Reviewer #1 (Public review):

In this manuscript, the authors aim to determine the ligand on Plasmodium falciparum-infected erythrocytes for the NK cell integrin, LFA-1, following up on previous evidence that LFA-1 is important for immune cell-mediated recognition of iRBCs.

They start by incubating LFA-1 with iRBCs and show by flow analysis that a substantial population of these iRBCs binds to the LFA-1 (Figure 1C). They do conduct the control with uninfected RBCs, but put this in the supplementary material. As this is a critical control, I think that it should be moved to Figure 1C as it is essential to allow interpretation of the iRBC data. The authors also do not state which strain of P. falciparum they used (line 144). This is critical information as different strains have different variant surface antigens and should be included. With these changes, this data seems convincing.

They next incubated LFA-1 with the iRBCs, cross-linked and conducted a pulldown, identifying GP130 as a binding partner. Using cross-linkers is a dangerous strategy as it risks non-specific cross-linking. Did they try without cross-linking and find an interaction?

They raised antibodies to PfGBP and showed IFA, which reveals that these antibodies stain iRBCs (Figure 2Ciii). This experiment lacks a critical control of uninfected RBCs, which needs to be included to show that the staining is specific. Without this, it is not possible to conclude that there is iRBC-specific staining with PfGBP.

They then conduct a pulldown using LFA-Fc, which does show GP130 only in the presence of the LFA-Fc, but not when empty beads are used. This is convincing. BLI measurements are also used to study this interaction (Figure 2Ci). The BLI data is presented in such a way that any association phase is obscured by the y-axis, which makes it impossible to know whether there is binding here. I think that the data needs to be shown with some baseline before the addition of the ligand so that the association can be seen. The data is also a bit messy with a downward drift and the curves showing different shapes, for example, with the 1.0uM curve seeming to have a different association rate. Also, is this n=1? I think that this data needs to be repeated and replicated. As this is the only data which shows a direct interaction between LFA1 and GBP, as pulldowns are done with lysates, which might mean bridging components. I think that it is important to repeat the BLI or use additional biophysical methods to assess binding, to obtain more convincing data.

The authors next do some modelling of the putative complex. This is done by homology modelling and docking, which is not the most up-to-date method and is overinterpreted. Personally, I would remove this data as I did not find it convincing, and it is not important for the story. If the authors wish to include it, then I think that they should validate the modelling by mutagenesis to show that the residues which the models indicate might bind are involved in the interaction.

They next made GP130 and tested the binding of this to THP-1 cells, which are often used as a model for macrophages. They observe greater binding of PfGBP-Fc to these cells when compared with hIgG and show that LFA-1 siRNA reduces this binding. I was a little confused about how the flow plots related to the graph in the bottom right corner of Figure 3Bii. In the flow plots, hIgG control shows 12.8% of cells in the gated region, while the unstained cells has 5.63%, but the MFI data shows a decrease in binding for hIgG vs unstained cells. How is this consistent? Also, the siRNA reduces the number of cells in the gated region from 66.6% to 25.9%, which is still substantially more that 5.63% in the unstained control. This also doesn't seem quite consistent with the MFI data. Could the authors explain this? Also, perhaps an additional experiment would be to add soluble LFA-1 into this assay as an additional control to determine whether this blocks PfGBP binding to the THP-1 cells? It could be that there are additional mechanisms of binding which indicate why the siRNA has a partial effect. The same is true for the NK cell experiments in Figure 3Ci, in which the siRNA has a partial effect. The authors also test binding to HEK, HepG2 and 'stem' cells and claim 'only background levels of binding', but in each case, there is more binding to these cells by PfGBP-Fc than by hIgG, albeit less than in THP-1 and NK cells. Why have the authors decided that these increases are not significant? All in all, these experiments do indicate a role for the GBP-LFA1 interaction in the binding of immune cells to iRBCs, but perhaps not as absolutely as is suggested.

The authors next produce CHO cells with PfGBP on the surface. These cells bind to LFA-1 specifically. When these cells were incubated with primary NK cells, they did see increases in activation markers, which were reduced by the addition of anti-CD11a, suggesting these to be specific. They also conduct the same experiment with anti-GBP with iRBCs, but this is in a different figure. It would be easier for the reader if Figure 5B were in the same figure as Figure 4B, as it is related data using the same method. I found this data convincing, showing that the LFA1:GBP interaction does contribute to immune cell recognition and activation.

The authors next conduct an experiment in which they assess parasite growth in the presence of NK cells and in the presence of anti-GBP. They use Heochst staining as a measure of parasite growth and claim that NK cells reduce the number of parasites, but that anti-GBP abolishes this effect (Figure 5A). I found this experiment very unconvincing as there are small effects and no demonstration of significance. More commonly used approaches to study parasite growth are lactate dehydrogenase GIA assays or calcein-AM labelling. I did not find this experiment convincing and would either remove or supplement with additional data using a more robust assay, with repeats and tests of statistical significance.

In summary, the authors present a set of data which comes together to indicate an interaction between LFA1 and PfGBP on the Plasmodium-infected erythrocyte surface. Pulldown studies show convincingly that these two proteins co-precipitate, and BLI data suggest that this is direct. Also convincing is that NK cell activation can be reduced using antibodies against either LFA1 or PfGBP, indicating that this interaction does play a role in immune cell recognition of iRBCs.

Reviewer #1 (Public review):

Summary:

This study provided key experimental evidence for the "Solstice-as-Phenology-Switch Hypothesis" through two temperature manipulation experiments.

Strengths:

The research is data-rich, particularly in exploring the effects of pre- and post-solstice cooling, as well as daytime versus nighttime cooling, on bud set timing, showcasing significant innovation. The article is well-written, logically clear, and is likely to attract a wide readership.

Comments on revisions:

This is the second round of review, and I am generally very satisfied with the authors' revisions. However, a few detailed issues still require attention:

The authors identified the summer solstice (June 21) as a phenological "switch point", but the flexibility of this switch point remains poorly understood. A more precise explanation of what "flexibility" means in this context is needed, along with a description of the specific experimental results that would demonstrate this flexibility.

The experiment did not directly measure the specific date of the phenological switch point. Instead, it was inferred by comparing temperature effects before and after the solstice. The manuscript should clearly state that this switch point remains an inferred conceptual node rather than a directly measured variable.

In Experiment 1, the effect of bud type (terminal vs. lateral) was inconsistent across the overall model and the different leafing groups. The authors should provide a more thorough discussion of potential reasons for this inconsistency. In addition, the statistical model for Experiment 1 indicates that the measured variables (summer cooling and leaf emergence date) explain only 23.4% of the variation in bud formation timing. This leaves over 76% of the variation unexplained, suggesting that other important factors are involved. The discussion should address this limitation in greater depth, moving beyond a focus on the measured variables.

Reviewer #1 (Public review):

Naim et al. use genetically engineered mouse models and tissue culture cell lines to investigate the role of the SLAP adaptor protein in colonic epithelium and colon tumour formation. The SLAP adaptor protein is known to be a negative regulator of tyrosine kinase signaling in hematopoietic cells, but its role outside the immune system is less well defined. Here, the authors use genetically engineered SLAP-deficient mice, tissue-specific SLAP KO, and colonic organoids to demonstrate that SLAP is expressed in cells of the colonic epithelium, where it acts as a cell-autonomous regulator of proliferation and differentiation. In addition, they provide biochemical evidence that loss of SLAP expression in cultured colonic organoids results in increased Src family kinase activity and global tyrosine phosphorylation, consistent with its known role as a suppressor of tyrosine kinase activity in immune cells. Consistently, treatment with an SRC kinase inhibitor inhibited the growth of SLAP-deficient organoids. These data provide solid evidence of a cell-autonomous role of SLAP in the colonic epithelium.

This work would be improved by further description and interpretation of the SLAP expression pattern shown in the constitutive and tissue-specific KO to further support the conclusions made. In Supplementary Figure 1, magnification of the colon epithelium areas with SLAP expression shown by b-gal and anti-SLAP staining, highlighting regions of interest, would better support the conclusions regarding SLAP expression in specific regions of the colon epithelium. In Supplementary Figure 1B, the authors should indicate that the SLAP staining referred to is epithelial and in resident immune cells, as is mentioned in the text. Also, magnification of the boxed area of LRG5 staining in Figure 1 would improve this figure.

Using a chemically induced model of colitis-associated cancer, the authors demonstrate that inactivation of SLAP shows a trend toward increased tumor formation (though this did not reach significance) as well as increased Src family kinase activity within tumors. Tumor spheres from SLAP-deficient animals showed enhanced growth that was suppressed by treatment with a Src family kinase inhibitor. Of note, the latter effect was specific to SLAP-deficient tumor spheres. These observations are convincing and support the authors' conclusion that SLAP has a tumor suppressor role in CRC through inhibition of SFK signaling.

Mechanistically, elevated expression of the RTK, EphB2, was detected in immunoblots of SLAP KO colonic crypts, while overexpression of SLAP in CRC cell lines downregulated EphB2 protein levels. Using an EPHB2 inhibitor, the role of EPHB2 in the growth of SLAP-deficient colonic organoids was demonstrated. While these data generally support the authors' conclusion that SLAP limits colonic organoid growth by downregulating RTKS such as EphB2 and downstream Src family kinase activity, they do not show which cell types/regions in the colonic epithelium have increased EPHB2 protein and how this relates to SLAP and phospho-SRC expression, as shown in Figure 1 and Figure S1 immunocytochemistry. The expression of EphB2 and its role in colonic tumorsphere growth were not investigated.

Overall, this work provides evidence of SLAP adaptor function in restricting tyrosine kinase signaling in the colonic epithelium, and suggests that loss of SLAP expression could promote tumorigenesis in this context.

Reviewer #1 (Public Review):

[Editors' note: This version has been assessed by the Reviewing Editor without further input from the original reviewers. Given the time elapsed since the original data collection, the authors have addressed the previous concerns by providing a more nuanced discussion of their results and acknowledging the limitations of the study to ensure the conclusions are supported by the existing data.]

Throughout the paper, the authors do a fantastic job of highlighting caveats in their approach, from image acquisition to analysis. Despite this, some conclusions and viewpoints portrayed in this study do not appear well-supported by the provided data. Furthermore, there are a few technical points regarding the analysis that should be addressed.

(1) Analysis of signaling traces

- Relevance of "modeled signaling level": It is not clear whether this added complexity and potential for error (below) provides benefits over a more simple analysis such as taking the derivative (shown in Figure 3C). Could the authors provide evidence for the benefits? For example, does the "maximal response" given a simpler metric correlate less well with cell fate than that calculated from the fitted response?

- Assumptions for "modeled signaling level": According to equation (1) Kaede levels are monotonically increasing. This is assumed given the stability of the fluorescent protein. However, this only holds for the "totally produced Kaede/fluorescence". Other metrics such as mean fluorescence can very well decrease over time due to growth and division. Does "intensity" mean total fluorescence? Visual inspection of the traces shown in Figure 2 suggests that "fluorescence intensity" can decrease. What does this mean for the inferred traces?

- Estimation of Kaede reporter half-live: It is not clear how the mRNA stability of Kaede is estimated. It sounds like it was just assessed visually, which seems not entirely appropriate given the quantitative aspects of the rest of the study. Also, given that Shh signaling was inhibited on the level of Smoothened, it is not obvious how the dynamics of signaling shutdown affect the estimate. Most results in Figure 7 seem to be quite robust to the estimate of the half-live. That they are, might suggest that the whole analysis is unnecessary in the first place. However, not all are. Thus, it would be important to make this estimate more quantitative.

(2) Assignment of fates and correlations

- Error estimate for cell-type assignment: Trying to correlate signaling traces to cell fate decisions requires accurate cell fate assignment post-tracking. The provided protocol suggests a rather manual, expert-directed process of making those decisions. Can the authors provide any error-bound on those decisions, for example comparing the results obtained by two experts or something comparable? I am particularly concerned about the results regarding the higher degree of variability in the correlation between signaling dynamics and cell fate in the posterior neural tube. Here, the expression of Olig2 does not seem to segregate between different assigned fates, while it does so nicely in the anterior neural tube. This would suggest to me that cells in the posterior neural tube might not yet be fully committed to a fate or that there could be a relatively high error rate in assigning fates. Thus, the results could emerge from technical errors or differences in pure timing. Could the authors please comment on these possibilities?

- Clustering and fates: One approach the authors use to analyze the correlation between signaling and fate is clustering of cell traces and comparison of the fate distributions in those clusters. There is a large number of clusters with only single traces, suggesting that the data (number of traces) might not be sufficient for this analysis. Furthermore, I am skeptical about clustering cells of different anterior-posterior identities together, given potential differences in the timing of signal reception and signaling. I am not convinced that this analysis reveals enough about how signaling maps to fate given the heterogeneity in traces in large clusters and the prevalence of extremely small clusters.

- Signaling vector and hand-picked metrics: As an alternative approach, that might be better suited for their data, the authors then pick three metrics (based on their model-predicted signaling dynamics) and show that the maximal response is a very good predictor of fate for different anterior-posterior identities. Previous information-theoretic analysis of signaling dynamics has found that a whole time-vector of signaling can carry much more information than individual metrics (Selimkhanov et al, 2014, PMID: 25504722). Have the authors tried to use approaches that make use of the whole trace (such as simple classifiers (Granados et al, 2018, PMID: 29784812), or can comment on why this is not feasible for their data? The authors should at least make clear that their results present a lower bound to how accurately cells can make cell-fate decisions based on signaling dynamics.

(3) Consequences of signaling heterogeneity

The authors focus heavily on portraying that signaling dynamics are highly variable, which seems visually true at first glance. However, there is no metric used or a description given of what this actually means. Mainly, the variability seems to relate to the correlation between signaling and fate. However, given the data and analysis, I would argue that the decoding of signaling dynamics into fate is surprisingly accurate. So signaling dynamics that seem quite noisy and variable by visual inspection can actually be very well discriminated by cells, which to me appears very exciting.

Indeed, simple features of signaling traces can predict cell fate as well as position (for anterior progenitors). Given that signaling should be a function of position, it naively seems as if signaling read-out could be almost perfect. It might be interesting to plot dorsal-ventral position vs the signaling metrics, to also investigate how Shh concentration/position maps to signaling dynamics, this would give an even more comprehensive view of signal transmission.

There remains the discrepancy between signaling traces and fate in the posterior neural tube. The authors point towards differences in tissue architecture and difficulties in interpreting a "small" Shh gradient. However, the data seems consistent with differences in timing of cell-fate decisions between anterior and posterior cells. The authors show that fate does initially not correlate well with position in the posterior neural tube. So, signaling dynamics should likely also not, as they should rather be a function of position, given they are downstream of the Shh gradient. As mentioned above, not even Olig2 expression does segregate the assigned fates well. All this points towards a difference in the time of fate assignment between the anterior and posterior. Given likely delays in reporter protein production and maturation, it can thus not be expected that signaling dynamics correlate better with cell fate than the reporter "83%". Can the authors please discuss this possibility in the paper?

Thus, while this paper represents an example of what the community needs to do to gain a better understanding of robust patterning under variability, the provided data is not always sufficient to make clear conclusions regarding the functional consequences of signaling dynamics.

Reviewer #2 (Public review):

Summary:

Almansour et al., investigate whether the proximity of TAD boundaries is directly linked to gene activity. The authors use high-throughput imaging to simultaneously measure the gene activity and physical distances between boundary regions in an allele-specific manner. Using transcriptional inhibitors, expression induction, and acute depletion of CTCF and cohesin, they test whether proximity of boundaries affects, or is affected by, gene activity.

Strengths:

The combined use of DNA and RNA imaging enabled simultaneous measurement of boundary proximity and transcriptional status at individual alleles. This allows single-allele correlation between boundary proximity and gene activity at multiple loci across thousands of alleles.

The use of both transcription inhibitors and transcription stimulation provides compelling and consistent evidence that boundary proximity can be disconnected from a gene's activity. The data convincingly support the conclusion that stable proximity between boundary regions is not required for ongoing transcription at the loci and timescales examined.

This work strengthens the emerging view that genome organization at the level of domain boundaries does not impose a deterministic control over transcription.

Strong disruption of boundary distances is only observed upon depletion of cohesin. Notably, this corresponds with the largest changes in gene activity. In contrast, depletion of CTCF actually had minimal impact on boundary distances and also had minimal impact on gene activity. This makes sense in light of previous work, where live cell imaging demonstrated that cohesin is more important for domain-structure, whereas CTCF is only important for blocking cohesin from continuing on, such that the fully formed loop occurs in a very small percentage of cells. Therefore, the fact that disruption of cohesin (more important for internal domain structure) affects gene activity while disruption of CTCF does not is exceptionally interesting.

Weaknesses:

In untreated cells, the distribution of distance measurements between boundary probes is exceptionally narrow. While depletion of RAD21 clearly demonstrates an ability to detect changes in this distribution, this tight baseline distribution may limit sensitivity to more subtle changes (like those one might expect from transcriptional influences).

This approach primarily tests the role of boundary interactions rather than domain organization as a whole.

