Reviewer #1 (Public review):

This paper presents a computational model of the evolution of two different kinds of helping ("work," presumably denoting provisioning, and defense tasks) in a model inspired by cooperatively breeding vertebrates. The helpers in this model are a mix of previous offspring of the breeder and floaters that might have joined the group, and can either transition between the tasks as they age or not. The two types of help have differential costs: "work" reduces "dominance value," (DV), a measure of competitiveness for breeding spots, which otherwise goes up linearly with age, but defense reduces survival probability. Both eventually might preclude the helper from becoming a breeder and reproducing. How much the helpers help, and which tasks (and whether they transition or not), as well as their propensity to disperse, are all evolving quantities. The authors consider three main scenarios: one where relatedness emerges from the model, but there is no benefit to living in groups, one where there is no relatedness, but living in larger groups gives a survival benefit (group augmentation, GA), and one where both effects operate. The main claim is that evolving defensive help or division of labor requires the group augmentation; it doesn't evolve through kin selection alone in the authors' simulations.

This is an interesting model, and there is much to like about the complexity that is built in. Individual-based simulations like this can be a valuable tool to explore the complex interaction of life history and social traits. Yet, models like this also have to take care of both being very clear on their construction and exploring how some of the ancillary but potentially consequential assumptions affect the results, including robust exploration of the parameter space. I think the current manuscript falls short in these areas, and therefore, I am not yet convinced of the results. Much of this is a matter of clearer and more complete writing: the Materials and Methods section in particular is incomplete or vague in some important junctions. However, there are also some issues with the assumptions that are described clearly.

Below, I describe my main issues, mostly having to do with model features that are unclear, poorly motivated (as they stand), or potentially unrealistic or underexplored.

One of the main issues I have is that there is almost no information on what happens to dispersers in the model. Line 369-67 states dispersers might join another group or remain as floaters, but gives no further information on how this is determined. Poring through the notation table also comes up empty as there is no apparent parameter affecting this consequential life history event. At some point, I convinced myself that dispersers remain floaters until they die or become breeders, but several points in the text contradict this directly (e.g., l 107). Clearly this is a hugely important model feature since it determines fitness cost and benefits of dispersal and group size (which also affects relatedness and/or fitness depending on the model). There just isn't enough information to understand this crucial component of the model, and without it, it is hard to make sense of the model output.

Related to that, it seems to be implied (but never stated explicitly) that floaters do no work, and therefore their DV increases linearly with age (H_work in eq.2 is zero). That means any floaters that manage to stick around long enough would have higher success in competition for breeding spots relative to existing group members. How realistic is this? I think this might be driving the kin selection-only results that defense doesn't evolve without group augmentation (one of the two main ways). Any subordinates (which are mainly zero in the no GA, according to the SI tables; this assumes N=breeder+subordinates, but this isn't explicit anywhere) would be outcompeted by floaters after a short time (since they evolve high H and floaters don't), which in turn increases the benefit of dispersal, explaining why it is so high. Is this parameter regime reasonable? My understanding is that floaters often aren't usually high resource holding potential individuals (either b/c high RHP ones would get selected out of the floater population by establishing territories or b/c floating isn't typically a thriving strategy, given that many resources are tied to territories). In this case, the assumption seems to bias things towards the floaters and against subordinates to inherit territories. This should be explored either with a higher mortality rate for floaters and/or a lower DV increase, or both.

When it comes to floaters replacing dead breeders, the authors say a bit more, but again, the actual equation for the scramble competition (which only appears as "scramble context" in the notation table) is not given. Is it simply proportional to R_i/\sum_j R_j ? Or is there some other function used? What are the actual numbers of floaters per breeding territory that emerge under different parameter values? These are all very important quantities that have to be described clearly.

I also think the asexual reproduction with small mutations assumption is a fairly strong one that also seems to bias the model outcomes in a particular way. I appreciate that the authors actually measured relatedness within groups (though if most groups under KS have no subordinates, that relatedness becomes a bit moot), and also eliminated it with their ingenious swapping-out-subordinates procedure. The fact remains that unless they eliminate relatedness completely, average relatedness, by design, will be very high. (Again, this is also affected by how the fate of the dispersers is determined, but clearly there isn't a lot of joining happening, just judging from mean group sizes under KS only.) This is, of course, why there is so much helping evolving (even if it's not defensive) unless they completely cut out relatedness.

Finally, the "need for division of labor" section is also unclear, and its construction also would seem to bias things against division of labor evolving. For starters, I don't understand the rationale for the convoluted way the authors create an incentive for division of labor. Why not implement something much simpler, like a law of minimum (i.e., the total effect of helping is whatever the help amount for the lowest value task is) or more intuitively: the fecundity is simply a function of "work" help (draw Poisson number of offspring) and survival of offspring (draw binomial from the fecundity) is a function of the "defense" help. As it is, even though the authors say they require division of labor, in fact, they only make a single type of help marginally less beneficial (basically by half) if it is done more than the other. That's a fairly weak selection for division of labor, and to me it seems hard to justify. I suspect either of the alternative assumptions above would actually impose enough selection to make division of labor evolve even without group augmentation.

Overall, this is an interesting model, but the simulation is not adequately described or explored to have confidence in the main conclusions yet. Better exposition and more exploration of alternative assumptions and parameter space are needed.

Reviewer #2 (Public review):

Summary:

This paper formulates an individual-based model to understand the evolution of division of labor in vertebrates. A main conclusion of the paper is that direct fitness benefits are the primary factor causing the evolution of vertebrate division of labor, rather than indirect fitness benefits.

Strengths:

The paper formulates an individual-based model that is inspired by vertebrate life history. The model incorporates numerous biologically realistic details, including the possibility to evolve age polytheism where individuals switch from work to defence tasks as they age or vice versa, as well as the possibility of comparing the action of group augmentation alone with that of kin selection alone.

Weaknesses:

The model makes assumptions that restrict the possibility that kin selection leads to the evolution of helping. In particular, the model assumes that in the absence of group augmentation, subordinates can only help breeders but cannot help non-breeders or increase the survival of breeders, whereas with group augmentation, subordinates can help both breeders and non-breeders and increase the survival of breeders. This is unrealistic as subordinates in real organisms can help other subordinates and increase the survival of non-breeders, even in the absence of group augmentation, for instance, with targeted helping to dominants or allies. This restriction artificially limits the ability of kin selection alone to lead to the evolution of helping, and potentially to division of labor. Hence, the conclusion that group augmentation is the primary driving factor driving vertebrate division of labor appears forced by the imposed restrictions on kin selection. The model used is also quite particular, and so the claimed generality across vertebrates is not warranted.

I describe some suggestions for improving the paper below, more or less in the paper's order.

First, the introduction goes to great lengths trying to convince the reader that this model is the first in this or another way, particularly in being only for vertebrates, as illustrated in the abstract where it is stated that "we lack a theoretical framework to explore the conditions under which division of labor is likely to evolve" (line 13). However, this is a risky and unnecessary motivation. There are many models of division of labor and some of them are likely to be abstract enough to apply to vertebrates even if they are not tailored to vertebrates, so the claims for being first are not only likely to be wrong but will put many readers in an antagonistic position right from the start, which will make it harder to communicate the results. Instead of claiming to be the first or that there is a lack of theoretical frameworks for vertebrate division of labor, I think it is enough and sufficiently interesting to say that the paper formulates an individual-based model motivated by the life history of vertebrates to understand the evolution of vertebrate division of labor. You could then describe the life history properties that the model incorporates (subordinates can become reproductive, low relatedness, age polyethism, etc.) without saying this has never been done or that it is exclusive to vertebrates; indeed, the paper states that these features do not occur in eusocial insects, which is surprising as some "primitively" eusocial insects show them. So, in short, I think the introduction should be extensively revised to avoid claims of being the first and to make it focused on the question being addressed and how it is addressed. I think this could be done in 2-3 paragraphs without the rather extensive review of the literature in the current introduction.

Second, the description of the model and results should be clarified substantially. I will give specific suggestions later, but for now, I will just say that it is unclear what the figures show. First, it is unclear what the axes in Figure 2 show, particularly for the vertical one. According to the text in the figure axis, it presumably refers to T, but T is a function of age t, so it is unclear what is being plotted. The legend explaining the triangle and circle symbols is unintelligible (lines 227-230), so again it is unclear what is being plotted; part of the reason for this unintelligibility is that the procedure that presumably underlies it (section starting on line 493) is poorly explained and not understandable (I detail why below). Second, the axes in Figure 3 are similarly unclear. The text in the vertical axis in panel A suggests this is T, however, T is a function of t and gamma_t, so something else must be being done to plot this. Similarly, in panel B, the horizontal axis is presumably R, but R is a function of t and of the helping genotype, so again some explanation is lacking. In all figures, the symbol of what is being plotted should be included.

Third, the conclusions sound stronger than the results are. A main conclusion of the paper is that "kin selection alone is unlikely to select for the evolution of defensive tasks and division of labor in vertebrates" (lines 194-195). This conclusion is drawn from the left column in Figure 2, where only kin selection is at play, and the helping that evolves only involves work rather than defense tasks. This conclusion follows because the model assumes that without group augmentation (i.e., xn=0, the kin selection scenario), subordinates can only help breeders to reproduce but cannot help breeders or other subordinates to survive, so the only form of help that evolves is the least costly, not the most beneficial as there is no difference in the benefits given among forms of helping. This assumption is unrealistic, particularly for vertebrates where subordinates can help other group members survive even in the absence of group augmentation (e.g., with targeted help to certain group members, because of dominance hierarchies where the helping would go to the breeder, or because of alliances where the helping would go to other subordinates). I go into further details below, but in short, the model forces a narrow scope for the kin selection scenario, and then the paper concludes that kin selection alone is unlikely to be of relevance for the evolution of vertebrate division of labor. This conclusion is particular to the model used, and it is misleading to suggest that this is a general feature of such a particular model.

Overall, I think the paper should be revised extensively to clarify its aims, model, results, and scope of its conclusions.

Reviewer #1 (Public review):

Summary:

This manuscript presents a practical modification of the orthogonal hybridization chain reaction (HCR) technique, a promising yet underutilized method with broad potential for future applications across various fields. The authors advance this technique by integrating peptide ligation technology and nanobody-based antibody mimetics - cost-effective and scalable alternatives to conventional antibodies - into a DNA-immunoassay framework that merges oligonucleotide-based detection with immunoassay methodologies. Notably, they demonstrate that this approach facilitates a modified ELISA platform capable of simultaneously quantifying multiple target protein expression levels within a single protein mixture sample.

Strengths:

The hybridization chain reaction (HCR) technique was initially developed to enable the simultaneous detection of multiple mRNA expression levels within the same tissue. This method has since evolved into immuno-HCR, which extends its application to protein detection by utilizing antibodies. A key requirement of immuno-HCR is the coupling of oligonucleotides to antibodies, a process that can be challenging due to the inherent difficulties in expressing and purifying conventional antibodies.

In this study, the authors present an innovative approach that circumvents these limitations by employing nanobody-based antibody mimetics, which recognize antibodies, instead of directly coupling oligonucleotides to conventional antibodies. This strategy facilitates oligonucleotide conjugation - designed to target the initiator hairpin oligonucleotide of HCR -through peptide ligation and click chemistry.

Weaknesses:

The sandwich-format technique presented in this study, which employs a nanobody that recognizes primary IgG antibodies, may have limited scalability compared to existing methods that directly couple oligonucleotides to primary antibodies. This limitation arises because the C-region types of primary antibodies are relatively restricted, meaning that the use of nanobody-based detection may constrain the number of target proteins that can be analyzed simultaneously. In contrast, the conventional approach of directly conjugating oligonucleotides to primary antibodies allows for a broader range of protein targets to be analyzed in parallel.

Additionally, in the context of HCR-based protein detection, the number of proteins that can be analyzed simultaneously is inherently constrained by fluorescence wavelength overlap in microscopy, which limits its multiplexing capability. By comparison, direct coupling of oligonucleotides to primary antibodies can facilitate the simultaneous measurement of a significantly greater number of protein targets than the sandwich-based nanobody approach in the barcode-ELISA/NGS-based technique.

Reviewer #1 (Public review):

Summary:

This study puts forth the model that under IFN-B stimulation, liquid-phase WTAP coordinates with the transcription factor STAT1 to recruit MTC to the promoter region of interferon stimulated genes (ISGs), mediating the installation of m6A on newly synthesized ISG mRNAs. This model is supported by strong evidence that the phosphorylation state of WTAP, regulated by PPP4, is regulated by IFN-B stimulation, and that this results in interactions between WTAP, the m6A methyltransferase complex, and STAT1, a transcription factor that mediates activation of ISGs. This was demonstrated via a combination of microscopy, immunoprecipitations, m6A sequencing, and ChIP. These experiments converge on a set of experiments that nicely demonstrate that IFN-B stimulation increases the interaction between WTAP, METTL3, and STAT1, that this interaction is lost with knockdown of WTAP (even in the presence of IFN-B), and that this IFN-B stimulation also induces METTL3-ISG interactions.

Strengths:

The evidence for the IFN-B stimulated interaction between METTL3 and STAT1, mediated by WTAP, is quite strong. Removal of WTAP in this system seems to be sufficient to reduce these interactions and the concomitant m6A methylation of ISGs. The conclusion that the phosphorylation state of WTAP is important in this process is also quite well supported. The authors have now also provided substantial evidence that phase separation of WTAP upon interferon stimulation facilitates m6A-methylation of multiple interferon stimulated genes.

Reviewer #2 (Public review):

In this study, Cai and colleagues investigate how one component of the m6A methyltransferase complex, the WTAP protein, responds to IFNb stimulation. They find that viral infection or IFNb stimulation induces the transition of WTAP from aggregates to liquid droplets through dephosphorylation by PPP4. This process affects the m6A modification levels of ISG mRNAs and modulates their stability. In addition, the WTAP droplets interact with the transcription factor STAT1 to recruit the methyltransferase complex to ISG promoters and enhance m6A modification during transcription. The investigation dives into a previously unexplored area of how viral infection or IFNb stimulation affects m6A modification on ISGs. The observation that WTAP undergoes a phase transition is significant in our understanding of the mechanisms underlying m6A's function in immunity. However, there are still key gaps that should be addressed to fully accept the model presented.

Major points:<br /> (1) More detailed analyses on the effects of WTAPsgRNA on the m6A modification of ISGs:<br /> a. A comprehensive summary of the ISGs, including the percentage of ISGs that are m6A-modified,<br /> b. The distribution of m6A modification across the ISGs, and<br /> c. A comparison of the m6A modification distribution in ISGs with non-ISGs.<br /> In addition, since the authors propose a novel mechanism where the interaction between phosphorylated STAT1 and WTAP direct the MTC to the promoter regions of ISGs to facilitate co-transcriptional m6A modification, it is critical to analyze whether the m6A modification distribution holds true in the data.

(2) Since a key part of the model includes the cytosol-localized STAT1 protein undergoing phosphorylation to translocate to the nucleus to mediate gene expression, the authors should focus on the interaction between phosphorylated STAT1 and WTAP in Figure 4, rather than the unphosphorylated STAT1. Only phosphorylated STAT1 localizes to the nucleus, so the presence of pSTAT1 in the immunoprecipitate is critical for establishing a functional link between STAT1 activation and its interaction with WTAP.

(3) The authors should include pSTAT1 ChIP-seq and WTAP ChIP-seq on IFNb-treated samples in Figure 5 to allow for a comprehensive and unbiased genomic analysis for comparing the overlaps of peaks from both ChIP-seq datasets. These results should further support for their hypothesis that WTAP interacts with pSTAT1 to enhance m6A modifications on ISGs.

Minor points:<br /> (1) Since IFNb is primarily known for modulating biological processes through gene transcription, it would be informative if the authors discussed the mechanism of how IFNb would induce the interaction between WTAP and PPP4.

(2) The authors should include mCherry alone controls in Figure 1D to demonstrate that mCherry does not contribute to the phase separation of WTAP. Does mCherry have or lack a PLD?

(3) The authors should clarify the immunoprecipitation assays in the methods. For example, the labeling in Fig. 2A suggests that antibodies against WTAP and pan-p were used for two immunoprecipitations. Is that accurate?

(4) The authors should include overall m6A modification levels quantified of GFPsgRNA and WTAPsgRNA cells, either by mass spectrometry (preferably) or dot blot.

Comments on revisions:

The authors thoroughly addressed the aforementioned points during the review process.

Reviewer #3 (Public review):

Summary:

This study presents a valuable finding on the mechanism used by WTAP to modulate the IFN-β stimulation. It describes the phase transition of WTAP driven by IFN-β-induced dephosphorylation. The evidence supporting the claims of the authors is solid.

Strength:

The key finding is the revelation that WTAP undergoes phase separation during virus infection or IFN-β treatment. The authors conducted a series of precise experiments to uncover the mechanism behind WTAP phase separation and identified the regulatory role of 5 phosphorylation sites. They also succeeded in pinpointing the phosphatase involved.

Reviewer #2 (Public review):

Summary:

TDP-43 mislocalization occurs in nearly all of ALS, roughly half of FTD, and as a co-pathology in roughly half of AD cases. Both gain of function and loss of function mechanisms associated with this mislocalization likely contribute to disease pathogeneisis.

Here, the authors describe a new method to induce TDP-43 mislocalization in cellular models. They endogenously-tagged TDP-43 with a C-terminal GFP tag in human iPSCs. They then expressed an intrabody - fused with a nuclear export signal (NES) - that targeted GFP to the cytosol. Expression of this intrabody-NES in human iPSC derived neurons induced nuclear depletion of homozygous TDP-43-GFP, caused its mislocalization to the cytosol, and at least in some cells appeared to cause cytosolic aggregates. This mislocalization was accompanied by induction of cryptic exons in well characterized transcripts known to be regulated by TDP-43, a hallmark of functional TDP-43 loss and consistent with pathological nuclear TDP-43 depletion. Interestingly, in heterozygous TDP-43-GFP neurons, expression of intrabody-NES appeared to also induce the mislocalization of untagged TDP-43 in roughly half of the neurons, suggesting that this system can also be used to study effects on untagged endogenous TDP-43 as well as TDP-43-GFP fusion protein.

Strengths:

A clearer understanding of how TDP-43 mislocalization alters cellular function, as well as pathways that mitigate clearance of TDP-43 aggregates, is critical. But modeling TDP-43 mislocalization in disease-relevant cellular systems has proven to be challenging. High levels of overexpression of TDP-43 lacking an NES can drive endogenous TDP-43 mislocalization, but such overexpression has direct and artificial consequences on certain cellular features (e.g. altered exon skipping) not seen in diseased patients. Toxic small molecules such as MG132 and arsenite can induce TDP-43 mislocalization, but co-induce myriad additional cellular dysfunctions unrelated to TDP-43 or ALS. TDP-43 binding oligonucleotides can cause cytosolic mislocalization as well. Each system has pros and cons, and additional ways to induce TDP-43 mislocalization would be useful for the field. The method described in this manuscript could provide researchers with a powerful way to study the combined biology of cytosolic TDP-43 mislocalization and nuclear TDP-43 depletion, with additional temporal control that is lacking in current method. Indeed, the author see some evidence of differences in RNA splicing caused by pure TDP-43 depletion versus their induced mislocalization model. Finally, their method may be especially useful in determining how TDP-43 aggregates are cleared by cells, potentially revealing new biological pathways that could be therapeutically targeted.

Weaknesses:

The method and supporting data have some limitations.

• Tagging of TDP-43 with a bulky GFP tag may alter its normal physiological functions, for example, phase separation properties and functions within complex ribonucleoprotein complexes. The authors show that normal splicing function of GFP-TDP-43 is maintained, suggesting that physiology is largely preserved, but other functions and properties of TDP-43 that were not directly tested could be altered.

• Potential differences in splicing and micro RNAs between TDP-43 knockdown and TDP-43 mislocalization are potentially interesting. However, different patterns of dysregulated RNA splicing can occur at different levels of TDP-knockdown and can differ in different batches of experiments, thus it is difficult to asses whether the changes observed in this paper are due to mislocalization per se, or rather just reflect differences in nuclear TDP-43 abundance or batch effects.

Reviewer #1 (Public review):

Summary:

This paper reports an intracranial SEEG study of speech coordination, where participants synchronize their speech output with a virtual partner that is designed to vary its synchronization behavior. This allows the authors to identify electrodes throughout the left hemisphere of the brain that have activity (both power and phase) that correlates with the degree of synchronization behavior. They find that high-frequency activity in secondary auditory cortex (superior temporal gyrus) is correlated to synchronization, in contrast to primary auditory regions. Furthermore, activity in inferior frontal gyrus shows a significant phase-amplitude coupling relationship that is interpreted as compensation for deviation from synchronized behavior with the virtual partner.

Strengths:<br /> (1) The development of a virtual partner model trained for each individual participant, which can dynamically vary its synchronization to the participant's behavior in real time, is novel and exciting.<br /> (2) Understanding real-time temporal coordination for behaviors like speech is a critical and understudied area.<br /> (3) The use of SEEG provides the spatial and temporal resolution necessary to address the complex dynamics associated with the behavior.<br /> (4) The paper provides some results that suggest a role for regions like IFG and STG in the dynamic temporal coordination of behavior both within an individual speaker and across speakers performing a coordination task.

Weaknesses:

(1) The main weakness of the paper is that the results are presented in a largely descriptive and vague manner. For instance, while the interpretation about predictive coding and error correction is interesting, it is not clear how the experimental design or analyses specifically support such a model, or how they differentiate that model from the alternatives. It's possible that some greater specificity could be achieved by a more detailed examination of this rich dataset, for example by characterizing the specific phase relationships (e.g., positive vs negative lags) in areas that show correlations with synchronization behavior. However, as written, it is difficult to understand what these results tell us about how coordination behavior arises.<br /> (2) In the results section, there's a general lack of quantification. While some of the statistics reported in the figures are helpful, there are also claims that are stated without any statistical test. For example, in the paragraph starting on line 342, it is claimed that there is an inverse relationship between rho-value and frequency band, "possibly due to the reversed desynchronization/synchronization process in low and high frequency bands". Based on Figure 3, the first part of this statement appears to be true qualitatively, but is not quantified, and is therefore impossible to assess in relation to the second part of the claim. Similarly, the next paragraph on line 348 describes optimal clustering, but statistics of the clustering algorithm and silhouette metric are not provided. More importantly, it's not entirely clear what is being clustered - is the point to identify activity patterns that are similar within/across brain regions? Or to interpret the meaning of the specific patterns? If the latter, this is not explained or explored in the paper.<br /> (3) Given the design of the stimuli, it would be useful to know more about how coordination relates to specific speech units. The authors focus on the syllabic level, which is understandable. But as far as the results relate to speech planning (an explicit point in the paper), the claims could be strengthened by determining whether the coordination signal (whether error correction or otherwise) is specifically timed to e.g., the consonant vs the vowel. If the mechanism is a phase reset, does it tend to occur on one part of the syllable?<br /> (4) In the discussion the results are related to a previously described speech-induced suppression effect. However, it's not clear what the current results have to do with SIS, since the speaker's own voice is present and predictable from the forward model on every trial. Statements such as "Moreover, when the two speech signals come close enough in time, the patient possibly perceives them as its own voice" are highly speculative and apparently not supported by the data.<br /> (5) There are some seemingly arbitrary decisions made in the design and analysis that, while likely justified, need to be explained. For example, how were the cutoffs for moderate coupling vs phase-shifted coupling (k ~0.09) determined? This is noted as "rather weak" (line 212), but it's not clear where this comes from. Similarly, the ROI-based analyses are only done on regions "recorded in at least 7 patients" - how was this number chosen? How many electrodes total does this correspond to? Is there heterogeneity within each ROI?

Comments on revisions:

The authors have generally responded to the critiques from the first round of review, and have provided additional details that help readers to understand what was done.

In my opinion, the paper still suffers from a lack of clarity about the interpretation, which is partly due to the fact that the results themselves are not straightforward. For example, the heterogeneity across individual electrodes that is obvious from Fig 3 makes it hard to justify the ROI-based approach. And even the electrode clustering, while more data-driven, does not substantially help the fact that the effects appear to be less spatially-organized than the authors may want to claim.

I recognize the value of introducing this new mutual adaptation paradigm, which is the main strength of the paper. However, the conclusions that can be drawn from the data presented here seem incomplete at best.

Reviewer #2 (Public review):

Summary:

This paper investigates the neural underpinnings of an interactive speech task requiring verbal coordination with another speaker. To achieve this, the authors recorded intracranial brain activity from the left (and to a lesser extent, the right) hemisphere in a group of drug-resistant epilepsy patients while they synchronised their speech with a 'virtual partner'. Crucially, the authors were able to manipulate the degree of success of this synchronisation by programming the virtual partner to either actively synchronise or desynchronise their speech with the participant, or else to not vary its speech in response to the participant (making the synchronisation task purely one-way). Using such a paradigm, the authors identified different brain regions that were either more sensitive to the speech of the virtual partner (primary auditory cortex), or more sensitive to the degree of verbal coordination (i.e. synchronisation success) with the virtual partner (left secondary auditory cortex and bilateral IFG). Such sensitivity was measured by (1) calculating the correlation between the index of verbal coordination and mean power within a range of frequency bands across trials, and (2) calculating the phase-amplitude coupling between the behavioural and brain signals within single trials (using the power of high-frequency neural activity only). Overall, the findings help to elucidate some of the brain areas involved in interactive speaking behaviours, particularly highlighting high-frequency activity of the bilateral IFG as a potential candidate supporting verbal coordination.

Strengths:

This study provides the field with a convincing demonstration of how to investigate speaking behaviours in more complex situations that share many features with real-world speaking contexts e.g. simultaneous engagement of speech perception and production processes, the presence of an interlocutor and the need for inter-speaker coordination. The findings thus go beyond previous work that has typically studied solo speech production in isolation, and represent a significant advance in our understanding of speech as a social and communicative behaviour. It is further an impressive feat to develop a paradigm in which the degree of cooperativity of the synchronisation partner can be so tightly controlled; in this way, this study combines the benefits of using pre-recorded stimuli (namely, the high degree of experimental control) with the benefits of using a live synchronisation partner (allowing the task to be truly two-way interactive, an important criticism of other work using pre-recorded stimuli). A further key strength of the study lies in its employment of stereotactic EEG to measure brain responses with both high temporal and spatial resolution, an ideal method for studying the unfolding relationship between neural processing and this dynamic coordination behaviour.

Weaknesses:

One limitation of the current study is the relatively sparse coverage of the right hemisphere by the implanted electrodes (91 electrodes in the right compared to 145 in the left). Of course, electrode location is solely clinically motivated, and so the authors did not have control over this. In a previous version of this article, the authors therefore chose not to include data from the right hemisphere in reported analyses. However, after highlighting previous literature suggesting that the right hemisphere likely has high relevance to verbal coordination behaviours such as those under investigation here, the authors have now added analyses of the right hemisphere data to the results. These confirm an involvement of the right hemisphere in this task, largely replicating left hemisphere results. Some hemispheric differences were found in responses within the STG; however, interpretation should be tempered by an awareness of the relatively sparse coverage of the right hemisphere meaning that some regions have very few electrodes, resulting in reduced statistical power.

Reviewer #1 (Public review):

Summary:

The authors set out to explore the role of upstream open reading frames (uORFs) in stabilizing protein levels during Drosophila development and evolution. By utilizing a modified ICIER model for ribosome translation simulations and conducting experimental validations in Drosophila species, the study investigates how uORFs buffer translational variability of downstream coding sequences. The findings reveal that uORFs significantly reduce translational variability, which contributes to gene expression stability across different biological contexts and evolutionary timeframes.

Strengths:

(1) The study introduces a sophisticated adaptation of the ICIER model, enabling detailed simulation of ribosomal traffic and its implications for translation efficiency.<br /> (2) The integration of computational predictions with empirical data through knockout experiments and translatome analysis in Drosophila provides a compelling validation of the model's predictions.<br /> (3) By demonstrating the evolutionary conservation of uORFs' buffering effects, the study provides insights that are likely applicable to a wide range of eukaryotes.

Weaknesses:

(1) Although the study is technically sound, it does not clearly articulate the mechanisms through which uORFs buffer translational variability. A clearer hypothesis detailing the potential molecular interactions or regulatory pathways by which uORFs influence translational stability would enhance the comprehension and impact of the findings.<br /> (2) The study could be further improved by a discussion regarding the evolutionary selection of uORFs. Specifically, it would be beneficial to explore whether uORFs are favored evolutionarily primarily for their role in reducing translation efficiency or for their capability to stabilize translation variability. Such a discussion would provide deeper insights into the evolutionary dynamics and functional significance of uORFs in genetic regulation.

Comments on revisions:

The authors have adequately addressed my previous concerns.

Reviewer #2 (Public review):

uORFs, short open reading frames located in the 5' UTR, are pervasive in genomes. However, their roles in maintaining protein abundance are not clear. In this study, the authors propose that uORFs act as "molecular dam", limiting the fluctuation of the translation of downstream coding sequences. First, they performed in silico simulations using an improved ICIER model, and demonstrated that uORF translation reduces CDS translational variability, with buffering capacity increasing in proportion to uORF efficiency, length, and number. Next, they analysed the translatome between two related Drosophila species, revealing that genes with uORFs exhibit smaller fluctuations in translation between the two species and across different developmental stages within the same species. Moreover, they identified that bicoid, a critical gene for Drosophila development, contains a uORF with substantial changes in translation efficiency. Deleting this uORF in Drosophila melanogaster significantly affected its gene expression, hatching rates, and survival under stress conditions. Lastly, by leveraging public Ribo-seq data, the authors showed that the buffering effect of uORFs is also evident between primates and within human populations. Collectively, the study significantly advances our understanding of how uORFs regulate the translation of downstream coding sequences at the genome-wide scale, as well as during development and evolution. It would be particularly interesting to explore whether similar buffering functions are conserved in other organisms, and whether their regulatory effects could be harnessed for practical applications, such as improving crop traits or benefiting human health.

Comments on revisions:

The authors have fully addressed all of my concerns, and the revisions have substantially improved the manuscript. I have no further comments.

Reviewer #1 (Public review):

Summary:

This study aimed at replicating two previous findings that showed (1) a link between prediction tendencies and neural speech tracking, and (2) that eye movements track speech. The main findings were replicated which supports the robustness of these results. The authors also investigated interactions between prediction tendencies and ocular speech tracking, but the data did not reveal clear relationships. The authors propose a framework that integrates the findings of the study and proposes how eye movements and prediction tendencies shape perception.

Strengths:

This is a well-written paper that addresses interesting research questions, bringing together two subfields that are usually studied in separation: auditory speech and eye movements. The authors aimed at replicating findings from two of their previous studies, which was overall successful and speaks for the robustness of the findings. The overall approach is convincing, methods and analyses appear to be thorough, and results are compelling.

Weaknesses:

Eye movement behavior could have presented in more detail and the authors could have attempted to understand whether there is a particular component in eye movement behavior (e.g., blinks, microsaccades) that drives the observed effects.

Reviewer #2 (Public review):

Summary

Schubert et al. recorded MEG and eye tracking activity while participants were listening to stories in single-speaker or multi-speaker speech. In a separate task, MEG was recorded while the same participants were listening to four types of pure tones in either structured (75% predictable) or random (25%) sequences. The MEG data from this task was used to quantify individual 'prediction tendency': the amount by which the neural signal is modulated by whether or not a repeated tone was (un)predictable, given the context. In a replication of earlier work, this prediction tendency was found to correlate with 'neural speech tracking' during the main task. Neural speech tracking is quantified as the multivariate relationship between MEG activity and speech amplitude envelope. Prediction tendency did not correlate with 'ocular speech tracking' during the main task. Neural speech tracking was further modulated by local semantic violations in the speech material and by whether or not a distracting speaker was present. The authors suggest that part of the neural speech tracking is mediated by ocular speech tracking. Story comprehension was negatively related with ocular speech tracking.

Strengths

This is an ambitious study, and the authors' attempt to integrate the many reported findings related to prediction and attention in one framework is laudable. The data acquisition and analyses appear to be done with great attention to methodological detail. Furthermore, the experimental paradigm used is more naturalistic than was previously done in similar setups (i.e.: stories instead of sentences).

Weaknesses

While the analysis pipeline is outlined in much detail, some analysis choices appear ad-hoc and could have been more uniform and/or better motivated (other than: this is what was done before).

Reviewer #3 (Public review):

I thank the authors for their extensive revision of this paper, and I found some elements greatly improved.<br /> In particular, the authors do embrace a somewhat more speculative tone in the current version, which I think is fitting for this work, as the data seem (to me) to be not fully conclusive. The data set collected here is clearly valuable and unique (and I would encourage the authors to make it publicly available!), however, my overall impression is that the specific analyses reported here might not fully

Despite the revised description of methods, results and figures, I still have trouble understanding many of the results and the authors conclusive interpretation of them. These are my main reservations:

(1) Regarding "individual prediction tendency" - thank you for adding clarifying methodological details and showing the data in a new Figure (#2). Honestly, however, I still can't say that I fully understand the result. For example, why is there also a significant response in the random condition as well? And how do you interpret the interesting time-course (with a peak ~200ms prior to the stimulus, and a reduction overtime from there?<br /> Also (I may have missed this, but..) what neural data was used to train the classifier and derive the "prediction tendency" index? Was it just the broadband neural response? Is there a way to know which sensors contributed to this metric (e.g., are they predominantly auditory? Frontal?)? And is there a way to establish the statistical significance of this metric (e.g., how good the decoder actually was in predicting behavioral sensitivity?). I don't see any statistics in the results section describing the individual prediction tendency.

