall, presumably indicating that neurons secrete more Shv. In this context which could then work via integrin signaling as described to control plasticity. They use a glutamate sensor and observe decreased signal (extracellular glutamate) from the sensor in glial Shv KD animals, however, this background has extremely high GluR levels at the synapse which may account for some or all of the decreases in sensor signal in this background. Additional controls to test if increased GluR density alone affects sensor readouts and/or independently modulating GluR levels in the glial KD background would help strengthen this data. In fact, glial-specific shv KD animals have baseline levels of GluR that are potentially high enough to have hit a ceiling of expression or detection that accounts for the inability for these levels to modulate any higher after strong stimulation and such a ceiling effect should be considered when interpreting the data and conclusions of this paper. Several outstanding questions remain-why can't glial derived Shv activate integrin pathways but exogenously applied recombinant Shv protein can? The effects of neuronal specific rescue of shv in a shv mutant are not provided vis-à-vis GluR levels and bouton size to compare to the glial only rescue. Inclusion of this data might provide more insight to outstanding questions of how and why the source of Shv seems to matter for some aspects of the phenotypes but not others despite the fact that exogenous Shv can rescue and in some experimental paradigms but not others.

Reviewer #3 (Public review):

Summary:

The manuscript by Chang and colleagues provides compelling evidence that glia-derived Shriveled (Shv) modulates activity-dependent synaptic plasticity at the Drosophila neuromuscular junction (NMJ). This mechanism differs from the previously reported function of neuronally released Shv, which activates integrin signaling. They further show that this requirement of Shv is acute and that glial Shv supports synaptic plasticity by modulating neuronal Shv release and the ambient glutamate levels. However, there are a number of conceptual and technical issues that need to be addressed.

Major comments

(1) From the images provided for Fig 2B +RU486, the bouton size appears to be bigger in shv RNAi + stimulation, especially judging from the outline of GluR clusters.<br /> (2) The shv result needs to be replicated with a separate RNAi.<br /> (3) The phenotype of shv mutant resembles that of neuronal shv RNAi - no increased GluR baseline. Any insights why that is the case?<br /> (4) In Fig 3B, SPG shv RNAi has elevated GluR baseline, while PG shv RNAi has a lower baseline. In both cases, there is no activity induced GluR increase. What could explain the different phenotypes?<br /> (5) In Fig 4C, the rescue of PTP is only partial. Does that suggest neuronal shv is also needed to fully rescue the deficit of PTP in shv mutants?<br /> (6) The observation in Fig 5D is interesting. While there is a reduction in Shv release from glia after stimulation, it is unclear what the mechanism could be. Is there a change in glial shv transcription, translation or the releasing machinery? It will be helpful to look at the full shv pool vs the released ones.<br /> (7) In Fig 5E, what will happen after stimulation? Will the elevated glial Shv after neuronal shv RNAi be retained in the glia?<br /> (8) It would be interesting to see if the localization of shv differs based on if it is released by neuron or glia, which might be able to explain the difference in GluR baseline. For example, by using glia-Gal4>UAS-shv-HA and neuronal-QF>QUAS-shv-FLAG. It seems important to determine if they mix together after release? It is unclear if the two shv pools are processed differently.<br /> (9) Alternatively, do neurons and glia express and release different Shv isoforms, which would bind different receptors?<br /> (10) It is claimed that Sup Fig 2 shows no observable change in gross glial morphology, further bolstering support that glial Shv does not activate integrin. This seems quite an overinterpretation. There is only one image for each condition without quantification. It is hard to judge if glia, which is labeled by GFP (presumably by UAS-eGFP?), is altered or not.<br /> (11) The hypothesis that glutamate regulates GluR level as a homeostatic mechanism makes sense. What is the explanation of the increased bouton size in the control after glutamate application in Fig 6?<br /> (12) What could be a mechanism that prevents elevated glial released Shv to activate integrin signaling after neuronal shv RNAi, as seen in Fig 5E?<br /> (13) Any speculation on how the released Shv pool is sensed?

Reviewer #1 (Public review):

Summary:

As TDP-43 mislocalization is a hallmark of multiple neurodegenerative diseases, the authors seek to identify pathways that modulate TDP-43 levels. To do this, they use a FACS based genome wide CRISPR KD screen in a Halo tagged TDP-43 KI iPSC line. Their screen identifies a number of genetic modulators of TDP-43 expression including BORC which plays a role in lysosome transport.

Strengths:

Genome wide CRISPR based screen identifies a number of modulators of TDP-43 expression to generate hypotheses regarding RNA BP regulation and perhaps insights into disease.

Weaknesses:

It is unclear how altering TDP-43 levels may relate to disease where TDP-43 is not altered in expression but mislocalized. This is a solid cell biology study, but the relation to disease is not clear without providing evidence of BORC alterations in disease or manipulation of BORC reversing TDP-43 pathology in disease.

The mechanisms by which BORC and lysosome transport modulate TDP-43 expression are unclear. Presumably, this may be through altered degradation of TDP protein but this is not addressed.

Previous studies have demonstrated that TDP-43 levels can be modulated by altering lysosomal degradation so the identification of lysosomal pathways is not particularly novel.

It is unclear whether this finding is specific to TDP-43 levels or whether lysosome localization may more broadly impact proteostasis in particular of other RNA BPs linked to disease.

Unclear whether BORC depletion alters lysosome function or simply localization.

Reviewer #2 (Public review):

Summary:

The authors employ a novel CRISPRi FACS screen and uncover the lysosomal transport complex BORC as a regulator of TDP-43 protein levels in iNeurons. They also find that BORC subunit knockouts impair lysosomal function, leading to slower protein turnover and implicating lysosomal activity in the regulation of TDP-43 levels. This is highly significant for the field given that a) other proteins could also be regulated in this way, b) understanding mechanisms that influence TDP-43 levels are significant given that its dysregulation is considered a major driver of several neurodegenerative diseases and c) the novelty of the proposed mechanism.

Strengths:

The novelty and information provided by the CRISPRi screen. The authors provide evidence indicating that BORC subunit knockouts impair lysosomal function, leading to slower protein turnover and implicating lysosomal activity in the regulation of TDP-43 levels and show a mechanistic link between lysosome mislocalization and TDP-43 dysregulation. The study highlights the importance of localized lysosome activity in axons and suggests that lysosomal dysfunction could drive TDP-43 pathologies associated with neurodegenerative diseases like FTD/ALS. Further, the methods and concepts will have an impact to the larger community as well. The work also sets up for further work to understand the somewhat paradoxical findings that even though the tagged TDP-43 protein is reduced in the screen, it does not alter cryptic exon splicing and there is a longer TDP-43 half-life with BORC KD.

Weaknesses:

While the data is very strong, the work requires some additional clarification.

Reviewer #3 (Public review):

Summary:

In this work, Ryan et al. have performed a state-of-the-art full genome CRISP-based screen of iNEurons expressing a teggd version of TDP-43 in order to determine expression modifiers of this protein. Unexpectedly, using this approach the authors have uncovered a previously undescribed role of the BORC complex in affecting the levels of TDP-43 protein, but not mRNA expression. Taken together, these findings represent a very solid piece of work that will certainly be important for the field.

Strengths:

- BORC is a novel TDP-43 expression modifier that has never been described before and it seemingly acts on regulating protein half life rather than transcriptome level. It has been long known that different labs have reported different half-lives for TDP-43 depending on the experimental system but no work has ever explained these discrepancies. Now, the work of Ryan et al. has for the time identified one of these factors which could account for these differences and play an important role in disease (although this is left to be determined in future studies).<br /> - The genome wide CRISPR screening has demonstrated to yield novel results with high reproducibility and could eventually be used to search for expression modifiers of many other proteins involved in neurodegeneration or other diseases

Weaknesses:

- The fact that TDP-43 mRNA does not change following BORCS6 KD is based on a single qRT-PCR that does not really cover all possibilities. For example, the mRNA total levels may not change but the polyA sites may have switched from the highly efficient pA1 to the less efficient and nuclear retained pA4. There are therefore a few other experiments that could have been performed to make this conclusion more compelling, maybe also performing RNAscope experiments to make sure that no change occurred in TDP-43 mRNA localisation in cells.<br /> - Even assuming that the mRNA does not change, no explanation for the change in TDP-43 protein half life has been proposed by the authors. This will presumably be addressed in future studies: for example, are mutants that lack different domains of TDP-43 equally affected in their half-lives by BORC KD?. Alternatively, can a mass-spec be attempted to see whether TDP-43 PTMs change following BORCS6 KD?

Reviewer #1 (Public review):

Summary of what is achieved: This manuscript validates and extends upon the sigh generating circuit between the NMB/GRP+ RTN/parafacial neurons and the NMBR/GRPR+ preBötC neurons established in Li et al., 2016. The authors generate multiple transgenic lines that enable selective targeting of these various sub-populations of cells and demonstrate the sufficiency of each type in generating a sigh breath. Additionally, they show that NMBR and GPRP preBötC neurons are glutamatergic, have overlapping and distinct expression, and do not express SST. Beyond this validation, the authors show that ectopic stimulation of SST neurons is sufficient to evoke sighs and that they are necessary for NMB/GRP induced sighing. This data is the first time that preBötC neurons downstream of NMBR/GRPR neurons have been identified that transform a eupneic breath into a sign breath. The five conclusions stated at the end of the introduction are supported by the data.

Summary of a primary weakness: A strong emphasis throughout the manuscript is the identification of an unsubstantiated slow sigh rhythm that is produced by NMBR/GRPR neurons. It is even suggested that this is an intrinsic property of these neurons. However, to make such a novel (and quite surprising) claim requires many more studies and the conclusion is dependent on how the authors have defined a sigh. Moreover, some data within the paper conflicts with this idea. The resubmitted manuscript does not contain any revisions and the rebuttal does not sufficiently address the critiques.

In summary, the optogenetic and chemogenetic characterization of the neuropeptide pathway transgenic lines nicely aligns with and provides important validation of the previous study by Li et. al., 2016 and the SST neuron studies provide a new mechanism for the transformation of NMBR/GRPR neuropeptide activation into a sigh. These are important findings, and they should be the points emphasized. The proposal of a slow sigh rhythm should be more rigorously established with new experiments and analysis or should be more carefully described and discussed.

Reviewer #2 (Public review):

Summary:

This study investigates in mice neural mechanisms generating sighs, which are periodic large-amplitude breaths occurring during normal breathing that subserve physiological pulmonary functions and are associated with emotional states such as relief, stress, and anxiety. Sighs are generated by a structure called the preBötzinger complex (preBötC) in the medulla oblongata that generates various forms of inspiratory activity including sighs. The authors have previously described a circuit involving neurons producing bombesin-related peptides Neuromedin B (NMB) and gastrin releasing peptide (GRP) that project to preBötC neurons expressing receptors for NMB (NMBRs) and GRP (GRPRs) and that activation of these preBötC neurons via these peptide receptors generates sighs. In this study the authors further investigated mechanisms of sigh generation by applying optogenetic and chemogenetic strategies to selectively activate the subpopulations of preBötC neurons expressing NMBRs and/or GRPRs, and a separate subpopulation of neurons expressing somatostatin (SST) but not NMBRs and GRPRs. The authors present convincing evidence that sigh-like inspirations can be evoked by photostimulation of the preBötC neurons expressing NMBRs or GRPRs. Photostimulation of SST neurons can independently evoke sighs, and chemogenetic inhibition of these neurons can abolish sighs. The results presented support the authors' conclusion that the preBötC neurons expressing NMBRs or GRPRs produce sighs via pathways to downstream SST neurons. Thus, these studies have identified some of the preBötC cellular elements likely involved in generating sighs.

Strengths:

(1) This study employs an effective combination of electrophysiological, transgenic, optogenetic, chemogenetic, pharmacological, and neuron activity imaging techniques to investigate sigh generation by distinct subpopulations of preBötC neurons in mice.

(2) The authors extend previous studies indicating that there is a peptidergic circuit consisting of NMB and GRP expressing neurons that project from the parafacial (pF) nucleus region to the preBötC and provides sufficient input to generate sighs, since photoactivation of either pF NMB or GRP neurons evoke ectopic sighs in this study.

(3) Solid evidence is presented that sighs can be evoked by direct photostimulation of preBötC neurons expressing NMBRs and/or GRPRs, and also a separate subpopulation of neurons expressing somatostatin (SST) but not NMBRs and GRPRs.

(4) The mRNA-expression data presented from in situ hybridization indicates that most preBötC neurons expressing NMBR, GRPR (or both) are glutamatergic and excitatory.

(5) Measurements in slices in vitro indicate that only the NMBR expressing neurons are normally rhythmically active during normal inspiratory activity and endogenous sigh activity.

(6) Evidence is presented that activation of preBötC NMBRs and/or GRPRs is not necessary for sigh production, suggesting that sighs are not the unique product of the preBötC bombesin-peptide signaling pathway.

(7) The novel conclusion is presented that the preBötC neurons expressing NMBRs and/or GRPRs produce sighs via the separate downstream population of preBötC SST neurons, which the authors demonstrate can independently generate sighs, whereas chemogenetic inhibition of preBötC SST neurons selectively abolishes sighs generated by activating NMBRs and GRPRs.

Weaknesses:

(1) While these studies have identified subpopulations of preBötC neurons capable of episodically evoking sigh-like inspiratory activity, mechanisms producing the normal slow sigh rhythm were not investigated and remain unknown.

(2) The authors have addressed some of the reviewers' main technical concerns and issues relating to interpretation of the results in their rebuttal letter, but have minimally revised the manuscript. Accordingly, there remain important technical and interpretation issues requiring resolution in the revised manuscript.

Comments on revisions:

The authors have clarified in their rebuttal letter the rationale for utilizing two different photostimulation paradigms but have not incorporated any of this explanation in Methods, which would be helpful for readers.

Reviewer #3 (Public review):

Summary:

This manuscript by Cui et al., studies the mechanisms for the generation of sighing, an essential breathing pattern. This is an important and interesting topic, as sighing maintains normal pulmonary function and is associated with various emotional conditions. However, the mechanisms of its generation remain not fully understood. The authors employed different approaches, including optogenetics, chemogenetics, intersectional genetic approach, and slice electrophysiology and calcium imaging, to address the question, and found several neuronal populations are sufficient to induce sighing when activated. Furthermore, ectopic sighs can be triggered without the involvement of neuromedin B (NMB) or gastrin releasing peptide (GRP) or their receptors in the preBötzinger Complex (preBötC) region of the brainstem. Additionally, activating SST neurons in the preBötC region induces sighing, even when other receptors are blocked. Based on these results, the authors concluded that increased excitability in certain neurons (NMBR or GRPR neurons) activates pathways leading to sigh generation, with SST neurons serving as a downstream component in converting regular breaths into sighs.

Strengths:

The authors employed a combination of various sophisticated approaches, including optogenetics, chemogenetics, intersectional genetic approach, and slice electrophysiology and calcium imaging, to precisely pinpoint the mechanism responsible for sigh generation. They utilized multiple genetically modified mouse lines, enabling them to selectively manipulate and observe specific neuronal populations involved in sighing.<br /> Using genetics and calcium imaging, the authors record the neuronal activity of NMBR and GRPR neurons, respectively, and identified their difference in activity pattern. Furthermore, by applying the intersectional approach, the authors were able to genetically target and manipulate several distinct neuronal populations, such as NMBR+, GRPR- neurons and GRPR+, NMBR- neurons, and conducted a detailed characterization of their functions in influencing sighing.

Weaknesses:

(1) The authors employed two conditions for optogenetic activation: long pulse photostimulation (LPP) and short pulse photostimulation (SPP), with durations ranging from 4-10s for LPP and 100-500 ms for SPP. These could generate huge variability in the experiments. The rationale behind the selection of these conditions in each experiment remains unclear in the manuscript. Additionally, it is not explained why these specific durations were chosen. Furthermore, the interpretation for the varied responses observed under these conditions is not provided. Clarification on the rationale and interpretation of these experimental parameters would enhance the understanding of the results. The description of the experiment conditions should be consistent throughout the manuscript.

(2) Regarding the fiber optics, my understanding is that they are placed outside of the brainstem from the ventral side. Given the locations of the pF and preBötC neurons, could the differences in responses be attributed to the varying distances of each population from the ventral surface? In fact, in Figure 8, NMBR is illustrated as being closer to the ventral surface. Does it represent the actual location of these neurons?

(3) The results of recording on NMBR neurons in Figure 4 were compelling. However, I'm curious why the recording of GRPR neurons and their response to the neuropeptide were not presented or examined. Additionally, considering the known cross-reaction between peptides and their receptors, it might be worthwhile to investigate how GRP modulates NMBR neurons and how NMB modulates GRPR neurons.

(4) The authors found that activation of several preBötC populations, including NMBR, GRPR, and SST neurons, despite pharmacological inhibition of NMBR and GRPR, can still induce sighing, and concluded that "activation of preBötC NMBRs and/or GRPRs is not necessary for sigh production". I disagree with this conclusion. Even when the receptors are silenced, artificial (optogenetic or chemogenetic) activation could still activate the same downstream pathways. This cannot be used as evidence to claim that the receptors are not required for sighing in vivo, because it is possible that the receptors are still necessary for the activation of these neurons under natural conditions. For instance, while diaphragm activation induces breathing, it does not negate the crucial role of the nervous system in regulating this process in physiological conditions.

(5) The authors noted varied responses upon activating specific subpopulations of the preBötC neurons, namely NMBR, GRPR, and SST neurons. Could these differences be attributed to variations in viral labeling efficiency among different mouse genetic lines? Are there discrepancies in the number of labeled neurons across the lines? Additionally, the authors did not thoroughly characterize the specificities of AAV targeting in their Cre and Flp lines. It's uncertain whether the AAV-labeled neurons are strictly restricted to the designated population without notable leakage into other populations. This is particularly crucial for the experiments manipulating SST neurons. If there's substantial labeling of NMBR or GRPR neurons, it could undermine the conclusions drawn. Further examination of the precision and selectivity of the labeling techniques is necessary to ensure the accurate interpretation of the experimental findings.

(6) The authors have addressed some of the reviewers' concerns in the revision; however, many important issues remain unaddressed.

Reviewer #1 (Public review):

Summary:

Dong et al here have studied the impact of the small Ras-like GTPase Rab10 on the exocytosis of dense core vesicles (DVC), which are important mediators of neuropeptide signaling in brain. They use optical imaging to show that lentiviral depletion of Rab10 in mouse hippocampal neurons in culture independent of the established defects in neurite outgrowth hamper DCV exocytosis. They further demonstrate that such defects are paralleled by changes in ER morphology and defective ER-based calcium buffering as well as reduced ribosomal protein expression in Rab10-depleted neurons. Re-expression of Rab10 or supplementation of exogenous L-leucine to restore defective neuronal protein synthesis rescues impaired DCV secretion. Based on these results they propose that Rab10 regulates DCV release by maintaining ER calcium homeostasis and neuronal protein synthesis.

Strengths:

This work provides interesting and potentially important new insights into the connection between ER function and the regulated secretion of neuropeptides via DCVs. The authors combine advanced optical imaging with light and electron microscopy, biochemistry and proteomics approaches to thoroughly assess the effects of Rab10 knockdown at the cellular level in primary neurons. The proteomic dataset provided may be valuable in facilitating future studies regarding Rab10 function. This work will thus be of interest to neuroscientists and cell biologists.

Weaknesses:

Whether and how the phenotypes of Rab10 reported in this study are linked remains an open question. Likewise, a possible role of Rab10 in exocytosis cannot be excluded at this stage.

Comments on revisions:

My previous questions and concerns have been satisfactorily addressed by the authors.

Reviewer #2 (Public review):

Summary:

In this paper, the authors assess the function of Rab10 in dense core vesicle (DCV) exocytosis using RNAi and cultured neurons. The author provides evidence that their knockdown (KD) is effective and provides evidence that DCV is compromised. They also perform proteomic analysis to identify potential pathway that are affected upon KD of Rab10 that may be involved in DCV release. Upon focusing on ER morphology and protein synthesis, the authors conclude that defects in protein synthesis and ER Ca2+ homeostasis contributes to the DVC release defect upon Rab10 KD.

Strengths:

The data related to Rab10's role in DCV release seems to be strong and carried out with rigor. While the paper lacks in vivo evidence that this gene is indeed involved in DCV in a living mammalian organism, I feel the cellular studies have value. The identification of ER defect in Rab10 manipulation is not truly novel but it is a good conformation of studies performed in other systems. The finding that DCV release defect and protein synthesis defect seen upon Rab10 KD can be significantly suppressed by Leucine supplementation is also a strength of this work.

Weaknesses:

The weaknesses mentioned in my previous comments have been addressed through the revision process.

Reviewer #3 (Public review):

In this study, Dong and colleagues set to dissect the role of Rab10 small GTPase on the intracellular trafficking and exocytosis of dense core vesicles (DCVs). While the authors have already shown that Rab3 plays a central role in the exocytosis of DVC in mammalian neurons, the roles of several other Rab-members have been identified genetically, but their precise mechanism of action in mammalian neurons remains unclear. In this study, the authors use a carefully designed and thoroughly executed series of experiments, including live-cell imaging, functional calcium-imaging, proteomics, and electron microscopy, to identify that DCV secretion upon Rab10 depletion in adult neurons is primarily a result of dysregulated protein synthesis and, to a lesser extent, disrupted intracellular calcium buffering. Given that the full deletion of Rab10 has deleterious effect on neurons and that Rab10 has a major role in axonal development, the authors cautiously employed the knock-down strategy from 7 DIV, to focus on the functional impact of Rab10 in mature neurons. The experiments in this study were meticulously conducted, incorporating essential controls and thoughtful considerations, ensuring rigorous and comprehensive results that fully support the conclusions.

Comments on revisions:

The authors have addressed all the comments and suggestions raised by reviewers, making this an excellent and timely study.

Reviewer #2 (Public review):

Summary.

Some forms of Artificial Intelligence (AI), particularly those based on artificial neural networks (ANNs), draw inspiration from biological brains and neurons. Understanding the functional repertoire and underlying logic of real neurons could, therefore, help improve ANNs. While the cell bodies and axons of neurons produce rapid, high-amplitude action potentials (~100 mV over ~2 ms), dendrites-constituting about 80% of neuronal membrane area-generate smaller but longer-lasting electrical signals, known as glutamate-mediated dendritic plateau potentials (~50 mV over >100 ms). The authors have designed artificial neurons capable of producing these dendritic plateau potentials and, through simulations, demonstrate that such prolonged dendritic signals reduce the negative effects of temporal jitter in real or artificial neural networks. Specifically, they show that in ANNs with neurons capable of dendritic plateau potentials, reliable sparse spiking computation can occur without the need for precise input synchronization. This means that despite fluctuations in network activity (such as delays in the brain circuit responses, for example), neurons can still link related network events. Thus, dendritic plateau potentials enable neurons to retain information longer, connecting events that are not exactly simultaneous. Interestingly, one of the indirect conclusions of the current study is that neurons equipped with dendritic plateau potentials may reduce the total number of cells (nodes, units) required to perform robust computations.

Strengths.

Most studies in neuroscience are descriptive, focusing on observations and measurements. Fewer tackle the more challenging task of explaining the rationale behind specific natural designs. This study does just that, addressing the fundamental problem of asynchrony in neural communication caused by conduction delays and noise. Given that neurons with short membrane time constants can integrate only nearly simultaneous inputs, the authors propose a solution: dendritic plateau potentials. These potentials, generated through glutamate-mediated depolarization within dendritic branches, effectively broaden the temporal integration window, allowing neurons to handle temporal jitter, variability, stochasticity, and maintain reliable computation. Thus, dendritic plateau potentials appear to be an adaptive feature evolved to support rapid, reliable CNS computations.

Weaknesses.

The authors have appropriately revised unsupported statements from previous versions, but the manuscript could benefit from examples of testable hypotheses derived from their findings. For example, what specific experimental questions could be investigated to validate these computational predictions? Providing concrete examples of potential experimental tests would make the work more accessible and actionable for experimentalists, assuming such experiments are feasible.

Additionally, many readers may lack a background in computational modeling or Artificial Neural Networks. To enhance accessibility, key terms and concepts should be explained at a level suitable for first-year graduate students, ensuring clarity for a broader audience.

Reviewer #2 (Public review):

This work aggregates data across 5 openly available stopping studies (3 at 7 tesla and 2 at 3 tesla) to evaluate activity patterns across the common contrasts of Failed Stop (FS) > Go, FS > stop success (SS), and SS > Go. Previous work has implicated a set of regions that tend to be positively active in one or more of these contrasts, including the bilateral inferior frontal gyrus, preSMA, and multiple basal ganglia structures. However, the authors argue that upon closer examination, many previous papers have not found subcortical structures to be more active on SS than FS trials, bringing into question whether they play an essential role in (successful) inhibition. In order to evaluate this with more data and power, the authors aggregate across five datasets and find many areas that are *more* active for FS than SS, including bilateral preSMA, GPE, thalamus, and VTA. They argue that this brings into question the role of these areas in inhibition, based upon the assumption that areas involved in inhibition should be more active on successful stop than failed stop trials, not the opposite as they observed.

Comments on revisions:

The authors have been responsive to the feedback of both reviewers and they have significantly improved the manuscript. I now judge the work as valuable and solid. The authors have achieved their aims to characterize subcortical BOLD activation in the stop-signal paradigm.

Reviewer #1 (Public review):

The authors set out to define the molecular basis for LP as the origin of BRCA1-deficient breast cancers. They showed that LPs have the highest level of replicative stress, and hypothesise that this may account for their tendency to transform. They went on to identify ELF3 as a candidate driver of LP transformation and showed that ELF3 expression is up-regulated in response to replicative stress as well as BRCA1 deficiency. They went on to show that ELF3 inactivation led to a higher level of DNA damage, which may result from compromised replicative stress responses.

While the manuscript supports the interesting idea wherein ELF3 may fuel LP cell transformation, it remains obscure how ELF3 promotes cell tolerance to DNA damage. Interestingly the authors proposed that ELF3 suppresses excessive genomic instability, but in my opinion, I do not see any evidence that supports this claim. In fact, one might think that genomic instability is key to cell transformation.

Comments on revisions:

The authors have addressed most of my concerns.

This being said, the one major criticism raised by both Reviewers is the lack of evidence to support ELF3 as a driver of transformation of and in LP cells. The authors appear to have invested much resource and time but were not successful in isolating LP cells for experimentations. I would therefore suggest that the authors tone down their claims throughout the manuscript.

Reviewer #1 (Public review):

Summary:

This study analyzed biomarker data from 28 subjects with geographic atrophy (GA) in a Phase I/II clinical trial of PPY988, a subretinal AAV2 complement factor I (CFI) gene therapy, to evaluate pharmacokinetics and pharmacodynamics. Post-treatment, a 2-fold increase in vitreous humor (VH) FI was observed, correlating with a reduction in FB breakdown product Ba but minimal changes in other complement factors. The aqueous humor (AH) was found to be an unreliable proxy for VH in assessing complement activation. In vitro assays showed that the increase in FI had a minor effect on the complement amplification loop compared to the more potent C3 inhibitor pegcetacoplan. These findings suggest that PPY988 may not provide enough FI protein to effectively modulate complement activation and slow GA progression, highlighting the need for thorough biomarker review to determine optimal dosing in future studies.

Strengths:

This manuscript provides critical data on the efficacy of gene therapy for the eye, specifically introducing complement FI expression. It presents the results from a halted clinical trial, making the publication of this data essential for understanding the outcomes of this gene therapy approach. The findings offer valuable insights and lessons for future gene therapy attempts in similar contexts.

Weaknesses:

No particular weaknesses. The study was carefully performed and limitations are discussed.

I have just some concerns about the methodology used. The authors use the MILLIPLEX assays, which allow for multiplexed detection of complement proteins and they mention extensive validation. How are the measurements with this assay correlating with gold standard methods? Is the specificity and the expected normal ranges preserved with this assay? This also stands for the Olink assay. Some of the proteins are measured by both assay and/or by standard ELISA. How do these measurements correlate?

Comments on revisions:

The authors answered part of my comments. Only one remained - please provide a comparison between ELISA/Multiplex and Olink data to judge the robustness of the Olinkl assay for complement.

Reviewer #2 (Public review):

Summary:

The results presented demonstrate AAV2-CFI gene therapy delivers long-term and marginally higher FI protein in vitreous humor that results in a concomitant reduction in the FB activation product Ba. However, the lack of clinical efficacy in the phase I/II study, possibly due to lower in vitro potency when compared to currently approved pegcetacoplan, raise important considerations for the utility of this therapeutic approach. Despite the early termination of the PPY988 clinical development program, the study achieved significant milestones, including the implementation of subretinal gene therapy delivery in older adults, complement biomarker comparison between serial vitreous humor and aqueous humor samples and vitreous humor proteomic assessment via Olink.

Strengths:

Long-term augmentation of FI protein in vitreous humor over 96-weeks and reduction of FB breakdown product Ba in vitreous humor suggests modulation of the complement system. Developed a novel in vitro assay suggesting FI's ability to reduce C3 convertase activity is weaker than pegcetacoplan and FH and may suggest a higher dose of FI will be required for clinical efficacy. Warn of the poor correlation between vitreous humor and aqueous humor biomarkers and suggest aqueous humor may not be a reliable proxy for vitreous humor with regard to complement activation/inhibition studies.

Weaknesses:

The vitrectomy required for subretinal route of administration causes long-term loss of total protein and may influence interpretation of complement biomarker results even with normalization. The modified in vitro assay of complement activation suggests a several hundred-fold increase in FI protein is required to significantly affect C3a levels. Interestingly, the in vitro assay demonstrates 100% inhibition of C3a with pegcetacoplan and FH therapeutics, but only a 50% reduction with FI even at the highest concentrations tested. This observation suggests FI may not be rate-limiting for negative complement regulation under the in vitro conditions tested and potentially in the eye. It is unclear if pharmacokinetic and pharmacodynamic properties in aqueous humor and vitreous humor compartments are a reliable predictor of FI level/activity after subretinal delivery AAV2-CFI gene therapy.

Reviewer #3 (Public review):

Summary:

The manuscript by Hallam et al describes the analysis of various biomarkers in patients undergoing complement factor I supplementation treatment (PPY988 gene therapy) as part of the FOCUS Phase I/II clinical trial. The authors used validated methods (multiplexed assays and OLINK proteomics) for measuring multiple soluble complement proteins in the aqueous humour (AH) and vitreous humour (VH) of 28 patients over a series of timepoints, up to and including 96 weeks. Based on biomarker comparisons, the levels of FI synthesised by PPY988 were believed to be insufficient to achieve the desired level of complement inhibition. Subsequent comparative experiments showed that PPY988-delievred FI was much less efficacious than Pegceptacoplan (FDA approved complement inhibitor under the name SYFORVE) when tested in an artificial VH matrix.

Strengths:

The manuscript is well written with data clearly presented and appropriate statistics used for the analysis itself. It's great to see data from real clinical samples that can help support future studies and therapeutic design. The identification that complement biomarker levels present in the AH do not represent the levels found in the VH is an important finding for the field, given the number of complement-targeting therapies in development and the desperate need for good biomarkers for target engagement. This study also provides a wealth of baseline complement protein measurements in both human AH and VH (and companion measurements in plasma) that will prove useful for future studies.

Weaknesses:

No real weaknesses in the manuscript itself. It is only a shame that it would appear that FI supplementation is not a viable way forward for treating GA secondary to AMD.

Comments on revisions:

I think the authors have done all that they can to present this study in the most robust manner possible.

Reviewer #1 (Public review):

Summary:

Chlamydia spp. has a biphasic developmental cycle consisting of an extracellular, infectious form called an elementary body (EB) and an intracellular, replicative form known as a reticular body (RB). The structural stability of EBs is maintained by extensive cross linking of outer membrane proteins while the outer membrane proteins of RBs are in a reduced state. The overall redox state of EBs is more oxidized than RBs. The authors propose that redox state may be a controlling factor in the developmental cycle. To test this, alkyl hydroperoxide reductase subunit C (ahpC) was overexpressed or knocked down to examine effects on developmental gene expression. KD of ahpC induced increased expression of EB-specific genes and accelerated EB production. Conversely, overexpression of phpC delayed differentiation to EBs. The results suggest that chlamydial redox state may play a role in differentiation.

Strengths:

Uses modern genetic tools to explore the difficult area of temporal gene expression throughout the chlamydial developmental cycle.

Weaknesses:

The environmental signals triggering ahpC expression/activity are not determined.

Comments on revisions:

I am satisfied with the modifications made to the manuscript.

Reviewer #2 (Public review):

The factors that influence the differentiation of EBs and RBs during Chlamydial development are not clearly understood. A previous study had shown a redox oscillation during the Chlamydial developmental cycle. Based on this observation, the authors hypothesize that the bacterial redox state may play a role in regulating the differentiation in Chlamydia. To test their hypothesis, they make knock-down and overexpression strains of the major ROS regulator, ahpC. They show that the knock-down of ahpC leads to a significant increase in ROS levels leading to an increase in the production of elementary bodies and overexpression leads to a decrease in EB production likely caused by a decrease in oxidation. From their observations, they present an interesting model wherein an increase in oxidation favors the production of EBs.

Comments on revisions:

Major concerns have been satisfactorily addressed.

Reviewer #2 (Public review):

Summary:

In this manuscript the authors evaluate the attenuation, immunogenicity, and protection efficacy of a live-attenuated SARS-CoV-2 vaccine candidate (BK2102) against SARS-CoV-2.

Strengths:

The authors demonstrate that intranasal inoculation of BK2102 is safe and able to induce humoral and cellular immune responses in hamsters, without apparent signs of damage in the lungs, that protects against homologous SARS-CoV-2 and Omicron BA.5 challenge. Safety of BK2102 was further confirmed in a new hACE2 transgenic mouse model generated by the authors.

Weaknesses:

The authors have addressed my previous comments on the first submission of the document.

Reviewer #3 (Public review):

Summary:

Suzuki-Okutani and collogues reported a new live-attenuated SARS-CoV-2 vaccine (BK2102) containing multiple deletion/substitution mutations. They show that the vaccine candidate is highly attenuated and demonstrates great safety profile in multiple animal models (hamsters and Tg-Mice). Of importance, their data show that singe intranasal immunization with BK2102 leads to strong protection of hamsters against D614G and BA.5 challenge in both lungs and URT (nasal wash). Both humoral and cellular responses were induced, and neutralization activity remained for >360 after single inoculation.

Strengths:

The manuscript describes a comprehensive study that evaluates safety, immunogenicity, and efficacy of a new live-attenuated vaccine. Strengths of the study include: 1) strong protection against immune evasive variant BA.5 in both lungs and NW; 2) durability of immunity for >360 days; 3) confirmation of URT protection through a transmission experiment.<br /> While first-generation COVID-19 vaccines have achieved much success, new vaccines that provide mucosal and durable protection remain needed. Thus, the study is significant.

Weaknesses:

Lack of a more detailed discussion of this new vaccine approach in the context of reported live-attenuated SARS-CoV-2 vaccines in terms of its advantages and/or weakness<br /> Antibody endpoint titers could be presented.<br /> Lack of elaboration on immune mechanisms of protection at the upper respiratory tract (URT) against an immune evasive variant in the absence of detectable neutralizing antibodies

Comments on revisions:

In the revised submission, the authors have added new data and have modified the manuscript accordingly. They have reasonably addressed my comments raised in the previous round of review. The quality and clarity of the manuscript are improved.

Reviewer #1 (Public Review):

Summary:

The present study's main aim is to investigate the mechanism of how VirR controls the magnitude of MEV release in Mtb. The authors used various techniques, including genetics, transcriptomics, proteomics, and ultrastructural and biochemical methods. Several observations were made to link VirR-mediated vesiculogenesis with PG metabolism, lipid metabolism, and cell wall permeability. Finally, the authors presented evidence of a direct physical interaction of VirR with the LCP proteins involved in linking PG with AG, providing clues that VirR might act as a scaffold for LCP proteins and remodel the cell wall of Mtb. Since the Mtb cell wall provides a formidable anatomical barrier for the entry of antibiotics, targeting VirR might weaken the permeability of the pathogen along with the stimulation of the immune system due to enhanced vesiculogenesis. Therefore, VirR could be an excellent drug target. Overall, the study is an essential area of TB biology.

Strengths:

The authors have done a commendable job of comprehensively examining the phenotypes associated with the VirR mutant using various techniques. Application of Cryo-EM technology confirmed increased thickness and altered arrangement of CM-L1 layer. The authors also confirmed that increased vesicle release in the mutant was not due to cell lysis, which contrasts with studies in other bacterial species.

Another strength of the manuscript is that biochemical experiments show altered permeability and PG turnover in the mutant, which fits with later experiments where authors provide evidence of a direct physical interaction of VirR with LCP proteins.

Transcriptomics and proteomics data were helpful in making connections with lipid metabolism, which the authors confirmed by analyzing the lipids and metabolites of the mutant.

Lastly, using three approaches, the authors confirm that VirR interacts with LCP proteins in Mtb via the LytR_C terminal domain.

Altogether, the work is comprehensive, experiments are designed well, and conclusions were made based on the data generated after verification using multiple complementary approaches.

Weaknesses:

The major weakness is that the mechanism of VirR-mediated EV release remains enigmatic. Most of the findings are observational and only associate enhanced vesiculogenesis observed in the VirR mutant with cell wall permeability and PG metabolism. Authors suggest that EV release occurs during cell division when PG is most fragile. However, this has yet to be tested in the manuscript-the AFM of the VirR mutant, which produces thicker PG with more pore density, displays enhanced vesiculogenesis. No evidence was presented to show that the PG of the mutant is fragile, and there are differences in cell division to explain increased vesiculogenesis. These observations, counterintuitive to the authors' hypothesis, need detailed experimental verification.

Transcriptomic data only adds a little substantial. Transcriptomic data do not correlate with the proteomics data. It remains unclear how VirR deregulates transcription. TLCs of lipids are not quantitative. For example, the TLC image of PDIM is poor; quantitative estimation needs metabolic labeling of lipids with radioactive precursors. Further, change in PDIMs is likely to affect other lipids (SL-1, PAT/DAT) that share a common precursor (propionyl- CoA).

The connection of cholesterol with cell wall permeability is tenuous. Cholesterol will serve as a carbon source and contribute to the biosynthesis of methyl-branched lipids such as PDIM, SL-1, and PAD/DAT. Carbon sources also affect other aspects of physiology (redox, respiration, ATP), which can directly affect permeability and import/export of drugs. Authors should investigate whether restoration of the normal level of permeability and EV release is not due to the maintenance of cell wall lipid balance upon cholesterol exposure of the VirR mutant.

Finally, protein interaction data is based on experiments done once without statistical analysis. If the interaction between VirR and LCP protein is expected on the mycobacterial membrane, how SPLIT_GFP system expressed in the cytoplasm is physiologically relevant. No explanation was provided as to why VirR interacts with the truncated version of LCP proteins and not with the full-length proteins.

Comments on revisions:

The authors have addressed my comments. I have no further issues.

Reviewer #2 (Public Review):

Summary:

In this work, Vivian Salgueiro et al. have comprehensively investigated the role of VirR in the vesicle production process in Mtb using state-of-the-art omics, imaging, and several biochemical assays. From the present study, authors have drawn a positive correlation between cell membrane permeability and vasculogenesis and implicated VirR in affecting membrane permeability, thereby impacting vasculogenesis.

Strengths:

The authors have discovered a critical factor (i.e. membrane permeability) that affects vesicle production and release in Mycobacteria, which can broadly be applied to other bacteria and may be of significant interest to other scientists in the field. Through omics and multiple targeted assays such as targeted metabolomics, PG isolation, analysis of Diaminopimelic acid and glycosyl composition of the cell wall, and, importantly, molecular interactions with PG-AG ligating canonical LCP proteins, the authors have established that VirR is a central scaffold at the cell envelope remodelling process which is critical for MEV production.

Comments on the revision.

Authors have addressed the concerns, specifically regarding the expression of downstream genes. It appears that they are not altered significantly.

Data in Fig 6C shows significantly higher expresssion of VirR compared to control or knock down. In the absence of using a regulatable expression such as nitrile, this is expected from a constitutive promoter.

I have no further questions for the author.

Reviewer #1 (Public review):

Summary:

In this preprint, the authors systematically and rigorously investigate how specific classes of residue mutations alter the critical temperature as a proxy for the driving forces for phase separation. The work is well executed, the manuscript well-written, and the results reasonable and insightful.