Reviewer #1 (Public review):

Summary:

In this manuscript, Rosero and Bai examined how the well-known thermosensory neuron in C. elegans, AFD, regulates context-dependent locomotory behavior based on the tactile experience. Here they show that AFD uses discrete cGMP signalling molecules and independent of its dendritic sensory endings regulates this locomotory behavior. The authors also show here that AFD's connection to one of the hub interneurons, AIB, through gap junction/electrical synapses, is necessary and sufficient for the regulation of this context-dependent locomotion modulation.

Strengths:

This is an interesting paper showcasing how a sensory neuron in C. elegans can employ a distinct set of molecular strategies and different physical parts to regulate a completely distinct set of behaviors, which were not been shown to be regulated by AFD before. The experiments were well performed and the results are clear. However, there are some questions about the mechanism of this regulation. This reviewer thinks that the authors should address these concerns before the final published version of this manuscript.

Comments on revisions:

In this revised manuscript, Rosero and Bai satisfactorily addressed all the concerns raised by this reviewer regarding their original manuscript. This reviewer appreciates the authors' effort. This revised and improved manuscript demonstrates that a sensory neuron in C. elegans can utilize distinct molecular strategies and circuit engagements to regulate distinct sets of behaviors. This reviewer believes that the manuscript is suitable for final acceptance in eLife.

Reviewer #1 (Public review):

Summary:

In this manuscript, Lei and co-workers aim to uncover the genetic underpinnings of thermal adaptation across three strains of the diamondback moth (Plutella xylostella) through experimental evolution over three years under three different thermal regimes. They identify systematic differences in trait responses (e.g., survival, fecundity), metabolic profiles, gene expression, and in the amino acid sequence of the PxSODC gene, among others. These results suggest that the diamondback moth has a strong potential for rapid physiological adaptation to different thermal regimes. Overall, this is a comprehensive and generally well-executed study that addresses an important question in the face of ongoing climate change.

Strengths:

The authors employ multiple approaches to identify signatures of thermal adaptation across the three strains, such as trait performance comparisons, metabolomics, transcriptomics, and amino acid sequence comparisons. All these different angles form a convincing picture of the underlying factors that underpin thermal adaptation in this experimental system. The manuscript is also generally well written and easy to understand.

Weaknesses:

I am unable to judge the validity of all aspects of this work; I will focus only on areas within my core expertise.

(1) The authors identify pathways that are enriched in different strain comparisons (Figure 3E), but do not provide a detailed interpretation of these results. It would be great if the authors could explain in more detail how the physiological processes of a cold-adapted strain of this species may differ from those of a warmer-adapted strain.

(2) The authors reconstruct a phylogenetic tree of the PxSODC gene using the neighbor-joining algorithm. The limitations of this algorithm have been known for many years now, especially for sequences separated by long evolutionary distances. According to Wang et al. (2016), the last common ancestor of the species shown in Figure S4C occurred 392-350 million years ago. Given this, I would strongly recommend that the authors infer a phylogenetic tree using model-based methods, such as those implemented in RAxML-NG or IQ-TREE. Also, in the absence of a valid outgroup sequence, I would show the gene tree as unrooted or rooted based on the corresponding species tree.

(3) There is a key piece of the puzzle that is currently missing: the structural mechanism behind the mutational effects described in this study (e.g., Figure 5). The authors could leverage AlphaFold to generate structural models of different mutants and conduct molecular dynamics simulations to examine their conformational dynamics.

References:

Wang, Yh., Engel, M., Rafael, J. et al. Fossil record of stem groups employed in evaluating the chronogram of insects (Arthropoda: Hexapoda). Sci Rep 6, 38939 (2016). https://doi.org/10.1038/srep38939

Reviewer #1 (Public review):

Summary:

When contemplating the role of any sensory area in the brain, an essential question is: How much of the neural code is inherited from the inputs versus constructed de novo by the local circuitry? This study tackles that important question for the case of the mouse superior colliculus (SC), a visual brain area that receives direct input from the retina. The specific aspects of the neural code are the representation of line orientation and direction of motion in the visual image. Over the past 10 years or so, there have been reports that the preferred directions and orientations of neurons vary systematically across the SC in a global map that is not present in the retina, and therefore computed locally.

Here, the authors revisit this question by expanding the range of measurements: They record from the axonal boutons of retinal ganglion cells in the input layer of the SC, from the post-synaptic neurons there, and from neurons in deeper layers of the SC. They conclude that at any given location in the SC, the signals in retinal boutons recapitulate the tuning of retinal ganglion cells, and that SC neurons follow that organization, though it is lost in the deeper layers. Notably, they find no evidence for a global map of these response properties other than what is contributed by retinal input.

Strengths:

The study combines multiple recording methods - calcium imaging and electrical recording - to capture the activity of retinal inputs to the colliculus, the tuning of neurons in the superficial layers close to the input, as well as neurons in deeper layers. Furthermore, the work connects to the recent literature on gradients of tuning properties among retinal ganglion cells. All these set the stage for testing the correspondence between retinal inputs and collicular outputs.

Weaknesses:

The methods used to identify direction-selective and orientation-selective neurons based on visual responses are overly permissive and don't match common usage in this research area. Furthermore, the measurements covered only a small fraction of the visual field, which limits their ability to distinguish between different hypotheses for the global map of visual response properties. Relatedly, the claim that retinal input patterns explain much of the layout in the superior colliculus should be made more quantitative.

Reviewer #1 (Public review):

Summary:

This work builds a theory to implement planning trajectories towards a goal in a known environment, inspired by analyses of prefrontal neural recordings. Unlike standard neural architectures for this task, such as value-based learning and successor representations, their proposed theory is able to adapt to novel goal locations within a trial. The key to the theory is that future times are represented by orthogonal groups of neurons. The recurrent connectivity between groups of neurons selective to specific future times and locations reflects the learned knowledge of the task. Finally, the authors show that standard networks trained on the task approximate their proposed theory.

Strengths:

The structure of the work is clear, and the presentation of the results is very well written, which is particularly noticeable given the consequential amount of results presented. The authors are able to link their theory with experimental findings in neural recordings. The reverse-engineering of trained recurrent neural networks is very thorough, by analyzing both dynamics and connectivity. The assumptions and predictions of their model are clearly stated.

Weaknesses:

It is unclear whether their proposed theory, "space-time attractors", actually is an attractor network. The authors used recurrent neural networks with very few timesteps, and long single neuron time constants with respect to the task time scales. Attractor networks, as the ones the authors cite, refer to networks that generate nontrivial patterns of activity through recurrent interactions, after long periods of time.

The authors gloss over how the reward inputs are calculated. Computing these reward inputs should be part of the planning process, and the authors are implicitly leaving this problem aside. How does the reward input, which includes future time and location, depend on the actions that have not yet been taken by the agent? It feels like most of the planning computation is already provided by these reward inputs at the beginning of the trial. It could be that the network is only learning to process the planned sequence of actions present in the inputs.

Reviewer #1 (Public review):

Summary:

This work aims to identify the transcription factor responsible for targeting constitutively active genes for repression during heat stress. While the mechanisms underlying heat-stress-induced gene activation are well characterized - primarily involving Heat Shock Factor (HSF), the GA-binding factor GAF, and RNA Polymerase II pausing regulators - far less is known about how repression of constitutive genes is directed. Because known activation factors such as HSF and GAF do not account for repression, the authors sought a DNA-binding factor that could selectively target these genes. They focused on CLAMP (Chromatin-linked adaptor for MSL complex proteins) for several reasons. First, CLAMP recognizes GA-rich DNA motifs similar to those bound by GAF, suggesting it could compete with GAF at regulatory elements and shift transcriptional outcomes. Second, CLAMP has been shown to antagonize GAF binding in certain genomic contexts, suggesting it could counteract activation mechanisms. Third, CLAMP interacts with Negative Elongation Factor (NELF), a factor known to regulate transcriptional repression during heat stress. Finally, CLAMP promotes long-range chromatin interactions, indicating it may influence local chromatin architecture during the heat-stress response. Together, these properties led the authors to hypothesize that CLAMP helps mediate heat-stress-induced transcriptional repression of constitutively active genes.

To test this hypothesis, the authors use immunofluorescence along with three techniques: (1) nascent RNA-sequencing (SLAM-seq) to define the function of CLAMP in heat stress-induced transcriptional activation and repression; (2) Micro-C to identify CLAMP-dependent and independent genome-wide, high-resolution local changes in chromatin organization after heat stress, and (3) HiChIP to identify CLAMP-bound 3D chromatin loop anchors associated with heat-stress-dependent transcriptional regulation.

Analysis of heat-shocked salivary glands or KC cells showed results that aligned across all experiments, indicating that CLAMP is the primary repressor of gene activation upon heat shock. CLAMP also inhibits chromatin loop formation.

Strengths:

The techniques used here are comprehensive, and impressively, the data is unambiguous.

Weaknesses:

These techniques do not reveal the molecular mechanisms, but the authors provide a strong rationale and molecular hypotheses for future studies to dissect.

Reviewer #1 (Public review):

The paper from Hudait and Voth details a number of coarse-grained simulations as well as some experiments focused on the stability of HIV capsids in the presence of the drug lenacapavir. The authors find that LEN hyperstabilizes the capsid, making it fragile and prone to breaking inside the nuclear pore complex.

I found the paper interesting. I have a few suggestions for clarification and/or improvement.

(1) How directly comparable are the NPC-capsid and capsid-only simulations? A major result rests on the conclusion that the kinetics of rupture are faster inside the NPC, but are the numbers of LENs bound identical? Is the time really comparable, given that the simulations have different starting points? I'm not really doubting the result, but I think it could be made more rigorous/quantitative.

(2) Related to the above, it is stated on page 12 that, based on the estimated free-energy barrier, pentamer dissociation should occur in ~10 us of CG time. But certainly, the simulations cover at least this length of time?

(3) At first, I was surprised that even in a CG simulation, LEN would spontaneously bind to the correct site. But if I read the SI correctly, LEN was parameterized specifically to bind to hexamers and not pentamers. This is fine, but I think it's worth describing in the main text.

Comments on revisions:

I found that the authors addressed my concerns satisfactorily. The other reviewer raised a number of important points regarding the nuances of the model and the interpretation of the simulations, which the authors rebutted. I think the paper in its current form now is a worthwhile addition to the literature.

Reviewer #2 (Public review):

This article focuses on the study of two E. coli tripartite efflux pumps, both using TolC as a partner in the outer membrane, namely MacAB-TolC and AcrABZ-TolC.

By preparing MacAB-TolC in Peptidiscs rather than in detergent for cryo-EM structure determination, they visualized an extra protein localized around TolC. The resolution was sufficient to build part of the structure, and using the AlphaFold2 database and DALI topology recognition program, they identified it as the lipoprotein YbjP. This protein has an anchorage in the outer membrane, and it was suggested that it could act as a support for TolC, which is the only OMF that does not have an N-terminal extension anchored in the outer membrane, which is very puzzling for the community working in this field of research.

Authors used a large number of different approaches to evaluate the importance of YbjP (structure, genomic evolution, microbiology, photocrosslink in vivo, proteomic profile), but did not succeed in finding it a clear role so far, even if it could be important depending on environmental stress. Nevertheless, their results, obtained with extreme rigour, are of main interest for the comprehension of the complexity of such systems and deserve publication.

Comments on revisions:

Thank you for clarifying the points that puzzled me concerning the crosslink experiments. This version does not need further modifications.

Reviewer #1 (Public review):

This study established a C921Y OGT-ID mouse model, systematically demonstrating in mammals the pathological link between O-GlcNAc metabolic imbalance and neurodevelopmental disorders (cortical malformation, microcephaly) as well as behavioral abnormalities (hyperactivity, impulsivity, learning/memory deficits). Researchers comprehensively assessed the model phenotype through integrated multi-level analysis methods, including long-term behavioral monitoring, high-resolution brain structural imaging (micro-CT and MRI), histopathology, and quantitative proteomics.

The core strength of this study lies in its multimodal experimental design. The evidence chain spanning in vivo behavior, brain structure, and molecular characteristics demonstrates high consistency and correlation. Of particular note is the combination of non-invasive behavioral tracking with quantitative neuroimaging techniques, providing objective validation for the observed phenotypes. The findings support the authors' core conclusion: O-GlcNAc homeostasis imbalance correlates with neurodevelopmental deficits, including structural abnormalities in specific brain regions and altered cognitive behaviors. Furthermore, this model reproduces certain clinical features observed in human patients.

Nevertheless, several avenues remain open for further exploration. For instance, sample sizes in certain omics analyses remain relatively small, and investigations into downstream molecular mechanisms are still confined to the level of correlation-direct causal validation through genetic or pharmacological interventions is still required. Furthermore, as this model focuses on a single recurrent mutation, the generalizability of its findings to other OGT-ID variants remains to be verified.

It provides the first actionable vertebrate model for neurodevelopmental disorders with unclear mechanisms, filling a critical gap in this field. The multidimensional research methods established in the paper-such as the digital behavioral phenotyping workflow-also offer valuable references for related disease studies.

Endovenous ablation is contraindicated or relatively unsuitable when venous anatomy precludes catheter-based treatment, specifically: aneurysmal dilation of the GSV close to the saphenofemoral junction, subcutaneous location of truncal veins above the saphenous fascia and close to the skin, and significant tortuosity of the GSV or SSV. [1] In these scenarios, high ligation and stripping is recommended as the preferred alternative (grade 1 strong recommendation

Endovenous ablation is the preferred treatment for symptomatic varicose veins with axial reflux, offering less postprocedure pain, reduced morbidity, and earlier return to activity

Endovenous thermal ablation (radiofrequency ablation [RFA] and endovenous laser ablation [EVLA]) has largely replaced surgery as the standard of care

Ultrasound-guided foam sclerotherapy (UGFS) represents a less invasive option but has higher recurrence rates

Reviewer #1 (Public review):

Summary:

In this study, Besson et al. investigate how environmental nutrient signals regulate chromosome biology through the TORC1 signaling pathway in Schizosaccharomyces pombe. Specifically, the authors explore the impact of TORC1 on cohesin function-a protein complex essential for chromosome segregation and transcriptional regulation. Through a combination of genetic screens, biochemical analysis, phospho-proteomics, and transcriptional profiling, they uncover a functional and physical interaction between TORC1 and cohesin. The data suggest that reduced TORC1 activity enhances cohesin binding to chromosomes and improves chromosome segregation, with implications for stress-responsive gene expression, especially in subtelomeric regions.

Strengths:

This work presents a compelling link between nutrient sensing and chromosome regulation. The major strength of the study lies in its comprehensive and multi-disciplinary approach. The authors integrate genetic suppression screens, live-cell imaging, chromatin immunoprecipitation, co-immunoprecipitation, and mass spectrometry to uncover the functional connection between TORC1 signaling and cohesin. The use of phospho-mutant alleles of cohesin subunits and their loader provides mechanistic insight into the regulatory role of phosphorylation. The addition of transcriptomic analysis further strengthens the biological relevance of the findings and places them in a broader physiological context. Altogether, the dataset convincingly supports the authors' main conclusions and opens up new avenues of investigation.

Points that remain open but are appropriately discussed by the authors:

(1) The authors propose that nutrient status influences cohesin regulation. While this is not directly tested under defined nutrient conditions (e.g., by systematically examining cohesin dynamics or phosphorylation across nutrient states), the rationale is well explained in the text, and the study provides a strong foundation for addressing this question in future work.

(2) The upstream signaling cascade downstream of TORC1 remains to be fully elucidated. In particular, the identity of the relevant kinases (e.g., whether Sck1/Sck2 or other effectors are involved) and whether TORC1 directly phosphorylates Mis4 or Psm1 are not resolved. The authors acknowledge these mechanistic gaps, which represent logical next steps rather than shortcomings of the current study.

Reviewer #1 (Public review):

Summary:

This manuscript presents high resolution cryoEM structures of VPS34-complex II bound to Rab5A at 3.2A resolution. The Williams group previously reported the structure of VPS34 complex II bound to Rab5A on liposomes using tomography, and therefore the previous structure, although very informative, was at lower resolution.

The first new structure they present is of the 'REIE>AAAA' mutant complex bound to RAB5A. The structure resembles the previously determined one except an additional molecule of RAB5A was observed bound to the complex in a new position, interacting with the solenoid of VPS15.

Although this second binding site exhibited reduced occupancy of RAB5A in the structure, the authors determined an additional structure in which the primary binding site was mutated to prevent RAB5A binding ('REIE>ERIR'). In this structure, there is no RAB5A bound to the primary binding site on VPS34, but the RAB5A bound to VPS15 now has strong density. The authors note that the way in which RAB5A interacts with each site is distinct, though both interfaces involve the switch regions. The authors confirm the location of this additional binding site using HDX-MS.

The authors then determine multiple structures of the wild-type complex bound to RAB5A from a single sample, as they use 3D classifications to separate out versions of the complex bound to 0, 1, or 2 copies of RAB5A. Overall the structure of VPS34-Complex II does not change between the different states, and the data indicate that both RAB5A binding sites can be occupied at the same time.