(2) Regarding the TRF analysis - Thanks for clarifying the approach used to obtain 2-second long "segments" of speech tracking. This is an interesting approach, however I think quite new(?) , and for me it raises a whole new set of questions, as well as additional controls and data that I would have liked to see, to be convinced that results are significant. I will elaborate:

- Do I understand correctly that you segment the real and predicted neural response into 2-second long segments and then calculate the Pearsons' correlation between them to assess the goodness of the model? This is very unclear, since in the methods section you state only that "the same" analysis was performed as for the full data - but what exactly? Clearly, values will be very different when using such short segments. I feel that additional details are still required (and perhaps data shown) to fully understand the "semantic violation" analysis of TRFs.

- I would like to reiterate my previous comment regarding the use of permutation tests to verify the validity of TRF-based measures derived. This would be especially important when using new approaches (such as the segmentation used here). The authors argue that this is not needed since this was not done in their previously published study. However, this sounds a bit like "two wrongs make a right" argument... why not just do it, and let us know that this 2-second segmentation approach allows estimating reliable speech tracking?

- Following up on my previous comment that defining "clusters" as at least two neighboring channels (Figure 3) - the fact that this is a default in Fieldtrip is by no means sufficient justification!. This seems quite liberal to me, especially given the many comparisons performed. Here too, permutations can help to determine the necessary data-driven threshold for corrections. This is of course critical for interpreting the result shown in Figures 3E&G that are critical "take home messages" of the paper - i.e., that the prediction-index from the first part of the experiment is related to speech tracking in the second part of the experiment. To my eyes, this does not look extremely convincing, but perhaps the authors can show more conclusive data to support this (e.g., scatter plots of the betas across participant?).<br /> - A similar point can be made for the effect of semantic violations (though here the scalp-level result is somewhat more clustered). The authors point out that the semantic effect is a "replication" of their result reported in Schubert et al. 2023, but if I am not mistaken the results there were somewhat different (as was the manipulation). It would be nice to explicitly discuss the similarity/difference between these effects.

(3) Regarding the ocular-TRFs -

- Maybe this is just me, but I believe that effects that are robust should be clearly visible in the data, without the need for fancy "black-box" statistical models. In the case of the ocular TRFs, it is hard for me to see how these time-courses are not just noise (and, again, a permutation test would have helped to convince me..). The inconsistent results for horizontal and vertical eye-movements vis a vis the experimental conditions (single vs. multi-speaker conditions) don't help either, despite the authors argument that these are "independent" - but why should this be the case, especially if there is nothing really to look at in this task?<br /> - I remain with this scepticism for the mediation-portion of the analysis as well... But perhaps replications from other groups or making the data public will help shed further light on this in the future.

Minor<br /> - Thanks for adding information about the creation of semantic-violation stimuli. Since the violations and lexical-controls were taken from different audio recordings, it would have been nice to verify that differences between neural responses cannot be attributed to differences in articulations (e.g., by comparing their spectro-temporal properties).

Reviewer #1 (Public review):

Summary:

The study tests the conservation of imprinting of the ZBDF2 locus across mammals. ZDBF2 is known to be imprinted in mouse, human and rat. The locus has a unique mechanism of imprinting: although imprinting is conferred by a germline DMR methylated in oocytes, the DMR is upstream to ZDBF2 (at GPR1) and monoallelic methylation of the gDMR does not persist beyond early developmental stages. Instead, a lncRNA (GPR1-AS, also known as Liz in mouse) initiating at the gDMR is expressed transiently in embryos and sets up a secondary DMR (by mechanisms not fully elucidated) that then confers monoallelic expression of ZDBF2 in somatic tissues.

In this study, the authors first interrogate existing placental RNA-seq datasets from multiple mammalian species, and detect GPR1-AS1 candidate transcripts in human, baboon, macaque and mouse, but not in about a dozen other mammals. Because of the varying depth, quality and nature of these RNA-seq libraries, the ability to definitely detect the GPR1-AS1 lncRNA is not guaranteed; therefore, they generate their own deep, directional RNA-seq data from tissues/embryos from five species, finding evidence of GPR1-AS in rabbit, chimpanzee, but not bovine, pig or opossum. From these surveys, the authors conclude that the lncRNA is present only in Euarchontoglires mammals. To test the association between GPR1-AS and ZDBF2 imprinting, they perform RT-PCR and sequencing in tissue from wallabies and cattle, finding biallelic expression of ZDBF2 in these species that also lack a detected GPR1-AS transcript. From inspection of the genomic location of the GPR1-AS first exon, the authors identify an overlap with a solo LTR of the MER21C retrotransposon family in those species in which the lncRNA is observed, except for some rodents, including mouse. However, they do detect a degree of homology (46%) to the MER21C consensus at the first exon on Liz in mouse. Finally, the authors explore public RNA-seq datasets to show that GPR1-AS is expression transiently during human preimplantation development, an expression dynamic that would be consistent with the induction of monoallelic methylation of a somatic DMR at ZDBF2 and consequent monoallelic expression.

Strengths:

The analysis uncovers a novel mechanism by which a retrotransposon-derived LTR may be involved in genomic imprinting.<br /> The genomic analysis is very well executed.<br /> New directional and deeply-sequenced RNA-seq datasets from placenta or trophectoderm of five mammalian species and marsupial embryos, which will be of value to the community.

Weaknesses:

Although the genomic analysis is very strong, the study remains entirely correlative. All of the data are descriptive, and much of the analysis is performed on RNA-seq and other datasets from the public domain; a small amount of primary data is generated by the authors.<br /> Evidence that the residual LTR in mouse is functionally relevant for Liz lncRNA expression is lacking.

Comments on revision:

The authors have responded very constructively to all points raised by me and the other reviewers. For example, the authors have gone to further, extensive efforts in seeking to identify an LTR at the mouse Liz locus - which is not found - but additional multiple genome alignments provide evidence for sequence conservation consistent with retention of a functional relic of the MER21C in rodent genomes. Moreover, they demonstrate the promoter activity of this mouse sequence region in transfections. They have also demonstrated imprinted expression of ZDBF2 in two additional species - rabbit and rhesus macaque - consistent with their model.

Reviewer #2 (Public review):

Summary:

This work concerns the evolution of ZDBF2 imprinting in mammalian species via initiation of GPR1 antisense (AS) transcription from a lineage-specific long-terminal repeat (LTR) retrotransposon. It extends previous work describing the mechanism of ZDBF2 imprinting in mice and humans by demonstrating conservation of GPR1-AS transcripts in rabbits and non-human primates. By identifying the origin of GPR1-AS transcription as the LTR MER21C, the authors claim to account for how imprinting evolved in these species but not in those lacking the MER21C insertion. This illustrates the principle of LTR co-option as a means of evolving new gene regulatory mechanisms, specifically to achieve parent-of-origin allele specific expression (imprinting). Examples of this phenomenon have been described previously, but usually involve initiation of transcription during gametogenesis rather than post-fertilization, as in this work. The findings of this paper are therefore relevant to biologists studying imprinted genes or interested more generally in the evolution of gene regulatory mechanisms.

Strengths:

(1) The authors convincingly demonstrate the existence of GPR1-AS orthologs in specific mammalian lineages using high quality RNA-seq libraries collected from diverse mammalian species.

(2) The authors demonstrate imprinting of the ZDBF2 locus in rabbits and Rhesus macaques using allele-specific expression analysis. The transcription of GPR1-AS orthologs therefore correlates with imprinting of the ZDBF2 locus.

Weaknesses:

(1) Experimental evidence directly linking GPR1-AS transcription to ZDBF2 imprinting in rabbits and non-human primates is lacking. Consideration should be given to the challenges associated with studying non-model species and manipulating repeat sequences. Further, this mechanism is established in humans and mice, so the authors' model is arguably sufficiently supported merely by the existence of GPR1-AS orthologs in other mammalian lineages.

Reviewer #3 (Public review):

Kobayashi et al identify MER21C as a common promoter of GPR1-AS/Liz in Euarchontoglires, which establishes a somatic DMR that controls ZFDB2 imprinting. In mice, MER21C appears to have diverged significantly from its primate counterparts and is no longer annotated as such.

The authors used high-quality cross-species RNA-seq data to characterise GPR1-AS-like transcripts, which included generating new data in five different species. The association between MER21C/B elements and the promoter of GPR1-AS in most species is clear and convincing. The expression pattern of MER21C/B elements overall further supports their role in enabling correct temporal expression of GPR1-AS during embryonic development.

In the revised version of the manuscript the authors provided additional support for the common evolutionary origin of the GPR1-AS/Liz promoter between primates and rodents. They also showed a more extensive concordance between the presence of GPR1-AS-like transcripts and ZDBF2 imprinting.

Altogether, these findings robustly support the conclusions of the paper, shedding light into the events underlying the evolution of imprinting at the ZDBF2 locus.

Reviewer #1 (Public Review):

Summary:

Glaser et al present ExA-SPIM, a light-sheet microscope platform with large volumetric coverage (Field of view 85mm^2, working distance 35mm ), designed to image expanded mouse brains in their entirety. The authors also present an expansion method optimized for whole mouse brains, and an acquisition software suite. The microscope is employed in imaging an expanded mouse brain, the macaque motor cortex and human brain slices of white matter.

This is impressive work, and represents a leap over existing light-sheet microscopes. As an example, it offers a ~ fivefold higher resolution than mesoSPIM (https://mesospim.org/), a popular platform for imaging large cleared samples. Thus while this work is rooted in optical engineering, it manifests a huge step forward and has the potential to become an important tool in the neurosciences.

Strengths:

-ExA-SPIM features an exceptional combination of field of view, working distance, resolution and throughput.

-An expanded mouse brain can be acquired with only 15 tiles, lowering the burden on computational stitching. That the brain does not need to be mechanically sectioned is also seen as an important capability.

-The image data is compelling, and tracing of neurons has been performed. This demonstrates the potential of the microscope platform.

Review of the revised manuscript:

The authors have carefully addressed my previous concerns and suggestions.

Reviewer #2 (Public Review):

In this manuscript, Glaser et al. describe a new selective plane illumination microscope designed to image a large field of view that is optimized for expanded and cleared tissue samples. For the most part, the microscope design follows a standard formula that is common among many systems (e.g. Keller PJ et al Science 2008, Pitrone PG et al. Nature Methods 2013, Dean KM et al. Biophys J 2015, and Voigt FF et al. Nature Methods 2019). The primary conceptual and technical novelty is to use a detection objective from the metrology industry that has a large field of view and a large area camera. The authors characterize the system resolution, field curvature, and chromatic focal shift by measuring fluorescent beads in a hydrogel and then show example images of expanded samples from mouse, macaque, and human brain tissue.

Glaser et al. have responded to the reviewer comments by removing some of the overstated claims from the prior manuscript and editing portions of the manuscript text to enhance the clarity. Although the manuscript would be stronger if the authors had been able to provide data that justified the original high-impact claims from the initial publication (e.g. that the images could be used for robust and automated neuronal tracing across large volumes), the amended manuscript text now more closely matches the supporting data. As with the initial submission, I believe that the microscope design and characterization is a useful contribution to the field and the data are quite stunning.

Reviewer #1 (Public review):

In this paper Weber et al. investigate the role of 4 dopaminergic neurons of the Drosophila larva in mediating the association between an aversive high-salt stimulus and a neutral odor. The 4 DANs belong to the DL1 cluster and innervate non-overlapping compartments of the mushroom body, distinct from those involved in appetitive associative learning. Using specific driver lines for individual neurons, the authors show that activation of the DAN-g1 is sufficient to mimic an aversive memory and it is also necessary to form a high-salt memory of full strength, although optogenetic silencing of this neuron has only a partial phenotype. The authors use calcium imaging to show that the DAN-g1 is not the only DAN responding to salt. DAN-c1 and d1 also respond to salt, but they seem to play no role for the associative memory. DAN-f1, which does not respond to salt, is able to lead to the formation of a memory (if optogenetically activated), but it is not necessary for the salt-odor memory formation in normal conditions. However, when silenced together with DAN-g1, it enhances the memory deficit of DAN-g1. Overall, this work brings evidence of a complex interaction between DL1 DANs in both the encoding of salt signals and their teaching role in associative learning, with none of them being individually necessary and sufficient for both functions.

Overall, the manuscript contributes interesting results that are useful to understand the organization and function of the dopaminergic system. The behavioral role of the specific DANs is accessed using specific driver lines which allow to test their function individually and in pairs. Moreover, the authors perform calcium imaging to test whether DANs are activated by salt, a prerequisite for inducing a negative association to it. Proper genetic controls are carried across the manuscript.

Reviewer #2 (Public review):

Summary:

In this work the authors show that dopaminergic neurons (DANs) from the DL1 cluster in Drosophila larvae are required for the formation of aversive memories. DL1 DANs complement pPAM cluster neurons which are required for the formation of attractive memories. This shows the compartmentalized network organization of how an insect learning center (the mushroom body) encodes memory by integrating olfactory stimuli with aversive or attractive teaching signals. Interestingly, the authors found that the 4 main dopaminergic DL1 neurons act partially redundant, and that single cell ablation did not result in aversive memory defects. However, ablation or silencing of a specific DL1 subset (DAN-f1,g1) resulted in reduced salt aversion learning, which was specific to salt but no other aversive teaching stimuli tested. Importantly, activation of these DANs using an optogenetic approach was also sufficient to induce aversive learning in the presence of high salt. Together with the functional imaging of salt and fructose responses of the individual DANs and the implemented connectome analysis of sensory (and other) inputs to DL1/pPAM DANs this represents a very comprehensive study linking the structural, functional and behavioral role of DL1 DANs. This provides fundamental insight into the function of a simple yet efficiently organized learning center which displays highly conserved features of integrating teaching signals with other sensory cues via dopaminergic signaling.

Strengths:

This is a very careful, precise and meticulous study identifying the main larval DANs involved in aversive learning using high salt as a teaching signal. This is highly interesting because it allows to define the cellular substrates and pathways of aversive learning down to the single cell level in a system without much redundancy. It therefore sets the basis to conduct even more sophisticated experiments and together with the neat connectome analysis opens the possibility to unravel different sensory processing pathways within the DL1 cluster and integration with the higher order circuit elements (Kenyon cells and MBONs). The authors' claims are well substantiated by the data and balanced, putting their data in the appropriate context. The authors also implemented neat pathway analyses using the larval connectome data to its full advantage, thus providing network pathways that contribute towards explaining the obtained results.

Weaknesses:

Previous comments were fully addressed by the authors.

Reviewer #3 (Public review):

The study of Weber et al. provides a thorough investigation of the roles of four individual dopamine neurons for aversive associative learning in the Drosophila larva. They focus on the neurons of the DL-1 cluster which already have been shown to signal aversive teaching signals. But the authors go beyond the previous publications and test whether each of these dopamine neurons responds to salt or sugar, is necessary for learning about salt, bitter, or sugar, and is sufficient to induce a memory when optogenetically activated. In addition, previously published connectomic data is used to analyze the synaptic input to each of these dopamine neurons. The authors conclude that the aversive teaching signal induced by salt is distributed across the four DL-1 dopamine neurons, with two of them, DAN-f1 and DAN-g1, being particularly important. Overall, the experiments are well designed and performed, support the authors' conclusions, and deepen our understanding of the dopaminergic punishment system.

Strengths:

(1) This study provides, at least to my knowledge, the first in vivo imaging of larval dopamine neurons in response to tastants. Although the selection of tastants is limited, the results close an important gap in our understanding of the function of these neurons.

(2) The authors performed a large number of experiments to probe for the necessity of each individual dopamine neuron, as well as combinations of neurons, for associative learning. This includes two different training regimen (1 or 3 trials), three different tastants (salt, quinine and fructose) and two different effectors, one ablating the neuron, the other one acutely silencing it. This thorough work is highly commendable, and the results prove that it was worth it. The authors find that only one neuron, DAN-g1, is partially necessary for salt learning when acutely silenced, whereas a combination of two neurons, DAN-f1 and DAN-g1, are necessary for salt learning when either being ablated or silenced.

(3) In addition, the authors probe whether any of the DL-1 neurons is sufficient for inducing an aversive memory. They found this to be the case for two of the neurons, largely confirming previous results obtained by a different learning paradigm, parameters and effector.

(4) This study also takes into account connectomic data to analyze the sensory input that each of the dopamine neurons receives. This analysis provides a welcome addition to previous studies and helps to gain a more complete understanding. The authors find large differences in inputs that each neuron receives, and little overlap in input that the dopamine neurons of the "aversive" DL-1 cluster and the "appetitive" pPAM cluster seem to receive.

(5) Finally, the authors try to link all the gathered information in order to describe an updated working model of how aversive teaching signals are carried by dopamine neurons to the larva's memory center. This includes important comparisons both between two different aversive stimuli (salt and nociception) and between the larval and adult stages.

Reviewer #1 (Public review):

Summary:

In this study, Setogawa et al. employ an auditory discrimination task in freely moving rats, coupled with small animal imaging, electrophysiological recordings, and pharmacological inhibition/lesioning experiments to better understand the role of two striatal subregions: the anterior Dorsal Lateral Striatum (aDLS) and the posterior Ventrolateral Striatum (pVLS), during auditory discrimination learning. Attempting to better understand the contribution of different striatal subregions to sensory discrimination learning strikes me as a highly relevant and timely question, and the data presented in this study are certainly of major interest to the field. The authors have set up a robust behavioral task, systematically tackled the question about a striatal role in learning with multiple observational and manipulative techniques. Additionally, the structured approach the authors take by using neuroimaging to inform their pharmacological manipulation experiments and electrophysiological recordings is a strength.

Comments on revisions:

The authors have addressed some concerns raised in the initial review but some remain. In particular it is still unclear what conclusions can be drawn about task-related activity from scans that are performed 30 minutes after the behavioral task. I continue to think that a reorganization/analysis data according to event type would be useful and easier to interpret across the two brain areas, but the authors did not choose to do this. Finally, switching the cue-response association, I am convinced, would help to strengthen this study.

Reviewer #2 (Public review):

The study by Setogawa et al. aims to understand the role that different striatal subregions belonging to parallel brain circuits have in associative learning and discrimination learning (S-O-R and S-R tasks). Strengths of the study are the use of multiple methodologies to measure and manipulate brain activity in rats, from microPET imaging to excitotoxic lesions and multielectrode recordings across anterior dorsolateral (aDLS), posterior ventral lateral (pVLS)and dorsomedial (DMS) striatum.

The main conclusions are that the aDLS promotes stimulus-response association and suppresses response-outcome associations. The pVLS is engaged in the formation and maintenance of the stimulus-response association. There is a lot of work done and some interesting findings however, the manuscript can be improved by clarifying the presentation and reasoning. The inclusion of important controls will enhance the rigor of the data interpretation and conclusions.

Comments on revisions:

The authors have made important revisions to the manuscript and it has improved in clarity. They also added several figures in the rebuttal letter to answer questions by the reviewers. I would ask that these figures are also made public as part of the authors' response or if not, included in the manuscript.

Reviewer #1 (Public review):

Summary:

In Causal associations between plasma proteins and prostate cancer: a Proteome-Wide Mendelian Randomization, the authors present a manuscript which seeks to identify novel markers for prostate cancer through analysis of large biobank-based datasets and to extend this analysis to potential therapeutic targets for drugs. This is an area that is already extensively researched, but remains important, due to the high burden and mortality of prostate cancer globally.

Strengths:

The main strengths of the manuscript are the identification and use of large biobank data assets, which provide large numbers of cases and controls, essential for achieving statistical power. The databases used (deCODE, FinnGen, and the UK Biobank) allow for robust numbers of cases and controls. The analytical method chosen, Mendelian Randomization, is appropriate to the problem. Another strength is the integration of multi-omic datasets, here using protein data as well as GWAS sources to integrate genomic and proteomic data.

Weaknesses:

The main weaknesses of the manuscript relate to the following areas:

(1) The failure of the study to analyse the data in the context of other closely related conditions such as benign prostatic hyperplasia (BPH) or lower urinary tract symptoms (LUTS), which have some pathways and biomarkers in common, such as inflammatory pathways (including complement) and specific markers such as KLK3. As a consequence, it is not possible for readers to know whether the findings are specific to prostate cancer or whether they are generic to prostate dysfunction. Given the prevalence of prostate dysfunction (half of men reaching their sixth decade), the potential for false positives and overtreatment from non-specific biomarkers is a major problem, resulting in the evidence presented in this manuscript being weak. Other researchers have addressed this issue using the same data sources as presented here, for example, in this paper, looking at BPH in the UK Biobank population.<br /> https://www.nature.com/articles/s41467-018-06920-9

(2) There is no discussion of Gleason scores with regard to either biomarkers or therapies, and a general lack of discussion around indolent disease as compared with more aggressive variants. These are crucial issues with regard to the triage and identification of genomically aggressive localized prostate cancers. See, for example, the work set out in: https://doi.org/10.1038/nature20788 .

(3) An additional issue is that the field of PCa research is fast-moving. The manuscript cites ~80 references, but too few of these are from recent studies, and many important and relevant papers are not included. The manuscript would be much stronger if it compared and contrasted its findings with more recent studies of PCa biomarkers and targets, especially those concerned with multi-omics and those including BPH.

(4) The Methods section provides no information on how the Controls were selected. There is no Table providing cohort data to allow the reader to know whether there were differences in age, BMI, ethnic grouping, social status or deprivation, or smoking status, between the Cases and Controls. These types of data are generally recorded in Biobank data, so this sort of analysis should be possible, or if not, the authors' inability to construct an appropriately matched set of Controls should be discussed as a Limitation.

Assessing impact:

Because of the weaknesses of the approach identified above, without further additions to the manuscript, the likely impact of the work on the field is minimal. There is no significant utility of the methods and data to the community, because the data are pre-existing and are not newly introduced to the community in this work, and Mendelian randomization is a well-described approach in common use, and therefore, the assets and methods described in the manuscript are not novel. With regard to the authors achieving their aims, without assessing specificity and without setting their findings in the context of the latest literature, the authors (and readers) cannot know or assess whether the biomarkers identified or the druggable targets will be useful in the clinic.

In conclusion, adding additional context and analysis to the manuscript would both help readers interpret and understand the work and would also greatly enhance its significance. For example, the UK Biobank includes data on men with BPH / LUTS, as analysed in this paper, for example, https://doi.org/10.1038/s41467-018-06920-9. By extending this analysis to identify which biomarkers and druggable targets are specific to PCa, and which are generic to prostate dysfunction, the authors would substantially reduce the risks of diagnostic false positives. This would help to manage the risks of inappropriate treatment or overtreatment.

Reviewer #2 (Public review):

This is potentially interesting work, but the analyses are attempted in a rather scattergun way, with little evident critical thought. The structure of the work (Results before Methods) can work in some manuscripts, but it is not ideal here. The authors discuss results before we know anything about the underlying data that the results come from. It gives the impression that the authors regard data as a resource to be exploited, without really caring where the data comes from. The methods can provide meaningful insights if correctly used, but while I don't have reasons to doubt that the analyses were conducted correctly, findings are presented with little discussion or interpretation. No follow-up analyses are performed.

In summary, there are likely some gems here, but the whole manuscript is essentially the output from an analytic pipeline.

Taking the researchers aims in turn:

(1) Meta-GWAS - while combining two datasets together can provide additional insights, the contribution of this analysis above existing GWAS is not clear. The PRACTICAL consortium has already reported the GWAS of 70% of these data. What additional value does this analysis provide? (Likely some, but it's not clear from the text.) Also, the presentation of results is unclear - authors state that only 5 gene regions contained variants at p<5x10-8, but Figure 1 shows dozens of hits above 5x10-8. Also, the red line in Figure 1 (supposedly at 5x10-8) is misplaced.

(2) Cross-phenotype analysis. It is not really clear what this analysis is, or why it is done. What is the iCPAGdb? A database? A statistical method? Why would we want to know cross-phenotype associations? What even are these? It seems that the authors have taken data from an online resource and have written a paragraph based on this existing data with little added value.

(3) PW-MR. I can see the value of this work, but many details are unclear. Was this a two-sample MR using PRACTICAL + FinnGen data for the outcome? How many variants were used in key analyses? Again, the description of results is sparse and gives little added value.

(4) Colocalization - seems clear to me.

(5) Additional post-GWAS analyses (pathway + druggability) - again, the analyses seem to be performed appropriately, although little additional insight other than the reporting of output from the methods.

Minor points:

(6) The stated motivation for this work is "early detection". But causality isn't necessary for early detection. If the authors are interested in early detection, other analysis approaches are more appropriate.

(7) The authors state "193 proteins were associated with PCa risk", but they are looking at MR results - these analyses test for disease associations of genetically-predicted levels of proteins, not proteins themselves.

Strengths:

The data and methods used are state-of-the-art.

Weaknesses:

The reader will have to provide their own translational insight.

Reviewer #1 (Public review):

Summary:

This meta-analysis synthesized data from 79 studies across 22 African countries, encompassing over 27,000 breast cancer patients, to estimate 5-year survival rates. The pooled survival rate was 48%, with substantial regional variation, ranging from 64% in Northern Africa to 32% in Western Africa. Survival outcomes were associated with socioeconomic indicators such as education level, Human Development Index (HDI), and Socio-demographic Index (SDI). Although no significant differences in survival were observed between sexes, non-Black Africans had better outcomes. Despite global advances in cancer care, breast cancer survival in Africa has largely stagnated since the early 2010s, underscoring the need for improved healthcare infrastructure, early detection, and equitable access to treatment.

Strengths:

The study has several strengths. It features a comprehensive literature search, adherence to the PRISMA reporting guideline, and prospective registration on PROSPERO, including documentation of protocol deviations. The authors employed rigorous meta-analytic techniques, including subgroup analyses and meta-regression, allowing for a nuanced investigation of potential effect modifiers.

Weaknesses:

Analyses of crude 5-year survival rates are inherently difficult to interpret, particularly in the absence of key clinical variables such as stage at diagnosis or whether cancers were detected through screening programs. This omission raises concerns about lead time bias, where earlier diagnosis (e.g., via screening) may falsely appear to improve survival without affecting actual mortality. The higher survival seen in North Africa, for example, may reflect earlier diagnosis rather than improved prognosis or care quality. In this context, the age of the study population is another important aspect.

Relatedly, the representativeness of the included study populations is unclear. The data sources for individual studies - whether from national cancer registries or single tertiary hospitals -are not systematically reported. This distinction is crucial, as survival outcomes differ significantly between population-based and hospital-based cohorts. Without this contextual information, the generalizability of the findings is limited.

The meta-regression analyses further raise concerns. The authors use study-level covariates (e.g., national HDI, average years of schooling) to explain variation in survival, yet they do not acknowledge the risk of ecological bias. Inferring individual-level effects from aggregated data is methodologically flawed, and the authors' causal interpretation of these associations is inappropriate, especially given the potential for confounding by unmeasured variables at both the individual and study levels.

The assessment of publication bias is similarly problematic. While funnel plot asymmetry and a significant Egger's test are interpreted as evidence of bias, such methods are unreliable in meta-analyses of observational studies. Smaller studies may differ meaningfully from larger ones, not due to selective reporting, but because they may recruit patients from specialized tertiary centers where outcomes are poorer. The observed relationship between study size and survival may therefore reflect true differences in patient populations, not publication bias.

Despite claiming to search for gray literature via Google Scholar, no such studies appear in the PRISMA flowchart. This is a missed opportunity. Gray literature - especially reports from cancer registries - could have enhanced the quality and completeness of the data. While cancer registration systems are not available in all African countries, several do exist, and the authors should have made greater efforts to incorporate routine surveillance data where available. Mortality data from vital statistics systems, available in some countries, could also have provided useful context or validation.

The study's approach to quality assessment is limited. The scoring tool, adapted from Ssentongo et al., conflates completeness of reporting with risk of bias and fails to address key domains such as study population representativeness, selection bias, and lead time bias. Rather than calculating an overall quality score, the authors should have used a structured tool that evaluates risk of bias across defined domains-such as ROBINS-I, ROBINS-E, or tools developed for prevalence studies (e.g., Tonia et al., BMJ Mental Health, 2023). Cochrane guidance and the textbook by Egger, Higgins, and Davey Smith (DOI:10.1002/9781119099369) provide valuable resources for this purpose.

The cumulative meta-analysis is not particularly informative, considering the massive heterogeneity in survival rates. It would be more meaningful to stratify the analysis by calendar period. In general, with such important heterogeneity, the calculation of an overall estimate does not add much.

The authors spend quite some time discussing differences in survival between men and women and between the current and the 2018 estimates, despite the fact that the survival rates are similar, with widely overlapping confidence intervals. The use of a Z-test in this context is inappropriate as it ignores the heterogeneity between studies.

Minor point:

The terms retrospective and prospective are not particularly helpful - every longitudinal study of survival is retrospective. What the authors mean is whether or not the data were collected within a study designed to address this question, or whether existing data were used that were collected for another purpose. See also DOI: 10.1136/bmj.302.6771.249.

Reviewer #2 (Public review):

Summary:

The study provides an updated literature review and meta-analysis for the 5-year survival estimates in breast cancer patients across continental Africa. The findings reveal substantial disparities between regions and other factors, highlighting the disadvantaged areas in Africa and the urgent need to address these inequities across the continent.

Strengths:

The main strengths of this study include:<br /> (1) the thorough literature search with an increasing number of included studies that enhances result reliability;<br /> (2) standard and appropriate statistical methods with clear reporting;<br /> (3) a comprehensive discussion.

Overall, the paper is well-structured, clearly presented, and provides useful insights.

Weaknesses:

However, I have a few concerns that I would like the authors to address.

(1) The conclusion "A country-wise comparison with 2018 estimates suggests a declining survival tendency, with WHO AFRO countries reporting the poorest estimates among other WHO regions." appears to have been drawn from the comparisons across both different regions and different time periods, which is incorrect! As shown in Figure 8, survival in Africa has increased from below 30% (WHO AFRO 2017) to around 50% (AFRICA 2024, presumably the current study). Section 3.5 is confusing and headed in the wrong direction. The key message in Figure 8 is that the current survival estimate in Africa is still lower than that of other WHO regions from a few years ago, highlighting the urgent need to improve survival in Africa.

(2) The previous review by Ssentongo et al. classified countries into North Africa and sub-Saharan Africa (SSA), regions divided by the Sahara Desert. This classification is not only geographical-based, but also accounts for the significant differences in ethnicity, health system, and socioeconomic factors. North Africa (especially Egypt, Tunisia, Morocco) has better cancer registries, earlier detection, more treatment access, and therefore better survival outcomes (as shown in Figure 2). SSA tends to have worse outcomes, due to later-stage diagnosis, limited pathology, and access barriers. Given that the survival in women with breast cancer is among the lowest for several SSA countries, the study would benefit from an additional comparison between pooled estimates of North African and SSA, and comparisons with previous pooled estimates.

(3) The authors classified studies under the female group. Females constituted at least 80% of the sample population, and subgroup analysis revealed only a marginal discrepancy in survival rates between the two sexes. However, most of the breast cancer patients and related studies consist predominantly of females. Given the non-negligible differences in various aspects between females and males, sensitivity analyses restricted to studies among females (as in Figure 2-3) would be informative for future research in breast cancer patients.

(4) Stage at diagnosis and treatment are the strongest prognostic factors for breast cancer survival. Though data regarding these variables are not available for all studies, and it's complicated to compare or pool the results from different studies (as mentioned in the limitation), could the authors perform the regression analyses regarding early vs. late stages, and the percentage of treatment received? These two factors are too significant to overlook in studies on breast cancer survival.

(5) The authors reported that studies published before 2019 had a higher survival than those conducted from 2019 onwards, which could be misleading and requires further explanation. As the authors noted ─"the year of publication may not be a reliable measure of the effect in question"─ a better approach would be to use the year of inclusion, i.e., the year the studies were conducted.

(6) Northern and Western Africa both have the highest incidence of breast cancer in Africa, yet their 5-year survival estimates differ substantially. However, the authors have discussed the survival disparities without considering their similarly higher incidence rates. Could this disparity reflect different contributing factors, with the higher incidence rate in Northern Africa resulting from better screening programs (leading to more detections), while that in Western Africa stems from other epidemiological factors despite lower screening participation? Though the incidence rate is not the primary focus of this study, briefly exploring this dichotomy would enhance the discussion and provide valuable insights for readers.

Reviewer #1 (Public review):

Summary:

This study uses mesoscale simulations to investigate how membrane geometry regulates the multiphase organization of postsynaptic condensates. It reveals that dimensionality shifts the balance between specific and non-specific interactions, thereby reversing domain morphology observed in vitro versus in vivo.

Strengths:

The model is grounded in experimental binding affinities, reproduces key experimental observations in 3D and 2D contexts, and offers mechanistic insight into how geometry and molecular features drive phase behavior.

Weaknesses:

The model omits other synaptic components that may influence domain organization and does not extensively explore parameter sensitivity or broader physiological variability.