Strengths:

The introductory material does an excellent job of being precise in language and ideas while summarizing the state of the art. The simulation design, execution, and analysis are exceptional and set the standard for large-scale simulation studies. The results, interpretations, and Discussion are largely nuanced, clear, and well-motivated, and the pedagogical nature with which sampling convergence is discussed is greatly appreciated. Finally, the underlying data are shared in a clear and accessible manner. Overall, the manuscript is a model

Weaknesses:

The simplicity of a one-bead-per-residue model parameterized to capture UCST-type phase behavior does perhaps impact some aspects of the generality of this work. That said, the authors carefully acknowledge these limitations, and overall, this is not seen as a major weakness of the conclusions drawn or the manuscript, given those conclusions are appropriately couched.

Reviewer #2 (Public review):

This is an interesting manuscript where a CA-only CG model (Mpipi) was used to examine the critical temperature (Tc) of phase separation of a set of 140 variants of prion-like low complexity domains (PLDs). The key result is that Tc of these PLDs seems to have a linear dependence on substitutions of various sticker and space residues. This is potentially useful for estimating the Tc shift when making novel mutations of a PLD.

Comments on revisions: The authors have addressed concerns raised previously.

Reviewer #3 (Public review):

Summary:

"Decoding Phase Separation of Prion-Like Domains through Data-Driven Scaling Laws" by Maristany et al. offers a significant contribution to the understanding of phase separation in prion-like domains (PLDs). The study investigates the phase separation behavior of PLDs, which are intrinsically disordered regions within proteins that have the propensity to undergo liquid-liquid phase separation (LLPS). This phenomenon is crucial in forming biomolecular condensates, which play essential roles in cellular organization and function. The authors employ a data-driven approach to establish predictive scaling laws that describe the phase behavior of these domains.

Strengths:

The study benefits from a robust dataset encompassing a wide range of PLDs, which enhances the generalizability of the findings. The authors' meticulous curation and analysis of this data add to the study's robustness. The scaling laws derived from the data provide predictive insights into the phase behavior of PLDs, which can be useful in the future for the design of synthetic biomolecular condensates.

Joint Public Review:

This manuscript by Tao et al. reports on an effort to better specify the underlying interactions driving the effects of biodiversity on productivity in biodiversity experiments. The authors are especially concerned with the potential for competitive interactions to drive positive biodiversity-ecosystem functioning relationships by driving down the biomass of subdominant species. The authors suggest a new partitioning schema that utilizes a suite of partial density treatments to capture so-called competitive ability.

Readers are encouraged to consider the original reviews in full, which outline the strengths and weaknesses of the work:

First version: https://elifesciences.org/reviewed-preprints/98073v1/reviews

Second version: https://elifesciences.org/reviewed-preprints/98073v2/reviews

There are no further reviews for this version because the authors declined to make further improvements to their manuscript.

Reviewer #1 (Public review):

Summary

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

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

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

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

Strengths of study

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

Limitations

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

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

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

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

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

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

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

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

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

The updated document has addressed this caveat.

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

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

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

This caveat has been addressed in the revised manuscript.

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

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

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

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

Comments on the latest version:

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

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

Conclusions:

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

Reviewer #3 (Public review):

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

First of all, I would like to disclose that I am not an expert in congenital visual deprivation, nor in MRS. My expertise is in EEG (particularly in the decomposition of periodic and aperiodic activity) and statistical methods. Although the authors addressed some of the concerns of the previous version, major concerns and flaws remain in terms of methodological and statistical approaches along with the (over)interpretation of the results. Specific concerns include:

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

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

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

Several points require clarification or improvement:<br /> (4) Correlation Methods: The manuscript does not specify whether the reported correlation analyses are based on Pearson or Spearman correlation.<br /> (5) Confidence Intervals: Include confidence intervals for correlations to represent the uncertainty associated with these estimates.<br /> (6) Permutation Statistics: Given the small sample size, I recommend using permutation statistics, as these are exact tests and more appropriate for small datasets.<br /> (7) Adjusted P-Values: Ensure that reported Bonferroni corrected p-values (e.g., p > 0.999) are clearly labeled as adjusted p-values where applicable.<br /> (8) Figure 2C<br /> Figure 2C still lacks crucial information that the correlation between Glx/GABA ratio and visual acuity was computed solely in the control group (as described in the rebuttal letter). Why was this analysis restricted to the control group? Please provide a rationale.<br /> (9 3.4) Interpretation of Aperiodic Signal<br /> Relying on previous studies to interpret the aperiodic slope as a proxy for excitation/inhibition (E/I) does not make the interpretation more robust.<br /> (10) Additionally, the authors state:<br /> "We cannot think of how any of the exploratory correlations between neurophysiological measures and MRS measures could be accounted for by a difference e.g. in skull thickness."<br /> (11) This could be addressed directly by including skull thickness as a covariate or visualizing it in scatterplots, for instance, by representing skull thickness as the size of the dots.<br /> (12 3.5) Problems with EEG Preprocessing and Analysis<br /> Downsampling: The decision to downsample the data to 60 Hz "to match the stimulation rate" is problematic. This choice conflates subsequent spectral analyses due to aliasing issues, as explained by the Nyquist theorem. While the authors cite prior studies (Schwenk et al., 2020; VanRullen & MacDonald, 2012) to justify this decision, these studies focused on alpha (8-12 Hz), where aliasing is less of a concern compared of analyzing aperiodic signal. Furthermore, in contrast, the current study analyzes the frequency range from 1-20 Hz, which is too narrow for interpreting the aperiodic signal as E/I. Typically, this analysis should include higher frequencies, spanning at least 1-30 Hz or even 1-45 Hz (not 20-40 Hz).<br /> (13) Baseline Removal: Subtracting the mean activity across an epoch as a baseline removal step is inappropriate for resting-state EEG data. This preprocessing step undermines the validity of the analysis. The EEG dataset has fundamental flaws, many of which were pointed out in the previous review round but remain unaddressed. In its current form, the manuscript falls short of standards for robust EEG analysis. If I were reviewing for another journal, I would recommend rejection based on these flaws.<br /> (14) The authors mention:<br /> "The EEG data sets reported here were part of data published earlier (Ossandón et al., 2023; Pant et al., 2023)." Thus, the statement "The group differences for the EEG assessments corresponded to those of a larger sample of CC individuals (n=38) " is a circular argument and should be avoided."<br /> The authors addressed this comment and adjusted the statement. However, I do not understand, why not the full sample published earlier (Ossandón et al., 2023) was used in the current study?

Reviewer #1 (Public review):

Contractile Injection Systems (CIS) are versatile machines that can form pores in membranes or deliver effectors. They can act extra or intracellularly. When intracellular they are positioned to face the exterior of the cell and hence should be anchored to the cell envelope. The authors previously reported the characterization of a CIS in Streptomyces coelicolor, including significant information on the architecture of the apparatus. However, how the tubular structure is attached to the envelope was not investigated. Here they provide a wealth of evidence to demonstrate that a specific gene within the CIS gene cluster, cisA, encodes a membrane protein that anchors the CIS to the envelope. More specifically, they show that:

- CisA is not required for assembly of the structure but is important for proper contraction and CIS-mediated cell death<br /> - CisA is associated to the membrane (fluorescence microscopy, cell fractionation) through a transmembrane segment (lacZ-phoA topology fusions in E. coli)<br /> - Structural prediction of interaction between CisA and a CIS baseplate component<br /> - In addition they provide a high-resolution model structure of the >750-polypeptide Streptomyces CIS in its extended conformation, revealing new details of this fascinating machine, notably in the baseplate and cap complexes.

All the experiments are well controlled including trans-complemented of all tested phenotypes.

One important information we miss is the oligomeric state of CisA.

While it would have been great to test the interaction between CisA and Cis11, to perform cryo-electron microscopy assays of detergent-extracted CIS structures to maintain the interaction with CisA, I believe that the toxicity of CisA upon overexpression or upon expression in E. coli render these studies difficult and will require a significant amount of time and optimization to be performed. It is worth mentioning that this study is of significant novelty in the CIS field because, except for Type VI secretion systems, very few membrane proteins or complexes responsible for CIS attachment have been identified and studied.

Reviewer #2 (Public review):

Summary:

The overall question that is addressed in this study is how the S. coelicolor contractile injection system (CISSc) works and affects both cell viability and differentiation, which it has been implicated to do in previous work from this group and others. The CISSc system has been enigmatic in the sense that it is free-floating in the cytoplasm in an extended form and is seen in contracted conformation (i.e. after having been triggered) mainly in dead and partially lysed cells, suggesting involvement in some kind of regulated cell death. So, how do the structure and function of the CISSc system compare to those of related CIS from other bacteria, does it interact with the cytoplasmic membrane, how does it do that, and is the membrane interaction involved in the suggested role in stress-induced, regulated cell death? The authors address these questions by investigating the role of a membrane protein, CisA, that is encoded by a gene in the CIS gene cluster in S. coelicolor. Further, they analyse the structure of the assembled CISSc, purified from the cytoplasm of S. coelicolor, using single-particle cryo-electron microscopy.

Strengths:

The beautiful visualisation of the CIS system both by cryo-electron tomography of intact bacterial cells and by single-particle electron microscopy of purified CIS assemblies are clearly the strengths of the paper, both in terms of methods and results. Further, the paper provides genetic evidence that the membrane protein CisA is required for the contraction of the CISSc assemblies that are seen in partially lysed or ghost cells of the wild type. The conclusion that CisA is a transmembrane protein and the inferred membrane topology are well supported by experimental data. The cryo-EM data suggest that CisA is not a stable part of the extended form of the CISSc assemblies. These findings raise the question of what CisA does.

Weaknesses:

The investigations of the role of CisA in function, membrane interaction, and triggering of contraction of CIS assemblies, are important parts of the paper and are highlighted in the title. However, the experimental data provided to answer these questions appear partially incomplete and not as conclusive as one would expect.

The stress-induced loss of viability is only monitored with one method: an in vivo assay where cytoplasmic sfGFP signal is compared to FM5-95 membrane stain. Addition of a sublethal level of nisin lead to loss of sfGFP signal in individual hyphae in the WT, but not in the cisA mutant (similarly to what was previously reported for a CIS-negative mutant). Technically, this experiment and the example images that are shown give rise to some concern. Only individual hyphal fragments are shown that do not look like healthy and growing S. coelicolor hyphae. Under the stated growth conditions, S. coelicolor strains would normally have grown as dense hyphal pellets. It is therefore surprising that only these unbranched hyphal fragments are shown in Fig. 4ab. Further, S. coelicolor would likely be in a stationary phase when grown 48 h in the rich medium that is stated, giving rise to concern about the physiological state of the hyphae that were used for the viability assay. It would be valuable to know whether actively growing mycelium is affected in the same way by the nisin treatment, and also whether the cell death effect could be detected by other methods.

The model presented in Fig. 5 suggests that stress leads to a CisA-dependent attachment of CIS assemblies to the cytoplasmic membrane, and then triggering of contraction, leading to cell death. This model makes testable predictions that have not been challenged experimentally. Given that sublethal doses of nisin seem to trigger cell death, there appear to be possibilities to monitor whether activation of the system (via CisA?) indeed leads to at least temporally increased interaction of CIS with the membrane. Further, would not the model predict that stress leads to an increased number of contracted CIS assemblies in the cytoplasm? No clear difference in length of the isolated assemblies if Fig. S7 is seen between untreated and nisin-exposed cells, and also no difference between assemblies from WT and cisA mutant hyphae.

The interaction of CisA with the CIS assembly is critical for the model but is only supported by Alphafold modelling, predicting interaction between cytoplasmic parts of CisA and Cis11 protein in the baseplate wedge. An experimental demonstration of this interaction would have strengthened the conclusions.

The cisA mutant showed a similarly accelerated sporulation as was previously reported for CIS-negative strains, which supports the conclusion that CisA is required for function of CISSc. But the results do not add any new insights into how CIS/CisA affects the progression of the developmental life cycle and whether this effect has anything to do with the regulated cell death that is caused by CIS. The same applies to the effect on secondary metabolite production, with no further mechanistic insights added, except reporting similar effects of CIS and CisA inactivations.

Concluding remarks:<br /> The work will be of interest to anyone interested in contractile injection systems, T6SS, or similar machineries, as well for people working on the biology of streptomycetes. There is also a potential impact of the work in the understanding of how such molecular machineries could have been co-opted during evolution to become a mechanism for regulated cell death. However, this latter aspect remains still poorly understood. Even though this paper adds excellent new structural insights and identifies a putative membrane anchor, it remains elusive how the Streptomyces CIS may lead to cell death. It is also unclear what the advantage would be to trigger death of hyphal compartments in response to stress, as well as how such cell death may impact (or accelerate) the developmental progression. Finally, it is inescapable to wonder whether the Streptomyces CIS could have any role in protection against phage infection.

Reviewer #3 (Public review):

Summary:

In this work, Casu et al. have reported the characterization of a previously uncharacterized membrane protein CisA encoded in a non-canonical contractile injection system of Streptomyces coelicolor, CISSc, which is a cytosolic CISs significantly distinct from both intracellular membrane-anchored T6SSs and extracellular CISs. The authors have presented the first high-resolution structure of extended CISSc structure. It revealed important structural insights in this conformational state. To further explore how CISSc interacted with cytoplasmic membrane, they further set out to investigate CisA that was previously hypothesized to be the membrane adaptor. However, the structure revealed that it was not associated with CISSc. Using fluorescence microscope and cell fractionation assay, the authors verified that CisA is indeed a membrane-associated protein. They further determined experimentally that CisA had a cytosolic N-terminal domain and a periplasmic C-terminus. The functional analysis of cisA mutant revealed that it is not required for CISSc assembly but is essential for the contraction, as a result, the deletion significantly affects CISSc-mediated cell death upon stress, timely differentiation, as well as secondary metabolite production. Although the work did not resolve the mechanistic detail how CisA interacts with CISSc structure, it provides solid data and a strong foundation for future investigation toward understanding the mechanism of CISSc contraction, and potentially, the relation between the membrane association of CISSc, the sheath contraction and the cell death.

Strengths:

The paper is well-structured, and the conclusion of the study is supported by solid data and careful data interpretation was presented. The authors provided strong evidence on (1) the high-resolution structure of extended CISSc determined by cryo-EM, and the subsequent comparison with known eCIS structures, which sheds light on both its similarity and different features from other subtypes of eCISs in detail; (2) the topological features of CisA using fluorescence microscopic analysis, cell fractionation and PhoA-LacZα reporter assays, (3) functions of CisA in CISSc-mediated cell death and secondary metabolite production, likely via the regulation of sheath contraction.

Weaknesses:

The data presented are not sufficient to provide mechanistic details of CisA-mediated CISSc contraction, as authors are not able to experimentally demonstrate the direct interaction between CisA with baseplate complex of CISSc (hypothesized to be via Cis11 by structural modeling), since they could not express cisA in E. coli due to its potential toxicity. Therefore, there is a lack of biochemical analysis of direct interaction between CisA and baseplate wedge. In addition, there is no direct evidence showing that CisA is responsible for tethering CISSc to the membrane upon stress, and the spatial and temporal relation between membrane association and contraction remains unclear. Further investigation will be needed to address these questions in future.

Discussion:

Overall, the work provides a valuable contribution to our understanding on the structure of a much less understood subtype of CISs, which is unique compared to both membrane-anchored T6SSs and host-membrane targeting eCISs. Importantly, the work serves as a good foundation to further investigate how the sheath contraction works here. The work contributes to expanding our understanding of the diverse CIS superfamilies.

Reviewer #1 (Public review):

Summary:

Carter et al. present the eduWOSM imaging platform, a promising development in open-source microscopy for educational purposes. The paper outlines the construction and setup of this versatile microscope, demonstrating its capabilities through three key examples: single fluorophore tracking of tubulin heterodimers in gliding microtubules, 4D deconvolution imaging and tracking of chromosome movements in dividing human cells, and automated single-particle tracking in vitro and in live cells, with motion classified into sub-diffusive, diffusive, and super-diffusive behaviors.

The paper is well-written and could be strengthened by providing more empirical data on its performance, addressing potential limitations, and offering detailed insights into its educational impact. The project holds great potential and more discussion on long-term support and broader applications would provide a more comprehensive view of its relevance in different contexts.

Strengths:

(1) The eduWOSM addresses a crucial need in education, providing research-quality imaging at a lower cost (<$10k). The fact that it is open-source adds significant value, enabling broad accessibility even in under resourced areas.<br /> (2) There is availability of extensive resources, including a dedicated website, YouTube channel, and comprehensive tutorial guides to help users replicate the microscope.<br /> (3) The compact, portable, and stable design makes it easy to build multiple systems for use in diverse environments, including crowded labs and classrooms. This is further enhanced by the fact multiple kind of imaging experiments can be run on the system, from live imaging to super-resolution imaging.<br /> (4) The paper highlights the user-friendly nature of the platform, with the imaging examples in the paper being acquired by undergrad students.

Weaknesses:

(1) The paper mentions the microscope is suitable not just for education but even for research purposes. This claim needs validation through quantitative comparison to existing research-grade microscopes in terms of resolution, signal-to-noise ratio, and other key metrics. Adding more rigorous comparisons would solidify its credibility for research use, which would immensely increase the potential of the microscope.<br /> (2) The open-source microscope field is crowded with various options catering to hobby, educational, and research purposes (e.g., openFLexure, Flamingo, Octopi, etc.). The paper would benefit from discussing whether any aspects set the eduWOSM platform apart or fulfill specific roles that other microscopes do not.<br /> (3) While the eduWOSM platform is designed to be user-friendly, the paper would benefit from discussing whether the microscope can be successfully built and operated by users without direct help from the authors. It's important to know if someone with basic technical knowledge, relying solely on the provided resources (website, YouTube tutorials, and documentation), can independently assemble, calibrate, and operate the eduWOSM.<br /> (4) Ensuring long-term support and maintenance of the platform is crucial. The paper would benefit from addressing how the eduWOSM developers plan to support updates, improvements, or troubleshooting.

Reviewer #2 (Public review):

The main strength of this work is the impressive performance of a microscope assembled for a fraction of the cost of a commercial, turnkey system. The authors have created a very clever design that removes everything that is not essential. They show compelling time-lapse data looking at single molecules, tracking particles visible in brightfield mode, and looking at cell division with multiple labels in a live cell preparation.

The weaknesses of the paper include:<br /> (1) the lack of more comprehensive explanations of the microscope and what it takes to build and operate it.<br /> For example, the dimensions of the microscope, how samples are mounted, which lenses are compatible, and whether eduWOSMs have been built by groups other than the authors would be useful information.<br /> (2) the absence of more detailed descriptions of some of the experiments, such as frame rates and Z-stack information.<br /> (3) the lack of standardized measures of performance.<br /> For example, images of subresolution tetraspeck beads and measurements of PSF would provide estimates on resolution in XY, resolution in Z, axial chromatic aberrations and lateral chromatic aberrations. Repeating these measurements on different eduWOSMs will provide an idea of how reliably the performance can be achieved.<br /> If these issues were addressed, it would make it more likely that other groups could build and operate this system successfully.

Overall, the authors have designed and built an impressive system at low cost. Providing a bit more information in the manuscript would make it much more likely that other laboratories could replicate this design in their own environments.

Reviewer #1 (Public review):

Summary:

The authors show that early life experience of juvenile bats shape their outdoor foraging behaviors. They achieve this by raising juvenile bats either in an impoverished or enriched environment. They subsequently test the behavior of bats indoors and outdoors. The authors show that behavioral measures outdoors were more reliable in delineating the effect of early life experiences as the bats raised in enriched environments were more bold, active and exhibit higher exploratory tendencies.

Strengths:

The major strength of the study is providing a quantitative study of animal "personality" and how it is likely shaped by innate and environmental conditions. The other major strength is the ability to do reliable long term recording of bats in the outdoors giving researchers the opportunity to study bats in their natural habitat. To this point, the study also shows that the behavioral variables measured indoors do not correlate to that measured outdoors, thus providing a key insight into the importance of testing animal behaviors in their natural habitat.

Weaknesses:

It is not clear from the analysis presented in the paper how persistent those environmentally induced changes, do they remain with the bats till the end of their lives.

Reviewer #2 (Public review):

Summary:

The authors present a paper that attempts to tackle an important question, with potential impact far beyond the field of animal behavior research: what are the relative contributions of innate personality traits versus early life experience on individual behavior in the wild? The study, performed on Egyptian fruit bats that are caught in the wild and later housed in an outdoor colony, is solidly executed, and benefits greatly from a unique setup in which controlled laboratory experiments are combined with monitoring of individuals as they undertake undirected, free exploration of their natural environment.

The primary finding of the paper is that there is a strong effect of early life experience on behavior in the wild, where individual bats that were exposed to an enriched environment as juveniles later travelled farther and over greater distances when permitted to explore and forage ad libitum, as compared with individual bats who were subjected to a more impoverished environment. Meanwhile, no prominent effect of innate "personality", as assessed by indices of indoor foraging behavior early on, before the bats were exposed to the controlled environmental treatment, was observed on three metrics of outdoor foraging behavior. The authors conclude that the early environment plays a larger role than innate personality on the behavior of adult bats.

Strengths:

(1) Elegant design of experiments and impressive combination of methods<br /> Bats used in the experiment were taken from wild colonies in different geographical areas, but housed during the juvenile stage in a controlled indoor environment. Bats are tested on the same behavioral paradigm at multiple points in their development. Finally, the bats are monitored with GPS as they freely explore the area beyond the outdoor colony.

(2) Development of a behavioral test that yields consistent results across time<br /> The multiple-foraging box paradigm, in which behavioral traits such as overall activity, levels of risk-taking, and exploratoriness can be evaluated as creative, and suggestive of behavioral paradigms other animal behavior researchers might be able to use. It is especially useful, given that it can be used to evaluate the activity of animals seemingly at most stages of life, and not just in adulthood.

Weaknesses:

(1) Robustness and validity of personality measures<br /> Coming up with robust measures of "personality" in non-human animals is tricky. While this paper represents an important attempt at a solution, some of the results obtained from the indoor foraging paradigm raise questions as to the reliability of this task for assessing "personality".

(2) Insufficient exploitation of data<br /> Between the behavioral measures and the very multidimensional GPS data, the authors are in possession of a rich data set. However, I don't feel that this data has been adequately exploited for underlying patterns and relationships. For example, many more metrics could be extracted from the GPS data, which may then reveal correlations with early measures of personality or further underscore the role of the early environment. In addition, the possibility that these personality measures might in combination affect outdoor foraging is not explored.

(3) Interpretation of statistical results and definition of statistical models<br /> Some statistical interpretations may not be entirely accurate, particularly in the case of multiple regression with generalized linear models. In addition, some effects which may be present in the data are dismissed as not significant on the basis of null hypothesis testing.

Below I have organized the main points of critique by theme, and ordered subordinate points by order of importance:

(1) Assessing personality metrics and the indoor paradigm: While I applaud this effort and think the metrics used are justified, I see a few issues in the results as they are currently presented:<br /> (a) [Major] I am somewhat concerned that here, the foraging box paradigm is being used for two somewhat conflicting purposes: (1) assessing innate personality and (2) measuring changes in personality as a result of experience. If the indoor foraging task is indeed meant to measure and reflect both at the same time, then perhaps this can be made more explicit throughout the manuscript. In this circumstance, I think the authors could place more emphasis on the fact that the task, at later trials/measurements, begins to take on the character of a "composite" measure of personality and experience.

(b) [Major] Although you only refer to results obtained in trials 1 and 2 when trying to estimate "innate personality" effects, I am a little worried that the paradigm used to measure personality, i.e. the stable components of behavior, is itself affected by other factors such as age (in the case of activity, Fig. 1C3, S1C1-2), the environment (see data re trial 3), and experience outdoors (see data re trials 4/5).

Ideally, a study that aims to disentangle the role of predisposition from early-life experience would have a metric for predisposition that is relatively unchanging for individuals, which can stand as a baseline against a separate metric that reflects behavioral differences accumulated as a result of experience.

I would find it more convincing that the foraging box paradigm can be used to measure personality if it could be shown that young bats' behavior was consistent across retests in the box paradigm prior to any environmental exposure across many baseline trials (i.e. more than 2), and that these "initial settings" were constant for individuals. I think it would be important to show that personality is consistent across baseline trials 1 and 2. This could be done, for example, by reproducing the plots in Fig. 1C1-3 while plotting trial 1 against trial 2. (I would note here that if a significant, positive correlation were to be found (as I would expect) between the measures across trial 1 and 2, it is likely that we would see the "habituation effect" the authors refer to expressed as a steep positive slope on the correlation line (indicating that bold individuals on trial 1 are much bolder on trial 2).)

(c) Related to the previous point, it was not clear to me why the data from trial 2 (the second baseline trial) was not presented in the main body of the paper, and only data from trial 1 was used as a baseline.

In the supplementary figure and table, you show that the bats tended to exhibit more boldness and exploratory behavior, but fewer actions, in trial 2 as compared with trial 1. You explain that this may be due to habituation to the experimental setup, however, the precise motivation for excluding data from trial 2 from the primary analyses is not stated. I would strongly encourage the authors to include a comparison of the data between the baseline trials in their primary analysis (see above), combine the information from these trials to form a composite baseline against which further analyses are performed, or further justify the exclusion of data as a baseline.

(2) Comparison of indoor behavioral measures and outdoor behavioral measures<br /> Regarding the final point in the results, correlation between indoor personality on Trial 4 and outdoor foraging behavior: It is not entirely clear to me what is being tested (neither the details of the tests nor the data or a figure are plotted). Given some of the strong trends in the data - namely, (1) how strongly early environment seems to affect outdoor behavior, (2) how strongly outdoor experience affects boldness, measured on indoor behavior (Fig. 1D) - I am not convinced that there is no relationship, as is stated here, between indoor and outdoor behavior. If this conclusion is made purely on the basis of a p-value, I would suggest revisiting this analysis.

(3) Use of statistics/points regarding the generalized linear models<br /> While I think the implementation of the GLMM models is correct, I am not certain that the interpretation of the GLMM results is entirely correct for cases where multivariate regression has been performed (Tables 4s and S1, and possibly Table 3). (You do not present the exact equation they used for each model (this would be a helpful addition to the methods), therefore it is somewhat difficult to evaluate if the following critique properly applies, however...)

The "estimate" for a fixed effect in a regression table gives the difference in the outcome variable for a 1 unit increase in the predictor variable (in the case of numeric predictors) or for each successive "level" or treatment (in the case of categorical variables), compared to the baseline, the intercept, which reflects the value of the outcome variable given by the combination of the first value/level of all predictors. Therefore, for example, in Table 4a - Time spend outside: the estimate for Bat sex: male indicates (I believe) the difference in time spent outside for an enriched male vs. an enriched female, not, as the authors seem to aim to explain, the effect of sex overall. Note that the interpretation of the first entry, Environmental condition: impoverished, is correct. I refer the authors to the section "Multiple treatments and interactions" on p. 11 of this guide to evaluating contrasts in G/LMMS: https://bbolker.github.io/mixedmodels-misc/notes/contrasts.pdf

Reviewer #1 (Public review):

Summary:

The manuscript aims to elucidate the impact of a prophage within the genome of Shewanella fidelis on its interaction with the marine tunicate Ciona robusta. The authors made a deletion mutant of S. fidelis that lacks one of its two prophages. This mutant exhibited an enhanced biofilm phenotype, as assessed through crystal violet staining, and showed reduced motility. The authors examined the effect of prophage deletion on several genes that could modulate cyclic-diGMP levels. While no significant changes were observed under in vitro conditions, the gene for one protein potentially involved in cyclic-diGMP hydrolysis was overexpressed during microbe-host interactions. The mutant was retained more effectively within a one-hour timeframe, whereas the wild-type (WT) strain became more abundant after 24 hours. Fluorescence microscopy was used to visualize the localization patterns of the two strains, which appeared to differ. Additionally, a significant difference in the expression of one immune protein was noted after one hour, but this difference was not evident after 23 hours. An effect of VCBC-C addition on the expression of one prophage gene was also observed.

Strengths:

I appreciate how the authors integrate diverse expertise and methods to address questions regarding the impact of prophages on gut microbiome-host interactions. The chosen model system is appropriate, as it allows for high-throughput experimentation and the application of simple imaging techniques.

Weaknesses:

My primary concern is that the manuscript primarily describes observations without providing insight into the molecular mechanisms underlying the observed differences. It is particularly unclear how the presence of the prophage leads to the phenotypic changes related to bacterial physiology and host-microbe interactions. Which specific prophage genes are critical, or is the insertion at a specific site in the bacterial genome the key factor? While significant effects on bacterial physiology are reported under in vitro conditions, there is no clear attribution to particular enzymes or proteins. In contrast, when the system is expanded to include the tunicate, differences in the expression of a cyclic-diGMP hydrolase become apparent. Why do we not observe such differences under in vitro conditions, despite noting variations in biofilm formation and motility? Furthermore, given that the bacterial strain possesses two prophages, I am curious as to why the authors chose to target only one and not both.

Regarding the microbe-host interaction, it is not clear why the increased retention ability of the prophage deletion strain did not lead to greater cell retention after 24 hours, especially since no differences in the immune response were observed at that time point.

Concerning the methodological approach, I am puzzled as to why the authors opted for qPCR instead of transcriptomics or proteomics. The latter approaches could have provided a broader understanding of the prophage's impact on both the microbe and the host.

Reviewer #2 (Public review):

Summary:

In the manuscript, "Prophage regulation of Shewanella fidelis 3313 motility and biofilm formation: implications for gut colonization dynamics in Ciona robusta", the authors are experimentally investigating the idea that integrated viruses (prophages) within a bacterial colonizer of the host Ciona robusta affect both the colonizer and the host. They found a prophage within the Ciona robusta colonizing bacterium Shewanella fidelis 3313, which affected both the bacteria and host. This prophage does so by regulating the phosphodiesterase gene pdeB in the bacterium when the bacterium has colonized the host. The prophage also regulates the activity of the host immune gene VCBP-C during early bacterial colonization. Prophage effects on both these genes affect the precise localization of the colonizing bacterium, motility of the bacterium, and bacterial biofilm formation on the host. Interestingly, VCBP-C expression also suppressed a prophage structural protein, creating a tripartite feedback loop in this symbiosis. This is exciting research that adds to the emerging body of evidence that prophages can have beneficial effects not only on their host bacteria but also on how that bacteria interacts in its environment. This study establishes the evolutionary conservation of this concept with intriguing implications of prophage effects on tripartite interactions.

Strengths:

This research effectively shows that a prophage within a bacterium colonizing a model ascidian affects both the bacterium and the host in vivo. These data establish the prophage effects on bacterial activity and expand these effects to the natural interactions within the host animal. The effects of the prophage through deletion on a suite of host genes are a strength, as shown by striking microscopy.

Weaknesses:

Unfortunately, there are abundant negative data that cast some limitations on the interpretation of the data. That is, examining specific gene expression has its limitations, which could be avoided by global transcriptomics of the bacteria and the host during colonization by the prophage-containing and prophage-deleted bacteria (1 hour and 24 hours). In this way, the tripartite interactions leading to mechanism could be better established.

Impact:

The authors are correct to speculate that this research can have a significant impact on many animal microbiome studies, since bacterial lysogens are prevalent in most microbiomes. Screening for prophages, determining whether they are active, and "curing" the host bacteria of active prophages are effective tools for understanding the effects these mobile elements have on microbiomes. There are many potential effects of these elements in vivo, both positive and negative, this research is a good example of why this research should be explored.

Context:

The research area of prophage effects on host bacteria in vitro has been studied for decades, while these interactions in combination with animal hosts in vivo have been recent. The significance of this research shows that there could be divergent effects based on whether the study is conducted in vitro or in vivo. The in vivo results were striking. This is particularly so with the microscopy images. The benefit of using Ciona is that it has a translucent body which allows for following microbial localization. This is in contrast to mammalian studies where following microbial localization would either be difficult or near impossible.

Reviewer #3 (Public review):

In this manuscript, Natarajan and colleagues report on the role of a prophage, termed SfPat, in the regulation of motility and biofilm formation by the marine bacterium Shewanella fidelis. The authors investigate the in vivo relevance of prophage carriage by studying the gut occupation patterns of Shewanella fidelis wild-type and an isogenic SfPat- mutant derivative in a model organism, juveniles of the marine tunicate Ciona robusta. The role of bacterial prophages in regulating bacterial lifestyle adaptation and niche occupation is a relatively underexplored field, and efforts in this direction are appreciated.

While the research question is interesting, the work presented lacks clarity in its support for several major claims, and, at times, the authors do not adequately explain their data.

Major concerns:

(1) Prophage deletion renders the SfPat- mutant derivative substantially less motile and with a higher biofilm formation capacity than the WT (Fig. 2a-b). The authors claim the mutant is otherwise isogenic to the WT strain upon sequence comparison of draft genome sequences (I'll take the opportunity to comment here that GenBank accessions are preferable to BioSample accessions in Table 1). Even in the absence of secondary mutations, complementation is needed to validate functional associations (i.e., phenotype restoration). A strategy for this could be phage reintegration into the mutant strain (PMID: 19005496).

(2) The authors claim that the downshift in motility (concomitant with an upshift in biofilm formation) is likely mediated by the activity of c-di-GMP turnover proteins. Specifically, the authors point to the c-di-GMP-specific phosphodiesterase PdeB as a key mediator, after finding lower transcript levels for its coding gene in vivo (lines 148-151, Fig. 2c), and suggesting higher activity of this protein in live animals (!)(line 229). I have several concerns here:<br /> (2.1) Findings shown in Fig. 2a-b are in vitro, yet no altered transcript levels for pdeB were recorded (Fig. 2c). Why do the authors base their inferences only on in vivo data?<br /> (2.2) Somewhat altered transcript levels alone are insufficient for making associations, let alone solid statements. Often, the activity of c-di-GMP turnover proteins is local and/or depends on the activation of specific sensory modules - in the case of PdeB, a PAS domain and a periplasmic sensor domain (PMID: 35501424). This has not been explored in the manuscript, i.e., specific activation vs. global alterations of cellular c-di-GMP pools (or involvement of other proteins, please see below). Additional experiments are needed to confirm the involvement of PdeB. Gaining such mechanistic insights would greatly enhance the impact of this study.<br /> (2.3) What is the rationale behind selecting only four genes to probe the influence of the prophage on Ciona gut colonization by determining their transcript levels in vitro and in vivo? If the authors attribute the distinct behavior of the mutant to altered c-di-GMP homeostasis, as may be plausible, why did the authors choose those four genes specifically and not, for example, the many other c-di-GMP turnover protein-coding genes or c-di-GMP effectors present in the S. fidelis genome? This methodological approach seems inadequate to me, and the conclusions on the potential implication of PdeB are premature.

(3) The behavior of the WT strain and the prophage deletion mutant is insufficiently characterized. For instance, how do the authors know that the higher retention capacity reported for the WT strain with respect to the mutant (Fig. 3b) is not merely a consequence of, e.g., a higher growth rate? It would be worth investigating this further, ideally under conditions reflecting the host environment.

(4) Related to the above, sometimes the authors refer to "retention" (e.g., line 162) and at other instances to "colonization" (e.g., line 161), or even adhesion (line 225). These are distinct processes. The authors have only tracked the presence of bacteria by fluorescence labeling; adhesion or colonization has not been assessed or demonstrated in vivo. Please revise.

(5) The higher CFU numbers for the WT after 24 h (line 161) might also indicate a role of motility for successful niche occupation or dissemination in vivo. The authors could test this hypothesis by examining the behavior of, e.g., flagellar mutants in their in vivo model.

(6) The endpoint of experiments with a mixed WT-mutant inoculum (assumedly 1:1? Please specify) was set to 1 h, I assume because of the differences observed in CFU counts after 24 h. In vivo findings shown in Fig. 3c-e are, prima facie, somewhat contradictory. The authors report preferential occupation of the esophagus by the WT (line 223), which seems proficient from evidence shown in Fig. S3. Yet, there is marginal presence of the WT in the esophagus in experiments with a mixed inoculum (Fig. 3d) or none at all (Fig. 3e). Likewise, the authors claim preferential "adhesion to stomach folds" by the mutant strain (line 225), but this is not evident from Fig. 3e. In fact, the occupation patterns by the WT and mutant strain in the stomach in panel 3e appear to differ from what is shown in panel 3d. The same holds true for the claimed "preferential localization of the WT in the pyloric cecum," with Fig. 3d showing a yellow signal that indicates the coexistence of WT and mutant.

(7) In general, and especially for in vivo data, there is considerable variability that precludes drawing conclusions beyond mere trends. One could attribute such variability in vivo to the employed model organism (which is not germ-free), differences between individuals, and other factors. This should be discussed more openly in the main text and presented as a limitation of the study. Even with such intrinsic factors affecting in vivo measurements, certain in vitro experiments, which are expected, in principle, to yield more reproducible results, also show high variability (e.g., Fig. 5). What do the authors attribute this variability to?

(8) Line 198-199: Why not look for potential prophage excision directly rather than relying on indirect, presumptive evidence based on qPCR?

Reviewer #1 (Public review):

Summary:

The authors showed the presence of Mtb in human liver biopsy samples of TB patients and reported that chronic infection of Mtb causes immune-metabolic dysregulation. Authors showed that Mtb replicates in hepatocytes in a lipid rich environment created by up regulating transcription factor PPARγ. Authors also reported that Mtb protects itself from anti-TB drugs by inducing drug metabolising enzymes.

Strengths:

It has been shown that Mtb induces storage of triacylglycerol in macrophages by induction of WNT6/ACC2 which helps in its replication and intracellular survival, however, creation of favorable replicative niche in hepatocytes by Mtb is not reported. It is known that Mtb infects macrophages and induces formation of lipid-laden foamy macrophages which eventually causes tissue destruction in TB patients. In a recent article it has been reported that "A terpene nucleoside from M. tuberculosis induces lysosomal lipid storage in foamy macrophages" that shows how Mtb manipulates host defense mechanisms for its survival. In this manuscript, authors reported the enhancement of lipid droplets in Mtb infected hepatocytes and convincingly showed that fatty acid synthesis and triacylglycerol formation is important for growth of Mtb in hepatocytes. The authors also showed the molecular mechanism for accumulation of lipid and showed that the transcription factor associated with lipid biogenesis, PPARγ and adipogenic genes were upregulated in Mtb infected cells.

The comparison of gene expression data between macrophages and hepatocytes by authors is important which indicates that Mtb modulates different pathways in different cell type as in macrophages it is related to immune response whereas, in hepatocytes it is related to metabolic pathways.

Authors also reported that Mtb residing in hepatocytes showed drug tolerance phenotype due to up regulation of enzymes involved in drug metabolism and showed that cytochrome P450 monooxygenase that metabolize rifampicin and NAT2 gene responsible for N-acetylation of isoniazid were up regulated in Mtb infected cells.

Weaknesses:

There are reports of hepatic tuberculosis in pulmonary TB patients especially in immune-compromised patients, therefore finding granuloma in human liver biopsy samples is not surprising.<br /> Mtb infected hepatic cells showed induced DME and NAT and this could lead to enhanced metabolism of drug by hepatic cells as a result Mtb in side HepG2 cells get exposed to reduced drug concentration and show higher tolerance to drug. The authors mentioned that " hepatocyte resident Mtb may display higher tolerance to rifampicin". In my opinion higher tolerance to drugs is possible only when DME of Mtb inside is up regulated or the target is modified. Although, in the end authors mentioned that drug tolerance phenotype can be better attributed to host intrinsic factors rather than Mtb efflux pumps. It may be better if the Drug tolerant phenotype section can be rewritten to clarify the facts.

Reviewer #2 (Public review):

The manuscript by Sarkar et al has demonstrated the infection of liver cells/hepatocytes with Mtb and the significance of liver cells in the replication of Mtb by reprogramming lipid metabolism during tuberculosis. Besides, the present study shows that similar to Mtb infection of macrophages (reviewed in Chen et al., 2024; Toobian et al., 2021), Mtb infects liver cells but with a greater multiplication owing to consumption of enhanced lipid resources mediated by PPARg that could be cleared by its inhibitors. The strength of the study lies in the clinical evaluation of the presence of Mtb in human autopsied liver samples from individuals with miliary tuberculosis and the presence of a clear granuloma-like structure. The interesting observation is of granuloma-like structure in liver which prompts further investigations in the field.

The modulation of lipid synthesis during Mtb infection, such as PPARg upregulation, appears generic to different cell types including both liver cells and macrophage cells. It is also known that infection affect PPARγ expression and activity in hepatocytes. It is also known that this can lead to lipid droplet accumulation in the liver and the development of fatty liver disease (as shown for HCV). This study is in a similar line for M.tb infection. As the liver is the main site for lipid regulation, the availability of lipid resources is greater and higher is the replication rate. In short, the observations from the study confirm the earlier studies with these additional cell types. It is known that higher the lipid content, the greater are Lipid Droplet-positive Mtb and higher is the drug resistance (Mekonnen et al., 2021). The DMEs of liver cells add further to the phenotype.