The authors then design a new mutant form of the complex (SHMIT>DDMIE) that is expected to disrupt the interaction at the secondary site between VPS15 and RAB5A. This mutation had a minor impact on the Kd for RAB5A binding, but when combined with the REIE>ERIR mutation of the primary binding site, RAB5A binding to the complex was abolished.

Comparison of sequences across species indicated that the RAB5A binding site on VPS15 was conserved in yeast while the RAB5A binding site on VPS34 is not.

The authors tested the impact of a correspond yeast Vps15 mutation (SHLITY>DDLIEY) predicted to disrupt interaction with yeast Rab5/Vps21, and found this mutant Vps15 protein was mislocalized and caused defective CPY processing.

The authors then compare these structures of the RAB5A-class II complex to recently published structures from the Hurley group of the RAB1A-class I complex, and find that in both complexes the Rab protein is bound to the VPS34 binding site in a somewhat similar manner. However, a key difference is the position of VPS34 is slightly different in the two complexes because of the unique ATL14L and UVRAG subunits in the class I and class II complexes, respectively. This difference creates a different RAB binding pocket that explains the difference in RAB specificity between the two complexes.

Finally, the higher resolution structures enable the authors to now model portions of BECLIN1 and UVRAG that were not previously modeled in the cryoET structure.

Strengths:

Overall I found this to be an interesting and comprehensive study of the structural basis for interaction of RAB5A with VPS34-complex II. The authors have performed experiments to validate their structural interpretations, and they present a clear and thorough comparative analysis of the Rab binding sites in the two different VPS34 complexes. The result is a much better understanding of how two different Rab GTPases specifically recruit two different, but highly similar complexes to the membrane surface.

Weaknesses:

No significant weaknesses noted.

Reviewer #1 (Public review):

Summary:

The manuscript from Jones and colleagues investigates a previously described phenomenon in which P. falciparum malaria parasites display increased trafficking of proteins displayed on the surface of infected RBCs as well as increased cytoadherence in response to febrile temperatures. While this parasite response was previously described, it was not uniformly accepted, and conflicting reports can be found in the literature. This variability likely arises due to differences in the methods employed and the degree of temperature increase that the parasites were exposed to. Here the authors are very careful to employ a temperature shift that likely reflects what is happening in infected humans and that they demonstrate is not detrimental to parasite viability or replication. In addition, they go on to investigate what steps in protein trafficking are affected by exposure to increased temperature and show that the effect is not specific to PfEMP1 but rather likely affects all transmembrane domain containing proteins that are trafficked to the RBC. They also detect increased rates of phosphorylation of trafficked proteins, consistent with overall increased protein export.

Strengths:

The authors used a relatively mild increase in temperature (39 degrees) that they demonstrate is not detrimental to parasite viability or replication. This enabled them to avoid potential complications of more severe heat shock that might have affected previously published studies. They employed a clever method of fractionation of RBCs infected with a var2csa-nanoluc fusion protein expressing parasite line to determine which step in the export pathway was likely accelerating in response to increased temperature. This enabled them to determine that export across the PVM is being affected. They also explored changes in phosphorylation of exported proteins and demonstrated that the effect is not limited to PfEMP1 but appears to affect numerous (or potentially all) exported transmembrane domain containing proteins.

Impact and conclusions:

The study shows that protein export, including PfEMP1 and PSAC, are accelerated in response to mild heat shock. This has implications for disease severity as well as our understanding of protein trafficking in these unique organisms. There is increasing interest in asymptomatic infections, which have been proposed to be a major reservoir for transmission and generally are not associated with fever. It will be interesting to consider whether reduced (or slower) trafficking of these proteins has a selective advantage for parasites in asymptomatic infections.

Reviewer #1 (Public review):

Summary:

It is well known that neurons in the medial prefrontal cortex (mPFC) are involved in higher cognitive functions such as executive planning, motivational processing and internal state mediated decision-making. These internal states often correlate with the emotional states of the brain. While several studies point to the role of mPFC in regulating behavior based on such emotional states, the diversity of information processing in its sub-populations remains a less explored territory. In this study, the authors try to address this gap by identifying and characterizing some of these sub-populations in mice using a combination of projection-specific imaging, function-based tagging of neurons, multiple behavioral assays and ex-vivo patch clamp recordings.

Strengths:

The authors targeted mPFC projections to the nucleus accumbens (NAc) and basolateral amygdala (BLA). Using the open field task (OFT), the authors identified four relevant behavioral states as well as neurons active while the animal was in the center region ("center-ON neurons"). By characterizing single unit activity and using dimensionality reduction, the authors show differentiated coding of behavioral events at both the projection and functional levels. They further substantiate this effect by showing higher sensitivity of mPFC-BLA center-ON neurons during time spent in the open arms of the elevated plus maze (EPM). The authors then pivoted to the three-chamber social interaction (SI) assay to show the different subsets of neurons encode preference of social stimulus over non-social. This reveals an interesting diversity in the function of these sub-populations on multiple levels. Lastly, the authors used the tube test as a manipulation of the anxiety state of mice and compared behavioral differences before/after in the OFT and social interaction tasks. This experiment revealed that "losers" of the tube test spend less time in the center of the open field while "winners" show a stronger preference for the familiar mouse over the object. Using patch-clamp experiments, the authors also found that "winners" exhibit stronger synaptic transmission in the mPFC-NAc projection while "losers" exhibit stronger synaptic transmission in the mPFC-BLA projection. Given the popularity of the tube test assay in rank determination, this provides useful insights into possible effects on anxiety levels and synaptic plasticity. Overall, the many experiments performed by the authors reveal interesting differences in mPFC neurons relative to their involvement in high or low anxiety behaviors, social preference and social rank.

Weaknesses:

The authors focused primarily on female mice limiting generalizability and leaving the readers with questions about the impact of sex differences on their results. The tube test is used as a manipulation of the "emotional state" in several of the experiments. While the authors show the changes to corticosterone levels as a consequence of win/loss in the tube test, stronger claims might be made with comparisons to other gold standard stressors such as forced social defeat or social isolation.

Reviewer #1 (Public review):

A well-designed and preregistered simulation study investigating whether replication-success metrics can be applied to assess animal-to-human translation. The study is comprehensive, uses realistic parameter settings, and provides valuable insights into how different metrics behave under varied conditions.

Strengths:

(1) Methodologically rigorous and transparently preregistered.

(2) Comprehensive simulation design covering a wide range of plausible scenarios.

(3) Clear description of metrics and decision rules.

(4) Valuable contribution to understanding the limitations of applying replication metrics to translation questions.

Weaknesses:

(1) The conceptual distinction between replication and translation could be more clearly emphasized.

(2) Interpretation of results is dense and can be challenging to follow without a clear and summarized.

(3) Some simulation parameters (effect sizes, heterogeneity, and number of animal studies) require more substantial justification.

(4) Practical recommendations could be more explicit to guide applied researchers.

Reviewer #1 (Public review):

Summary:

T cells that recognize lipids - CD1c - are frequent in circulation; however, their role in infection is unclear. This study aims to understand how Mtb infection can shape the responses of CD1c-specific T cells. CD1c is expressed in MTB granuloma, but in lower amounts than in nearby inflamed tissue. Mtb infection downregulates the expression of CD1c on monocyte-derived DCs. Single-cell RNA sequencing revealed the cytotoxic program inherent to the lipid-CD1c-specific T cells. Using an in vitro APC system where CD1c expression remains intact upon Mtb infection, the authors suggest that these T cells react better to Mtb-infected than uninfected Cd1c-expressing APC and reduce Mtb burden in infected cells. Therefore, Cd1c downregulation could be an immune evasion strategy used by Mtb.

Strengths:

This study asks an important question. The single-cell transcription analysis suggests the inherent cytotoxic program of lipid-CD1c cells and provides insights into their phenotypic and potential functional profiles. Function experiments suggest that these autoreactive T cells can react to Mtb infection, adding to the paradigm of infection control by these non-conventional T cell populations.

Weaknesses:

The study lacks sufficient rigor; conclusions may be strengthened with the incorporation of more controls, and some deeper characterization of the THP1 system and the CD1c-specific T cells isolated from blood. Crucial conclusions are drawn from the cell mixing experiments involving the engineered THP-1 system and CD1c-lipid-specific T cells from blood. These cells need more in-depth characterization. The expression of MHC-I/II is clearly reduced in THP1-CD1c cells. However, it is important to ensure that it is completely abolished, since a residual expression can skew the result with activation of conventional T cells in the blood or low levels of conventional T cells that may be present in the CD1c-tetra/multimer sorted T cells. CD1c-tetra/multimer sorting should include more markers than used in this study.

Figure 2: The immunohistochemistry appears to be shown only for one biopsy; it may be worth quantifying the immunohistochemistry of all five. The expression of CD1 molecules goes up during the differentiation of MoDC. And Mtb infection prevents or dampens the upregulation. Does Mtb infection downregulate the CD1 expression of mature DCs? Can the effect of Mtb on the expression of CD1a,b,c molecules be investigated using CD1c-expressing DCs from blood? What could be the reason THP-1 cells do not downregulate CD1 molecules upon Mtb infection, and how about the expression of CD1a and b?

Figure 3: (F) What does the X-axis read for the no infection group? The value for MOI = 0 should be incorporated for the infected T cell group.

Figure 4: In the lysis assay, THP1-CD1c cells (uninfected and infected) incubated alone should be incorporated.

Figure 5: A quantitative brief on the single cell TCR sequencing - including how many T cells were sequenced and the frequency of different clone including EM1 and EM2 - should be shown.

Selection

Initial Assessment: Transthoracic echocardiography (TTE) is recommended at diagnosis to assess aortic valve anatomy, valve function, and thoracic aortic diameters. CT or MRI is reasonable for comprehensive anatomic assessment. [1]

Surveillance Imaging: The choice depends on aneurysm location: [2]

Aortic root/proximal ascending aorta: TTE can be used if measurements correlate well with CT/MRI

Mid-ascending, arch, or descending thoracic aorta: CT or MRI is recommended

MRI is preferred for long-term surveillance to avoid cumulative radiation exposure from serial CT scans [1][3]

Surveillance Intervals

Size-Based Recommendations: [2-4]

<4.0 cm: Every 2-3 years if stable

4.0-4.4 cm: Every 2 years

4.5-4.9 cm: Annually

5.0-5.4 cm: Every 6-12 months (consider optimization for repair)

≥5.5 cm: Surgical evaluation indicated

Initial surveillance: Obtain follow-up imaging at 6-12 months after diagnosis to establish the growth rate. If stable, adjust interval based on size. [1]

Growth rate considerations: Descending thoracic aneurysms grow faster than ascending aneurysms (mean 2.76 mm/year vs 1 mm/year overall). Growth accelerates exponentially above 4.5 cm diameter. [3-4]

elective surgical repair is suggested at 5.5 cm in patients without underlying connective tissue disorders, with earlier intervention at 4.5-5.0 cm in patients with connective tissue disorders or bicuspid aortic valve

Reviewer #1 (Public review):

The study by Lotonin et al. investigates correlates of protection against African swine fever virus (ASFV) infection. The study is based on a comprehensive work, including the measurement of immune parameters using complementary methodologies. An important aspect of the work is the temporal analysis of the immune events, allowing to capture the dynamics of the immune responses induced after infection. Also, the work compares responses induced in farm and SPF pigs, showing the later an enhanced capacity to induce a protective immunity. Overall, the results obtained are interesting and relevant for the field. The findings described in the study further validate work form previous studies (critical role of virus-specific T cell responses), and provide new evidence on the importance of a balanced innate immune response during the immunization process. This information increases our knowledge on basic ASF immunology, one of the important gaps in ASF research that needs to be addressed for a more rational design of effective vaccines. As discussed in the manuscript, the results provide targets which can be further validated in other models, such as immunization using live attenuated vaccines.

Overall the conclusions of the work are well supported by the results, and most of the issues mentioned during the review have been properly addressed during the revision, improving the quality of the final manuscript. While some limitations remain, I consider that they do not invalidate the results obtained and are well discussed by the authors.

The study is highly relevant for the field, representing a step forward in our understanding of ASF protective immunity, providing immune targets to be further explored in other models and during vaccine development.

Reviewer #1 (Public review):

Summary:

This manuscript investigates how herbivorous insects, specifically whiteflies and planthoppers, utilize salivary effectors to overcome plant immunity by targeting the RLP4 receptor.

Strengths:

The authors present a strong case for the independent evolution of these effectors and provide compelling evidence for their functional roles.

Comments on revisions:

The authors have addressed all my concerns.

Reviewer #1 (Public review):

Summary:

Zeng et al. characterized the dynamic brain states that emerged during episodic encoding and the reactivation of these states during the offline rest period in children aged 8-13. In the study, participants encoded scene images during fMRI and later performed a memory recognition test. The authors adopted the BSDS approach and identified four states during encoding, including an "active-encoding" state. The occupancy rate of, and the state transition rates towards, this active-encoding state positively predicted memory accuracy across participants. The authors then decoded the brain states during pre- and post-encoding rests with the model trained on the encoding data to examine state reactivation. They found that the state temporal profile and transition structure shifted from encoding to post-encoding rest. They also showed that the mean lifetime and stability (measured with self-transition probability) of the "default-mode" state during post-encoding rest predict memory performance.

Strengths:

How brain dynamics during encoding and offline rest support long-term memory remains understudied, particularly in children. Thus, this study addresses an important question in the field. The authors implemented an advanced computational framework to identify latent brain states during encoding and carefully characterized their spatiotemporal features. The study also showed evidence for the behavioral relevance of these states, providing valuable insights into the link between state dynamics and successful encoding and consolidation.

Weaknesses:

(1) If applicable, please provide information on the decoding performance of states during pre- and post-encoding rests. The Methods noted that the authors applied a threshold of 0.1 z-scored likelihood, and based on Figure S2, it seems like most TRs were assigned a reinstated state during post-encoding rest. It would be useful to know, for the decodable TRs, how strong the evidence was in favor of one state over others. Further, was decoding performance better during post- vs. pre- encoding rest? This is critical for establishing that these states were indeed "reinstated" during rest. The authors showed individual-specific correlations between encoding and post-encoding state distribution, which is an important validation of the method, but this result alone is not sufficient to suggest that the states during encoding were the ones that occurred during rest. The authors found that the state dynamics vary substantially between encoding and rest, and it would be helpful to clarify whether these differences might be related to decoding performance. I am also curious whether, if the authors apply the BSDS approach to independently identify brain states during rest periods (instead of using the trained model from encoding), they find similar states during rest as those that emerged during encoding?

(2) During post-encoding rest, the intermediate activation state (S1) became the dominant state. Overall, the paper did not focus too much on this state. For example, when examining the relationship between state transitions and memory performance, the authors also did not include this state as a part of the analyses presented in the paper (lines 203-211). Could the author report more information about this state and/or discuss how this state might be relevant to memory formation and consolidation?

(3) Two outcome measures from the BSDS model were the occupancy rate and the mean lifetime. The authors found a significant association with behavior and occupancy rate in some analyses, and mean lifetime in others. The paper would benefit from a stronger theoretical framing explaining how and why these two different measures provide distinct information about the brain dynamics, which will help clarify the interpretation of results when association with behavior was specific to one measure.

(4) For performance on a memory recognition test, d' is a more common metric in the literature as it isolates the memory signal for the old items from response bias. According to Methods (line 451), the authors have computed a different metric as their primary behavioral measure (hits + correction rejections - misses - false alarms). Please provide a rationale for choosing this measure instead. Have the authors considered computing d' as well and examining brain-behavior relationships using d'?

(5) While this study examined brain state dynamics in children, there was no adult sample to compare with. Therefore, it is hard to conclude whether the findings are specific to children (or developing brains). It would be helpful to discuss this point in the paper.

Reviewer #2 (Public review):

Summary:

The molecular mechanisms underlying ciliogenesis are not well understood. Previously, work from the same group (Wu et al., 2018) identified myosin-Va as an important protein in transporting preciliary vesicles to the mother vesicles, allowing for initiation of ciliogenesis. The exocyst complex has previously been implicated in ciliogenesis and protein trafficking to cilia. Here, Lin et al. investigate the role of exocyst complex protein EXOC6A in cilia formation. The authors find that EXOC6A localizes to preciliary vesicles, ciliary vesicles, and the ciliary sheath. EXOC6A colocalizes with Myo-Va in the ciliary vesicle and the ciliary sheath, and both proteins are removed from fully assembled cilia. EXOC6A is not required for Myo-Va localization, but Myo-VA and EHD1 are required for EXOC6A to localize in ciliary vesicles. The authors propose that EXOC6A vesicles continually remodel the cilium: FRAP analysis demonstrates that EXOC6A is a dynamic protein, and live imaging shows that EXOC6A fuses with and buds off from the ciliary membrane. Loss of EXOC6A reduces, but does not eliminate, the number of cilia formed in cells. Any cilia that are still present are structurally abnormal, with either bent morphologies or transition zone defects. Overall, the analyses and imaging are well done, and the conclusions are well supported by the data. The work will be of interest to cell biologists, especially those interested in centrosomes and cilia.