Reviewer #2 (Public review):

This is a timely and insightful study aiming to explore the general physical principles for the sub-compartmentalization--or lack thereof--in the phase separation processes underlying the assembly of postsynaptic densities (PSDs), especially the markedly different organizations in three-dimensional (3D) droplets on one hand and the two-dimensional (2D) condensates associated with a cellular membrane on the other. Simulation of a highly simplified model (one bead per protein domain) is carefully executed. Based on a thorough consideration of various control cases, the main conclusion regarding the trade-off between repulsive excluded volume interactions and attractive interactions among protein domains in determining the structures of 3D vs 2D model PSD condensates is quite convincing. The results in this manuscript are novel; however, as it stands, there is substantial room for improvement in the presentation of the background and the findings of this work. In particular, (i) conceptual connections with prior works should be better discussed, (ii) essential details of the model should be clarified, and (iii) the generality and limitations of the authors' approach should be better delineated. Specifically, the following items should be addressed (with the additional references mentioned below cited and discussed):

(1) Excluded volume effects are referred to throughout the text by various terms and descriptions such as "repulsive force according to the volume" (e.g., in the Introduction), "nonspecific volume interaction", and "volume effects" in this manuscript. This is somewhat curious and not conducive to clarity, because these terms have alternate or connotations of alternate meanings (e.g., in biomolecular modeling, repulsive interactions usually refer to those with longer spatial ranges, such as that between like charges). It will be much clearer if the authors simply refer to excluded volume interactions as excluded volume interactions (or effects).

(2) Inasmuch as the impact of excluded volume effects on subcompartmentalization of condensates ("multiple phases" in the authors' terminology), it has been demonstrated by both coarse-grained molecular dynamics and field-theoretic simulations that excluded volume is conducive to demixing of molecular species in condensates [Pal et al., Phys Rev E 103:042406 (2021); see especially Figures 4-5 of this reference]. This prior work bears directly on the authors' observation. Its relationship with the present work should be discussed.

(3) In the present model setup, activation of the CaMKII kinase affects only its binding to GluN2Bc. This approach is reasonable and leads to model predictions that are essentially consistent with the experiment. More broadly, however, do the authors expect activation of the CaMKII kinase to lead to phosphorylation of some of the molecular species involved with PSDs? This may be of interest since biomolecular condensates are known to be modulated by phosphorylation [Kim et al., Science 365:825-829 (2019); Lin et al, eLife 13:RP100284 (2025)].

(4) The forcefield for confinement of AMPAR/TARP and NMDAR/GluN2Bc to 2D should be specified in the main text. Have the authors explored the sensitivity of their 2D findings on the strength of this confinement?

(5) Some of the labels in Figure 1 are confusing. In Figure 1A, the structure labeled as AMPAR has the same shape as the structure labeled as TARP in Figure 1B, but TARP is labeled as one of the smaller structures (like small legs) in the lower part of AMPAR in Figure 1A. Does the TARP in Figure 1B correspond to the small structures in the lower part of AMPAR? If so, this should be specified (and better indicated graphically), and in that case, it would be better not to use the same structural drawing for the overall structure and a substructure. The same issue is seen for NMDAR in Figure 1A and GluN2Bc in Figure 1B.

(6) In addition to clarifying Figure 1, the authors should clarify the usage of AMPAR vs TARP and NMDAR vs GluN2Bc in other parts of the text as well.

(7) The physics of the authors' model will be much clearer if they provide an easily accessible graphical description of the relative interaction strengths between different domain-representing spheres (beads) in their model. For this purpose, a representation similar to that given by Feric et al., Cell 165:1686-1697 (2016) (especially Figure 6B in this reference) of the pairwise interactions among the beads in the authors' model should be provided as an additional main-text figure. Different interaction schemes corresponding to inactive and activated CAMKII should be given. In this way, the general principles (beyond the PSD system) governing 3D vs 2D multiple-component condensate organization can be made much more apparent.

(8) Can the authors' rationalization of the observed difference between 3D and 2D model PSD condensates be captured by an intuitive appreciation of the restriction on favorable interactions by steric hindrance and the reduction in interaction cooperativity in 2D vs 3D?

(9) In the authors' model, the propensity to form 2D condensates is quite weak. Is this prediction consistent with the experiment? Real PSDs do form 2D condensates around synapses.

(10) More theoretical context should be provided in the Introduction and/or Discussion by drawing connections to pertinent prior works on physical determinants of co-mixing and de-mixing in multiple-component condensates (e.g., amino acid sequence), such as Lin et al., New J Phys 19:115003 (2017) and Lin et al., Biochemistry 57:2499-2508 (2018).

(11) In the discussion of the physiological/neurological significance of PSD in the Introduction and/or Discussion, for general interest it is useful to point to a recently studied possible connection between the hydrostatic pressure-induced dissolution of model PSD and high-pressure neurological syndrome [Lin et al., Chem Eur J 26:11024-11031 (2020)].

(12) It is more accurate to use "perpendicular to the membrane" rather than "vertical" in the caption for Figure 3E and other such descriptions of the orientation of the CaMKII hexagonal plane in the text.

Reviewer #3 (Public review):

Summary:

In this work, Yamada, Brandani, and Takada have developed a mesoscopic model of the interacting proteins in the postsynaptic density. They have performed simulations, based on this model and using the software ReaDDy, to study the phase separation in this system in 2D (on the membrane) and 3D (in the bulk). They have carefully investigated the reasons behind different morphologies observed in each case, and have looked at differences in valency, specific/non-specific interactions, and interfacial tension.

Strengths:

The simulation model is developed very carefully, with strong reliance on binding valency and geometry, experimentally measured affinities, and physical considerations like the hydrodynamic radii. The presented analyses are also thorough, and great effort has been put into investigating different scenarios that might explain the observed effects.

Weaknesses:

The biggest weakness of the study, in my opinion, has to do with a lack of more in-depth physical insight about phase separation. For example, the authors express surprise about similar interactions between components resulting in different phase separation in 2D and 3D. This is not surprising at all, as in 3D, higher coordination numbers and more available volume translate to lower free energy, which easily explains phase separation. The role of entropy is also significantly missing from the analyses. When interaction strengths are small, entropic effects play major roles.

In the introduction, the authors present an oversimplified view of associative and segregative phase transitions based on the attractive and repulsive interactions, and I'm afraid that this view, in which all the observed morphologies should have clear pairwise enthalpic explanations, diffuses throughout the analysis. Meanwhile, I believe the authors correctly identify some relevant effects, where they consider specific/non-specific interactions, or when they investigate the reduced valency of CaMKII in the 2D system.

Also, I sense some haste in comparing the findings with experimental observations. For example, the authors mention that "For the current four component PSD system, the product of concentrations of each molecule in the dilute phase is in good agreement with that of the experimental concentrations (Table S2)." But the data used here is the dilute phase, which is the remnant of a system prepared at very high concentrations and allowed to phase separate. The errors reported in Table S2 already cast doubt on this comparison. Or while the 2D system is prepared via confining the particles to the vicinity of the membrane, the different diffusive behavior in the membrane, in contrast to the bulk (i.e., the Saffman-Delbrück model), is not considered. This would thus make it difficult to interpret the results of a coupled 2D/3D system and compare them to the actual system.

Reviewer #1 (Public review):

The authors present a substantial improvement to their existing tool, MorphoNet, intended to facilitate assessment of 3D+t cell segmentation and tracking results, and curation of high-quality analysis for scientific discovery and data sharing. These tools are provided through a user-friendly GUI, making them accessible to biologists who are not experienced coders. Further, the authors have re-developed this tool to be a locally installed piece of software instead of a web interface, making the analysis and rendering of large 3D+t datasets more computationally efficient. The authors evidence the value of this tool with a series of use cases, in which they apply different features of the software to existing datasets and show the improvement to the segmentation and tracking achieved.

While the computational tools packaged in this software are familiar to readers (e.g., cellpose), the novel contribution of this work is the focus on error correction. The MorphoNet 2.0 software helps users identify where their candidate segmentation and/or tracking may be incorrect. The authors then provide existing tools in a single user-friendly package, lowering the threshold of skill required for users to get maximal value from these existing tools. To help users apply these tools effectively, the authors introduce a number of unsupervised quality metrics that can be applied to a segmentation candidate to identify masks and regions where the segmentation results are noticeably different from the majority of the image.

This work is valuable to researchers who are working with cell microscopy data that requires high-quality segmentation and tracking, particularly if their data are 3D time-lapse and thus challenging to segment and assess. The MorphoNet 2.0 tool that the authors present is intended to make the iterative process of segmentation, quality assessment, and re-processing easier and more streamlined, combining commonly used tools into a single user interface.

One of the key contributions of the work is the unsupervised metrics that MorphoNet 2.0 offers for segmentation quality assessment. These metrics are used in the use cases to identify low-quality instances of segmentation in the provided datasets, so that they can be improved with plugins directly in MorphoNet 2.0. However, not enough consideration is given to demonstrating that optimizing these metrics leads to an improvement in segmentation quality. For example, in Use Case 1, the authors report their metrics of interest (Intensity offset, Intensity border variation, and Nuclei volume) for the uncurated silver truth, the partially curated and fully curated datasets, but this does not evidence an improvement in the results. Additional plotting of the distribution of these metrics on the Gold Truth data could help confirm that the distribution of these metrics now better matches the expected distribution.

Similarly, in Use Case 2, visual inspection leads us to believe that the segmentation generated by the Cellpose + Deli pipeline (shown in Figure 4d) is an improvement, but a direct comparison of agreement between segmented masks and masks in the published data (where the segmentations overlap) would further evidence this.

We would appreciate the authors addressing the risk of decreasing the quality of the segmentations by applying circular logic with their tool; MorphoNet 2.0 uses unsupervised metrics to identify masks that do not fit the typical distribution. A model such as StarDist can be trained on the "good" masks to generate more masks that match the most common type. This leads to a more homogeneous segmentation quality, without consideration for whether these metrics actually optimize the segmentation

In Use case 5, the authors include details that the errors were corrected by "264 MorphoNet plugin actions ... in 8 hours actions [sic]". The work would benefit from explaining whether this is 8 hours of human work, trying plugins and iteratively improving, or 8 hours of compute time to apply the selected plugins.

Reviewer #2 (Public review):

Summary:

This article presents Morphonet 2.0, a software designed to visualise and curate segmentations of 3D and 3D+t data. The authors demonstrate their capabilities on five published datasets, showcasing how even small segmentation errors can be automatically detected, easily assessed, and corrected by the user. This allows for more reliable ground truths, which will in turn be very much valuable for analysis and training deep learning models. Morphonet 2.0 offers intuitive 3D inspection and functionalities accessible to a non-coding audience, thereby broadening its impact.

Strengths:

The work proposed in this article is expected to be of great interest to the community by enabling easy visualisation and correction of complex 3D(+t) datasets. Moreover, the article is clear and well written, making MorphoNet more likely to be used. The goals are clearly defined, addressing an undeniable need in the bioimage analysis community. The authors use a diverse range of datasets, successfully demonstrating the versatility of the software.

We would also like to highlight the great effort that was made to clearly explain which type of computer configurations are necessary to run the different datasets and how to find the appropriate documentation according to your needs. The authors clearly carefully thought about these two important problems and came up with very satisfactory solutions.

Weaknesses:

There is still one concern: the quantification of the improvement of the segmentations in the use cases and, therefore, the quantification of the potential impact of the software. While it appears hard to quantify the quality of the correction, the proposed work would be significantly improved if such metrics could be provided.

The authors show some distributions of metrics before and after segmentations to highlight the changes. This is a great start, but there seem to be two shortcomings: first, the comparison and interpretation of the different distributions does not appear to be trivial. It is therefore difficult to judge the quality of the improvement from these. Maybe an explanation in the text of how to interpret the differences between the distributions could help. A second shortcoming is that the before/after metrics displayed are the metrics used to guide the correction, so, by design, the scores will improve, but does that accurately represent the improvement of the segmentation? It seems to be the case, but it would be nice to maybe have a better assessment of the improvement of the quality.

Reviewer #3 (Public review):

Summary:

A very thorough technical report of a new standalone, open-source software for microscopy image processing and analysis (MorphoNet 2.0), with a particular emphasis on automated segmentation and its curation to obtain accurate results even with very complex 3D stacks, including timelapse experiments.

Strengths:

The authors did a good job of explaining the advantages of MorphoNet 2.0, as compared to its previous web-based version and to other software with similar capabilities. What I particularly found more useful to actually envisage these claimed advantages is the five examples used to illustrate the power of the software (based on a combination of Python scripting and the 3D game engine Unity). These examples, from published research, are very varied in both types of information and image quality, and all have their complexities, making them inherently difficult to segment. I strongly recommend the readers to carefully watch the accompanying videos, which show (although not thoroughly) how the software is actually used in these examples.

Weaknesses:

Being a technical article, the only possible comments are on how methods are presented, which is generally adequate, as mentioned above. In this regard, and in spite of the presented examples (chosen by the authors, who clearly gave them a deep thought before showing them), the only way in which the presented software will prove valuable is through its use by as many researchers as possible. This is not a weakness per se, of course, but just what is usual in this sort of report. Hence, I encourage readers to download the software and give it time to test it on their own data (which I will also do myself).

In conclusion, I believe that this report is fundamental because it will be the major way of initially promoting the use of MorphoNet 2.0 by the objective public. The software itself holds the promise of being very impactful for the microscopists' community.

Reviewer #1 (Public review):

Summary:

This in situ cryo-ET workflow of selected plant structures provides several detailed strategies using plunge-freezing and the HPF waffle method and lift-out for notoriously difficult samples (compared to cell culture, yeast, and algae, which are far more prevalent in the literature).

Strengths:

A very difficult challenge whereby the authors demonstrate successful vitrification of selected plants/structures using waffle and lift-out approaches for cryoET. Because there are relatively few examples of multi-cellular plant cryo-ET in the literature, it is important for the scientific community to be motivated and have demonstrated strategies that it is achievable. This manuscript has a number of very helpful graphics and videos to help guide researchers who would be interested in undertaking that would help shorten the learning curve of admittedly tedious and complex workflows. This is a slow and tedious process, but you have to start somewhere, and I applaud the authors for sharing their experiences with others, and I expect will help other early adopters to come up to speed sooner.

Weaknesses:

While important, the specific specimen and cell-types selected that were successful (perhaps other plant specimen and tissues tried were unsuccessful and thus not reported) in this approach did not demonstrate success to broadly applicable to other much more prevalent and interesting and intensive areas plant biology and plant structures (some mentioned in more detail below).

This manuscript is essentially a protocol paper and in its paragraph form, and even with great graphics, will definitely be difficult to follow and reproduce for a non-expert. Also considering the use of 3 different FIB-SEM platforms and 2 different cryo-FLM platforms, I wonder if a master graphic of the full workflow(s) could be prepared as a supplementary document that walks through the major steps and points to the individual figures at the critical steps to make it more accessible to the broader readership.

Multiple times in the manuscript, important workflow details seemed to point to and be dependent on two "unpublished" manuscripts:

(1) Line 583, 755, 790, 847-848, (Poge et al., will soon be published as a protocol).

(2) Lines 140, 695, 716 (Capitanio et al., will soon be described in a manuscript).

It is not clear if/when these would be publicly available. It may be important to wait until these papers can be included in published form.

Reviewer #2 (Public review):

Summary:

Poge et al. present a workflow for studying plant tissue by combining high-pressure freezing, cryo-fluorescence microscopy, FIB milling, and cryo-electron tomography (cryo-ET). They tested various plant tissues, including Physcomitrium patens, Arabidopsis thaliana, and Limonium bicolor. The authors successfully produce thin lamellae suitable for cryo-ET studies. Using sub-tomogram averaging, they determined the Rubisco structure at subnanometer resolution, demonstrating the potential of this workflow for plant tissue studies.

Strengths:

This manuscript is likely the first to systematically apply FIB milling and cryo-ET to plant tissue samples. It provides a detailed methodological description, which is not only valuable for plant tissue studies but also adaptable to a broader range of biological tissue samples. The study compares the plunge freezing method with a high-pressure freezing method, demonstrating that high-pressure freezing can vitrify thick tissues while preserving their native state. Additionally, the authors explore two methods for plant tissue sample preparation, the "waffle" method and in-carrier high-pressure freezing combined with the "lift-out" approach. The "waffle" method is suitable for samples less than 25um, while the in-carrier high-pressure freezing method can process samples up to 100um.

Weaknesses:

The described workflow is very complicated and requires special expertise. The success rate of this workflow is not very high, particularly for high-pressure freezing and life-out technology. Further improvements are needed for automation and increasing throughput.

Reviewer #3 (Public review):

Summary:

The authors aimed to improve cryo-TEM workflows for plant cells. The authors present details on high-pressure-freezing protocols to vitrify, ion-mill, and image certain plant cell types.

Strengths:

Clear step-by-step outline on how to preserve and image cryo samples derived from plants.

Weaknesses:

A general current weakness of cryo-TEM is the problem of vitrifying cells that are embedded in tissues. The vast majority of cells in the plant body are currently not accessible to this technology. This is not a weakness of this specific manuscript but a general problem.

The manuscript is well organized and well written, and the discussion covers practically all questions I had while reading the results section. I only have a few comments, all of which I consider minor.

Reviewer #1 (Public review):

This is a well-designed and very interesting study examining the impact of imprecise feedback on outcomes in decision-making. I think this is an important addition to the literature, and the results here, which provide a computational account of several decision-making biases, are insightful and interesting.

I do not believe I have substantive concerns related to the actual results presented; my concerns are more related to the framing of some of the work. My main concern is regarding the assertion that the results prove that non-normative and non-Bayesian learning is taking place. I agree with the authors that their results demonstrate that people will make decisions in ways that demonstrate deviations from what would be optimal for maximizing reward in their task under a strict application of Bayes' rule. I also agree that they have built reinforcement learning models that do a good job of accounting for the observed behavior. However, the Bayesian models included are rather simple, per the author's descriptions, applications of Bayes' rule with either fixed or learned credibility for the feedback agents. In contrast, several versions of the RL models are used, each modified to account for different possible biases. However, more complex Bayes-based models exist, notably active inference, but even the hierarchical Gaussian filter. These formalisms are able to accommodate more complex behavior, such as affect and habits, which might make them more competitive with RL models. I think it is entirely fair to say that these results demonstrate deviations from an idealized and strict Bayesian context; however, the equivalence here of Bayesian and normative is, I think, misleading or at least requires better justification/explanation. This is because a great deal of work has been done to show that Bayes optimal models can generate behavior or other outcomes that are clearly not optimal to an observer within a given context (consider hallucinations for example) but which make sense in the context of how the model is constructed as well as the priors and desired states the model is given.

As such, I would recommend that the language be adjusted to carefully define what is meant by normative and Bayesian and to recognize that work that is clearly Bayesian could potentially still be competitive with RL models if implemented to model this task. An even better approach would be to directly use one of these more complex modelling approaches, such as active inference, as the comparator to the RL models, though I would understand if the authors would want this to be a subject for future work.

Abstract:

The abstract is lacking in some detail about the experiments done, but this may be a limitation of the required word count. If word count is not an issue, I would recommend adding details of the experiments done and the results.<br /> One comment is that there is an appeal to normative learning patterns, but this suggests that learning patterns have a fixed optimal nature, which may not be true in cases where the purpose of the learning (e.g. to confirm the feeling of safety of being in an in-group) may not be about learning accurately to maximize reward. This can be accommodated in a Bayesian framework by modelling priors and desired outcomes. As such, the central premise that biased learning is inherently non-normative or non-Bayesian, I think, would require more justification. This is true in the introduction as well.

Introduction:

As noted above, the conceptualization of Bayesian learning being equivalent to normative learning, I think requires further justification. Bayesian belief updating can be biased and non-optimal from an observer perspective, while being optimal within the agent doing the updating if the priors/desired outcomes are set up to advantage these "non-optimal" modes of decision making.

Results:

I wonder why the agent was presented before the choice, since the agent is only relevant to the feedback after the choice is made. I wonder if that might have induced any false association between the agent identity and the choice itself. This is by no means a critical point, but it would be interesting to get the authors' thoughts.

The finding that positive feedback increases learning is one that has been shown before and depends on valence, as the authors note. They expanded their reinforcement learning model to include valence, but they did not modify the Bayesian model in a similar manner. This lack of a valence or recency effect might also explain the failure of the Bayesian models in the preceding section, where the contrast effect is discussed. It is not unreasonable to imagine that if humans do employ Bayesian reasoning that this reasoning system has had parameters tuned based on the real world, where recency of information does matter; affect has also been shown to be incorporable into Bayesian information processing (see the work by Hesp on affective charge and the large body of work by Ryan Smith). It may be that the Bayesian models chosen here require further complexity to capture the situation, just like some of the biases required updates to the RL models. This complexity, rather than being arbitrary, may be well justified by decision-making in the real world.

The methods mention several symptom scales- it would be interesting to have the results of these and any interesting correlations noted. It is possible that some of the individual variability here could be related to these symptoms, which could introduce precision parameter changes in a Bayesian context and things like reward sensitivity changes in an RL context.

Discussion:

(For discussion, not a specific comment on this paper): One wonders also about participants' beliefs about the experiment or the intent of the experimenters. I have often had participants tell me they were trying to "figure out" a task or find patterns even when this was not part of the experiment. This is not specific to this paper, but it may be relevant in the future to try and model participant beliefs about the experiment especially in the context of disinformation, when they might be primed to try and "figure things out".

As a general comment, in the active inference literature, there has been discussion of state-dependent actions, or "habits", which are learned in order to help agents more rapidly make decisions, based on previous learning. It is also possible that what is being observed is that these habits are at play, and that they represent the cognitive biases. This is likely especially true given, as the authors note, the high cognitive load of the task. It is true that this would mean that full-force Bayesian inference is not being used in each trial, or in each experience an agent might have in the world, but this is likely adaptive on the longer timescale of things, considering resource requirements. I think in this case you could argue that we have a departure from "normative" learning, but that is not necessarily a departure from any possible Bayesian framework, since these biases could potentially be modified by the agent or eschewed in favor of more expensive full-on Bayesian learning when warranted.

Indeed, in their discussion on the strategy of amplifying credible news sources to drown out low-credibility sources, the authors hint at the possibility of longer-term strategies that may produce optimal outcomes in some contexts, but which were not necessarily appropriate to this task. As such, the performance on this task- and the consideration of true departure from Bayesian processing- should be considered in this wider context.

Another thing to consider is that Bayesian inference is occurring, but that priors present going in produce the biases, or these biases arise from another source, for example, factoring in epistemic value over rewards when the actual reward is not large. This again would be covered under an active inference approach, depending on how the priors are tuned. Indeed, given the benefit of social cohesion in an evolutionary perspective, some of these "biases" may be the result of adaptation. For example, it might be better to amplify people's good qualities and minimize their bad qualities in order to make it easier to interact with them; this entails a cost (in this case, not adequately learning from feedback and potentially losing out sometimes), but may fulfill a greater imperative (improved cooperation on things that matter). Given the right priors/desired states, this could still be a Bayes-optimal inference at a social level and, as such, may be ingrained as a habit that requires effort to break at the individual level during a task such as this.

The authors note that this task does not relate to "emotional engagement" or "deep, identity-related issues". While I agree that this is likely mostly true, it is also possible that just being told one is being lied to might elicit an emotional response that could bias responses, even if this is a weak response.

Reviewer #2 (Public review):

This valuable paper studies the problem of learning from feedback given by sources of varying credibility. The solid combination of experiment and computational modeling helps to pin down properties of learning, although some ambiguity remains in the interpretation of results.

Summary:

This paper studies the problem of learning from feedback given by sources of varying credibility. Two bandit-style experiments are conducted in which feedback is provided with uncertainty, but from known sources. Bayesian benchmarks are provided to assess normative facets of learning, and alternative credit assignment models are fit for comparison. Some aspects of normativity appear, in addition to deviations such as asymmetric updating from positive and negative outcomes.

Strengths:

The paper tackles an important topic, with a relatively clean cognitive perspective. The construction of the experiment enables the use of computational modeling. This helps to pinpoint quantitatively the properties of learning and formally evaluate their impact and importance. The analyses are generally sensible, and parameter recovery analyses help to provide some confidence in the model estimation and comparison.

Weaknesses:

(1) The approach in the paper overlaps somewhat with various papers, such as Diaconescu et al. (2014) and Schulz et al. (forthcoming), which also consider the Bayesian problem of learning and applying source credibility, in terms of theory and experiment. The authors should discuss how these papers are complementary, to better provide an integrative picture for readers.

Diaconescu, A. O., Mathys, C., Weber, L. A., Daunizeau, J., Kasper, L., Lomakina, E. I., ... & Stephan, K. E. (2014). Inferring the intentions of others by hierarchical Bayesian learning. PLoS computational biology, 10(9), e1003810.<br /> Schulz, L., Schulz, E., Bhui, R., & Dayan, P. Mechanisms of Mistrust: A Bayesian Account of Misinformation Learning. https://doi.org/10.31234/osf.io/8egxh

(2) It isn't completely clear what the "cross-fitting" procedure accomplishes. Can this be discussed further?

(3) The Credibility-CA model seems to fit the same as the free-credibility Bayesian model in the first experiment and barely better in the second experiment. Why not use a more standard model comparison metric like the Bayesian Information Criterion (BIC)? Even if there are advantages to the bootstrap method (which should be described if so), the BIC would help for comparability between papers.

(4) As suggested in the discussion, the updating based on random feedback could be due to the interleaving of trials. If one is used to learning from the source on most trials, the occasional random trial may be hard to resist updating from. The exact interleaving structure should also be clarified (I assume different sources were shown for each bandit pair). This would also relate to work on RL and working memory: Collins, A. G., & Frank, M. J. (2012). How much of reinforcement learning is working memory, not reinforcement learning? A behavioral, computational, and neurogenetic analysis. European Journal of Neuroscience, 35(7), 1024-1035.

(5) Why does the choice-repetition regression include "only trials for which the last same-pair trial featured the 3-star agent and in which the context trial featured a different bandit pair"? This could be stated more plainly.

(6) Why apply the "Truth-CA" model and not the Bayesian variant that it was motivated by?

(7) "Overall, the results from this study support the exact same conclusions (See SI section 1.2) but with one difference. In the discovery study, we found no evidence for learning based on 50%-credibility feedback when examining either the feedback effect on choice repetition or CA in the credibility-CA model (SI 1.2.3)" - this seems like a very salient difference, when the paper reports the feedback effect as a primary finding of interest, though I understand there remains a valence-based difference.

(8) "Participants were instructed that this feedback would be "a lie 50% of the time but were not explicitly told that this meant it was random and should therefore be disregarded." - I agree that this is a possible explanation for updating from the random source. It is a meaningful caveat.

(9) "Future studies should investigate conditions that enhance an ability to discard disinformation, such as providing explicit instructions to ignore misleading feedback, manipulations that increase the time available for evaluating information, or interventions that strengthen source memory." - there is work on some of this in the misinformation literature that should be cited, such as the "continued influence effect". For example: Johnson, H. M., & Seifert, C. M. (1994). Sources of the continued influence effect: When misinformation in memory affects later inferences. Journal of experimental psychology: Learning, memory, and cognition, 20(6), 1420.

(10) Are the authors arguing that choice-confirmation bias may be at play? Work on choice-confirmation bias generally includes counterfactual feedback, which is not present here.

Reviewer #3 (Public review):

Summary

This paper investigates how disinformation affects reward learning processes in the context of a two-armed bandit task, where feedback is provided by agents with varying reliability (with lying probability explicitly instructed). They find that people learn more from credible sources, but also deviate systematically from optimal Bayesian learning: They learned from uninformative random feedback, learned more from positive feedback, and updated too quickly from fully credible feedback (especially following low-credibility feedback). Overall, this study highlights how misinformation could distort basic reward learning processes, without appeal to higher-order social constructs like identity.

Strengths

(1) The experimental design is simple and well-controlled; in particular, it isolates basic learning processes by abstracting away from social context.

(2) Modeling and statistics meet or exceed the standards of rigor.

(3) Limitations are acknowledged where appropriate, especially those regarding external validity.

(4) The comparison model, Bayes with biased credibility estimates, is strong; deviations are much more compelling than e.g., a purely optimal model.

(5) The conclusions are interesting, in particular the finding that positivity bias is stronger when learning from less reliable feedback (although I am somewhat uncertain about the validity of this conclusion)

Weaknesses

(1) Absolute or relative positivity bias?

In my view, the biggest weakness in the paper is that the conclusion of greater positivity bias for lower credible feedback (Figure 5) hinges on the specific way in which positivity bias is defined. Specifically, we only see the effect when normalizing the difference in sensitivity to positive vs. negative feedback by the sum. I appreciate that the authors present both and add the caveat whenever they mention the conclusion (with the crucial exception of the abstract). However, what we really need here is an argument that the relative definition is the *right* way to define asymmetry....

Unfortunately, my intuition is that the absolute difference is a better measure. I understand that the relative version is common in the RL literature; however previous studies have used standard TD models, whereas the current model updates based on the raw reward. The role of the CA parameter is thus importantly different from a traditional learning rate - in particular, it's more like a logistic regression coefficient (as described below) because it scales the feedback but *not* the decay. Under this interpretation, a difference in positivity bias across credibility conditions corresponds to a three-way interaction between the exponentially weighted sum of previous feedback of a given type (e.g., positive from the 75% credible agent), feedback positivity, and condition (dummy coded). This interaction corresponds to the non-normalized, absolute difference.

Importantly, I'm not terribly confident in this argument, but it does suggest that we need a compelling argument for the relative definition.

(2) Positivity bias or perseveration?

A key challenge in interpreting many of the results is dissociating perseveration from other learning biases. In particular, a positivity bias (Figure 5) and perseveration will both predict a stronger correlation between positive feedback and future choice. Crucially, the authors do include a perseveration term, so one would hope that perseveration effects have been controlled for and that the CA parameters reflect true positivity biases. However, with finite data, we cannot be sure that the variance will be correctly allocated to each parameter (c.f. collinearity in regressions). The fact that CA- is fit to be negative for many participants (a pattern shown more strongly in the discovery study) is suggestive that this might be happening. A priori, the idea that you would ever increase your value estimate after negative feedback is highly implausible, which suggests that the parameter might be capturing variance besides that it is intended to capture.

The best way to resolve this uncertainty would involve running a new study in which feedback was sometimes provided in the absence of a choice - this would isolate positivity bias. Short of that, perhaps one could fit a version of the Bayesian model that also includes perseveration. If the authors can show that this model cannot capture the pattern in Figure 5, that would be fairly convincing.

(3) Veracity detection or positivity bias?

The "True feedback elicits greater learning" effect (Figure 6) may be simply a re-description of the positivity bias shown in Figure 5. This figure shows that people have higher CA for trials where the feedback was in fact accurate. But, assuming that people tend to choose more rewarding options, true-feedback cases will tend to also be positive-feedback cases. Accordingly, a positivity bias would yield this effect, even if people are not at all sensitive to trial-level feedback veracity. Of course, the reverse logic also applies, such that the "positivity bias" could actually reflect discounting of feedback that is less likely to be true. This idea has been proposed before as an explanation for confirmation bias (see Pilgrim et al, 2024 https://doi.org/10.1016/j.cognition.2023.105693 and much previous work cited therein). The authors should discuss the ambiguity between the "positivity bias" and "true feedback" effects within the context of this literature....

The authors get close to this in the discussion, but they characterize their results as differing from the predictions of rational models, the opposite of my intuition. They write:

Alternative "informational" (motivation-independent) accounts of positivity and confirmation bias predict a contrasting trend (i.e., reduced bias in low- and medium credibility conditions) because in these contexts it is more ambiguous whether feedback confirms one's choice or outcome expectations, as compared to a full-credibility condition.

I don't follow the reasoning here at all. It seems to me that the possibility for bias will increase with ambiguity (or perhaps will be maximal at intermediate levels). In the extreme case, when feedback is fully reliable, it is impossible to rationally discount it (illustrated in Figure 6A). The authors should clarify their argument or revise their conclusion here.

(4) Disinformation or less information?

Zooming out, from a computational/functional perspective, the reliability of feedback is very similar to reward stochasticity (the difference is that reward stochasticity decreases the importance/value of learning in addition to its difficulty). I imagine that many of the effects reported here would be reproduced in that setting. To my surprise, I couldn't quickly find a study asking that precise question, but if the authors know of such work, it would be very useful to draw comparisons. To put a finer point on it, this study does not isolate which (if any) of these effects are specific to *disinformation*, rather than simply _less information._ I don't think the authors need to rigorously address this in the current study, but it would be a helpful discussion point.

(5) Over-reliance on analyzing model parameters

Most of the results rely on interpreting model parameters, specifically, the "credit assignment" (CA) parameter. Exacerbating this, many key conclusions rest on a comparison of the CA parameters fit to human data vs. those fit to simulations from a Bayesian model. I've never seen anything like this, and the authors don't justify or even motivate this analysis choice. As a general rule, analyses of model parameters are less convincing than behavioral results because they inevitably depend on arbitrary modeling assumptions that cannot be fully supported. I imagine that most or even all of the results presented here would have behavioral analogues. The paper would benefit greatly from the inclusion of such results. It would also be helpful to provide a description of the model in the main text that makes it very clear what exactly the CA parameter is capturing (see next point).

(6) RL or regression?

I was initially very confused by the "RL" model because it doesn't update based on the TD error. Consequently, the "Q values" can go beyond the range of possible reward (SI Figure 5). These values are therefore *not* Q values, which are defined as expectations of future reward ("action values"). Instead, they reflect choice propensities, which are sometimes notated $h$ in the RL literature. This misuse of notation is unfortunately quite common in psychology, so I won't ask the authors to change the variable. However, they should clarify when introducing the model that the Q values are not action values in the technical sense. If there is precedent for this update rule, it should be cited.

Although the change is subtle, it suggests a very different interpretation of the model.