Reviewer #3 (Public review):

This manuscript by Sarkar et al. examines the infection of the liver and hepatocytes during M. tuberculosis infection. They demonstrate that aerosol infection of mice and guinea pigs leads to appreciable infection of the liver as well as the lung. Transcriptomic analysis of HepG2 cells showed differential regulation of metabolic pathways including fatty acid metabolic processing. Hepatocyte infection is assisted by fatty acid synthesis in the liver and inhibiting this caused reduced Mtb growth. The nuclear receptor PPARg was upregulated by Mtb infection and inhibition or agonism of its activity caused a reduction or increase in Mtb growth, respectively, supporting data published elsewhere about the role of PPARg in lung macrophage Mtb infection. Finally, the authors show that Mtb infection of hepatocytes can cause upregulation of enzymes that metabolize antibiotics, resulting in increased tolerance of these drugs by Mtb in the liver.

Overall, this is an interesting paper on an area of TB research where we lack understanding. However, some additions to the experiments and figures are needed to improve the rigor of the paper and further support the findings. Most importantly, although the authors show that Mtb can infect hepatocytes in vitro, they fail to describe how bacteria get from the lungs to the liver in an aerosolized infection. They also claim that "PPARg activation resulting in lipid droplets formation by Mtb might be a mechanism of prolonging survival within hepatocytes" but do not show a direct interaction between PPARg activation and lipid droplet formation and lipid metabolism, only that PPARg promotes Mtb growth. Thus, the correlations with PPARg appear to be there but causation, implied in the abstract and discussion, is not proven.

The human photomicrographs are important and overall well done (lung and liver from the same individuals is excellent). However, in lines 120-121, the authors comment on the absence of studies on the precise involvement of different cells in the liver. In this study there is no attempt to immunophenotype the nature of the cells harboring Mtb in these samples (esp. hepatocytes). Proving that hepatocytes specifically harbor the bacteria in these human samples would add significant rigor to the conclusions made.

Reviewer #1 (Public review):

Summary:

This is an interesting theoretical study examining the viability of Virtual Circular Genome (VCG) model, a recently proposed scenario of prebiotic replication in which a relatively long sequence is stored as a collection of its shorter subsequences (and their compliments). It was previously pointed out that VCG model is prone to so-called sequence scrambling which limits the overall length of such a genome. In the present paper, additional limitations are identified. Specifically, it is shown that VCG is well replicated when the oligomers are elongated by sufficiently short chains from "feedstock" pool. However, ligation of oligomers from VCG itself results in a high error rate. I believe the research is of high quality and well written. However, the presentation could be improved and the key messages could be clarified.

(1) It is not clear from the paper whether the observed error has the same nature as sequence scrambling<br /> (2) The authors introduce two important lengths LS1 and LS2 only in the conclusions and do not explain enough which each of them is important. It would make sense to discuss this early in the manuscript.<br /> (3) It is not entirely clear why specific length distribution for VCG oligomers has to be assumed rather than emerged from simulations.<br /> (4) Furthermore, the problem has another important length, L0 that is never introduced or discussed: a minimal hybridization length with a lifetime longer than the ligation time. From the parameters given, it appears that L0 is sufficiently long (~10 bases). In other words, it appears that the study is done is a somewhat suboptimal regime: most hybridization events do not lead to a ligation. Am I right in this assessment? If that is the case, the authors might want to explore another regime, L0<br /> Strengths:

High-quality theoretical modeling of an important problem is implemented.

Weaknesses:

The conclusions are somewhat convoluted and could be presented better.

Reviewer #2 (Public review):

Summary:

This important theoretical and computational study by Burger and Gerland attempts to set environmental, compositional, kinetic, and thermodynamic constraints on the proposed virtual circular genome (VCG) model for the early non-enzymatic replication of RNA. The authors create a solid kinetic model using published kinetic and thermodynamic parameters for non-enzymatic RNA ligation and (de)hybridization, which allows them to test a variety of hypotheses about the VCG. Prominently, the authors find that the length (longer is better) and concentration (intermediate is better) of the VCG oligos have an outsized impact on the fidelity and yield of VCG production with important implications for future VCG design. They also identify that activation of only RNA monomers, which can be achieved using environmental separation of the activation and replication, can relax the constraints on the concentration of long VCG component oligos by avoiding the error-prone oligo-oligo ligation. Finally, in a complex scenario with multiple VCG oligo lengths, the authors demonstrate a clear bias for the extension of shorter oligos compared to the longer ones. This effect has been observed experimentally (Ding et al., JACS 2023) but was unexplained rigorously until now. Overall, this manuscript will be of interest to scientists studying the origin of life and the behavior of complex nucleic acid systems.

Strengths:

- The kinetic model is carefully and realistically created, enabling the authors to probe the VCG thoroughly.<br /> - Fig. 6 outlines important constraints for scientists studying the origin of life. It supports the claim that the separation of activation and replication chemistry is required for efficient non-enzymatic replication. One could easily imagine a scenario where activation of molecules occurs, followed by their diffusion into another environment containing protocells that encapsulate a VCG. The selective diffusion of activated monomers across protocell membranes would then result in only activated monomers being available to the VCG, which is the constraint outlined in this work. The proposed exclusive replication by monomers also mirrors the modern biological systems, which nearly exclusively replicate by monomer extension.<br /> - Another strength of the work is that it explains why shorter oligos extend better compared to the long ones in complex VCG mixtures. This point is independent of the activation chemistry used (it simply depends on the kinetics and thermodynamics of RNA base-pairing) so it should be very generalizable.

Weaknesses:

- Most of the experimental work on the VCG has been performed with the bridged 2-aminoimidazolium dinucleotides, which are not featured in the kinetic model of this work. Oher studies by Szostak and colleagues have demonstrated that non-enzymatic RNA extension with bridged dinucleotides have superior kinetics (Walton et al. JACS 2016, Li et al. JACS 2017), fidelity (Duzdevich et al. NAR 2021), and regioselectivity (Giurgiu et al. JACS 2017) compared to activated monomers, establishing the bridged dinucleotides as important for non-enzymatic RNA replication. Therefore, the omission of these species in the kinetic model presented here can be perceived as problematic. The major claim that avoidance of oligo ligations is beneficial for VCGs may be irrelevant if bridged dinucleotides are used as the extending species, because oligo ligations (V + V in this work) are kinetically orders of magnitude slower than monomer extensions (F + V in this work) (Ding et al. NAR 2022). Formally adding the bridged dinucleotides to the kinetic model is likely outside of the scope of this work, but perhaps the authors could test if this should be done in the future by simply increasing the rate of monomer extension (F + V) to match the bridged dinucleotide rate without changing rate of V + V ligation?<br /> - The kinetic and thermodynamic parameters for oligo binding appear to be missing two potentially important components. First, base-paired RNA strands that contain gaps where an activated monomer or oligo can bind have been shown to display significantly different kinetics of ligation and binding/unbinding than complexes that do not contain such gaps (see Prywes et al. eLife 2016, Banerjee et al. Nature Nanotechnology 2023, and Todisco et al. JACS 2024). Would inclusion of such parameters alter the overall kinetic model? Second, it has been shown that long base-paired RNA can tolerate mismatches to an extent that can result in monomer ligation to such mismatched duplexes (see Todisco et al. NAR 2024). Would inclusion of the parameters published in Todisco et al. NAR 2024 alter the kinetic model significantly?

Reviewer #1 (Public review):

Summary:

Persistence is a phenomenon by which genetically susceptible cells are able to survive exposure to high concentrations of antibiotics. This is especially a major problem when treating infections caused by slow growing mycobacteria such as M. tuberculosis and M. abscessus. Studies on the mechanisms adopted by the persisting bacteria to survive and evade antibiotic killing can potentially lead to faster and more effective treatment strategies.

To address this, in this study, the authors have used a transposon mutagenesis based sequencing approach to identify the genetic determinants of antibiotic persistence in M. abscessus. To enrich for persisters they employed conditions, that have been reported previously to increase persister frequency - nutrient starvation, to facilitate genetic screening for this phenotype. M.abs transposon library was grown in nutrient rich or nutrient depleted conditions and exposed to TIG/LZD for 6 days, following which Tn-seq was carried out to identify genes involved in spontaneous (nutrient rich) or starvation-induced conditions. About 60% of the persistence hits were required in both the conditions. Pathway analysis revealed enrichment for genes involved in detoxification of nitrosative, oxidative, DNA damage and proteostasis stress. The authors then decided to validate the findings by constructing deletions of 5 different targets (pafA, katG, recR, blaR, Mab_1456c) and tested the persistence phenotype of these strains. Rather surprisingly only 2 of the 5 hits (katG and pafA) exhibited a persistence defect when compared to wild type upon exposure to TIG/LZD and this was complemented using an integrative construct. The authors then investigated the specificity of delta-katG susceptibility against different antibiotic classes and demonstrated increased killing by rifabutin. The katG phenotype was shown to be mediated through the production of oxidative stress which was reverted when the bacterial cells were cultured under hypoxic conditions. Interestingly, when testing the role of katG in other clinical strains of Mab, the phenotype was observed only in one of the clinical strains demonstrating that there might be alternative anti-oxidative stress defense mechanisms operating in some clinical strains.

Strengths:

While the role of ROS in antibiotic mediated killing of mycobacterial cells have been studied to some extent, this paper presents some new findings with regards to genetic analysis of M. abscessus susceptibility, especially against clinically used antibiotics, which makes it useful. Also, the attempts to validate their observations in clinical isolates is appreciated.

Weaknesses:

- Fig. 3 - 5 of the hits from the transposon screen were reconstructed as clean deletion strains and tested for persistence. However, only 1 (katG) gave a strong and 1 (Mab_1456c) exhibited a minor defect. Two of the clones did not show any persistence phenotype (blaR and recR) and one (pafA) showed a minor phenotype, however it was not clear if this difference was really relevant as the mutant exhibited differences at Day 0, prior to the addition of antibiotics. Considering these results from the validation, the conclusion would be that the Tn-seq approach to screen persistence defects is not reliable and is more likely to result in misses than hits.

- Fig 3 - Why is there such a huge difference in the extent of killing of the control strain in media, when exposed to TIG/LZD, when compared to Fig. 1C and Fig. 4. In Fig. 1C, M. abs grown in media decreases by >1 log by Day 3 and >4 log by Day 6, whereas in Fig. 3, the bacterial load decreases by <1 log by Day 3 and <2 log by Day 6. This needs to be clarified, if the experimental conditions were different, because if comparing to Fig. 1C data then the katG mutant strain phenotype is not very different.

Reviewer #2 (Public review):

Summary:

The work set out to better understand the phenomenon of antibiotic persistence in mycobacteria. Three new observations are made using the pathogenic Mycobacterium abscessus as an experimental system: phenotypic tolerance involves suppression of ROS, protein synthesis inhibitors can be lethal for this bacterium, and levofloxacin lethality is unaffected by deletion of catalase, suggesting that this quinolone does not kill via ROS.

Strengths:

The ROS experiments are supported in three ways: measurement of ROS by a fluorescent probe, deletion of catalase increases lethality of selected antibiotics, and a hypoxia model suppresses antibiotic lethality. A variety of antibiotics are examined, and transposon mutagenesis identifies several genes involved in phenotypic tolerance, including one that encodes catalase. The methods are adequate for making these statements.

Weaknesses:

The work can be improved in two major ways. First, word-choice decisions could better conform to the published literature. Alternatively, novel definitions could be included. In particular, the data support the concept of phenotypic tolerance, not persistence. Second, two of the novel observations could be explored more extensively to provide mechanistic explanations for the phenomena.

Overall impact: Showing that ROS accumulation is suppressed during phenotypic tolerance, while expected, adds to the examples of the protective effects of low ROS levels. Moreover, the work, along with a few others, extends the idea of antibiotic involvement with ROS to mycobacteria. These are field-solidifying observations.

Reviewer #3 (Public review):

Summary:

The manuscript demonstrates that starvation induces persister formation in M. abscesses. They also utilized Tn-Seq for the identification of genes involved in persistence. They identified the role of catalase-peroxidase KatG in preventing death from translation inhibitors Tigecycline and Linezolid. They further demonstrated that a combination of these translation inhibitors leads to the generation of ROS in PBS-starved cells.

Strengths:

The authors used high-throughput genomics-based methods for identification of genes playing a role in persistence.

Weaknesses:

The findings could not be validated in clinical strains.

Reviewer #1 (Public review):

Summary:

The imaging pipeline presented in this paper is a useful tool for visualizing and dynamically tracking bacterial colony formation at the individual worm level, enabling the study of microbiome colonization's association with host physiology, including lifespan, infection severity, and genetic mutations in real-time. This technique allows for certain biological information to be obtained that was previously missed such as pmk-1 mutants exhibiting a higher rate of colonization by E. coli OP50 than wild-type animals. Overall, this platform could be of interest to many labs studying C. elegans interactions with their microbiome and with bacterial pathogens.

Strengths:

This platform allows for unbiased quantifications of microbe colonization of bacteria at scale. This is particularly important in a field studying dynamic responses or potentially more subtle or variable phenotypes.

Platform could be adapted for multiple uses or potentially other species of nematodes for evolutionary comparisons.

The platform allows researchers to correlate bacterial colonization with predicted lifespan.

Weaknesses:

Platform will require optimization for any given bacteria species which restricts its ease of use for researchers that won't regularly be studying the same bacteria.

Requires the bacteria to be genetically tractable so cannot be easily adapted to microbes that do not have established ways of expressing GFP or other reporters.

This platform requires the use of relatively older adult animals that are more prone to larger gut colonies of bacteria. Thus, studies using this platform are restricted to studying older populations.

The relationship between bacterial colonization and host lifespan requires further investigation. The current SICKO platform and experimentation cannot fully address whether animals in poorer health are more susceptible to colonization, or whether colonization casually contributes to a decline in health. Furthermore, while such effects are statistically significant their effect size in some cases is modest.

Reviewer #2 (Public review):

Summary:

In this manuscript, Espejo et al describe a method, SICKO, that allows for long-term longitudinal examination of bacterial colonization in the gut of C. elegans. SICKO utilizes a well-plate format where single worms are housed in each well with a small NGM pad surrounded by an aversive palmitic acid barrier to prevent worms from fleeing the well. The main benefit of this method is that it captures longitudinal data across individual worms with the ability to capture tens to hundreds of worms at once. The output data of SICKO in the heatmap is also very clear and robustly shows bacterial colonization in the gut across a large sample size, which is far superior to the current gold standard of imaging 10-20 worms in a cross-sectional matter at various timepoints of aging. They then provide a few examples of how this method can be applied to understand how colonization correlates with animal health.

Strengths:

-The method presented in this manuscript is sure to be of great utility to the host-pathogen field of C. elegans. The method also allows for utilization of large sample sizes and a way to present highly transparent data, both of which are excellent for promoting rigor and reproducibility of science.<br /> -The manuscript also does a great job in describing the limitations of the system, which is always appreciated.<br /> -The methods section for the SICKO data analysis pipeline and the availability of the code on Github are strong pluses.

Weaknesses:

-There are minor weaknesses in the methods that could be addressed relatively easily by expanding the explanation of how to set up the individual worm chambers (see comment 1 below).

I am making all my comments and suggestions to the reviewers public, as I believe these comments can be useful to the general readership as well. Comment 1 is important to make the methods more accessible and comment 2 is important to make the data presentation more accessible to a broader audience. However, comments 3-4 are things/suggestions that should be considered by the authors and future users of SICKO for interpretation of all the data presented in the manuscript.

(1) The methods section needs to be described in more detail. Considering that this is a methods development paper, more detailed explanation is required to ensure that readers can actually adapt these experiments into their labs.<br /> (a) What is the volume of lmNGM in each well?<br /> (b) Recommended volume of bacteria to seed in each well?<br /> (c) A file for the model for the custom printed 3D adaptor should be provided.<br /> (d) There should be a bit more detail on how the chambers should be assembled with all the components. After reading this, I am not sure I would be able to put the chamber together myself.<br /> (e) What is the recommended method to move worms into individual wells? Manual picking? Pipetting in a liquid?<br /> (f) Considering that a user-defined threshold is required (challenging for non-experienced users), example images should be provided on what an acceptable vs. nonacceptable threshold would look like.

(2) The output data in 1e is very nice - it is a very nice and transparent plot, which I like a lot. However, since the data is complex, a supplemental figure to explain the data better would be useful to make it accessible for a broader audience. For example, highlighting a few rows (i.e., individual worms) and showing the raw image data for each row would be useful. What I mean is that it would be useful to show what does the worm actually look like for a "large colony size" or "small colony size"? What is the actual image of the worm that represents the yellow (large), versus dark blue (small), versus teal (in the middle)? And also the transition from dark blue to yellow would also be nice to be shown. This can probably also just be incorporated into Fig. 1d by just showing what color each of those worm images from day 1 to day 8 would represent in the heat map (although I still think a dedicated supplemental figure where you highlight a few rows and show matching pictures for each row in image files would be better).

(3) I am not sure that doing a single-time point cross-sectional data is a fair comparison since several studies do multi-timepoint cross-sectional studies (e.g., day 1, day 5, day 9). This is especially true for using only day 1 data - most people do gut colonization assays at later timepoints since the gut barrier has been shown to break down at older ages, not day 1. The data collected by SICKO is done every day across many individuals worms and is clearly superior to this type of cross-sectional data (even with multiple timepoints), and I think this message would be further strengthened by comparing it directly to cross-sectional data collected across more than 1 timepoint of aging.

(4) The authors show that SICKO can detect differences in wild-type vs. pmk-1 loss of function and between OP50 and PA14. However, these are very dramatic conditions that conventional methods can easily detect. I would think that the major benefit of SICKO over conventional methods is that it can detect subtle differences that cross-sectional methods would fail to visualize. It might be useful to see how well SICKO performs for these more subtle effects (e.g., OP50 on NGM vs. bacteria-promoting media; OP50 vs. HT115; etc.).<br /> (a) Similar to the above comment, the authors discuss how pmk-1 has colonization-independent effects on host-pathogen interactions. Maybe using a more direct approach to affect colonization (e.g., perturbing gut actin function like act-5) would be better.

Reviewer #3 (Public Review):

In multiple cancers, the key roles of B cells are emerging in the tumor microenvironment (TME). The authors of this study appropriately introduce that B cells are relatively under-characterised in the TME and argue correctly that it is not known how the B cell receptor (BCR) repertoires across tumor, lymph node and peripheral blood relate. The authors therefore supply a potentially useful study evaluating the tumor, lymph node and peripheral blood BCR repertoires and site-to-site as well as intra-site relationships. The authors employ sophisticated analysis techniques, although the description of the methods is incomplete.

Major strengths:

(1) The authors provide a unique analysis of BCR repertoires across tumor, dLN, and peripheral blood. The work provides useful insights into inter- and intra-site BCR repertoire heterogeneity. While patient-to-patient variation is expected, the findings with regard to intra-tumor and intra-dLN heterogeneity with the use of fragments from the same tissue are of importance, contribute to the understanding of the TME, and will inform future study design.

(2) A particular strength of the study is the detailed CDR3 physicochemical properties analysis which leads the authors to observations that suggest a less-specific BCR repertoire of TIL-B compared to circulating B cells.

Comments on revisions:

Your efforts in addressing concerns related to methodological details, narrative clarity, and data representation are commendable. The expanded descriptions of Fig. 1A and the experimental design, as well as the restructuring of the discussion, have greatly enhanced the manuscript's clarity and coherence.

Reviewer #1 (Public review):

Summary:

In this work, a screening platform is presented for rapid and cost-effective screening of candidate genes involved in Fragile Bone Disorders. The authors validate the approach of using crispants, generating FO mosaic mutants, to evaluate the function of specific target genes in this particular condition. The design of the guide RNAs is convincingly described, while the effectiveness of the method is evaluated to 60% to 92% of the respective target genes being presumably inactivated. Thus, injected F0 larvae can be directly used to investigate the consequences of this inactivation.

Skeletal formation is then evaluated at 7dpf and 14dpf, first using a transgenic reporter line revealing fluorescent osteoblasts, second using alizarin-red staining of mineralized structures. In general, it appears that the osteoblast-positive areas are more often affected in the crispants compared to the mineralized areas, an observation that appears to correlate with the observed reduced expression of bglap, a marker for mature osteoblasts, and the increased expression of col1a1a in more immature osteoblasts.

Finally, the injected fish (except two lines that revealed a high mortality) are also analyzed at 90dpf, using alizarin red staining and micro-CT analysis, revealing an increased incidence of skeletal deformities in the vertebral arches, fractures, as well as vertebral fusions and compressions for all crispants except those for daam2. Finally, the Tissue Mineral Density (TMD) as determined by micro-CT is proposed as an important marker for investigating genes involved in osteoporosis.<br /> Taken together, this manuscript is well presented, the data are clear and well analyzed, and the methods well described. It makes a compelling case for using the crispant technology to screen the function of candidate genes in a specific condition, as shown here for bone disorders.

Strengths:

Strengths are the clever combination of existing technologies from different fields to build a screening platform. All the required methods are comprehensively described.

Weaknesses:

One may have wished to bring one or two of the crispants to the stage of bona fide mutants, to confirm the results of the screening, however, this is done for some of the tested genes as laid out in the discussion.

Comments on latest version:

All my issues were resolved.

Reviewer #2 (Public review):

Summary:

More and more genes and genetic loci are being linked to bone fragility disorders like osteoporosis and osteogenesis imperfecta through GWAS and clinical sequencing. In this study, the authors seek to develop a pipeline for validating these new candidate genes using crispant screening in zebrafish. Candidates were selected based on GWAS bone density evidence (4 genes) or linkage to OI cases plus some aspect of bone biology (6 genes). NGS was performed on embryos injected with different gRNAs/Cas9 to confirm high mutagenic efficacy, and off-target cutting was verified to be low. Bone growth, mineralization, density, and gene expression levels were carefully measured and compared across crispants using a battery of assays at three different stages.

Strengths:

(1) The pipeline would be straightforward to replicate in other labs, and the study could thus make a real contribution towards resolving the major bottleneck of candidate gene validation.

(2) The study is clearly written and extensively quantified.

(3) The discussion attempts to place the phenotypes of different crispant lines into the context of what is already known about each gene's function.

(4) There is added value in seeing the results for the different crispant lines side by side for each assay.

(5) Caveats to the interpretability of crispant data and limitations of their gene-focused analyses and RT-PCR assays are discussed.

Weaknesses:

(1) The study uses only well-established methods and is strategy-driven rather question/hypothesis-driven. This is in line with the researchers' primary goal of developing a workflow for rapid in vivo functional screening of candidate genes. However, this means that less attention is paid to what the results obtained for a given gene may mean regarding potential disease mechanisms, and how contradictions with prior reports of mouse or fish null mutant phenotypes might be explained.

(2) Normalization to body size was not performed. Measurements of surface area covered by osteoblasts or mineralized bone (Fig. 1) are typically normalized to body size - especially in larvae and juvenile fish - to rule out secondary changes due to delayed or accelerated overall growth. This was not done here; the authors argue that "variations in growth were considered as part of the phenotypic outcome." This is reasonable, but because standard length was reported only for fish at 90 dpf (not significantly different in any line), the reader is not given the opportunity to consider whether earlier differences in, e.g. surface area covered by osteoblasts at 14 dpf, could be accounted for by delayed or accelerated overall growth. Images in Figure S5 were not taken at the same magnification, further confounding this effort.

Comments on latest version:

The authors have largely addressed my comments by making changes to the text.

However, in response to one of my original comments ("It would be helpful to note the grouping of candidates into OI vs. BMD GWAS throughout the figures"), they added a sentence to this effect to the legends. However, because two of the lines were larval-lethal, the legends to Figs. S6-8 are now incorrect in referring to ten genes when only eight mutants are shown.

Reviewer #3 (Public review):

The manuscript describes the use of CRISPR gene editing coupled with phenotyping mosaic zebrafish larvae to characterize functions of genes implicated in heritable fragile bone disorders (FBDs). Authors targeted six high-confident candidate genes implicated in severe recessive forms of FBDs and four Osteoporosis GWAS-implicated genes and observe varied developmental phenotypes across all crispants, in addition to adult skeletal phenotypes. While the study lacks insight on underlying mechanisms that contribute to disease phenotypes, a major strength of the paper is the streamlined method that produced significant phenotypes for all candidate genes tested. It also represents a significant increase in number of candidate genes tested using their crispant approach beyond the single mutant that was previously published.

One weakness was the variability of developmental phenotypes, addressed by authors in the Discussion. This might be a product of maternal transcripts not targeted by CRISPR or genetic compensation, which authors have not fully explored. Overall, the paper was well-written and easy to read.

Comments on latest version:

The authors have addressed many concerns in this revision. Figure 1 and Table 2 are much improved.

While details of orthologous gene expression profiles of target genes is a welcome addition, other features of target genes remain unaddressed. For example, do genes with maternally deposited transcript exhibit dampened phenotypes? Or does genetic compensation impact certain genes more than others? Since authors state that the study represents a methods paper, it will be important for users to understand the caveats of gene selection to effectively implement and interpret results of the approach.

Reviewer #1 (Public review):

Bacterial effectors that interfere with the inner molecular workings of eukaryotic host cells are of great biological significance across disciplines. On the one hand they help us to understand the molecular strategies that bacteria use to manipulate host cells. On the other hand they can be used as research tools to reveal molecular details of the intricate workings of the host machinery that is relevant for the interaction/defence/symbiosis with bacteria. The authors investigate the function and biological impact of a rhizobial effector that interacts with and modifies, and curiously is modified by, legume receptors essential for symbiosis. The molecular analysis revealed a bacterial effector that cleaves a plant symbiosis signaling receptor to inhibit signaling and the host counterplay by phosphorylation via a receptor kinase. These findings have potential implications beyond bacterial interactions with plants.

Bao and colleagues investigated how rhizobial effector proteins can regulate the legume root nodule symbiosis. A rhizobial effector is described to directly modify symbiosis-related signaling proteins, altering the outcome of the symbiosis. Overall, the paper presents findings that will have a wide appeal beyond its primary field.

Out of 15 identified effectors from Sinorhizobium fredii, they focus on the effector NopT, which exhibits proteolytic activity and may therefore cleave specific target proteins of the host plant. They focus on two Nod factor receptors of the legume Lotus japonicus, NFR1 and NFR5, both of which were previously found to be essential for the perception of rhizobial nod factor, and the induction of symbiotic responses such as bacterial infection thread formation in root hairs and root nodule development (Madsen et al., 2003, Nature; Tirichine et al., 2003; Nature). The authors present evidence for an interaction of NopT with NFR1 and NFR5. The paper aims to characterize the biochemical and functional consequences of these interactions and the phenotype that arises when the effector is mutated.

Evidence is presented that in vitro NopT can cleave NFR5 at its juxtamembrane region. NFR5 appears also to be cleaved in vivo. and NFR1 appears to inhibit the proteolytic activity of NopT by phosphorylating NopT. When NFR5 and NFR1 are ectopically over-expressed in leaves of the non-legume Nicotiana benthamiana, they induce cell death (Madsen et al., 2011, Plant Journal). Bao et al., found that this cell death response is inhibited by the coexpression of nopT. Mutation of nopT alters the outcome of rhizobial infection in L. japonicus. These conclusions are well supported by the data.

The authors present evidence supporting the interaction of NopT with NFR1 and NFR5. In particular, there is solid support for cleavage of NFR5 by NopT (Figure 3) and the identification of NopT phosphorylation sites that inhibit its proteolytic activity (Figure 4C). Cleavage of NFR5 upon expression in N. benthamiana (Figure 3A) requires appropriate controls (inactive mutant versions) that have been provided, since Agrobacterium as a closely rhizobia-related bacterium might increase defense related proteolytic activity in the plant host cells.

Key results from N. benthamiana appear consistent with data from recombinant protein expression in bacteria. For the analysis in the host legume L. japonicus transgenic hairy roots were included. To demonstrate that the cleavage of NFR5 occurs during the interaction in plant cells the authors build largely on western blots. Regardless of whether Nicotiana leaf cells or Lotus root cells are used as the test platform, the Western blots indicate that only a small proportion of NFR5 is cleaved when co-expressed with nopT, and most of the NFR5 persists in its full-length form (Figures 3A-D). It is not quite clear how the authors explain the loss of NFR5 function (loss of cell death, impact on symbiosis), as a vast excess of the tested target remains intact. It is also not clear why a large proportion of NFR5 is unaffected by the proteolytic activity of NopT. This is particularly interesting in Nicotiana in the absence of Nod factor that could trigger NFR1 kinase activity.

Comments on latest version:

The presentation of the figures and the language has greatly improved and the specific mistakes pointed out in the last review have been corrected. I especially appreciate the new images used to illustrate the observed mutant phenotypes, which are much clearer and easier to understand. The pictures used to illustrate the mutant phenotypes seem to be of more comparable root regions than before. Overall, the requested changes have been implemented, with some exceptions described below.

• Figure 1: New representative images are shown for BAX1 and CERK1. These pictures are more consistent with the phenotype seen in other treatments, but since the data has not changed, I presume the data from leaf discs (where the leaf discs for these treatments looked very different) previously shown is still included. The criteria for what was considered cell death is in my opinion still not described in the legend. The cell death/total ratio has been added for all leaf discs, as requested.<br /> • Figure 2: the discussion of the figure now emphasizes direct protein interaction. There is still no size marker in 2D or a description of size in the figure legend, making it difficult to compare the result to Figure 3. If I understand the rebuttal comments correctly, there are other bands on the blot, including non-specific bands. This does not negate the need to include the full blot as a supplemental figure to show cleaved NFR5 as well as other bands. I do not see any other clarifications on this subject in the manuscript.<br /> • Figure 5: From the pictures, it is now easier to understand what is meant by "infection foci". Although there is no description in the methods of how these were distinguished from infection threads, I believe the images are clear enough.<br /> • Figure 6: The changes in the discussion are appreciated, but panel E still misrepresents the evidence in the paper, as from the drawing it still seems that the cleaved NFR5 is somehow directly responsible for suppressing infection when this was not shown

Reviewer #2 (Public review):

Summary:

This manuscript presents data demonstrating NopT's interaction with Nod Factor Receptors NFR1 and NFR5 and its impact on cell death inhibition and rhizobial infection. The identification of a truncated NopT variant in certain Sinorhizobium species adds an interesting dimension to the study. These data try to bridge the gaps between classical Nod-factor-dependent nodulation and T3SS NopT effector-dependent nodulation in legume-rhizobium symbiosis. Overall, the research provides interesting insights into the molecular mechanisms underlying symbiotic interactions between rhizobia and legumes.

Strengths:

The manuscript nicely demonstrates NopT's proteolytic cleavage of NFR5, regulated by NFR1 phosphorylation, promoting rhizobial infection in L. japonicus. Intriguingly, authors also identify a truncated NopT variant in certain Sinorhizobium species, maintaining NFR5 cleavage but lacking NFR1 interaction. These findings bridge the T3SS effector with the classical Nod-factor-dependent nodulation pathway, offering novel insights into symbiotic interactions.

Weaknesses:

(1) In the previous study, when transiently expressed NopT alone in Nicotiana tobacco plants, proteolytically active NopT elicited a rapid hypersensitive reaction. However, this phenotype was not observed when expressing the same NopT in Nicotiana benthamiana (Figure 1A). Conversely, cell death and a hypersensitive reaction were observed in Figure S8. This raises questions about the suitability of the exogenous expression system for studying NopT proteolysis specificity.

(2) NFR5 Loss-of-function mutants do not produce nodules in the presence of rhizobia in lotus roots, and overexpression of NFR1 and NFR5 produces spontaneous nodules. In this regard, if the direct proteolysis target of NopT is NFR5, one could expect the NGR234's infection will not be very successful because of the Native NopT's specific proteolysis function of NFR5 and NFR1. Conversely, in Figure 5, authors observed the different results.

(3) In Figure 6E, the model illustrates how NopT digests NFR5 to regulate rhizobia infection. However, it raises the question of whether it is reasonable for NGR234 to produce an effector that restricts its own colonization in host plants.

(4) The failure to generate stable transgenic plants expressing NopT in Lotus japonicus is surprising, considering the manuscript's claim that NopT specifically proteolyzes NFR5, a major player in the response to nodule symbiosis, without being essential for plant development.

Comments on revised version:

This version has effectively addressed most of my concerns. However, one key issue remains unresolved regarding the mechanism of NopT in regulating nodule symbiosis. Specifically, the explanation of how NopT catabolizes NFR5 to regulate symbiosis is still not convincing within the current framework of plant-microbe interaction, where plants are understood to genetically control rhizobial colonization.

While alternative regulatory mechanisms in plant-microbe interactions are plausible, the notion that the NRG234-secreted effector NopT could reduce its own infection by either suppressing plant immunity or degrading the symbiosis receptor remains unsubstantiated. I believe further revisions are needed in the discussion section to more clearly address and clarify these findings and any lingering uncertainties.

Reviewer #1 (Public review):

Summary:

The authors introduced their previous paper with the concise statement that "the relationships between lineage-specific attributes and genotypic differences of tumors are not understood" (Chen et al., JEM 2019, PMID: 30737256). For example, it is not clear why combined loss of RB1 and TP53 is required for tumorigenesis in SCLC or other aggressive neuroendocrine (NE) cancers, or why the oncogenic mutations in KRAS or EGFR that drive NSCLC tumorigenesis are found so infrequently in SCLC. This is the main question addressed by the previous and current papers.

One approach to this question is to identify a discrete set of genetic/biochemical manipulations that are sufficient to transform non-malignant human cells into SCLC-like tumors. One group reported transformation of primary human bronchial epithelial cells into NE tumors through a complex lentiviral cocktail involving inactivation of pRB and p53 and activation of AKT, cMYC and BCL2 (PARCB) (Park et al., Science 2018, PMID: 30287662). The cocktail previously reported by Chen and colleagues to transform human pluripotent stem-cell (hPSC)-derived lung progenitors (LPs) into NE xenografts was more concise: DAPT to inactivate NOTCH signaling combined with shRNAs against RB1 and TP53. However, the resulting RP xenografts lacked important characteristics of SCLC. Unlike SCLC, these tumors proliferated slowly and did not metastasize, and although small subpopulations expressed MYC or MYCL, none expressed NEUROD1.

MYC is frequently amplified or expressed at high levels in SCLC, and here, the authors have tested whether inducible expression of MYC could increase the resemblance of their hPSC-derived NE tumors to SCLC. These RPM cells (or RPM T58A with stabilized cMYC) engrafted more consistently and grew more rapidly than RP cells, and unlike RP cells, formed liver metastases when injected into the renal capsule. Gene expression analyses reveled that RPM tumor subpopulations expressed NEUROD1, ASCL1 and/or YAP1.

The hPSC-derived RPM model is a major advance over the previous RP model. This may become a powerful tool for understanding SCLC tumorigenesis and progression and for discovering gene dependencies and molecular targets for novel therapies. However, the specific role of cMYC in this model needs to be clarified.

Recommended Revision:

cMYC can drive proliferation, tumorigenesis or apoptosis in a variety of lineages depending on concurrent mutations. For example, in the Park et al., study, normal human prostate cells could be reprogrammed to form adenocarcinoma-like tumors by activation of cMYC and AKT alone, without manipulation of TP53 or RB1. In their previous manuscript, the authors carefully showed the role of each molecular manipulation in NE tumorigenesis. DAPT was required for NE differentiation of LPs to PNECs, shRB1 was required for expansion of the PNECs, and shTP53 was required for xenograft formation. cMYC expression could influence each of these steps, and importantly, could render some steps dispensable. For example, shRB1 was previously necessary to expand the DAPT-induced PNECs, as neither shTP53 nor activation of KRAS or EGFR had no effect on this population, but perhaps cMYC overexpression could expand PNECs even in the presence of pRB, or even induce LPs to become PNECs without DAPT. Similarly, both shRB1 and shTP53 were necessary for xenograft formation, but maybe not if cMYC is overexpressed. If a molecular hallmark of SCLC, such as loss of RB1 or TP53, has become dispensable with the addition of cMYC, this information is critically important in interpreting this as a model of SCLC tumorigenesis.

To interpret the role of cMYC expression in hPSC-derived RPM tumors, we need to know what this manipulation does without manipulation of pRB, p53 or NOTCH, alone or in combination. There are 7 relevant combinations that should be presented in this manuscript: (1) cMYC alone in LPs, (2) cMYC + DAPT, (3) cMYC + shRB1, (4) cMYC + DAPT + shRB1, (5) cMYC + shTP53, (6) cMYC + DAPT + shTP53, and (7) cMYC + shRB1 + shTP53. Wild-type cMYC is sufficient; further exploration with the T58A mutant would not be necessary.

Please present the effects of these combinations on LP differentiation to PNECs, expansion of PNECs as well as other lung cells, xenograft formation and histology, and xenograft growth rate and capacity for metastasis. If this could be clarified experimentally, and the results discussed in the context of other similar approaches such as the Park et al., paper, this study would be a major addition to the field.

Reviewer #3 (Public review):

This revision and the accompanying rebuttal indicates the authors want to publish their studies without providing several of the reviewer requested additional experiments (such as determining the impact of other Myc family members on metastatic behavior and expression characteristics compared to overexpression of c-Myc), and determining whether the tumors were responsive or not to standard clinically used therapies. Their argument is the author team has moved on to other endeavors, it is important to communicate their findings to the research field, and they have indicated these issues in the Discussion. All of these things are reasonable. However, there two things that would help. The first is to have the authors clearly state in the Discussion section "Limitations of the current study" and then list these out. In the current format the indication that the authors recognize the "limitations" is not clearly stated. An example - of such a limitation is how well their model now provides a human SCLC like tumor that metastasizes. We know that in patients SCLC is widely metastatic, but in SCLC patient derived xenografts with subcutaneous injection that is not seen, so if their model now generated widely metastatic behavior like that seen in patients, this report and the associated resources would be a significant advance to the field. However, their data shows that using their model the subcutaneous tumors don't metastasize, and even with renal capsule models metastases are not common and do not go to important sites (e.g. brain). Second, a major reason for publishing this paper is that their model system would be available as a resource for the field to study. However, I could not find in the paper or the Methods section any statement as to the availability of this presumable important resource. If the resources will not be easily available in a format that others can readily study (e.g. with instructions on how to handle the cells which would seem to be more complicated than other patient derived SCLC models) then of course the value of this paper to the field as a whole is dramatically reduced. I would assume the authors want their model to be used by other investigators and thus a clear statement of model availability and how to routinely handle their model is important to include in their manuscript.

Reviewer #1 (Public review):

Summary:

Here the authors convincingly identify and characterize the SERBP1 interactome and further define its role in the nucleus, where it is associated with complexes involved in splicing, cell division, chromosome structure, and ribosome biogenesis. Many of the SERBP1-associated proteins are RNA-binding proteins and SERBP1 exerts its impact, at least in part, through these players. SERBP1 is mostly disordered but along with its associated proteins displays a preference for G4 binding and can can bind to PAR and be PARylated. They present data that strongly suggest that complexes in which SERBP1 participates are assembled through G4 or PAR binding. The authors suggest that because SERBP1 lacks traditional functional domains yet is clearly involved in distinct regulatory complexes, SERBP1 likely acts in the early steps of assembly through the recognition of interacting sites present in RNA, DNA, and proteins.

Strengths:

The data is very convincing and demonstrated through multiple approaches.

Weaknesses:

None. The authors have adequately addressed earlier reviewer concerns.

Reviewer #2 (Public review):

Summary:

In this study the authors have used pull-down experiments in a cell line overexpressing tagged SERPINE1 mRNA binding protein 1 (SERBP1) followed by mass spectrometry-based proteomics, to establish its interactome. Extensive analyses are performed to connect the data to published resources. The authors attempt to connect SERBP1 to stress granules and Alzheimer's disease associated tau pathology. Based on the interactome, the authors propose a cross-talk between SERBP1 and PARP1 functions.

Strengths:

The main strength of this study lies in the extensive proteomics data analysis, and its effort to connect the data to published studies.

Weaknesses:

Support for the proposed model: While the authors propose a feedback regulatory model for SERBP1 and PARP1 function, strong evidence for PARylation modulating SERBP1 functions is lacking. PARP inhibition decreasing the amount of PARylated proteins associated with SERBP1 and likely all other PARylated proteins is expected.<br /> Evidence from autopsy brain tissue: This study shows unexplained round, punctate staining for SERBP1 in immunohistochemistry (IHC) staining. This may be due to poor preservation of cellular structures in frozen autopsy brain tissue. SERBP1 and pTau co-staining lacks an age matched non-AD control. Most quantifications of human IHC staining and co-localization do not indicate the number of cases and what data points are shown.<br /> The link to stress granules (SGs): G3BP1 staining indicates cytoplasmic mislocalization and perhaps aggregation pathology, but not necessarily SGs. It is not clear whether physiological transient stress granules are preserved in autopsy brain tissue. The co-localization of abundant cytoplasmic G3BP1 and SERBP1 under normal conditions does not indicate association with SGs. Stress granule proteins assemble phase-separated granules in the cytoplasm under cellular stress, whereas here it is shown that normally cytoplasmic SERBP1 has a nucleocytoplasmic distribution in the presence of H2O2, with no evidence for SG formation.