Strengths:

The TEM micrographs are of excellent quality. The quality of the imaging overall is very good, especially considering that these are dynamic processes occurring in a small region of the cell. The data analysis is well done and the quantifications are very helpful. The manuscript is well-written and the final figure is especially helpful in understanding the model.

The manuscript has greatly improved after revision. In particular, testing GPR161 and BBS9 localization is helpful evidence to demonstrate that transition zone function is disrupted when EXOC6A is lost. The generation of a second knockout clone and tests of antibody specificity are also great additions.

Weaknesses:

None

Reviewer #1 (Public review):

Lipid transfer proteins (LTPs) play a crucial role in the intramembrane lipid exchange within cells. However, the molecular mechanisms that govern this activity remain largely unclear. Specifically, the way in which LTPs surmount the energy barrier to extract a single lipid molecule from a lipid bilayer is not yet fully understood. This manuscript investigates the influence of membrane properties on the binding of Ups1 to the membrane and the transfer of phosphatidic acid (PA) by the LTP. The findings reveal that Ups1 shows a preference for binding to membranes with positive curvature. Moreover, coarse-grained molecular dynamics simulations indicate that positive curvature decreases the energy barrier associated with PA extraction from the membrane. Additionally, lipid transfer assays conducted with purified proteins and liposomes in vitro demonstrate that the size of the donor membrane significantly impacts lipid transfer efficiency by Ups1-Mdm35 complexes, with smaller liposomes (characterized by high positive curvature) promoting rapid lipid transfer.

This study offers significant new insights into the reaction cycle of phosphatidic acid (PA) transfer by Ups1 in mitochondria. The experiments are technically robust and carefully interpreted by the authors. They provide compelling evidence that a positive membrane curvature and the presence of negatively charged phospholipids govern the transfer of PA by the mitochondrial lipid transfer protein Ups1-Mdm35.

Reviewer #1 (Public review):

Summary:

Kim and Parsons present a timely overview of the NTR/prodrug system and its applications in regenerative biology research, with particular emphasis on tissue-specific cell ablation. The system has substantially advanced the field by enabling non-invasive, conditional cell elimination, and has proven especially powerful in zebrafish, though applications in other classical model organisms are also noted. The review covers the historical origins of the NTR system, its use in regeneration studies, small-molecule screening, and genetic and CRISPR-based screening, as well as future directions, including the development of the highly efficient NTR2 enzyme variant.

Strengths:

This is a useful and well-structured contribution. The manuscript is a valuable resource for the regeneration biology community.

Weaknesses:

The impact and scientific value of this paper could be meaningfully enhanced by addressing several points outlined below. The concerns centre on completeness, conceptual precision, and the depth of mechanistic discussion.

(1) Title: Species specificity.

Given that the review's primary focus is the zebrafish model, it would be appropriate to include the species name in the title. This would improve discoverability and accurately set the scope of the article for prospective readers.

(2) Subchapter: Physical injury.

The subchapter enumerates different types of physical injury models but would benefit from a more substantive comparative discussion. In particular, the authors are encouraged to address the following:

(2.1) Outcome comparison: Surgical and other invasive approaches cause damage to entire tissue structures comprising multiple cell types, whereas tissue-specific genetic ablation eliminates a defined cell population while leaving the surrounding architecture largely intact. This fundamental distinction has direct implications for the interpretation of regenerative outcomes and should be clearly articulated.

(2.2) Inflammatory response: Invasive injuries typically trigger a robust inflammatory response, which itself can be a potent driver of regeneration. By contrast, genetic cell ablation may elicit a qualitatively different inflammatory reaction. A comparative discussion of this distinction would help readers appreciate a critical limitation of genetic ablation systems relative to models of natural, accidental tissue damage.

(3) Subchapter: Cell-specific toxins.

This subchapter would benefit from several targeted expansions:

(3.1) Off-target effects: The authors should include evidence that the exemplified drugs have known off-target activities, with a discussion of how these confounded the interpretation of experimental data. At least a few concrete published examples should be cited.

(3.2) Completeness of the toxin list: The current list appears illustrative rather than comprehensive. A more complete enumeration would be valuable, particularly for neurotoxins and drugs targeting sensory cells, as these are highly relevant to the zebrafish regeneration field.

(3.3) Interspecies differences: It would be informative to specify whether drug specificity differs across species, as this is a practical consideration for researchers working in organisms other than zebrafish.

(4) Subchapter: Optogenetic cell ablation.

The authors note that optogenetic cell ablation has not yet been applied in conventional regeneration studies. It would strengthen this section to include a discussion of the underlying reasons for this gap, whether technical or biological, so that readers can appreciate the barriers and potential for future adoption.

(5) Terminology: "Suicide gene".

The use of the term "suicide gene" to nitroreductase is conceptually imprecise and merits reconsideration. Strictly speaking, a suicide gene is one whose expression alone is sufficient to kill the cell, as in the case of genes encoding direct triggers of apoptosis or the catalytic A subunit of diphtheria toxin (DTA). NTR does not meet this criterion: it requires the exogenous administration of a prodrug (e.g., metronidazole) to produce a cytotoxic metabolite, and is therefore only conditionally lethal.

It is worth noting that nitroreductases evolved in bacteria and fungi as enzymes involved in chemoprotection and detoxification, converting potentially toxic and mutagenic nitroaromatic compounds into less harmful metabolites (PMID: 18355273). This biological context further underscores that NTR is not inherently a lethal protein. The authors are encouraged to replace or qualify the term "suicide gene" and instead adopt terminology that more accurately reflects the conditional, prodrug-dependent nature of the system.

(6) NTR/MTZ in regenerative studies: Mechanistic depth.

While the review catalogues several studies employing the NTR/MTZ system, it lacks mechanistic depth regarding the cellular basis of ablation. The following questions should be addressed, where evidence exists in the literature:

(6.1) Temporal dynamics of cell death: What is known about the kinetics of NTR/MTZ-induced lethality across different tissue types in larval and adult zebrafish, as well as other organisms? Are there age- and tissue-specific differences in the speed or completeness of ablation?

(6.2) Mechanism of cell death: What is the cellular basis of NTR/MTZ-induced cytotoxicity in zebrafish? In particular, do the toxic metabolites preferentially cause mitochondrial damage or nuclear DNA damage, and what downstream death pathways are engaged?

(6.3) Proliferative versus post-mitotic cells: Are proliferating and non-proliferating cells equally sensitive to the NTR/MTZ system, or does the proliferative status of a cell influence susceptibility? This is a practically important question for researchers designing ablation experiments in tissues with mixed cell populations.

(6.4) Ablation of progenitor cells: Are there published examples demonstrating that co-ablation of differentiated functional cells and organ-specific progenitor cells abolishes regenerative capacity? Such examples would be highly informative in illustrating the system's power to dissect the cellular requirements for regeneration.

Addressing the points above, particularly the comparative discussion of injury models and inflammatory responses, the clarification of terminology, and the mechanistic discussion of NTR/MTZ-induced cell death would substantially strengthen the review's scientific contribution and utility.

Reviewer #1 (Public review):

Summary:

Chen et al. describe metabolic phenotypes in Dp16 Down Syndrome mice, specifically the Dp(16)1Yey/+ mice - segmental duplication model carrying a majority of the triplicated Hsa21 gene orthologs. The group has performed metabolic phenotyping data in chow and high-fat diets, as well as undertaking a transcriptomic and metabolomic approach in tissues such as white and brown adipose tissues, liver, skeletal muscle, and hypothalamus to reveal both shared and sex-specific differences. The group describes sexual dimorphism in body weight, body temperature, food intake, and physical activity. Core shared features are insulin resistance, glucose intolerance, impaired lipid clearance, and dyslipidaemia in the Dp16 mice. They report tissue signatures of immune activation and a pro-inflammatory state, ER and oxidative stress, fibrosis, impaired glucose and fatty acid catabolism, altered lipid and bile acid profiles, and reduced mitochondrial respiration in Dp16 mice.

Strengths:

Overall, this is a good study with detailed, comprehensive data from an excellent group who have previously published on metabolic phenotyping of 2 other Down Syndrome mouse models. Although somewhat descriptive, it does certainly add to the current field and understanding of strengths and weaknesses of Down Syndrome mouse models, as well as identifying new features whilst strengthening previously suggested mechanisms.

Weaknesses:

Many aspects of this study have been described in other Down syndrome mouse models, though there are certainly aspects that are new. It would be useful if the authors could do a direct critique and comparison with previous publications in the area, utilising the same Down Syndrome mouse model. There are also a few limitations in the number of animals used and the interpretation of the data that should be acknowledged.

Reviewer #1 (Public review):

Summary:

Noell et al have presented a careful study of the dissociation kinetics of Kinesin (1,2,3) classes of motors moving in vitro on a microtubule. These motors move against the opposing force from a ~1 micron DNA strand (DNA tensiometer) that is tethered to the microtubule and also bound to the motor via specific linkages (Figure 1A). The authors compare the time for which motors remain attached to the microtubule when they are tethered to the DNA, versus when they are not. If the former is longer, the interpretation is that the force on the motor from the stretched DNA (presumed to be working solely along the length of the microtubule) causes the motor's detachment rate from the microtubule to be reduced. Thus, the specific motor exhibits "catch-bond" like behaviour.

Strengths:

The motivation is good - to understand how kinesin competes against dynein through the possible activation of a catch bond. Experiments are well done, and there is an effort to model the results theoretically.

Weaknesses:

The motivation of these studies is to understand how kinesin (1/2/3) motors would behave when they are pitted in a tug of war against dynein motors as they transport cargo in a bidirectional manner on microtubules. Earlier work on dynein and kinesin motors using optical tweezers has suggested that dynein shows a catch bond phenomenon, whereas such signatures were not seen for kinesin. Based on their data with the DNA tensiometer, the authors would like to claim that (i) Kinesin1 and Kinesin2 also show catch-bonding and (ii) the earlier results using optical traps suffer from vertical forces, which complicates the catch-bond interpretation.

While the motivation of this work is reasonable, and the experiments are careful, I find significant issues that the authors have not addressed:

(1) Figure 1B shows the PREDICTED force-extension curve for DNA based on a worm-like chain model. Where is the experimental evidence for this curve? This issue is crucial because the F-E curve will decide how and when a catch-bond is induced (if at all it is) as the motor moves against the tensiometer. Unless this is actually measured by some other means, I find it hard to accept all the results based on Figure 1B.

(2) The authors can correct me on this, but I believe that all the catch-bond studies using optical traps have exerted a load force that exceeds the actual force generated by the motor. For example, see Figure 2 in reference 42 (Kunwar et al). It is in this regime (load force > force from motor) that the dissociation rate is reduced (catch-bond is activated). Such a regime is never reached in the DNA tensiometer study because of the very construction of the experiment. I am very surprised that this point is overlooked in this manuscript. I am therefore not even sure that the present experiments even induce a catch-bond (in the sense reported for earlier papers).

(3) I appreciate the concerns about the Vertical force from the optical trap. But that leads to the following questions that have not at all been addressed in this paper:

(i) Why is the Vertical force only a problem for Kinesins, and not a problem for the dynein studies?

(ii) The authors state that "With this geometry, a kinesin motor pulls against the elastic force of a stretched DNA solely in a direction parallel to the microtubule". Is this really true? What matters is not just how the kinesin pulls the DNA, but also how the DNA pulls on the kinesin. In Figure 1A, what is the guarantee that the DNA is oriented only in the plane of the paper? In fact, the DNA could even be bending transiently in a manner that it pulls the kinesin motor UPWARDS (Vertical force). How are the authors sure that the reaction force between DNA and kinesin is oriented SOLELY along the microtubule?

(4) For this study to be really impactful and for some of the above concerns to be addressed, the data should also have included DNA tensiometer experiments with Dynein. I wonder why this was not done?

While I do like several aspects of the paper, I do not believe that the conclusions are supported by the data presented in this paper for the reasons stated above.

Reviewer #1 (Public review):

Summary:

Eroglu and Hobert demonstrate that injecting CRISPR guides and repair constructs to target three genes at a time, tagging each with a different fluorescent protein, and selecting which gene to tag with which fluorophore based on genes' expression levels, can improve the efficiency of gene tagging.

Strengths:

This manuscript demonstrates that three genes can be targeted efficiently with three different fluorophores. It also presents some practical considerations, like using the fluorophore least complicated by agar/worm autofluorescence for genes with low expression levels, and cost calculations if the same methods were used on all genes.

Weaknesses:

Eroglu has demonstrated in a previous publication that single-stranded DNA injection can increase the efficiency of CRISPR in C. elegans while inserting two fluorescent proteins and a co-CRISPR marker into three loci. The current work is, therefore, an incremental advance. In general, I applaud the authors' willingness to think ahead to how whole proteome tagging might be accomplished, but I predict that the advance here will be one of many small advances that will get the field to that goal. The title vastly oversells the advance in my view, and the first sentence of the Discussion seems a more apt summary of the key advance here.

Some injections target genes on the same chromosome together, which will create unnecessary issues when doing necessary backcrossing, especially if the mutation rate is increased by CRISPR. Also, the need for backcrossing and perhaps sequencing made me wonder if injecting 3 together really is helpful vs targeting each gene separately, since only 5 worms need to be injected.

The limited utility of current blue fluorescent proteins makes me wonder if it's worth using at all at this stage, before there are better blue (or far red) fluorescent proteins.

Some literature reviews, particularly in the Introduction and Abstract, rely too much on recent examples from the authors' laboratory instead of presenting the state of the field. I'd like to have known what exactly has been done with simultaneous injection targeting multiple loci more thoroughly, comparing what has been accomplished to date by various laboratories' advances to date.

Reviewer #1 (Public review):

This manuscript describes the pattern of relaxed selection observed at spermatogenesis genes in gorillas, presumably due to the low sperm competition associated with single-male polygyny. The analyses to detect patterns of selection are very thorough, as are the follow-up analyses to characterize the function of these genes. Furthermore, the authors take the extra steps of in vivo determination of function with a Drosophila model.

This is an excellent paper. It addresses the interesting phenomenon of relaxation of selection as a genomic signal of reproductive strategies using multiple computational approaches and follow-up analyses by pulling in data from GO, mouse knockouts, human infertility database, and even Drosophila RNAi experiments. I really appreciate the comprehensive and creative approach to analyze and explore the data. As far as I can tell, the analyses were performed soundly and statistics are appropriate. The Introduction and Discussion sections are thoughtful and well-written. I have no major criticisms of the manuscript, just a few minor thoughts.

In the "Caveats and Limitations" section of the Discussion, the first paragraph of this section states the obvious that genetic manipulation of gorillas is not feasible. Beyond a reminder to the reader that this was a rationale for the Drosophila work, it isn't really adding much insight.

I do agree with one of the initial reviewers that a comparative approach would add powerful perspective on the evolution of these genes. At the same time, I agree with the authors that the present work is comprehensive and can stand in its own in providing convincing evidence that many male reproductive genes in gorillas have experienced relaxed selection, without reference to other species with similar mating systems. I do not think that the elephant seal data adds a useful perspective.

Reviewer #1 (Public review):

Summary:

This study presents an interesting investigation into the role of trained immunity in inflammatory bowel disease, demonstrating that β-glucan-induced reprogramming of innate immune cells can ameliorate experimental colitis. The findings are novel and clinically relevant, with potential implications for therapeutic strategies in IBD. The combination of functional assays, adoptive transfer experiments, and single-cell RNA sequencing provides comprehensive mechanistic insights. However, some aspects of the study could benefit from further clarification to strengthen the conclusions.

Strengths:

(1) This study elegantly connects trained immunity with IBD, demonstrating how β-glucan-induced innate immune reprogramming can mitigate chronic inflammation.

(2) Adoptive transfer experiments robustly confirm the protective role of monocytes/macrophages in colitis resolution.

(3) Single-cell RNA sequencing provides mechanistic depth, revealing the expansion of reparative Cx3cr1⁺ macrophages and their contribution to epithelial repair.

(4) The work highlights the therapeutic potential of trained immunity in restoring gut homeostasis, offering new directions for IBD treatment.

Weaknesses:

While β-glucan may exert its training effect on hematopoietic stem cells, performing ATAC-seq on HSCs or monocytes to profile chromatin accessibility at antibacterial defense and mucosal repair-related genes would further validate the trained immunity mechanism. Alternatively, the authors could acknowledge this as a study limitation and future research direction.

Comments on revisions:

My concerns have been fully addressed. I have no additional comments.

Reviewer #1 (Public review):

Summary:

Noell et al have presented a careful study of the dissociation kinetics of Kinesin (1,2,3) classes of motors moving in-vitro on a microtubule. These motors move against the opposing force from a ~1 micron DNA strand (DNA tensiometer) that is tethered to the microtubule and also bound to the motor via specific linkages (Fig 1A). Authors compare the time for which motors remain attached to the microtubule when they are tethered to the DNA, versus when they are not. If the former is longer, the intepretation is that the force on the motor from the stretched DNA (presumed to be working solely along the length of the microtubule) causes the motor's detachment rate from the microtubule to be reduced. Thus, the specific motor exhibits "catch-bond" like behaviour.