Specifically, I think the "RL model" is better understood as a sophisticated logistic regression, rather than a model of value learning. Ignoring the decay term, the CA term is simply the change in log odds of repeating the just-taken action in future trials (the change is negated for negative feedback). The PERS term is the same, but ignoring feedback. The decay captures that the effect of each trial on future choices diminishes with time. Importantly, however, we can re-parameterize the model such that the choice at each trial is a logistic regression where the independent variables are an exponentially decaying sum of feedback of each type (e.g., positive-cred50, positive-cred75, ... negative-cred100). The CA parameters are simply coefficients in this logistic regression.

Critically, this is not meant to "deflate" the model. Instead, it clarifies that the CA parameter is actually not such an assumption-laden model estimate. It is really quite similar to a regression coefficient, something that is usually considered "model agnostic". It also recasts the non-standard "cross-fitting" approach as a very standard comparison of regression coefficients for model simulations vs. human data. Finally, using different CA parameters for true vs false feedback is no longer a strange and implausible model assumption; it's just another (perfectly valid) regression. This may be a personal thing, but after adopting this view, I found all the results much easier to understand.

Reviewer #1 (Public review):

The authors identified five complex amacrine cell (CAM) subtypes based on their morphology and synaptic connectivity. It's suggested that the differences in structure may be directly correlated with different functional roles. The authors also describe synaptic compartmentalization in the SFL tract relating to three types of CAM input regions, again implying a specialized role for these cells. The authors also identified neural progenitor cells, which suggests that the octopus's vertical lobe can undergo neurogenesis throughout its life.

The work presented here is valuable and convincing. Below are some suggestions the authors may wish to incorporate:

a) Quantitative measurements to define the CAM subtypes<br /> I think the categorization of the CAMs into five subtypes is convincing, however, I wonder how easily these categories could be identified by other researchers. Would it be possible for the authors to include additional quantitative measurements of these cell types to make their categorization less qualitative and more quantitative? For example, density, volume, and orientation of their dendritic fields?

b) The definition of the neuritic backbone is included in the methods, but I found the term confusing when I first encountered it in the results, so I would suggest adding the definition to the results too.

c) The authors wrote, 'Note that given the pronounced difference in diameters between the neuritic backbones (208.27 +/-87.95 nm) and axons (121.55 +/- 21.28 nm)'. What figure is this in?

d) I am slightly confused about how the authors decided on the specific cubes to reflect the different synaptic compartments in the SFL tract. Is this organisation arranged/repeated vertically or horizontally throughout the SFL tract? The location of the cubes looks to me to be chosen at random, so more information here would be helpful.

e) In Figure 2, could the authors plot the number of synapses per cube to make the result clearer, so that cube 1 has the lowest synaptic density and cube 2 has the highest?

f) SAMs are ACh and excitatory<br /> The authors refer to SAMs as excitatory cholinergic. They should provide more detailed explanations/citations to back up this claim. Could SAMs be synthesizing any other neurotransmitters? Could there be a subpopulation of inhibitory SAMs?

g) CAMs are GABA and inhibitory

The 5 subtypes of CAMs described here have never been directly confirmed to be GABAergic. Could CAMs be synthesizing any other neurotransmitters? Could a subpopulation of CAMs be excitatory? I believe the authors should make this clearer to readers when referring to CAMs, perhaps by saying, 'hypothesized to be inhibitory neurons', or 'putative inhibitory neurons'.

h) Fast neurotransmitters and neuromodulators<br /> The authors refer to neuromodulatory connections in their summary in Figure 4, however, cephalopod receptors have yet to be extensively functionally characterized, therefore, the role different molecules play as neurotransmitters or neuromodulators is not yet known. For example, many invertebrates are known to have functional diversity in their receptors: C. elegans has both excitatory and inhibitory receptors for a range of neurotransmitters, anionic ACh- and glutamate-gated channels, and cationic peptide-gated channels have also been identified in some molluscs. So, probably the authors should be cautious in speculating about how a particular transmitter/modulator acts in the octopus brain.

i) In the methods, the authors refer to "an adult Octopus", what age and size was it? I also know this is Octopus vulgaris, but it would be good to specify it here.

j) A general comment about all figures. All panels should have a letter associated with them to make it easier to refer to them in the text. For example, in Figure 4, please also add letters to the main schematic, the CAM subtypes, and the VL wiring diagram. In addition, D and E are missing boxes on the main schematic. It's also not immediately obvious that A-E are zooms of the larger schematic; perhaps this could be made clearer with colours or arrows. Please also add names to the CAM subtypes.

a) Typo: 'Additionally, the unique characteristics of LTP in the octopus VL, such as its reliance on a NO-dependent mechanism, independent of de novo protein synthesis, persistent activation of (Turchetti-Maia et al., 2018).'

Reviewer #2 (Public review):

Summary:

The paper examines the diversity of complex amacrine neurons in the ventral lobe of the adult octopus brain, a structure involved in learning and memory. The work builds on a recent paper by the authors that described the connectivity of the much larger population of simple amacrine (SAM) interneurons from the same pioneering EM volume.

Strengths:

While the EM volume only provides a snapshot of a tiny fraction of an adult octopus' brain, the authors can make specific conclusions and formulate precise hypotheses about neuron function, synaptic pathways, and developmental trajectories. One example is the reconstruction of a putative maturation sequence for the SAM neuronal lineage, based on the correlation of soma position and the number of synapses, uncovering a plausible developmental sequence of cell morphologies, with interesting parallels to vertebrate neurogenesis.

Weaknesses:

The weakness of the study is that it is examining a relatively small volume (260 × 390 × 27 µm), and several neurons are only incompletely reconstructed. It also remains unclear approximately how many neurons remain to be reconstructed from this volume.

To improve the presentation, the authors should consider showing videos with the volumetric reconstructions of the different types with their partners/synapses and their relation to the SFL track and SAMs. Such videos would help the reader to appreciate the morphological differences between the cell types. The authors could also consider carrying out further morphological analyses to strengthen their cell-type classification, including Sholl value, radial density of input and output synapses, the number of branch nodes, and similar measures.

Reviewer #3 (Public review):

(1) The authors described "the excitatory glutamatergic SFL axons and cholinergic SAM inputs". However, the evidence of their transmitter specificity has not been provided. Compelling evidence was neither provided nor discussed in the context of the study.

(2) Specific interference for inhibitory or excitatory synapses based on EM or other studies must be detailed and elaborated

(3) Different local microcircuits (submodules) referred to in the text should be better described and more specifically defined.

(4) I would recommend incorporating a more detailed description of synapses and, especially, synaptic vesicles, clarifying their diversity and similarity across cell subtypes. Are there any differences between cholinergic and glutamatergic synaptic vesicles, postsynaptic densities, or other features...? It would be good, if possible, to explicitly clarify: how many vesicles per different types of synapses? How many synapses per neuron of different types? How many inputs and outputs per a given neuron?

(5) Authors discuss retrograde messengers like NO? Is there any identifiable morphological type of neuron(s) or synapses that might be nitrergic?

(6) It would be good to provide separate illustrations showing the detailed organization of any glial cell or different types of glial cells they identified in this study. Authors mainly discuss glial processes but refer to "recognized glial types, such as radial glia and astrocyte-like glia" without specific illustrations, which can be deciphered from their EM data. What are vesicular organizations within different types of glial cells?

(7) The authors also discuss "supervising inputs of inhibitory (pain) and neuromodulatory (supervising) signals", without any details. It would be important to provide these details in the discussion. Specifically, I suggest incorporating comments about differences/similarities of transmitters and morphology between pain and modulatory pathways/signaling/circuits.

Reviewer #4 (Public review):

Summary:

The authors present a follow-up to their initial publication of a volume EM reconstruction of a part of the Octopus vulgaris vertical lobe (VL) (Bidel, Meirovitch et al., eLife 2023). In their previous study, they presented a swath of novel observations pertaining to the neuron types making up the VL and their synaptic connectivity. Here, the authors present an extension of those findings in which they (1) demonstrate that the Complex Amacrine cells (CAMs), which they identified previously, can be grouped into at least 5 distinct subclasses; (2) show that there appears to be distinct compartments in the SFL tract that contain specific synapse types; and (3) present morphological evidence that there may be a neurogenic niche in the VL. The findings are intriguing, advance our understanding of memory circuitry in octopus and across the phylogenetic tree, and open new avenues for deeper investigation.

Strengths:

A deeper dissection of the morphologies of CAMs and their distinct complements of synapse types is valuable. The identification of multiple categories of CAMs makes it clearer how the very simple SFL-to-SAM connectivity is likely enriched by a population of diverse interneurons.

The observation that synapse types may be compartmentalized in the superior frontal lobe tract is an intriguing one, and invites more extensive segmentation and future anatomical studies to further characterize the precise architecture of these compartments.

Finally, the evidence of the possibility of a neurogenic niche in the VL is exciting as it suggests that ongoing neurogenesis may be a common feature of memory circuitry, perhaps contributing to keeping the representation space of the circuit flexible and adequately sparse.

Weaknesses:

A key weakness is the reconstruction and grouping of the CAMs:

(1) CAMs are relatively few in number compared to SAMs, and as such, only 53 are reconstructed in this study. Of those 53 cells, 18 were not classified into one of the 5 categories the authors designate, begging the question of how robust those categories are.

(2) Related to (1), in Figure 1B, the proportions given in the bar graph are given cumulatively across the entire population of each category. The proportions should be presented as means within each category to adequately capture the variability of the small sample sizes.

(3) While the xy dimensions of the serial section EM volume are adequate to capture relatively whole cells and neuronal arbors, the volume is only 27µm thick. Thus, many neurite branches are likely truncated in the z-dimension. This may have contributed to ~1/3 of CAMs eluding categorization. However, it is hard to estimate the effect this may have had without knowing the extent of the truncation. It may be worth the authors' time to count the proportion of CAM neurites that are cut off at the edges of the volume.

(4) The authors state that CAMs appear to have axons and dendrites based on neurite widths. This is an interesting finding, given that amacrine cells are generally thought to possess only one type of neurite, which both send and receive synaptic potentials, and therefore deserves more attention. Is the distribution of neurite widths indeed bimodally distributed? Can the axons and dendrites be differentiated by examining the presence and absence of synaptic vesicle pools, respectively?

In Figure 2, the compartmentalization of synapse types is intriguing; however, due to the 3D nature of the data, it is difficult to appreciate clearly from the panels presented. This is particularly true for the suggestion that glia may be forming a barrier around these compartments. This could be rectified by providing Neuroglancer links for these specific reconstructions (neurites, synapses, and glia).

Lastly, although the identification of a putative neurogenic niche is tantalizing, morphological data alone is only an initial hint. Although the chances are slim, it would be more convincing if the authors could identify any actively dividing cells in the proposed niche. More likely, further work, for instance, immunofluorescence, which the lab has previously shown to be viable in octopus, will be needed to add weight to the claim.

Reviewer #1 (Public review):

Summary:

Parise presents another instantiation of the Multisensory Correlation Detector model that can now accept stimulus-level inputs. This is a valuable development as it removes researcher involvement in the characterization/labeling of features and allows analysis of complex stimuli with a high degree of nuance that was previously unconsidered (i.e., spatial/spectral distributions across time). The author demonstrates the power of the model by fitting data from dozens of previous experiments, including multiple species, tasks, behavioral modalities, and pharmacological interventions.

Strengths:

One of the model's biggest strengths, in my opinion, is its ability to extract complex spatiotemporal co-relationships from multisensory stimuli. These relationships have typically been manually computed or assigned based on stimulus condition and often distilled to a single dimension or even a single number (e.g., "-50 ms asynchrony"). Thus, many models of multisensory integration depend heavily on human preprocessing of stimuli, and these models miss out on complex dynamics of stimuli; the lead modality distribution apparent in Figures 3b and c is provocative. I can imagine the model revealing interesting characteristics of the facial distribution of correlation during continuous audiovisual speech that have up to this point been largely described as "present" and almost solely focused on the lip area.

Another aspect that makes the MCD stand out among other models is the biological inspiration and generalizability across domains. The model was developed to describe a separate process - motion perception - and in a much simpler organism - Drosophila. It could then describe a very basic neural computation that has been conserved across phylogeny (which is further demonstrated in the ability to predict rat, primate, and human data) and brain area. This aspect makes the model likely able to account for much more than what has already been demonstrated with only a few tweaks akin to the modifications described in this and previous articles from Parise.

What allows this potential is that, as Parise and colleagues have demonstrated in those papers since our (re)introduction of the model in 2016, the MCD model is modular - both in its ability to interface with different inputs/outputs and its ability to chain MCD units in a way that can analyze spatial, spectral, or any other arbitrary dimension of a stimulus. This fact leaves wide open the possibilities for types of data, stimuli, and tasks a simplistic, neutrally inspired model can account for.

And so it's unsurprising (but impressive!) that Parise has demonstrated the model's ability here to account for such a wide range of empirical data from numerous tasks (synchrony/temporal order judgement, localization, detection, etc.) and behavior types (manual/saccade responses, gaze, etc.) using only the stimulus and a few free parameters. This ability is another of the model's main strengths that I think deserves some emphasis: it represents a kind of validation of those experiments, especially in the context of cross-experiment predictions (but see some criticism of that below).

Finally, what is perhaps most impressive to me is that the MCD (and the accompanying decision model) does all this with very few (sometimes zero) free parameters. This highlights the utility of the model and the plausibility of its underlying architecture, but also helps to prevent extreme overfitting if fit correctly (but see a related concern below).

Weaknesses:

There is an insufficient level of detail in the methods about model fitting. As a result, it's unclear what data the models were fitted and validated on. Were models fit individually or on average group data? Each condition separately? Is the model predictive of unseen data? Was the model cross-validated? Relatedly, the manuscript mentions a randomization test, but the shuffled data produces model responses that are still highly correlated to behavior despite shuffling. Could it be that any stimulus that varies in AV onset asynchrony can produce a psychometric curve that matches any other task with asynchrony judgements baked into the task? Does this mean all SJ or TOJ tasks produce correlated psychometric curves? Or more generally, is Pearson's correlation insensitive to subtle changes here, considering psychometric curves are typically sigmoidal? Curves can be non-overlapping and still highly correlated if one is, for example, scaled differently. Would an error term such as mean-squared or root mean-squared error be more sensitive to subtle changes in psychometric curves? Alternatively, perhaps if the models aren't cross-validated, the high correlation values are due to overfitting?

While the model boasts incredible versatility across tasks and stimulus configurations, fitting behavioral data well doesn't mean we've captured the underlying neural processes, and thus, we need to be careful when interpreting results. For example, the model produces temporal parameters fitting rat behavior that are 4x faster than when fitting human data. This difference in slope and a difference at the tails were interpreted as differences in perceptual sensitivity related to general processing speeds of the rat, presumably related to brain/body size differences. While rats no doubt have these differences in neural processing speed/integration windows, it seems reasonable that a lot of the differences in human and rat psychometric functions could be explained by the (over)training and motivation of rats to perform on every trial for a reward - increasing attention/sensitivity (slope) - and a tendency to make mistakes (compression evident at the tails). Was there an attempt to fit these data with a lapse parameter built into the decisional model as was done in Equation 21? Likewise, the fitted parameters for the pharmacological manipulations during the SJ task indicated differences in the decisional (but not the perceptual) process and the article makes the claim that "all pharmacologically-induced changes in audiovisual time perception" can be attributed to decisional processes "with no need to postulate changes in low-level temporal processing." However, those papers discuss actual sensory effects of pharmacological manipulation, with one specifically reporting changes to response timing. Moreover, and again contrary to the conclusions drawn from model fits to those data, both papers also report a change in psychometric slope/JND in the TOJ task after pharmacological manipulation, which would presumably be reflected in changes to the perceptual (but not the decisional) parameters.

The case for the utility of a stimulus-computable model is convincing (as I mentioned above), but its framing as mission-critical for understanding multisensory perception is overstated, I think. The line for what is "stimulus computable" is arbitrary and doesn't seem to be followed in the paper. A strict definition might realistically require inputs to be, e.g., the patterns of light and sound waves available to our eyes and ears, while an even more strict definition might (unrealistically) require those stimuli to be physically present and transduced by the model. A reasonable looser definition might allow an "abstract and low-dimensional representation of the stimulus, such as the stimulus envelope (which was used in the paper), to be an input. Ultimately, some preprocessing of a stimulus does not necessarily confound interpretations about (multi)sensory perception. And on the flip side, the stimulus-computable aspect doesn't necessarily give the model supreme insight into perception. For example, the MCD model was "confused" by the stimuli used in our 2018 paper (Nidiffer et al., 2018; Parise & Ernst, 2025). In each of our stimuli (including catch trials), the onset and offset drove strong AV temporal correlations across all stimulus conditions (including catch trials), but were irrelevant to participants performing an amplitude modulation detection task. The to-be-detected amplitude modulations, set at individual thresholds, were not a salient aspect of the physical stimulus, and thus only marginally affected stimulus correlations. The model was of course, able to fit our data by "ignoring" the on/offsets (i.e., requiring human intervention), again highlighting that the model is tapping into a very basic and ubiquitous computational principle of (multi)sensory perception. But it does reveal a limitation of such a stimulus-computable model: that it is (so far) strictly bottom-up.

The manuscript rightly chooses to focus a lot of the work on speech, fitting the MCD model to predict behavioral responses to speech. The range of findings from AV speech experiments that the MCD can account for is very convincing. Given the provided context that speech is "often claimed to be processed via dedicated mechanisms in the brain," a statement claiming a "first end-to-end account of multisensory perception," and findings that the MCD model can account for speech behaviors, it seems the reader is meant to infer that energetic correlation detection is a complete account of speech perception. I think this conclusion misses some facets of AV speech perception, such as integration of higher-order, non-redundant/correlated speech features (Campbell, 2008) and also the existence of top-down and predictive processing that aren't (yet!) explained by MCD. For example, one important benefit of AV speech is interactions on linguistic processes - how complementary sensitivity to articulatory features in the auditory and visual systems (Summerfield, 1987) allow constraint of linguistic processes (Peelle & Sommers, 2015; Tye-Murray et al., 2007).

References

Campbell, R. (2008). The processing of audio-visual speech: empirical and neural bases. Philosophical Transactions of the Royal Society B: Biological Sciences, 363(1493), 1001-1010. https://doi.org/10.1098/rstb.2007.2155<br /> Nidiffer, A. R., Diederich, A., Ramachandran, R., & Wallace, M. T. (2018). Multisensory perception reflects individual differences in processing temporal correlations. Scientific Reports 2018 8:1, 8(1), 1-15. https://doi.org/10.1038/s41598-018-32673-y<br /> Parise, C. V, & Ernst, M. O. (2025). Multisensory integration operates on correlated input from unimodal transient channels. ELife, 12. https://doi.org/10.7554/ELIFE.90841<br /> Peelle, J. E., & Sommers, M. S. (2015). Prediction and constraint in audiovisual speech perception. Cortex, 68, 169-181. https://doi.org/10.1016/j.cortex.2015.03.006<br /> Summerfield, Q. (1987). Some preliminaries to a comprehensive account of audio-visual speech perception. In B. Dodd & R. Campbell (Eds.), Hearing by Eye: The Psychology of Lip-Reading (pp. 3-51). Lawrence Erlbaum Associates.<br /> Tye-Murray, N., Sommers, M., & Spehar, B. (2007). Auditory and Visual Lexical Neighborhoods in Audiovisual Speech Perception: Trends in Amplification, 11(4), 233-241. https://doi.org/10.1177/1084713807307409

Reviewer #2 (Public review):

Summary:

Building on previous models of multisensory integration (including their earlier correlation-detection framework used for non-spatial signals), the author introduces a population-level Multisensory Correlation Detector (MCD) that processes raw auditory and visual data. Crucially, it does not rely on abstracted parameters, as is common in normative Bayesian models," but rather works directly on the stimulus itself (i.e., individual pixels and audio samples). By systematically testing the model against a range of experiments spanning human, monkey, and rat data, the authors show that their MCD population approach robustly predicts perception and behavior across species with a relatively small (0-4) number of free parameters.

Strengths:

(1) Unlike prior Bayesian models that used simplified or parameterized inputs, the model here is explicitly computable from full natural stimuli. This resolves a key gap in understanding how the brain might extract "time offsets" or "disparities" from continuously changing audio-visual streams.

(2) The same population MCD architecture captures a remarkable range of multisensory phenomena, from classical illusions (McGurk, ventriloquism) and synchrony judgments, to attentional/gaze behavior driven by audio-visual salience. This generality strongly supports the idea that a single low-level computation (correlation detection) can underlie many distinct multisensory effects.

(3) By tuning model parameters to different temporal rhythms (e.g., faster in rodents, slower in humans), the MCD explains cross-species perceptual data without reconfiguring the underlying architecture.

Weaknesses:

(1) The authors show how a correlation-based model can account for the various multisensory integration effects observed in previous studies. However, a comparison of how the two accounts differ would shed light on the correlation model being an implementation of the Bayesian computations (different levels in Marr's hierarchy) or making testable predictions that can distinguish between the two frameworks. For example, how uncertainty in the cue combined estimate is also the harmonic mean of the unimodal uncertainties is a prediction from the Bayesian model. So, how the MCD framework predicts this reduced uncertainty could be one potential difference (or similarity) to the Bayesian model.

2) The authors show a good match for cue combination involving 2 cues. While Bayesian accounts provide a direction extension to more cues (also seen empirically, for eg, in Hecht et al. 2008), discussion on how the MCD model extends to more cues would benefit the readers.

Likely Impact and Usefulness:

The work offers a compelling unification of multiple multisensory tasks- temporal order judgments, illusions, Bayesian causal inference, and overt visual attention - under a single, fully stimulus-driven framework. Its success with natural stimuli should interest computational neuroscientists, systems neuroscientists, and machine learning scientists. This paper thus makes an important contribution to the field by moving beyond minimalistic lab stimuli, illustrating how raw audio and video can be integrated using elementary correlation analyses.

Reviewer #1 (Public review):

Summary:

Identifying drugs that target specific disease phenotypes remains a persistent challenge. Many current methods are only applicable to well-characterized small molecules, such as those with known structures. In contrast, methods based on transcriptional responses offer broader applicability because they do not require prior information about small molecules. Additionally, they can be rapidly applied to new small molecules. One of the most promising strategies involves the use of "drug response signatures"-specific sets of genes whose differential expression can serve as markers for the response to a small molecule. By comparing drug response signatures with expression profiles characteristic of a disease, it is possible to identify drugs that modulate the disease profile, indicating a potential therapeutic connection.

This study aims to prioritize potential drug candidates and to forecast novel drug combinations that may be effective in treating triple-negative breast cancer (TNBC). Large consortia, such as the LINCS-L1000 project, offer transcriptional signatures across various time points after exposing numerous cell lines to hundreds of compounds at different concentrations. While this data is highly valuable, its direct applicability to pathophysiological contexts is constrained by the challenges in extracting consistent drug response profiles from these extensive datasets. The authors use their method to create drug response profiles for three different TNBC cell lines from LINCS.<br /> To create a more precise, cancer-specific disease profile, the authors highlight the use of single-cell RNA sequencing (scRNA-seq) data. They focus on TNBC epithelial cells collected from 26 diseased individuals compared to epithelial cells collected from 10 healthy volunteers. The authors are further leveraging drug response data to develop inhibitor combinations.

Strengths:

The authors of this study contribute to an ongoing effort to develop automated, robust approaches that leverage gene expression similarities across various cell lines and different treatment regimen, aiming to predict drug response signatures more accurately. There remains a gap in computational methods for inferring drug responses at the cell subpopulation level, which the authors are trying to address.

Weaknesses:

The major deficiencies in this revised manuscript are a lack of benchmarking against established methods, clarification of method limitations, and experimental validation.

(1) The manuscript still lacks a direct comparison between the retriever tool and well-established methods. How does it perform compared to metaLINCS? Evaluating its performance relative to existing approaches is essential to demonstrate its added value and robustness.<br /> (2) The study remains limited by the absence of experimental validation. Are there supporting data from biological models or clinical trials? Figure 5F is important as this is the validation of the identified compounds in three cell lines. In the previous review, it was noted that the identified drugs had only a modest effect on cell viability. Furthermore, the efficacy of QL-XII-47 and GSK-690693 was found to be cell-line specific-showing activity against BT20 (the cell line used for LINCS transcriptional signature generation) but not against CAL120 and DU4475, which were not included in the signature derivation process. This raises concerns about the tool's ability to predict effective drugs. Additionally, the combination may have an effect because the drugs were tested at high concentrations. How does this effect compare in non-TNBC or normal immortalized breast cell lines? Finally, the DU4475 data were not reproducible, and the experiment must be repeated to ensure reliable comparisons.<br /> (3) A previous review requested a discussion on the limitations of the retriever tool, but the authors instead focused on the well-documented constraints of the LINCS dataset. Clearly defining limitations of the retriever will be critical for evaluating its potential applications and reliability.<br /> (4) Description of the database that the authors used should be corrected. Two examples are below:<br /> "The LINCS-L1000 project published transcriptional profiles of several cell lines." Exploring LINCS metadata will help to introduce the reader to this impressive catalog.<br /> "The portal then returns a ranked list of compounds that are likely to have an inverse effect on disease-associated gene expression levels". When selecting small molecules for use in LINCS-L1000 platform, no link was established between the compounds and disease-associated gene expression levels.<br /> (5) Fig. 3 presents data on differentially expressed genes. However, without indicating whether these genes are up- or downregulated, it is difficult to assess their relevance to TNBC phenotypes and cancer burden.<br /> Additionally, presenting the new Biological Process Gene Ontology analysis in a format similar to Fig. 3C would be beneficial. The statement that these processes are closely related to cancer deregulation is somewhat vague. Instead, the findings may be discussed in relation to each enriched pathway, specifically in the context of TNBC biology and available treatments.

Reviewer #2 (Public review):

Summary:

In their study, Osorio and colleagues present 'retriever,' an innovative computational tool designed to extract disease-specific transcriptional drug response profiles from the LINCS-L1000 project. This tool has been effectively applied to TNBC, leveraging single-cell RNA sequencing data to predict drug combinations that may effectively target the disease. The public review highlights the significant integration of extensive pharmacological data with high-resolution transcriptomic information, which enhances the potential for personalized therapeutic applications.

Strengths:

A key finding of the study is the prediction and validation of the drug combination QL-XII-47 and GSK-690693 for the treatment of TNBC. The methodology employed is robust, with a clear pathway from data analysis to experimental confirmation.

Comments on revisions:

I commend the authors for their thorough and thoughtful revisions, which have significantly strengthened the manuscript. The expanded discussion on the limitations of the LINCS-L1000 dataset and the inherent challenges of imputation techniques provides critical context for interpreting the tool's predictive accuracy. The addition of clinical implications, including strategies for integrating retriever into clinical trial design and its broader applicability to other diseases, enhances the translational relevance of the work. Addressing drug resistance mechanisms in the context of combination therapy further underscores the biological rationale for the approach.

The transparency regarding computational requirements and ethical considerations-particularly data privacy, bias mitigation, and model validation-demonstrates a responsible and forward-thinking approach to computational biology. These additions not only improve the manuscript's rigor but also set a precedent for ethical practices in personalized medicine research.

With these revisions, the authors have effectively addressed prior concerns and elevated the impact of their work. The manuscript now presents a compelling case for the retriever as a valuable tool in precision oncology.

Reviewer #2 (Public review):

In this study, the authors aim to investigate habituation, the phenomenon of increasing reduction in activity following repeated stimuli, in the context of its information theoretic advantage. To this end, they consider a highly simplified three-species reaction network where habituation is encoded by a slow memory variable that suppresses the receptor and therefore the readout activity. Using analytical and numerical methods, they show that in their model the information gain, the difference between the mutual information between the signal and readout after and before habituation, is maximal for intermediate habituation strength. Furthermore, they demonstrate that the Pareto front corresponding to an optimization strategy that maximizes the mutual information between signal and readout in the steady-state and minimizes dissipation in the system also exhibits similar intermediate habituation strength. Finally, they briefly compare predictions of their model to whole-brain recordings of zebrafish larvae under visual stimulation.

The author's simplified model serves as a good starting point for understanding habituation in different biological contexts as the model is simple enough to allow for some analytic understanding but at the same time exhibits most basic properties of habituation in sensory systems. Furthermore, the author's finding of maximal information gain for intermediate habituation strength via an optimization principle is, in general, interesting. However, the following points remain unclear:

(1) How general is their finding that the optimal Pareto front coincides with the region of maximal information gain? For instance, what happens if the signal H_st (H_max) isn't very strong? Does it matter that in this case, H_st only has a minor influence on delta Q_R? In the binary switching case, what happens if H_max is rather different from H_st (and not just 20% off)? Or in a case where the adapted value corresponds to the average of H_max and H_min?

(2) The comparison to experimental data isn't very convincing. For instance, is PCA performed simultaneously on both the experimental data set and on the model or separately? What are the units of the PCs in Fig. 6(b,c)? Given that the model parameters are chosen so that the activity decrease in the model is similar to the one in the data (i.e., that they show similar habituation in terms of the readout), isn't it expected that the dynamics in the PC1/2 space look very similar?

Reviewer #3 (Public review):

The authors use a generic model framework to study the emergence of habituation and its functional role from information-theoretic and energetic perspectives. Their model features a receptor, readout molecules, and a storage unit, and as such, can be applied to a wide range of biological systems. Through theoretical studies, the authors find that habituation (reduction in average activity) upon exposure to repeated stimuli should occur at intermediate degrees to achieve maximal information gain. Parameter regimes that enable these properties also result in low dissipation, suggesting that intermediate habituation is advantageous both energetically and for the purpose of retaining information about the environment.

A major strength of the work is the generality of the studied model. The presence of three units (receptor, readout, storage) operating at different time scales and executing negative feedback can be found in many domains of biology, with representative examples well discussed by the authors (e.g. Figure 1b). A key takeaway demonstrated by the authors that has wide relevance is that large information gain and large habituation cannot be attained simultaneously. When energetic considerations are accounted for, large information gain and intermediate habituation appear to be the favorable combination.

Comments on the revision:

The authors have adequately addressed the points I raised during the initial review. The text has been clarified at multiple instances, and the treatment of energy expenditure is now more rigorous. The manuscript is much improved both in terms of readability and scientific content.

Reviewer #1 (Public review):

This is a simple and potentially valuable approach to reduce Cre leak in amplified systems designed to improve CreER use across alleles. The revised work is improved with a direct comparison to the Benedito iSure-Cre line, providing some practical guidance for investigators. The authors do not address the issue of Cre toxicity or mosaic efficiency with low Tamoxifen use.

The major improvement in my mind is the inclusion of Supp Fig 7 where the authors compare their loxCre to iSureCre. The discussion is somewhat improved, but still fails to discuss significant issues such as Cre toxicity in detail. As noted by most reviewers, without a biological question, the paper is entirely a technical description of a couple of new tools. Whether and to what extent journals such as eLife should publish every new technical innovation without rigorous functional comparison to prior tools is an important question raised by this study. There is already a plethora of available techniques, most of which look better on paper than they function in mice.

However, I do feel that these tools will be of potential use to the field.

Reviewer #2 (Public review):

This work presents new genetic tools for enhanced Cre-mediated gene deletion and genetic lineage tracing. The authors optimise and generate mouse models that convert temporally controlled CreER or DreER activity to constitutive Cre expression, coupled with the expression of tdT reporter for the visualizing and tracing of gene-deleted cells. This was achieved by inserting a stop cassette into the coding region of Cre, splitting it into N- and C-terminal segments. Removal of the stop cassette by Cre-lox or Dre-rox recombination results in the generation of modified Cre that is shown to exhibit similar activity to native Cre. The authors further demonstrate efficient gene knockout in cells marked by the reporter using these tools, including intersectional genetic targeting of pericentral hepatocytes.

The new models offer several important advantages. They enable tightly controlled and highly effective genetic deletion of even alleles that are difficult to recombine. By coupling Cre expression to reporter expression, these models reliably report Cre-expressing i.e. gene-targeted cells and circumvent false positives that can complicate analyses in genetic mutants relying on separate reporter alleles. Moreover, the combinatorial use of Dre/Cre permits intersectional genetic targeting, allowing for more precise fate mapping.

The study and the new models have also limitations. The demonstration of efficient deletion of multiple floxed alleles in a mosaic fashion, a scenario where the lines would demonstrate their full potential compared to already existing models, has not been tested in the current study. Mosaic genetics is increasingly recognized as a key methodology for assessing cell-autonomous gene functions. The challenge lies in performing such experiments, as low doses of tamoxifen needed for inducing mosaic gene deletion may not be sufficient to efficiently recombine multiple alleles in individual cells while at the same time accurately reporting gene deletion. In addition, as discussed by the authors, a limitation of this line is the constitutive expression of Cre, which is associated with toxicity in some cases.

Comments on revisions: I have no further comments.

Reviewer #3 (Public review):

Shi et al describe a new set of tools to facilitate Cre or Dre-recombinase-mediated recombination in mice. The strategies are not completely novel but have been pursued previously by the lab, which is world-leading in this field, and by others. The authors report a new version of the iSuRe-Cre approach, which was originally developed by Rui Benedito's group in Spain. Shi et al describe that their approach shows reduced leakiness compared to the iSuRe-Cre line. Furthermore, a new R26-roxCre-tdT mouse line was established after extensive testing, which enables efficient expression of the Cre recombinase after activation of the Dre recombinase. The authors carefully evaluated efficiency and leakiness of the new line and demonstrated the applicability by marking peri-central hepatocytes in an intersectional genetics approach. The paper represents the result of enormous, carefully executed efforts. Although I would have preferred to see a study which uses the wonderful new tools to address a major biological question, carefully conducted technical studies have an enormous value for the scientific community, clearly justifying publication.