Reviewer #1 (Public review):

Summary:

In cells undergoing Flavivirus infection, cellular translation is impaired but the viruses themselves escape this inhibition and are efficiently translated. In this study, the authors use very elegant and direct approaches to identify the regions in the 5' and 3' UTRs that are important for this phenomenon and then use them to retrieve two cellular proteins that associate with them and mediate translational shutoff evasion (DDX3 and PABP1). A number of experimental approaches are used with a series of well-controlled experiments that fully support the authors' conclusions.

Strengths:

The work identifies the regions in the 5' and 3' UTRs of the viral genome that mediate the escape of JEV from cellular transcriptional shutoff, they evaluate the infectivity of the mutant viruses bearing or not these structures and even explore their pathogenicity in mice. They then identify the cellular proteins that bind to these regions (DDX3 and PABP1) and determine their role in translation blockade escape, in addition to examining and assessing the conservation of the stem-loop identified in JEV in other Flaviviridae.

In almost all of their systematic analyses, translational effects are put in parallel with the replication kinetics of the different mutant viruses. The experimental thread followed in this study is rigorous and direct, and all experiments are truly well-controlled, fully supporting the authors' conclusions

Reviewer #2 (Public review):

Summary:

The authors use a combination of techniques including viral genetics, in vitro reporters, and purified proteins and RNA to interrogate how the Japanese encephalitis virus maintains translation of its RNA to produce viral proteins after the host cell has shut down general translation as a means to block viral replication. They report a role for the RNA helicase DDX3 in promoting virus translation in a cap-independent manner through binding a dumbbell RNA structure in the 3' untranslated region previously reported to drive Japanese encephalitis virus cap-independent translation and a stem-loop at the viral RNA 5' end.

Strengths:

The authors clearly show that the Japanese encephalitis virus does not possess an IRES activity to initiate translation using a range of mono- and bi-cistronic mRNAs. Surprisingly, using a replicon system, the translation of a capped or uncapped viral RNA is reported to have the same translation efficiency when transfected into cells. The authors have applied a broad range of techniques to support their hypotheses.

Weaknesses:

(1) The authors' original experiments in Figure 1 where the virus is recovered following transfection of in vitro transcribed viral RNA with alternative 5' ends such as capped or uncapped ignore that after a single replication cycle of that transfected RNA, the subsequent viral RNA will be capped by the viral capping proteins making the RNA in all conditions the same.

(2) The authors report that deletion of the dumbbell and the large 3' stem-loop RNA reduce replication of a Japanese encephalitis virus replicon. These structures have been reported for other flaviviruses to be important respectively for the accumulation of short flaviviral RNAs that can regulate replication and stability of the viral RNA that lacks a polyA tail. The authors don't show any assessment of RNA stability or degradation state.

(3) The authors propose a model for DDX3 to drive 5'-3' end interaction of the Japanese encephalitis virus viral genome but no direct evidence for this is presented.

(4) The authors' final model in Figure 10 proposes a switch from a cap-dependent translation system in early infection to cap-independent DDX3-driven translation system late in infection. The replicon data that measures translation directly however shows identical traces for capped and uncapped RNAs in all untreated conditions so that which mechanism is used at different stages of the infection is not clear.

Reviewer #3 (Public review):

Summary:

This work is a valuable study that aims to decipher the molecular mechanisms underlying the translation process in Japanese encephalitis virus (JEV), a relevant member of the genus Flavivirus. The authors provide evidence that cap-independent translation, which has already been demonstrated for other flaviviruses, could also account in JEV. This process depends on the genomic 3' UTR, as previously demonstrated in other flaviviruses. Further, the authors find that cellular proteins such as DDX3 or PABP1 could contribute to JEV translation in a cap-independent way. Both DDX3 and PABP1 had previously been described to have a role in cellular protein synthesis and also in the translation step of other flaviviruses distinct from JEV; therefore, this work would expand the cap-independent translation in flaviviruses as a general mechanism to bypass the translation repression exerted by the host cell during viral infection. Further, the findings can be relevant for the development of specific drugs that could interfere with flaviviral translation in the future. Nevertheless, the conclusions are not fully supported by the provided results.

Strengths:

The results provide a good starting point to investigate the molecular mechanism underlying the translation in flaviviruses, which even today is an area of knowledge with many limitations.

Weaknesses:

The main limit of the work is related to the fact that the role of the 3' UTR structural elements and DDX3 is not only circumscribed to translation, but also to replication and encapsidation. In fact, some of the provided results suggest this idea. Particularly, it is intriguing why the virus titer can be completely abrogated while the viral protein levels are only partially affected by the knockdown of DDX3. This points to the fact that many of the drawn conclusions could be overestimated or, at least, all the observed effect cannot be attributed only to the DDX3 effect on translation. Finally, it is noteworthy that the use of uncapped transcripts could be misleading, since this is not the natural molecular context of the viral genome.

Reviewer #1 (Public review):

Summary:

The authors revealed the cellular heterogeneity of companion cells (CCs) and demonstrated that the florigen gene FT is highly expressed in a specific subpopulation of these CCs in Arabidopsis. Through a thorough characterization of this subpopulation, they further identified NITRATE-INDUCIBLE GARP-TYPE TRANSCRIPTIONAL REPRESSOR 1 (NIGT1)-like transcription factors as potential new regulators of FT. Overall, these findings are intriguing and valuable, contributing significantly to our understanding of florigen and the photoperiodic flowering pathway. However, there is still room for improvement in the quality of the data and the depth of the analysis. I have several comments that may be beneficial for the authors.

Strengths:

The usage of snRNA-seq to characterize the FT-expressing companion cells (CCs) is very interesting and important. Two findings are novel: 1) Expression of FT in CCs is not uniform. Only a subcluster of CCs exhibits high expression level of FT. 2) Based on consensus binding motifs enriched in this subcluster, they further identify NITRATE-INDUCIBLE GARP-TYPE TRANSCRIPTIONAL REPRESSOR 1 (NIGT1)-like transcription factors as potential new regulators of FT.

Weaknesses:

(1) Title: "A florigen-expressing subpopulation of companion cells". It is a bit misleading. The conclusion here is that only a subset of companion cells exhibit high expression of FT, but this does not imply that other companion cells do not express it at all.<br /> (2) Data quality: Authors opted for fluorescence-activated nuclei sorting (FANS) instead of traditional cell sorting method. What is the rationale behind this decision? Readers may wonder, especially given that RNA abundance in single nuclei is generally lower than that in single cells. This concern also applies to snRNA-seq data. Specifically, the number of genes captured was quite low, with a median of only 149 genes per nucleus. Additionally, the total number of nuclei analyzed was limited (1,173 for the pFT:NTF and 3,650 for the pSUC2:NTF). These factors suggest that the quality of the snRNA-seq data presented in this study is quite low. In this context, it becomes challenging for the reviewer to accurately assess whether this will impact the subsequent conclusions of the paper. Would it be possible to repeat this experiment and get more nuclei?<br /> (3) Another disappointment is that the authors did not utilize reporter genes to identify the specific locations of the FT-high expressing cells (cluster 7 cells) within the CC population in vivo. Are there any discernible patterns that can be observed?<br /> (4) The final disappointment is that the authors only compared FT expression between the nigtQ mutants and the wild type. Does this imply that the mutant does not have a flowering time defect particularly under high nitrogen conditions?

Reviewer #2 (Public review):

This manuscript submitted by Takagi et al. details the molecular characterization of the FT-expressing cell at a single-cell level. The authors examined what genes are expressed specifically in FT-expressing cells and other phloem companion cells by exploiting bulk nuclei and single-nuclei RNA-seq and transgenic analysis. The authors found the unique expression profile of FT-expressing cells at a single-cell level and identified new transcriptional repressors of FT such as NIGT1.2 and NIGT1.4.

Although previous researchers have known that FT is expressed in phloem companion cells, they have tended to neglect the molecular characterization of the FT-expressing phloem companion cells. To understand how FT, which is expressed in tiny amounts in phloem companion cells that make up a very small portion of the leaf, can be a key molecule in the regulation of the critical developmental step of floral transition, it is important to understand the molecular features of FT-expressing cells in detail. In this regard, this manuscript provides insight into the understanding of detailed molecular characteristics of the FT-expressing cell. This endeavor will contribute to the research field of flowering time.

Here are my comments on how to improve this manuscript.

(1) The most noble finding of this manuscript is the identification of NTGI1.2 as the upstream regulator of FT-expressing cluster 7 gene expression. The flowering phenotypes of the nigtQ mutant and the transgenic plants in which NIGT1.2 was expressed under the SUC2 gene promoter support that NIGT1.2 functions as a floral repressor upstream of the FT gene. Nevertheless, the expression patterns of NIGT1.2 genes do not appear to have much overlap with those of NIGT1.2-downstream genes in the cluster 7 (Figs S14 and F3). An explanation for this should be provided in the discussion section.<br /> (2) To investigate gene expression in the nuclei of specific cell populations, the authors generated transgenic plants expressing a fusion gene encoding a Nuclear Targeting Fusion protein (NTF) under the control of various cell type-specific promoters. Since the public audience would not know about NTF without reading reference 16, some explanation of NTF is necessary in the manuscript. Please provide a schematic of constructs the authors used to make the transformants.

Reviewer #1 (Public review):

Summary

Chabukswar et al analysed endogenous retrovirus (ERV) Env variation in a set of primate genomes using consensus Env sequences from ERVs known to be present in hominoids using a Blast homology search with the aim of characterising env gene changes over time. The retrieved sequences were analysed phylogenetically, and showed that some of the integrations are LTR-env recombinants.

Strengths

The strength of the manuscript is that such an analysis has not been performed yet for the subset of ERV Env genes selected and most of the publicly available primate genomes.

Weaknesses

Unfortunately, the weaknesses of the manuscript outnumber its strengths. Especially the methods section does not contain sufficient information to appreciate or interpret the results. The results section contains methodological information that should be moved, while the presentation of the data is often substandard. For instance, the long lists of genomes in which a certain Env was found could better be shown in tables. Furthermore, there is no overview of the primate genomes, or accession numbers, used. It is unclear whether the analyses, such as the phylogenetic trees, are based on nucleotide or amino acid sequences since this is not stated. tBLASTn was used in the homology searches, so one would suppose aa are retrieved. In the Discussion, both env (nt?) and Env (aa?) are used.

For the non-hominoids, genome assembly of publicly available sequences is not always optimal, and this may require Blasting a second genome from a species. Which should for instance be done for the HML2 sequences found in the Saimiri boliviensis genome, but not in the related Callithrix jacchus genome. Finally, the authors propose to analyse recombination in Env sequences but only retrieve env-LTR recombinant Envs, which should likely not have passed the quality check.

Since the Methods section does not contain sufficient information to understand or reproduce the results, while the Results are described in a messy way, it is unclear whether or not the aims have been achieved. I believe not, as characterisation of env gene changes over time is only shown for a few abberrant integrations containing part of the LTR in the env ORF.

Reviewer #2 (Public review):

Summary:

The manuscript by Chabukswar et al. describes a comprehensive attempt to identify and describe the diversity of retroviral envelope (env) gene sequences present in primate genomes in the form of ancient endogenous retrovirus (ERV) sequences.

Strengths:

The focus on env can be justified because of the role the Env proteins likely played in determining viral tropism and host range of the viruses that gave rise to the ERV insertions, and to a lesser extent, because of the potential for env ORFs to be coopted for cellular functions (in the rare cases where the ORF is still intact and capable of encoding a functional Env protein). In particular, these analyses can reveal the potential roles of recombination in giving rise to novel combinations of env sequences. The authors began by compiling env sequences from the human genome (from human endogenous retrovirus loci, or "HERVs") to build consensus Env protein sequences, and then they use these as queries to screen other primate genomes for group-specific envs by tBLASTn. The "groups" referred to here are previously described, as unofficial classifications of endogenous retrovirus sequences into three very broad categories - Class I, Class II and Class III. These are not yet formally recognized in retroviral taxonomy, but they each comprise representatives of multiple genera, and so would fall somewhere between the Family and Genus levels. The retrieved sequences are subject to various analyses, most notably they are screened for evidence of recombination. The recombinant forms appear to include cases that were probably viral dead-ends (i.e. inactivating the env gene) even if they were propagated in the germline.<br /> The availability of the consensus sequences (supplement) is also potentially useful to others working in this area.

Weaknesses:

The weaknesses are largely in presentation. Discussions of ERVs are always complicated by the lack of a formal and consistent nomenclature and the confusion between ERVs as loci and ERVs as indirect information about the viruses that produced them. For this reason, additional attention needs to be paid to precise wording in the text and/or the use of illustrative figures.

Reviewer #3 (Public review):

Summary:

Retroviruses have been endogenized into the genome of all vertebrate animals. The envelope protein of the virus is not well conserved and acquires many mutations hence can be used to monitor viral evolution. Since they are incorporated into the host genome, they also reflect the evolution of the hosts. In this manuscript the authors have focused their analyses on the env genes of endogenous retroviruses in primates. Important observations made include the extensive recombination events between these retroviruses that were previously unknown and the discovery of HML species in genomes prior to the splitting of old and new world monkeys.

Strengths:

They explored a number of databases and made phylogenetic trees to look at the distribution of retroviral species in primates. The authors provide a strong rationale for their study design, they provide a clear description of the techniques and the bioinformatics tools used.

Weaknesses:

The manuscript is based on bioinformatics analyses only. The reference genomes do not reflect the polymorphisms in humans or other primate species. The analyses thus likely under estimates the amount of diversity in the retroviruses. Further experimental verification will be needed to confirm the observations.<br /> Not sure which databases were used, but if not already analyzed, ERVmap.com and repeatmesker are ones that have many ERVs that are not present in the reference genomes. Also, long range sequencing of the human genome has recently become available which may also be worth studying for this purpose.

Reviewer #1 (Public review):

Summary:

In this study, the authors sequenced emm89 serotype genomes of clinical isolates from patients in Japan, where the number of invasive Group A Streptococcus (GAS), especially those of the emm89 serotype, has drastically increased over the past 10-15 years. The sequences from this cohort were compared against a large collection of publicly available global isolates, yielding a total of almost 1000 genomes in the analysis. Because the researchers focused on the emm89 serotype, they could construct a common core genome, with subsequent ability to analyze genomic differences in accessory genes and intergenic regions that contributed to the invasive phenotype using multiple types of GWAS analysis (SNP, k-mer). Their analysis demonstrates some mutations responsible for invasiveness are specific to the Japanese strains, and that multiple independent virulence factors can contribute to invasiveness. None of the invasive phenotypes were correlated with new gene acquisition. Together, the data support that synergy between bacterial survival and upregulation of virulence factors contributes to the development of severe infection.

Strengths:

• The authors verify their analysis by confirming that covS is one of the more frequently mutated genes in invasive strains of GAS, as has been shown in other publications.

• A mutation in one of the SNPs attributed to invasiveness (SNP fhuB) was introduced into an invasive strain. The authors demonstrate that this mutant strain survives less well in human blood. Therefore, the authors have experimental data to support their claims that their analysis uncovered a new mutation/SNP that contributed to invasiveness.

Weaknesses:

• It would be helpful for the authors to highlight why their technique (large scale analysis of one emm type) can yield more information than a typical GWAS analysis of invasive vs. non-invasive strains. Are SNPs easier to identify using a large-scale core genome? Is it more likely evolutionarily to find mutations in non-coding regions as opposed to the core genome and accessory genes, and this is what this technique allows? Did the analysis yield unexpected genes or new genes that had not been previously identified in other GWAS analyses? These points may need to be made more apparent in the results and deserve some thought in the discussion section.

• The Alpha-fold data does not demonstrate why the mutations the authors identified could contribute to the invasive phenotype. It would be helpful to show an overlay of the predicted structures containing the different SNPs to demonstrate the potential structural differences that can occur due to the SNP. This would make the data more convincing that the SNP has a potential impact on the function of the protein. Similarly, the authors discuss modification of the hydrophobicity of the side chain in the ferrichrome transporter (lines 317-318) due to a SNP, but this is not immediately obvious in the figure (Fig. 5).

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors aim to identify genetic determinants associated with the invasion profile of Streptococcus pyogenes strains of the emm89 type, which has been increasingly linked to invasive infections. The study leverages both in-house sequenced genomes and publicly available genomic data. Several GWAS approaches are applied to these datasets, leading to the identification of potential genetic targets. For these targets, the authors conduct additional analyses, including three-dimensional structural modeling of the encoded proteins, as well as the development of mutant strains. The functional impact of these mutations is further explored through transcriptomic comparisons between the mutants and wild-type strains

Strengths:

The strengths of this manuscript include the large amount of data analyzed and the various methodologies applied. The identification of CovS, a gene known to influence the invasion profile, as a significant variation further validates the methodology employed in this study. Then, the gene fhuD is an intriguing target, identified through both bioinformatics and wet lab approaches.

Weaknesses:

I do not identify any additional weaknesses in the manuscript, beyond those already acknowledged by the authors themselves.

Reviewer #1 (Public review):

Overall, the manuscript reveals the role of actin polymerization to drive the fusion of myoblasts during adult muscle regeneration. This pathway regulates fusion in many contexts, but whether it was conserved in adult muscle regeneration remained unknown. Robust genetic tools and histological analyses were used to support the claims convincingly.

There are a few interpretations that could be adjusted.

The beginning of the results about macrophages traversing ghost fibers after regeneration was a surprise given the context in the abstract and introduction. These results also lead to new questions about this biology that would need to be answered to substantiate the claims in this section. Also, it is unclear the precise new information learned here because it seems obvious that macrophages would need to extravasate the basement membrane to enter ghost fibers and macrophages are known to have this ability. Moreover, the model in Figure 4D has macrophages and BM but there is not even mention of this in the legend. The authors may wish to consider removing this topic from the manuscript.

Which Pax7CreER line was used? In the methods, the Jax number provided is the Gaka line but in the results, Lepper et al 2009 are cited, which is not the citation for the Gaka line.

Did the authors assess regeneration in the floxed mice that do not contain Cre as a control? Or is it known these alleles do not perturb the function of the targeted gene?

The authors comment: 'Interestingly, expression of the fusogenic proteins, MymK and MymX, was up-regulated in the TA muscle of these mice (Fig. S4F), suggesting that fusogen overexpression is not able to rescue the SCM fusion defect resulted from defective branched actin polymerization.' It is unclear if fusogens are truly overexpressed because the analysis is performed at dpi 4 when the expression of fusogens may be decreased in control mice because they have already fused. Also, only two animals were analyzed and it is unclear if MymX is definitively increased. The authors should consider adjusting the interpretation to SCM fusion defect resulting from defective branched actin polymerization is unlikely to be caused by a lack of fusogen expression.

Reviewer #2 (Public review):

To fuse, differentiated muscle cells must rearrange their cytoskeletaon and assemble actin-enriched cytoskeletal structures. These actin foci are proposed to generate mechanical forces necessary to drive close membrane apposition and fusion pore formation.

While the study of these actin-rich structures has been conducted mainly in drosophila, the present manuscript presents clear evidence this mechanism is necessary for the fusion of adult muscle stem cells in vivo, in mice.

However, the authors need to tone down their interpretation of their findings and remember that genetic proof for cytoskeletal actin remodeling to allow muscle fusion in mice has already been provided by different labs (Vasyutina E, et al. 2009 PMID: 19443691; Gruenbaum-Cohen Y, et al., 2012 PMID: 22736793; Hamoud et al., 2014 PMID: 24567399). In the same line of thought, the authors write they "demonstrated a critical function of branched actin-propelled invasive protrusions in skeletal muscle regeneration". I believe this is not a premiere, since Randrianarison-Huetz V, et al., previously reported the existence of finger-like actin-based protrusions at fusion sites in mice myoblasts (PMID: 2926942) and Eigler T, et al., live-recorded said "fusogenic synapse" in mice myoblasts (PMID: 34932950).

Hence, while the data presented here clearly demonstrate that ARP2/3 and SCAR/WAVE complexes are required for differentiating satellite cell fusion into multinucleated myotubes, this is an incremental story, and the authors should put their results in the context of previous literature.

Reviewer #3 (Public review):

The manuscript by Lu et al. explores the role of the Arp2/3 complex and the actin nucleators N-WASP and WAVE in myoblast fusion during muscle regeneration. The results are clear and compelling, effectively supporting the main claims of the study. However, the manuscript could benefit from a more detailed molecular and cellular analysis of the fusion synapse. Additionally, while the description of macrophage extravasation from ghost fibers is intriguing, it seems somewhat disconnected from the primary focus of the work.

Despite this, the data are robust, and the major conclusions are well supported. Understanding muscle fusion mechanism is still a widely unexplored topic in the field and the authors make important progress in this domain.

I have a few suggestions that might strengthen the manuscript as outlined below.

(1) Could the authors provide more detail on how they defined cells with "invasive protrusions" in Figure 4C? Membrane blebs are commonly observed in contacting cells, so it would be important to clarify the criteria used for counting this specific event.

(2) Along the same line, please clarify what each individual dot represents in Figure 4C. The authors mention quantifying approximately 83 SCMs from 20 fibers. I assume each dot corresponds to data from individual fibers, but if that's the case, does this imply that only around four SCMs were quantified per fiber? A more detailed explanation would be helpful.

(3) Localizing ArpC2 at the invasive protrusions would be a strong addition to this study. Furthermore, have the authors examined the localization of Myomaker and Myomixer in ArpC2 mutant cells? This could provide insights into potential disruptions in the fusion machinery.

(4) As a minor curiosity, can ArpC2 WT and mutant cells fuse with each other?

(5) The authors report a strong reduction in CSA at 14 dpi and 28 dpi, attributing this defect primarily to failed myoblast fusion. Although this claim is supported by observations at early time points, I wonder whether the Arp2/3 complex might also play roles in myofibers after fusion. For instance, Arp2/3 could be required for the growth or maintenance of healthy myofibers, which could also contribute to the reduced CSA observed, since regenerated myofibers inherit the ArpC2 knockout from the stem cells. Could the authors address or exclude this possibility? This is rather a broader criticism of how things are being interpreted in general beyond this paper.

Reviewer #1 (Public review):

Summary:

The authors use FIB SEM methods to generate 3D volumes of almost all cells comprising a miniature wasp eye and describe the anatomy of each cell type in detail. The function of each cell type is determined through comparisons with descriptions using other methods from larger insect species.

Strengths:

The data show that, despite the small size, many elements of the eye are consistent with those found in larger insects. In addition, the powerful FIB-SEM technique revealed a hitherto unknown case of ectopic photoreceptors.

Weaknesses:

As this paper only uses anatomical analyses, no functional interpretations of cell function are tested.

The aim of this paper was to describe the ultrastructural organization of compound eyes in the extremely small wasp Megaphragma viggianii. The authors successfully achieved this aim and provided an incredibly detailed description of all cell types with respect to their location, volume, and dimensions. As this is the first of its kind, the results cannot easily be compared with previous work. The findings are likely to be an important reference for future work that uses similar techniques to reconstruct the eyes of other insect species. The FIB-SEM method used is being used increasingly often in structural studies of insect sensory organs and brains and this work demonstrates the utility of this method.

Reviewer #2 (Public review):

Summary:

Makarova et al. provide the first complete cellular-level reconstruction of an insect eye. They use the extremely miniaturized parasitoid wasp, Megaphragma viggiani, and apply improved and optimized volumetric EM methods they can describe, the size, volume, and position of every single cell in the insect compound eye.

This data has previously only been inferred from TEM cross-sections taken in different parts of the eye, but in this study and in the associated 3d datasets video and stacks, one can observe the exact position and orientation in 3D space.

The authors have made a very rigorous effort to describe and assess the variation in each cell type and have also compared two different classes of the dorsal rim and non-dorsal rim ommatidia and the associated visual apparatus for each, confirming previous known findings about the distribution and internal structure that assists in polarization detection in these insects.

Strengths:

The paper is well written and strives to compare the data with previous literature wherever possible and goes beyond cell morphology, calculating the optical properties of the different ommatidia and estimating light sensitivity and spatial resolution limits using rhabdom diameter, focal length and showing how this varies across the eye.

Finally, the authors provide very informative and illustrative videos showing how the cones, lenses, photoreceptors, pigment cells, and even the mitochondria are arranged in 3D space, comparing the structure of the dorsal rim and non-dorsal rim ommatidia. They also describe three 'ectopic' photoreceptors in more anatomical detail providing images and videos of them.

Reviewer #3 (Public review):

Summary:

The article presents a meticulous and quantitative anatomical reconstruction of the compound eye of a tiny wasp at the level of subcellular structures, and cellular and optical organization of the ommatidia and reveals the ectopic photoreceptors, which are decoupled from the eye's dioptrical apparatus.

Strengths:

The graphic material is of very high quality, beautifully organized, and presented in a logical order. The anatomical analysis is fully supported by quantitative numerical data at all scales, from organelles to cells and ommatidia, which should be a valuable source for future studies in cellular biology and visual physiology. The 3D renders are highly informative and a real eye candy.

Weaknesses:

The claim that the large dorsal part of the eye is the dorsal rim area (DRA), supported by anatomical data on rhabdomere geometry and connectomics in authors' earlier work, would eventually greatly benefit from additional evidence, obtained by immunocytochemical staining, that could also reveal a putative substrate for colour vision. The cell nuclei that are located in the optical path in the DRA crystalline cone have only a putative optical function, which may be either similar to pore canals in hymenopteran DRA cornea (scattering) or to photoreceptor nuclei in camera-type eyes (focussing), both explanations being mutually exclusive.

Reviewer #1 (Public review):

Summary:

Mallimadugula et al. combined Molecular Dynamics (MD) simulations, thiol-labeling experiments, and RNA-binding assays to study and compare the RNA-binding behavior of the Interferon Inhibitory Domain (IID) from Viral Protein 35 (VP35) of Zaire ebolavirus, Reston ebolavirus, and Marburg marburgvirus. Although the structures and sequences of these viruses are similar, the authors suggest that differences in RNA binding stem from variations in their intrinsic dynamics, particularly the opening of a cryptic pocket. More precisely, the dynamics of this pocket may influence whether the IID binds to RNA blunt ends or the RNA backbone.

Overall, the authors present important findings to reveal how the intrinsic dynamics of proteins can influence their binding to molecules and, hence, their functions. They have used extensive biased simulations to characterize the opening of a pocket which was not clearly seen in experimental results - at least when the proteins were in their unbound forms. Biochemical assays further validated theoretical results and linked them to RNA binding modes. Thus, with the combination of biochemical assays and state-of-the-art Molecular Dynamics simulations, these results are clearly compelling.

Strengths:

The use of extensive Adaptive Sampling combined with biochemical assays clearly points to the opening of the Interferon Inhibitory Domain (IID) as a factor for RNA binding. This type of approach is especially useful to assess how protein dynamics can affect its function.

Weaknesses :

Although a connection between the cryptic pocket dynamics and RNA binding mode is proposed, the precise molecular mechanism linking pocket opening to RNA binding still remains unclear.

Reviewer #2 (Public review):

Summary:

The authors aimed to determine whether a cryptic pocket in the VP35 protein of Zaire ebolavirus has a functional role in RNA binding and, by extension, in immune evasion. They sought to address whether this pocket could be an effective therapeutic target resistant to evolutionary evasion by studying its role in dsRNA binding among different filovirus VP35 homologs. Through simulations and experiments, they demonstrated that cryptic pocket dynamics modulate the RNA binding modes, directly influencing how VP35 variants block RIG-I and MDA5-mediated immune responses.

The authors successfully achieved their aim, showing that the cryptic pocket is not a random structural feature but rather an allosteric regulator of dsRNA binding. Their results not only explain functional differences in VP35 homologs despite their structural similarity but also suggest that targeting this cryptic pocket may offer a viable strategy for drug development with reduced risk of resistance.

This work represents a significant advance in the field of viral immunoevasion and therapeutic targeting of traditionally "undruggable" protein features. By demonstrating the functional relevance of cryptic pockets, the study challenges long-standing assumptions and provides a compelling basis for exploring new drug discovery strategies targeting these previously overlooked regions.

Strengths:

The combination of molecular simulations and experimental approaches is a major strength, enabling the authors to connect structural dynamics with functional outcomes. The use of homologous VP35 proteins from different filoviruses strengthens the study's generality, and the incorporation of point mutations adds mechanistic depth. Furthermore, the ability to reconcile functional differences that could not be explained by crystal structures alone highlights the utility of dynamic studies in uncovering hidden allosteric features.

Weaknesses:

While the methodology is robust, certain limitations should be acknowledged. For example, the study would benefit from a more detailed quantitative analysis of how specific mutations impact RNA binding and cryptic pocket dynamics, as this could provide greater mechanistic insight. This study would also benefit from providing a clear rationale for the selection of the amber03 force field and considering the inclusion of volume-based approaches for pocket analysis. Such revisions will strengthen the robustness and impact of the study.

Reviewer #3 (Public review):

Summary:

The authors suggest a mechanism that explains the preference of viral protein 35 (VP35) homologs to bind the backbone of double-stranded RNA versus blunt ends. These preferences have a biological impact in terms of the ability of different viruses to escape the immune response of the host.<br /> The proposed mechanism involves the existence of a cryptic pocket, where VP35 binds the blunt ends of dsRNA when the cryptic pocket is closed and preferentially binds the RNA double-stranded backbone when the pocket is open.<br /> The authors performed MD simulation results, thiol labelling experiments, fluorescence polarization assays, as well as point mutations to support their hypothesis.

Strengths:

This is a genuinely interesting scientific question, which is approached through multiple complementary experiments as well as extensive MD simulations. Moreover, structural biology studies focused on RNA-protein interactions are particularly rare, highlighting the importance of further research in this area.

Weaknesses:

- Sequence similarity between Ebola-Zaire (94% similarity) explains their similar behaviour in simulations and experimental assays. Marburg instead is a more distant homolog (~80% similarity relative to Ebola/Zaire). This difference is sequence and structure can explain the propensities, without the need to involve the existence of a cryptic pocket.<br /> - No real evidence for the presence of a cryptic pocket is presented, but rather a distance probability distribution between two residues obtained from extensive MD simulations. It would be interesting to characterise the modelled RNA-protein interface in more detail.

Reviewer #1 (Public review):

Summary:

In this manuscript, Pakula et al. explore the impact of reactive oxygen species (ROS) on neonatal cerebellar regeneration, providing evidence that ROS activates regeneration through Nestin-expressing progenitors (NEPs). Using scRNA-seq analysis of FACS-isolated NEPs, the authors characterize injury-induced changes, including an enrichment in ROS metabolic processes within the cerebellar microenvironment. Biochemical analyses confirm a rapid increase in ROS levels following irradiation, and forced catalase expression, which reduces ROS levels, and impairs external granule layer (EGL) replenishment post-injury.

Strengths:

Overall, the study robustly supports its main conclusion and provides valuable insights into ROS as a regenerative signal in the neonatal cerebellum.

Weaknesses:

Below are specific comments and concerns:

(1) The diversity of cell types recovered from scRNA-seq libraries of sorted Nes-CFP cells is unexpected, especially the inclusion of minor types such as microglia, meninges, and ependymal cells. The authors should validate whether Nes and CFP mRNAs are enriched in the sorted cells; if not, they should discuss the potential pitfalls in sampling bias or artifacts that may have affected the dataset, impacting interpretation.<br /> (2) The authors should de-emphasize that ROS signaling and related gene upregulation exclusively in gliogenic NEPs. Genes such as Cdkn1a, Phlda3, Ass1, and Bax are identified as differentially expressed in neurogenic NEPs and granule cell progenitors (GCPs), with Ass1 absent in GCPs. According to Table S4, gene ontology (GO) terms related to ROS metabolic processes are also enriched in gliogenic NEPs, neurogenic NEPs, and GCPs.<br /> (3) The authors need to justify the selection of only the anterior lobe for EGL replenishment and microglia quantification.<br /> (4) Figure 1K: The figure presents linkages between genes and GO terms as a network but does not depict a gene network. The terminology should be corrected accordingly.<br /> (5) Figure 1H and S2: The x-axis appears to display raw p-values rather than log10(p.value) as indicated. The x-axis should ideally show -log10(p.adjust), beginning at zero. The current format may misleadingly suggest that the ROS GO term has the lowest p-values.<br /> (6) Genes such as Ppara, Egln3, Foxo3, Jun, and Nos1ap were identified by bulk ATAC-seq based on proximity to peaks, not by scRNA-seq. Without additional expression data, caution is needed when presenting these genes as direct evidence of ROS involvement in NEPs.<br /> (7) The authors should annotate cell identities for the different clusters in Table S2.<br /> (8) Reiterative clustering analysis reveals distinct subpopulations among gliogenic and neurogenic NEPs. Could the authors clarify the identities of these subclusters? Can we distinguish the gliogenic NEPs in the Bergmann glia layer from those in the white matter?<br /> (9) In the Methods section, the authors mention filtering out genes with fewer than 10 counts. They should specify if these genes were used as background for enrichment analysis. Background gene selection is critical, as it influences the functional enrichment of gene sets in the list.<br /> (10) Figure S1C: The authors could consider using bar plots to better illustrate cell composition differences across conditions and replicates.<br /> (11) Figures 4-6: It remains unclear how the white matter microglia contribute to the recruitment of BgL-NEPs to the EGL, as the mCAT-mediated microglia loss data are all confined to the white matter.

Reviewer #2 (Public review):

Summary:

The authors have previously shown that the mouse neonatal cerebellum can regenerate damage to granule cell progenitors in the external granular layer, through reprogramming of gliogenic nestin-expressing progenitors (NEPs). The mechanisms of this reprogramming remain largely unknown. Here the authors used scRNAseq and ATACseq of purified neonatal NEPs from P1-P5 and showed that ROS signatures were transiently upregulated in gliogenic NEPs ve neurogenic NEPs 24 hours post injury (P2). To assess the role of ROS, mice transgenic for global catalase activity were assessed to reduce ROS. Inhibition of ROS significantly decreased gliogenic NEP reprogramming and diminished cerebellar growth post-injury. Further, inhibition of microglia across this same time period prevented one of the first steps of repair - the migration of NEPs into the external granule layer. This work is the first demonstration that the tissue microenvironment of the damaged neonatal cerebellum is a major regulator of neonatal cerebellar regeneration. Increased ROS is seen in other CNS damage models including adults, thus there may be some shared mechanisms across age and regions, although interestingly neonatal cerebellar astrocytes do not upregulate GFAP as seen in adult CNS damage models. Another intriguing finding is that global inhibition of ROS did not alter normal cerebellar development.

Strengths:

This paper presents a beautiful example of using single cell data to generate biologically relevant, testable hypotheses of mechanisms driving important biological processes. The scRNAseq and ATACseq analyses are rigorously conducted and conclusive. Data is very clearly presented and easily interpreted supporting the hypothesis next tested by reduce ROS in irradiated brains.

Analysis of whole tissue and FAC sorted NEPS in transgenic mice where human catalase was globally expressed in mitochondria were rigorously controlled and conclusively show that ROS upregulation was indeed decreased post injury and very clearly the regenerative response was inhibited. The authors are to be commended on the very careful analyses which are very well presented and again, easy to follow with all appropriate data shown to support their conclusions.

Weaknesses:

The authors also present data to show that microglia are required for an early step of mobilizing gliogenic NEPs into the damaged EGL. While the data that PLX5622 administration from P0-P5 or even P0-P8 clearly shows that there is an immediate reduction of NEPs mobilized to the damaged EGL, there is no subsequent reduction of cerebellar growth such that by P30, the treated and untreated irradiated cerebella are equivalent in size. There is speculation in the discussion about why this might be the case, but there is no explanation for why further, longer treatment was not attempted nor was there any additional analyses of other regenerative steps in the treated animals. The data still implicate microglia in the neonatal regenerative response, but how remains uncertain.

Reviewer #1 (Public review):

Summary:

This manuscript investigates genes that escape X-Chromosome Inactivation (XCI) across human tissues, using females that exhibit skewed or non-random XCI. The authors identified 2 female individuals with skewed XCI in the GTex database, in addition to the 1 female skewed sample in this database that has been described in a previous publication (Ref.16). The authors also determined the genes that escape XCI for 380 X-linked genes across 30 different tissues.

Strengths:

The novelty of this manuscript is that the authors have identified the XCI expression status for a total of 380 genes across 30 different human tissues, and also discovered the XCI status (escape, variable escape, or silenced) for 198 X-linked genes, whose status was previously not determined. This report is a good resource for the field of XCI, and would benefit from additional analyses and clarification of their comparisons of XCI status.

Weaknesses:

Specific comments:

(1) The authors state that they have reclassified the allelic expression status of 32 genes (shown in Table S5, Supplementary Figure 3). The concern is the source of the tissue or cell line which was originally used to make the classification of XCI status, and whether the comparisons are equivalent. For example, if cell lines (and not tissues) were used to define the XCI status for EGFL6, TSPAN6, and CXorf38, then how can the authors be sure that the escape status in whole tissues would be the same? Also along these lines, the authors should consider whether escape status in previous studies using immortalized/cancer cell lines (such as the meta analyses done in Balaton publication) would be different compared to healthy tissues (seems like it should be). Therefore making comparisons between healthy whole tissues and cancer cell lines doesn't make sense.

(2) The authors note that skewed XCI is prevalent in the human population, and cite some publications (references 8, 10-12). If RNAseq data is available from these female individuals with skewed XCI (such as ref 12), the authors should consider using their allelic expression pipeline to identify XCI status of more X-linked genes.

(3) It has been well established that the human inactive X has more XCI escape genes compared to the mouse inactive X. In light of the author's observations across human tissues, how does the XCI status compare with the same tissues in mice?

Reviewer #2 (Public review):

Summary:

Gylemo et al. present a manuscript focused on identifying the X-inactivation or X-inactivation escape status for 380 genes across 30 normal human tissues. X-inactivation status of X-linked genes across tissues is important for understanding sex-specific differences in X-linked gene expression and therefore traits, and the likely effect of X-linked pathogenic variants in females. These new data are significant as they double the number of genes that have been classified in the human, and double the number of tissues studied previously.

Strengths:

The strengths of this work are that they analyse 3 individuals from the GTex dataset (2 newly identified, 1 previously identified and published) that have highly/ completely skewed X inactivation, which allows the study of escape from X inactivation in bulk RNA-sequencing. The number of individuals and breadth of tissues analysed add significantly to both the number of genes that have been classified and the weight of evidence for their claims. The additional 198 genes that have been classified and the reclassification of genes that previously had only limited support for their status is useful for the field.

In analysing the data they find that tissue-specific escape from X inactivation appears relatively rare. Rather, if genes escape, even variably, it tends to occur across tissues. Similarly, if a gene is inactivated, it is stable across tissues.

Weaknesses:

In my view there are only minor weaknesses in this work, that tend to come about due to the requirement to study individuals with highly skewed X inactivation. I wonder whether the cause of the highly skewed X inactivation may somehow influence the likelihood of observing tissue-specific escape from X inactivation. In this light, it would be interesting to further understand the genetic cause for the highly skewed X inactivation in each of these three cases in the whole exome sequencing data. Future additional studies may validate these findings using single-cell approaches in unrelated individuals across tissues, where there is normal X inactivation.

Reviewer #3 (Public review):

Summary:

Nestor and colleagues identify genes escaping X chromosome inactivation (XCI) in rare individuals with non-mosaic XCI (nmXCI) whose tissue-specific RNA-seq datasets were obtained from the GTEX database. Because XCI is non-mosaic, read counts representing a second allele are tested for statistically significant escape, in this case > 2.5% of active X expression. Whereas a prior GTEX analysis found only one nmXCI female, this study finds two additional donors in GTEX, therefore expanding the number of assessed X-linked genes to 380. Although this is fewer than half of X-linked genes, the study demonstrates that although rare, nmXCI females are represented in RNA-seq databases such as GTEX. Therefore this analytical approach is worthwhile pursuing in other (larger) databases as well, to provide deeper insight into escape from XCI which is relevant to X-linked diseases and sex differences.

Strengths:

The analysis is well-documented, straightforward, and valuable. The supplementary tables are useful, and the claims in the main text well-supported.

Weaknesses:

There are very few, except that this escape catalogue is limited to 3 donors, based on a single (representative) tissue screen in 285 female donors, mostly using muscle samples. However, if only pituitary samples had been screened, nmXCI-1 would have been missed. Additional donors in the 285 representative samples cross a lower threshold of AE = 0.4. It would be worthwhile to query all tissues of the 285 donors to discover more nmXCI cases, as currently fewer than half of X-linked genes received a call using this very worthwhile approach.