Strengths:

The motivation is good - to understand how kinesin competes against dynein through the possible activation of a catch bond. Experiments are well done and there is an effort to model the results theoretically.

Weaknesses:

The motivation of these studies is to understand how kinesin (1/2/3) motors would behave when they are pitted in a tug of war against dynein motors as they transport cargo in bidirectional manner on microtubules. Earlier work on dynein and kinesin motors using optical tweezers has suggested that dynein shows catch bond phenomenon, whereas such signatures were not seen for kinesin. Based on their data with DNA tensiometer, the authors would like to claim that (i) Kinesin1 and kinesin2 also show catch-bonding and (ii) The earlier results using optical traps suffer from vertical forces, which complicates the catch-bond interpretation.

Comments on revised version:

I am not fully convinced about the responses from authors, so I would like to retain my original assessment of the paper. The same may be made available for public viewing, along with the responses of the authors. Readers can go through both and form their opinion.

Reviewer #1 (Public review):

Summary:

This manuscript by Xiong and colleagues presents a compelling validation of UniDesign, a fully computational protein design framework, by using it to engineer a novel, PAM-relaxed variant of Staphylococcus aureus Cas9 (SaCas9) named KRH. The core achievement is the successful de novo generation of a high-performance nuclease (E782K/N968R/R1015H) solely through in silico modeling, without any subsequent experimental optimization or directed evolution. The authors demonstrate that KRH expands the SaCas9 PAM specificity from NNGRRT to NNNRRT, achieving genome editing and base editing efficiencies across multiple human cell types that are comparable to, and sometimes exceed, the well-known evolution-derived KKH variant. The work positions UniDesign not merely as an analytical tool, but as a powerful engine for the generative design of complex molecular functions, offering a scalable and mechanistically insightful alternative to traditional experimental screening.

Strengths:

This is an outstanding manuscript that serves as a powerful proof-of-concept for the next generation of computational protein design. The primary selling point-the raw predictive and generative power of UniDesign-is convincingly demonstrated throughout.

The manuscript shows that the tool can:<br /> (1) successfully navigate a complex sequence landscape to identify a minimal set of three mutations (KRH) that remodel a critical protein-DNA interface;<br /> (2) accurately model and balance the delicate interplay between specific base contacts and non-specific backbone interactions to achieve relaxed PAM specificity;<br /> (3) deliver a final product whose performance is indistinguishable from, and in some cases superior to, a variant that required extensive wet-lab evolution.

The experimental validation is rigorous, thorough, and directly supports the computational predictions. This work will stand as a landmark study for the field, illustrating that computational design has matured to the point where it can reliably generate sophisticated tools for genome engineering.

(1) Demonstration of Generative Power:

The most significant finding is that UniDesign, without any experimental feedback, generated a variant (KRH) that matches the performance of the evolution-derived KKH. This is a remarkable achievement. The iterative design strategy-first reducing PAM bias (R1015H), then restoring binding through non-specific interactions (e.g., N968R, E782K)-is a textbook example of rational design, but it is executed entirely by the algorithm. This validates UniDesign's energy function and search algorithm as capable of capturing the subtle biophysical principles governing PAM recognition.

(2) Mechanistic Insight as a Built-in Feature:

A key advantage of UniDesign highlighted by this work is its inherent ability to provide mechanistic explanations. The computational models not only predicted which mutations would work (e.g., N968R over N968K in the KRH variant) but also why they work. The structural and energetic analyses showing the bidentate salt bridge formed by Arg968 versus the single bond formed by Lys968 (Figure 4A) is a perfect example of how the tool's output can rationalize functional differences, a level of insight that is rarely attainable from directed evolution campaigns alone.

(3) Scalability and Accessibility for Engineering:

The authors explicitly contrast UniDesign's efficiency (minutes to hours per design run) with the computational expense of methods like COMET and the experimental overhead of directed evolution. The improvements to UniDesign v1.2, specifically the mutation-count and sequence-uniqueness penalties, directly address a key challenge in computational design (generating diverse, low-energy point-mutant libraries). This positions the tool as a highly accessible and scalable platform for engineering other CRISPR systems, a point that will be of immense interest to the community.

Weaknesses:

(1) Title and Abstract Emphasis:

The title and abstract are effective but could be slightly sharpened to emphasize the primary message. Consider a title like "Fully computational design of a PAM-relaxed SaCas9 variant with UniDesign demonstrates power to match directed evolution." The abstract could more explicitly state upfront that the design was achieved without any experimental iteration.

(2) Figure 1, Panel M:

The data points in panel M are currently presented at a font size that makes them difficult to read, particularly the labels for the many triple-mutant variants. This density obscures the clear identification of the top-performing designs, such as the KRH variant selected for experimental validation. I recommend that the authors increase the font size of all text elements within this panel, including axis labels, tick marks, and data point labels, to improve legibility. If necessary, the panel dimensions can be adjusted or the layout reorganized to accommodate the larger text without compromising clarity. Ensuring this figure is readable is important, as it visually communicates the energetic convergence that led to the selection of KRH.

(3) Generality of the Design Strategy for Other PAM Positions:

The design strategy focused on relaxing specificity at the highly constrained third position of the PAM (the guanine in NNGRRT). How transferable is this specific strategy (i.e., disrupting a key specific contact and compensating with non-specific backbone binders) to relaxing other positions in the PAM or to other Cas enzymes with different PAM-interaction architectures? A short discussion on this point would help readers understand the broader applicability of the "fine-tuning the balance" principle.

Reviewer #1 (Public review):

Summary:

While the results show some loss in the eyelid meibomian glands, there is significant gland retention in HSD3b6 KO mice, as shown in Figure 2. This is supported by the lack of DEG patterns showing downregulation of Meibum lipid genes (AWAT2, Far2, Soat1, Plin2, SCD, etc.), and no decrease in Pparg expression, known to be critical for meibomian gland lipid gene expression.

Weaknesses:

It should be noted that while the authors indicate that CD38 is significantly up-regulated in the HSD3b6 KO mouse, the increase was not sufficient to show a significant adjusted P-value. Bulk RNA sequencing also shows no significant change in meibum lipid gene expression for aged mice that are treated with 78c, an inhibitor of CD38, which the authors indicate increases NAD levels, leading to increased meibomian gland size compared to vehicle-treated mice. Unfortunately, there was no increase in meibum lipid gene expression with 78c, as identified by adjusted P-value. However, it should be noted that the supplemental file covering DEG expression was labeled as a Microarray analysis. This did not include the 78c+NMN treated mice, which the authors contend show a more impactful effect on the meibomian gland.

Reviewer #1 (Public review):

It is widely accepted that the number of muscle stem cells (MuSCs) declines with aging, leading to diminished regenerative capacity. In this study, when MuSCs were labeled with YFP at a young age, the authors found that the YFP-positive MuSC population remained stable with aging. However, VCAM1 and Pax7 expression levels were reduced in the YFP-positive MuSCs. These VCAM1-negative/low cells exhibited limited proliferative potential and reduced regenerative ability upon transplantation into MuSC-depleted mice. Furthermore, Vcam1-/low MuSCs were highly sensitive to senolysis and represented the population in which Vcam1 expression could be restored by DHT. Finally, the authors identified CD200 and CD63 as markers capable of detecting the entire geriatric MuSC population, including Vcam1-/low cells. Although numerous studies have reported an age-related decline in MuSC numbers, this study challenges that consensus. Therefore, the conclusions require further careful validation.

Major comments:

(1) As mentioned above, numerous studies have reported that the number of MuSCs declines with aging. The authors' claim is valid, as Pax7 and Vcam1 were widely used for these observations. However, age-related differences have also been reported even when using these markers (Porpiglia et al., Cell Stem Cell 2022; Liu et al., Cell Rep 2013). When comparing geriatric Vcam1⁺ MuSCs with young MuSCs in this study, did the authors observe any of the previously reported differences? Furthermore, would increasing the sample size in Figure 1 reveal a statistically significant difference? The lack of significance appears to result from variation within the young group. In addition, this reviewer requests the presentation of data on MuSC frequency in geriatric control mice using CD200 and CD63 in the final figure.

(2) Can the authors identify any unique characteristics of Pax7-VCAM-1 GER1-MuSCs using only the data generated in this study, without relying on public databases? For example, reduced expression of Vcam1 and Pax7. The results of such analyses should be presented.

(3) In the senolysis experiment, the authors state that GER1-MuSCs were depleted. However, no data are provided to support this conclusion. Quantitative cell count data would directly address this concern. In addition, the FACS profile corresponding to Figure 4D should be included.

(4) Figure S4: It remains unclear whether DHT enhances regenerative ability through restoration of the VCAM1 expression in GER1-MuSCs, as DHT also acts on non-MuSC populations. Analyses of the regenerative ability of Senolysis+DHT mice may help to clarify this issue.

(5) Why are there so many myonuclear transcripts detected in the single-cell RNA-seq data? Was this dataset actually generated using single-nucleus RNA-seq? This reviewer considers it inappropriate to directly compare scRNA-seq and snRNA-seq results.

Comments on revisions:

Related to Comment#3: The percentage is also influenced by the number of other cell types. Therefore, to demonstrate cell removal, it is necessary to present the absolute number of cells. If the cells were removed and were not replenished from Vcam1+ cells, the absolute number of cells should be reduced.

Related to Comment#4: Without the DHT+Senolysis experiment proposed by this reviewer or related experiments, there is no evidence demonstrating that GERI-MuSCs functionally rejuvenate. The current data only show that VCAM1 expression is restored.

Related to Comment#8: Individual results from 3-4 biological replicates should be shown in Figure 4. It will help readers to recognize the variation of each sample.

Reviewer #1 (Public review):

Summary:

The manuscript by Xu et al. reported base-resolution mapping of RNA pseudouridylation in five bacterial species, utilizing recently developed BID-seq. They detected pseudouridine (Ψ) in bacterial rRNA, tRNA, and mRNA, and found growth phase-dependent Ψ changes in tRNA and mRNA. They then focused on mRNA and conducted comparative analysis of Ψ profiles across different bacterial species. Finally, they developed a deep learning model to predict Ψ sites based on RNA sequence and structure.

Strengths:

This is the first comprehensive Ψ map across multiple bacterial species, and systematically reveals Ψ profiles in rRNA, tRNA, and mRNA under exponential and stationary growth conditions. It provides a valuable resource for future functional studies of Ψ in bacteria.

Weaknesses:

Ψ is highly abundant on non-coding RNA such as rRNA and rRNA, while its level on mRNA is very low. The manuscript focuses primarily on Ψ on mRNA, which is prone to false positives. Many conclusions in the manuscript are speculative, based solely on the sequencing data, but not supported by additional experiments.

Reviewer #1 (Public review):

Summary:

This important study functionally profiled ligands targeting the LXR nuclear receptors using biochemical assays in order to classify ligands according to pharmacological functions. Overall, the evidence is solid, but nuances in the reconstituted biochemical assays and cellular studies and terminology of ligand pharmacology limit the potential impact of the study. This work will be of interest to scientists interested in nuclear receptor pharmacology.

Strengths:

(1) The authors rigorously tested their ligand set in CRTs for several nuclear receptors that could display ligand-dependent cross-talk with LXR cellular signaling and found that all compounds display LXR selectivity when used at ~1 µM.

(2) The authors tested the ligand set for selectivity against two LXR isoforms (alpha and beta). Most compounds were found to be LXRbeta-specific.

(3) The authors performed extensive LXR CRTs, performed correlation analysis to cellular transcription and gene expression, and classification profiling using heatmap analysis-seeking to use relatively easy-to-collect biochemical assays with purified ligand-binding domain (LBD) protein to explain the complex activity of full-length LXR-mediated transcription.

Comments on revisions:

The authors have addressed the comments from the prior round of review with care. I find the revised manuscript significantly strengthened.

Reviewer #1 (Public review):

Summary:

This preprint from Shaowei Zhao and colleagues presents results that suggest tumorous germline stem cells (GSCs) in the Drosophila ovary mimic the ovarian stem cell niche and inhibit the differentiation of neighboring non-mutant GSC-like cells. The authors use FRT-mediated clonal analysis driven by a germline-specific gene (nos-Gal4, UASp-flp) to induce GSC-like cells mutant for bam or bam's co-factor bgcn. Bam-mutant or bgcn-mutant germ cells produce tumors in the stem cell compartment (the germarium) of the ovary (Fig. 1). These tumors contain non-mutant cells - termed SGC for single-germ cells. 75% of SGCs do not exhibit signs of differentiation (as assessed by bamP-GFP) (Fig. 2). The authors demonstrate that block in differentiation in SGC is a result of suppression of bam expression (Fig. 2). They present data suggesting that in 73% of SGCs BMP signaling is low (assessed by dad-lacZ) (Fig. 3) and proliferation is less in SGCs vs GSCs. They present genetic evidence that mutations in BMP pathway receptors and transcription factors suppress some of the non-autonomous effects exhibited by SGCs within bam-mutant tumors (Fig. 4). They show data that bam-mutant cells secrete Dpp, but this data is not compelling (see below) (Fig. 5). They provide genetic data that loss of BMP ligands (dpp and gbb) suppresses the appearance of SGCs in bam-mutant tumors (Fig. 6). Taken together, their data support a model in which bam-mutant GSC-like cells produce BMPs that act on non-mutant cells (i.e., SGCs) to prevent their differentiation, similar to what in seen in the ovarian stem cell niche. This preprint from Shaowei Zhao and colleagues presents results that suggest tumorous germline stem cells (GSCs) in the Drosophila ovary mimic the ovarian stem cell niche and inhibit the differentiation of neighboring non-mutant GSC-like cells. The authors use FRT-mediated clonal analysis driven by a germline-specific gene (nos-Gal4, UASp-flp) to induce GSC-like cells mutant for bam or bam's co-factor bgcn. Bam-mutant or bgcn-mutant germ cells produce tumors in the stem cell compartment (the germarium) of the ovary (Fig. 1). These tumors contain non-mutant cells - termed SGC for single-germ cells. 75% of SGCs do not exhibit signs of differentiation (as assessed by bamP-GFP) (Fig. 2). The authors demonstrate that block in differentiation in SGC is a result of suppression of bam expression (Fig. 2). They present data suggesting that in 73% of SGCs BMP signaling is low (assessed by dad-lacZ) (Fig. 3) and proliferation is less in SGCs vs GSCs. They present genetic evidence that mutations in BMP pathway receptors and transcription factors suppress some of the non-autonomous effects exhibited by SGCs within bam-mutant tumors (Fig. 4). They show data that bam-mutant cells secrete Dpp, but this data is not compelling (see below) (Fig. 5). They provide genetic data that loss of BMP ligands (dpp and gbb) suppresses the appearance of SGCs in bam-mutant tumors (Fig. 6). Taken together, their data support a model in which bam-mutant GSC-like cells produce BMPs that act on non-mutant cells (i.e., SGCs) to prevent their differentiation, similar to what in seen in the ovarian stem cell niche.

Strengths:

(1) Use of an excellent and established model for tumorous cells in a stem cell microenvironment

(2) Powerful genetics allow them to test various factors in the tumorous vs non-tumorous cells

(3) Appropriate use of quantification and statistics

Weaknesses:

(1) What is the frequency of SGCs in nos>flp; bam-mutant tumors? For example, are they seen in every germarium, or in some germaria, etc or in a few germaria.

This concern was addressed in the rebuttal. The line number is 106, not line 103.

(2) Does the breakdown in clonality vary when they induce hs-flp clones in adults as opposed to in larvae/pupae?

This concern was addressed in the rebuttal. However, these statements are no on lines 331-335 but instead starting on line 339. Please be accurate about the line numbers cited in the rebuttal. They need to match the line numbers in the revised manuscript.

(3) Approximately 20-25% of SGCs are bam+, dad-LacZ+. Firstly, how do the authors explain this? Secondly, of the 70-75% of SGCs that have no/low BMP signaling, the authors should perform additional characterization using markers that are expressed in GSCs (i.e., Sex lethal and nanos).

The authors did not perform additional staining for GSC-enriched protein like Sex lethal and nanos.

(4) All experiments except Fig. 1I (where a single germarium with no quantification) were performed with nos-Gal4, UASp-flp. Have the authors performed any of the phenotypic characterizations (i.e., figures other than figure 1) with hs-flp?

In the rebuttal, the authors stated that they used nos>flp for all figures except for Fig. 1I. It would be more convincing for them to prove in Fig. 1 than there is not phenoytpic difference between the two methods and then switch to the nos>FLP method for the rest of the paper.

(5) Does the number of SGCs change with the age of the female? The experiments were all performed in 14-day old adult females. What happens when they look at young female (like 2-day old). I assume that the nos>flp is working in larval and pupal stages and so the phenotype should be present in young females. Why did the authors choose this later age? For example, is the phenotype more robust in older females? or do you see more SGCs at later time points?

The authors did not supply any data to prove that the clones were larger in 14-day-old flies than in younger flies. Additionally, the age of "younger" flies was not specified. Therefore, the authors did not satisfactorily answer my concern.