The new mouse lines generated in this study will enhance the precision of genetic manipulation in distinct cell types and greatly facilitate future work in numerous laboratories. The authors expertly eradicated weaknesses from initial submissions. Remaining open questions regarding potential toxicity of expressing multiple recombinases and fluorescence reports were convincingly answered.

Reviewer #1 (Public review):

Summary:

This noteworthy paper examines the role of planar cell polarity and Wnt signalling in body axis formation of the hydrozoan Clytia. In contrast to the freshwater polyp Hydra or the sea anemone Nematostella, Clytia represents a cnidarian model system with a complete life cycle (planula larva-polyp-medusa). In this species, classical experiments have demonstrated that a global polarity is established from the oral end of the embryos (Freeman, 1981). Prior research has demonstrated that Wnt3 plays a role in the formation of the oral organiser in Clytia and other cnidarians, acting in an autocatalytic feedback-loop with β-catenin. However, the question of whether and to what extent an oral-aboral gradient of Wnt activity is established remained unanswered. This gradient is thought to control both tissue differentiation and tissue polarity. The planar cell polarity (PCP) pathway has been linked to this polarity, although it is generally considered to be β-catenin independent.

Comments on major strengths and weaknesses:

Beautiful and solid experiments to clarify the role of canonical Wnt signalling and PCP core factors in coordinating planar cell polarity of Clytia. The authors have conducted a series of sophisticated experiments utilising morpholinos, mRNA microinjections and immunofluorescent visualisation of PCP. The objective of these experiments was to address the function of Wnt3, β-catenin and PCP core proteins in the coordination of the global polarity of Clytia embryos. The authors conclude that PCP plays a role in regulating polarity along the oral-aboral axis of embryos and larvae. This offers a conceivable explanation for how polarity information is established and distributed globally during Clytia embryogenesis, with implications for our understanding of axis formation in cnidarians and the evolution of Wnt signalling in general. - While the experiments are well-designed and executed, there are some criticisms, questions or suggestions that should be addressed.

(i) Wnt3 cue and global PCP. PCP has been described in detail in a previous paper on Clytia (Momose et al, 2012): its orientation along the oral-aboral body axis (ciliary basal body positioning studies), and its function in directional polarity during gastrulation (Stbm-, Fz1-, and Dsh-MO experiments). I wonder if this part could be shortened. What is new, however, are the knockdown and Wnt3-mRNA rescue experiments, which provide a deeper insight into the link between Wnt3 function in the blastopore organiser as a source or cue for axis formation. These experiments demonstrate that the Wnt3 knockdown induces defects equivalent to PCP factor knockdown, but can be rescued by Wnt3-mRNA injection, even at a distance of 200 µm away from the Wnt-positive area. The experimental set-up of these new molecular experiments follows in important aspects those of Freeman's experiments of 1981 (who in turn was motivated to re-examine Teissier's work of 1931/1933 ...). Freeman did not use the term "global polarity" but the concept of an axis-inducing source and a long-range tissue polarity can be traced back to both researchers.

(ii) PCP propagation and β-catenin. The central but unanswered question in this study focuses on the interaction between Wnt3 and PCP and the propagation of PCP. Wnt3 has been described in cnidarians but also in vertebrates and insects as a canonical Wnt interacting with β-catenin in an autocatalytic loop. The surprising result of this study is that the action of Wnt3 on PCP orientation is not inhibited in the presence of a dominant-negative form of CheTCF (dnTCF) ruling out a potential function of β-catenin in PCP. This was supported by studies with constitutively active β-catenin (CA-β-cat) mRNA which was unable to restore PCP coordination nor elongation of Wnt3-depleted embryos but did restore β-catenin-dependent gastrulation. Based on these data, the authors conclude that Wnt3 has two independent roles: Wnt/β-catenin activation and initial PCP orientation (two step model for PCP formation). However, the molecular basis for the interaction of Wnt3 with the PCP machinery and how the specificity of Wnt3 for both pathways is regulated at the level of Wnt-receiving cells (Fz-Dsh) remains unresolved. - Also, with respect to PCP propagation, there is no answer with respect to the underlying mechanisms. The authors found that PCP components are expressed in the mid-blastula stage, but without any further indication of how the signal might be propagated, e.g., by a wavefront of local cell alignment. Here, it is necessary to address the underlying possible cellular interactions more explicitly.

(iii) The proposed two step model for PCP formation has important evolutionary implications in that it excludes the current alternate model according to which a long-range Wnt3-gradient orients PCP ("Wnt/β-catenin-first"). Nevertheless, the initial PCP orientation by Wnt3 - as proposed in the two-step-model - is not explained at all on the molecular level. Another possible, but less well discussed and studied option for linking Wnt3 with PCP action could be a role of other Wnt pathways. The authors present compelling evidence that Wnt3 is the most highly expressed Wnt in Clytia at all stages of development. The authors convincingly show that Wnt3 is the most highly expressed Wnt in Clytia at all stages of development (Fig. S1). However, Wnt7 is also more highly expressed, which makes it a candidate for signal transduction from canonical Wnts to PCP Wnts. An involvement of Wnt7 in PCP regulation has been described in vertebrates (http://dx.doi.org/10.1016/j.celrep.2013.12.026). This would challenge the entire discussion and speculation on the evolutionary implications according to which PCP Wnt signaling comes first (PCP-first scenario") and canonical Wnt signaling later in metazoan evolution.

(iv) The discussion, including Figure 6, is strongly biased towards the traditional evolutionary scenario postulating a choanzoan-sponge ancestry of metazoans. Chromosome-linkage data of pre-metazoans and metazoans (Schulz et al., 2023; https://doi.org/10 (1038/s41586-023-05936-6) now indicate a radically different scenario according to which ctenophores represent the ancestral form and are sister to sponges, cnidarians and bilaterians (the Ctenophora-sister hypothesis). This also has implications for the evolution of Wnt signalling, as discussed in the recent Nature Genetics Review by Holzem et al. (2024) (https://doi.org/10.1038/s41576-024-00699-w). Furthermore, it calls into question the hypothesis of a filter-feeding multicellular gastrula-like ancestor as proposed by Haeckel (Maegele et al., 2023). These papers have not yet been referenced, but they would provide a more robust discussion.

General appraisal:

The authors have carefully addressed all important points raised in this review. Aims and results support their conclusions.

Impact of the work, utility of methods and data:

As stated above, there will be a major impact on our understanding of the role of Wnt signaling in gradient formation and particularly the role of non canonical wnt signaling. As mentioned above, this will have a major impact on our understanding of the role of Wnt signalling in gradient formation, particularly the role of non-canonical Wnt signalling. - It will also be important to better understand the role of Wnt-Frizzled interactions in these basal organisms, as cnidarians have a smaller repertoire of Frizzled receptors compared to the relatively complete repertoire of Wnt subfamilies. This may imply that Wnt 3 is active in both canonical and PCP.

Additional context:

With regard to the question of the evolution of the body plan and Wnt signalling, it would be helpful and important for readers unfamiliar with cnidarians to know that the Hydrozoa/Medusozoa, to which Clytia belongs, are an "evolutionary derived group" within the Cnidaria, as opposed to the Anthozoa (e.g. sea anemone Nematostella). Hydrozoans possess planula larvae that are devoid of a mouth and any form of feeding mechanism, relying instead on the yolk of a fertilised egg for sustenance. The substantial divergence between the Anthozoa and Medusozoa was accompanied by significant gene reductions within the Medusozoa, which likely exerts an influence on the evolution of Wnt signalling in this group as well. This should not detract from the value of the work, but may help to put it in perspective.

Reviewer #2 (Public review):

Summary:

Canonical Wnt signaling has previously been shown to be responsible for correct patterning of the oral-aboral axis as well as germ layer formation in several cnidarians. The post-gastrula stage, the planula larvae is not only elongated, it has a specific swimming direction due to the decentralized cellular positioning and slanted anchoring of the cilia. This, in turn, is in most other animals the result of a Wnt-Planar-cell polarity pathway. This paper by Uveira et al investigates the role of Wnt3 signaling in serving as a local cue for the PCP pathway which then is responsible for the orientation of the cilia and elongation of the planula larva of the hydrozoan Clytia hemisphaerica. Wnt3 was shown before to activate the canonical pathway via ß-catenin and to act as an axial organizer. The authors provide compelling evidence for this somewhat unusual direct link between the pathways through the same signaling molecule, Wnt3. In conclusion, they propose a two-step model: 1) local orientation by Wnt3 secretion 2) global propagation by the PCP pathway over the whole embryo.

Strengths:

In a series of elegant and also seemingly sophisticated experiments, they show that Wnt3 activates the PCP pathway directly, as it happens in the absence of canonical Wnt signaling (e.g. through co-expression of dnTCF). Conversely, constitutive active ß-catenin was not able to rescue PCP coordination upon Wnt3 depletion, yet restored gastrulation. This uncouples the effect of Wnt3 on axis specification and morphogenetic movements from the elongation via PCP. Through transplantation of single blastomeres providing a local source of Wnt3, they also demonstrate the reorganization of cellular polarity immediately adjacent to the Wnt3 expressing cell patch. These transplantation experiments also uncover that mechanical cues can also trigger the polarization, suggesting a mechanotransduction or direct influence on subcellular structures, e.g. actin fiber orientation.

This is a beautiful and elegant study addressing an important question. The results have significant implications also for our understanding of the evolutionary origin of axis formation and the link of these two ancient pathways, which in most animals are controlled by distinct Wnt ligands and Frizzled receptors. The quality of the data is stunning and the paper is written in a clear and succinct manner. This paper has the potential to become a widely cited milestone paper.

Weaknesses:

I can not detect any major weaknesses. The work only raises a few more follow-up questions, which the authors are invited to comment on.

I acknowledge the revisions made by the authors. Some open questions remain that need to be addressed in future work, and I accept the limitations of this study, as argued by the authors. Besides the elegant and high-quality experiments, I also appreciate the thoughtful and inspiring discussion.

Reviewer #1 (Public review):

Summary:

Compelling and clearly described work that combines two elegant cell fate reporter strains with mathematical modelling to describe the kinetics of CD4+ TRM in mice. The aim is to investigate the cell dynamics underlying maintenance of CD4+TRM.

The main conclusions are that 1) CD4+ TRM are not intrinsically long-lived 2) even clonal half lives are short: 1 month for TRM in skin, even shorter (12 days) for TRM in lamina propria 3) TRM are maintained by self-renewal and circulating precursors.

Strengths:

(1) Very clearly and succinctly written. Though in some places too succinctly! See suggestions below for areas I think could benefit from more detail.

(2) Powerful combination of mouse strains and modelling to address questions that are hard to answer with other approaches.

(3) The modelling of different modes of recruitment (quiescent, neutral, division linked) is extremely interesting and often neglected (for simpler neutral recruitment).

Comments on revised version: This reviewer is satisfied with the author responses and the changes made in the manuscript.

Reviewer #2 (Public review):

This manuscript addresses a fundamental problem of immunology - the persistence mechanisms of tissue-resident memory T cells (TRMs). It introduces a novel quantitative methodology, combining the in vivo tracing of T cell cohorts with rigorous mathematical modeling and inference. Interestingly, the authors show that immigration plays a key role for maintaining CD4+ TRM populations in both skin and lamina propria (LP), with LP TRMs being more dependent on immigration than skin TRMs. This is an original and potentially impactful manuscript.

Comments on revised version: This reviewer is satisfied with the author responses and the changes made in the manuscript.

Reviewer #1 (Public review):

Summary:

Wang et al. identify Hamlet, a PR-containing transcription factor, as a master regulator of reproductive development in Drosophila. Specifically, the fusion between the gonad and genital disc that is necessary for development of a continuous testes and seminal vesicle tissue essential for fertility. To do so, the authors generate novel Hamlet null mutants by CRISPR/Cas9 gene editing and characterize the morphological, physiological, and gene expression changes of the mutants using immunofluorescence, RNA-seq, cut-tag, and in-situ analysis. Thus, Hamlet is discovered to regulate a unique expression program, which includes Wnt2 and Tl, that is necessary for testis development and fertility.

Strengths:

This is a rigorous and comprehensive study that identifies the Hamlet dependent gene expression program mediating reproductive development in Drosophila. The Hamlet transcription targets are further characterized by Gal4/UAS-RNAi confirming their role in reproductive development. Finally, the study points to a role for Wnt2 and Tl as well as other Hamlet transcriptionally regulated genes in epithelial tissue fusion.

Weaknesses:

None noted.

Reviewer #2 (Public review):

Strengths:

Wang and colleagues successfully uncovered an important function of the Drosophila PRDM16/PRDM3 homolog Hamlet (Ham) - a PR domain containing transcription factor with known roles in the nervous system in Drosophila. To do so, they generated and analyzed new mutants lacking the PR domain, and also employed diverse preexisting tools. In doing so, they made a fascinating discovery: They found that PR-domain containing isoforms of ham are crucial in the intriguing development of the fly genital tract. Wang and colleagues found three distinct roles of Ham: (1) Specifying the position of the testis terminal epithelium within the testis, (2) allowing normal shaping and growth of the anlagen of the seminal vesicles and paragonia and (3) enabling the crucial epithelial fusion between the seminal vesicle and the testis terminal epithelium. The mutant blocks fusion even if the parts are positioned correctly. The last finding is especially important, as there are few models allowing one to dissect the molecular underpinnings of heterotypic epithelial fusion in development. Their data suggest that they found a master regulator of this collective cell behavior. Further, they identified some of the cell biological players downstream of Ham, like for example E-Cadherin and Crumbs. In a holistic approach, they performed RNAseq and intersected them with the CUT&TAG-method, to find a comprehensive list of downstream factors directly regulated by Ham. Their function in the fusion process was validated by a tissue-specific RNAi screen. Meticulously, Wang and colleagues performed multiplexed in situ hybridization and analyzed different mutants, to gain a first understanding of the most important downstream-pathways they characterized - which are Wnt2 and Toll.

This study pioneers a completely new system. It is a model for exploring a process crucial in morphogenesis across animal species, yet not well-understood. Wang and colleagues not only identified a crucial regulator of heterotypic epithelial fusion but took on the considerable effort of meticulously pinning down functionally important downstream effectors by using many state-of-the-art methods. This is especially impressive, as dissection of pupal genital discs before epithelial fusion is a time-consuming and difficult task. This promising work will be the foundation future studies build on, to further elucidate how this epithelial fusion works, for example on a cell biological and biomechanical level.

Weaknesses:

The developing testis-genital disc system has many moving parts. Myotube migration was previously shown to be crucial for testis shape. This means, that there is the potential of non-tissue autonomous defects upon knockdown of genes in the genital disc or the terminal epithelium, affecting myotube behavior which in turn affects epithelial fusion, as myotubes might create the first "bridge" bringing the two epithelia together. Nevertheless, this is outside the scope of this work and could be addressed in the future.

Reviewer #1 (Public review):

Summary:

In this manuscript the Treisman and colleagues address the question of how protein phosphatase 1 (PP1) regulatory subunits (or PP1-interacting protein (PIPs)) confer specificity on the PP1 catalytic subunit which by itself possesses little substrate specificity. In prior work the authors showed that the PIP Phactrs confers specificity by remodelling a hydrophobic groove immediately adjacent to the PP1 catalytic site through residues within the RVxF- ø ø -R-W string of Phactrs. Specifically, the residues proximal and including the 'W' of the RVxF- ø ø -R-W string remodel the hydrophobic groove. Other residues the of the RVxF- ø ø -R-W string (i.e. the RVxF- ø ø -R) are not involved in this remodelling.

The authors suggest that the RVxF- ø ø -R-W string is a conserved feature of many PIPs including PNUTS, Neurabin/spinophilin and R15A. However from a sequence and structural perspective only the RVxF- ø ø -R- is conserved. The W is not conserved in most and in the R15A structure (PDB:7NZM) the Trp side chain points away from the hydrophobic channel - this could be a questionable interpretation due to model building into the low resolution cryo-EM map (4 A).

In this paper the authors convincingly show that Neurabin confers substrate specificity through interactions of its PDZ domain with the PDZ domain-binding motif (PBM) of 4E-BP. They show the PBM motif is required for Neurabin to increase PP1 activity towards 4E-BP and a synthetic peptide modelled on 4E-BP and also a synthetic peptide based on IRSp53 with a PBM added. The PBM of 4E-BP1 confers high affinity binding to the Neurabin PDZ domain. A crystal structure of a PP1-4E-BP1 fusion with Neurabin shows that the PBM of 4E-BP interacts with the PDZ domain of Neurabin. No interactions of 4E-BP and the catalytic site of PP1 are observed. Cell biology work showed that Neurabin-PP1 regulates the TOR signalling pathway by dephosphorylating 4E-BPs.

Strengths:

This work demonstrates convincingly using a variety of cell biology, proteomics, biophysics and structural biology that the PP1 interacting protein Neurabin confers specificity on PP1 through an interaction of its PDZ domain with a PDZ-binding motif of 4E-BP1 proteins. Remodelling of the hydrophobic groove of the PP1 catalytic subunit is not involved in Neurabin-dependent substrate specificity, in contrast to how Phactrs confers specificity on PP1. The active site of the Neurabin/PP1 complex does not recognise residues in the vicinity of the phospho-residue, thus allowing for multiple phospho-sites on 4E-BP to be dephosphorylated by Neurabin/PP1. This contrasts with substrate specificity conferred by the Phactrs PIP that confers specificity of Phactrs/PP1 towards its substrates in a sequence-specific context by remodelling the hydrophobic groove immediately adjacent to the catalytic. The structural and biochemical insights are used to explore the role of Neurabin/PP1 in dephosphorylation 4E-BPs in vivo, showing that Neurabin/PP1 regulates the TOR signalling pathway, specifically mTORC1-dependent translational control.

Weaknesses:

The only weakness is the suggestion that a conserved RVxF- ø ø -R-W string exists in PIPs. The 'W' is not conserved in sequence and 3-dimensions in most of the PIPs discussed in this manuscript. The lack of conservation of the W would be consistent with the finding based on multiple PP1-PIP structures that apart from Phactrs, no other PIP appears to remodel the PP1 hydrophobic channel.

Comments on revisions:

The authors have addressed my comments.

One aspect of the manuscript and response to reviewers is misleading regarding the statement: 'Like many PIPs, they interact with PP1 using the previously defined "RVxF", "ΦΦ", and "R" motifs (Choy et al, 2014).' This statement, and similar in the authors' response, implies that Choy et al discovered the "RVxF" and "ΦΦ" motifs. The Choy et al, 2014 paper reports the discovery of the "R" motif. The "RVxF" and "ΦΦ" motifs were discovered and reported in earlier papers not cited in the authors' manuscript. Perhaps the authors can correct this.

Reviewer #2 (Public review):

This manuscript explores the molecular mechanisms that are involved in substrate recognition by the PP1 phosphatase. The authors previously showed that the PP1 interacting protein (PPI), PhactrI, conferred substrate specificity by remodelling the PP1 hydrophobic substrate groove. In this work, the authors aimed to understand the key determinant of how other PIPs, Neurabin and Spinophilin, mediate substrate recognition.

The authors generated a few PP1-PIP fusion constructs, undertook TMT phosphoproteomics and validated their method using PP1-Phactr1/2/3/4 fusion constructs. Using this method, the authors identified phsophorylation sites controlled by PP1-Neurabin and focussed their work on 4E-BP1, thereby linking PP1-Neurabin to mTORC1 signalling. Upon validating that PP1-Neurabin dephosphorylates 4E-BP1, they determined that 4E-BP1 PBM binds to the PDZ domain of Neurabin with an affinity that was greater than 30 fold as compared to other substrates. PP1-Neurabin dephosphorylated 4E-BP1WT and IRSp53WT with a catalytic efficiency much greater than PP1 alone. However, PP1-Neurabin bound to 4E-BP1 and IRSp53 mutants lacking the Neurabin PDZ domain with a catalytic efficiency lesser than that observed with 4E-BP1WT. These results indicate the involvement of the PDZ domain in facilitating substrate recruitment by PP1-Neurabin. Interestingly, PP1-Phactr1 dephosphorylation of 4E-BP1 phenocopies PP1 alone, while PP1-Phactr1 dephosphorylates IRSp53 to a much higher extent than PP1 alone. These results highlights the importance of the PDZ domain and also shed light on how different PP1-PIP holoenzymes mediate substrate recognition using distinct mechanisms. The authors also show that the remodelling of the hydrophobic PP1 substrate groove which is essential for substrate recognition by PP1-Phactr1, was not required by PP1-Neurabin. Additionally, the authors also resolved the structure of a PP1-4E-BP1 fusion with the PDZ-containing C-terminal of Neurabin and observed that the Neurabin/PP1-4E-BP1 complex structure was oriented at 21{degree sign} to that in the unliganded Spinophilin/PP1 complex (resolved by Ragusa et al., 2010) owing to a slight bend in the C-terminal section that connects it to the RVxF-ΦΦ-R-W string. Since, no interaction was observed with the remodelled PP1-Neurabin hydrophobic groove, the authors utilised AlphaFold3 to further answer this. They observed a high confidence of interaction between the groove and phosphorylated substrate and a low confidence of interaction between the groove and unphosphorylated substrate, thereby suggesting that the hydrophobic groove remodelling is not involved in PP1-Neurabin recognition and dephosphorylation of 4E-BP1.

In this work, the authors provide novel insights into how Neurabin depends on the interaction between its PDZ domain and PBM domains of potential substrates to mediate its recruitment by PP1. Additionally, they uncover a novel PP1-Neurabin substrate, 4E-BP1. They systematically employ phosphoproteomics, biochemical and structural methods to investigate substrate specifity in a robust fashion. Furthermore, the authors also compares the interactions between PP1-Neurabin to 4E-BP1 and IRSp53 (PP1-Phactr1 substrate) with PP1-Phactr1, to showcase the specificity of the mode of action employed by these complexes in mediating substrate specificity. The authors do employ an innovative PP1-PIP fusion strategy previously explored by Oberoi et al., 2016 and the authors themselves in Fedoryshchak et al., 2020. This method, allows for a more controlled investigation of the interactions between PP1-PIPs and its substrates. Furthermore, the authors have substantially characterised the importance of the PDZ domain using their fusion constructs, however, I believe that a further exploration into either structural or AlphaFold3 modelling of PBM domain substrate mutants, or a Neurabin PDZ-domain mutant might further strengthen this claim. Overall, the paper makes a substantial contribution to understanding substrate recognition and specificity in PP1-PIP complexes. The study's innovative methods, biological relevance, and mechanistic insights are strengths, but whether this mechanism occurs in a physiological context is unclear.

Reviewer #3 (Public review):

Protein Phosphatase 1 (PP1), a vital member of the PPP superfamily, drives most cellular serine/threonine dephosphorylation. Despite PP1's low intrinsic sequence preference, its substrate specificity is finely tuned by over 200 PP1-interacting proteins (PIPs), which employ short linear motifs (SLIMs) to bind specific PP1 surface regions. By targeting PP1 to cellular sites, modifying substrate grooves, or altering surface electrostatics, PIPs influence substrate specificity. Although many PIP-PP1-substrate interactions remain uncharacterized, the Phactr family of PIPs uniquely imposes sequence specificity at dephosphorylation sites through a conserved "RVxF-ΦΦ-R-W" motif. In Phactr1-PP1, this motif forms a hydrophobic pocket that favors substrates with hydrophobic residues at +4/+5 in acidic contexts (the "LLD motif"), a specificity that endures even in PP1-Phactr1 fusions. Neurabin/Spinophilin remodel PP1's hydrophobic groove in distinct ways, creating unique holoenzyme surfaces, though the impact on substrate specificity remains underexplored. This study investigates Neurabin/Spinophilin specificity via PDZ domain-driven interactions, showing that Neurabin/PP1 specificity is governed more by PDZ domain interactions than by substrate sequence, unlike Phactr1/PP1.

A significant strength of this work is the use of PP1-PIP fusion proteins to effectively model intact PP1•PIP holoenzymes by replicating the interactions that remodel the PP1 interface and confer site-specific substrate specificity. When combined with proteomic analyses to assess phospho-site depletion in mammalian cells, these fusions offer critical insights into holoenzyme specificity, revealing new candidate substrates for Neurabin and Spinophilin. The studies present compelling evidence that the PDZ domain of PP1-Neurabin directs its specificity, with the remodeled PP1 hydrophobic groove interactions having minimal impact. This mechanism is supported by structural analysis of the PP1-4E-BP1 substrate fusion bound to a Neurabin construct, highlighting the 4E-BP1/PDZ interaction. This work delivers crucial insights into PP1-PIP holoenzyme function, combining biochemical, proteomic, and structural approaches. It validates the PP1-PIP fusion protein model as a powerful tool, suggesting it may extend to studying additional holoenzymes. While an extremely useful model, it must be considered unlikely the PP1-PIP fusions fully recapitulate the specificity and regulation of the holoenzyme.

Reviewer #1 (Public review):

Summary:

This article presents an analysis that challenges established abundance-occupancy relationships (AORs) by utilizing the largest known bird observation database. The analysis yields contentious outcomes, raising the question of whether these findings could potentially refute AORs.

Strengths:

The study employed an extensive aggregation of datasets to date to scrutinize the abundance-occupancy relationships (AORs).

Weaknesses:

The authors should thoroughly address the correlation between checklist data and global range data, ensuring that the foundational assumptions and potential confounding factors are explicitly examined and articulated within the study's context.

In the revision, the authors have refined their findings to birds and provided additional clarifications and discussion. However, the primary concerns raised by reviewers remain inadequately addressed. My main concern continues to be whether testing AOR at a global scale is meaningful given the numerous confounding factors involved. With the current data and analytical approach, these confounders appear inseparable. The study would be significantly strengthened if the authors identified specific conditions under which AORs are valid.

Reviewer #1 (Public review):

Summary:

This paper investigates the physical mechanisms underlying cell intercalation, which then enables collective cell flows in confluent epithelia. The authors show that T1 transitions (the topological transitions responsible for cell intercalation) correspond to the unbinding of groups of hexatic topological defects. Defect unbinding, and hence cell intercalation and collective cell flows, are possible when active stresses in the tissue are extensile. This result helps to rationalize the observation that many epithelial cell layers have been found to exhibit extensile active nematic behavior.

Strengths:

The authors obtain their results based on a combination of active hexanematic hydrodynamics and a multiphase field (MPF) model for epithelial layers, whose connection is a strength of the paper. With the hydrodynamic approach, the authors find the active flow fields produced around hexatic topological defects, which can drive defect unbinding. Using the MPF simulations, the authors show that T1 transitions tend to localize close to hexatic topological defects.

Weaknesses:

Citations are sometimes not comprehensive. Cases of contractile behavior found in collective cell flows, which would seemingly contradict some of the authors' conclusions, are not discussed.

I encourage the authors to address the comments and questions below.

(1) In Equation 1, what do the authors mean by the cluster's size \ell? How is this quantity defined? The calculations in the Methods suggest that \ell indicates the distance between the p-atic defects and the center of the T1 cell cluster, but this is not clearly defined.

(2) The multiphase field model was developed and reviewed already, before the Loewe et al. 2020 paper that the authors cite. Earlier papers include Camley et al. PNAS 2014, Palmieri et al. Sci. Rep. 2015, Mueller et al. PRL 2019, and Peyret et al. Biophys. J. 2019, as reviewed in Alert and Trepat. Annu. Rev. Condens. Matter Phys. 2020.

(3) At what time lag is the mean-squared displacement in Figure 3f calculated? How does the choice of a lag time affect these data and the resulting conclusions?

(4) The authors argue that their results provide an explanation for the extensile behavior of cell layers. However, there are also examples of contractile behavior, such as in Duclos et al., Nat. Phys., 2017 and in Pérez-González et al., Nat. Phys., 2019. In both cases, collective cell flows were observed, which in principle require cell intercalations. How would these observations be rationalized with the theory proposed in this paper? Can these experiments and the theory be reconciled?

Reviewer #2 (Public review):

Summary:

This paper studies the role of hexatic defects in the collective migration of epithelia. The authors emphasize that epithelial migration is driven by cell intercalation events and not just isolated T1 events, and analyze this through the lens of hexatic topological defects. Finally, the authors study the effect of active and passive forces on the dynamics of hexatic defects using analytical results, and numerical results in both continuum and phase-field models.

The results are very interesting and highlight new ways of studying epithelial cell migration through the analysis of the binding and unbinding of hexatic defects.

Strengths:

(1) The authors convincingly argue that intercalation events are responsible for collective cell migration, and that these events are accompanied by the formation and unbinding of hexatic topological defects.

(2) The authors clearly explain the dynamics of hexatic defects during T1 transitions, and demonstrate the importance of active and passive forces during cell migration.

(3) The paper thoroughly studies the T1 transition through the viewpoint of hexatic defects. A continuum model approach to study T1 transitions in cell layers is novel and can lead to valuable new insights.

Weaknesses:

(1) The authors could expand on the dynamics of existing hexatic defects during epithelial cell migration, in addition to how they are created during T1 transitions.

(2) The different terms in the MPF model used to study cell layer dynamics are not fully justified. In particular, it is not clear why the model includes self-propulsion and rotational diffusion in addition to nematic and hexatic stresses, and how these quantities are related to each other.

(3) The authors could provide some physical intuition on what an active extensile or contractile term in the hexatic order parameter means, and how this is related to extensility and contractility in active nematics and/or for cell layers.

Reviewer #3 (Public review):

Summary:

In this manuscript, the authors discuss epithelial tissue fluidity from a theoretical perspective. They focus on the description of topological transitions whereby cells change neighbors (T1 transitions). They explain how such transitions can be described by following the fate of hexatic defects. They first focus on a single T1 transition and the surrounding cells using a hydrodynamic model of active hexatics. They show that successful T1 intercalations, which promote tissue fluidity, require a sufficiently large extensile hexatic activity in the neighborhood of the cells attempting a T1 transition. If such activity is contractile or not sufficiently extensile, the T1 is reversed, hexatic defects annihilate, and the epithelial network configuration is unchanged. They then describe a large epithelium, using a phase field model to describe cells. They show a correlation between T1 events and hexatic defects unbinding, and identify two populations of T1 cells: one performing T1 cycles (failed T1), and not contributing to tissue migration, and one performing T1 intercalation (successful T1) and leading to the collective cell migration.

Strengths:

The manuscript is scientifically sound, and the variety of numerical and analytical tools they use is impressive. The approach and results are very interesting and highlight the relevance of hexatic order parameters and their defects in describing tissue dynamics.

Weaknesses:

(1) Goal and message of the paper.

a) In my opinion, the article is mainly theoretical and should be presented as such. For instance, their conclusions and the consequences of their analysis in terms of biology are not extremely convincing, although they would be sufficient for a theory paper oriented to physicists or biophysicists. The choice of journal and potential readership should be considered, and I am wondering whether the paper structure should be re-organized, in order to have side-by-side the methods and the results, for instance (see also below).

b) Currently, the two main results sections are somewhat disconnected, because they use different numerical models, and because the second section only marginally uses the results from the first section to identify/distinguish T1 (see also below).

(2) Quite surprisingly, the authors use a cell-based model to describe the macroscopic tissue-scale behavior, and a hydrodynamic model to describe the cell-based events. In particular, their hydrodynamic description (the active hexatic model) is supposed to be a coarse-grained description, valid to capture the mesoscopic physics, and yet, they use it to describe cell-scale events (T1 transitions). For instance, what is the meaning of the velocity field they are discussing in Figure 2? This makes me question the validity of the results of their first part.

(3) The quality of the numerical results presented in the second part (phase field model) could be improved.

a) In terms of analysis of the defects. It seems that they have all the tools to compare their cell-resolved simulations and their predictions about how a T1 event translates into defects unbinding. However, their analysis in Figure 3e is relatively minimal: it shows a correlation between T1 cells and defects. But it says nothing about the structure and evolution of the defects, which, according to their first section, should be quite precise. I believe it should be possible to identify and quantify more precisely the unbinding or annihilation of the defects and hence to characterize more precisely the T1 events.

b) In terms of clarity of the presentation. For instance, in Figure 3f, they plot the mean-square displacement as a function of a defect density. I thought that MSD was a time-dependent quantity: they must therefore consider MSD at a given time, or averaged over time (in that case, what they are showing is rather an effective diffusivity). They should, in any case, be explicit about what their definition of this quantity is.

c) In terms of statistics. For instance, Figure 3g is used to study the role of rotational diffusion on the average time between T1s. The error bars in this figure are huge and make their claims hardly supported. It is, for instance, hard to believe that the dynamics of T1 cycles are unaffected by D_r. In the limit where D_r vanishes, for instance, there should be no T1 and the period of a T1 cycle should diverge, which is not observed. Their claim of a "monotonic decay" of the average time between intercalations is also not fully supported given their statistics.