Reviewer #1 (Public review):

Summary<br /> In this beautiful paper the authors examined the role and function of NR2F2 in testis development and more specifically on fetal Leydig cells development. It is well known by now that FLC are developed from an interstitial steroidogenic progenitors at around E12.5 and are crucial for testosterone and INSL3 production during embryonic development, which in turn shapes the internal and external genitalia of the male. Indeed, lack of testosterone or INSL3 are known to cause DSD as well as undescended testis, also termed as cryptorchidism.<br /> The authors first characterized the expression pattern of the NR2R2 protein during testis development and then used two cKO systems of NR2F2, namely the Wt1-creERT2 and the Nr5a1-cre to explore the phenotype of loss of NR2F2. They found in both cases that mice are presenting with undescended testis and major reduction in FLC numbers. They show that NR2F2 has no effect on the amount and expression of the progenitor cells but in its absence, there are less FLC and they are immature.<br /> The effect of NR2F2 is cell autonomous and does not seem to affect other signalling pathways implemented in Leydig cell development as the DHH, PDGFRA and the NOTCH pathway.

Overall, this paper is excellent, very well written, fluent and clear. The data is well presented, and all the controls and statistics are in place. I think this paper will be of great interest to the field and paves the way for several interesting follow up studies as stated in the discussion

Reviewer #2 (Public review):

The major conclusion of the manuscript is expressed in the title: "NR2F2 is required in the embryonic testis for Fetal Leydig Cell development" and also at the end of the introduction and all along the result part. All the authors' assertions are supported by very clear and statistically validated results from ISH, IHC, precise cell counting and gene expression levels by qPCR. The authors used two different conditional Nr2f2 gene ablation systems that demonstrate the same effects at the FLC level. They also showed that the haplo-insufficiency of Wt1 in the first system (knock-in Wt1-cre-ERT2) aggravated the situation in FLC differentiation by disturbing the differentiation of Sertoli cells and their secretion of pro-FLC factors, which had a confounding effect and encouraged them to use the second system. This demonstrates the great rigor with which the authors interpreted the results. In conclusion, all authors' claims and conclusions are justified by their high-quality results.

Reviewer #1 (Public review):

Summary:

This study examines the role of host blood meal source, temperature, and photoperiod on the reproductive traits of Cx. quinquefasciatus, an important vector of numerous pathogens of medical importance. The host use pattern of Cx. quinquefasciatus is interesting in that it feeds on birds during spring and shifts to feeding on mammals towards fall. Various hypotheses have been proposed to explain the seasonal shift in host use in this species but have provided limited evidence. This study examines whether the shifting of host classes from birds to mammals towards autumn offers any reproductive advantages to Cx. quinquefasciatus in terms of enhanced fecundity, fertility, and hatchability of the offspring. The authors found no evidence of this, suggesting that alternate mechanisms may drive the seasonal shift in host use in Cx. quinquefasciatus.

Strengths:

Host blood meal source, temperature, and photoperiod were all examined together.

Weaknesses:

The study was conducted in laboratory conditions with a local population of Cx. quinquefasciatus from Argentina. I'm not sure if there is any evidence for a seasonal shift in the host use pattern in Cx. quinquefasciatus populations from the southern latitudes.

Comments on the revision:

Overall, the manuscript is much improved. However, the introduction and parts of the discussion that talk about addressing the question of seasonal shift in host use pattern of Cx. quin are still way too strong and must be toned down. There is no strong evidence to show this host shift in Argentinian mosquito populations. Therefore, it is just misleading. I suggest removing all this and sticking to discussing only the effects of blood meal source and seasonality on the reproductive outcomes of Cx. quin.

Reviewer #2 (Public review):

Summary:

Conceptually, this study is interesting and is the first attempt to account for the potentially interactive effects of seasonality and blood source on mosquito fitness, which the authors frame as a possible explanation for previously observed host-switching of Culex quinquefasciatus from birds to mammals in the fall. The authors hypothesize that if changes in fitness by blood source change between seasons, higher fitness on birds in the summer and on mammals in the autumn could drive observed host switching. To test this, the authors fed individuals from a colony of Cx. quinquefasciatus on chickens (bird model) and mice (mammal model) and subjected each of these two groups to two different environmental conditions reflecting the high and low temperatures and photoperiod experienced in summer and autumn in Córdoba, Argentina (aka seasonality). They measured fecundity, fertility, and hatchability over two gonotrophic cycles. The authors then used generalized linear mixed models to evaluate the impact of host species, seasonality, and gonotrophic cycle on fecundity, fertility, and hatchability. The authors were trying to test their hypothesis by determining whether there was an interactive effect of season and host species on mosquito fitness. This is an interesting hypothesis; if it had been supported, it would provide support for a new mechanism driving host switching. While the authors did report an interactive impact of seasonality and host species, the directionality of the effect was the opposite from that hypothesized. The authors have done a very good job of addressing many of the reviewer's concerns, especially by adding two additional replicates. Several minor concerns remain, especially regarding unclear statements in the discussion.

Strengths:

(1) Using a combination of laboratory feedings and incubators to simulate seasonal environmental conditions is a good, controlled way to assess the potentially interactive impact of host species and seasonality on the fitness of Culex quinquefasciatus in the lab.<br /> (2) The driving hypothesis is an interesting and creative way to think about a potential driver of host switching observed in the field.

Weaknesses:

(1) The methods would be improved by some additional details. For example, clarifying the number of generations for which mosquitoes were maintained in colony (which was changed from 20 to several) and whether replicates were conducted at different time points.<br /> (2) The statistical analysis requires some additional explanation. For example, you suggest that the power analysis was conducted a priori, but this was not mentioned in your first two drafts, so I wonder if it was actually conducted after the first replicate. It would be helpful to include further detail, such as how the parameters were estimated. Also, it would be helpful to clarify why replicate was included as a random effect for fecundity and fertility but as a fixed effect for hatchability. This might explain why there were no significant differences for hatchability given that you were estimating for more parameters.<br /> (3) A number of statements in the discussion are not clear. For example, what do you mean by a mixed perspective in the first paragraph? Also, why is the expectation mentioned in the second paragraph different from the hypothesis you described in your introduction?<br /> (4) According to eLife policy, data must be made freely available (not just upon request).

Reviewer #1 (Public review):

The aim of this paper is to describe a novel method for genetic labelling of animals or cell populations, using a system of DNA/RNA barcodes.

Strengths:

• The author's attempt at providing a straightforward method for multiplexing Drosophila samples prior to scRNA-seq is commendable. The perspective of being able to load multiple samples on a 10X Chromium without antibody labelling is appealing.<br /> • The authors are generally honest about potential issues in their method, and areas that would benefit from future improvement.<br /> • The article reads well. Graphs and figures are clear and easy to understand.

Weaknesses:

• The usefulness of TaG-EM for phototaxis, egg laying or fecundity experiments is questionable. The behaviours presented here are all easily quantifiable, either manually or using automated image-based quantification, even when they include a relatively large number of groups and replicates. Despite their claims (e.g., L311-313), the authors do not present any real evidence about the cost- or time-effectiveness of their method in comparison to existing quantification methods.<br /> • Behavioural assays presented in this article have clear outcomes, with large effect sizes, and therefore do not really challenge the efficiency of TaG-EM. By showing a T-maze in Fig 1B, the authors suggest that their method could be used to quantify more complex behaviours. Not exploring this possibility in this manuscript seems like a missed opportunity.<br /> • Experiments in Figs S3 and S6 suggest that some tags have a detrimental effect on certain behaviours or on GFP expression. Whereas the authors rightly acknowledge these issues, they do not investigate their causes. Unfortunately, this question the overall suitability of TaG-EM, as other barcodes may also affect certain aspects of the animal's physiology or behaviour. Revising barcode design will be crucial to make sure that sequences with potential regulatory function are excluded.<br /> • For their single-cell experiments, the authors have used the 10X Genomics method, which relies on sequencing just a short segment of each transcript (usually 50-250bp - unknown for this study as read length information was not provided) to enable its identification, with the matching paired-end read providing cell barcode and UMI information (Macosko et al., 2015). With average fragment length after tagmentation usually ranging from 300-700bp, a large number of GFP reads will likely not include the 14bp TaG-EM barcode. When a given cell barcode is not associated with any TaG-EM barcode, then demultiplexing is impossible. This is a major problem, which is particularly visible in Figs 5 and S13. In 5F, BC4 is only detected in a couple of dozen cells, even though the Jon99Ciii marker of enterocytes is present in a much larger population (Fig 5C). Therefore, in this particular case, TaG-EM fails to detect most of the GFP-expressing cells. Similarly, in S13, most cells should express one of the four barcodes, however many of them (maybe up to half - this should be quantified) do not. Therefore, the claim (L277-278) that "the pan-midgut driver were broadly distributed across the cell clusters" is misleading. Moreover, the hypothesis that "low expressing driver lines may result in particularly sparse labelling" (L331-333) is at least partially wrong, as Fig S13 shows that the same Gal4 driver can lead to very different levels of barcode coverage.<br /> • Comparisons between TaG-EM and other, simpler methods for labelling individual cell populations are missing. For example, how would TaG-EM compare with expression of different fluorescent reporters, or a strategy based on the brainbow/flybow principle?<br /> • FACS data is missing throughout the paper. The authors should include data from their comparative flow cytometry experiment of TaG-EM cells with or without additional hexameric GFP, as well as FSC/SSC and fluorescence scatter plots for the FACS steps that they performed prior to scRNA-seq, at least in supplementary figures.<br /> • The authors should show the whole data described in L229, including the cluster that they chose to delete. At least, they should provide more information about how many cells were removed. In any case, the fact that their data still contains a large number of debris and dead cells despite sorting out PI negative cells with FACS and filtering low abundance barcodes with Cellranger is concerning.

Overall, although a method for genetic tagging cell populations prior to multiplexing in single-cell experiments would be extremely useful, the method presented here is inadequate. However, despite all the weaknesses listed above, the idea of barcodes expressed specifically in cells of interest deserves more consideration. If the authors manage to improve their design to resolve the major issues and demonstrate the benefits of their method more clearly, then TaG-EM could become an interesting option for certain applications.

Comments on revisions:

The authors have addressed many important points, providing reassurances about the initial weaknesses of their work. Although the TaG-EM is unlikely to have a significant influence on the field due to its limited benefits, the results are now sound and provide the reader with an unbiased view of the possibilities and limitations of the method.

Reviewer #2 (Public review):

The authors developed the TaG-EM system to address challenges in multiplexing Drosophila samples for behavioral and transcriptomic studies. This system integrates DNA barcodes upstream of the polyadenylation site in a UAS-GFP construct, enabling pooled behavioral measurements and cell type tracking in scRNA-seq experiments. The revised manuscript expands on the utility of TaG-EM by demonstrating its application to complex assays, such as larval gut motility, and provides a refined analysis of its limitations and cost-effectiveness.

Strengths

(1) Novelty and Scope: The study demonstrates the potential for TaG-EM to streamline multiplexing in both behavioral and transcriptomic contexts. The additional application to labor-intensive larval gut motility assays highlights its scalability and practical utility.

(2) Data Quality and Clarity: Figures and supplemental data are mostly clear and significantly enhanced in the revised manuscript. The addition of Supplemental Figures 18-21 addresses initial concerns about scRNA-seq data and driver characterization.

(3) Cost-Effectiveness Analysis: New analyses of labor and cost savings (e.g., Supplemental Figure 8) provide a practical perspective.

(4) Improvements in Barcode Detection and Analysis: Enhanced enrichment protocols (Supplemental Figures 18-19) demonstrate progress in addressing limitations of barcode detection and increase the detection rate of labeled cells.

Weaknesses

(1) Barcode Detection Efficiency: While improvements are noted, the low barcode detection rate (~37% in optimized conditions) limits the method's scalability in some applications, such as single-cell sequencing experiments with complex cell populations.

(2) Sparse Labeling: Sparse labeling of cell populations, particularly in scRNA-seq assays, remains a concern. Variability in driver strength and regional expression introduces inconsistencies in labeling density.

(3) Behavioral Applications: The utility of TaG-EM in quantifying more complex behaviors remains underexplored, limiting the generalizability of the method beyond simpler assays like phototaxis and oviposition.

(4) Driver Line Characterization: While improvements in driver line characterization were made, variability in expression patterns and sparse labeling emphasize the need for further refinement of constructs and systematic backcrossing to standardize the genetic background.

Reviewer #1 (Public review):

Summary:

BMP signaling is, arguably, best known for its role in the dorsoventral patterning, but not in nematodes, where it regulates body size. In their paper, Vora et al. analyze ChIP-Seq and RNA-Seq data to identify direct transcriptional targets of SMA-3 (Smad) and SMA-9 (Schnurri) and understand the respective roles of SMA-3 and SMA-9 in the nematode model Caenorhabditis elegans. The Authors use SMA-3 and SMA-9 ChIP-Seq data and RNA-Seq data from SMA-3 and SMA-9 mutants, and bioinformatic analyses to identify the genes directly controlled by these two transcription factors (TFs) and find approximately 350 such targets for each. They show that all SMA-3-controlled targets are positively controlled by SMA-3 binding, while SMA-9-controlled targets can be either up- or downregulated by SMA-9. 129 direct targets were shared by SMA-3 and SMA-9, and, curiously, the expression of 15 of them was activated by SMA-3 but repressed by SMA-9. In case of such opposing effects, the SMA-9 appears to act epistatically to SMA-3. Since genes responsible for cuticle collagen production were eminent among the SMA-3 targets, the Authors focused on trying to understand the body size defect known to be elicited by the modulation of BMP signaling. Vora et al. provide compelling evidence that this defect is likely to be due to problems with the BMP signaling-dependent collagen secretion necessary for cuticle formation.

Strengths:

Vora et al. provide a valuable analysis of ChIP-Seq and RNA-Seq datasets, which will be very useful for the community. They also shed light on the mechanism of the BMP-dependent body size control by identifying SMA-3 target genes regulating cuticle collagen synthesis and by showing that downregulation of these genes affects body size in C. elegans.

Weaknesses:

(1) Although the analysis of the SMA-3 and SMA-9 ChIP-Seq and RNA-Seq data is extremely useful, the goal "to untangle the roles of Smad and Schnurri transcription factors in the developing C. elegans larva", has not been reached. While the role of SMA-3 as a transcriptional activator appears to be quite straightforward, the function of SMA-9 in the BMP signaling remains obscure.

(2) The Authors clearly show that both TFs can bind independently of each other, however, by using distances between SMA-3 and SMA-9 ChIP peaks, they claim that when the peaks are close these two TFs likely act as complexes. In the absence of proof that SMA-3 and SMA-9 physically interact (e.g. that they co-immunoprecipitate - as they do in Drosophila), this is an unfounded claim, which still has to be experimentally substantiated. In the revised version of the manuscript, the authors acknowledge this.

(3) The second part of the results (the collagen story) is loosely connected the first part. dpy-11 encodes an enzyme important for cuticle development, and it is a differentially expressed direct target of SMA-3. dpy-11 can be bound by SMA-9, but it is not affected by this binding according to RNA-Seq. Thus, technically, this part of the paper does not require any information about SMA-9. However, this can likely be improved by addressing the function of the 15 genes, with the opposing mode of regulation by SMA-3 and SMA-9.

Comments on revisions:

In comparison to the first version of the manuscript, the authors have significantly improved the "readability" of the paper, made the Discussion much better, and toned down some of the less supported arguments.

Reviewer #1 (Public review):

Summary:

The study aims to create a comprehensive repository about the changes in protein abundance and their modification during oocyte maturation in Xenopus laevis.

Strengths:

The results contribute meaningfully to the field.

Weaknesses:

The manuscript could have benefitted from more comprehensive analyses and clearer writing. Nonetheless, the key findings are robust and offer a valuable resource for the scientific community.

Reviewer #2 (Public review):

Summary:

The authors analyzed Xenopus oocytes at different stages of meiosis using quantitative phosphoproteomics. Their advanced methods and analyses revealed changes in protein abundances and phosphorylation states to an unprecedented depth and quantitative detail. In the manuscript they provide an excellent interpretation of these findings putting them in the context of past literature in Xenopus as well as in other model systems.

Strengths:

High quality data, careful and detailed analysis, outstanding interpretation in the context of the large body of the literature.

Weaknesses:

Merely a resource, none of the findings are tested in functional experiments.

I am very impressed by the quality of the data and the careful and detailed interpretation of the findings. In this form the manuscript will be an excellent resource to the cell division community in general, and it presents a very large number of hypotheses that can be tested in future experiments.

Xenopus has been and still is a popular and powerful model system that led to critical discoveries around countless cellular processes, including the spindle, nuclear envelope, translational regulation, just to name a few. This also includes a huge body of literature on the cell cycle describing its phosphoregulation. It is indeed somewhat frustrating to see that these earlier studies using phospho-mutants and phospho-antibodies were just scratching the surface. The phosphoproteomics analysis presented here reveals much more extensive and much more dynamic changes in phosphorylation states. Thereby, in my opinion, this manuscript opens a completely new chapter in this line of research, setting the stage for more systematic future studies.

Reviewer #3 (Public review):

Summary:

The authors performed time-resolved proteomics and phospho-proteomics in Xenopus oocytes from prophase I through the MII arrest of the unfertilized egg. The data contains protein abundance and phosphorylation sites of a large number set of proteins at different stages of oocyte maturation. The large sets of the data are of high quality. In addition, the authors discussed several key pathways critical for the maturation. The data is very useful for the researchers not only researchers in Xenopus oocytes but also those in oocyte biology in other organisms.

Strengths:

The data of proteomics and phospho-proteomics in Xenopus oocyte maturation is very useful for future studies to understand molecular networks in oocyte maturation.

Weaknesses:

Although the authors offered molecular pathways of the phosphorylation in the translation, protein degradation, cell cycle regulation, and chromosome segregation. The author did not check the validity of the molecular pathways based ontheir proteomic data by the experimentation.

Reviewer #1 (Public review):

Summary:

In this article, Gupta and colleagues explore the parameters that could promote the elimination of active Ras cells when surrounded by WT cells. The elimination of active Ras cells by surrounding WT cells was previously described extensively and associated with a process named cell competition, a context dependant elimination of cells. Several mechanisms have been associated with competition, including more recently elimination processes based on mechanical stress. This was explored theoretically and experimentally and was either associated with differential growth and sensitivity to pressure and/or differences in homeostatic density/pressure. This was extensively validated for the case of Scribble mutant cells which are eliminated by WT MDCK cells due to their higher homeostatic density. However, there has been so far very little systematic characterisation of the mechanical parameters and properties of these different cell types and how this could contribute to mechanical competition.

Here, the authors used the context of active Ras cells in MDCK cells (with some observations in vivo in mice gut which are a bit more anecdotal) to explore the parameters causal to Ras cell elimination. Using for the first time traction force microscopy, stress microscopy combined with Bayesian inference, they first show that clusters of active Ras cells experience higher pressure compared to WT. Interestingly, this occurs in absence of differences in growth rate, and while Ras cells seems to have lower homeostatic density, in contractions with the previous models associated with mechanical cell competition. Using a self-propelled Voronoi model, they explored more systematically the conditions that will promote the compression of transformed cells, showing globally that higher Area compressibility and/or lower junctional tension are associated with higher compressibility. Using then an original and novel experimental method to measure bulk compressibility of cell populations, they confirmed that active Ras cells are globally twice more compressible than WT cells. This compressibility correlates with a disruption of adherens junctions. Accordingly, the higher pressure near transformed Ras cells can be completely rescued by increasing cell-cell adhesion through E-cad overexpression, which also reduces the compressibility of the transformed cells. Altogether, these results go along the lines of a previous theoretical work (Gradeci et al. eLife 2021) which was suggesting that reduced stiffness/higher compressibility was essential to promote loser cell elimination. Here, the authors provide for the first time a very convincing experimental measurement and validation of this prediction. Moreover, their modelling approach goes far beyond what was performed before in terms of exploration of conditions promoting compressibility, and their experimental data point at alternative mechanisms that may contribute to mechanical competition.

Strengths:

- Original methodologies to perform systematic characterisation of mechanical properties of Ras cells during cell competition, which include a novel method to measure bulk compressibility.<br /> - A very extensive theoretical exploration of the parameters promoting cell compaction in the context of competition.

Weaknesses:

- Most of the theoretical focus is centred on the bulk compressibility, but so far does not really explain the final fate of the transformed cells. Classic cell competition scenario (including the one involving active Ras cells) lead to the elimination of one cell population either by cell extrusion/cell death or global delamination. This aspect is absolutely not explored in this article, experimentally or theoretically, and as such it is difficult to connect all the observables with the final outcome of cell competition. For instance, higher compressibility may not lead to loser status if the cells can withstand high density without extruding compared to the WT cells (and could even completely invert the final outcome of the competition). Down the line, and as suggested in most of the previous models/experiments, the relationship between pressure/density and extrusion/death will be the key factor that determine the final outcome of competition. However, there is absolutely no characterisation of cell death/cell extrusion in the article so far.

- While the compressibility measurement are very original and interesting, this bulk measurement could be explained by very different cellular processes, from modulation of cell shape, to cell extrusion and tissue multilayering (which by the way was already observed for active Ras cells, see for instance https://pubmed.ncbi.nlm.nih.gov/34644109/). This could change a lot the interpretation of this measurement and to which extend it can explain the compression observed in mixed culture. This compressibility measurement could be much more informative if coupled with an estimation of the change of cell aspect ratio and the rough evaluation of the contribution of cell shape changes versus alternative mechanisms.

- So far, there is no clear explanation of why transformed Ras cells get more compacted in the context of mixed culture compared to pure Ras culture. Previously, the compaction of mutant Scribble cells could be explained by the higher homeostatic density of WT cells which impose their prefered higher density to Scribble mutant (see Wagstaff et al. 2016 or Gradeci et al 2021), however that is not the case of the Ras cells (which have even slightly higher density at confluency). If I understood properly, the Voronoid model assumes some directional movement of WT cell toward transformed which will actively compact the Ras cells through self-propelled forces (see supplementary methods), but this is never clearly discussed/described in the results section, while potentially being one essential ingredient for observing compaction of transformed cells. In fact, this was already described experimentally in the case of Scribble competition and associated with chemoattractant secretion from the mutant cells promoting directed migration of the WT (https://pubmed.ncbi.nlm.nih.gov/33357449/). It would be essential to show what happens in absence of directional propelled movement in the model and validate experimentally whether there is indeed directional movement of the WT toward the transformed cells. Without this, the current data does not really explain the competition process.

- Some of the data lack a bit of information on statistic, especially for all the stress microscopy and traction forces where we do no really know how representative at the stress patterns (how many experiment, are they average of several movies ? integrated on which temporal window ?)

Reviewer #2 (Public review):

The work by Gupta et al. addresses the role of tissue compressibility as a driver of cell competition. The authors use a planar epithelial monolayer system to study cell competition between wild type and transformed epithelial cells expressing HRasV12. They combine imaging and traction force measurements from which the authors propose that wild type cells generate compressive forces on transformed epithelial cells. The authors further present a novel setup to directly measure the compressibility of adherent epithelial tissues. These measurements suggest a higher compressibility of transformed epithelial cells, which is causally linked to a reduction in cell-cell adhesion in transformed cells. The authors support their conclusions by theoretical modelling using a self-Propelled Voronoi model that supports differences in tissue compressibility can lead to compression of the softer tissue type.

The experimental framework to measure tissue compressibility of adherent epithelial monolayers establishes a novel tool, however additional controls of this measurement appear required. Moreover, the experimental support of this study is mostly based on single representative images and would greatly benefit from additional data and their quantitative analysis to support the authors' conclusions. Specific comments are also listed in the following:

Major points:

It is not evident in Fig2A that traction forces increase along the interface between wild type and transformed populations and stresses in Fig2C also seem to be similar at the interface and surrounding cell layer. Only representative examples are provided and a quantification of sigma_m needs to be provided.

In Figure 1-3 only panel 2G and 2H provide a quantitative analysis, but it is not clear how many regions of interest and clusters of transform cells were quantified.

Several statements appear to be not sufficiently justified and supported by data.<br /> For example the statement on pg 3. line 38 seems to lack supportive data 'This comparison revealed that the thickness of HRasV12-expressing cells was reduced by more than 1.7-fold when they were surrounded by wild type cells. These observations pointed towards a selective, competition-dependent compaction of HRasV12-expressing transformed cells but not control cells, in the intestinal villi of mice.'<br /> Similarly, the statement about a cell area change of 2.7 fold (pg 3 line 47) lacks support by measurements.

What is the rationale for setting 𝐾p = 1 in the model assumptions if clear differences in junctional membranes of transformed versus wild type cells occur, including dynamic ruffling? This assumption does not seem to be in line with biological observations.

The novel approach to measure tissue compressibility is based on pH dependent hydrogels. As the pH responsive hydrogel pillar is placed into a culture medium with different conditions, an important control would be if the insertion of this hydrogel itself would change the pH or conditions of the culture assays and whether this alters tissue compressibility or cell adhesion. The authors could for example insert a hydrogel pillar of a smaller diameter that would not lead to compression or culture cells in a larger ring to assess the influence of the pillar itself.

The authors focus on the study of cell compaction of the transformed cells, but how does this ultimately lead to a competitive benefit of wild type cells? Is a higher rate of extrusion observed and associated with the compaction of transformed cells or is their cell death rate increased? While transformed cells seem to maintain a proliferative advantage it is not clear which consequences of tissue compression ultimately drive cell competition between wild type and transformed cells.

The argumentation that softer tissues would be more easily compressed is plausible. However, which mechanism do the authors suggest is generating the actual compressive stress to drive the compaction of transformed cells? They exclude a proliferative advantage of wild type cells, which other mechanisms will generate the compressive forces by wild type cells?

Reviewer #1 (Public review):

Summary:

In this article, Gupta and colleagues explore the parameters that could promote the elimination of active Ras cells when surrounded by WT cells. The elimination of active Ras cells by surrounding WT cells was previously described extensively and associated with a process named cell competition, a context dependant elimination of cells. Several mechanisms have been associated with competition, including more recently elimination processes based on mechanical stress. This was explored theoretically and experimentally and was either associated with differential growth and sensitivity to pressure and/or differences in homeostatic density/pressure. This was extensively validated for the case of Scribble mutant cells which are eliminated by WT MDCK cells due to their higher homeostatic density. However, there has been so far very little systematic characterisation of the mechanical parameters and properties of these different cell types and how this could contribute to mechanical competition.

Here, the authors used the context of active Ras cells in MDCK cells (with some observations in vivo in mice gut which are a bit more anecdotal) to explore the parameters causal to Ras cell elimination. Using for the first time traction force microscopy, stress microscopy combined with Bayesian inference, they first show that clusters of active Ras cells experience higher pressure compared to WT. Interestingly, this occurs in absence of differences in growth rate, and while Ras cells seems to have lower homeostatic density, in contractions with the previous models associated with mechanical cell competition. Using a self-propelled Voronoi model, they explored more systematically the conditions that will promote the compression of transformed cells, showing globally that higher Area compressibility and/or lower junctional tension are associated with higher compressibility. Using then an original and novel experimental method to measure bulk compressibility of cell populations, they confirmed that active Ras cells are globally twice more compressible than WT cells. This compressibility correlates with a disruption of adherens junctions. Accordingly, the higher pressure near transformed Ras cells can be completely rescued by increasing cell-cell adhesion through E-cad overexpression, which also reduces the compressibility of the transformed cells. Altogether, these results go along the lines of a previous theoretical work (Gradeci et al. eLife 2021) which was suggesting that reduced stiffness/higher compressibility was essential to promote loser cell elimination. Here, the authors provide for the first time a very convincing experimental measurement and validation of this prediction. Moreover, their modelling approach goes far beyond what was performed before in terms of exploration of conditions promoting compressibility, and their experimental data point at alternative mechanisms that may contribute to mechanical competition.

Strengths:

- Original methodologies to perform systematic characterisation of mechanical properties of Ras cells during cell competition, which include a novel method to measure bulk compressibility.<br /> - A very extensive theoretical exploration of the parameters promoting cell compaction in the context of competition.

Weaknesses:

- Most of the theoretical focus is centred on the bulk compressibility, but so far does not really explain the final fate of the transformed cells. Classic cell competition scenario (including the one involving active Ras cells) lead to the elimination of one cell population either by cell extrusion/cell death or global delamination. This aspect is absolutely not explored in this article, experimentally or theoretically, and as such it is difficult to connect all the observables with the final outcome of cell competition. For instance, higher compressibility may not lead to loser status if the cells can withstand high density without extruding compared to the WT cells (and could even completely invert the final outcome of the competition). Down the line, and as suggested in most of the previous models/experiments, the relationship between pressure/density and extrusion/death will be the key factor that determine the final outcome of competition. However, there is absolutely no characterisation of cell death/cell extrusion in the article so far.

- While the compressibility measurement are very original and interesting, this bulk measurement could be explained by very different cellular processes, from modulation of cell shape, to cell extrusion and tissue multilayering (which by the way was already observed for active Ras cells, see for instance https://pubmed.ncbi.nlm.nih.gov/34644109/). This could change a lot the interpretation of this measurement and to which extend it can explain the compression observed in mixed culture. This compressibility measurement could be much more informative if coupled with an estimation of the change of cell aspect ratio and the rough evaluation of the contribution of cell shape changes versus alternative mechanisms.

- So far, there is no clear explanation of why transformed Ras cells get more compacted in the context of mixed culture compared to pure Ras culture. Previously, the compaction of mutant Scribble cells could be explained by the higher homeostatic density of WT cells which impose their prefered higher density to Scribble mutant (see Wagstaff et al. 2016 or Gradeci et al 2021), however that is not the case of the Ras cells (which have even slightly higher density at confluency). If I understood properly, the Voronoid model assumes some directional movement of WT cell toward transformed which will actively compact the Ras cells through self-propelled forces (see supplementary methods), but this is never clearly discussed/described in the results section, while potentially being one essential ingredient for observing compaction of transformed cells. In fact, this was already described experimentally in the case of Scribble competition and associated with chemoattractant secretion from the mutant cells promoting directed migration of the WT (https://pubmed.ncbi.nlm.nih.gov/33357449/). It would be essential to show what happens in absence of directional propelled movement in the model and validate experimentally whether there is indeed directional movement of the WT toward the transformed cells. Without this, the current data does not really explain the competition process.

- Some of the data lack a bit of information on statistic, especially for all the stress microscopy and traction forces where we do no really know how representative at the stress patterns (how many experiment, are they average of several movies ? integrated on which temporal window ?)

Reviewer #2 (Public review):

The work by Gupta et al. addresses the role of tissue compressibility as a driver of cell competition. The authors use a planar epithelial monolayer system to study cell competition between wild type and transformed epithelial cells expressing HRasV12. They combine imaging and traction force measurements from which the authors propose that wild type cells generate compressive forces on transformed epithelial cells. The authors further present a novel setup to directly measure the compressibility of adherent epithelial tissues. These measurements suggest a higher compressibility of transformed epithelial cells, which is causally linked to a reduction in cell-cell adhesion in transformed cells. The authors support their conclusions by theoretical modelling using a self-Propelled Voronoi model that supports differences in tissue compressibility can lead to compression of the softer tissue type.

The experimental framework to measure tissue compressibility of adherent epithelial monolayers establishes a novel tool, however additional controls of this measurement appear required. Moreover, the experimental support of this study is mostly based on single representative images and would greatly benefit from additional data and their quantitative analysis to support the authors' conclusions. Specific comments are also listed in the following:

Major points:

It is not evident in Fig2A that traction forces increase along the interface between wild type and transformed populations and stresses in Fig2C also seem to be similar at the interface and surrounding cell layer. Only representative examples are provided and a quantification of sigma_m needs to be provided.

In Figure 1-3 only panel 2G and 2H provide a quantitative analysis, but it is not clear how many regions of interest and clusters of transform cells were quantified.

Several statements appear to be not sufficiently justified and supported by data.<br /> For example the statement on pg 3. line 38 seems to lack supportive data 'This comparison revealed that the thickness of HRasV12-expressing cells was reduced by more than 1.7-fold when they were surrounded by wild type cells. These observations pointed towards a selective, competition-dependent compaction of HRasV12-expressing transformed cells but not control cells, in the intestinal villi of mice.'<br /> Similarly, the statement about a cell area change of 2.7 fold (pg 3 line 47) lacks support by measurements.

What is the rationale for setting 𝐾p = 1 in the model assumptions if clear differences in junctional membranes of transformed versus wild type cells occur, including dynamic ruffling? This assumption does not seem to be in line with biological observations.

The novel approach to measure tissue compressibility is based on pH dependent hydrogels. As the pH responsive hydrogel pillar is placed into a culture medium with different conditions, an important control would be if the insertion of this hydrogel itself would change the pH or conditions of the culture assays and whether this alters tissue compressibility or cell adhesion. The authors could for example insert a hydrogel pillar of a smaller diameter that would not lead to compression or culture cells in a larger ring to assess the influence of the pillar itself.

The authors focus on the study of cell compaction of the transformed cells, but how does this ultimately lead to a competitive benefit of wild type cells? Is a higher rate of extrusion observed and associated with the compaction of transformed cells or is their cell death rate increased? While transformed cells seem to maintain a proliferative advantage it is not clear which consequences of tissue compression ultimately drive cell competition between wild type and transformed cells.

The argumentation that softer tissues would be more easily compressed is plausible. However, which mechanism do the authors suggest is generating the actual compressive stress to drive the compaction of transformed cells? They exclude a proliferative advantage of wild type cells, which other mechanisms will generate the compressive forces by wild type cells?

Reviewer #1 (Public review):

Summary:

Olfaction is fundamental to the survival and reproduction of animals, as they rely on olfactory sensory neurons (OSNs) in the olfactory epithelium (OE) to detect volatile chemical cues in their environment. Most mature OSNs adhere to the 'one neuron one receptor' rule, wherein each neuron selects a single receptor for expression from a large repertoire of olfactory receptor genes. The precise regulation of olfactory receptor expression is critical for accurate odorant recognition. Since the seminal discovery of olfactory receptors by Linda Buck and Richard Axel in 1991, substantial efforts have been made to elucidate the mechanisms underlying OSN differentiation and receptor expression. However, these processes remain incompletely understood. The development of in vitro olfactory epithelium organoids offers a promising platform to address these fundamental questions. The in vivo OE is composed of a complex array of cell types, which has posed a significant challenge for recapitulating its structure and function in vitro. Previous attempts to generate olfactory organoids from adult human or mouse OE cells yielded tissue containing OSNs, but these constructs were structurally distinct from the in vivo OE and lacked the characteristic pseudostratified epithelium.

In this study, Kazuya et al. successfully established olfactory epithelium organoids from E13.5 mouse embryonic OE stem cells, which developed into a pseudostratified structure closely resembling the native OE. They further examined the influence of different cultural conditions on OE differentiation, confirming the pivotal role of niche factors in promoting OSN development. Through immunofluorescence staining and single-cell RNA sequencing, they demonstrated that the organoids encompass a diverse range of cell types analogous to those present in the in vivo OE. Notably, calcium imaging revealed that the organoids were functionally responsive to odorants, and single-cell transcriptomic analysis showed that the majority of mature OSNs conformed to the 'one neuron one receptor' rule. Using these organoids, the authors performed a preliminary investigation into the developmental trajectories of OSNs, developed a tool to predict subpopulations of mature OSNs, and identified novel markers associated with OSN maturation. Collectively, the data provide compelling evidence for the reliability and utility of this olfactory organoid model. Further in-depth analyses may enable readers to better assess and utilize this tool to advance the study of olfactory biology.

Strengths:

The authors developed and established olfactory epithelium organoids, with immunofluorescence imaging confirming the presence of a pseudostratified structure similar to that of the in vivo olfactory epithelium, representing a significant advancement. Single-cell sequencing and calcium imaging further demonstrated the utility of these organoids, as they contain multiple cell types analogous to the in vivo olfactory epithelium. Importantly, they are physiologically functional, capable of responding to odor stimuli.

Weakness:

Although the authors have made significant progress in the technique, there are some gaps in understanding its underlying principles. First, it remains unclear what specific characteristics of E13.5 embryonic olfactory stem cells enable them to generate organoids in vitro that more closely resemble the in vivo olfactory epithelium, compared to adult mouse olfactory stem cells. Second, it is not clearly defined which specific cell type(s) from the embryonic olfactory epithelium give rise to these organoids, and the efficiency of organoid formation from the isolated cells also warrants further clarification.

Reviewer #2 (Public review):

Summary:

Suzuki and colleagues aim to develop an in vitro organoid system to recapitulate the developmental process of the olfactory epithelium. The authors have succeeded in using a combination of niche factors to induce organoid development, which gives rise to multiple cell types including those with characteristics of mature olfactory sensory neurons. By comparing different cultural media in inducing lineage specification in the organoids, the authors show that the niche factors play an important role in the neuronal lineage whereas serum promotes the development of the respiratory epithelium. The authors further utilized single-cell RNASeq and trajectory analysis to demonstrate that the organoids recapitulate the developmental process of the olfactory epithelium and that some of the factory sensory neurons express only one receptor type per cell. Using these analyses, the authors proposed that a specific set of guidance modules are associated with individual receptor types to enable the formation of the factory map.

Strengths:

The strength of the paper is that the authors have demonstrated that olfactory epithelium organoids can develop from dissociated cells from embryonic or tissue. This provides a valuable tool for studying the development of processes of the factory epithelium in vitro. Defining various factors in the media that influence the development trajectories of various cell types also provides valuable information to guide further development of the method. Single-cell RNA-Seq experiments provide information about the developmental processes of the olfactory system.

Weaknesses:

The manuscript is also marked by a number of weaknesses. The premise of the studies is not well argued. The authors set out to use organoid culture to study the developmental process in order to unravel the mechanisms of single receptor choice, and its role in setting up the factory map. However, the paper has mostly focused on characterizing the organization rather than providing insights into the problem. The statement that the organoids can develop from single cells is misleading, because it's mostly likely that organoids develop after the dissociated cells form aggregates before developing into organoids. It is not known whether coarsely separated tissue chunks can develop into organoids with the same characteristics. Re-aggregation of the cells to form organoids is in and of itself is interesting. Unfortunately, the heterogeneity of the cells and how they contribute to the development of overnight is not explored. There is also a missed opportunity to compare single-cell RNASeq data from this study with existing ones. The in vitro system is likely to be different from embryonic development. It is critical to compare and determine how much the organoid is recapitulating the development of the OSNs in vivo. There are a number of comprehensive datasets from the OE in addition to that presented in the Fletcher paper. Finally, the quality of the functional assay (calcium imaging) of factory sensory neurons is poor. Experiments are of high quality are needed to verify the results.

Major points:

(1) Adding FBS in organoid culture medium has been shown to negatively affect the organoid formation and growth. Previous OE organoids culture method did not use FBS. Also, day 10 is an odd choice to compare the two conditions after showing day 20 of NF+ culture shows a better differentiation state. It is not known whether and how the differentiation may be different on day 20. Moreover, comparing Figure 2R to 2S, FBS treatment alone appears to have not only more Foxj1+ cells but also more Tuj1+ cells than NFs/FBS. This is inconsistent with the model. The authors should provide statistics for Tuj1+ cells as well.

(2) As opposed to the statement in the manuscript, Plxnb2 had been shown to be expressed by the OSNs (Mclntyre et al. 2010; JNR), specifically in immature OSNs. It would be important to mention that Plxnb2 is expressed in OMP+ OSNs in the OE organoid system and its potential reasons to better guide the readers of the system mimicking the in vivo OSNs. Similarly, OSN expression of Cdh2 has been shown by Akins and colleagues. As Plxnb2 showed an expression pattern (immunofluorescence) with an anterior-posterior axis while Cdh2 expression level was not, it would be informative to show the odorant receptor types regarding the expression pattern of Plxnb2 (versus that of Cdh2) using single cell RNAseq data4.

(3) There is no real layering of the organoids, although some cells show biases toward one side or the other in some regions of the organoid. The authors should not make a sweeping claim that the organoids establish layered structures.

(4) Figure 2P, it is clear whether OMP is present in the cell bodies. The signal is not very convincing. Even the DAPI signal does not seem to be on a comparable scale compared to Figures 2N and 2O.

(5) Annotation of the cell types in different single-cell RNA-Seq analysis. The iOSN is only marked in Figure 3A. In the marker expression panel, it appears that those marked as mOSN have high GAP43, which are an iOSN marker. These discrepancies are not detailed nor discussed.

(6) The authors should merge the single-cell datasets from day 10 organoids cultured in NF-medium and FBS-medium to compare their differences.

(7) The quality of the calcium imaging experiment is poor. Labeling and experimental details are not provided. The concentration of IVA, the manner of its delivery, and delivery duration are not provided. How many ROIs have been imaged, and what percentage of them responded to IVA? Do they respond to more than one odor? Do they respond to repeated delivery? There is no control for solution osmolarity. Cell body response was not recorded. Given that only a small number of cells express a receptor, it seems extraordinary that these axons respond to IVA receptors. The authors should also determine whether IVA receptor genes are found in their dataset.