(6) Can the authors distinguish one copy of GFP versus 2 copies of GFP in germ cells of the ovary? This is not possible in the Drosophila testis. I ask because this could impact on the clonal analyses diagrammed in Fig. 4A and 4G and in 6A and B. Additionally, in most of the figures, the GFP is saturated so it is not possible to discern one vs two copies of GFP.

In the rebuttal, the authors stated that they cannot differential one vs two copies of GFP. They used other clone labeling methods in Fig. 4 and 6. I think that the authors should make a statement in the manuscript that they cannot distinguish one vs two copies of GFP for the record.

(7) More evidence is needed to support the claim of elevated Dpp levels in bam or bgcn mutant tumors. The current results with dpp-lacZ enhancer trap in Fig 5A,B are not convincing. First, why is the dpp-lacZ so much brighter in the mosaic analysis (A) than in the no-clone analysis (B); it is expected that the level of dpp-lacZ in cap cells should be invariant between ovaries and yet LacZ is very faint in Fig. 5B. I think that if the settings in A matched those in B, the apparent expression of dpp-lacZ in the tumor would be much lower and likely not statistically significantly. Second, they should use RNA in situ hybridization with a sensitive technique like hybridization chain reactions (HCR) - an approach that has worked well in numerous Drosophila tissues including the ovary.

The HCR FISH in Fig.5 of the revised manuscript needs an explanation for how the mRNA puncta were quantified. Currently, there is no information in the methods. What is meant but relative dpp levels. I think that the authors should report in and unbiased manner "number" of dpp or gbb puncta in TFs. For the germaria, I think that they should report the number of puncta of dpp or gbb divide by the total area in square pixels counted. Additionally, the background fluorescence is noticeably much higher in bamBG/delta86 germaria, which would (falsely) increase the relative intensity of dpp and gbb in bam mutants. Although, I commend the authors for performing HCR FISH, these data are still not convincing to me.

(8) In Fig 6, the authors report results obtained with the bamBG allele. Do they obtain similar data with another bam allele (i.e., bamdelta86)?

The authors did not try any experiments with the bamdelta86 allele, despite this allele being molecularly defined, where the bamBG allele is not defined.

Reviewer #2 (Public review):

Summary:

This paper is an exciting follow-up to two recent publications in eLife: one from the same lab, reporting that slender forms can successfully infect tsetse flies (Schuster, S et al., 2021), and another independent study claiming the opposite (Ngoune, TMJ et al., 2025). Here, the authors address four criticisms raised against their original work: the influence of N-acetyl-glucosamine (NAG), the use of teneral and male flies, and whether slender forms bypass the stumpy stage before becoming procyclic forms.

Strengths:

We applaud the authors' efforts in undertaking these experiments and contributing to a better understanding of the T. brucei life cycle. The paper is well-written and the figures are clear.

Comments on revisions:

We thank the authors for the revised manuscript and for considering our comments.

We outline below the 3 points that, in our opinion, remain to be clarified.

(1) Effect of NAG on slender-form infections in tsetse flies<br /> The conclusion that "NAG has a negligible effect on slender infections in tsetse flies" based on Figure 1, cannot be fully supported in the absence of a positive control. A relevant positive control is well established in the literature, namely that NAG promotes Tsetse infection by stumpy forms. Without such a control, it is not possible to exclude technical issues (for example, an ineffective NAG treatment), which would yield results similar to those presented in Figure 1.

(2) Infection of non-teneral flies<br /> Because the experiments shown in Figure 1 (teneral flies) and Figure 2 (non-teneral flies) were not conducted in parallel or under identical conditions, it is important that the figure legends clearly state the parasite numbers used in each case. Specifically, infections of teneral flies were performed with 200 parasites/mL (approximately 4 parasites per bloodmeal), whereas non-teneral infections used 1 × 10⁶ parasites/mL (approximately 20,000 parasites per bloodmeal?). At present, this information is scattered across the Methods and Supplementary Tables 1 and 2, making it difficult for readers to immediately appreciate that the parasite load differs by roughly 5,000-fold between these conditions.

As previously shown by the authors (Schuster et al., 2021) and in the Rotureau laboratory (Tsagmo Ngoune et al.), and as generally expected, the initial parasite dose strongly influences infection outcomes in teneral flies. In this context, it would be informative to know whether the authors have attempted infections of non-teneral flies using lower parasite numbers (noting that Tsagmo Ngoune et al. used a maximum of 10,000 parasites) and what the infection rate was.<br /> Relatedly, the statement in line 370 appears to be an overgeneralization, as fly age was not directly tested under matched experimental conditions:

Line 370 - "Here, we unambiguously show that, in the absence of immunosuppressive treatment, slender forms can establish infections in tsetse flies, irrespective of the fly's age or sex."

(3) Transcriptomic analysis<br /> Supplementary Figure 8 lacks statistical analysis, which limits its interpretability. Two types of comparisons would be particularly helpful:<br /> (i) a comparison of PAD1/2 expression levels between slender and stumpy forms at 0 h; and<br /> (ii) for each gene, a comparison of the overall change in expression (from 0 to 72 h) between infections initiated with slender versus stumpy forms.<br /> In addition, the figure legend should clarify what "expression levels" refer to. TPM? Normalized counts?

Finally, for the benefit of the field, eLife could encourage publishing a collaborative study in which the Engstler and Rotureau laboratories exchange parasite lines and culture protocols (including media with and without methylcellulose) and perform tsetse fly infections in parallel in their respective laboratories. Such an approach could help resolve the remaining discrepancies and provide a valuable reference for the community.

Reviewer #1 (Public review):

Summary:

This study investigates the roles of the two tumor necrosis factor genes (tnfa and tnfb) in zebrafish during inflammatory responses. TNF is a central regulator of inflammation across vertebrates; however, while mammalian TNF signaling is well characterized, the functional divergence of duplicated TNF genes in teleosts remains less well understood. In this work, the authors generate novel zebrafish fluorescent reporter lines for tnfb and use them to perform comparative analyses of the spatial and temporal expression patterns of tnfa and tnfb during inflammation. They report that these paralogous genes are produced by distinct immune cell populations and exhibit different induction kinetics during inflammatory processes. Based on these observations, the authors propose that tnfa and tnfb may fulfill non-redundant roles in the zebrafish immune response.

Strengths:

The study addresses an important gap in understanding the functional divergence of TNF paralogs in teleosts. Given that gene duplication events are common in fish genomes, clarifying how duplicated cytokines partition their functions is valuable for both evolutionary immunology and zebrafish model research. The work makes effective use of the zebrafish model, which is particularly well suited for in vivo imaging of dynamic immune cell behaviors during inflammation. A key strength of the study is the integration of analyses of cell-type specificity, transcriptional regulation, and temporal expression dynamics. In particular, the live imaging experiments are compelling and provide clear visual evidence that tnfa and tnfb differ in both cellular sources and expression kinetics, which strengthens the claim that these paralogs may have diverged in their regulation and potentially their function. By distinguishing these aspects of the two cytokines, the study provides useful conceptual and methodological guidance for future investigations of inflammatory signaling in zebrafish.

Weaknesses:

(1) While the manuscript convincingly documents distinct expression patterns, the functional consequences of these differences remain unexplored. The conclusions regarding non-redundant roles would benefit from functional perturbation experiments. Relatedly, the authors propose that tnfa and tnfb may play different immunological roles, but the mechanistic basis underlying these differences is not addressed. For example, do the two cytokines engage different receptors or signaling pathways? Do they trigger distinct downstream transcriptional programs?

(2) Some imaging-based observations appear largely qualitative. Additional quantitative analyses, such as statistical comparisons of expression levels across time points or cell populations, would strengthen the robustness of the conclusions. For instance, in Figure 4, the expression levels of tnfa and tnfb reporter transgenes in immune cells should be quantitatively compared between control and amputated conditions.

(3) It would also be important to clarify whether the distinct maturation kinetics of the fluorescent reporters were taken into account when interpreting expression timing. Since GFP typically matures more rapidly than mCherry in vivo, the authors should comment on whether this difference could influence the apparent expression kinetics of tnfa versus tnfb.

Reviewer #1 (Public review):

Summary:

It has long been known that Drosophila embryonic ventral nerve cord neuroblasts incorporate both spatial and temporal transcription factor expression to generate 30 distinct neuroblasts and lineages per hemisegment. This manuscript aims to elucidate the mechanism by which this integration of spatial and temporal transcription factors occurs through "direct regulation" or "epigenetic regulation". Direct regulation is defined as both spatial and temporal factors binding to open chromatin and working together to dictate specific lineages. Epigenetic regulation is defined as a spatial factor priming the chromatin in a neuroblast-specific manner to allow for the integration of temporal factors to generate specific lineages. The authors conclude that there is a two-step model in which a spatial transcription factor code "primes" the chromatin in terms of accessibility and then recruits temporal factors to ensure lineage-specific enhancer activation.

Strengths:

The authors tested two models, "direct regulation" vs "epigenetic regulation" in a well-defined pool of neural stem cells during normal development.

Weaknesses:

The data in this study cannot clearly substantiate these two models.

Overall, there are a number of issues that are inconsistent and not supportive of the model proposed in this manuscript. Firstly, there is no evidence of pioneer factor activity in any of the NB lineages described - i.e., any changes in chromatin accessibility being shown over time. The authors must show chromatin conformation changes during the window of spatial transcription factor expression in order to convince the readers of this phenomenon. Secondly, the phenotypic data do not align with the sequencing data - the story would be more cohesive if the sequencing data and phenotypic data were in the same NB subtypes. On one hand, we are shown that Gsb misexpression induces loss of chromatin accessibility in NB 7-4, however in the widespread loss model, we are not shown a phenotype in these NB7-4 - which suggest that the chromatin accessibility at these sites (sites that have already been distinguished as SoIs for that NB subtype) does not play an important role in distinguishing NB 7-4 identity. However, the authors report loss of NB3-5 identity but have no evidence as to how the chromatin has changed (or if it has at all) in that subtype, leaving the readers to wonder how the loss of identity occurred.

Reviewer #1 (Public review):

Summary:

This study presents an interesting approach for finding electrophysiological models that match experimental patch-clamp data. The authors develop a new method for deriving optimized current clamp protocols by training a neural network on synthetic data. This optimized current clamp is then used on both computational training data and on experimental data to predict current gating and conductance parameters that correctly reconstruct the electrical phenotype.

Strengths:

(1) The fitting of gating variables through an optimized patch clamp protocol is interesting.

(2) The inclusion of experimental data is important, and the approach is shown to be effective in fitting them.

Weaknesses:

(1) Some clarity is necessary on the generation and selection of variable IPSC models. With such a large variation in so many parameters, I would expect some resulting parameters to generate non-realistic phenotypes, quiescent cells, etc. Are all 200,000 or 1,100,000 generated cells viable? Or are they selected somehow for realistic cell properties?

(2) The error shown in Figure 4 between different population sizes is not completely explained in the text - there seems to be a minimal difference between a population of 1,000 and 10,000, followed by a very good fit at 200,000. Is there a particular threshold that needs to be crossed where the error drops off? Related, how was the 200,000 number chosen?

(3) Related to the point above, the 1,100,000 population for fitting experimental data also needs a more complete explanation: how was this number chosen, and how does the error compare with the other population sizes shown in Figure 4?

(4) Why are the optimized current clamp protocols different between panels A and B in Figure 5? Are they somehow informed by experimental data?

(5) Figure 6D: Is the EAD risk in panel D specific to cell 1, 2, or the pooled variants of both?

(6) How sensitive is the fitting to minor parameter variation? Further, if one were to pick, let's say, the next-best fitting value, would that fall close to the best one? Is the solution found unique, or are there multiple sets with good fits?

Reviewer #1 (Public review):

Summary:

Here, Mattenburger et al use structural biology, biochemistry, and genetics to analyze the membrane-attacking end (spike/spike tip) of the contractile injection systems of two DNA phages (P2 and T4). Understanding how a phage tail mediates host recognition and injects DNA into the host is an important question. This manuscript is divided into two stories. First is a biochemical fractionation showing that the fused spike-spike tip protein of P2 (GpV) is translocated into the host periplasm. Second is a somewhat separate story about the spike tip protein of T4 (gp5.4), which is structurally characterized and shown to aid in infection of E. coli with truncated lipopolysaccharides (LPS). I find the suggestion that gp5.4 aids in penetration of the bacterial envelope the most compelling portion of the manuscript, but I find this conclusion to be insufficiently supported, and the presentation could be described as awkward. Further, while the experiments are generally elegant, I believe additional experiments and a discussion to fully connect the two stories of the manuscript would increase impact.

Strengths:

The manuscript is methodologically careful and adds nuance to our understanding of P2 and T4 spike function. The T4 gp5.4 structure is extensively characterized, with crystallography and cryo-EM support. Many experiments are elegant and clever, specifically the P2 periplasmic fractionation and the ex vivo gp5.4 phage reconstitution. If completely supported and explained, the finding that gp5.4 aids in penetration of the bacterial envelope rather than adsorption is compelling.

Weaknesses:

The novelty of the work is somewhat incremental, as phage injection is known to occur into the periplasm and gp5.4 is known to be part of the spike tip (Taylor et al, 2016). The finding that gp5.4 promotes penetration and DNA delivery in strains with truncated LPS is incompletely supported. The gp5.4am phage plaquing data are incompletely explained, and may generate a more modest effect for gp5.4 than is claimed. The P2 results, although well-performed, do not directly support the T4 experiments given the evolutionary divergence between these two phages. Lastly, the overall organization of the manuscript and writing is lacking as (1) the P2 results are presented within the T4 data, (2) many figures are presented out of order, and (3) there is no discussion to contextualize the results for the reader.

Reviewer #1 (Public review):

Disclaimer:

This reviewer is not an expert on MD simulations but has a basic understanding of the findings reported and is well-versed with mycobacterial lipids.

Summary:

In this manuscript titled "Dynamic Architecture of Mycobacterial Outer Membranes Revealed by All-Atom 1 Simulations", Brown et al describe outcomes of all-atom simulation of a model outer membrane of mycobacteria. This compelling study provided three key insights:

(1) The likely conformation of the unusually long chain alpha-branched, beta-methoxy fatty acids-mycolic acids in the mycomembrane to be the extended U or Z type rather than the compacted W-type.

(2) Outer leaflet lipids such as PDIM and PAT provide regional vertical heterogeneity and disorder in the mycomembrane that is otherwise prevented in a mycolic acid only bilayer.

(3) Removal of specific lipid classes from the symmetric membrane systems lead to significant changes in membrane thickness and resilience to high temperatures. (4) The asymmetric mycomembrane presents a phase transition from a disordered outer leaflet to an ordered inner leaflet.

Strengths:

The authors take a stepwise approach to increasing the membrane's complexity and highlight the limitations of each approach. A case in point is the use of supraphysiological temperatures of 333 K or higher in some simulations. Overall, this is a very important piece of work for the mycobacterial field and will likely help develop membrane-disrupting small molecules and provide important insights into lipid-lipid interactions in the mycomembrane.

Weaknesses:

The authors used alpha-mycolic acids only for their models. The ratios of alpha-, keto-, and methoxy-mycolic acids are well documented in the literature, and it may be worth including them in their model. Future studies can aim to address changes in the dynamic behavior of the MOM by altering this ratio, but including all three forms in the current model will be important and may alter the other major findings of the current study.

Reviewer #1 (Public review):

Summary:

Gosselin et al., develop a method to target protein activity using synthetic single-domain nanobodies (sybodies). They screen a library of sybodies using ribosome/ phage display generated against bacillus Smc-ScpAB complex. Specifically, they use an ATP hydrolysis deficient mutant of SMC so as to identify sybodies that will potentially disrupt Smc-ScpAB activity. They next screen their library in vivo, using growth defects in rich media as a read-out for Smc activity perturbation. They identify 14 sybodies that mirror smc deletion phenotype including defective growth in fast-growth conditions, as well as chromosome segregation defects. The authors use a clever approach by making chimeras between bacillus and S. pnuemoniae Smc to narrow-down to specific regions within the bacillus Smc coiled-coil that are likely targets of the sybodies. Using ATPase assays, they find that the sybodies either impede DNA-stimulated ATP hydrolysis or hyperactivate ATP hydrolysis (even in the absence of DNA). The authors propose that the sybodies may likely be locking Smc-ScpAB in the "closed" or "open" state via interaction with the specific coiled-coil region on Smc. I have a few comments that the authors should consider:

Major comments:

(1) Lack of direct in vitro binding measurements:<br /> The authors do not provide measurements of sybody affinities, binding/ unbinding kinetics, stoichiometries with respect to Smc-ScpAB. Additionally, do the sybodies preferentially interact with Smc in ATP/ DNA-bound state? And do the sybodies affect the interaction of ScpAB with SMC?<br /> It is understandable that such measurements for 14 sybodies is challenging, and not essential for this study. Nonetheless, it is informative to have biochemical characterization of sybody interaction with the Smc-ScpAB complex for at least 1-2 candidate sybodies described here.