Reviewer #1 (Public review):

This manuscript uses a well-validated behavioural estimation task to investigate the degree to which optimistic belief updating was attenuated during the 2020 global pandemic. Online participants estimated how likely different negative life events were to happen to them in the future and were given statistics about these events. Belief updating (measured as the degree to which estimations changed after viewing the statistics) was less optimistically biased during the pandemic (compared to outside of it). This resulted from reduced updating from "good news" (better than expected information). Computational models were used to try to unpack how statistics were integrated and used to revise beliefs. Two families of models were compared - an RL set of models where "estimation errors" (analogous to prediction errors in classic RL models) predict belief change and a Bayesian set of models where an implied likelihood ratio was calculated (derived from participants estimations of their own risk and estimation of the base rate risk) and used to predict belief change. The authors found evidence that the former set of models accounted for updating better outside of the pandemic, but the latter accounted for updating during the pandemic. In addition, the RL model provides evidence that learning was asymmetrically positively biased outside of the pandemic but symmetric during it (as a result of reduced learning rates from good news estimation errors).

Strengths

Understanding whether biases in learning are fixed modes of information processing or flexible and adapt in response to environmental shocks (like a global pandemic or economic recession) is an important area of research relevant to a wide range of fields, including cognitive psychology, behavioural economics, and computational psychiatry. The study uses a well-validated task, and the authors conduct a power analysis to show that the sample sizes are appropriate. Furthermore, the authors test that their results hold in both a between-group analysis (the focus of the main paper) and a within-group analysis (mainly in the supplemental).

The finding that optimistic biases are reduced in response to acute stress, perceived threat, and depression has been shown before using this task both in the lab (social stress manipulation), in the real world (firefighters on duty), and clinical groups (patients with depression). However, the work does extend these findings here in important ways:

(1) Examining the effect of a new real-world adverse event (the pandemic).<br /> (2) The reduction in optimistic updating here arises due to reduced updating from positive information (previously, in the case of environmental threat, this reduction mainly arose from increased sensitivity to negative information).<br /> (3) Leveraging new RL-inspired computational approaches, demonstrating that the bias - and its attenuation - can be captured using trial-by-trial computational modelling with separate learning rates for positive and negative estimation errors.

The authors now take great care to caveat that the findings cannot directly attribute the observed lack of optimistically biased belief updating during lockdown to psychological causes such as heightened anxiety and stress.

The authors have added model recovery results. Whilst there are some cases within a family (RL or Bayesian) of models where they can be confused (e.g., Bayesian model 10-the winning model during the pandemic-sometimes gets confused with Bayesian model 9), there is no confusion between families of models (RL models don't get confused with Bayesian models and vice versa), which is reassuring.

Weaknesses

The authors now conduct model recovery (SI Figure 5) and show how the behaviour of the two best-fitting models (Rational Bayesian model and optimistically biased RL-like model) approximates the actual data observed by showing them alongside each other (Figure 1b). It seems from Figure 1b that the 2 models predict similar behaviour for bad news but diverge for good news, with the optimistically biased RL-like model predicting greater updates than the rational Bayesian model. However, it is difficult to tell from the figure (partly because of the y-axis scale) how much of a divergence this is and how distinctive a pattern relative to the other models. I think the interpretation could be improved further by a clearer sense of the behavioural signatures of each model, enabling them to be reliably teased apart from one another in the model recovery.

Reviewer #2 (Public review):

The authors investigated how experiencing the COVID-19 pandemic affected optimism bias in updating beliefs about the future. They ran a between-subjects design testing participants on cognitive tasks before, during and after the lift of the sanitary state of emergency during the pandemic. The authors show that optimism bias varied depending on the context in which it was tested. Namely, it disappeared during COVID-19 and it re-emerged at the time of lift of sanitary emergency measures. Via advanced computational modelling they are able to thoroughly characterise the nature of such alterations, pinpointing specific mechanisms underlying the lack of optimistic bias during the pandemic.

Strengths pertain to the comprehensive assessment of the results via computational modelling, and from a theoretical point of view, the notion that environmental factors can affect cognition. Power analysis was conducted to ensure that the study was powered to observe the effect of interest despite the relatively small sample size.

As the authors also noted, a major impediment to the interpreting the findings pertains to the lack of additional measures. While information on, for example, risk perception or need for social interaction were collected from participants during the pandemic, the fact that these could not be included in the analysis hindered the interpretation of findings. While the interpretation of the findings remains challenging, this work offers an example of the influence of real-life conditions on the belief-updating process.

Reviewer #1 (Public review):

This study presents valuable findings on the GABA and BOLD changes induced by continuous theta burst stimulation (cTBS) and on the relationships between ATL GABA level and performance in a semantic task. However, I'm afraid that the current results are incomplete to support some primary claims of the paper, for example, the purported inverted-U-shaped relationship between GABA levels in the ATL and semantic task performance. The influence of practice effects also complicates the interpretation of the results. Additional concerns include potential double dipping in the analysis depicted in Figure 3A and the use of inconsistent behavioral measures (IE and accuracy) across various analyses.

The authors have made two beneficial revisions in this round: (1) acknowledging the insufficient data points supporting the inverted U-shaped curve; (2) attempting to control for practice effects. However, I believe unresolved issues remain:

(1) The authors have not addressed my specific concern about Figure 4D - the analysis attempts to fit an inverted U-shaped curve to the data without distinguishing between data points influenced by practice effects and those unaffected, rendering its reliability questionable.

(2) The authors appear to have misunderstood my question regarding Figure 3A. This issue is unrelated to practice effects. My point was that even if we randomly generated pre- and post-test data points and grouped/analyzed them according to the authors' methodology, we would still likely reproduce the pattern in Figure 3A due to the double dipping problem. Thus, this statistical analysis and its conclusions currently lack methodological validity.

(3) Regarding the inconsistency in behavioral measures, the authors' explanation fails to remove my concerns. If the authors argue that accuracy is the most appropriate behavioral dependent variable for this study, why did they employ inverse efficiency in some of their analyses? My understanding is that a study should either consistently use the single most suitable measure or report multiple measures while providing adequate discussion of inconsistent results.

Reviewer #3 (Public review):

As a result of a number of rounds of reviews and consultations between reviewers, Jung et al. present important work on the relationship between gamma-aminobutyric acid (GABA) levels within the anterior temporal lobes (ATL) to semantic memory while accounting for inter-individual differences. They provide solid evidence suggesting that inhibitory continuous theta burst transcranial magnetic stimulation (cTBS TMS) increased GABA concentration and decreased the blood-oxygen dependent signal (BOLD) during a semantic task.

The authors fully addressed my comments from the first and second rounds of reviews, and I do not have additional concerns. I have, however, scaled down my short assessment, given the concerns of reviewers 1 and 2.

Reviewer #1 (Public review):

Summary:

The results offer compelling evidence that L5-L5 tLTD depends on presynaptic NMDARs, a concept that has previously been somewhat controversial.

It documents the novel finding that presynaptic NMDARs facilitate tLTD through their metabotropic signaling mechanism.

Strengths:

The experimental design is clever and clean.

The approach of comparing the results in cell pairs where NMDA is deleted either presynaptically or postsynaptically is technically insightful and yields decisive data.

The MK801 experiments are also compelling.

Weaknesses:

No major weaknesses were noted by this reviewer.

Reviewer #2 (Public review):

Summary:

The study characterized the dependence of spike-timing-dependent long-term depression (tLTD) on presynaptic NMDA receptors and the intracellular cascade after NMDAR activation possibly involved in the observed decrease in glutamate probability release at L5-L5 synapses of the visual cortex in mouse brain slices.

Strengths:

The genetic and electrophysiological experiments are thorough. The experiments are well-reported and mainly support the conclusions. This study confirms and extends current knowledge by elucidating additional plasticity mechanisms at cortical synapses, complementing existing literature.

Weaknesses:

While one of the main conclusions (preNMDARs mediating presynaptic LTD) is resolved in a very convincing genetic approach, the second main conclusion of the manuscript (non-ionotropic preNMDARs) relies on the use of a high concentration of extracellular blockers (MK801, 2 mM; 7-clorokinurenic acid: 100 microM), but no controls for the specific actions of these compounds are shown. In addition, no direct testing for ions passing through preNMDAR has been performed.

It is not known if the results can be extrapolated to adult brain as the data were obtained from 11-18 days-old mice slices, a period during which synapses are still maturing and the cortex is highly plastic.

Reviewer #3 (Public review):

Summary:

In this manuscript, "Neocortical Layer-5 tLTD Relies on Non-Ionotropic Presynaptic NMDA Receptor Signaling", Thomazeau et al. seek to determine the role of presynaptic NMDA receptors and the mechanism by which they mediate expression of frequency-independent timing-dependent long-term depression (tLTD) between layer-5 (L5) pyramidal cells (PCs) in the developing mouse visual cortex. By utilizing sophisticated methods, including sparse Cre-dependent deletion of GluN1 subunit via neonatal iCre-encoding viral injection, in vitro quadruple patch clamp recordings, and pharmacological interventions, the authors elegantly show that L5 PC->PC tLTD is (1) dependent on presynaptic NMDA receptors, (2) mediated by non-ionotropic NMDA receptor signaling, and (3) is reliant on JNK2/Syntaxin-1a (STX1a) interaction (but not RIM1αβ) in the presynaptic neuron. The study elegantly and pointedly addresses a long-standing conundrum regarding the lack of frequency dependence of tLTD.

Strengths:

The authors did a commendable job presenting a very polished piece of work with high-quality data that this Reviewer feels enthusiastic about. The manuscript has several notable strengths. Firstly, the methodological approach used in the study is highly sophisticated and technically challenging and successfully produced high-quality data that were easily accessible to a broader audience. Secondly, the pharmacological interventions used in the study targeted specific players and their mechanistic roles, unveiling the mechanism in question step-by-step. Lastly, the manuscript is written in a well-organized manner that is easy to follow. Overall, the study provides a series of compelling evidence that leads to a clear illustration of mechanistic understanding.

I have a couple of small items below, which the authors can address in a minor revision if they so wish.

Minor comments:

(1) For the broad readership, a brief description of JNK2-mediated signaling cascade underlying tLTD, including its intersection with CB1 receptor signaling may be desired.

(2) The authors used juvenile mice, P11 to P18 of age. It is a typical age range used for plasticity experiments, but it is also true that this age range spans before and after eye-opening in mice (~P13) and is a few days before the onset of the classical critical period for ocular dominance plasticity in the visual cortex. Given the mechanistic novelty reported in the study, can authors comment on whether this signaling pathway may be age-dependent?

Reviewer #1 (Public review):

Summary:

The authors describe a role of sumoylation at K81 in p66Shc which affects endothelial dysfunction. This explores a new mechanism for understanding the role of PTMs in cellular processes.

Strengths:

The experiments are well planned and the results are well represented.<br /> Vascular tonality experiments were carried out nicely, given the amount of time and effort one needs to put in to get clean results from these experiments.

Weaknesses:

(1) The production of ROS has been measured in a very superficial way.<br /> The term "ROS" confers a plethora of chemical species which exerts different physiological effects on different cells and situations.<br /> Mitochondria through one of the source , but not the only source of ROS production. Only measuring ROS with mitosox do not reflect the cellular condition of ROS in a specific condition. I would suggest authors consider doing IF of oxidative stress specific markers , carbonyl group and also, maybe, Amplex red for determining average oxidative stress and ros production in the cells.<br /> (2) 8-OHG signal seems very confusing in Figure 7E. 8-ohg is supposed to be mainly in the nucleus and to some extent in mitochondria. The signal is very diffused in the images. I would suggest a higher magnification and better resolution images for 8-ohg. Also, the VWF signal is pretty weak whereas it should be strong given the staining is in aorta. Authors should redo the experiments.<br /> (3) PCA analysis is quite not clear. Why is there a convergence among the plots? Authors should explain. Also, I would suggest that the authors do the analysis done in Figure 8B again with R based packages. IPA, though being user-friendly, mostly does not yield meaningful results and the statistics carried out is not accurate. Authors should redo the analysis in R or Python whichever is suitable for them.<br /> (4) The MS analysis part seems pretty vague in methods. Please rewrite.

Reviewer #2 (Public review):

Summary:

The article builds on the earlier work that both p66Shc and SUMOylation are essential nitric oxide (NO) based development of endothelial vasculature (PMID: 10580504; 28760777 and 35187108). The current manuscript brings forward a finding of how SUMO2ylation of p66Shc mediated ROS production which is essential for endothelial cells. They further identify that lysine 81 of p66Shc is the residue which is conjugated to SUMO2 and is crucial for mitochondrial localization. They further show that K81 SUMO2ylation is essential for S36 phosphorylation.

Strengths:

Convincingly shows that p66Shc is SUMO2ylated on lysine 81 in cells and also shows that the phosphorylation (serine 36) reduces upon loss of this critical SUMOylation site.

Weaknesses:

All the experiments performed here are in overexpression background therefore, it would be crucial to show that p66Shc is SUMO2ylated at physiological levels.

Reviewer #3 (Public review):

Summary:

The authors set out to determine how SUMO2 impairs endothelial function through direct modification of the protein p66Shc. p66Shc is known to promote reactive oxygen species production, and here the authors demonstrate that SUMO2 modifies p66Shc at lysine-81, resulting in increased phosphorylation, mitochondrial translocation. These are prosed to mediate the detrimental effects of SUMO2 in a mouse model of hyperlipidemia.

Strengths:

A major strength of this work is the multi-pronged approach combining biochemical assays, proteomic analyses, and a genetically modified mouse model expressing a SUMOylation resistant mutant of p66Shc. These experiments comprehensively illustrate that lysine-81 SUMOylation of p66Shc is necessary for the observed endothelial dysfunction in hyperlipidemic conditions.

Weaknesses:

One notable weakness is that the link between the observed cellular changes and the ultimate in vivo phenotype remains only partially explored. While the authors successfully show that p66ShcK81R knockin mice are protected from endothelial dysfunction in a hyperlipidemic context, additional experiments characterizing the broader tissue-specific roles, or examining further endothelial assays in vivo, would strengthen the mechanistic conclusions. It would also be beneficial to see more direct evaluations of p66Shc subcellular localization in the protective knockin mice to complement the proteomic findings.

Despite these gaps, the data broadly support the authors' main conclusions. The authors lay out a plausible mechanistic pathway for how hyperlipidemia and increased global SUMOylation can converge on the oxidative stress pathway to provoke vascular dysfunction.

The likely impact of this work on the field is noteworthy. Beyond clarifying how a single post-translational modification event can influence the pathophysiology of endothelial cells, the study provides a model for investigating broader roles of SUMO2 in other cardiovascular conditions and highlights the importance of identifying additional SUMOylation sites and their downstream impact.

In conclusion, by demonstrating the direct SUMOylation of p66Shc at lysine-81 and linking that modification to endothelial dysfunction in a hyperlipidemic mouse model, this paper offers valuable insights into how broadly acting post-translational modifiers can evoke specific pathological effects.

Reviewer #1 (Public review):

Summary:

This manuscript assesses the utility of spatial image correlation spectroscopy (ICS) for measuring physiological responses to DNA damage. ICS is a long-established (~1993) method, similar to fluorescence correlation spectroscopy, for deriving information about the fluorophore density that underlies the intensity distributions of images.

The revisions to the current manuscript have improved the understanding of the strengths and limitations of the spatial ICS method. In particular, since the measurements are obtaining complementary information to traditional focus counting, one does not expect a simple linear relationship between the quantities obtained by ICS and by immunostaining. The explanations are satisfactory to me and, I expect, to the interested reader.

Additionally, I am satisfied with the code availability now that it is placed on Github.

Reviewer #2 (Public review):

This valuable study presents image correlation spectroscopy (ICS) an alternative method to foci counting as a quantitative measurement of recruitment of DNA damage response associated proteins to chromatin following exposure of cells to various genotoxic agents. The evidence presented to demonstrate that this method is more sensitive than traditional foci counting is convincing, although the two methods provide similar results for many of the comparisons. This work will be of interest to scientists using immunostaining to study DNA repair.

Comments on revisions:

The authors adequately addressed the comments raised and improved the manuscript. The authors accurately state that there is subjectivity in foci counting, e.g., different thresholds and/or algorithms produce different absolute counts. In addition, the conditions for pre-extraction also introduce variability, and any pre-extraction may inadvertently remove meaningful signal. Yet it is unclear whether these differences in absolute counts impact the conclusions that can be drawn from these experiments, which do not usually make a claim about the absolute number of foci, but rather a comparison between two different conditions with the same pre-extraction conditions and the same threshold/counting algorithm applied, with appropriate controls. Moreover, when the authors compared ICS to foci counting, the results were largely similar, although ICS was superior in a few instances. Overall, how transitioning from the widely-used foci counting method to ICS will offer a major advantage is unclear.

Reviewer #3 (Public review):

Summary:

This paper described a new tool called "Image Correlation Spectroscopy; ICS) to detect clustering fluorescence signals such as foci in the nucleus (or any other cellular structures). The authors compared ICS DA (degree of aggregation) data with Imaris Spots data (and ImageJ Find Maxima data) and found a comparable result between the two analyses and that the ICS sometimes produced a better quantification than the Imaris software. Moreover, the authors extended the application of ICS to detect cell-cycle stages by analyzing the DAPI image of cells. This is a useful tool without the subjective bias of researchers and provides novel quantitative values in cell biology.

Strengths:

The authors developed a new tool to detect and quantify the aggregates of immuno-fluorescent signals, which is a center of modern cell biology, such as the fields of DNA damage responses (DDR), including DNA repair. This new method could detect the "invisible" signal in cells without pre-extraction, which could prevent the effect of extracted materials on the pre-assembled ensembles, a target for the detection. This would be an alternative method for the quantification of fluorescent signals relative to conventional methods.

Comments on revisions:

The authors addressed previous comments properly.

Reviewer #2 (Public review):

Summary:

This study aims to explore the ferroptosis-related immune landscape of TNBC through the integration of single-cell and bulk RNA sequencing data, followed by the development of a risk prediction model for prognosis and drug response. The authors identified key subpopulations of immune cells within the TME, particularly focusing on T cells and macrophages. Using machine learning algorithms, the authors constructed a ferroptosis-related gene risk score that accurately predicts survival and the potential response to specific drugs in TNBC patients.

Strengths:

The study identifies distinct subpopulations of T cells and macrophages with differential expression of ferroptosis-related genes. The clustering of these subpopulations and their correlation with patient prognosis is highly insightful, especially the identification of the TREM2+ and FOLR2+ macrophage subtypes, which are linked to either favorable or poor prognoses. The risk model thus holds potential not only for prognosis but also for guiding treatment selection in personalized oncology.

Reviewer #1 (Public review):

Summary:

In this revised report, Yamanaka and colleagues investigate a proposed mechanism by which testosterone modulates seminal plasma metabolites in mice. Based on limited evidence in previous versions of the report, the authors softened the claim that oleic acid derived from seminal vesicle epithelium strongly affects linear progressive motility in isolated cauda epididymal sperm in vitro. Though the report still contains somewhat ambiguous references to the strength of the relationship between fatty acids and sperm motility.

Strengths:

Often, reported epidydimal sperm from mice have lower percent progressive motility compared with sperm retrieved from the uterus or by comparison with human ejaculated sperm. The findings in this report may improve in vitro conditions to overcome this problem, as well as add important physiological context to the role of reproductive tract glandular secretions in modulating sperm behaviors. The strongest observations are related to the sensitivity of seminal vesicle epithelial cells to testosterone. The revisions include the addition of methodological detail, modified language to reflect the nuance of some of the measurements, as well as re-performed experiments with more appropriate control groups. The findings are likely to be of general interest to the field by providing context for follow-on studies regarding the relationship between fatty acid beta oxidation and sperm motility pattern.

Weaknesses:

The connection between media fatty acids and sperm motility pattern remains inconclusive.

Reviewer #2 (Public review):

Using a combination of in vivo studies with testosterone-inhibited and aged mice with lower testosterone levels as well as isolated mouse and human seminal vesicle epithelial cells the authors show that testosterone induces an increase in glucose uptake. They find that testosterone induces a difference in gene expression with a focus on metabolic enzymes. Specifically, they identify increased expression of enzymes regulating cholesterol and fatty acid synthesis, leading to increased production of 18:1 oleic acid. The revised version strengthens the role of ACLY as the main regulator of seminal vesicle epithelial cell metabolic programming. The authors propose that fatty acids are secreted by seminal vesicle epithelial cells and are taken up by sperm, positively affecting sperm function. A lipid mixture mimicking the lipids secreted by seminal vesicle epithelial cells, however, only has a small and mostly non-significant effect on sperm motility, suggesting the authors were not apply to pinpoint the seminal vesicle fluid component that positively affects sperm function.

Reviewer #1 (Public review):

This work introduces and describes a useful curation pipeline of antibody-antigen structures downloaded from the PDB database. The antibody-antigen structures are presented in a new database called AACDB - with associated website - alongside annotations that were either corrected from those present in the PDB database, or added de-novo with solid methodology. Sequences, structures and annotations can be very easily downloaded from the AACDB website, speeding up the development of structure-based algorithms and analysis pipelines to characterize antibody-antigen interactions. However, AACDB is missing some important annotations that I believe would greatly enhance its usefulness, such as binding affinity annotations.

I think the potentially most significant contribution of this database is the manual data curation to fix errors present in the PDB entries, by cross-referencing with the literature. The authors also seem to describe, whenever possible, the procedures they took to correct the annotations.

I have personally verified some of the examples presented by the authors, and found that SAbDab appears to fix the mistakes related to mis-identification of antibody chains, but not other annotations.

"(1) the species of the antibody in 7WRL was incorrectly labeled as "SARS coronavirus B012" in both PDB and SabDab" → I have verified the mistake and fix, and that SAbDab does not fix is, just uses the pdb annotation.<br /> "(2) 1NSN, the resolution should be 2.9 , but it was incorrectly labeled as 2.8" → I have verified the mistake and fix, and that saabdab does not fix it, just uses the PDB annotation.<br /> "(3) mislabeling of antibody chains as other proteins (e.g. in 3KS0, the light chain of B2B4 antibody was misnamed as heme domain of flavocytochrome b2)" → SAbDab fixes this as well in this case.<br /> "(4) misidentification of heavy chains as light chains (e.g. both two chains of antibody were labeled as light chain in 5EBW)" → SAbDab fixes this as well in this case.

I believe the splitting of the pdb files is a valuable contribution as it standardizes the distribution of antibody-antigen complexes. Indeed, there is great heterogeneity in how many copies of the same structure are present in the structure uploaded to the PDB, generating potential artifacts for machine learning applications to pick up on. That being said, I have two thoughts both for the authors and the broader community. First, in the case of multiple antibodies binding to different epitopes on the same antigen, one should not ignore the potentially stabilizing effect that the binding of one antibody has on the complex, thereby enabling the binding of the second antibody. In general, I urge the community to think about what is the most appropriate spatial context to consider when modeling the stability of interactions from crystal structure data. Second, and in a similar vein, some antigens occur naturally as homomultimers - e.g. influenza hemagglutinin is a homotrimer. Therefore, to analyze the stability of a full-antigen-antibody structure, I believe it would be necessary to consider the full homo-trimer, whereas in the current curation of AACDB with the proposed data splitting, only the monomers are present.

I think the annotation of interface residues is a very useful addition to structural datasets.

I am, however, not convinced of the utility of *change* in SASA as a useful metric for identifying interacting residues, beyond what is already identified via pairwise distances between the antibody and antigen residues. If we had access to the unbound conformation of most antibodies and antigens, then we could analyze the differences in structural conformations upon binding, which can be in part quantified by change in SASA. However, as only bound structures are usually available, one is usually force to approximate a protein's unbound structure by computationally removing its binding partner - as it seems to me the authors of this work are doing.

Some obvious limitations of AACDB in its current form include:

AACDB only contains entries with protein-based antigens of at most 50 amino-acids in length. This excludes non-protein-based antigens, such as carbohydrate- and nucleotide-based, as well as short peptide antigens.<br /> AACDB does not include annotations of binding affinity, which are present in SAbDab and have been proven useful both for characterizing drivers of antibody-antigen interactions (cite https://www.sciencedirect.com/science/article/pii/S0969212624004362?via%3Dihub) and for benchmarking antigen-specific antibody-design algorithms (cite https://www.biorxiv.org/content/10.1101/2023.12.10.570461v1))

Reviewer #2 (Public review):

Summary:

Antibodies, thanks to their high binding affinity and specificity to cognate protein targets, are increasingly used as research and therapeutic tools. In this work, Zhou et al. have created, curated and made publicly available a new database of antibody-antigen complexes to support research in the field of antibody modelling, development and engineering.

Strengths:

The authors have performed a manual curation of antibody-antigen complexes from the Protein Data Bank, rectifying annotation errors; they have added two methods to estimate paratope-epitope interfaces; they have produced a web interface capable of effective visualisation and of summarising the key useful information in one page. The database is also cross-linked to other databases that contain information relevant to antibody developability and therapeutic applications.

Weaknesses:

The database does not import all the experimental information from PDB and contains only complexes with large protein targets.

Comments on revisions: I thank the authors for having incorporated my feedback and I look forward to the next releases of this database.

Reviewer #1 (Public review):

In their manuscript, Papadopoli et al explore the role of ETFDH in transformation. They note that ETFDH protein levels are decreased in cancer, and that deletion of ETFDH in cancer cell lines results in increased tumorigenesis, elevated OXPHOS and glycolysis, and a reduction in lipid and amino acid oxidation. The authors attribute these effects to increased amino acid levels stimulating mTORC1 signaling and driving alterations in BCL6 and EIF4EBP1. They conclude that ETFDH1 is epigenetically silenced in a proportion of neoplasms, suggesting a tumor-suppressive function. Overall, the authors logically present clear data and perform appropriate experiments to support their hypotheses. I only have a few minor points related to the semantics of a few of the author's statements.

Minor Points

Authors state, "we identified ETF dehydrogenase (ETFDH) as one of the most dispensable metabolic genes in neoplasia." Surely there are thousands of genes that are dispensable for neoplasia. Perhaps the authors can revise this sentence and similar sentiments in the text.

Authors state, " These findings show that ETFDH loss elevates glutamine utilization in the CAC to support mitochondrial metabolism." While elevated glutamine to CAC flux is consistent with the statement that increased glutamine, the authors have not measured the effect of restoring glutamine utilization to baseline on mitochondrial metabolism. Thus, the causality implied by the authors can only be inferred based on the data presented. Indeed, the increased glutamine consumption may be linked to the increase in ROS, as glutamate efflux via system xCT is a major determinant of glutamine catabolism in vitro.

Authors state that the mechanism described is an example of "retrograde signaling". However, the mechanism seems to be related to a reduction in BCAA catabolism, suggesting that the observed effects may be a consequence of altered metabolic flux rather than a direct signaling pathway. The data presented do not delineate whether the observed effects stem from disrupted mitochondrial communication or from shifts in nutrient availability and metabolic regulation.

The authors should discuss which amino acids that are ETFDH substrates might affect mTORC1 activity, or consider whether other ETFDH substrates might also affect mTORC1 in their discussion. Along these lines, the authors might consider discussing why amino acids that are not ETFDH substrates are increased upon ETFDH loss.

Reviewer #2 (Public review):

Summary:

The altered metabolism of tumors enables their growth and survival. Classically, tumor metabolism often involves increased activity of a given pathway in intermediary metabolism to provide energy or substrates needed for growth. Papadopoli et al. investigate the converse - the role of mitochondrial electron transfer flavoprotein dehydrogenase (ETFDH) in cancer metabolism and growth. The authors present compelling evidence that ETFDH insufficiency, which is detrimental in non-malignant tissues, paradoxically enhances bioenergetic capacity and accelerates neoplastic growth in cancer cells in spite of the decreased metabolic fuel flexibility that this affords tumor cells. This is achieved through the retrograde activation of the mTORC1/BCL-6/4E-BP1 axis, leading to metabolic and signaling reprogramming that favors tumor progression.

Strengths:

This review focuses primarily on the cancer metabolism aspects of the manuscript.

The study provides robust evidence linking ETFDH insufficiency to enhanced cancer cell bioenergetics and tumor growth.

The use of multiple cancer cell lines and in vivo models strengthens the generalizability of the findings.

The mechanistic insights into the mTORC1/BCL-6/4E-BP1 axis and its role in metabolic reprogramming are of general interest within and outside the immediate field of tumor metabolism.

Weaknesses:

The ETFDH knockout experiments are well-controlled by the addback of sgRNA-resistant ETFDH, but do not determine if the catalytic activity of this enzyme is required for the phenotypes induced by ETFDH loss.

Although this is not critical, it would be nice to see if the increased labeled aspartate pools result in higher nucleotide pools to support tumor growth.

Conclusion:

This manuscript provides significant insights into the role of ETFDH insufficiency in cancer metabolism and growth. The findings highlight the potential of targeting the mTORC1/BCL-6/4E-BP1 axis in ETFDH-deficient cancers. The compelling data support the conclusions presented in the manuscript, which will be valuable to the cancer metabolism community.

Reviewer #1 (Public review):

To elucidate the mechanisms and evolution of animal biomineralization, Voigt et al. focused on the sponge phylum - the earliest branching extant metazoan lineages exhibiting biomineralized structures - with a particular emphasis on deciphering the molecular underpinnings of spicule formation. This study centered on calcareous sponges, specifically Sycon ciliatum, as characterized in previous work by Voigt et al. In S. ciliatum, two morphologically distinct spicule types are produced by a set of two different types of cells that secrete extracellular matrix proteins, onto which calcium carbonate is subsequently deposited. Comparative transcriptomic analysis between a region with active spicule formation and other body regions identified 829 candidate genes involved in this process. Among these, the authors focused on the calcarine gene family, which is analogous to the Galaxins, the matrix proteins known to participate in coral calcification. The authors performed three-dimensional structure prediction using AlphaFold, examined mRNA expression of Calcarin genes in spicule-forming cell types via in situ hybridization, conducted proteomic analysis of matrix proteins isolated from purified spicules, and carried out chromosome arrangement analysis of the Calcarin genes.

Based on these analyses, it was revealed that the combination of Calcarin genes expressed during spicule formation differs between the founder cells-responsible for producing diactines and triactines-and the thickener cells that differentiate from them, underscoring the necessity for precise regulation of Calcarin gene expression in proper biomineralization. Furthermore, the observation that 4 Calcarin genes are arranged in tandem arrays on the chromosome suggests that two rounds of gene duplication followed by neofunctionalization have contributed to the intricate formation of S. ciliatum spicules. Additionally, similar subtle spatiotemporal expression patterns and tandem chromosomal arrangements of Galaxins during coral calcification indicate parallel evolution of biomineralization genes between S. ciliatum and aragonitic corals.

Strengths:

(1) An integrative research approach, encompassing transcriptomic, genomic, and proteomic analyses as well as detailed FISH.

(2) High-quality FISH images of Calcarin genes, along with a concise summary clearly illustrating their expression patterns, is appreciated.

(3) It was suggested that thickener cells originate from founder cells. To the best of my knowledge, this is the first study to demonstrate trans-differentiation of sponge cells based on the cell-type-specific gene expression, as determined by in situ hybridization.

(4) The comparison between Calcarins of Calcite sponge and Galaxins of aragonitic corals from various perspective-including protein tertiary structure predictions, gene expression profiling during calcification, and chromosomal sequence analysis to reveal significant similarities between them.

(5) The conclusions of this paper are generally well supported by the data; however, some FISH images require clearer indication or explanation.

(6) Figure S2 (B, C, D): The fluorescent signals in these images are difficult to discern. If the authors choose to present signals at such low magnification, enhancing the fluorescence signals would improve clarity. Additionally, incorporating Figure S2A as an inset within Figure S2E may be sufficient to convey the necessary information about signal localization.

(7) Figure S3A: The claim that Cal2-expressing spherical cells are closely associated with the choanoderm at the distal end of the radial tube is difficult to follow. Are these Cal2-expressing spherical cells interspersed among choanoderm cells, or are they positioned along the basal surface of the choanoderm? Clarifying their precise localization and indicating it in the image would strengthen the interpretation.

(8) To further highlight the similarities between S.ciliatum and aragonitic corals in the molecular mechanisms of calcification, consider including a supplementary figure providing a concise depiction of the coral calcification process. This would offer valuable context for readers.

Reviewer #2 (Public review):

Summary:

This paper reports on the discovery of calcarins, a protein family that seems involved in calcification in the sponge Sycon ciliatum, based on specific expression in sclerocytes and detection by mass spectrometry within spicules. Two aspects stand out: (1) the unexpected similarity between Sycon calcarins and the galaxins of stony corals, which are also involved in mineralization, suggesting a surprising, parallel co-option of similar genes for mineralization in these two groups; (2) the impressively cell-type-specific expression of specific calcarins, many of which are restricted to either founder or thickener cells, and to either diactines, triactines, or tetractines. The finding that calcarins likely diversified at least partly by tandem duplications (giving rise to gene clusters) is a nice bonus.

Strengths:

I enjoyed the thoroughness of the paper, with multiple lines of evidence supporting the hypothesized role of calcarins: spatially and temporally resolved RNAseq, mass spectrometry, and whole-mount in situ hybridization using CISH and HCR-FISH (the images are really beautiful and very convincing). The structural predictions and the similarity to galaxins are very surprising and extremely interesting, as they suggest parallel evolution of biomineralization in sponges and cnidarians during the Cambrian explosion by co-option of the same "molecular bricks".

Weaknesses:

I did not detect any major weakness, beyond those inherent to working with sponges (lack of direct functional inhibition of these genes) or with fast-evolving gene families with complex evolutionary histories (lack of a phylogenetic tree that would clarify the history of galaxins/calcarins and related proteins).