Reviewer #3 (Public review):

Summary:

The present work by Suzuki et al seeks to develop a new embryonic olfactory epithelium organoid culture model, to study OR gene expression and mechanisms involved in epithelium-to-bulb targeting. They characterize an organoid culture derived from E13 mouse olfactory tissue, using RT-qPCR, immunostaining, limited calcium imaging, and single-cell RNA-seq. Main findings show that the cultures produce major olfactory cell types; many olfactory neurons express a single OR; scSeq analysis identifies transcriptional programs associated with specific OR class expressions that may help define mechanisms involved in projection to specific bulb sites (glomeruli).

Strengths:

The organoid model is generally well-characterized and may be a useful approach for studying this question and other problems, such as basal cell lineage choice or damage and repair mechanisms. Overall, the paper is well-written, and the figures are of high quality.

The cultures, produced from E13 mice, appear to produce HBCs, GBCs, neurons, and non-neural cells, providing an important tool. I think a really interesting question is: when do HBCs first appear in these cultures? Developmentally, in rodents, HBCs do not arise until near the end of gestation, and the OE cell populations are instead made from a more GBC-like cell (keratin negative, p63 negative) that proliferates as an apical or basal progenitor. The cell type and architectural descriptions used here repeatedly are really descriptions of the adult OE, yet the cultures are made from E13 mouse olfactory epithelium. Perhaps an important question could be addressed by this model - how this specific adult reserve epithelial stem cell (the HBC) is generated remains unclear. HBCs are a reserve multipotential cell that reconstitutes the entire olfactory epithelium in adults following severe injury, yet is not present during embryonic development until after the epithelium has been largely generated.

Weaknesses:

The paper should discuss the transcriptional programs identified here that correlate with OR class expression in the context of findings from Tsukahara et al, Cell 2021. Tsukahara identified from in vivo olfactory neuron scSeq fixed gene expression programs defining olfactory neuron position in AP or DV axes correlating highly with OR expression.

While the current findings do define the expression of putative targeting, guidance or adhesion molecules in specific OR-expressing neurons in culture, the current results do not provide any experimental evidence that glomerulus targeting is actually mediated by these factors. Further discussion of this limitation may be helpful, along with a discussion of additional approaches to explore these questions.

Calcium imaging: it is not clear why isovaleric acid was chosen as a stimulus for Ca imaging. Is it's known receptor expressed widely in these cultures? Why not use a cocktail of odorants, to activate a broader range of ORs, as has been widely used in in vitro calcium imaging studies of olfactory neurons? Can you show positive control activation (i.e. high potassium)?

How many unique ORs are identified as expressed in the cultures? Figure 5 indicates only 78 genes. Since mice express about 1200 ORs, is this a limitation? How many replicates (individual cells) are found to express each of the ORs? Again, Figure 5 suggests only 202 cells are OR+? Is this enough to define the gene expression programs reliably associated with a given OR or OR class? More detail on this analysis would be helpful.

Reviewer #1 (Public review):

Summary:

van der Linden et al. report on the development of a new green-fluorescent sensor for calcium, following a novel rational design strategy based on the modification of the cyan-emissive sensor mTq2-CaFLITS. Through a mutational strategy similar to the one used to convert EGFP into EYFP, coupled with optimization of strategic amino acids located in proximity of the chromophore, they identify a novel sensor, G-CaFLITS. Through a careful characterization of the photophysical properties in vitro and the expression level in cell cultures, the authors demonstrate that G-CaFLITS combines a large lifetime response with a good brightness in both the bound and unbound states. This relative independence of the brightness on calcium binding, compared with existing sensors that often feature at least one very dim form, is an interesting feature of this new type of sensors, which allows for a more robust usage in fluorescence lifetime imaging. Furthermore, the authors evaluate the performance of G-CaFLITS in different subcellular compartments and under two-photon excitation in Drosophila. While the data appears robust and the characterization thorough, the interpretation of the results in some cases appears less solid, and alternative explanations cannot be excluded.

Strengths:

- The approach is innovative and extends the excellent photophysical properties of the mTq2-based to more red-shifted variants. While the spectral shift might appear relatively minor, as the authors correctly point out, it has interesting practical implications, such as the possibility to perform FLIM imaging of calcium using widely available laser wavelengths, or to reduce background autofluorescence, which can be a significant problem in FLIM.<br /> - The screening was simple and rationally guided, demonstrating that, at least for this class of sensors, a careful choice of screening positions is an excellent strategy to obtain variants with large FLIM responses without the need of high-throughput screening.<br /> - The description of the methodologies is very complete and accurate, greatly facilitating the reproduction of the results by others, or the adoption of similar methods. This is particularly true for the description of the experimental conditions for optimal screening of sensor variants in lysed bacterial cultures.<br /> - The photophysical characterization is very thorough and complete, and the vast amount of data reported in the supporting information is a valuable reference for other researchers willing to attempt a similar sensor development strategy. Particularly well done is the characterization of the brightness in cells, and the comparison on multiple parameters with existing sensors.<br /> - Overall, G-CaFLITS displays excellent properties for a FLIM sensor: very large lifetime change, bright emission in both forms and independence from pH in the physiological range.

Weaknesses:

- The paper demonstrates the application of G-CaFLITS in various cellular sub-compartments without providing direct evidence that the sensor's response is not affected by the targeting. Showing at least that the lifetime values in the saturated state are similar in all compartments would improve the robustness of the claims.<br /> - In some cases, the interpretation of the results is not fully convincing, leaving alternative hypotheses as a possibility. This is particularly the case for the claim of the origin of the strongly reduced brightness of G-CaFLITS in Drosophila. The explanation of the intensity changes of G-CaFLITS also shows some inconsistency with the basic photophysical characterization.<br /> - While the claims generally appear robust, in some cases they are conveyed with a lack of precision. Several sentences in the introduction and discussion could be improved in this regard. Furthermore, the use of the signal-to-noise ratio as a means of comparison between sensors appears to be imprecise, since it is dependent on experimental conditions.

Reviewer #2 (Public review):

Summary:

Van der Linden et al. describe the addition of the T203Y mutation to their previously described fluorescence lifetime calcium sensor Tq-Ca-FLITS to shift the fluorescence to green emission. This mutation was previously described to similarly red-shift the emission of green and cyan FPs. Tq-Ca-FLITS_T203Y behaves as a green calcium sensor with opposite polarity compared with the original (lifetime goes down upon calcium binding instead of up). They then screen a library of variants at two linker positions and identify a variant with slightly improved lifetime contrast (Tq-Ca-FLITS_T203Y_V27A_N271D, named G-Ca-FLITS). The authors then characterize the performance of G-Ca-FLITS relative to Tq-Ca-FLITS in purified protein samples, in cultured cells, and in the brains of fruit flies.

Strengths:

This work is interesting as it extends their prior work generating a calcium indicator scaffold for fluorescent protein-based lifetime sensors with large contrast at a single wavelength, which is already being adopted by the community for production of other FLIM biosensors. This work effectively extends that from cyan to green fluorescence. While the cyan and green sensors are not spectrally distinct enough (~20-30nm shift) to easily multiplex together, it at least shifts the spectra to wavelengths that are more commonly available on commercial microscopes.

The observations of organellar calcium concentrations were interesting and could potentially lead to new biological insight if followed up.

Weaknesses:

The new G-Ca-FLITS sensor doesn't appear to be significantly improved in performance over the original Tq-Ca-FLITS, no specific benefits are demonstrated.

Although it was admirable to attempt in vivo demonstration in Drosophila with these sensors, depolarizing the whole brain with high potassium is not a terribly interesting or physiological stimulus and doesn't really highlight any advantages of their sensors; G-Ca-FLITS appears to be quite dim in the flies.

Reviewer #3 (Public review):

Summary:

The authours present a variant of a previously described fluorescence lifetime sensor for calcium. Much of the manuscript describes the process of developing appropriate assays for screening sensor variants, and thorough characterization of those variants (inherent fluorescence characteristics, response to calcium and pH, comparisons to other calcium sensors). The final two figures show how the sensor performs in cultured cells and in vivo drosophila brains.

Strengths:

The work is presented clearly and the conclusion (this is a new calcium sensor that could be useful in some circumstances) is supported by the data.

Weaknesses:

There are probably few circumstances where this sensor would facilitate experiments (calcium measurements) that other sensors would prove insufficient.

Joint Public Review:

Summary of the work:

This manuscript defines the differential stress response signaling induced by nuclear and cytoplasmic protein misfolding. To accomplish this, the authors used superfolder GFP fused to a destabilized FKBP protein-bearing targeting signal for cytosolic or nuclear localization. When cells were grown in the presence of the ligand Shield-1, this protein was stable, allowing fluorescence of the GFP protein. Upon removal of Shield-1, the FKBP protein is unfolded targeting the entire fusion protein to proteasomal degradation. Using this approach, they performed RNAseq to probe similarities and differences in transcriptional responses to the accumulation of unfolded proteins in the cytosol or nucleus. As expected, many of the pathways upregulated in both datasets involved protein homeostasis pathways such as the proteasome and cytosolic chaperones. The increase in proteasome subunits correlated with the stabilization of Nrf1 under these conditions, suggesting that protein misfolding might induce proteasome subunits through an Nrf1-dependent mechanism, but this was not explicitly tested. In contrast, the authors report that the p53-dependent transcriptional response was selectively induced by protein misfolding stress in the nucleus, but not the cytosol. Deletion of p53 blocked this increase, indicating that this response is attributable to p53 stabilization. The increased p53 transcriptional activity corresponded with the stabilization of p53 and its target p21 in cells subjected to nuclear but not cytosolic protein misfolding stress. Using a reporter of nuclear proteasome activity, they show that nuclear proteasome activity is reduced in cells following protein misfolding stress in the nucleus, indicating that the stabilization of p53 (and other transcription factors such as NRF1) might be attributed to reduced proteasomal degradation. Additionally, the authors showed that nuclear misfolding stress also induces cell cycle arrest. However, this effect was not dependent on p53 deletion, indicating that this is mediated by other unknown mechanisms.

Major strengths and weaknesses of the methods and results:

The findings reported here define specific transcriptional outputs induced by targeted protein misfolding stress in the nucleus and cytosol, revealing new insights into the organelle-specific stress signaling. The approach is interesting and effective at revealing cellular responses induced by compartment-specific protein misfolding stress.

One major weakness of the study is the lack of mechanistic follow-up for the transcriptional study. For example, what is the mechanistic basis for p53 stabilization by nuclear-destabilized domain (Nuc DD)? Is this entirely caused by diminished nuclear degradation activity as shown in Figure 6 or are there additional factors to be considered? If limited proteasome degradation capacity is the main reason for p53 upregulation, wouldn't the authors also see stabilization of other short-lived transcription factors? The fact that Nrf1 and Nrf2 are also stabilized by Nuc DD is consistent with the authors' hypothesis. On the other hand, if Nuc DD also affects other short-lived transcription factors such as c-fos or c-myc via proteasome inhibition, why did the gene expression analysis only pick up the p53 pathway as the one differentially regulated by Nuc DD? Would this imply that only p53 is specifically targeted by the nuclear proteasome, whereas other short-lived transcription factors are degraded either by the cytosolic proteasome or by both nuclear and cytosolic proteasome like Nrf1? Is there any evidence in the literature that supports this speculation? Additionally, how does Nuc DD affect the UPS system in the nucleus? Does it clog the proteasome directly or affect other assisting factors like chaperones or ubiquitinating enzymes? Lastly, it isn't clear what the functional implications of p53 stabilization would be for cells subjected to nuclear protein misfolding stress, particularly as the small effect on cell cycle arrest is not dependent on p53. In the end, the lack of mechanistic and/or functional follow-up reduces the overall importance of this manuscript. While the reviewers do not expect the authors to answer all these questions by experiments, additional work/clarifications/discussions along these lines would significantly improve the paper (see the recommendations).

Another major weakness is the lack of statistical analysis (SA) to better support their conclusions. In fact, no SA was provided for many figures even though the authors tried to make many comparisons.

The failure of the DD reporter to mount a significant heat shock response was puzzling. The presence of non-native proteins is the primary trigger for the heat shock response, but the authors acknowledge that inducible chaperones such as Hspa1a/b and Hsp90aa1 were not significantly changed in their system (page 8). Could this suggest a problem with the approach? What exactly is the nature of the stress mounted by Nuc DD?

The cell cycle data presented in Figure 5 is less robust, particularly as the p53 data in panels C and D was collected only once.

The Western blot data shown in Figure 6 does not have quantification to show how representative the blot is and how robust the changes in protein levels are over time. Western blots are known to be variable with different replicates and therefore the authors need to mention the number of biological repeats represented by the blot.

Reviewer #1 (Public review):

This manuscript discusses from a theory point of view he mechanisms underlying the formation of specialized or mixed factories. To investigate this, a chromatin polymer model was developed to mimic the chromatin binding-unbinding dynamics of various complexes of transcription factors (TFs).

The model revealed that both specialized (i.e., demixed) and mixed clusters can emerge spontaneously, with the type of cluster formed primarily determined by cluster size. Non-specific interactions between chromatin and proteins were identified as the main factor promoting mixing, with these interactions becoming increasingly significant as clusters grow larger.

These findings, observed in both simple polymer models and more realistic representations of human chromosomes, reconcile previously conflicting experimental results. Additionally, the introduction of different types of TFs was shown to strongly influence the emergence of transcriptional networks, offering a framework to study transcriptional changes resulting from gene editing or naturally occurring mutations.

Overall I think this is an interesting paper discussing a valuable model of how chromosome 3D organisation is linked to transcription. I would only advise the authors to polish and shorten their text to better highlight their key findings and make it more accessible to the reader.

Reviewer #2 (Public review):

Summary:

With this report, I suggest what are in my opinion crucial additions to the otherwise very interesting and credible research manuscript "Cluster size determines morphology of transcription factories in human cells".

Strengths:

The manuscript in itself is technically sound, the chosen simulation methods are completely appropriate the figures are well-prepared, the text is mostly well-written spare a few typos. The conclusions are valid and would represent a valuable conceptual contribution to the field of clustering, 3D genome organization and gene regulation related to transcription factories, which continues to be an area of most active investigation.

Weaknesses:

However, I find that the connection to concrete biological data is weak. This holds especially given that the data that are needed to critically assess the applicability of the derived cross-over with factory size is, in fact, available for analysis, and the suggested experiments in the Discussion section are actually done and their results can be exploited. In my judgement, unless these additional analysis are added to a level that crucial predictions on TF demixing and transcriptional bursting upon TU clustering can be tested, the paper is more fitted for a theoretical biophysics venue than for a biology journal.

Major points

(1) My first point concerns terminology. The Merriam-Webster dictionary describes morphology as the study of structure and form. In my understanding, none of the analyses carried out in this study actually address the form or spatial structuring of transcription factories. I see no aspects of shape, only size. Unless the authors want to assess actual shapes of clusters, I would recommend to instead talk about only their size/extent. The title is, by the same argument, in my opinion misleading as to the content of this study.

(2) Another major conceptual point is the choice of how a single TF:pol particle in the model relates to actual macromolecules that undergo clustering in the cell. What about the fact that even single TF factories still contain numerous canonical transcription factors, many of which are also known to undergo phase separation? Mediator, CDK9, Pol II just to name a few. This alone already represents phase separation under the involvement of different species, which must undergo mixing. This is conceptually blurred with the concept of gene-specific transcription factors that are recruited into clusters/condensates due to sequence-specific or chromatin-epigenetic-specific affinities. Also, the fact that even in a canonical gene with a "small" transcription factory there are numerous clustering factors takes even the smallest factories into a regime of several tens of clustering macromolecules. It is unclear to me how this reality of clustering and factory formation in the biological cell relates to the cross-over that occurs at approximately n=10 particles in the simulations presented in this paper.

(3) The paper falls critically short in referencing and exploiting for analysis existing literature and published data both on 3D genome organization as well as the process of cluster formation in relation to genomic elements. In terms of relevant literature, most of the relevant body of work from the following areas has not been included:

(i) mechanisms of how the clustering of Pol II, canonical TFs, and specific TFs is aided by sequence elements and specific chromatin states

(ii) mechanisms of TF selectivity for specific condensates and target genomic elements

(iii) most crucially, existing highly relevant datasets that connect 3D multi-point contacts with transcription factor identity and transcriptional activity, which would allow the authors to directly test their hypotheses by analysis of existing data

Here, especially the data under point iii are essential. The SPRITE method (cited but not further exploited by the authors), even in its initial form of publication, would have offered a data set to critically test the mixing vs. demixing hypothesis put forward by the authors. Specifically, the SPRITE method offers ordered data on k-mers of associated genomic elements. These can be mapped against the main TFs that associate with these genomic elements, thereby giving an account of the mixed / demixed state of these k-mer associations. Even a simple analysis sorting these associations by the number of associated genomic elements might reveal a demixing transition with increasing association size k. However, a newer version of the SPRITE method already exists, which combines the k-mer association of genomic elements with the whole transcriptome assessment of RNAs associated with a particular DNA k-mer association. This can even directly test the hypotheses the authors put forward regarding cluster size, transcriptional activation, correlation between different transcription units' activation etc.

To continue, the Genome Architecture Mapping (GAM) method from Ana Pombo's group has also yielded data sets that connect the long-range contacts between gene-regulatory elements to the TF motifs involved in these motifs, and even provides ready-made analyses that assess how mixed or demixed the TF composition at different interaction hubs is. I do not see why this work and data set is not even acknowledged? I also strongly suggest to analyze, or if they are already sufficiently analyzed, discuss these data in the light of 3D interaction hub size (number of interacting elements) and TF motif composition of the involved genomic elements.

Further, a preprint from the Alistair Boettiger and Kevin Wang labs from May 2024 also provides direct, single-cell imaging data of all super-enhancers, combined with transcription detection, assessing even directly the role of number of super-enhancers in spatial proximity as a determinant of transcriptional state. This data set and findings should be discussed, not in vague terms but in detailed terms of what parts of the authors' predictions match or do not match these data.

For these data sets, an analysis in terms of the authors' key predictions must be carried out (unless the underlying papers already provide such final analysis results). In answering this comment, what matters to me is not that the authors follow my suggestions to the letter. Rather, I would want to see that the wealth of available biological data and knowledge that connects to their predictions is used to their full potential in terms of rejecting, confirming, refining, or putting into real biological context the model predictions made in this study.

References for point (iii):

RNA promotes the formation of spatial compartments in the nucleus<br /> https://www.cell.com/cell/fulltext/S0092-8674(21)01230-7?dgcid=raven_jbs_etoc_email

Complex multi-enhancer contacts captured by genome architecture mapping<br /> https://www.nature.com/articles/nature21411

Cell-type specialization is encoded by specific chromatin topologies<br /> https://www.nature.com/articles/s41586-021-04081-2

Super-enhancer interactomes from single cells link clustering and transcription<br /> https://www.biorxiv.org/content/10.1101/2024.05.08.593251v1.full

For point (i) and point (ii), the authors should go through the relevant literature on Pol II and TF clustering, how this connects to genomic features that support the cluster formation, and also the recent literature on TF specificity. On the last point, TF specificity, especially the groups of Ben Sabari and Mustafa Mir have presented astonishing results, that seem highly relevant to the Discussion of this manuscript.

(4) Another conceptual point that is a critical omission is the clarification that there are, in fact, known large vs. small transcription factories, or transcriptional clusters, which are specific to stem cells and "stressed cells". This distinction was initially established by Ibrahim Cisse's lab (Science 2018) in mouse Embryonic Stem Cells, and also is seen in two other cases in differentiated cells in response to serum stimulus and in early embryonic development:

Mediator and RNA polymerase II clusters associate in transcription-dependent condensates<br /> https://www.science.org/doi/10.1126/science.aar4199

Nuclear actin regulates inducible transcription by enhancing RNA polymerase II clustering<br /> https://www.science.org/doi/10.1126/sciadv.aay6515

RNA polymerase II clusters form in line with surface condensation on regulatory chromatin<br /> https://www.embopress.org/doi/full/10.15252/msb.202110272

If "morphology" should indeed be discussed, the last paper is a good starting point, especially in combination with this additional paper:

Chromatin expansion microscopy reveals nanoscale organization of transcription and chromatin<br /> https://www.science.org/doi/10.1126/science.ade5308

(5) The statement "scripts are available upon request" is insufficient by current FAIR standards and seems to be non-compliant with eLife requirements. At a minimum, all, and I mean all, scripts that are needed to produce the simulation outcomes and figures in the paper, must be deposited as a publicly accessible Supplement with the article. Better would be if they would be structured and sufficiently documented and then deposited in external repositories that are appropriate for the sharing of such program code and models.

Reviewer #3 (Public review):

Summary:<br /> In this work, the authors present a chromatin polymer model with some specific pattern of transcription units (TUs) and diffusing TFs; they simulate the model and study TFclustering, mixing, gene expression activity, and their correlations. First, the authors designed a toy polymer with colored beads of a random type, placed periodically (every 30 beads, or 90kb). These colored beads are considered a transcription unit (TU). Same-colored TUs attract with each other mediated by similarly colored diffusing beads considered as TFs. This led to clustering (condensation of beads) and correlated (or anti-correlation) "gene expression" patterns. Beyond the toy model, when authors introduce TUs in a specific pattern, it leads to emergence of specialized and mixed cluster of different TFs. Human chromatin models with realistic distribution of TUs also lead to the mixing of TFs when cluster size is large.

Strengths:<br /> This is a valuable polymer model for chromatin with a specific pattern of TUs and diffusing TF-like beads. Simulation of the model tests many interesting ideas. The simulation study is convincing and the results provide solid evidence showing the emergence of mixed and demixed TF clusters within the assumptions of the model.

Weaknesses:<br /> Weakness of the work: The model has many assumptions. Some of the assumptions are a bit too simplistic. Concerns about the work are detailed below:

The authors assume that when the diffusing beads (TFs) are near a TU, the gene expression starts. However, mammalian gene expression requires activation by enhancer-promoter looping and other related events. It is not a simple diffusion-limited event. Since many of the conclusions are derived from expression activity, will the results be affected by the lack of looping details?

Authors neglect protein-protein interactions. Without protein-protein interactions, condensate formation in natural systems is unlikely to happen.

What is described in this paper is a generic phenomenon; many kinds of multivalent chromatin-binding proteins can form condensates/clusters as described here. For example, if we replace different color TUs with different histone modifications and different TFs with Hp1, PRC1/2, etc, the results would remain the same, wouldn't they? What is specific about transcription factor or transcription here in this model?<br /> What is the logic of considering 3kb chromatin as having a size of 30 nm? See Kadam et al. (Nature Communications 2023). Also, DNA paint experimental measurement of 5kb chromatin is greater than 100 nm (see work by Boettiger et al.).

Reviewer #1 (Public review):

Summary:

This study has preliminarily revealed the role of ACVR2A in trophoblast cell function, including its effects on migration, invasion, proliferation, and clonal formation, as well as its downstream signaling pathways.

Strengths:

The use of multiple experimental techniques, such as CRISPR/Cas9-mediated gene knockout, RNA-seq, and functional assays (e.g., Transwell, colony formation, and scratch assays), is commendable and demonstrates the authors' effort to elucidate the molecular mechanisms underlying ACVR2A's regulation of trophoblast function. The RNA-seq analysis and subsequent GSEA findings offer valuable insights into the pathways affected by ACVR2A knockout, particularly the Wnt and TCF7/c-JUN signaling pathways.

Weaknesses:

The molecular mechanisms underlying this study require further exploration through additional experiments. While the current findings provide valuable insights into the role of ACVR2A in trophoblast cell function and its involvement in the regulation of migration, invasion, and proliferation, further validation in both in vitro and in vivo models is needed. Additionally, more experiments are required to establish the functional relevance of the TCF7/c-JUN pathway and its clinical significance, particularly in relation to pre-eclampsia. Additional techniques, such as animal models and more advanced clinical sample analyses, would help strengthen the conclusions and provide a more comprehensive understanding of the molecular pathways involved.

Reviewer #2 (Public review):

Summary:

ACVR2A is one of a handful of genes for which significant correlations between associated SNPs and the incidences of preeclampsia have been found in multiple populations. It is one of the TGFB family receptors, and multiple ligands of ACVR2A, as well as its coreceptors and related inhibitors, have been implicated in placental development, trophoblast invasion, and embryo implantation. This useful study builds on this knowledge by showing that ACVR2A knockout in trophoblast-related cell lines reduces trophoblast invasion, which could tie together many of these observations. Support for this finding is incomplete, as reduced proliferation may be influencing the invasion results. The implication of cross-talk between the WNT and ACRV2A/SMAD2 pathways is an important contribution to the understanding of the regulation of trophoblast function.

Strengths:

(1) ACVR2A is one of very few genes implicated in preeclampsia in multiple human populations, yet its role in pathogenesis is not very well studied and this study begins to address that hole in our knowledge.

(2) ACVR2A is also indirectly implicated in trophoblast invasion and trophoblast development via its connections to many ligands, inhibitors, and coreceptors, suggesting its potential importance.

(3) The authors have used multiple cell lines to verify their most important observations.

Weaknesses:

(1) There are a number of claims made in the introduction without attribution. For example, there are no citations for the claims that family history is a significant risk factor for PE, that inadequate trophoblast invasion of spiral arteries is a key factor, and that immune responses, and renin-angiotensin activity are involved.

(2) The introduction states "As a receptor for activin A, ACVR2A..." It's important to acknowledge that ACVR2A is also the receptor for other TGFB family members, with varying affinities and coreceptors. Several TGFB family members are known to regulate trophoblast differentiation and invasion. For example, BMP2 likely stimulates trophoblast invasion at least in part via ACVR2A (PMID 29846546).

(3) An alternative hypothesis for the potential role of ACVR2A in preeclampsia is its functions in the endometrium. In the mouse ACVR2A knockout in the uterus (and other progesterone receptor-expressing cells) leads to embryo implantation failure.

(4) In the description of the patient population for placental sample collections, preeclampsia is defined only by hypertension, and this is described as being in accordance with ACOG guidelines. ACOG requires a finding of hypertension in combination with either proteinuria or one of the following: thrombocytopenia, elevated creatinine, elevated liver enzymes, pulmonary, edema, and new onset unresponsive headache.

(5) I believe that Figures 1a and 1b are data from a previously published RNAseq dataset, though it is not entirely clear in the text. The methods section does not include a description of the analysis of these data undertaken here. It would be helpful to include at least a brief description of the study these data are taken from - how many samples, how were the PE/control groups defined, gestational age range, where is it from, etc. For the heatmap presented in B, what is the significance of the other genes/ why are they being shown? If the purpose of these two panels is to show differential expression specifically of ACVR2A in this dataset, that could be shown more directly.

(6) More information is needed in the methods section to understand how the immunohistochemistry was quantified. "Quantitation was performed" is all that is provided. Was staining quantified across the whole image or only in anchoring villous areas? How were HRP & hematoxylin signals distinguished in ImageJ? How was the overall level of HRP/DAB development kept constant between the NC and PE groups?

(7) In Figure 1E it is not immediately obvious to many readers where the EVT are. It is probably worth circling or putting an arrow to the little region of ACVR2A+ EVT that is shown in the higher magnification image in Figure 1E. These are actually easier to see in the pictures provided in the supplement Figure 1. Of note, the STB is also staining positive. This is worth pointing out in the results text.

(8) It is not possible to judge whether the IF images in 1F actually depict anchoring villi. The DAPI is really faint, and it's high magnification, so there isn't a lot of context. Would it be possible to include a lower magnification image that shows where these cells are located within a placental section? It is also somewhat surprising that this receptor is expressed in the cytoplasm rather than at the cell surface. How do the authors explain this?

(9) The results text makes it sound like the data in Figure 2A are from NCBI & Protein atlas, but the legend says it is qPCR from this lab. The methods do not detail how these various cell lines were grown; only HTR-SVNeo cell culture is described. Similarly, JAR cells are used for several experiments and their culture is not described.

(10) Under RT-qPCR methods, the phrase "cDNA reverse transcription cell RNA was isolated..." does not make any sense.

(11) The paragraph beginning "Consequently, a potential association..." is quite confusing. It mentions analyzing ACVR2A expression in placentas, but then doesn't point to any results of this kind and repeats describing the results in Figure 2a, from various cell lines.

(12) The authors should acknowledge that the effect of the ACVR2A knockout on proliferation makes it difficult to draw any conclusions from the trophoblast invasion assays. That is, there might be fewer migrating or invading cells in the knockout lines because there are fewer cells, not because the cells that are there are less invasive. Since this is a central conclusion of the study, it is a major drawback.

(13) The legend and the methods section do not agree on how many fields were selected for counting in the transwell invasion assays in Figure 3C. The methods section and the graph do not match the number of replicate experiments in Figure 3D (the number of replicate experiments isn't described for 3C).

(14) Discussion says "Transcriptome sequencing analysis revealed low ACVR2A expression in placental samples from PE patients, consistent with GWAS results across diverse populations." The authors should explain this briefly. Why would SNPs in ACVR2A necessarily affect levels of the transcript?

(15) "The expression levels of ACVR2A mRNA were comparable to those of tumor cells such as A549. This discovery suggested a potential pivotal role of ACVR2A in the biological functions of trophoblast cells, especially in the nurturing layer." Alternatively, ACVR2A expression resembles that of tumors because the cell lines used here are tumor cells (JAR) or immortalized cells (HTR8). These lines are widely used to study trophoblast properties, but the discussion should at least acknowledge the possibility that the behavior of these cells does not always resemble normal trophoblasts.

(16) The authors should discuss some of what is known about the relationship between the TCF7/c-JUN pathway and the major signaling pathway activated by ACVR2A, Smad 2/3/4. The Wnt and TGFB family cross-talk is quite complex and it has been studied in other systems.

Reviewer #1 (Public review):

Summary:

Meissner-Bernard et al present a biologically constrained model of telencephalic area of adult zebrafish, a homologous area to the piriform cortex, and argue for the role of precisely balanced memory networks in olfactory processing.

This is interesting as it can add to recent evidence on the presence of functional subnetworks in multiple sensory cortices. It is also important in deviating from traditional accounts of memory systems as attractor networks. Evidence for attractor networks has been found in some systems, like in the head direction circuits in the flies. However, the presence of attractor dynamics in other modalities, like sensory systems, and their role in computation has been more contentious. This work contributes to this active line of research in experimental and computational neuroscience by suggesting that, rather than being represented in attractor networks and persistent activity, olfactory memories might be coded by balanced excitation-inhibitory subnetworks.

Strengths:

The main strength of the work is in: (1) direct link to biological parameters and measurements, (2) good controls and quantification of the results, and (3) comparison across multiple models.

(1) The authors have done a good job of gathering the current experimental information to inform a biological-constrained spiking model of the telencephalic area of adult zebrafish. The results are compared to previous experimental measurements to choose the right regimes of operation.<br /> (2) Multiple quantification metrics and controls are used to support the main conclusions, and to ensure that the key parameters are controlled for - e.g. when comparing across multiple models.<br /> (3) Four specific models (random, scaled I / attractor, and two variant of specific E-I networks - tuned I and tuned E+I) are compared with different metrics, helping to pinpoint which features emerge in which model.

In the revised manuscript, the authors have also:<br /> (a) made a good effort to provide a mechanistic explanation of their results (especially on the mechanism underlying medium amplification in specific E/I network models);<br /> (b) performed a systematic analysis of the parameter space by changing different parameters of E and I neurons (specifically showing that different time constants of E and I neurons do not change the results and therefore the main effects result from connectivity);<br /> (c) added further analysis and discussion on the potential functional and computational significance of balanced specific E-I subnetworks.

These additions substantially strengthen the study, presenting compelling evidence for how networks with specific E-I structure can underpin olfactory processing and memory representations. The findings have potential implications that extend beyond the olfactory system and may be applicable to other neural systems and species.

Reviewer #2 (Public review):

Summary:

The authors conducted a comparative analysis of four networks, varying in the presence of excitatory assemblies and the architecture of inhibitory cell assembly connectivity. They found that co-tuned E-I assemblies provide network stability and a continuous representation of input patterns (on locally constrained manifolds), contrasting with networks with global inhibition that result in attractor networks.

Strengths:

The findings presented in this paper are very interesting and cutting-edge. The manuscript effectively conveys the message and presents a creative way to represent high-dimensional inputs and network responses. Particularly, the result regarding the projection of input patterns onto local manifolds and continuous representation of input/memory is very Intriguing and novel. Both computational and experimental neuroscientists would find value in reading the paper.

Weaknesses:

Intuitively, classification (decodability) in discrete attractor networks is much better than in networks with continuous representations. This could also be shown in Figure 5B, along with the performance of the random and tuned E-I networks. The latter networks have the advantage of providing network stability compared to the Scaled I network, but at the cost of reduced network salience and, therefore, reduced input decodability. Thus, tuned E-I networks cannot always perform better than any other network.

Reviewer #3 (Public review):

Summary:

This work investigates computational consequences of assemblies containing both excitatory and inhibitory neurons (E/I assembly) in a model with parameters constrained by experimental data from the telencephalic area Dp of zebrafish. The authors show how this precise E/I balance shapes the geometry of neuronal dynamics in comparison to unstructured networks and networks with more global inhibitory balance. Specifically, E/I assemblies lead to the activity being locally restricted onto manifolds - a dynamical structure in-between high-dimensional representations in unstructured networks and discrete attractors in networks with global inhibitory balance. Furthermore, E/I assemblies lead to smoother representations of mixtures of stimuli while those stimuli can still be reliably classified, and allows for more robust learning of additional stimuli.

Strengths:

Since experimental studies do suggest that E/I balance is very precise and E/I assemblies exist, it is important to study the consequences of those connectivity structures on network dynamics. The authors convincingly show that E/I assemblies lead to different geometries of stimulus representation compared to unstructured networks and networks with global inhibition. This finding might open the door for future studies for exploring the functional advantage of these locally defined manifolds, and how other network properties allow to shape those manifolds.

The authors also make sure that their spiking model is well-constrained by experimental data from the zebrafish pDp. Both, spontaneous and odor stimulus triggered spiking activity is within the range of experimental measurements. But the model is also general enough to be potentially applied to findings in other animal models and brain regions.

Weaknesses:

All my previous points have been addressed.

Reviewer #1 (Public review):

Summary:

It is evident that studying leukocyte extravasation in vitro is a challenge. One needs to include physiological flow, culture cells and isolate primary immune cells. Timing is of utmost importance and a reproducible setup is essential. Extra challenges are met when extravasation kinetics in different vascular beds is required, e.g., across the blood-brain barrier. In this study, the authors describe a reliable and reproducible method to analyze leukocyte TEM under physiological flow conditions, including this analysis. That the software can also detect reverse TEM is a plus.

Strengths:

It is quite a challenge to get this assay reproducible and stable, in particular as there is flow included. Also for the analysis, there is currently no clear software analysis program, and many labs have their own methods. This paper gives the opportunity to unify the data and results obtained with this assay under label-free conditions. This should eventually lead to more solid and reproducible results.

Also, the comparison between manual and software analysis is appreciated.

Reviewer #2 (Public review):

Summary:

This paper develops an under-flow migration tracker to evaluate all the steps of the extravasation cascade of immune cells across the BBB. The algorithm is useful and has important applications.

Strengths:

The algorithm is almost as accurate as manual tracking and importantly saves time for researchers. The authors have discussed how their tool compares to other tracking methods.

Weaknesses:

Applicability can be questioned because the device used is 2D and physiological biology is in 3D. However, the authors have addressed this point in their manuscript.

Reviewer #1 (Public review):

Summary:

In this manuscript, Shibata describes a method to assess rapidly fluctuating CpG sites (fCpGs) from single-cell methylation sequencing (sc-MeSeq) data. Assuming that fCpGs are largely consistent over time with changes induced by inheritable events during replication, the author infers lineage relationships in available brain-derived sc-MeSeq. Supplementing current lineage tracing through genomic and mitochondrial mosaic variants is an interesting concept that could supplement current work or allow additional lineage analysis in existing data.

However, the author failed to convincingly show the power of fCpG analysis to determine lineages in the human brain. While the correlation with cellular division and distinction of cell types appears plausible and strong, the application to detect specific lineages is less convincing. Aspects of this might be due to a lack of clarity in presentation and erroneous use of developmental concepts. However, without addressing these problems it is challenging for a reader to come to the same conclusions as the author.

On the flip side, this novel application of fCpGs will allow the re-use of existing sc-MeSeq to infer additional features that were previously unavailable, once the biological relevance has been further elucidated.

Strengths:

• Novel re-analysis application of methylation data to infer the status of fCpGs and the use as a lineage marker<br /> • Application of this method to an innovative existing data set to benchmark this framework against existing developmental knowledge

Weaknesses:

• Inconsistent or erroneous use of neurodevelopmental concepts which hinders appropriate interpretation of the results.<br /> • Somewhat confusing presentation at times which makes it hard to judge the value of this novel approach.

Reviewer #3 (Public review):

Summary:

Cell lineage tracing necessitates continuous visible tracking or permanent molecular markers that daughter cells inherit from their progenitors. To successfully trace cell lineages, it is essential to generate and detect sufficient new markers during each cell division. Thus, molecular cell lineages have been predominantly studied with stably inherited genetic markers in animal models and somatic DNA mutations in the human brain. DNA methylation is unstable across cell divisions and differentiation, and is hardly called barcodes. The use of "Human Brain Barcodes" in the title and across the whole paper lacks convincing evidence - it is questionable that CpG methylation is always stably inherited by daughter cells.

Strengths:

Analysis of DNA methylation.

Weaknesses:

The unstable nature of CpG methylation would introduce significant problems in inferring the true cell lineage. To establish DNA methylation as a means for lineage tracing, it is necessary to test whether the DNA methylation patterns can faithfully track cell lineages with in vitro differentiated & visibly tracked cell lineages.

The unreliable CpG methylation status also raises the question of what the "Barcodes" refer to in the title and across this study. Barcodes should be stable in principle and not dynamic across cell generations, as defined in the Reference #1. The CRISPR/Cas9 mutable barcodes or the somatic mutations may be considered barcodes, but the reviewer is not convinced that the "dynamic" CpG methylation fits the "barcodes" terminology. This problem is even more concerning in the last section of the results, where CpG status fluctuates in post-mitotic cells.

The manuscript frequently states assumptions in a tone of conclusions and interprets results without rejecting alternative hypotheses. For example, the title "Human Brain Barcodes" should be backed with solid supporting evidence. For another example, the author assumed that the early-formed brain stem would resemble progenitors better and have a higher average methylation level than the forebrain - however, this difference in DNA methylation status could well reflect cell-type-specific gene expression instead of cell lineage progression.

Other points:

(1) The conclusion that excitatory neurons undergo tangential migration is unclear - how far away did the author mean for the tangential direction? Lateral dispersion is known, but it is hard to believe that the excitatory neurons travel across different brain regions. More importantly, how would the author interpret shared or divergent methylation for the same cell type across different brain regions?

(2) The sparsity and resolution of the single-cell DNA methylation data. The methylation status is detected in only a small fraction (~500/31,000 = 1.6%) of fCpGs per cell, with only 48 common sites identified between cell pairs. Given that the human genome contains over 28 million CpG sites, it is important to evaluate whether these fCpGs are truly representative.

(3) While focusing on the X-chromosome may simplify the identification of polymorphic fCpGs, the confidence in determining its methylation status (0 or 1) is questionable when a CpG site is covered by only one read.

Reviewer #1 (Public review):

Summary:

The authors intended to investigate the earliest mechanisms enabling self-prioritization, especially in the attention. Combining a temporal order judgement task with computational modelling based on the Theory of Visual Attention (TVA), the authors suggested that the shapes associated with the self can fundamentally alter the attentional selection of sensory information into awareness. This self-prioritization in attentional selection occurs automatically at early perceptual stages. Furthermore, the processing benefits obtained from attentional selection via self-relatedness and physical salience were separated from each other.

Strengths:

The manuscript is written in a way that is easy to follow. The methods of the paper are very clear and appropriate.

Comments on revisions:

The authors clearly showed the relationship between attention and self-prioritization.

Reviewer #2 (Public review):

Summary:

The main aim of this research was to explore whether and how self-associations (as opposed to other-associations) bias early attentional selection, and whether this can explain well-known self-prioritization phenomena, such as the self-advantage in perceptual matching tasks. The authors adopted the Visual Attention Theory (VAT) by estimating VAT parameters using a hierarchical Bayesian model from the field of attention and applied it to investigate the mechanisms underlying self-prioritization. They also discussed the constraints on the self-prioritization effect in attentional selection. The key conclusions reported were: (1) self-association enhances both attentional weights and processing capacity, (2) self-prioritization in attentional selection occurs automatically but diminishes when active social decoding is required, and (3) social and perceptual salience capture attention through distinct mechanisms.