(2) Many modes of sybody binding to Smc are plausible<br /> The authors provide an elaborate discussion of sybodies locking the Smc-ScpAB complex in open/ closed states. However, in the absence of structural support, the mechanistic inferences may need to be tempered. For example, is it also not possible for the sybodies to bind the inner interface of the coiled-coil, resulting in steric hinderance to coiled-coil interactions. It is also possible that sybody interaction disrupts ScpAB interaction (as data ruling this possibility out has not been provided). Thus, other potential mechanisms would be worth considering/ discussing. In this direction, did AlphaFold reveal any potential insights into putative binding locations?

(3) Sybody expression in vivo<br /> Have the authors estimated sybody expression in vivo? Are they all expressed to similar levels?

(4) Sybodies should phenocopy ATP hydrolysis mutant of Smc<br /> The sybodies were screened against an ATP hydrolysis deficient mutant of Smc, with the rationale that these sybodies would interfere this step of the Smc duty cycle. Does the expression of the sybodies in vivo phenocopy the ATP hydrolysis deficient mutant of Smc? Could the authors consider any phenotypic read-outs that can indicate whether the sybody action results in an smc-null effect or specifically an ATP hydrolysis deficient effect?

Significance:

Overall, this is an impressive study that uses an elegant strategy to find inhibitors of protein activity in vivo. The manuscript is clearly written and the experiments are logical and well-designed. The findings from the study will be significant to the broad field of genome biology, synthetic biology and also SMC biology. Specifically, the coiled coil domain of SMC proteins have been proposed to be of high functional value. The authors have elegantly identified key coiled-coil regions that may be important for function, and parallelly exhibited potential of the use of synthetic sybody/designed binders for inhibition of protein activity.

Reviewer #1 (Public review):

Summary:

Tkacik et al describe their efforts to reconstitute and biochemically characterize ARAF, BRAF, and CRAF proteins and measure their ability to be paradoxically activated by current clinical and preclinical RAF inhibitors. Paradoxical activation of MAPK signaling is a major clinical problem plaguing current RAF inhibitors, and the mechanisms are complex and relatively poorly understood. The authors utilize their preparations of purified ARAF, BRAF, and CRAF kinase domains to measure paradoxical activation by type I and type II inhibitors, utilizing MEK protein as the substrate, and show that CRAF is activated in a similar fashion to BRAF, whereas ARAF appears resistant to activation. These data are analyzed using a simple cooperativity model with the goal of testing whether paradoxical activation involves negative cooperativity between RAF dimer binding sites, as has been previously reported. The authors conclude that it does not. They also test activation of B- and CRAF isoforms prepared in their full-length autoinhibited states and show that under the conditions of their assays, activation by inhibitors is not observed. In a particularly noteworthy part of the paper, the authors show that mutation of the N-terminal acidic (NtA) motif of ARAF and CRAF to match that of BRAF enhances paradoxical activation of CRAF and dramatically restores paradoxical activation of ARAF, which is not activated at all in its WT form, indicating a clear role for the NtA motif in the paradoxical activation mechanism. Additional experiments use mass photometry to measure BRAF dimer induction by inhibitors. The mass photometry measurements are a relatively novel way of achieving this, and the results are qualitatively consistent with previous studies that tracked BRAF dimerization in response to inhibitors using other methods. Overall, the paper establishes that WT CRAF is paradoxically activated by the same inhibitors that activate BRAF, and that ARAF contains the latent potential for activation that appears to be controlled by its NtA motif. The biochemical activation data for BRAF are qualitatively consistent with previous work.

Strengths:

While previous studies have put forward detailed molecular mechanisms for paradoxical activation of BRAF, comparatively little is known about the degree to which ARAF and CRAF are prone to this problem, and relatively little biochemical data of any sort are available for ARAF. Seen in this light, the current work should be considered of substantial potential significance for the RAF signaling field and for efforts to understand paradoxical activation and design new inhibitors that avoid it.

Weaknesses:

There are, unfortunately, some significant flaws in the data analysis and fitting of the RAF activation data that render the primary conclusion of the paper about the detailed activation mechanism, namely that it does not involve negative cooperativity between active sites, unjustified. This claim is made repeatedly throughout the manuscript, including in the title. Unfortunately, their data analysis approach is overly simplistic and does not probe this question thoroughly. This is the primary weakness of the study and should be addressed. A full biochemical modeling approach that accurately captures what is happening in the experiment needs to be applied in order for detailed inferences to be drawn about the mechanism beyond just the observation of activation.

The authors' analysis of their RAF:MEK "monomer" paradoxical activation data (Figures 1, 3, and Tables 1, 2) suffers from two fundamental flaws that render the resulting AC50/IC50 and cooperativity (Hill) parameters essentially uninterpretable. Without explaining or justifying their choice, the authors use a two-phase cooperative binding model from GraphPad Prism to fit their activation/inhibition data. This model is intended to describe cooperative ligand binding to multiple coupled sites within a preformed receptor assembly, and does not provide an adequate description of what is happening in this complicated experiment. Specifically, it has two fundamental flaws when applied to the analysis in question:

(a) It does not account for ligand depletion effects that occur with high-affinity drugs, and that profoundly affect the shapes of the dose-response curves, which are what are being fit

The chosen model is one of a class of ligand-binding models that are derived by assuming that the free ligand concentration is effectively equal to the total ligand concentration. Under these conditions, binding curves have a characteristic steepness, and the presence of cooperativity can be inferred from changes in this steepness as described by a Hill coefficient. However, many RAF inhibitors, including most of the type II inhibitors in this study, bind to the dimerized forms of at least one of the RAF isoforms with ultra-high affinity in the picomolar range (particularly apparent in Figure 1 with LY inhibiting BRAF). Under these conditions, the model assumption is not valid. Instead, binding occurs in the high-affinity regime in which the drug titrates the receptor and effectively all the added drug molecules bind, so there is hardly any free ligand (see e.g. Jarmoskaite and Herschlag eLife 2020 for a full description of this "titration" regime). The shapes of the curves under these conditions reflect the total amount of RAF protein (and to some extent drug affinity), rather than the presence of cooperativity. Fitting dose response curves with the chosen model under these conditions will result in conflating binding affinity and protein concentration with cooperativity.

(b) It does not model the RAF monomer-dimer equilibrium, which is dramatically modulated by drug binding, rendering the results RAF-concentration dependent in a manner not accounted for by the analysis.

The chosen analysis model also fails to consider the monomer-dimer equilibrium of RAF. This has two ramifications. Since drug binding is coupled to dimerization to a very strong degree, the observed apparent affinities of drug binding (reflected in AC50 and IC50 values) are functions of the concentration of RAF molecules used in the experiment. Since dimerization affinities are likely different for ARAF, BRAF, and CRAF, the measured AC50 values also cannot be compared between isoforms. This concentration dependence is not addressed by the authors. A related issue is that the model assumes drug binding occurs to two coupled sites on preformed dimers, not to a mixture of monomers and dimers. "Cooperativity" parameters determined in this manner will reflect the shifting monomer-dimer equilibrium rather than the cooperativity within dimers. Additionally, the inhibition side of the activation/inhibition curves is driven by binding of the drug to the single remaining site on the dimer, not to two coupled sites, and so one cannot determine cooperativity values for this process in this manner.

As a result of both of these issues, the parameters reported in the tables do not correctly reflect cooperativity and cannot be used to infer the presence or absence of negative cooperativity between RAF dimer subunits. To address these major issues, the authors would need to apply a data analysis/fitting procedure that correctly models the biochemical interactions occurring in the sample, including both the monomer-dimer equilibrium and how this equilibrium is coupled to drug binding, such as that developed in e.g., Kholodenko Cell Reports 2015. Alternatively, the authors should remove the statements claiming a lack of negative cooperativity from the manuscript and alter the title to reflect this.

Some other points to consider

(1) The observation that ARAF is not activated by type II inhibitors is interesting. A detailed comparison of the activation magnitudes between inhibitors and between A-, B-, and CRAF is hampered by the arbitrary baseline signal in the assay, which arises from a non-zero FRET ratio in the absence of any RAF activity. The authors might consider background correcting their data using a calibration curve constructed using MEK samples of known degrees of phosphorylation, so that they can calculate turnover numbers and fold activation values rather than an increase over baseline. This will likely reveal that the activation effects are more substantial than they appear against the high background signal.

(2) The authors note that full-length autoinhibited 14-3-3-bound RAF monomers are not activated by type I and II inhibitors. However, since this process involves the formation of a RAF dimer from two monomers, the process would also be expected to be concentration dependent, and the authors have only investigated this at a single protein concentration. Since disassembly of the autoinhibited state must also occur before dimerization, it might be expected to be kinetically disfavored as well. Have the authors tested this?

(3) ATP concentration modulates activation. While this is an interesting observation, some of this analysis suffers from the same issue discussed above, of not considering high-affinity binding effects. For instance, LY is not affected by ATP concentration in their data (Figure 4D), but this is easily explained as being due to its very tight binding affinity, resulting in titration of the receptor and the shape of the inhibition curve reflecting the amount of RAF kinase in the experiment and not the effective Kd or IC50 value.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed the comments raised in the previous round of review, shown below.]

In this study, the noncanonical amino acid acridon-2-ylalanine (Acd) was inserted at various positions within the human Hv1 protein using a genetic code expansion approach. The purified mutants with incorporated fluorophore were shown to be functional using a proton flux assay in proteoliposomes. FRET between native tryptophan and tyrosine residues and Acd were quantified using spectral FRET analysis. Predicted FRET efficiencies calculated from an AlphaFold model of the Hv1 dimer were compared to the corresponding experimental values. Spectral FRET analysis was also used to test whether structural rearrangements caused by Zn2+, a well-known Hv1 inhibitor, could be detected. The experimental data provide a good validation of the approach, but further expansion of the analysis will be necessary to differentiate between intra- and intersubunit structural features.

Interestingly, the observed rearrangements induced by Zn2+ were not limited to the protein region proximal to the extracellular binding site but extended to the intracellular side of the channel. This finding agrees with previous studies showing that some extracellular Hv1 inhibitors, such as Zn2+ or AGAP/W38F, can cause long-range structural changes propagating to the intracellular vestibule of the channel (De La Rosa et al. J. Gen. Physiol. 2018, and Tang et al. Brit J. Pharm 2020). The authors should consider adding these references.

Since one of the main goals of this work was to validate Acd incorporation and the spectral FRET analysis approach to detect conformational changes in hHv1 in preparation for future studies, the authors should consider removing one subunit from their dimer model, recalculating FRET efficiencies for the monomer, and comparing the predicted values to the experimental FRET data. This comparison could support the idea that the reported FRET measurements can inform not only on intrasubunit structural features but also on subunit organization.

Reviewer #1 (Public review):

Summary:

This manuscript addresses the temporal patterns in how cholinergic signaling to the gut affects the lifespan of the worm C. elegans, which should make the manuscript of wide interest to those who study aging, as well as those who study the brain-gut axis in health and disease. The authors show that early acetylcholine (ACh) signaling to the intestine via the ACR-6 receptor shortens worm lifespan, which depends on the DAF-16/FOXO transcription factor. However, later ACh signaling to the intestine via the GAR-3 receptor extends lifespan, which in turn depends on the heat shock factor HSF-1. The authors also show a potential mechanism through which these two temporal patterns of ACh signaling might be coordinated to influence longevity in the worm, and possibly in other animals.

Strengths:

The authors observed that the functional ablation of acr-2-expressing cholinergic neurons in C. elegans (Pacr-2::TeTx) produced a lifespan curve that intersects the lifespan curve of a wild-type population. The first quartile of Pacr-2::TeTx worms shows a longer lifespan than the first quartile of wild-type worms, whereas the last quartile of Pacr-2::TeTx worms exhibits a shorter lifespan than wild type. These observations raised the hypothesis that cholinergic neurons have two opposing effects on longevity: an early longevity-inhibiting effect and a later longevity-promoting effect. Much of the data support the authors' conclusions.

The authors have also addressed the points raised in the previous review.

Reviewer #1 (Public review):

This manuscript presents a comprehensive and technically impressive study investigating the interplay between active (H3K4me1) and silencing (H3K27me3) chromatin states and gene expression during early zebrafish development. By applying an optimized single-cell multi-omics method (whole-organism T-ChIC) to profile histone modifications and transcriptomes simultaneously in thousands of cells from 4 to 24 hours post-fertilization, the work addresses a significant gap in understanding how epigenetic states are established and propagated during vertebrate embryogenesis.

There are several obvious strengths:

(1) Innovative Methodology: The adaptation and application of the T-ChIC protocol to a whole-organism, multiplexed time-course design is a major technical achievement. The generation of a high-quality, paired chromatin (H3K27me3 and H3K4me1) and full-length transcriptome dataset from the same single cells is a powerful resource for the field.

(2) Novel Biological Insights:

(2.1) It provides single-cell evidence for the promoter-anchored cis-spreading of H3K27me3 as a mechanism for gene silencing during differentiation, a process that appears largely lineage-agnostic.

(2.2) It demonstrates that global chromatin states (both active and repressive) are initially decoupled from transcriptional output in pluripotent cells and become correlated as cells mature, suggesting this coupling is a hallmark of identity formation.

(2.3) It develops a predictive model using TF expression and the H3K4me1 state at TF binding sites to infer lineage-specific activator/repressor functions and epigenetic regulation of TFs themselves, revealing novel roles for factors like zbtb16a and zeb1a.

There are also several weaknesses for further clarification:

(1) The study focuses on H3K27me3 and H3K4me1. Why these two specific histone modifications were chosen as the primary focus for this study on early fate commitment?

(2) There are some similar single-cell techniques available (histone modifications and transcription from the same single cell), what is the performance of T-ChIC when comparing to other methods？

Comments on revised version:

Other histone modifications and TFs, or even DNA methylation could be tested to see the robustness of T-ChIC.

Reviewer #1 (Public review):

Summary:

This study builds upon a major theoretical account of value-based choice, the 'attentional drift diffusion model' (aDDM), and examines whether and how this might be implemented in the human brain using functional magnetic resonance imaging (fMRI). The aDDM states that the process of internal evidence accumulation across time should be weighted by the decision maker's gaze, with more weight being assigned to the currently fixated item. The present study aims to test whether there are (a) regions of the brain where signals related to the currently presented value are affected by the participant's gaze; (b) regions of the brain where previously accumulated information is weighted by gaze.

To examine this, the authors developed a novel paradigm that allowed them to dissociate currently and previously presented evidence, at a timescale amenable to measuring neural responses with fMRI. They asked participants to choose between bundles or 'lotteries' of food times, which they revealed sequentially and slowly to the participant across time. This allowed modelling of the haemodynamic response to each new observation in the lottery, separately for previously accumulated and currently presented evidence.

Using this approach, they find that regions of the brain supporting valuation (vmPFC and ventral striatum) have responses reflecting gaze-weighted valuation of the currently presented item, where as regions previously associated with evidence accumulation (preSMA and IPS) have responses reflected gaze-weighted modulation of previously accumulated evidence.

A major strength of the current paper is the design of the task, nicely allowing the researchers to examine evidence accumulation across time despite using a technique with poor temporal resolution. The dissociation between currently presented and previously accumulated evidence in different brain regions in GLM1 (before gaze-weighting), as presented in Figure 5, is already compelling. The result that regions such as preSMA response positively to |AV| (absolute difference in accumulated value) is particularly interesting, as it would seem that the 'decision conflict' account of this region's activity might predict the exact opposite result. Additionally, the behaviour has been well modelled at the end of the paper when examining temporal weighting functions across the multiple samples.

In response to reviewer comments, the authors have explicitly tested for the effects of gaze-weighting over and above any main effect of value, and convincingly shown that these effects are both present in the main regions of interest - namely |SV| and gaze-weighted |SV| in the vmPFC, alongside |AV| and |AV_gaze| in the pre-SMA. This provides clear evidence in support of the notion of gaze-weighting of value signals in these regions.

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

Reviewer #1 (Public review):

The new experiments on the HOX and XIC look strong. A limited (conservative) number of proteins are determined to be enriched at the respective loci. And the number of cells used is a good advancement for these kinds of methods.

Unfortunately, the warnings about mitochondrial to nuclear comparisons and validations do not appear to be taken seriously. It's not that "...there could be non-specific nuclear comparison." There are definitely non-specific enriched proteins. Minimizing false positives is the responsibility of those developing the method and generating the hit lists. I think you saying our probes go to where they are supposed to and label the proteins in that compartment is fine. But that is as far as that should go. Any non-validated protein hits in those comparisons need to be removed. It will contaminate the literature by having all the proteins in 1E, S4D-F, and S5 reported (even though it appears there is no tables reporting the new proteins claimed to be associated with that locus. Why is that?).

I think the line "...we have not made any claims about new proteins at specific loci." is the heart of the issue. What is the point of this method then? Isn't it to identify unknown proteins at a locus of interest? Without that, it's just generating a long list of proteins, where an unknown number of which are likely erroneous, and highlighting the ones you already knew to be there. Along those lines, it is not validation to show proteins that we already knew were at a locus are at the locus. Validation is developing a method to help find new things, then testing those new things to confirm the new method's fidelity.