Reviewer #3 (Public review):

Summary:

The study explores the extent to which the biomineralization process in the calcitic sponge Sycon ciliatum resembles aragonitic skeleton formation in stony corals. To investigate this, the authors performed transcriptomic, genomic, and proteomic analyses on S. ciliatum and examined the expression patterns of biomineralization-related genes using in situ hybridization. Among the 829 differentially expressed genes identified in sponge regions associated with spicule formation, the authors focused on calcarin genes, which encode matrix proteins analogous to coral galaxins. The expression patterns of calcarins were found to be diverse but specific to particular spicule types. Notably, these patterns resemble those of galaxins in stony corals. Moreover, the genomic organization of calcarine genes in S. ciliatum closely mirrors that of galaxin genes in corals, suggesting a case of parallel evolution in carbonate biomineralization between calcitic sponges and aragonitic corals.

Strengths:

The manuscript is well written, and the figures are of high quality. The study design and methodologies are clearly described and well-suited to addressing the central research question. Particularly noteworthy is the authors´ integration of various omics approaches with molecular and cell biology techniques. Their results support the intriguing conclusion that there is a case of parallel evolution in skeleton-building gene sets between calcitic sponges and aragonitic corals. The conclusions are well supported by the data and analyses presented.

Weaknesses:

The manuscript is strong, and I have not identified any significant weaknesses in its current form.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors investigated factors required for neural progenitors to exit the cell cycle before the adult stage. They first show that Kr is turned on in pupal stage MBNBs, and depletion of Kr from pupal stage NBs leads to retention of MBNBs into the adult stage. Then they demonstrate that these retained NBs maintain the expression of Imp, and co-depletion of Imp abolishes the extended neurogenesis. Further, they show that co-depletion of kr-h1 significantly reduces the retained MBNBs caused by loss of kr, suggesting antagonistic genetic interactions between these two. In addition, they demonstrate that over-expressing Kr-h1 leads to the striking phenotype of tumor-like neuroblast overgrowth in adult brains.

Strengths:

(1) The authors leveraged well-controlled, powerful genetic tools (including temporal control of RNAi knockdown using the Gal80ts system), and provided strong evidence that Kr expression in pupal stage MBNBs is required to repress Imp and promote the end of neurogenesis. Similarly, the experimental result of co-depleting Kr-h1 and Kr, and the striking phenotype upon Kr-h1 mis-expression, support the antagonistic roles played by Kr-h1 and Kr in this process.

(2) The sample sizes, quantification methods, and p-values are well documented for all experiments. In most parts, the data presented strongly support their conclusions.

(3) Identification of two transcription factors with opposite roles in controlling cell cycle exit, and their possible interactions with the Imp/Syp axis, is highly significant for the study on how the proliferation of neural progenitors is regulated and limited before the adult stage.

Weaknesses:

(1) The nature of the KrIf-1 allele is not clear. It is mentioned that this allele leads to misexpression of Kr in various tissues. However, it is not clear if Kr is mis-expressed or lost in MBNBs in the KrIf-1 mutant. If Kr is mis-expressed in MBNBs in the KrIf-1 mutant, then it would be difficult to explain why both loss of Kr and mis-expression of Kr in MBNBs lead to the same NB retention phenotype. The authors should examine Kr expression in MBNBs in the KrIf-1 mutant.

(2) Some parts of the regulations and interactions between Kr, Kr-h1, Imp, Syp, and E93 are not well-defined. For example, the data suggest that Kr is turned on in the pupal stage MBNBs, and is required to end neurogenesis through repressing Imp and Kr-h1. To further support this conclusion, the authors can examine if Kr-h1 expression is up-regulated in kr-RNAi. The authors suggested that Kr-h1 may act upstream or in parallel to Imp/Syp, but also suggested that Kr-h1 may repress E93. The expression of Imp, Syp, and E93 can be examined in brains with Kr-h1 mis-expression to determine where Kr-h1 acts. If Imp expression is elevated when Kr-h1 is mis-expressed, then Kr-h1 may act upstream of Imp. If Imp/Syp expression does not change, then Kr-h1 may act on the E93 level.

Reviewer #2 (Public review):

Summary:

In this paper, the authors study the role of Kruppel in regulating the survival of mushroom body neuroblasts. They first confirm that adult wild-type brains have no proliferation and report that Kruppel mutants and Kruppel RNAi in neuroblasts show a few proliferative clones; they show that these proliferative clones are localized in the mushroom body. They then show that Kruppel is expressed mostly during pupal stages and acts by downregulating the expression of Imp, which has been shown to positively regulate neuroblast proliferation and survival. Expectedly, this also affects neuronal diversity in the mushroom body, which is enriched in gamma neurons that are born during the Imp-expression window. Finally, they show that Kr acts antagonistically to Kr-h1, which is expressed predominantly in larval stages.

Strengths:

The main strength of this paper is that it identified a novel regulator of Imp expression in the mushroom body neuroblasts. Imp is a conserved RNA-binding protein that has been shown to regulate neural stem cell proliferation and survival in different animals.

Weaknesses:

(1) The main weakness of the paper is that the authors want to test adult neurogenesis in a system where no adult neurogenesis exists. To achieve this, they force neuroblasts to survive in adulthood by altering the genetic program that prevents them from terminating their proliferation. If this was reminiscing about "adult neurogenesis", the authors should at least show how adult neurons incorporate into the mushroom body even if they are born much later. On the contrary, this more likely resembles a tumorigenic phenotype, when stem cells divide way past their appropriate timing.

(2) Moreover, the figures are, in many cases, hard to understand, and the interpretation of the figures doesn't always match what one sees. The manuscript would benefit from better figures; for example, in Figure 2C, Miranda expression in insc>GFP in Kr-IF-1 is not visible.

(3) The authors describe a targeted genetic screen, but they don't describe which genes were tested, how they were chosen, and why Kruppel was finally selected.

(4) The authors argue that Kr does not behave as a typical tTF in MBNBs. However, they show no expression in the embryo, limited expression in the larva and early pupa, and a peak around P24-P48. This sounds like a temporally regulated expression of a transcription factor. Importantly, they mentioned that they tested their observations against different datasets (FlyAtlas2, modENCODE, and MBNB-lineage-specific RNA-seq data), but they don't provide the data.

(5) Finally, the contribution of Kr to the neuronal composition of the mushroom body is expected (since Imp is known to regulate neuronal diversity in the MB), but the presentation in the paper is very incomplete.

Unfortunately, based on the above, I am not convinced that the authors can use this framework to infer anything about adult neurogenesis. Therefore, the impact of this work is limited to the role of Kruppel in regulating Imp, which has already been shown to regulate the extent of neuroblast division, as well as the neuronal types that are born at different temporal windows.

Reviewer #3 (Public review):

Summary:

Drosophila neuroblasts (NBs) serve as a well-established model for studying neural stem cell biology. The intrinsic genetic programs that control their mitotic potential throughout development have been described in remarkable detail, highlighting a series of sequentially expressed transcription factors and RNA-binding proteins that together constitute the temporal patterning system.

However, the mechanisms that limit the number of NB divisions remain largely unknown in a specific subset of NBs known as mushroom body neuroblasts (MB NBs). Unlike other NBs, which terminate proliferation before or shortly after the onset of metamorphosis, MB NBs continue dividing until the end of metamorphosis, ceasing only just before adulthood.<br /> In this study, the authors identify the transcription factor Krüppel (Kr), a member of the conserved Krüppel-like family, as temporally regulated in MB NBs. They demonstrate that Kr knockdown during pupal stages maintains expression of the RNA-binding protein Imp and results in prolonged MB NB proliferation into adulthood. Their data suggest that Kr contributes to the timely silencing of Imp during metamorphosis. The authors further identify Kr-h1, a related transcription factor, as a potential antagonist. While Kr-h1 appears dispensable for the timely termination of MB NBs under normal conditions, its overexpression leads to their continued proliferation and tumor-like expansion in adults.

This work provides the first evidence for a transcription factor-driven temporal regulation mechanism in MB NBs, offering new insight into the control of neural stem cell self-renewal. Given the evolutionary conservation of Krüppel-like factors, this study may have broader implications for the neural stem cell field.

Strengths:

(1) The study possibly identifies a new series of temporal transcription factors that are specific for mushroom body neuroblasts.

(2) The mechanism could be conserved in vertebrates.

Weaknesses:

Some proposed regulatory interactions, particularly between Kr, Kr-h1, and other temporal factors like Imp, Chinmo, and E93, have not been thoroughly investigated, which weakens the support for the proposed model. Additional experimental validation is needed to confirm these relationships and strengthen the mechanistic framework.

Reviewer #1 (Public review):

Summary:

The manuscript by Garcia et al. describes how the expression of a respiratory chain alternative oxidase (AOX) from the tunicate Ciona intestinalis, capable of transferring electrons directly from reduced coenzyme Q (CoQ) to oxygen, is able to induce an increase in the mass of Drosophila melanogaster larvae and an accelerated development, especially when the larvae are kept at low temperatures. In order to explain this phenomenon, the paper addresses the modifications in the activity and levels of the 'canonical' electron transfer system (ETS), i.e., complexes I-IV and of the ATP synthase. In addition, the abundance of different metabolites as well as the NAD+/NADH ratios are measured, finding significant differences between the larvae.

Strengths:

The observations of differences in growth, body mass and food intake in the wt D. melanogaster larvae vs. those expressing the AOX transgene are solid. The evidence that mild uncoupling of the ETS might accelerate development of the fly larvae is convincing.

Weaknesses:

Some of the observations, especially those concerning the origin of the metabolic remodelling in AOX-expressing larvae, are left unexplained, and the argumentation is somewhat speculative. What the authors mean by "reconfiguration" of the mitochondrial electron transfer system is not clear. If this implies that there is an actual change in ETS function and/or structural organisation in the presence of AOX, this conclusion is not supported by the experimental data. In addition, the influence of AOX activity in the mitochondrial ETS system is tested in vitro in the presence of saturating concentrations of substrates. The real degree to which AOX activity is actually influencing ETS activity in vivo remains unknown.

Reviewer #2 (Public review):

Summary:

This manuscript presents intriguing findings about the role of alternative oxidase (AOX) from the tunicate Ciona intestinalis in accelerating growth and development when expressed in Drosophila melanogaster.

Strengths:

The study is overall well-constructed, including appropriate analysis. Likewise, the manuscript is written clearly and supported by high-quality figures. The present study provides valuable insights into AOX's role in Drosophila development. The paper attempts to explore a unique mechanism by which AOX influences Drosophila development, providing insights into mitochondrial respiration and its physiological effects. This is relevant for understanding mitochondrial dysfunction and potential therapeutic applications. The study employs a variety of approaches, including calorimetry, infrared thermography, and genetic analyses, to investigate AOX's impact on metabolism and development.

Weaknesses:

There are a number of methodological limitations and substantial gaps in the interpretation of the data presented, which reduces the strength of its conclusions. For instance, there is a misunderstanding of the non-proton motive nature of the AOX - it does not uncouple respiration, merely decouple it as it neither contributes to nor dissipates the proton motive force, in contrast to chemical uncouplers or proton uncouplers such as UCPs. The authors need to reassess their data in light of the above.

Reviewer #1 (Public review):

Summary:

The authors have used gene deletion approaches in zebrafish to investigate the function of genes of the hox clusters in pectoral fin "positioning" (but perhaps more accurately pectoral fin "formation").

Strengths:

The authors have employed a robust and extensive genetic approach to tackle an important and unresolved question.

The results are largely presented in a very clear way.

Weaknesses:

The Abstract suggests that no genetic evidence exists in model organisms for a role of Hox genes in limb positioning. There are, however, several examples in mouse and other models (both classical genetic and other) providing evidence for a role of Hox genes in limb position, which is elaborated on in the Introduction.

It would perhaps be more accurate to state that several lines of evidence in a range of model organisms (including the mouse) support a role for Hox genes in limb positioning. The author's work is not weakened by a more inclusive introduction that cites the current literature more comprehensively.

It would be helpful for the authors to make a clear distinction between "positioning" of the limb/fin and whether a limb/fin "forms" at all, independent of the relative position of this event along the body axis.

Discussion of why the zebrafish is sensitive to Hoxb loss with reference to the fin, but mouse Hoxb mutants do make a limb?

Is this down to exclusive expression of Hoxbs in the zebrafish pectoral fin forming region rather than a specific functional role of the protein? This is important as it has implications for the interpretation of results throughout the paper and could explain some apparently conflicting results.

Why is Hoxba more potent than Hoxbb? Is this because Hoxba has Hox4/5 present, while Hoxbb has only Hoxb5? Hoxba locus has retained many more Hox genes in cluster than hoxbb; therefore, one might expect to see greater redundancy in this locus).

Deletion of either Hoxa or Hoxd in the background of the Hoxba mutant does have some effect. Is this a reflection of protein function or expression dynamics of Hoxa/Hoxd genes?

Can we really be confident that there is a "transformation of pectoral fin progenitor cells into cardiac cells"?

The failure to repress Nkx2.5 in the posterior (pelvic fin) domain is clear, but have these cells actually acquired cardiac identity? They would be expected to express Tbx5a (or b) as cardiac precursors, but this domain does not broaden. There is no apparent expansion of the heart (field)/domain or progenitors beyond the 16 somite stage. The claimed "migration" of heart precursors in the mutant is not clear. The heart/cardiac domain that does form in the mutant is not clearly expanded in the mutant. The domain of cmlc2 looks abnormal in the mutant, but I am not convinced it is "enlarged" as claimed by the authors. The authors have not convincingly shown that "the cells that should form the pectoral fin instead differentiate into cardiac cells."

The only clear conclusion is the loss of pectoral fin-forming cells rather than these fin-forming cells being "transformed" into a new identity. It would be interesting to know what has happened to the cells of the pectoral fin-forming region in these double mutants.

It is not clear what the authors mean by a "converse" relationship between forelimb/pectoral fin and heart formation. The embryological relationship between these two populations is distinct in amniotes.

The authors show convincing data that RA cannot induce Tbx5a in the absence of Hob clusters, but I am not convinced by the interpretation of this result. The results shown would still be consistent with RA acting directly upstream of tbx5a, but merely that RA acts in concert with hox genes to activate tbx5a. In the absence of one or the other, Tbx5a would not be expressed. It is not necessary that RA and hoxbs act exclusively in a linear manner (i.e., RA regulates hoxb that in turn regulates tbx5a).

The authors have carried out a functional test for the function of hoxb6 and hoxb8 in the hemizygous hoxb mutant background. What is lacking is any expression analysis to demonstrate whether Hoxb6b or Hoxb8b are even expressed in the appropriate pectoral fin territory to be able to contribute to pectoral fin development, either in this assay or in normal pectoral fin development.

(The term "compensate" used in this section is confusing/misleading.)

The authors' confounding results described in Figures 6-7 are consistent with the challenges faced in other model organisms in trying to explore the function of genes in the hox cluster and the known redundancy that exists across paralogous groups and across individual clusters.

Given the experimental challenges in deciphering the actual functions of individual or groups of hox genes, a discussion of the normal expression pattern of individual and groups of hox genes (and how this may change in different mutant backgrounds) could be helpful to make conclusions about likely normal function of these genes and compensation/redundancy in different mutant scenarios.

Reviewer #2 (Public review):

Summary:

The authors of this manuscript performed a fascinating set of zebrafish mutant analyses on hox cluster deletion and pinpointed the cause of the pectoral fin loss in one combinatorial hox cluster mutant of Hoxba and Hoxbb.

Strengths:

The study is based on a variety of existing experimental tools that enabled the authors' past construction of hox cluster mutants, and is well-designed. The manuscript is well written to report the authors' findings on the mechanism that positions the pectoral fin.

Weaknesses:

The study does not focus on the other hox clusters other than ba and bb, and is confined to the use of zebrafish, as well as the comparison with existing reports from mouse experiments.

Reviewer #1 (Public review):

The manuscript by Ivan et al aimed to identify epitopes on the Abeta peptide for a large set of anti-Abeta antibodies, including clinically relevant antibodies. The experimental work was well done and required a major experimental effort, including peptide mutational scanning, affinity determinations, molecular dynamics simulations, IP-MS, WB, and IHC. Therefore, it is of clear interest to the field. The first part of the work is mainly based on an assay in which peptides (15-18-mers) based on the human Abeta sequence, including some containing known PTMs, are immobilized, thus preventing aggregation. Although some results are in agreement with previous experimental structural data (e.g. for 3D6), and some responses to disease-associated mutations were different when compared to wild-type sequences (e.g. in the case of Aducanumab) - which may have implications for personalized treatment - I have concerns about the lack of consideration of the contribution of conformation (as in small oligomers and large aggregates) in antibody recognition patterns. The second part of the study used full-length Abeta in monomeric or aggregated forms to further investigate the differential epitope interaction between Aducanumab, donanemab, and lecanemab (Figures 5-7). Interestingly, these results confirmed the expected preference of these antibodies for aggregated Abeta, thus reinforcing my concerns about the conclusions drawn from the results obtained using shorter and immobilized forms of Abeta. Overall, I understand that the work is of interest to the field and should be published without the need for additional experimental data. However, I recommend a thorough revision of the structure of the manuscript in order to make it more focused on the results with the highest impact (second part).

Reviewer #2 (Public review):

This paper investigates binding epitopes of different anti-Abeta antibodies. Background information on the clinical outcome of some of the antibodies in the paper, which might be important for readers to know, is lacking. There are no references to clinical outcomes from antibodies that have been in clinical trials. This paper would be much more complete if the status of the antibodies were included. The binding characteristics of aducanumab, donanemab, and lecanemab should be compared with data from clinical phase 3 studies.

Aducanumab was identified at Neurimmune in Switzerland and licensed to Biogen and Eisai. Aducanumab was retracted from the market due to a very high frequency of the side-effect amyloid-related imaging abnormalities-edema (ARIA-E). Gantenerumab was developed by Roche and had two failed phase 3 studies, mainly due to a high frequency of ARIA-E and low efficacy of Abeta clearance. Lecanemab was identified at Uppsala University, humanized by BioArctic, and licensed to Eisai, who performed the clinical studies. Eisai and Biogen are now marketing lecanemab as Leqembi on the world market. Donanemab was developed by Ely Lilly and is sold in the US as Kisunla.

Limitations:

(1) Conclusions are based on Abeta antigens that may not be the primary targets for some conformational antibodies like aducanumab and lecanemab. There is an absence of binding data for soluble aggregated species.

(2) Quality controls and characterization of different Abeta species are missing. The authors need to verify if monomers remain monomeric in the blocking studies for Figures 5 and 6.

(3) The authors should discuss the limitations of studying synthetic Abeta species and how aggregation might hide or reveal different epitopes.

(4) The authors should elaborate on the differences between synthetic Abeta and patient-derived Abeta. There is a potential for different epitopes to be available.

Reviewer #1 (Public review):

Summary:

The manuscript "Targeted Protein Degradation by KLHDC2 Ligands Identified by High Throughput Screening" by Zhou, H. et al. describes the development of a high-throughput FP-based screen and the identification of a KLHDC2 ligand from a small molecule library. A counter screen and other filtering criteria led to the identification of lead compounds that contained a tetrahydroquinoline scaffold. Commercially available analogs (52 compounds) that shared this scaffold were characterized by a KLHDC2 competitive binding assay. Optimized compounds were obtained that demonstrated improved potency and increased binding affinity by SPR. Docking of a lead candidate (compound 6) suggested it bound at a distal lipophilic site within the SelK binding pocket of KLHDC2. Based on this model, the authors then synthesized PROTACs that linked the KLHDC2 binder to a BRD4-binding molecule, JQ1. These PROTAC candidates possessed different linker configurations, and PROTAC 8 was able to cause BRD4 degradation in cells, with a half-maximal degradation concentration (DC50) of 80 nM. The authors demonstrate the identification and characterization of small-molecule KLHDC2 ligands that can be used to generate PROTACs that result in BRD4 degradation in cells.

Strengths:

The study by Zhou, H. et al. expands the E3 ligase toolkit by targeting KLHDC2 to identify ligands for PROTAC development, which has predominantly relied on VHL and CRBN. This was accomplished using a described FP-based high-throughput screening strategy (high Z' values in 1536 well format). Both target-specific and counter-specific assays were performed, along with subsequent stringent follow-up assays designed to address non-specific binding/specificity concerns. Label-free direct binding validations by SPR were used to determine binding affinity/kinetics. A strength of the study is the characterization of the interaction between candidate compounds and KLHDC2 versus related KEAP1.

Structural insight into the potential mode of binding was inferred by computational docking studies of the newly discovered KLHDC2 ligands. This was performed to identify where the identified scaffolds could be modified by linker incorporation for the design of PROTACs. The computational predictions were evaluated by linking a solvent-exposed site on the KLHDC2 ligand to JQ1. Three linkers were tested, and two compounds were found to result in BRD4 degradation in cells by HiBiT degradation assay and western blot. These findings demonstrate the feasibility of these compounds for the design of PROTAC-based degraders.

The authors present compelling KLHDC2 binding data for their lead compounds and demonstrate degradation of a target using a PROTAC strategy. Accordingly, the screening approach and compounds identified are likely to be of interest to the field and are likely to be generalizable to other PROTAC targets of interest.

Weaknesses:

The specificity of compounds for KLHDC2 was assessed by using a counter screen against KEAP1 and in vitro binding assays. However, off-target effects might occur in a cellular context, which weren't fully explored in the study. Notably, the authors do not demonstrate that the degradation induced by their PROTACs in cells is KLHDC2-dependent. A requirement for KLHDC2-mediated degradation could be evaluated, for example, by using knockout/knockdown of KLHDC2, or other means, to demonstrate specificity. Addressing specificity is deemed important to evaluate the proposed PROTAC mechanism of action in a cellular context that results in the degradation of BRD4. Specificity is important when considering the utility of these new compounds for PROTAC design.

Additional rationale behind the selection of linkers used to generate candidate PROTACs would be informative and would benefit from additional discussion and/or citation. The reasons for the lack of activity, such as for compound 9, were not fully explored or discussed, such as whether complex assembly is potentially affected by linker choice. Perhaps related to this point, the authors note that a trifluoromethoxy group increased the binding affinity of compound 6. However, the subsequent docking analysis revealed this moiety to be solvent-exposed. The relationship between this site of functionalization, linker selection, and the resulting binding affinity or effect on DC50 was not clear and/or could be developed further.

Minor issues related to the presentation of the manuscript include sections that would benefit from either additional citation and/or description, such as the KI-696 inhibitor used and the BRD4 HiBiT degradation assay that was used to assess PROTAC potency. Figure captions should be reviewed to ensure that the number of independent experiments is indicated, and what data points and error bars represent, as these are not indicated in several figures. BRD4 levels were quantified in 4E; however, error/reproducibility (n) is not indicated.

Reviewer #2 (Public review):

PROTACs are a class of small molecules that induce an interaction between a target protein and a ubiquitin ligase, thereby leading to the target protein's ubiquitination and subsequent proteasomal degradation. Given that the vast majority of PROTACs rely on the cereblon and VHL ubiquitin ligases, a major goal within this field has been to identify and develop ligands for additional ubiquitin ligases, in particular those whose expression affords tissue or subcellular specificity or those whose structure allows them to degrade targets that are otherwise incompatible with cereblon or VHL.

In this work, Zhou and colleagues from the Bollong group at Scripps utilize a high-throughput fluorescence polarization screen of >350,000 compounds to identify and optimize a novel ligand for KLHDC2, a ubiquitin ligase which had previously been discovered to be capable of proximity-induced degradation of target proteins. Zhou et al go on to show that this ligand can be used as the basis for PROTACs capable of degrading BRD4 in a cell line. Of note, prior to this paper, three other groups had also developed ligands to KLHDC2 and used them to generate active PROTACs. Interestingly, docking studies by Zhou suggest that their compound may bind to a different region of the KLHDC2's kelch domain.

The major strengths of this work are its brevity and the clarity of the writing and figures. Their claim that they have discovered a ligand for KLHDC2, which can be used to develop BRD4-degrading PROTACs, is well-supported by their findings from the screen, SPR, and cellular assays. The weakness of the work then, is not so much relevant to the paper at hand but rather stems from the fact that their story leaves me wanting to know more. Indeed, there are a number of interesting experiments that we need as a field in order to assess 1) how generalizable their findings are across cell lines and targets, and 2) how this new KLHDC2 ligand stacks up against the other recently discovered ligands for KLDHC2 as well as the existing standards, cereblon and VHL.

Nonetheless, Zhou and colleagues provide a valuable addition to the emerging repertoire of KLHDC2 ligands, and I'm certain that with time, we will come to understand what ligands work best for KLHDC2-based PROTACs and how they compare to the growing set of ubiquitin ligases in our armamentarium.

Reviewer #1 (Public review):

The study aims to determine the role of Slit-Robo signaling in the development and patterning of cardiac innervation, a key process in heart development. Despite the well-studied roles of Slit axon guidance molecules in the development of the central nervous system, their roles in the peripheral nervous system are less clear. Thus, the present study addresses an important question. The study uses genetic knockout models to investigate how Slit2, Slit3, Robo1, and Robo2 contribute to cardiac innervation.

Using constitutive and cell type-specific knockout mouse models, they show that the loss of endothelial-derived Slit2 reduces cardiac innervation. Additionally, Robo1 knockout, but not Robo2 knockout, recapitulated the Slit2 knockout effect on cardiac innervation, leading to the conclusion that Slit2-Robo1 signaling drives sympathetic innervation in the heart. Finally, the authors also show a reduction in isoproterenol-stimulated heart rate but not basal heart rate in the absence of endothelial Slit2.

The conclusions of this paper are mostly well supported by the data, but some should be modified to account for the study's limitations and discussed in the context of previous literature.

(1) It is well established that Slit ligands undergo proteolytic cleavage, generating N- and C-terminal fragments with distinct biological functions. Full-length Slit proteins and their fragments differ in cell association, with the N-terminal fragment typically remaining membrane-bound, while the C-terminal fragment is more diffusible. This distinction is crucial when evaluating the role of Slit proteins secreted by different cell types in the heart. However, this study does not examine or discuss the specific contributions of different Slit2 fragments, limiting its mechanistic insight into how Slit2 regulates cardiac innervation.

(2) The endothelial-specific deletion of Slit2 leads to its loss in endothelial cells across various organs and tissues in the developing embryo. Therefore, the phenotypes observed in the heart may be influenced by defects in other parts of the embryo, such as the CNS or sympathetic ganglia, and this possibility cannot be ruled out.

Reviewer #2 (Public review):

The aims of investigating Slit-Robo signaling in cardiac innervation were achieved by the experiments designed. While questions remain regarding signal regulation and interplay between established axon guidance signals and further role of other Slit ligands and Robo expression in endothelium, the results strongly support the conclusions drawn.

Writing and presentation are easy to follow and well structured, Appropriate controls are used, statistical analysis applied appropriately, and experiments directly test aims following a logical story.

The authors demonstrate a novel mechanism for Slit-Robo signaling in cardiac sympathetic innervation. The data establishes a framework for future studies.

Recommendations:

Further assessment of interplay between Slit ligands as well as other signaling pathways (Semaphorin, NGF, etc) could be investigated. Is it possible to rescue the phenotype by modulation of other signaling pathways? Can combined Slit2/Slit3 KO rescue? Additionally, as the authors state, conditional Robo1 knockouts will be important to validate the findings of constitutive knockout.

Reviewer #1 (Public review):

Summary:

Lysosomal damage is commonly found in many diseases including normal aging and age-related disease. However, the transcriptional programs activated by lysosomal damage have not been thoroughly characterized. This study aimed to investigate lysosome damage-induced major transcriptional responses and the underlying signaling basis. The authors have convincingly shown that lysosomal damage activates a ubiquitination-dependent signaling axis involving TAB, TAK1, and IKK, which culminates in the activation of NF-kB and subsequent transcriptional upregulation of pro-inflammatory genes and pro-survival genes. Overall, the major aims of this study were successfully achieved.

Strengths:

This study is well-conceived and strictly executed, leading to clear and well-supported conclusions. Through unbiased transcriptomics and proteomics screens, the authors identified NF-kB as a major transcriptional program activated upon lysosome damage. TAK1 activation by lysosome damage-induced ubiquitination was found to be essential for NF-kB activation and MAP kinase signaling. The transcriptional and proteomic changes were shown to be largely driven by TAK1 signaling. Finally, the TAK1-IKK signaling was shown to provide resistance to apoptosis during lysosomal damage response. The main signaling axis of this pathway was convincingly demonstrated.

Weaknesses:

One weakness was the claim of K63-linked ubiquitination in lysosomal damage-induced NF-kB activation. While it was clear that K63 ubiquitin chains were present on damaged lysosomes, no evidence was shown in the current study to demonstrate the specific requirement of K63 ubiquitin chains in the signaling axis being studied. Clarifying the roles of K63-linked versus other types of ubiquitin chains in lysosomal damage-induced NF-kB activation may improve the mechanistic insights and overall impact of this study.

Another weakness was that the main conclusions of this study were all dependent on an artificial lysosomal damage agent. It will be beneficial to confirm key findings in other contexts involving lysosomal damage.

Reviewer #2 (Public review):

Summary:

Endo et al. investigate the novel role of ubiquitin response upon lysosomal damage in activating cellular signaling for cell survival. The authors provide a comprehensive transcriptome and proteome analysis of aging-related cells experiencing lysosomal damage, identifying transcription factors involved in transcriptome and proteome remodeling with a focus on the NF-κB signaling pathway. They further characterized the K63-ubiquitin-TAB-TAK1-NF-κB signaling axis in controlling gene expression, inflammatory responses, and apoptotic processes.

Strengths:

In the aging-related model, the authors provide a comprehensive transcriptome and characterize the K63-ubiquitin-TAB-TAK1-NF-κB signaling axis. Through compelling experiments and advanced tools, they elucidate its critical role in controlling gene expression, inflammatory responses, and apoptotic processes.

Weaknesses:

The study lacks deeper connections with previous research, particularly:<br /> • The established role of TAB-TAK1 in AMPK activation during lysosomal damage<br /> • The potential significance of TBK1 in NF-κB signaling pathways

Reviewer #3 (Public review):

Summary:

The response to lysosomal damage is a fast-moving and timely field. Besides repair and degradation pathways, increasing interest has been focusing on damaged-induced signaling. The authors conducted both transcriptomics and proteomics to characterize the cellular response to lysosomal damage. They identify a signaling pathway leading to activation of NFkappaB. Based on this and supported by Western blot and microscopy data, the authors nicely show that TAB2/3 and TAK1 are activated at damaged lysosomes and kick off the pathway to alter gene expression, which induces cytokines and protect from cell death. TAB2/3 activation is proposed to occur through K63 ubiquitin chain formation. Generally, this is a careful and well conducted study that nicely delineates the pathway under lysosomal stress. The "omics" data serves as a valuable resource for the field. More work should be invested into how TAB2/3 are activated at the damaged lysosomes, also to increase novelty in light of previous reports.

Strengths:

Generally, this is a careful and well-conducted study that nicely delineates the pathway under lysosomal stress. The "omics" data serves as a valuable resource for the field.

Weaknesses:

More work should be invested into how TAB2/3 are activated at the damaged lysosomes, also to increase novelty in light of previous reports. Moreover, different damage types should be tested to probe relevance for different pathophysiological conditions.

Suggestions:

(1) A recent paper claims that NFkappaB is activated by Otulin/M1 chains upon lysosome damage through TBK1 (PMID: 39744815). In contrast, Endo et al. nicely show that ubiquitylation is needed (shown by TAK-243) for NFkB activation but only have correlative data to link it specifically to K63 chains. On page 15, line 11, the authors even argue a "potential" involvement of K63. This point should be better dealt with. Can the authors specifically block K63 formation? K63R overexpression or swapping would be one way. Is the K63 ligase ITCH involved (PMID: 38503285) or any other NEDD4-like ligase? This could be compared to LUBAC inhibition. Also, the point needs to be dealt with more controversially in the discussion as these are alternative claims (M1 vs K63, TAB vs TBK1).

(2) It would be interesting to know what the trigger is that induces the pathway. Lipid perturbation by LLOMe is a good model, but does activation also occur with GPN (osmotic swelling) or lipid peroxidation (oxidative stress) that may be more broadly relevant in a pathophysiological way? Moreover, what damage threshold is needed? Does loss of protons suffice? Can activation be induced with a Ca2+ agonist in the absence of damage?

(3) The authors nicely define JNK and p38 activation. This should be emphasized more, possibly also in the abstract, as it may contribute to the claim of increased survival fitness.

Reviewer #1 (Public review):

Summary:

This work by Govorunova et al. identified three naturally blue-shifted channelrhodopsins (ChRs) from ancyromonads, namely AnsACR, FtACR, and NlCCR. The phylogenetic analysis places the ancyromonad ChRs in a distinct branch, highlighting their unique evolutionary origin and potential for novel applications in optogenetics. Further characterization revealed the spectral sensitivity, ionic selectivity, and kinetics of the newly discovered AnsACR, FtACR, and NlCCR. This study also offers valuable insights into the molecular mechanism underlying the function of these ChRs, including the roles of specific residues in the retinal-binding pocket. Finally, this study validated the functionality of these ChRs in both mouse brain slices (for AnsACR and FtACR) and in vivo in Caenorhabditis elegans (for AnsACR), demonstrating the versatility of these tools across different experimental systems.

In summary, this work provides a potentially valuable addition to the optogenetic toolkit by identifying and characterizing novel blue-shifted ChRs with unique properties.

Strengths:

This study provides a thorough characterization of the biophysical properties of the ChRs and demonstrates the versatility of these tools in different ex vivo and in vivo experimental systems. The mutagenesis experiments also revealed the roles of key residues in the photoactive site that can affect the spectral and kinetic properties of the channel.