Strengths:

Transferring the Theory of Visual Attention parameters estimated by a hierarchical Bayesian model to investigate self-prioritization in attentional selection was a smart approach. This method provides a valuable tool for accessing the very early stages of self-processing, i.e., the attention selection. The authors conclude that self-associations can bias visual attention by enhancing both attentional weights and processing capacity, and that this process occurs automatically. These findings offer new insights into the self-prioritization from the perspective of early stage of attentional selection.

Weaknesses:

The results are still not convincing enough to definitively support their conclusions. The generalization of the findings needs further examination. Whether this attentional selection mechanism of self-prioritization can be generalized to other stimuli, such as self-name, self-face, or other domains of self-association advantages, remains to be tested. More empirical data are needed.

Reviewer #1 (Public review):

Summary:

Aicardi-Goutières Syndrome (AGS) is a genetic disorder that primarily affects the brain and immune system through excessive interferon production. The authors sought to investigate the role of microglia in AGS by first developing bone-marrow-derived progenitors in vitro that carry the estrogen-regulated (ER) Hoxb8 cassette, allowing them to expand indefinitely in the presence of estrogen and differentiate into macrophages when estrogen is removed. When injected into the brains of Csf1r-/- mice, which lack microglia, these cells engraft and resemble wild-type (WT) microglia in transcriptional and morphological characteristics, although they lack Sall1 expression. The authors then generated CRISPR-Cas9 Adar1 knockout (KO) ER-Hoxb8 macrophages, which exhibited increased production of inflammatory cytokines and upregulation of interferon-related genes. This phenotype could be rescued using a Jak-Stat inhibitor or by concurrently mutating Ifih1 (Mda5). However, these Adar1-KO macrophages fail to successfully engraft in the brain of both Csf1r-/- and Cx3cr1-creERT2:Csf1rfl/fl mice. To overcome this, the authors used a mouse model with a patient-specific Adar1 mutation (Adar1 D1113H) to derive ER-Hoxb8 bone marrow progenitors and macrophages. They discovered that Adar1 D1113H ER-Hoxb8 macrophages successfully engraft the brain, although at lower levels than WT-derived ER-Hoxb8 macrophages, leading to increased production of Isg15 by neighboring cells. These findings shed new light on the role of microglia in AGS pathology.

Strengths:

The authors convincingly demonstrate that ER-Hoxb8 differentiated macrophages are transcriptionally and morphologically similar to bone marrow-derived macrophages. They also show evidence that when engrafted in vivo, ER-Hoxb8 microglia are transcriptomically similar to WT microglia. Furthermore, ER-Hoxb8 macrophages engraft the Csf1r-/- brain with high efficiency and rapidly (2 weeks), showing a homogenous distribution. The authors also effectively use CRISPR-Cas9 to knock out TLR4 in these cells with little to no effect on their engraftment in vivo, confirming their potential as a model for genetic manipulation and in vivo microglia replacement.

Weaknesses:

The robust data showing the quality of this model at the transcriptomic level can be strengthened with confirmation at protein and functional levels. The authors were unable to investigate the effects of Adar1-KO using ER-Hoxb8 cells and instead had to rely on a mouse model with a patient-specific Adar1 mutation (Adar1 D1113H). Additionally, ER-Hoxb8-derived microglia do not express Sall1, a key marker of microglia, which limits their fidelity as a full microglial replacement, as has been rightfully pointed out in the discussion.

Overall, this paper demonstrates an innovative approach to manipulating microglia using ER-Hoxb8 cells as surrogates. The authors present convincing evidence of the model's efficacy and potential for broader application in microglial research, given its ease of production and rapid brain engraftment potential in microglia-deficient mice. While Adar1-KO macrophages do not engraft well, the success of TLR4-KO line highlights the model's potential for investigating other genes. Using mouse-derived cells for transplantation reduces complications that can come with the use of human cell lines, highlighting the utility of this system for research in mouse models.

Reviewer #2 (Public review):

Summary:

Microglia have been implicated in brain development, homeostasis, and diseases. "Microglia replacement" has gained traction in recent years, using primary microglia, bone marrow or blood-derived myeloid cells, or human iPSC-induced microglia. Here, the authors extended their previous work in the area and provided evidence to support: (1) Estrogen-regulated (ER) homeobox B8 (Hoxb8) conditionally immortalized macrophages from bone marrow can serve as stable, genetically manipulated cell lines. These cells are highly comparable to primary bone marrow-derived (BMD) macrophages in vitro, and, when transplanted into a microglia-free brain, engraft the parenchyma and differentiate into microglia-like cells (MLCs). Taking advantage of this model system, the authors created stable, Adar1-mutated ER-Hoxb8 lines using CRISPR-Cas9 to study the intrinsic contribution of macrophages to the Aicardi-Goutières Syndrome (AGS) disease mechanism.

Strengths:

The studies are carefully designed and well-conducted. The imaging data and gene expression analysis are carried out at a high level of technical competence and the studies provide strong evidence that ER-Hoxb8 immortalized macrophages from bone marrow are a reasonable source for "microglia replacement" exercise. The findings are clearly presented, and the main message will be of general interest to the neuroscience and microglia communities.

Joint Public Review:

Summary:

Microfossils from the Paleoarchean Eon represent the oldest evidence of life, but their nature has been strongly debated among scientists. To resolve this, the authors reconstructed the lifecycles of Archaean organisms by transforming a Gram-positive bacterium into a primitive lipid vesicle-like state and simulating early Earth conditions. They successfully replicated all morphologies and life cycles of Archaean microfossils and studied cell degradation processes over several years, finding that encrustation with minerals like salt preserved these cells as fossilized organic carbon. Their findings suggest that microfossils from 3.8 to 2.5 billion years ago were likely liposome-like protocells with energy conservation pathways but without regulated morphology.

Strengths:

The authors have crafted a compelling narrative about the morphological similarities between microfossils from various sites and proliferating wall-deficient bacterial cells, providing detailed comparisons that have never been demonstrated in this detail before. The extensive number of supporting figures is impressive, highlighting numerous similarities. While conclusively proving that these microfossils are proliferating protocells morphologically akin to those studied here is challenging, we applaud this effort as the first detailed comparison between microfossils and morphologically primitive cells.

Summary of reviewer comments on this revision:

Each of the original reviewers evaluated the revised manuscript and were complimentary about how the authors addressed their original concerns. One reviewer added: "It is a thought-provoking manuscript that will be well received." We encourage readers of this version of the paper to consider the original reviewer comments and the authors' responses: https://elifesciences.org/reviewed-preprints/98637/reviews

Reviewer #1 (Public review):

Summary:

In their manuscript, the authors provide compelling evidence that stimulus-frequency otoacoustic emission (SFOAE) phase-gradient delays predict the sharpness (quality factors) of auditory-nerve-fiber (ANF) frequency tuning curves in budgerigars. In contrast with mammals, neither SFOAE- nor ANF-based measures of cochlear tuning match the frequency dependence of behavioral tuning in this species of parakeet. Although the reason for the discrepant behavioral results (taken from previous studies) remains unexplained, the present data provide significant and important support for the utility of otoacoustic estimates of cochlear tuning, a methodology previously explored only in mammals.

Strengths:

* The OAE and ANF data appear solid and believable. (The behavioral data are taken from previous studies.)

* No other study in birds (and only a single previous study in mammals) has combined behavioral, auditory-nerve, and otoacoustic estimates of cochlear tuning in a single species.

* SFOAE-based estimates of cochlear tuning now avoid possible circularity and were are obtained by assuming that the tuning ratio estimated in chicken applies also to the budgerigar.

Weaknesses:

* In mammals, accurate prediction of neural Q_ERB from otoacoustic N_SFOAE involves the application of species-invariance of the tuning ratio combined with an attempt to compensate for possible species differences in the location of the so-called apical-basal transition (for a review, see Shera & Charaziak, Cochlear frequency tuning and otoacoustic emissions. Cold Spring Harb Perspect Med 2019; 9:pii a033498. doi: 10.1101/cshperspect.a033498; in particular, the text near Eq. 2 and the value of CFa|b).

Despite this history, the manuscript makes no mention of the apical-basal transition, its possible role in birds, or why it was ignored in the present analysis. As but one result, the comparative discussion of the tuning ratio (paragraph beginning on lines 383) is incomplete and potentially misleading. Although the paragraph highlights differences in the tuning ratio across groups, perhaps these differences simply reflect differences in the value of CFa|b. For example, if the cochlea of the budgerigar is assumed to be entirely "apical" in character (so that CFa|b is around 7-8 kHz), then the budgerigar tuning ratios appear to align remarkably well with those previously obtained in mammals (see Shera et al 2010, Fig 9).

* For the most part, the authors take previous behavioral results in budgerigar at face value, attributing the discrepant behavioral results to hypothesized "central specializations for the processing of masked signals". But before going down this easy road, the manuscript would be stronger if the authors discussed potential issues that might affect the reliability of the previous behavioral literature. For example, the ANF data show that thresholds rise rapidly above about 5 kHz. Might the apparent broadening of the behavioral filters arise as<br /> a consequence of off-frequency listening due to the need to increase signal levels at these frequencies? Or perhaps there are other issues. Inquiring readers would appreciate an informed discussion.

Reviewer #2 (Public review):

Summary:

This manuscript describes two new sets of data involving budgerigar hearing: 1) auditory-nerve tuning curves (ANTCs), which are considered the 'gold standard' measure of cochlear tuning, and 2) stimulus-frequency otoacoustic emissions (SFOAEs), which are a more indirect measure (requiring some assumptions and transformations to infer cochlear tuning) but which are non-invasive, making them easier to obtain and suitable for use in all species, including humans. By using a tuning ratio (relating ANTC bandwidths and SFOAE delay) derived from another bird species (chicken), the authors show that the tuning estimates from the two methods are in reasonable agreement with each other over the range of hearing tested (280 Hz to 5.65 kHz for the ANTCs), and both show a slow monotonic increase in cochlear tuning quality over that range, as expected. These new results are then compared with (much) older existing behavioral estimates of frequency selectivity in the same species.

Strengths:

This topic is of interest, because there are some indications from the older behavioral literature that budgerigars have a region of best tuning, which the current authors refer to as an 'acoustic fovea', at around 4 kHz, but that beyond 5 kHz the tuning degrades. Earlier work has speculated that the source could be cochlear or higher (e.g., Okanoya and Dooling, 1987). The current study appears to rule out a cochlear source to this phenomenon.

Weaknesses:

The conclusions are rendered questionable by two major problems.

The first problem is that the study does not provide new behavioral data, but instead relies on decades-old estimates that used techniques dating back to the 1970s, which have been found to be flawed in various ways. The behavioral techniques that have been developed more recently in the human psychophysical literature have avoided these well-documented confounds, such as nonlinear suppression effects (e.g., Houtgast, https://doi.org/10.1121/1.1913048; Shannon, https://doi.org/10.1121/1.381007; Moore, https://doi.org/10.1121/1.381752), perceptual confusion between pure-tone maskers and targets (e.g., Neff, https://doi.org/10.1121/1.393678), beats and distortion products produced by interactions between simultaneous maskers and targets (e.g., Patterson, https://doi.org/10.1121/1.380914), unjustified assumptions and empirical difficulties associated with critical band and critical ratio measures (Patterson, https://doi.org/10.1121/1.380914), and 'off-frequency listening' phenomena (O'Loughlin and Moore, https://doi.org/10.1121/1.385691). More recent studies, tailored to mimic to the extent possible the techniques used in ANTCs, have provided reasonably accurate estimates of cochlear tuning, as measured with ANTCs and SFOAEs (Shera et al., 2003, 2010; Sumner et al., 2010). No such measures yet exist in budgerigars, and this study does not provide any. So the study fails to provide valid behavioral data to support the claims made.

The second, and more critical, problem can be observed by considering the frequencies at which the old behavioral data indicate a worsening of tuning. From the summary shown in the present Fig. 2, the conclusion that behavioral frequency selectivity worsens again at higher frequencies is based on four data points, all with probe frequencies between 5 and 6 kHz. Comparing this frequency range with the absolute thresholds shown in Fig. 3 (as well as from older budgerigar data) shows it to be on the steep upper edge of the hearing range. Thus, we are dealing not so much with a fovea as the point where hearing starts to end. The point that anomalous tuning measures are found at the edge of hearing in the budgerigar has been made before: Saunders et al. (1978) state in the last sentence of their paper that "the size of the CB rapidly increases above 4.0 kHz and this may be related to the fact that the behavioral audibility curve, above 4.0 kHz, loses sensitivity at the rate of 55 dB per octave."

Hearing abilities are hard to measure accurately on the upper frequency edge of the hearing range, in humans as well as in other species. The few attempts to measure human frequency selectivity at that upper edge have resulted in quite messy data and unclear conclusions (e.g., Buus et al., 1986, https://doi.org/10.1007/978-1-4613-2247-4_37). Indeed, the only study to my knowledge to have systematically tested human frequency selectivity in the extended high frequency range (> 12 kHz) seems to suggest a substantial broadening, relative to the earlier estimates at lower frequencies, by as much as a factor of 2 in some individuals (Yasin and Plack, 2005; https://doi.org/10.1121/1.2035594) - in other words by a similar amount as suggested by the budgerigar data. The possible divergence of different measures at the extreme end of hearing could be due to any number of factors that are hard to control and calibrate, given the steep rate of threshold change, leading to uncontrolled off-frequency listening potential, the higher sound levels needed to exceed threshold, as well as contributions from middle-ear filtering. As a side note, in the original ANTC data presented in this study, there are actually very few tuning curves at or above 5 kHz, which are the ones critical to the argument being forwarded here. To my eye, all the estimates above 5 kHz in Fig. 3 fall below the trend line, potentially also in line with poorer selectivity going along with poorer sensitivity as hearing disappears beyond 6 kHz.

The basic question posed in the current study title and abstract seems a little convoluted (why would you expect a behavioral measure to reflect cochlear mechanics more accurately than a cochlear-based emissions measure?). A more intuitive (and likely more interesting) way of framing the question would be "What is the neural/mechanical source of a behaviorally observed acoustic fovea?" Unfortunately, this question does not lend itself to being answered in the budgerigar, as that 'fovea' turns out to be just the turning point at the end of the hearing range. There is probably a reason why no other study has referred to this as an acoustic fovea in the budgerigar.

Overall, a safe interpretation of the data is that hearing starts to change (and becomes harder to measure) at the very upper frequency edge, and not just in budgerigars. Thus, it is difficult to draw any clear conclusions from the current work, other than that the relations between ANTC and SFOAEs estimates of tuning are consistent in budgerigar, as they are in most (all?) other species that have been tested so far.

Reviewer #1 (Public review):

Tu, Wen, et al. investigated the activity of mPFC putative glutamatergic neurons during a probabilistic threat discrimination and avoidance learning task using miniaturized GRIN lens implantation and single-photon calcium imaging in freely moving mice. In conjunction with this cellular recording, they employed channelrhodopsin-mediated optogenetic excitation of terminals from basal forebrain cholinergic projection neurons coupled to the delivery of an air puff on either of two maze paths with differential threat probability. The authors found that the optogenetic manipulation altered mPFC encoding of outcomes and disrupted animals' behavioral adaptation. Over the course of multiple learning sessions, optogenetically stimulated mice lagged behind control animals in resolving the differential threat probabilities on the two paths and making adaptive choices. In particular, the animals with optogenetic stimulation of cholinergic terminals were significantly more likely to switch to the path with higher threat probability after having just gotten a rare air puff on the generally "safer" path. Combined with data from a deterministic version of the task showing that optogenetically stimulated mice could behaviorally discriminate between the paths appropriately under such circumstances, these results suggest an impairment in the experimental animals' ability to make use of threat history over multiple trials. This comparison of probabilistic and deterministic versions of the same task is a highlight of this paper, representing a thoughtfulness about what information can be gleaned from such variations in the design of behavioral experiments that is all too often lacking. These data are timely in contributing to an ongoing discussion in the field about the role of phasic cholinergic signaling to the cortex, about which relatively little is known.

While the ensemble recording of mPFC neurons during the task appears to be reliable and well-designed and the behavioral effects of the optogenetic stimulation are convincing, some major weaknesses of the paper limit its usefulness to others in the field:

(1) Optogenetic excitation of presynaptic terminals can lead to antidromic action potentials that alter the firing properties of the target cell (see the excellent review on challenges of and strategies for presynaptic optogenetic experiments Rost et al., Nat Neurosci 2022). To their credit, the authors explicitly acknowledge this fact, but they believe that the only alternative possibility is that their intervention could lead to increased acetylcholine release at collateral projections in other prefrontal subregions. In fact, we do not know that the mechanism mediating the behavioral changes observed involves acetylcholine at all, as many ChAT+ basal forebrain neurons co-transmit using GABA (Saunders et al., Nature, 2015; Saunders et al., eLife, 2015; Granger et al., Neuropharmacology, 2016). A very useful internal control, which is recommended by Rost et al. for such presynaptic excitation experiments, would be to locally infuse nicotinic or muscarinic cholinergic antagonists into the mPFC in an attempt to reverse the optogenetically induced deficit; this would resolve whether the effect is indeed mediated by cholinergic neurotransmission and if it is specific to the mPFC.

(2) In a similar vein, the fact that LED illumination in the no-opsin control group appears to increase activity in prefrontal neurons (Figure 2C) and, moreover, has a functional effect in disrupting location-selective cellular activity to a similar extent as in the ChrimsonR group (Figure S3) is inadequately explained and cause for concern. Although the authors argue that the degree or "robustness" of puff-evoked activity was significantly greater in the ChrimsonR group as compared to fluorophore-only controls, their statistical test for demonstrating this is the Kolmogorov-Smirnov test (Figure 2D), thus showing that the two samples likely are drawn from different distributions but little else.

(3) Throughout the paper, the authors rely heavily on the Kolmogorov-Smirnov and binomial tests (Figures 2D, 3, 4D, S3, S4) to compare distributions in this manner, but it is unclear to me why these would be the most appropriate statistical tests for what they seek to demonstrate. Given the holistic nature of these tests in comparing the shape and spread of distributions, I am concerned that they might be inflating the significance of the differences between groups. Even if the authors were seeking a nonparametric statistical test, which most likely would be quite appropriate, there are nonparametric versions of ANOVA that they could use (e.g. Kruskal-Wallis, Friedman). Indeed, in much of this data set a repeated measures statistical analysis would seem to be called for, whereas the Kolmogorov-Smirnov test assumes that the two samples must be independent of each other. The most notable example of this premise being violated is in Figure 3, where data from the same cell populations in the same animals are being compared between experimental days and across various trial types.

Reviewer #2 (Public review):

Summary:

The authors tested:

(1) Whether mice learn that they are more/less likely to receive an aversive air puff outcome at different corners of a square-shaped open field apparatus, under 75%/25% probabilistic contingencies;

(2) Whether stimulating basal forebrain cholinergic neurons and terminals in the prefrontal cortex affects learning in this context; and

(3) Whether stimulating cholinergic neurons affects prefrontal cortical single neuron calcium signaling about outcome expectations during learning and contingency changes. They found that mice that received cholinergic stimulation approached high and low aversive outcome probability sites at similar velocities, while control mice approached high probability sites slower, suggesting that cholinergic stimulation impaired learning. Cholinergic stimulation reduced cortical neuron calcium activity during trials on the high-probability corner when the outcome was not delivered. The authors provide additional characterization of cellular responses during delivery/omission trials in high/low probability corners, using running speed as a proxy for low versus high expectations. The study will likely be of interest to those who are interested in prediction and error signaling in the cortex; however, the task and analyses do not permit very easy or clear dissociation of prediction versus prediction error signaling and place field versus place field-expectation multiplexing. The study has several strengths but some weaknesses, which are discussed below.

Strengths:

It is clear the authors were very careful and did a great job with their image processing and segmentation procedures. The details in the methods are appreciated, as are the supplemental descriptive statistics on cell counts.

There are careful experimental controls - for example, the authors showed that the effects of cholinergic stimulation with air puff present are greater than without it, thus ruling out effects of stimulation on cellular physiology that were independent of learning or the task.

The addition of a channelrhodopsin stimulation group is helpful to show that the effects are robust and not wavelength/opsin-specific.

The prefrontal cortex cholinergic terminal stimulation experiment is a great addition. It shows that the behavioral effects of cell body stimulation, which was used in the imaging experiments, are similar to cortical terminal stimulation, where the imaging was performed.

Weaknesses:

The analyses were a bit difficult to follow and therefore it is difficult to determine whether the cells are signaling predictions versus prediction errors - a very important distinction.

The task does not fully dissociate place field coding, since learning about the different probabilities necessarily took place at different areas in the apparatus. Some additional analyses could help address this.

Reviewer #3 (Public review):

Summary:

Using a combination of optogenetic tools and single-photon calcium imaging, the authors collected a set of high-quality data and conducted thorough analyses to demonstrate the importance of cholinergic input to the prelimbic cortex in probabilistic spatial learning, particularly pertaining to threat.

Strengths:

Given the importance of the findings, this paper will appeal to a broad audience in the systems, behavioural, and cognitive neuroscience community.

Weaknesses:

I have only a few concerns that I consider need to be addressed.

(1) Can the authors describe the basic effect of cholinergic stimulation on PL neurons' activity, during pretraining, probabilistic, and random stages? From the plot, it seems that some neurons had an increase and others had a decrease in activity. What are the percentages for significant changes in activities, given the intensity of stimulation? Were these changes correlated with the neurons' selectivity for the location? If they happen to have the data, a dose-response plot would be very helpful too.

(2) Figure 2B: The current sorting does not show the effects of puff and LED well. Perhaps it's best to sort based on the 'puff with no stim' condition in the middle, by the total activity in 2s following the puff, and then by the timing in the rise/drop of activity (from early to late). This way perhaps the optogenetic stimulation would appear more striking. Figure 3Aa and Ba have the same issue: by the current sorting, the effects are not very visible at all. Perhaps they want to consider not showing the cells that did not show the effect of puff and/or LED.

Also, I would recommend that the authors use ABCD to refer to figure panels, instead of Aa, Ab, etc. This is very hard to follow.

(3) The authors mentioned the laminar distribution of ACh receptors in discussion. Can they show the presence/absence of topographic distribution of neurons responding to puff and/or LED?

(4) Figure 2C seems to show only neurons with increased activity to an air puff. It's also important to know how neurons with an inhibitory response to air-puff behaved, especially given that in tdTomato animals, the proportion of these neurons was the same as excitatory responders.

(5) Page 5, lines 107 and 110: Following 2-way ANOVA, the authors used a 'follow-up 1-way rmANOVA' and 'follow-up t-test' instead of post hoc tests (e.g. Tukey's). This doesn't seem right. Please use post hoc tests instead to avoid the problem of multiple comparisons.

(6) Figure 1H: in the running speed analysis, were all trials included, both LED+ and LED-? This doesn't affect the previous panels in Figure 1 but it could affect 1H. Did stimulation affect how the running speed recovers?

On a related note, does a surprising puff/omission affect the running speed on the subsequent trial?

(7) On Page 7, line 143, it says "In the absence of LED stimulation, the magnitude of their puff-evoked activity was reduced in ChrimsonR-expressing mice...", but then on line 147 it says "This group difference was not detected without the LED stimulation". I don't follow what is meant by the latter statement, it seems to be conflicting with line 143. The red curves in the left vs right panels do not seem different. The effect of air puff seems to differ, but is this due to a higher gray curve ('no puff' condition) in the ChrimsonR group?

(8) Did the neural activity correlate with running speed? Since the main finding was the absence of difference in running speed modulation by probability in ChrimsonR mice, one would expect to see PL cells showing parallel differences.

Reviewer #1 (Public review):

This manuscript presents an interesting exploration of the potential activation mechanisms of DLK following axonal injury. While the experiments are beautifully conducted and the data are solid, I feel that there is insufficient evidence to fully support the conclusions made by the authors.

In this manuscript, the authors exclusively use the puc-lacZ reporter to determine the activation of DLK. This reporter has been shown to be induced when DLK is activated. However, there is insufficient evidence to confirm that the absence of reporter activation necessarily indicates that DLK is inactive. As with many MAP kinase pathways, the DLK pathway can be locally or globally activated in neurons, and the level of DLK activation may depend on the strength of the stimulation. This reporter might only reflect strong DLK activation and may not be turned on if DLK is weakly activated. The results presented in this manuscript support this interpretation. Strong stimulation, such as axotomy of all synaptic branches, caused robust DLK activation, as indicated by puc-lacZ expression. In contrast, weak stimulation, such as axotomy of some synaptic branches, resulted in weaker DLK activation, which did not induce the puc-lacZ reporter. This suggests that the strength of DLK activation depends on the severity of the injury rather than the presence of intact synapses. Given that this is a central conclusion of the study, it may be worthwhile to confirm this further. Alternatively, the authors may consider refining their conclusion to better align with the evidence presented.

As noted by the authors, DLK has been implicated in both axon regeneration and degeneration. Following axotomy, DLK activation can lead to the degeneration of distal axons, where synapses are located. This raises an important question: how is DLK activated in distal axons? The authors might consider discussing the significance of this "synapse connection-dependent" DLK activation in the broader context of DLK function and activation mechanisms.

Reviewer #2 (Public review):

Summary:

The authors study a panel of sparsely labeled neuronal lines in Drosophila that each form multiple synapses. Critically, each axonal branch can be injured without affecting the others, allowing the authors to differentiate between injuries that affect all axonal branches versus those that do not, creating spared branches. Axonal injuries are known to cause Wnd (mammalian DLK)-dependent retrograde signals to the cell body, culminating in a transcriptional response. This work identifies a fascinating new phenomenon that this injury response is not all-or-none. If even a single branch remains uninjured, the injury signal is not activated in the cell body. The authors rule out that this could be due to changes in the abundance of Wnd (perhaps if incrementally activated at each injured branch) by Wnd, Hiw's known negative regulator. Thus there is both a yet-undiscovered mechanism to regulate Wnd signaling, and more broadly a mechanism by which the neuron can integrate the degree of injury it has sustained. It will now be important to tease apart the mechanism(s) of this fascinating phenomenon. But even absent a clear mechanism, this is a new biology that will inform the interpretation of injury signaling studies across species.

Strengths:

(1) A conceptually beautiful series of experiments that reveal a fascinating new phenomenon is described, with clear implications (as the authors discuss in their Discussion) for injury signaling in mammals.

(2) Suggests a new mode of Wnd regulation, independent of Hiw.

Weaknesses:

(1) The use of a somatic transcriptional reporter for Wnd activity is powerful, however, the reporter indicates whether the transcriptional response was activated, not whether the injury signal was received. It remains possible that Wnd is still activated in the case of a spared branch, but that this activation is either local within the axons (impossible to determine in the absence of a local reporter) or that the retrograde signal was indeed generated but it was somehow insufficient to activate transcription when it entered the cell body. This is more of a mechanistic detail and should not detract from the overall importance of the study

(2) That the protective effect of a spared branch is independent of Hiw, the known negative regulator of Wnd, is fascinating. But this leaves open a key question: what is the signal?

Reviewer #3 (Public review):

Summary:

This manuscript seeks to understand how nerve injury-induced signaling to the nucleus is influenced, and it establishes a new location where these principles can be studied. By identifying and mapping specific bifurcated neuronal innervations in the Drosophila larvae, and using laser axotomy to localize the injury, the authors find that sparing a branch of a complex muscular innervation is enough to impair Wallenda-puc (analogous to DLK-JNK-cJun) signaling that is known to promote regeneration. It is only when all connections to the target are disconnected that cJun-transcriptional activation occurs.

Overall, this is a thorough and well-performed investigation of the mechanism of spared-branch influence on axon injury signaling. The findings on control of wnd are important because this is a very widely used injury signaling pathway across species and injury models. The authors present detailed and carefully executed experiments to support their conclusions. Their effort to identify the control mechanism is admirable and will be of aid to the field as they continue to try to understand how to promote better regeneration of axons.

Strengths:

The paper does a very comprehensive job of investigating this phenomenon at multiple locations and through both pinpoint laser injury as well as larger crush models. They identify a non-hiw based restraint mechanism of the wnd-puc signaling axis that presumably originates from the spared terminal. They also present a large list of tests they performed to identify the actual restraint mechanism from the spared branch, which has ruled out many of the most likely explanations. This is an extremely important set of information to report, to guide future investigators in this and other model organisms on mechanisms by which regeneration signaling is controlled (or not).

Weaknesses:

The weakest data presented by this manuscript is the study of the actual amounts of Wallenda protein in the axon. The authors argue that increased Wnd protein is being anterogradely delivered from the soma, but no support for this is given. Whether this change is due to transcription/translation, protein stability, transport, or other means is not investigated in this work. However, because this point is not central to the arguments in the paper, it is only a minor critique.

As far as the scope of impact: because the conclusions of the paper are focused on a single (albeit well-validated) reporter in different types of motor neurons, it is hard to determine whether the mechanism of spared branch inhibition of regeneration requires wnd-puc (DLK/cJun) signaling in all contexts (for example, sensory axons or interneurons). Is the nerve-muscle connection the rule or the exception in terms of regeneration program activation?

Because changes in puc-lacZ intensity are the major readout, it would be helpful to better explain the significance of the amount of puc-lacZ in the nucleus with respect to the activation of regeneration. Is it known that scaling up the amount of puc-lacZ transcription scales functional responses (regeneration or others)? The alternative would be that only a small amount of puc-lacZ is sufficient to efficiently induce relevant pathways (threshold response).

Reviewer #1 (Public review):

This study identifies two behavioral processes that underlie learned pathogen avoidance behavior in C. elegans: exiting and re-entry of pathogenic bacterial lawns. Long-term behavioral tracking indicates that animals increase the prevalence of both behaviors over long-term exposure to the pathogen Pseudomonas aeruginosa. Using an optogenetic silencing screen, the authors identify groups of neurons, whose activity regulates lawn occupancy. Surprisingly, they find that optogenetic inhibition of neurons during only the first two hours of pathogen exposure can establish subsequent long-term changes in pathogen aversion. By leveraging a compressed sensing approach, the authors define a set of neurons involved in either lawn exit or lawn re-entry behavior using a constrained set of transgenic lines that drive Arch-3 expression in overlapping groups of neurons. They then measure the calcium activity of the candidate neurons involved in lawn re-entry in freely moving animals using GCaMP, and observe a reduction in their neural activity after exposure to pathogen. Optogenetic inhibition of AIY and SIA neurons during acute pathogen exposure in naïve animals delays lawn entry whereas activating these neurons in animals previously exposed to pathogen enhances lawn entry, albeit transiently.

This work is missing experiments and analyses that are necessary to substantiate their claims. Although the authors convincingly show that neuronal inhibition experiments during pathogen exposure reveal separable groups of neurons controlling pathogenic lawn exiting and re-entry, their methods to validate these results at single neuron cell-type resolution lack rigor.

In Figure 4, the authors claim that the reduction in calcium activity in cells of interest following pathogen exposure encodes pathogen experience. However, they make no effort to correlate the observed decreased activity with concomitant shifts in increased immobility (decreased forward locomotion) or the increased age of the worms since pathogen exposure began (24 hours have elapsed), either of which could easily explain these results. A better comparison would be between age-matched naive animals and animals exposed to pathogen. More to the point, we are interested in the involvement of these neurons' activity patterns with the behavioral motifs associated with lawn exits and re-entries, so examining these activity patterns in the absence of any pathogen before or after long-term pathogen exposure yields little insight into their relevant signaling roles. To substantiate the authors' claims, a better experiment would measure these neurons' calcium activity during lawn exits and re-entries in naive and post-exposed age-matched worms.

In Figure 5, the authors attempt to show that manipulating AIY and SIA/SIB neuronal activity controls pathogenic lawn re-entry behavior. Although they show that inhibiting these neurons in naive animals increases latency to enter pathogenic lawns, they never test the effect of neuronal inhibition in post-exposed animals. Instead they activate these neurons using channelrhodopsin, whereby they observe an increase in lawn entry and exit behavior, indicative of high forward locomotion speed. Although suggestive, neither of these experiments prove these neurons' involvement in pathogenic lawn re-entry behavior following pathogen exposure. To rigorously test the hypothesis that AIY and SIA/SIB neurons are required to sustain higher latency to lawn re-entry following pathogen exposure, the authors should perform neuronal inhibition experiments in post-pathogen-exposed animals as well and compare the results. The interpretation of this figure is further complicated by the fact that Npr-4::ChR2 animals express ChR2 in AIY in addition to SIA/SIB neurons: experiments that calculated lawn re-entry rates in Npr-4::ChR2 activation in post-exposed animals may include the known effect of stimulating AIY alone (Fig. 5J) since no discernible attempt at structured illumination to limit excitation to SIA/SIB neurons was made in these animals (Fig. 5 K, L).

This work raises the interesting possibility that different sets of neurons control lawn exit and lawn re-entry behaviors following pathogen exposure. However, the authors never directly test this claim. To rigorously show this, the authors would need to show that lawn-exit promoting neurons (CEPs, HSNs, RIAs, RIDs, SIAs) are dispensable for lawn re-entry behavior and that lawn re-entry promoting neurons (AVK, SIA, AIY, MI) are dispensable for lawn exit behavior in pathogen-exposed animals. The authors identify AVK neurons as important for modulating lawn re-entry behavior by brief inhibition at the start of pathogen exposure but fail to find that these neurons are required for increased latency to re-entry in naïve animals (Fig. 5D). Recent work from Marquina-Solis et al (2024) shows that chronic silencing of these neurons delays pathogen lawn leaving, due to impaired release of flp-1 neuropeptide. Authors may wish to connect their work more closely with the existing literature by investigating the behavioral process by which AVK contributes to lawn evacuation.

Reviewer #2 (Public review):

In this manuscript, Hallacy et al. used a compressed sensing-based optogenetic screening method to investigate the crucial neurons that regulate pathogenic avoidance behavior in C. elegans. They further substantiate their findings using complementary optogenetic activation and imaging techniques to confirm the roles of the key neurons identified through extensive screening efforts. Notably, they identified AIY and SIA as pivotal neurons in the dynamic process of pathogenic avoidance. Their significant discovery is the delayed or stalled reentry process, which drives avoidance behavior; to my knowledge, this dynamic has not been previously documented. Additionally, the successful integration of quantitative optogenetic tools and compressed sensing algorithms is noteworthy, demonstrating the potential for obtaining highly quantitative data from the C. elegans nervous system. This approach is quite rare in this field, yet it represents a promising direction for studying this simple nervous system.

However, the paper's main weakness lies in its lack of a detailed mechanism explaining how the delayed reentry process directly influences the actual locomotor output that results in avoidance. The term 'delayed reentry' is used as a dynamic metric for quantifying the screening, yet the causal link between this metric and the mechanistic output remains unclear. Despite this, the study is well-structured, with comprehensive control experiments, and is very well constructed.

Comments on revisions:

The authors have addressed all my concerns and suggestions. They particularly further clarified the AIY's role in navigation by providing a new figure. They also provided supplementary videos representing the re-entry process.

Reviewer #1 (Public review):

Summary:

In this manuscript by Lopez-Blanch and colleagues, 21 microexons are selected for a deep analysis of their impacts on behavior, development, and gene expression. The authors begin with a systematic analysis of microexon inclusion and conservation in zebrafish and use these data to select 21 microexons for further study. The behavioral, transcriptomic, and morphological data presented are for the most part convincing. Furthermore, the discussion of the potential explanations for the subtle impacts of individual microexon deletions versus loss-of-function in srrm3 and/or srrm4 is quite comprehensive and thoughtful. One major weakness: data presentation, methods, and jargon at times affect readability / might lead to overstated conclusions. However, overall this manuscript is well-written, easy to follow, and the results are of broad interest.

Strengths:

(1) The study uses a wide variety of techniques to assess the impacts of microexon deletion, ranging from assays of protein function to regulation of behavior and development.

(2) The authors provide comprehensive analyses of the molecular impact of their microexon deletions, including examining how host-gene and paralog expression is affected.

Weaknesses / Major Points:

(1) According to the methods, it seems that srrm3 social behavior is tested by pairing a 3mpf srrm3 mutant with a 30dpf srrm3 het. Is this correct? The methods seem to indicate that this decision was made to account for a slower growth rate of homozygous srrm3 mutant fish. However, the difference in age is potentially a major confound that could impact the way that srrm3 mutants interact with hets and the way that srrm3 mutants interact with one another (lower spread for the ratio of neighbour in front value, higher distance to neighbour value). This reviewer suggests testing het-het behavior at 3 months to provide age-matched comparisons for del-del, testing age-matched rather than size-matched het-del behavior, and also suggests mentioning this in the main text / within the figure itself so that readers are aware of the potential confound.

(2) Referring to srrm3+/+; srrm4-/- controls for double mutant behavior as "WT for simplicity" is somewhat misleading. Why do the authors not refer to these as srrm4 single mutants?

(3) It's not completely clear how "neurally regulated" microexons are defined / how they are different from "neural microexons"? Are these terms interchangeable?

(4) Overexpression experiments driving srrm3 / srrm4 in HEK293 cells are not described in the methods.

(4) Suggest including more information on how neurite length was calculated. In representative images, it appears difficult to determine which neurites arise from which soma, as they cross extensively. How was this addressed in the quantification?

Reviewer #2 (Public review):

Summary:

This manuscript explores in zebrafish the impact of genetic manipulation of individual microexons and two regulators of microexon inclusion (Srrm3 and Srrm4). The authors compare molecular, anatomical, and behavioral phenotypes in larvae and juvenile fish. The authors test the hypothesis that phenotypes resulting from Srrm3 and 4 mutations might in part be attributable to individual microexon deletions in target genes.

The authors uncover substantial alterations in in vitro neurite growth, locomotion, and social behavior in Srrm mutants but not any of the individual microexon deletion mutants. The individual mutations are accompanied by broader transcript level changes which may resemble compensatory changes. Ultimately, the authors conclude that the severe Srrm3/4 phenotypes result from additive and/or synergistic effects due to the de-regulation of multiple microexons.

Strengths:

The work is carefully planned, well-described, and beautifully displayed in clear, intuitive figures. The overall scope is extensive with a large number of individual mutant strains examined. The analysis bridges from molecular to anatomical and behavioral read-outs. Analysis appears rigorous and most conclusions are well-supported by the data.

Overall, addressing the function of microexons in an in vivo system is an important and timely question.

Weaknesses:

The main weakness of the work is the interpretation of the social behavior phenotypes in the Srrm mutants. It is difficult to conclude that the mutations indeed impact social behavior rather than sensory processing and/or vision which precipitates apparent social alterations as a secondary consequence. Interpreting the phenotypes as "autism-like" is not supported by the data presented.

Reviewer #3 (Public review):

Summary:

Microexons are highly conserved alternative splice variants, the individual functions of which have thus far remained mostly elusive. The inclusion of microexons in mature mRNAs increases during development, specifically in neural tissues, and is regulated by SRRM proteins. Investigation of individual microexon function is a vital avenue of research since microexon inclusion is disrupted in diseases like autism. This study provides one of the first rigorous screens (using zebrafish larvae) of the functions of individual microexons in neurodevelopment and behavioural control. The authors precisely excise 21 microexons from the genome of zebrafish using CRISPR-Cas9 and assay the downstream impacts on neurite outgrowth, larvae motility, and sociality. A small number of mild phenotypes were observed, which contrasts with the more dramatic phenotypes observed when microexon master regulators SRRM3/4 are disrupted. Importantly, this study attempts to address the reasons why mild/few phenotypes are observed and identify transcriptomic changes in microexon mutants that suggest potential compensatory gene regulatory mechanisms.

Strengths:

(1) The manuscript is well written with excellent presentation of the data in the figures.

(2) The experimental design is rigorous and explained in sufficient detail.

(3) The identification of a potential microexon compensatory mechanism by transcriptional alterations represents a valued attempt to begin to explain complex genetic interactions.

(4) Overall this is a study with a robust experimental design that addresses a gap in knowledge of the role of microexons in neurodevelopment.

Reviewer #1 (Public review):

Summary:

The authors aimed to investigate the cellular mechanisms underlying place field formation (PFF) in hippocampal CA1 pyramidal cells by performing in vivo two-photon calcium imaging in head-restrained mice navigating a virtual environment. Specifically, they sought to determine whether BTSP-like (behavioral time scale synaptic plasticity) events, characterized by large calcium transients, are the primary mechanism driving PFFs or if other mechanisms also play a significant role. Through their extensive imaging dataset, the authors found that while BTSP-like events are prevalent, a substantial fraction of new place fields are formed via non-BTSP-like mechanisms. They further observed that large calcium transients, often associated with BTSP-like events, are not sufficient to induce new place fields, indicating the presence of additional regulatory factors (possibly local dendritic spikes).