The comparison of OMAP identified proteins to the several other methods that look at similar regions is not there. A Figure 1F is referred to in the rebuttal but is not in the manuscript. If you mean the Bioplex comparison, that is not the goal. The goal of this analysis to see how much overlap, if any, is being identified across methods. OMAP has so many proteins claimed to be associated with telomeres that are not tested or validated, it would be nice if other methods see similar ones.

Minor points: You have now done label free proteomics. A) Methodological details are needed. It is not clear if you mean MS1 or DIA based quant. B) Do you need all the language about how multiplexed proteomics is enabling this methods?

Labeling the all the enriched proteins in the volcano plots would be nice. I don't want to see just the "relevant" ones that support your claims. I want to see all the "new" ones your discovery method is claiming to discover.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have comprehensively addressed the comments raised in the previous round of review.]

Summary:

These authors have developed a method to induce MI or MII arrest. While this was previously possible in MI, the advantage of the method presented here is it works for MII, and chemically inducible because it is based on a system that is sensitive to the addition of ABA. Depending on when the ABA is added, they achieve a MI or MII delay. The ABA promotes dimerizing fragments of Mps1 and Spc105 that can't bind their chromosomal sites. The evidence that the MI arrest is weaker than the MII arrest is convincing and consistent with published data and indicating the SAC in MI is less robust than MII or mitosis. The authors use this system to find evidence that the weak MI arrest is associated with PP1 binding to Spc105. This is a nice use of the system.

The remainder of the paper uses the SynSAC system to isolate populations enriched for MI or MII stages and conduct proteomics. This shows a powerful use of the system, but more work is needed to validate these results, particularly in normal cells.

Overall, the most significant aspect of this paper is the technical achievement, which is validated by the other experiments. They have developed a system and generated some proteomics data that maybe useful to others when analyzing kinetochore composition at each division.

Reviewer #1 (Public review):

[Editors' note: This version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed comments raised in the previous round of review, shown below, through minor changes to the text without additional experiments.]

Summary:

Taylar Hammond and colleagues identified new regulators of the G1/S transition of the cell cycle. They did so by screening publicly available data from the Cancer Dependency Map and identified FAM53C as a positive regulator of the G1/S transition. Using biochemical assays they then show that FAM53 interacts with the DYRK1A kinase to inhibit its function. They show in RPE1 cells that loss of FAMC53 leads to a DYRK1A + P53-dependent cell cycle arrest. Combined inactivation of FAM53C and DYRK1A in a TP53-null background caused S-phase entry with subsequent apoptosis. Finally the authors assess the effect of FAM53C deletion in a cortical organoid model, and in Fam53c knockout mice. Whereas proliferation of the organoids is indeed inhibited, mice show virtually no phenotype.

Reviewer #2 (Public review):

The authors sought to identify new regulators of the G1/S transition by mining the Cancer Dependency Map (DepMap) co-dependency dataset. This analysis successfully identified FAM53C, a poorly characterized protein, as a candidate. The strength of the paper lies in this initial discovery and the subsequent biochemical work convincingly showing that FAM53C can directly interact with the kinase DYRK1A, a known cell cycle regulator.

The authors then present evidence, primarily from acute siRNA knockdown in RPE-1 cells, that loss of FAM53C induces a strong G1 cell cycle arrest. Their follow-up investigation proposes a model where FAM53C normally inhibits DYRK1A, thereby protecting Cyclin D from degradation and preventing p53 activation, to allow for G1/S progression. The authors have commendably addressed some concerns from the initial review: they have now demonstrated the G1 arrest using two independent siRNAs (an improvement over the initial pool), shown the effect in several additional cancer cell lines (U2OS, A549, HCT-116), and developed a more nuanced model that incorporates p53 activation, which helps to explain some of the complex data.

Reviewer #1 (Public review):

Summary:

The authors test the hypotheses, using an effort-exertion and an effort-based decision-making task, while recording brain dynamics with EEG, that the brain processes reward outcomes for effort differentially when they earned for themselves versus others.

Strengths:

The strengths of this experiment include what appears to be a novel finding of opposite signed effects of effort on the processing of reward outcomes when the recipient is self versus others. Also, the experiment is well-designed, the study seems sufficiently powered, and the data and code are publicly available.

Weaknesses:

There is some concern about the fact that participants report feeling less subjective effort, but also more disliking of tasks when they were earning rewards for others versus self. The concern is that participants worked with less vigor during self-versus-others trials and this may partly account for a key two-way Recipient x Effort interaction on the size of the Reward Positivity EEG component. Of note, participants took longer to complete tasks when working for others. While it is true that, in all cases, participants met the requisite task demands (they pressed the required number of buttons) they did so more sluggishly when earning rewards for others. The Authors argue that this reflects less motivation when working for others, which is a plausible explanation. The Authors also try to rule out this diminished vigor as a confounding explanation by showing that the two way interaction remains even when including reaction times (and also self-reported task liking) as a covariate. Nevertheless, it is possible that covariates do not fully account for the effects of differential motivation levels which would otherwise explain the two-way interaction. As such, I think a caveat is warranted regarding this particular result.

Reviewer #1 (Public review):

Summary:

Del Rosario et al characterized the extent and cell types of sibling chimerism in marmosets. To do so, they took advantage of the thousands of SNPs that are transcribed in single-nucleus RNA-seq (snRNA-seq) data to identify the sibling genotype of origin for all sequenced cells across 4 tissues (blood, liver, kidney, and brain) from many marmosets. They found that chimerism is prevalent and widespread across tissues in marmosets, which has previously been shown. However, their snRNA-seq approach allowed them to identify precisely which cells were of sibling origin, and which were not. In doing so they definitively show that sibling chimerism across tissues is limited to cells of myeloid and lymphoid lineages. The authors then focus on a large sample of microglia sequenced across many brain regions to quantify: (1) variation in chimerism across brain regions in the same individual, and (2) the relative importance of genetic vs. environmental context on microglia function/identity. (1) Much like across different tissues in the same individual, they found that the proportion of chimeric microglia varies across brain regions collected from the same individuals (as well as differing from the proportion of sibling cells found in blood of the same animals), suggesting that cells from different genetic backgrounds may differ in their recruitment and/or proliferation across regions and local tissue contexts, or that this may be linked to stochastic bottleneck effects during brain development. (2) Their (admittedly smaller sample size) analyses of host-sibling gene expression showed that the local environment dominates genotype. All told, this thoughtful and thorough manuscript accomplishes two important goals. First, it all but closes a previously open question on the extent and cell origins of sibling chimerism. Second, it sets the stage for using this unique model system to examine, in a natural context, how genetic variation in microglia may impact brain development, function, and disease.

The conclusions of this paper are well supported by the data, and the authors exert appropriate care when extrapolating their results that come from smaller samples. However, there are a few concerns that should be addressed.

The "modest correlation" mentioned in lines 170-172 does not take into account the uncertainty in estimates of each chimeric cell proportion (although the plot shows those estimates nicely). This is particularly important for the macrophages, which are far less abundant. Perhaps a more appropriate way to model this would be in a binomial framework (with a random effect for individual of origin). Here, you could model sibling identity of each macrophage as a function of the proportion of sibling-origin microglia and then directly estimate the percent variance explained.

A similar (albeit more complicated because of the number of regions being compared) approach could be applied to more rigorously quantify the variation in chimerism across brain regions (L198-215; Fig 4). This would also help to answer the question of whether specific brain regions are more "amenable" to microglia chimerism than others.

While the sample size is small, it would be exciting to see if any microglia eQTL are driven by sibling chimerism across the marmosets.

L290-292: The authors should propose ways in which they could test the two different explanations proposed in this paragraph. For instance, a simulation-based modeling approach could potentially differential more stochastic bottleneck effects from recruitment-like effects.

While intriguing, the gene expression comparison (Fig 5) is extremely underpowered. It would be helpful to clarify this and note the statistical thresholds used for identifying DEGs (the black points in the figure).

Comments on revisions:

The authors have thoroughly addressed all my suggestions.

Reviewer #1 (Public review):

Summary:

This study aims to investigate the development of infants' responses to music by examining neural activity via EEG and spontaneous body kinematics using video-based analysis. The authors also explore the role of musical pitch in eliciting neural and motor responses, comparing infants at 3, 6, and 12 months of age.

Strengths:

A key strength of the study lies in its analysis of body kinematics and modeling of stimulus-motor coupling, demonstrating how the amplitude envelope of music predicts infant movement, and how higher musical pitch may enhance auditory-motor synchronization.

EEG data provide evidence for enhanced neural responses to music compared to shuffled auditory sequences. These findings ecourage further investigation of the proposed developmental trajectory of neural responses to music and their link to musical behavior in infants.

Comments on revisions:

I thank the authors for the considerable effort devoted to revising the manuscript and addressing the raised questions and comments. I particularly appreciate the additional analyses and the extended arguments included in the discussion. I believe that this paper represents a valuable contribution to the literature on music development.

One remaining comment concerns the evoked response observed in the shuffled condition, which I still find intriguing. Considering that the auditory events in the shuffled condition display a clear rise time, particularly for those events that were selected based on being preceded and followed by longer periods of silence, one would expect to observe an evoked response emerging from baseline. However, this pattern is not evident in the presented curves. The authors may further examine and discuss the shape and characteristics of these response patterns.

Reviewer #1 (Public review):

Summary:

This manuscript addresses an important methodological issue-the fragility of meta-analytic findings-by extending fragility concepts beyond trial-level analysis. The proposed EOIMETA framework provides a generalizable and analytically tractable approach that complements existing methods such as the traditional Fragility Index and Atal et al.'s algorithm. The findings are significant in showing that even large meta-analyses can be highly fragile, with results overturned by very small numbers of event recodings or additions. The evidence is clearly presented, supported by applications to vitamin D supplementation trials, and contributes meaningfully to ongoing debates about the robustness of meta-analytic evidence. Overall, the strength of evidence is moderate to strong.

Strengths:

(1) The manuscript tackles a highly relevant methodological question on the robustness of meta-analytic evidence.<br /> (2) EOIMETA represents an innovative extension of fragility concepts from single trials to meta-analyses.<br /> (3) The applications are clearly presented and highlight the potential importance of fragility considerations for evidence synthesis.

Reviewer #1 (Public review):

Summary:

In this manuscript, Guin and colleagues establish a microscopy-based CRISPR screen to find new factors involved in global chromatin organization. As a proxy of global chromatin organization they use centromere clustering in two different cell lines. They find 52 genes whose CRISPR depletion leads to centrome clustering defects in both cell lines. Using cell cycle synchronisation, they demonstrate that centromeres-redistribution upon depletion of these hits necessitates cell cycle progression through mitosis.

Strengths:

This manuscript explores the mechanisms of global chromatin organization, which is a scale of chromatin organization which remains poorly understood. The imaging based CRISPR screeen is very elegant and use of appropriate positive and negative controls reinforces the solidity of the findings.

Weaknesses:

The manuscript shows interesting observations but left a major question unanswered: what is the functional relevance of centromeres clustering?

Reviewer #1 (Public review):

In the revised manuscript, the authors refine their conclusions, narrow their interpretation, and add limited new analyses but have not added additional new data or made fundamental changes in the analyses of their data.

The central findings are that the SuM contains neurons that are activated by stressors (foot shock and social defeat). Chemogenetic activation of SuM and the neurons genetically tagged as active during foot shocks, which the authors define as Stress Activated Neurons, increases classic anxiety-like behaviors. The subiculum projects to the SuM, and terminals in the SuM from the ventral versus dorsal subiculum are differentially active during elevated plus-maze transitions. Chronic inhibition of vSub neurons that project to SuM mitigates CSDS-induced anxiety-like behaviors.

Due to limitations in the data and experimental design the findings are felt to remain incomplete. A central limitation is the discordance between the temporal resolution of the behavioral assays and the neural interventions used. This weakens support for the conclusions drawn about the causal roles the SuM and specific vSub projections to SuM (vSub→SuM) may play in anxiety and anxiety-like behaviors. The authors acknowledge this limitation but do not address it experimentally in the revised manuscript. Furthermore, the connection between chronic inhibition of vSub→SuM neurons for 10 days and the alleviation of CSDS-induced anxiety is incomplete. Separately, the use of foot shock and social defeat stressors in connection with SuM neurons, with limited exploration of the potential (or lack thereof) relation between the two groups, further limits the ability to draw conclusions from the data.

Although a number of interesting points are raised through the experiments the weakness noted will reduce the impact of the work in the field.

Reviewer #1 (Public review):

Summary:

GID/CTLH-type RING ligases are huge multi-protein complexes that play an important role in protein ubiquitylation. The subunits of its core complex are distinct and form a defined structural arrangement, but there can be variations in subunit composition, such as exchange of RanBP9 and RanBP10. In this study, van gen Hassend and Schindelin provide new crystal structures of (parts of) key subunits and use those structures to elucidate the molecular details of the pairwise binding between those subunits. They identify key residues that mediate binding partner specificity. Using in vitro binding assays with purified protein, they show that altering those residues can switch specificity to a different binding partner.

Strengths:

This is a technically demanding study that sheds light on an interesting structural biology problem in residue-level detail. The combination of crystallization, structural modeling and binding assays with purified mutant proteins is elegant and, in my eyes, convincing.

Weaknesses:

This study has no major weaknesses.

It will be very interesting to see follow-up studies that use the mutants generated here to dive deeper into the biology of RING ligases, or design new mutants of multi-subunit complexes with an analogous methodology.

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

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

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

Weaknesses:

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

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

Comments on revisions:

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

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

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

Weaknesses:

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

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

Reviewer #1 (Public Review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed the comments raised in the previous round of review.]

Summary:

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

Strengths:

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

Reviewer #1 (Public review):

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

Strengths:

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

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

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

Weaknesses:

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

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

Comments on revisions:

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

Comments on revisions:

I have no further comments.

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

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

Reviewer #1 (Public review):

Summary:

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

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

Strengths:

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

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

Minor weaknesses:

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

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

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

Comments on revisions:

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

Reviewer #1 (Public review):

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

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

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

Comments on revisions:

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

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

Weaknesses:

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

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

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

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

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

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

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

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

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

Reviewer #1 (Public review):

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

Strengths:

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

Weaknesses:

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

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

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

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

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

Reviewer #2 (Public review):

Summary:

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

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

Strengths:

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

Weaknesses:

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

Comments:

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

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

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

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

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

Reviewer #1 (Public review):

Summary:

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

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

Strengths:

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

Weaknesses:

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

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

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

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

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

Joint Public Review:

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

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

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

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

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

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

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

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

Reviewer #2 (Public review):

Summary:

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

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

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

Comments on revisions:

The authors did a great job addressing my comments.

Reviewer #1 (Public review):

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

Comments on revisions:

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

Comments on revisions:

The reviewer has no further recommendations for the authors.

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

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

Reviewer #1 (Public review):

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

Strengths:

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

Weaknesses:

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

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

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

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

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

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

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

Reviewer #1 (Public review):

Summary

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

Strengths.

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

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

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

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

Weaknesses

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

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

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

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

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

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

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

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

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

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

Weaknesses:

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

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

Impact:

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

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

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

Weaknesses:

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

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

Comments on revisions:

The authors did a good job in addressing the reviews.

Reviewer #1 (Public review):

Summary:

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

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

Strengths:

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

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

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

Weaknesses:

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

Reviewer #1 (Public review):

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

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

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

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

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

Reviewer #1 (Public review):

Summary:

This study reports a novel and potentially impactful role for NINJ2 in maintaining lysosomal integrity and regulating cellular susceptibility to ferroptosis. The authors demonstrate that NINJ2 localizes to lysosomes and interacts with LAMP1, a key lysosomal membrane glycoprotein involved in sensing lysosomal stress. Loss of NINJ2 increases lysosomal membrane permeabilization (LMP), resulting in selective leakage of lysosomal contents, including labile iron, into the cytosol. The authors further show that NINJ2 deficiency reduces the expression of ferritin storage proteins, thereby sensitizing cells to ferroptosis induced by RSL3 and erastin. Collectively, the work proposes a mechanistic link between NINJ2-mediated control of LMP, iron homeostasis, and ferroptotic vulnerability, with potential relevance to cancer biology.

Strengths:

This study identifies a novel role for NINJ2 in regulating lysosomal integrity and ferroptosis and establishes a mechanistic link between lysosomal membrane permeabilization, iron homeostasis, and ferroptotic sensitivity, with potential translational relevance in cancer.

Weaknesses:

The results overall support the authors' conclusions and provide a plausible mechanistic framework; however, additional quantification of Western blot data and further discussion of mechanistic questions would strengthen the study.

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

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

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

Weaknesses:

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

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

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

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

Reviewer #1 (Public review):

Summary:

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

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

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

Strengths:

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

Weaknesses:

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

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

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

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

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

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Comments on revisions:

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

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

Reviewer #1 (Public review):

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

Reviewer #2 (Public review):

Summary:

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

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

Strengths:

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

Weaknesses:

No major new finding is reported.

Comments on revisions:

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

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

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

Reviewer #3 (Public review):

Summary:

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

Strengths:

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

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

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

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

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

Comments on revisions:

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