Strengths

The study makes use of a robust and extensive dataset collected from 163 imaging sessions across 45 mice, providing a comprehensive examination of CA1 place-cell activity during navigation in both familiar and novel virtual environments. The use of two-photon calcium imaging allows the authors to observe the detailed dynamics of neuronal activity and calcium transients, offering insights into the differences between BTSP-like and non-BTSP-like PFF events. The study's ability to distinguish between these two mechanisms and analyze their prevalence under different conditions is a key strength, as it provides a nuanced understanding of how place fields are formed and maintained. The paper supports the idea that BTSP is not the only driving force behind PFF, and other mechanisms are likely sufficient to drive PFF, and BTSP events may also be insufficient to drive PFF in some cases. The longer-than-usual virtual track used in the experiment allowed place cells to express multiple place fields, adding a valuable dimension to the dataset that is typically lacking in similar studies. Additionally, the authors took a conservative approach in classifying PFF events, ensuring that their findings were not confounded by noise or ambiguous activity.

Weaknesses

Despite the impressive dataset, there are several methodological and interpretational concerns that limit the impact of the findings. Firstly, the virtual environment appears to be poorly enriched, relying mainly on wall patterns for visual cues, which raises questions about the generalizability of the results to more enriched environments. Prior studies have shown that environmental enrichment can significantly influence spatial coding, and it would be important to determine how a more immersive VR environment might alter the observed PFF dynamics. Secondly, the study relies on deconvolution methods in some cases to infer spiking activity from calcium signals without in vivo ground truth validation. This introduces potential inaccuracies, as deconvolution is an estimate rather than a direct measure of spiking, and any conclusions drawn from these inferred signals should be interpreted with caution. Thirdly, the figures would benefit from clearer statistical annotations and visual enhancements. For example, several plots lack indicators of statistical significance, making it difficult for readers to assess the robustness of the findings. Furthermore, the use of bar plots without displaying underlying data distributions obscures variability, which could be better visualized with violin plots or individual data points. The manuscript would also benefit from a more explicit breakdown of the proportion of place fields categorized as BTSP-like versus non-BTSP-like, along with clearer references to figures throughout the results section. Lastly, the authors' interpretation of their data, particularly regarding the sufficiency of large calcium transients for PFF induction, needs to be more cautious. Without direct confirmation that these transients correspond to actual BTSP events (including associated complex spikes and calcium plateau potentials), concluding that BTSP is not necessary or sufficient for PFF formation is speculative.

Reviewer #2 (Public review):

Summary:

The authors of this manuscript aim to investigate the formation of place fields (PFs) in hippocampal CA1 pyramidal cells. They focus on the role of behavioral time scale synaptic plasticity (BTSP), a mechanism proposed to be crucial for the formation of new PFs. Using in vivo two-photon calcium imaging in head-restrained mice navigating virtual environments, employing a classification method based on calcium activity to categorize the formation of place cells' place fields into BTSP, non-BTSP-like, and investigated their properties.

Strengths:

A new method to use calcium imaging to separate BTSP and non-BTSP place field formation. This work offers new methods and factual evidence for other researchers in the field.

The method enabled the authors to reveal that while many PFs are formed by BTSP-like events, a significant number of PFs emerge with calcium dynamics that do not match BTSP characteristics, suggesting a diversity of mechanisms underlying PF formation. The characteristics of place fields under the first two categories are comprehensively described, including aspects such as formation timing, quantity, and width.

Weaknesses:

There are some issues about data and statistics that need to be addressed before these research findings can be considered as rigorous conclusions.

While the authors mentioned 3 features of PF generated by BTSP during calcium imaging in the Introduction, the classification method used features 1 and 2. The confirmation by feature 3 in its current form is important but not strong enough.

Some key data is missing such as the excluded PFs, the BTSP/non-BTSP of each animal, etc

Impact:

This work is likely to provide a new method to classify BTSP and non-BTSP place field formation using calsium image to the field.

Reviewer #3 (Public review):

Summary:

In this manuscript, Sumegi et al. use calcium imaging in head-fixed mice to test whether new place fields tend to emerge due to events that resemble behavioral time scale plasticity (BTSP) or other mechanisms. An impressive dataset was amassed (163 sessions from 45 mice with 500-1000 neurons per sample) to study the spontaneous emergence of new place fields in area CA1 that had the signature of BTSP. The authors observed that place fields could emerge due to BTSP and non-BTSP-like mechanisms. Interestingly, when non-BTSP mechanisms seemed to generate a place field, this tended to occur on a trial with a spontaneous reset in neural coding (a remapping event). Novelty seemed to upregulate non-BTSP events relative to BTSP events. Finally, large calcium transients (presumed plateau potentials) were not sufficient to generate a place field.

Strengths:

I found this manuscript to be exceptionally well-written, well-powered, and timely given the outstanding debate and confusion surrounding whether all place fields must arise from BTSP event. Working at the same institute, Albert Lee (e.g. Epszstein et al., 2011 - which should be cited) and Jeff Magee (e.g. Bittner et al., 2017) showed contradictory results for how place fields arise. These accounts have not fully been put toe-to-toe and reconciled in the literature. This manuscript addresses this gap and shows that both accounts are correct - place fields can emerge due to a pre-existing map and due to BTSP.

Weaknesses:

I find only three significant areas for improvement in the present study:

First, can it be concluded that non-BTSP events occur exclusively due to a global remapping event, as stated in the manuscript "these PFF surges included a high fraction of both non-BTSP- and BTSP-like PFF events, and were associated with global remapping of the CA1 representation"? Global remapping has a precise definition that involves quantifying the stability of all place fields recorded. Without a color scale bar in Figure 3D (which should be added), we cannot know whether the overall representations were independent before and after the spontaneous reset. It would be good to know if some neurons are able to maintain place coding (more often than expected by chance), suggestive of a partial-remapping phenomenon.

Second, BTSP has a flip side that involves the weakening of existing place fields when a novel field emerges. Was this observed in the present study? Presumably place fields can disappear due to this bidirectional BTSP or due to global remapping. For a full comparison of the two phenomena, the disappearance of place fields must also be assessed.

Finally, it would be good to know if place fields differ according to how they are born. For example, are there differences in reliability, width, peak rate, out-of-field firing, etc for those that arise due to BTSP vs non-BTSP.

Reviewer #1 (Public review):

Summary:

Zhang et al. addressed the question of whether advantageous and disadvantageous inequality aversion can be vicariously learned and generalized. Using an adapted version of the ultimatum game (UG), in three phases, participants first gave their own preference (baseline phase), then interacted with a "teacher" to learn their preference (learning phase), and finally were tested again on their own (transfer phase). The key measure is whether participants exhibited similar choice preferences (i.e., rejection rate and fairness rating) influenced by the learning phase, by contrasting their transfer phase and baseline phase. Through a series of statistical modeling and computational modeling, the authors reported that both advantageous and disadvantageous inequality aversion can indeed be learned (Study 1), and even be generalised (Study 2).

Strengths:

This study is very interesting, it directly adapted the lab's previous work on the observational learning effect on disadvantageous inequality aversion, to test both advantageous and disadvantageous inequality aversion in the current study. Social transmission of action, emotion, and attitude have started to be looked at recently, hence this research is timely. The use of computational modeling is mostly appropriate and motivated. Study 2, which examined the vicarious inequality aversion in conditions where feedback was never provided, is interesting and important to strengthen the reported effects. Both studies have proper justifications to determine the sample size.

Weaknesses:

Despite the strengths, a few conceptual aspects and analytical decisions have to be explained, justified, or clarified.

INTRODUCTION/CONCEPTUALIZATION<br /> (1) Two terms seem to be interchangeable, which should not, in this work: vicarious/observational learning vs preference learning. For vicarious learning, individuals observe others' actions (and optionally also the corresponding consequence resulting directly from their own actions), whereas, for preference learning, individuals predict, or act on behalf of, the others' actions, and then receive feedback if that prediction is correct or not. For the current work, it seems that the experiment is more about preference learning and prediction, and less so about vicarious learning. The intro and set are heavily around vicarious learning, and later the use of vicarious learning and preference learning is rather mixed in the text. I think either tone down the focus on vicarious learning, or discuss how they are different. Some of the references here may be helpful: Charpentier et al., Neuron, 2020; Olsson et al., Nature Reviews Neuroscience, 2020; Zhang & Glascher, Science Advances, 2020

EXPERIMENTAL DESIGN<br /> (2) For each offer type, the experiment "added a uniformly distributed noise in the range of (-10 ,10)". I wonder what this looks like? With only integers such as 25:75, or even with decimal points? More importantly, is it possible to have either 70:30 or 90:10 option, after adding the noise, to have generated an 80:20 split shown to the participants? If so, for the analyses later, when participants saw the 80:20 split, which condition did this trial belong to? 70:30 or 90:10? And is such noise added only to the learning phase, or also to the baseline/transfer phases? This requires some clarification.

(3) For the offer conditions (90:10, 70:30, 50:50, 30:70, 10:90) - are they randomized? If so, how is it done? Is it randomized within each participant, and/or also across participants (such that each participant experienced different trial sequences)? This is important, as the order especially for the learning phase can largely impact the preference learning of the participants.

STATISTICAL ANALYSIS & COMPUTATIONAL MODELING<br /> (4) In Study 1 DI offer types (90:10, 70:30), the rejection rate for DI-AI averse looks consistently higher than that for DI averse (ie, the blue line is above the yellow line). Is this significant? If so, how come? Since this is a between-subject design, I would not anticipate such a result (especially for the baseline). Also, for the LME results (eg, Table S3), only interactions were reported but not the main results.

(5) I do not particularly find this analysis appealing: "we examined whether participants' changes in rejection rates between Transfer and Baseline, could be explained by the degree to which they vicariously learned, defined as the change in punishment rates between the first and last 5 trials of the Learning phase." Naturally, the participants' behavior in the first 5 trials in the learning phase will be similar to those in the baseline; and their behavior in the last 5 trials in the learning phase would echo those at the transfer phase. I think it would be stronger to link the preference learning results to the change between the baseline and transfer phase, eg, by looking at the difference between alpha (beta) at the end of the learning phase and the initial alpha (beta).

(6) I wonder if data from the baseline and transfer phases can also be modeled, using a simple Fehr-Schimdt model. This way, the change in alpha/beta can also be examined between the baseline and transfer phase.

(7) I quite liked Study 2 which tests the generalization effect, and I expected to see an adapted computational modeling to directly reflect this idea. Indeed, the authors wrote, "[...] given that this model [...] assumes the sort of generalization of preferences between offer types [...]". But where exactly did the preference learning model assume the generalization? In the methods, the modeling seems to be only about Study 1; did the authors advise their model to accommodate Study 2? The authors also ran simulation for the learning phase in Study 2 (Figure 6), and how did the preference update (if at all) for offers (90:10 and 10:90) where feedback was not given? Extending/Unpacking the computational modeling results for Study 2 will be very helpful for the paper.

Reviewer #2 (Public review):

Summary:

This study investigates whether individuals can learn to adopt egalitarian norms that incur a personal monetary cost, such as rejecting offers that benefit them more than the giver (advantageous inequitable offers). While these behaviors are uncommon, two experiments demonstrate that individuals can learn to reject such offers through vicarious learning - by observing and acting in line with a "teacher" who follows these norms. The authors use computational modelling to argue that learners adopt these norms through a sophisticated process, inferring the latent structure of the teacher's preferences, akin to theory of mind.

Strengths:

This paper is well-written and tackles a critical topic relevant to social norms, morality, and justice. The findings, which show that individuals can adopt just and fair norms even at a personal cost, are promising. The study is well-situated in the literature, with clever experimental design and a computational approach that may offer insights into latent cognitive processes. Findings have potential implications for policymakers.

Weaknesses:

Note: in the text below, the "teacher" will refer to the agent from which a participant presumably receives feedback during the learning phase.

(1) Focus on Disadvantageous Inequity (DI): A significant portion of the paper focuses on responses to Disadvantageous Inequitable (DI) offers, which is confusing given the study's primary aim is to examine learning in response to Advantageous Inequitable (AI) offers. The inclusion of DI offers is not well-justified and distracts from the main focus. Furthermore, the experimental design seems, in principle, inadequate to test for the learning effects of DI offers. Because both teaching regimes considered were identical for DI offers the paradigm lacks a control condition to test for learning effects related to these offers. I can't see how an increase in rejection of DI offers (e.g., between baseline and generalization) can be interpreted as speaking to learning. There are various other potential reasons for an increase in rejection of DI offers even if individuals learn nothing from learning (e.g. if envy builds up during the experiment as one encounters more instances of disadvantageous fairness).

(2) Statistical Analysis: The analysis of the learning effects of AI offers is not fully convincing. The authors analyse changes in rejection rates within each learning condition rather than directly comparing the two. Finding a significant effect in one condition but not the other does not demonstrate that the learning regime is driving the effect. A direct comparison between conditions is necessary for establishing that there is a causal role for the learning regime.

(3) Correlation Between Learning and Contagion Effects:<br /> The authors argue that correlations between learning effects (changes in rejection rates during the learning phase) and contagion effects (changes between the generalization and baseline phases) support the idea that individuals who are better aligning their preferences with the teacher also give more consideration to the teacher's preferences later during generalization phase. This interpretation is not convincing. Such correlations could emerge even in the absence of learning, driven by temporal trends like increasing guilt or envy (or even by slow temporal fluctuations in these processes) on behalf of self or others. The reason is that the baseline phase is temporally closer to the beginning of the learning phase whereas the generalization phase is temporally closer to the end of the learning phase. Additionally, the interpretation of these effects seems flawed, as changes in rejection rates do not necessarily indicate closer alignment with the teacher's preferences. For example, if the teacher rejects an offer 75% of the time then a positive 5% learning effect may imply better matching the teacher if it reflects an increase in rejection rate from 65% to 70%, but it implies divergence from the teacher if it reflects an increase from 85% to 90%. For similar reasons, it is not clear that the contagion effects reflect how much a teacher's preferences are taken into account during generalization.

(4) Modeling Efforts: The modelling approach is underdeveloped. The identification of the "best model" lacks transparency, as no model-recovery results are provided, and fits for the losing models are not shown, leaving readers in the dark about where these models fail. Moreover, the reinforcement learning (RL) models used are overly simplistic, treating actions as independent when they are likely inversely related (for example, the feedback that the teacher would have rejected an offer provides feedback that rejection is "correct" but also that acceptance is "an error", and the later is not incorporated into the modelling). It is unclear if and to what extent this limits current RL formulations. There are also potentially important missing details about the models. Can the authors justify/explain the reasoning behind including these variants they consider? What are the initial Q-values? If these are not free parameters what are their values?

(5) Conceptual Leap in Modeling Interpretation: The distinction between simple RL models and preference-inference models seems to hinge on the ability to generalize learning from one offer to another. Whereas in the RL models learning occurs independently for each offer (hence to cross-offer generalization), preference inference allows for generalization between different offers. However, the paper does not explore RL models that allow generalization based on the similarity of features of the offers (e.g., payment for the receiver, payment for the offer-giver, who benefits more). Such models are more parsimonious and could explain the results without invoking a theory of mind or any modelling of the teacher. In such model versions, a learner learns a functional form that allows to predict the teacher's feedback based on said offer features (e.g., linear or quadratic form). Because feedback for an offer modulates the parameters of this function (feature weights) generalization occurs without necessarily evoking any sophisticated model of the other person. This leaves open the possibility that RL models could perform just as well or even show superiority over the preference learning model, casting doubt on the authors' conclusions. Of note: even the behaviourists knew that as Little Albert was taught to fear rats, this fear generalized to rabbits. This could occur simply because rabbits are somewhat similar to rats. But this doesn't mean little Alfred had a sophisticated model of animals he used to infer how they behave.

(6) Limitations of the Preference-Inference Model: The preference-inference model struggles to capture key aspects of the data, such as the increase in rejection rates for 70:30 DI offers during the learning phase (e.g. Figure 3A, AI+DI blue group). This is puzzling.

Thinking about this I realized the model makes quite strong unintuitive predictions that are not examined. For example, if a subject begins the learning phase rejecting the 70:30 offer more than 50% of the time (meaning the starting guilt parameter is higher than 1.5), then overleaning the tendency to reject will decrease to below 50% (the guilt parameter will be pulled down below 1.5). This is despite the fact the teacher rejects 75% of the offers. In other words, as learning continues learners will diverge from the teacher. On the other hand, if a participant begins learning to tend to accept this offer (guilt < 1.5) then during learning they can increase their rejection rate but never above 50%. Thus one can never fully converge on the teacher. I think this relates to the model's failure in accounting for the pattern mentioned above. I wonder if individuals actually abide by these strict predictions. In any case, these issues raise questions about the validity of the model as a representation of how individuals learn to align with a teacher's preferences (given that the model doesn't really allow for such an alignment).

Reviewer #1 (Public review):

Summary:

Optical blur is characterized by contrast losses and phase shifts that alter the local relationship between the component spatial frequencies in the image. The eye experiences optical blur on several occasions - for instance, physiologically, when the focus state of the eye does not match the optical vergence demand and, in cases of pathologies like keratoconus where the cornea gets progressively distorted leading to degraded retinal image quality. Recalibration of the visual system to suprathreshold contrast losses arising from the optical blur and the mechanisms that may underlie such a recalibration have been well-researched. This study by Barbot et al presents convincing evidence that the visual system could also recalibrate itself to the phase distortions experienced with optical blur. This was demonstrated, in principle, on a small number of participants with normal vision but with induced blur (?? experienced psychophysical observers) and in a few keratoconic patients using their state-of-the-art adaptive optics apparatus. In the former cohort, known magnitudes of radially asymmetric blur from a vertical coma were induced while participants judged the position of a compound grating target that shifted in predictable ways with the induction of blur. Immediate exposure to images blurred with such higher-order aberrations resulted in position shifts that were consistent with optical theory, but prolonged exposure to such blur resulted in the position shift returning to veridical perception (albeit, not completely). When the blur was removed after the adaptation phase, after effects of the position offset were noticed. In the keratoconic cohort, such position offsets were observed even when the eye was completely corrected for optical degradation. These results are discussed in the context of the perception of real-world targets, the underlying neurophysiology, and what it means to space perception in disease conditions like keratoconus.

Strengths:

A clear hypothesis, a parameterized experimental space, rigor of optical correction and psychophysical judgements, and clarity in the explanation of results are the major strengths of the paper. Additional strengths include the control experiments to address confounders and the additional analyses shown in the supplementary section to rule out analytical inconsistencies in explaining the results.

Weaknesses:

The small sample size (especially in the keratoconic cohort) may be a limitation of the study. While the experiments conducted in this study are meant to demonstrate a basic visual phenomenon, that only 6 keratoconic patients were included in the study precludes the results from being extrapolated to the heterogeneity of disease presentation. It must, however, be noted that these are difficult experiments to conduct, and getting multiple participants to agree to such an experiment is not an easy task.

Second, the analysis shown in Figure 6C relating the magnitude of habitual higher-order RMS to the absolute PSE shift is not convincing. The PSE's were both positive and negative in the KC patients. The direction of the phase shift experienced by the patient (i.e., positive or negative shift in the PSE) should also be determined by the pattern of HOA's in their eyes. Simply comparing the absolute magnitudes does not make sense. Would it be possible to convolve the compound grating with the PSF obtained from each patient and predict which direction should the PSE shift? This prediction can then be compared with the observed shift in the PSE's.

A third weakness of the study may be the assumption that the phase recalibration in keratoconic cohort may be eye-specific. That is, if the participant has dissimilar severities of keratoconus, the probed eye's aberration profile may determine the phase profile that the eye is calibrated to. I am not sure to what extent this assumption is valid. Further, under natural viewing, the pupil size will change with light intensity and accommodative state and this will, in turn, determine the optical quality of the eye. Given this, it is not clear what will the visual system recalibrate itself to, when the phase shifts in the retinal image may keep changing from the underlying blur profile in the retina. Also, if the disease is progressive in nature (in their cohort, the authors indicate that the disease did not progress), the calibration state should also constantly change. What is the time scale of such a calibration and could there be multiple states of such adaptation remains to be explored. This, of course, is not a weakness of the present study, but an open question for the future.

Finally, one additional experiment could have been performed (this is good to have information and certainly not a necessity). What is the wavefront profile of a few keratoconic patients that participated in the study, used as the adaptation profile in the 2nd experiment (as opposed to a fixed level of coma)? Would a 60-min paradigm result in adapted states that will result in phase shifts matching what is experienced by keratoconic eyes (see Marella et al., Vis Res, 2024 for a similar induced experiment for studying the impact of phase shifts on visual and stereoacuities)?

Reviewer #2 (Public review):

Summary:

The authors examine the ability of the human visual system to adapt to optically induced phase shifts. The study shows clear adaptation to the relative phase created by exposure to vertical coma. The study assesses the impact of adaptation to the coma on the perceived relative phase of f and 3f compound gratings. It is observed that during the first couple of minutes of a 1-hour exposure to induced vertical coma, the apparent relative locations of the f and 3f shifted in the opposite direction to that induced by the coma, a classic adaptation effect. This result highlights a neural mechanism by which flawed information is used to create seemingly accurate perceptions of the visual environment.

Strengths:

Sophisticated and rigorous optical and psychophysical methods, and a clear research question. The manuscript is well-written and the data quality is very high. The authors are to be congratulated on this challenging and complex optics and psychophysics study.

Weaknesses:

Some more details on the phase and amplitude consequences of the induced coma would add value to the reader.

Reviewer #1 (Public review):

Summary:

This study uses information from the UK Biobank and aims to investigate the role of BMI on various health outcomes, with a focus on differences by sex. They confirm the relevance of many of the well-known associations between BMI and health outcomes for males and females and suggest that associations for some endpoints may differ by sex. Overall their conclusions appear supported by the data. The significance of the observed sex variations will require confirmation and further assessment.

Strengths:

This is one of the first systematic evaluations of sex differences between BMI and health outcomes.

The hypothesis that BMI may be associated with health differentially based on sex is relevant and even expected. As muscle is heavier than adipose tissue, and as men typically have more muscle than women, as a body composition measure BMI is sometimes prone to classifying even normal weight/muscular men as obese, while this measure is more lenient when used in women.

Confirmation of the many well-known associations is as expected and attests to the validity of their approach.

Demonstration of the possible sex differences is interesting, with this work raising the need for further study.

Weaknesses:

Many of the statistical decisions appeared to target power at the expense of quality/accuracy. For example, they chose to use self-reported information rather than doctor diagnoses for disease outcomes for which both types of data were available.

Despite known problems and bias arising from the use of one sample approach, they chose to use instruments from the UK Biobank instead of those available from the independent GIANT GWAS, despite the difference in sample size being only marginally greater for UKB for the context. With the way the data is presented, it is difficult to assess the extent to which results are compatible across approaches.

The approach to multiple testing correction appears very lenient, although the lack of accuracy in the reporting makes it difficult to know what was done exactly. The way it reads, FDR correction was done separately for men, and then for women (assuming that the duplication in tests following stratification does not affect the number of tests). In the second stage, they compared differences by sex using Z-test, apparently without accounting for multiple testing.

Presentation lacks accuracy in a few places, hence assessment of the accuracy of the statements made by the authors is difficult.

Conclusion "These findings highlight the importance of retaining a healthy BMI" is rather uninformative, especially as they claim that for some attributes the effects of BMI may be opposite depending on sex/gender.

Reviewer #2 (Public review):

Summary:

In this present Mendelian randomization-phenome-wide association study, the authors found BMI to be positively associated with many health-related conditions, such as heart disease, heart failure, and hypertensive heart disease. They also found sex differences in some traits such as cancer, psychological disorders, and ApoB.

Strengths:

The use of the UK-biobank study with detailed phenotype and genotype information.

Weaknesses:

Previous studies have performed this analysis using the same cohort, with in-depth analysis. See this paper: Searching for the causal effects of body mass index in over 300,000 participants in UK Biobank, using Mendelian randomization. https://journals.plos.org/plosgenetics/article?id=10.1371/journal.pgen.1007951

I believe that the authors' claim, "To our knowledge, no sex-specific PheWAS has investigated the effects of BMI on health outcomes," is not well supported. They have not cited a relevant paper that conducted both overall and sex-stratified PheWAS using UK Biobank data with a detailed analysis. Given the prior study linked above, I am uncertain about the additional contributions of the present research.

Reviewer #1 (Public review):

Summary:

This study highlights the strengths of using predictive computational models to inform C. elegans screening studies of compounds' effects on aging and lifespan. The authors primarily focus on all-trans retinoic acid (atRA), one of the 5 compounds (out of 16 tested) that extended C. elegans lifespan in their experiments. They show that atRA has positive effects on C. elegans lifespan and age-related health, while it has more modest and inconsistent effects (i.e., some detrimental impacts) for C. briggsae and C. tropicalis. In genetic experiments designed to evaluate contributing mediators of lifespan extension with atRA exposure, it was found that 150 µM of atRA did not significantly extend lifespan in akt-1 or akt-2 loss-of-function mutants, nor in animals with loss of function of aak-2, or skn-1 (in which atRA had toxic effects); these genes appear to be required for atRA-mediated lifespan extension. hsf-1 and daf-16 loss-of-function mutants both had a modest but statistically significant lifespan extension with 150 µM of atRA, suggesting that these transcription factors may contribute towards mediating atRA lifespan extension, but that they are not individually required for some lifespan extension. RNAseq assessment of transcriptional changes in day 4 atRA-treated adult wild-type worms revealed some interesting observations. Consistent with the study's genetic mutant lifespan observations, many of the atRA-regulated genes with the greatest fold-change differences are known regulated targets of daf-2 and/or skn-1 signaling pathways in C. elegans. hsf-1 loss-of-function mutants show a shifted atRA transcriptional response, revealing a dependence on hsf-1 for ~60% of the atRA-downregulated genes. On the other hand, RNAseq analysis in aak-2 loss-of-function mutants revealed that aak-2 is only required for less than a quarter of the atRA transcriptional response. All together, this study is proof of the concept that computational models can help optimize C. elegans screening approaches that test compounds' effects on lifespan, and provide comprehensive transcriptomic and genetic insights into the lifespan-extending effects of all-trans retinoic acid (atRA).

Strengths:

(1) A clearly described and well-justified account describes the approach used to prioritize and select compounds for screening, based on using the top candidates from a published list of computationally ranked compounds (Fuentealba et al., 2019) that were cross-referenced with other bioinformatics publications to predict anti-aging compounds, after de-selecting compounds previously evaluated in C. elegans as per the DrugAge database. 16 compounds were tested at 4-5 different concentrations to evaluate effects on C. elegans lifespan.

(2) Robust experimental design was undertaken evaluating the lifespan effects of atRA, as it was tested on three strains each of C. elegans, C. briggsae, and C. tropicalis, with trial replication performed at three distinct laboratories. These observations extended beyond lifespan to include evaluations of health metrics related to swimming performance.

(3) In-depth analyses of the RNAseq data of whole-worm transcriptional responses to atRA revealed interesting insights into regulator pathways and novel groups of genes that may be involved in mediating lifespan-extension effects (e.g., atRA-induced upregulation of sphingolipid metabolism genes, atRA-upregulation of genes in a poorly-characterized family of C. elegans paralogs predicted to have kinase-like activity, and disproportionate downregulation of collagen genes with atRA).

Weaknesses:

(1) The authors' computational-based compound screening approach led to a ~30% prediction success rate for compounds that could extend the median lifespan of C. elegans. However, follow-up experiments on the top compounds highlighted the fact that some of these observed "successes" could be driven by indirect, confounding effects of these compounds on the bacterial food source, rather than direct beneficial effects on C. elegans physiology and lifespan. For instance, this appeared to be the case for the "top" hit of propranolol; other compounds were not tested with metabolically inert or killed bacteria. In addition, there are no comparative metrics provided to compare this study's ~30% success rate to screening approaches that do not use computational predictions.

(2) Transcriptomic analyses of atRA effects were extensive in this study, but evaluations and discussions of non-transcriptional effects of key proposed regulators (such as AMPK) were limited. For instance, non-transcriptional effects of aak-2/AMPK might account for its requirement for mediating lifespan extension effects, since aak-2 was not required for a major proportion of atRA transcriptional responses.

Reviewer #2 (Public review):

Summary:

In this manuscript, Banse et al. experimentally validate the power of computational approaches that predict anti-aging molecules using the multi-species approach of the Caenorhabditis Intervention Testing Program (CITP). Filtering candidate molecules based on transcriptional profiles, ML models, literature searches, and the DrugAge database, they selected 16 compounds for testing. Of those, eight did not affect C.elegan's lifespan, three shortened it, and five extended C.elegan's lifespan, resulting in a hit rate of over 30%. Of those five, they then focused on all-trans-retinoic acid (atRA), a compound that has previously resulted in contradictory effects. The lifespan-extending effect of atRA was consistent in all C. elegans strains tested, was absent in C. briggsae, and a small effect was observed in some C. tropicalis strains. Similar results were obtained for measures of healthspan. The authors then investigated the mechanism of action of atRA and showed that it was only partially dependent on daf-16 but required akt-1, akt-2, skn-1, hsf-1, and, to some degree, pmk-1. The authors further investigate the downstream effects of atRA exposure by conducting RNAseq experiments in both wild-type and mutant animals to show that some, but surprisingly few, of the gene expression changes that are observed in wild-type animals are lost in the hsf-1 and aak-2 mutants.

Strengths:

Overall, this study is well conceived and executed as it investigates the effect of atRA across different concentrations, strains, and species, including life and health span. Revealing the variability between sites, assays, and the method used is a powerful aspect of this study. It will do a lot to dispel the nonsensical illusion that we can determine a percent increase in lifespan to the precision of two floating point numbers.

An interesting and potentially important implication arises from this study. The computational selection of compounds was agnostic regarding strain or species differences and was predominantly based on observations made in mammalian systems. The hit rate calculated is based on the results of C. elegans and not on the molecules' effectiveness in Briggsae or Tropicalis. If it were, the hit rate would be much lower. How is that? It would suggest that ML models and transcriptional data obtained from mammals have a higher predictive value for C. elegans than for the other two species. This selectivity for C.elegans over C.tropicalis and C.Briggsae seems both puzzling and unexpected. The predictions for longevity were based on the transcriptional data in cell lines. Would it be feasible to compare the mammalian data to the transcriptional data in Figure 5 and see how well they match? While this is clear beyond the focus of this study, an implied prediction is that running RNAseqs for all these strains exposed to atRA would reveal that the transcriptional changes observed in the strains where it extends lifespan the most should match the mammalian data best. Otherwise, how could the mammalian datasets be used to predict the effects of C.elegans over C.Briggsae or C.Tropicalis have more predictive for one species than the other? There are a lot of IFs in this prediction, but such an experiment would reconsider and validate the basis on which the original predictions were made.

Weaknesses:

Many of the most upregulated genes, such as cyps and pgps are xenobiotic response genes upregulated in many transcriptional datasets from C.elegans drug studies. Their expression might be necessary to deal with atRA breakdown metabolites to prevent toxicity rather than confer longevity. Because atRA is very light sensitive and has toxicity of breakdown, metabolites may explain some of the differences observed with the lifespan of machine effects compared to standard assay practices.

Reviewer #3 (Public review):

Summary:

In this study, Banse et al., demonstrate that combining computer prediction with genetic analysis in distinct Caenorhabditis species can streamline the discovery of aging interventions by taking advantage of the diverse pool of compounds that are currently available. They demonstrate that through careful prioritization of candidate compounds, they are able to accomplish a 30% positive hit rate for interventions that produce significant lifespan extensions. Within the positive hits, they focus on all-trans retinoic acid (atRA) and discover that it modulates lifespan through conserved longevity pathways such as AKT-1 and AKT-2 (and other conserved Akt-targets such as Nrf2/SKN-1 and HSF1/HSF-1) as well as through AAK-2, a conserved catalytic subunit of AMPK. To better understand the genetic mechanisms behind lifespan extension upon atRA treatment, the authors perform RNAseq experiments using a variety of genetic backgrounds for cross-comparison and validation. Using this current state-of-the-art approach for studying gene expression, the authors determine that atRA treatment produces gene expression changes across a broad set of stress-response and longevity-related pathways. Overall, this study is important since it highlights the potential of combining traditional genetic analysis in the genetically tractable organism C. elegans with computational methods that will become even more powerful with the swift advancements being made in artificial intelligence. The study possesses both theoretical and practical implications not only in the field of aging but also in related fields such as health and disease. Most of the claims in this study are supported by solid evidence, but the conclusions can be refined with a small set of additional experiments or re-analysis of data.

Strengths:

(1) The criteria for prioritizing compounds for screening are well-defined and easy to replicate (Figure 1), even for scientists with limited experience in computational biology. The approach is also adaptable to other systems or model organisms.

(2) I commend the researchers for doing follow-up experiments with the compound propranolol to verify its effect on lifespan (Figure 2 Supplement 2), given the observation that it affected the growth of OP50. To prevent false hits in the future, the reviewer recommends the use of inactivated OP50 for future experiments to remove this confounding variable.

(3) The sources of variation (Figure 3, Figure Supplement 2) are taken into account and demonstrate the need for advancing our understanding of the lifespan phenotype due to inter-individual variation.

(4) The addition of the C. elegans swim test in addition to the lifespan assays provides further evidence of atRA-induced improvement in longevity.

(5) The RNAseq approach was performed in a variety of genetic backgrounds, which allowed the authors to determine the relationship between AAK-2 and HSF-1 regulation of the retinoic acid pathway in C. elegans, specifically, that the former functions downstream of the latter.

Weaknesses:

(1) The filtering of compounds for testing using the DrugAge database requires that the database is consistently updated. In this particular case, even though atRA does not appear in the database, the authors themselves cite literature that has already demonstrated atRA-induced lifespan extension, which should have precluded this compound from the analysis in the first place.

(2) The threshold for determining positive hits is arbitrary, and in this case, a 30% positive hit rate was observed when the threshold is set to a lifespan extension of around 5% based on Figure 1B (the authors fail to explicitly state the cut-off for what is considered a positive hit).

(3) The authors demonstrate that atRA extends lifespan in a species-specific manner (Figure 3). Specifically, this extension only occurs in the species C. elegans yet, the title implies that atRA-induced lifespan extension occurs in different Caenorhabditis species when it is clearly not the case. While the authors state that failure to observe phenotypes in C. briggsae and C. tropicalis is a common feature of CITP tests, they do not speculate as to why this phenomenon occurs.

(4) There are discrepancies between the lifespan curves by hand (Figure 3 Figure Supplement 1) and using the automated lifespan machine (Figure 3 Supplement 3). Specifically, in the automated lifespan assays, there are drastic changes in the slope of the survival curve which do not occur in the manual assays. This may be due to improper filtering of non-worm objects, improper annotation of death times, or improper distribution of plates in each scanner.

(5) The authors miss an opportunity to determine whether the lifespan extension phenotype attributed to the retinoic acid pathway is mostly transcriptional in nature or whether some of it is post-transcriptional. The authors even state "that while aak-2 is absolutely required for the longevity effects of atRA, aak-2 is required only for a small proportion (~1/4) of the transcriptional response", suggesting that some of the effects are post-transcriptional. Further information could have been obtained had the authors also performed RNAseq analysis on the tol-1 mutant which exhibited an enhanced response to atRA compared to wild-type animals, and comparing the magnitude of gene expression changes between the tol-1 mutant and all other genetic backgrounds for which RNAseq was performed.

Reviewer #1 (Public review):

Summary:

The authors demonstrate that female Spodoptera littoralis moths prefer to oviposit on well-watered tomato plants and avoid drought-stressed plants. The study then recorded the sounds produced by drought-stressed plants and found that they produce 30 ultrasonic clicks per minute. Thereafter, the authors tested the response of female S. littoralis moths to clicks with a frequency of 60 clicks per minute in an arena with and without plants and in an arena setting with two healthy plants of which one was associated with 60 clicks per minute. These experiments revealed that in the absence of a plant, the moths preferred to lay eggs on the side of the area in which the clicks could be heard, while in the presence of a plant the S. littoralis females preferred to oviposit on the plant where the clicks were not audible. In addition, the authors also tested the response of S. littoralis females in which the tympanic membrane had been pierced making the moths unable to detect the click sounds. As hypothesised, these females placed their eggs equally on both sites of the area. Finally, the authors explored whether the female oviposition choice might be influenced by the courtship calls of S. littoralis males which emit clicks in a range similar to a drought-stressed tomato plant. However, no effect was found of the clicks from ten males on the oviposition behaviour of the female moths, indicating that the females can distinguish between the two types of clicks. Besides these different experiments, the authors also investigated the distribution of egg clusters within a longer arena without a plant, but with a sugar-water feeder. Here it was found that the egg clusters were mostly aggregated around the feeder and the speaker producing 60 clicks per minute. Lastly, video tracking was used to observe the behaviour of the area without a plant, which demonstrated that the moths gradually spent more time at the arena side with the click sounds.

Strengths:

This manuscript is very interesting to read and the possibility that female moths might use sound as an additional sensory modality during host-searching is exciting and very relevant to the field of insect-plant interactions.

Weaknesses:

The study addresses a very interesting question by asking whether female moths incorporate plant acoustic signals into their oviposition choice, unfortunately, I find it very difficult to judge how big the influence of the sound on the female choice really is as the manuscript does not provide any graphs showing the real numbers of eggs laid on the different plants, but instead only provides graphs with the Bayesian model fittings for each of the experiments. In addition, the numbers given in the text seem to be relatively similar with large variations e.g. Figure 1B3: 1.8 {plus minus} 1.6 vs. 1.1 {plus minus} 1.0. Furthermore, the authors do not provide access to any of the raw data or scripts of this study, which also makes it difficult to assess the potential impact of this study. Hence, I would very much like to encourage the authors to provide figures showing the measured values as boxplots including the individual data points, especially in Figure 1, and to provide access to all the raw data underlying the figures.

Regarding the analysis of the results, I am also not entirely convinced that each night can be taken as an independent egg-laying event, as the amount of eggs and the place were the eggs are laid by a female moth surely depends on the previous oviposition events. While I must admit that I am not a statistician, I would suggest, from a biological point of view, that each group of moths should be treated as a replicate and not each night. I would therefore also suggest to rather analyse the sum of eggs laid over the different consecutive nights than taking the eggs laid in each night as an independent data point.

Furthermore, it did not become entirely clear to me why a click frequency of 60 clicks per minute was used for most experiments, while the plants only produce clicks at a range of 30 clicks per minute. Independent of the ecological relevance of these sound signals, it would be nice if the authors could provide a reason for using this frequency range. Besides this, I was also wondering about the argument that groups of plants might still produce clicks in the range of 60 clicks per minute and that the authors' tests might therefore still be reasonable. I would agree with this, but only in the case that a group of plants with these sounds would be tested. Offering the choice between two single plants while providing the sound from a group of plants is in my view not the most ecologically reasonable choice. It would be great if the authors could modify the argument in the discussion section accordingly and further explore the relevance of different frequencies and dB-levels.

Finally, I was wondering how transferable the findings are towards insects and Lepidopterans in general. Not all insects possess a tympanic organ and might therefore not be able to detect the plant clicks that were recorded. Moreover, I would imagine that generalist herbivorous like Spodoptera might be more inclined to use these clicks than specialists, which very much rely on certain chemical cues to find their host plants. It would be great if the authors would point more to the fact that your study only investigated a single moth species and that the results might therefore only hold true for S. littoralis and closely related species, but not necessary for other moth species such as Sphingidae or even butterflies.

Reviewer #2 (Public review):

This paper presents an interesting and fresh approach as it investigates whether female moths utilize plant-emitted ultrasounds, particularly those associated with dehydration stress, in their egg-laying decision-making process.

Female moths showed a preference for moist, fresh plants over dehydrated ones in experiments using actual plants. Additionally, when both plants were fresh but ultrasonic sounds specific to dehydrated plants were presented from one side, the moths chose the silent plant. However, in experiments without plants, contrary to the hypothesis derived from the above results, the moths preferred to oviposit near ultrasonic playback mimicking the sounds of dehydrated plants.　

The results are intriguing, and I think the experiments are very well designed. However, if female moths use the sounds emitted by dehydrated plants as cues to decide where to oviposit, the hypothesis would predict that they would avoid such sounds. The discussion mentions the possibility of a multi-modal moth decision-making process to explain these contradictory results, and I also believe this is a strong possibility. However, since this remains speculative, careful consideration is needed regarding how to interpret the findings based solely on the direct results presented in the results section.

Additionally, the final results describing differences in olfactory responses to drying and hydrated plants are included, but the corresponding figures are placed in the supplementary materials. Given this, I would suggest reconsidering how to best present the hypotheses and clarify the overarching message of the results. This might involve reordering the results or re-evaluating which data should appear in the main text versus the supplementary materials.

There were also areas where more detailed explanations of the experimental methods would be beneficial.