Weaknesses:

While the novel ChRs identified in this work are spectrally blue-shifted, there still seems to be some spectral overlap with other optogenetic tools. The authors should provide more evidence to support the claim that they can be used for multiplex optogenetics and help potential end-users assess if they can be used together with other commonly applied ChRs. Additionally, further engineering or combination with other tools may be required to achieve truly orthogonal control in multiplexed experiments.

In the C. elegans experiments, partial recovery of pharyngeal pumping was observed after prolonged illumination, indicating potential adaptation. This suggests that the effectiveness of these ChRs may be limited by cellular adaptation mechanisms, which could be a drawback in long-term experiments. A thorough discussion of this challenge in the application of optogenetics tools would prove very valuable to the readership.

Reviewer #2 (Public review):

Summary:

Govorunova et al present three new anion opsins that have potential applications in silencing neurons. They identify new opsins by scanning numerous databases for sequence homology to known opsins, focusing on anion opsins. The three opsins identified are uncommonly fast, potent, and are able to silence neuronal activity. The authors characterize numerous parameters of the opsins.

Strengths:

This paper follows the tradition of the Spudich lab, presenting and rigorously characterizing potentially valuable opsins. Furthermore, they explore several mutations of the identified opsin that may make these opsins even more useful for the broader community. The opsins AnsACR and FtACR are particularly notable, having extraordinarily fast onset kinetics that could have utility in many domains. Furthermore, the authors show that AnsACR is usable in multiphoton experiments having a peak photocurrent in a commonly used wavelength. Overall, the author's detailed measurements and characterization make for an important resource, both presenting new opsins that may be important for future experiments, and providing characterizations to expand our understanding of opsin biophysics in general.

Weaknesses:

First, while the authors frequently reference GtACR1, a well-used anion opsin, there is no side-by-side data comparing these new opsins to the existing state-of-the-art. Such comparisons are very useful to adopt new opsins.

Next, multiphoton optogenetics is a promising emerging field in neuroscience, and I appreciate that the authors began to evaluate this approach with these opsins. However, a few additional comparisons are needed to establish the user viability of this approach, principally the photocurrent evoked using the 2p process, for given power densities. Comparison across the presented opsins and GtACR1 would allow readers to asses if these opsins are meaningfully activated by 2P.

Reviewer #3 (Public review):

Summary:

The authors aimed to develop Channelrhodopsins (ChRs), light-gated ion channels, with high potency and blue action spectra for use in multicolor (multiplex) optogenetics applications. To achieve this, they performed a bioinformatics analysis to identify ChR homologues in several protist species, focusing on ChRs from ancyromonads, which exhibited the highest photocurrents and the most blue-shifted action spectra among the tested candidates. Within the ancyromonad clade, the authors identified two new anion-conducting ChRs and one cation-conducting ChR. These were characterized in detail using a combination of manual and automated patch-clamp electrophysiology, absorption spectroscopy, and flash photolysis. The authors also explored sequence features that may explain the blue-shifted action spectra and differences in ion selectivity among closely related ChRs.

Strengths:

A key strength of this study is the high-quality experimental data, which were obtained using well-established techniques such as manual patch-clamp and absorption spectroscopy, complemented by modern automated patch-clamp approaches. These data convincingly support most of the claims. The newly characterized ChRs expand the optogenetics toolkit and will be of significant interest to researchers working with microbial rhodopsins, those developing new optogenetic tools, as well as neuro- and cardioscientists employing optogenetic methods.

Weaknesses:

This study does not exhibit major methodological weaknesses. The primary limitation of the study is that it includes only a limited number of comparisons to known ChRs, which makes it difficult to assess whether these newly discovered tools offer significant advantages over currently available options. Additionally, although the study aims to present ChRs suitable for multiplex optogenetics, the new ChRs were not tested in combination with other tools. A key requirement for multiplexed applications is not just spectral separation of the blue-shifted ChR from the red-shifted tool of interest but also sufficient sensitivity and potency under low blue-light conditions to avoid cross-activation of the respective red-shifted tool. Future work directly comparing these new ChRs with existing tools in optogenetic applications and further evaluating their multiplexing potential would help clarify their impact.

Reviewer #1 (Public review):

Summary:

The authors assess the role of map3k1 in adult Planaria through whole body RNAi for various periods of time. The authors' prior work has shown that neoblasts (stem cells that can regenerate the entire body) for various tissues are intermingled in the body. Neoblasts divide to produce progenitors that migrate within a "target zone" to the "differentiated target tissues" where they differentiate into a specific cell type. Here the authors show that map3k1-i animals have ectopic eyes that form along the "normal" migration path of eye progenitors (Fig. 1), ectopic neurons and glands along the AP axis (Fig. 2) and pharynx in ectopic anterior positions (Fig. 3). The rest of the study show that positional information is largely unaffected by loss of map3k1 (Fig. 4,5). However, loss of map3k1 leads to premature differentiated of progenitors along their normal migratory route (Fig. 6). They also show that an ill-defined "long-term" whole body depletion of map3k1 results in mis-specified organs and teratomas.

Strengths:

(1) The study has appropriate controls, sample sizes and statistics.<br /> (2) The work appears to be high-quality.<br /> (3) The conclusions are supported by the data.<br /> (4) Planaria is a good system to analyze the function of map3k1, which exists in mammals but not in other invertebrates.

Weaknesses:

(1) The paper is largely descriptive with no mechanistic insights.<br /> (2) Given the severe phenotypes of long-term depletion of map3k1, it is important that this exact timepoint is provided in the methods, figures, figure legends and results.<br /> (3) Fig. 1C, the ectopic eyes are difficult to see, please add arrows.<br /> (4) line 217 - why does the n=2/12 animals not match the values in Fig. 3B, which is 11/12 and 12/12. The numbers don't add up. Please correct/explain.<br /> (5) Figure panels do not match what is written in the results section. There is no Fig. 6E. Please correct.

Reviewer #2 (Public review):

Summary:<br /> The flatworm planarian Schmidtea mediterranea is an excellent model for understanding cell fate specification during tissue regeneration and adult tissue maintenance. Planarian stem cells, known as neoblasts, are continuously deployed to support cellular turnover and repair tissues damaged or lost due to injury. This reparative process requires great precision to recognize the location, timing, and cellular fate of a defined number of neoblast progeny. Understanding the molecular mechanisms driving this process could have important implications for regenerative medicine and enhance our understanding of how form and function are maintained in long-lived organisms such as humans. Unfortunately, the molecular basis guiding cell fate and differentiation remains poorly understood.

In this manuscript, Canales et al. identified the role of the map3k1 gene in mediating the differentiation of progenitor cells at the proper target tissue. The map3k1 function in planarians appears evolutionarily conserved as it has been implicated in regulating cell proliferation, differentiation, and cell death in mammals. The results show that the downregulation of map3k1 with RNAi leads to spatial patterning defects in different tissue types, including the eye, pharynx, and the nervous system. Intriguingly, long-term map3k1-RNAi resulted in ectopic outgrowths consistent with teratomas in planarians. The findings suggest that map3k1 mediates signaling, regulating the timing and location of cellular progenitors to maintain correct patterning during adult tissue maintenance.

Strengths:

The authors provide an entry point to understanding molecular mechanisms regulating progenitor cell differentiation and patterning during adult tissue maintenance.

The diverse set of approaches and methods applied to characterize map3k1 function strengthens the case for conserved evolutionary mechanisms in a selected number of tissue types. The creativity using transplantation experiments is commendable, and the findings with the teratoma phenotype are intriguing and worth characterizing.

Weaknesses:

The article presents a provocative idea related to the importance of positional control for organs and cells, which is at least in part regulated by map3k1. Nonetheless, the role of map3k1 or its potential interaction with regulators of the anterior-posterior, mediolateral axes, and PCGs is somewhat superficial. The authors could elaborate or even speculate more in the discussion section and the different scenarios incorporating these axial modulators into the map3k1 model presented in Figure 8.

The article can be improved by addressing inconsistencies and adding details to the results, including the main figures and supplements. This represents one of the most significant weaknesses of this otherwise intriguing manuscript. Below are some examples of a few figures, but the authors are expected to pay close attention to the remaining figures in the paper.

Details associated with the number of animals per experiment, statistical methods used, and detailed descriptions of figures appear inconsistent or lacking in almost all figures. In some instances, the percentage of animals affected by the phenotype is shown without detailing the number of animals in the experiment or the number of repeats. Figures and their legends throughout the paper lack details on what is represented and sometimes are mislabeled or unrelated. Specifically, the arrows in Figure 1A are different colors. Still, no reasoning is given for this, and in the exact figure, the top side (1A) shows the percentages and the number of animals below. Conversely, in Figures 1B, C, and D, no details on the number of animals or percentages are shown, nor an explanation of why opsin was used in Figure 1A but not 1B. Is Figure 1B missing an image for the respective control? Figure 1C needs details regarding what the two smaller boxes underneath are. Figure 1C could use an AP labeling map in 10 days (e.g., AP6 has one optic cup present). Figure 1C and F counts do not match. In Figure 1C, we do not know the number of animals tested, controls used, the scale bar sizes in the first two images, nor the degree of magnification used despite the pharynx region appearing magnified in the second image. Figure 1C is also shown out of chronological order; 36 days post RNAi is shown before 10 days post RNAi. Moreover, the legends for Figures 1C and 1D are swapped.

Additionally, Figure 1F and many other figures throughout the paper lack overall statistical considerations. Furthermore, Figure 1F has three components, but only one is labeled. Labeling each of them individually and describing them in the corresponding figure legend may be more appropriate.

Figure 2C shows images of gene expression for two genes, but the counts are shown for only one in Figure 2D. It is challenging to follow the author's conclusions without apparent reasoning and by only displaying quantitative considerations for one case but not the other. These inconsistencies are also observed in different figures. In Figure 2D, 24/24 animals were reported to show the phenotype, but only eight were counted (is there a reason for this?). In Figure 2E, the expression for three genes is shown, with some displaying anterior and posterior regions while others only show the anterior picture. Is there a particular reason for this? Also, in Figure 2F, the counts are shown for only the posterior region of two genes out of the three displayed in Figure 2E. It is unclear why the authors do not show counts for the anterior areas considered in Figure 2E. Furthermore, the legend for Figure 2D is missing, and the legend for 2F is mislabeled as a description for Figure 2D.

Supplement Figure 1 B reports data up to 6 weeks, but no text in the manuscript or supplement mentions any experiment going up to 6 weeks. There are no statistics for data in Supplement Figure 1E. Any significance between groups is unclear.

Reviewer #1 (Public review):

Summary:

This manuscript investigated the mechanism underlying boundary formation necessary for proper separation of vestibular sensory end organs. In both chick and mouse embryos, it was shown that a population of cells abutting the sensory (marked by high Sox2 expression) /nonsensory cell populations (marked by Lmx1a expression) undergo apical expansion, elongation, alignment and basal constriction to separate the lateral crista (LC) from the utricle. Using Lmx1a mouse mutant, organ cultures, pharmacological and viral-mediated Rock inhibition, it was demonstrated that the Lmx1a transcription factor and Rock-mediated actomyosin contractility is required for boundary formation and LC-utricle separation.

Strengths:

Overall, the morphometric analyses were done rigorously and revealed novel boundary cell behaviors. The requirement of Lmx1a and Rock activity in boundary formation was convincingly demonstrated.

Weaknesses:

However, the precise roles of Lmx1a and Rock in regulating cell behaviors during boundary formation were not clearly fleshed out. For example, phenotypic analysis of Lmx1a was rather cursory; it is unclear how Lmx1a, expressed in half of the boundary domain, control boundary cell behaviors and prevent cell mixing between Lmx1a+ and Lmx1a- compartments? Well-established mechanisms and molecules for boundary formation were not investigated (e.g. differential adhesion via cadherins, cell repulsion via ephrin-Eph signaling). Moreover, within the boundary domain, it is unclear whether apical multicellular rosettes and basal constrictions are drivers of boundary formation, as boundary can still form when these cell behaviors were inhibited. Involvement of other cell behaviors, such as radial cell intercalation and oriented cell division, also warrant consideration. With these lingering questions, the mechanistic advance of the present study is somewhat incremental.

Reviewer #2 (Public review):

Summary:

Chen et al. describe the mechanisms that separate the common pan-sensory progenitor region into individual sensory patches, which presage the formation of the sensory epithelium in each of the inner ear organs. By focusing on the separation of the anterior and then lateral cristae, they find that long supra-cellular cables form at the interface of the pan-sensory domain and the forming cristae. They find that at these interfaces, the cells have a larger apical surface area, due to basal constriction, and Sox2 is down-regulated. Through analysis of Lmx1 mutants, the authors suggest that while Lmx1 is necessary for the complete segregation of the sensory organs, it is likely not necessary for the initial boundary formation, and the down-regulation of Sox2.

Strengths:

The manuscript adds to our knowledge and provides valuable mechanistic insight into sensory organ segregation. Of particular interest are the cell biological mechanisms: The authors show that contractility directed by ROCK is important for the maintenance of the boundary and segregation of sensory organs.

Weaknesses:

The manuscript would benefit from a more in-depth look at contractility - the current images of PMLC are not too convincing. Can the authors look at p or ppMLC expression in an apical view? Are they expressed in the boundary along the actin cables? Does Y-27362 inhibit this expression?

The authors suggest that one role for ROCK is the basal constriction. I was a little confused about basal constriction. Are these the initial steps in the thinning of the intervening non-sensory regions between the sensory organs? What happens to the basally constricted cells as this process continues?

The steps the authors explore happen after boundaries are established. This correlates with a down-regulation of Sox2, and the formation of a boundary. What is known about the expression of molecules that may underlie the apparent interfacial tension at the boundaries? Is there any evidence for differential adhesion or for Eph-Ephrin signalling? Is there a role for Notch signalling or a role for Jag1 as detailed in the group's 2017 paper?

A comment on whether cellular intercalation/rearrangements may underlie some of the observed tissue changes.

The change in the long axis appears to correlate with the expression of Lmx1a (Fig 5d). The authors could discuss this more. Are these changes associated with altered PCP/Vangl2 expression?

Reviewer #3 (Public review):

Summary:

Lmx1a is an orthologue of apterous in flies, which is important for dorsal-ventral border formation in the wing disc. Previously, this research group has described the importance of the chicken Lmx1b in establishing the boundary between sensory and non-sensory domains in the chicken inner ear. Here, the authors described a series of cellular changes during border formation in the chicken inner ear, including alignment of cells at the apical border and concomitant constriction basally. The authors extended these observations to the mouse inner ear and showed that these morphological changes occurred at the border of Lmx1a positive and negative regions, and these changes failed to develop in Lmx1a mutants. Furthermore, the authors demonstrated that the ROCK-dependent actomyosin contractility is important for this border formation and blocking ROCK function affected epithelial basal constriction and border formation in both in vitro and in vivo systems.

Strengths:

The morphological changes described during border formation in the developing inner ear are interesting. Linking these changes to the function of Lmx1a and ROCK dependent actomyosin contractile function are provocative.

Weaknesses:

There are several outstanding issues that need to be clarified before one could pin the morphological changes observed being causal to border formation and that Lmx1a and ROCK are involved.

Reviewer #1 (Public review):

Summary:

In this manuscript, Taujale et al describe an interdisciplinary approach to mine the human channelome and further discover orthologues across diverse organisms, culminating in delineating co-conserved patterns in an example ion channel: CALHM. Overall, this paper comes in two sections, one where 419 human ion channels and 48,000+ channels from diverse organisms are found through a multidisciplinary data mining approach, and a second where this data is used to find co-conserved sequences, whose functional significance is validated via experiments on CALHM1 and CALHM6. Overall, this is an intriguing data-first approach to better understand even understudied ion channels like CALHM6. However, more needs to be done to pull this story together into a single, coherent narrative.

Strengths:

This manuscript takes advantage of modern-day LLM tools to better mine the literature for ion channel sequences in humans and other species with orthologous ion channel sequences. They explore the 'dark channome' of understudied ion channels to better reveal the information evolution has to tell us about our own proteins, and illustrate the information this provides access to in experimental studies in the final section of the paper. Finally, they provide a wealth of information in the supplementary tables (in the form of Excel spreadsheets) for others to explore. Overall, this is a creative approach to a wide-reaching problem that can be applied to other families of proteins.

Weaknesses:

Overall, while a considerable amount of work has been done for this manuscript, the presentation, both in terms of writing and figures, leaves much to be desired. One can imagine a story that clearly describes the need for a better-curated sequence database of ion channels, and clearly describes how existing resources fall short, but here this is not very clearly illustrated.

One question that arises with the part of the manuscript that discusses the identification and classification of ion channels is whether they plan to make these sequences available to the wider public. For the 419 human sequences, making a small database to share this result so that these sequences can be easily searched and downloaded would be desirable. There are a variety of acceptable formats for this: GitHub/figshare/zenodo/university website that allows a wider community to access their hard work. The authors have included enough information in the supplementary tables that this could be done by a motivated reader, but providing such a resource would greatly expand the impact of this paper. The same question can be asked of the 48,000+ ion channels from diverse organisms. For these, one is even worried that these are not properly sequenced genes? What checks have been done to confirm this? Uniport contains a good deal of unreviewed sequences, especially from single-celled organisms. Potentially, this is covered in the sentence in the Methods: "Finally, the results obtained from both the full-length and pore domains were retained as true orthologous relationships to remove extraneous hits." But this process could be discussed in more detail, clearly illustrating that the risk of gene duplicates and fragments in this final set of ion channel orthologues has been avoided. Related to this, does this analysis include or exclude isoforms?

Another aspect of the identification and classification of ion channel genes that could be improved is the figures for this section. One is relatively used to seeing trees as shown in Figures 3 and 4, which show relationships between genes as distances or evolutionary relationships. The decision to show the families of ion channels in Figure 1 as pie charts within a UMAP embedding is intriguing but somewhat non-intuitive and difficult to understand. Illustrating these results with a standard tree-like visualization of the relationship of these channels to each other would be preferred.

One aspect of the pie-chart/UMAP visualization that works well is the highlighting of the 'dark' ion channels according to the status as designated by IDG, which highlights a strength of this whole paper. However, throughout the paper, this could be emphasized more as the key advantage of this approach and how this or similar approaches could be used for other families of proteins. Specifically, in the initial statement describing 'light' vs 'dark channels', the importance of this distinction and the historical preference in science to study that which has already been studied can be discussed more, even including references to other studies that take this kind of approach. An example of a relevant reference here is to the Structural Genomics Consortium and its goals to achieve structures of proteins for which functions may not be well-characterized. Furthermore, this initial statement mentioning 'light channels' was initially confusing -- does this mean light-sensing channels? As one reads on this is clearly not the case, but for such an important central focus of this paper, these kinds of misunderstandings do not serve the authors well. Clarifying these motivations throughout the entire paper would strengthen it considerably.

Additionally, since the authors have generated this UMAP visualization, it would be interesting to understand how the human vs orthologue gene sets compare in this space. Furthermore, Figure 1, for just the human analysis, should say more clearly that this is an analysis of the human gene set and include more of the information in the text: 419 human ion channel sequences, 75 sequences previously unidentified, 4 major groups and 55 families, 62 outliers, etc. Clearer visualizations of these categories and numbers within the UMAP (and newly included tree) visualization would help guide the reader to better understand these results.

One of the most peculiar aspects of this paper is that it feels like two papers, one about better documenting the ion channel genes across species, and another with well-executed experiments on CALHM channels. One suggestion for how to link these two sections together better is to show that previous methods to analyze conserved residues in CALHM were significantly lacking. What results would that give? Why was this not enough? Were there just not enough identified CALHM orthologues to give strong signals in conservation analysis?

Some of the analysis pipeline is unclear. Specifically, the RAG analysis seems critical, but it is unclear how this works - is it on top of the GPT framework and recursively inquires about the answer to prompts? Some example prompts would be useful to understand this. Furthermore, the existence of 76 auxiliary non-pore containing 'ion channel' genes in this analysis is a little confusing, as it seems a part of the pipeline is looking for pore-lining residues. Furthermore, how many of these are picked up in the larger orthologues search? Are these harder to perform checks on to ensure that they are indeed ion channel genes? A further discussion of the choice to include these auxiliary sequences would be relevant. This could just be further discussion of the literature that has decided to do this in the past.

Overall, this manuscript is a valuable contribution to the field, but it requires a few main things to make it truly useful. Namely, how has this approach really improved the ability to identify conserved residues over a less-involved approach? A better description of their methods and results is required in the first section of the paper, as well as some cosmetic improvements.

Reviewer #2 (Public review):

Summary:

In this paper, the authors defined the "channelome," consisting of 419 predicted human ion channels as well as 48,000 ion channel orthologs from other organisms. Using this information, the ion channels were clustered into groups, which can potentially be used to make predictions about understudied ion channels in the groups. The authors then focused on the CALHM ion channel family, mutating conserved residues and assessing channel function.

Strengths:

The curation of the channelome provides an excellent resource for researchers studying ion channels. Supplemental Table 1 is well organized with an abundance of useful information.

Weaknesses:

There are substantial concerns regarding the analysis of the CALHM channels as detailed below.

(1) There are significant problems with the methodology used for the electrophysiology studies. Pulse protocol is used to assess the current voltage relationship (-100 to +140 mV), which extends far beyond the physiological range; currents for the mutant channels were only assessed at +120 mV. It is also unclear why a holding potential of 0 mV was used for CALHM6 recordings; the channel is already open at this voltage (and in Figure 4, only n = 3 for CALHM6). Further, proper controls were not performed. Inhibitors such as Gd3+ can be used to ensure that only CALHM currents are being measured.

(2) In line 334, the authors state that "expression levels of wild-type proteins and mutants are comparable." However, Western blots showing CALHM protein abundance (Supplementary Figure 3) are not of acceptable quality - in the top blot, WT CALHM1 can't even be seen. Representative blots were not shown for all mutants, and there was no effort to determine if levels were statistically significant compared to the wild-type control. Even if there is more or less protein, what does this mean? The protein could be in an intracellular compartment and not at the plasma membrane. In mammalian cells, CALHM6 is localized to intracellular compartments and only translocates to the plasma membrane upon activating stimulus (Danielli et al, EMBO J, 2023). Thus, if CALHM6 is only intracellular, the protein amount would not change, but the measured current would. Abundant intracellular CALHM1 has also been observed in mammalian cells transfected with this protein (Dreses-Werringloer et al., Cell, 2008). The best way to determine if mutations impact CALHM channel localization is to express GFP-tagged constructs in Xenopus oocytes and look for surface expression.

(3) Since the authors have not definitively shown that there are no defects in localization, they cannot make the claim in lines 346-356 that the mutations "either abolished or markedly reduced channel activity." Further, from their data, there is speculation regarding how these residues impact conformational changes during channel opening and closing. Line 404 - again, there is no concrete evidence that any of these residues play a role in gating function. Lines 406-433 - this entire paragraph is speculation without data to back it up. There is also a lack of specificity with statements such as "all mutants showed either reduced or completely abolished activity." What is meant by activity? Do the authors mean conductance?

(4) Line 303 - 13 aligned amino acids were conserved across all CALHM homologs - are these also aligned in related connexin and pannexin families? It is likely that cysteines and proline in TM2 are since CALHM channels overall share a lot of similarities with connexins and pannexins (Siebert et al, JBC, 2013). As in line 207, it would be expected that pannexins, connexins, and CALHM channel families would group together. Related to this, see Line 406 - in connexins, there is also a proline kink in TM2 that may play a role in mediating conformational changes between channel states (Ri et al, Biophysical Journal, 1999).

Reviewer #1 (Public review):

Summary:

This useful work extends a prior study from the authors to observe distance changes within the CNBD domains of a full-length CNG channel based on changes in single photon lifetimes due to tmFRET between a metal at an introduced chelator site and a fluorescent non-canonical amino acid at another site. The data are excellent and convincingly support the authors' conclusions. The methodology is of general use for other proteins. The authors also show that coupling of the CNBDs to the rest of the channel stabilizes the CNBDs in their active state, relative to an isolated CNBD construct.

Strengths:

The manuscript is very well written and clear.

Reviewer #2 (Public review):

The manuscript "Domain Coupling in Allosteric Regulation of SthK Measured Using Time-Resolved Transition Metal Ion FRET" by Eggan et al. investigates the energetics of conformational transitions in the cyclic nucleotide-gated (CNG) channel SthK. This lab pioneered transition metal FRET (tmFRET), which has previously provided detailed insights into ion channel conformational changes. Here, the authors analyze tmFRET fluorescence lifetime measurements in the time domain, yielding detailed insights into conformational transitions within the cyclic nucleotide binding domains (CNBDs) of the channel. The integration of tmFRET with time-correlated single-photon counting (TCSPC) represents an advancement of this technique.

The results summarize known conformational transitions of the C-helix and provide distance distributions that agree with predicted values based on available structures. The authors first validated their TCSPC approach using the isolated CNBD construct previously employed for similar experiments. They then study the more complex full-length SthK channel protein. The findings agree with earlier results from this group, demonstrating that the C-helix is more mobile in the closed state than static structures reflect. Upon adding the activating ligand cAMP, the C-helix moves closer to the bound ligand, as indicated by a reduced fluorescence lifetime, suggesting a shorter distance between the donor and acceptor. The observed effects depend on the cAMP concentration, with affinities comparable to functional measurements. Interestingly, a substantial amount of CNBDs appear to be in the activated state even in the absence of cAMP (Figure 6E and F, fA2 ~ 0.4).

This may be attributed to cooperativity among the CNBDs, which the authors could elaborate on further. In this context, the major limitation of this study is that distance distributions are observed only in one domain. While inter-subunit FRET is detected and accounted for, the results focus exclusively on movements within one domain. Thus, the resulting energetic considerations must be assessed with caution. In the absence of the activator, the closed state is favored, while the presence of cAMP favors the open state. This quantifies the standard assumption; otherwise, an activator would not effectively activate the channel. However, the numerical values of approximately 3 kcal/mol are limited by the fact that only one domain is observed in the experiment, and only one distance (C- helix relative to the CNBD) is probed. Additional conformational changes leading to pore opening (including rotation and upward movement of the CNBD, and radial dilation of the tetrameric assembly) are not captured by the current experiments. These limitations should be taken into account when interpreting the results.

Reviewer #3 (Public review):

Summary:

This is a lucidly written manuscript describing the use of transition-metal FRET to assess distance changes during functional conformational changes in a CNG channel. The experiments were performed on an isolated C-terminal nucleotide binding domain (CNBD) and on a purified full-length channel, with FRET partners placed at two positions in the CNBD.

Strengths:

The data and quantitative analysis are exemplary, and they provide a roadmap for use of this powerful approach in other proteins.

Weaknesses/Comments:

A ~3x lower Kd for nucleotide is seen for the detergent-solubilized full-length channel, compared to electrophysiological experiments. This is worth a comment in the Discussion, particularly in the context of the effect of the pore domain on the CNBD energetics.

Reviewer #1 (Public review):

The authors investigate how the viscoelasticity of the fingertip skin can affect the firing of mechanoreceptive afferents and they find a clear effect of recent physical skin state (memory), which is different between afferents. The manuscript is extremely well-written and well-presented. It uses a large dataset of low threshold mechanoreceptive afferents in the fingertip, where it is particularly noteworthy that the SA-2s have been thoroughly analyzed and play an important role here. They point out in the introduction the importance of the non-linear dynamics of the event when an external stimulus contacts the skin, to the point at which this information is picked up by receptors. Although clearly correlated, these are different processes, and it has been very well-explained throughout. I have some comments and ideas that the authors could think about that could further improve their already very interesting paper. Overall, the authors have more than achieved their aims, where their results very much support the conclusions and provoke many further questions. This impact of the previous dynamics of skin affecting current state can be explored further in so many ways and may help us in understanding skin aging and the effects of anatomical changes of the skin better.

Comments on revised submission:

The authors have taken all my considerations into account and provided excellent responses to them. They have modified their paper accordingly, which improves its clarity even more. Very interesting work and I have no further comments.

Reviewer #2 (Public review):

Summary:

The authors sought to identify the impact skin viscoelasticity has on neural signalling of contact forces that are representative of those experienced during normal tactile behaviour. The evidence presented in the analyses indicate there is a clear effect of viscoelasticity on the imposed skin movements from a force-controlled stimulus. Both skin mechanics and evoked afferent firing were affected based on prior stimulation, which has not previously been thoroughly explored. This study outlines that viscoelastic effects have an important impact on encoding in the tactile system, which should be considered in the design and interpretation of future studies. Viscoelasticity was shown to affect the mechanical skin deflections and stresses/strains imposed by previous and current interaction force, and also the resultant neuronal signalling. The result of this was an impaired coding of contact forces based upon previous stimulation. The authors may be able to strengthen their findings, by using the existing data to further explore the link between skin mechanics and neural signalling, giving a clearer picture than demonstrating shared variability. This is not a critical addition, but I believe would strengthen the work and make it more generally applicable.

Strengths:

-Elegant design of the study. Direct measurements have been made from the tactile sensory neurons to give detailed information on touch encoding. Experiments have been well designed and the forces/displacements have been thoroughly controlled and measured to give accurate measurements of global skin mechanics during a set of controlled mechanical stimuli.<br /> -Analytical techniques used. Analysis of fundamental information coding and information representation in the sensory afferents reveals dynamic coding properties to develop putative models of the neural representation of force. This advanced analysis method has been applied to a large dataset to study neural encoding of force, the temporal dynamics of this, and the variability in this.

Weaknesses:<br /> -Lack of exploration of the variation in neural responses. Although there is a viscoelastic effect which produces variability in the stimulus effects based on prior stimulation, it is a shame that the variability in neural firing and force induced skin displacements have been presented, and are similarly variable, but there has been no investigation of a link between the two. I believe with these data the authors can go beyond demonstrating shared variability. The force per se is clearly not faithfully represented in the neural signal, being masked by stimulation history, and it is of interest if the underlying resultant contact mechanics are.

Validity of conclusions:

The authors have succeeded in demonstrating skin viscoelasticity has an impact on skin contact mechanics with a given force and that this impacts on the resultant neural coding of force. Their study has been well designed and the results support their conclusions. The importance and scope of the work is adequately outlined for readers to interpret the results and significance.

Impact:

This study will have important implications for future studies performing tactile stimulation and evaluating tactile feedback during motor control tasks. In detailed studies of tactile function, it illustrates the necessity to measure skin contact dynamics to properly understand the effects of a force stimulus on the skin and mechanoreceptors.

Reviewer #1 (Public review):

Summary:

The authors demonstrate that two human preproprotein human mutations in the BMP4 gene cause a defect in proprotein cleavage and BMP4 mature ligand formation, leading to hypomorphic phenotypes in mouse knock-in alleles and in Xenopus embryo assays.

Strengths:

They provide compelling biochemical and in vivo analyses supporting their conclusions, showing the reduced processing of the proprotein and concomitant reduced mature BMP4 ligand protein from impressively mouse embryonic lysates. They perform excellent analysis of the embryo and post-natal phenotypes demonstrating the hypomorphic nature of these alleles. Interesting phenotypic differences between the S91C and E93G mutants are shown with excellent hypotheses for the differences. Their results support that BMP4 heterodimers act predominantly throughout embryogenesis whereas BMP4 homodimers play essential roles at later developmental stages.

Weaknesses:

In the revision the authors have appropriately addressed the previous minor weaknesses.

Reviewer #2 (Public review):

Summary:

The revised paper by Kim et al. reports two disease mutations in proBMP4, S91C and E93G, disrupt the FAM20C phosphorylation site at Ser91, blocking the activation of proBMP4 homodimers, while still allowing BMP4/7 heterodimers to function. Analysis of DMZ explants from Xenopus embryos expressing the proBMP4 S91C or E93G mutants showed reduced expression of pSmad1 and tbxt1. The expert amphibian tissue transplant studies were expanded to in vivo studies in Bmp4S91C/+ and Bmp4E93G/+ mice, highlighting the impact of these mutations on embryonic development, particularly in female mice, consistent with patient studies. Additionally, studies in mouse embryonic fibroblasts (MEFs) demonstrated that the mutations did not affect proBMP4 glycosylation or ER-to-Golgi transport but appeared to inhibit the furin-dependent cleavage of proBMP4 to BMP4. Based on these findings and AI modeling using AlphaFold of proBMP4, the authors speculate that pSer91 influences access of furin to its cleavage site at Arg289AlaLysArg292 in a new "Ideas and Speculation" section. Overall, the authors addressed the reviewers' comments, improving the presentation.

Strengths:

The strengths of this work continue to lie in the elegant Xenopus and mouse studies that elucidate the impact of the S91C and E93G disease mutations on BMP signaling and embryonic development. Including an "Ideas and Speculation" subsection for mechanistic ideas reduces some shortcomings regarding the analysis of the underlying mechanisms.

Reviewer #3 (Public review):

Summary:

The authors describe important new biochemical elements in the synthesis of a class of critical developmental signaling molecules, BMP4. They also present a highly detailed description of developmental anomalies in mice bearing known human mutations at these specific elements.

Strengths:

This paper presents exceptionally detailed descriptions of pathologies occurring in BMP4 mutant mice. Novel findings are shown regarding the interaction of propeptide phosphorylation and convertase cleavage, both of which will move the field forward. Lastly, a provocative hypothesis regarding furin access to cleavage sites is presented, supported by Alphafold predictions.

Reviewer #1 (Public review):

This study investigates the role of microtubules (MT) in regulating insulin secretion from pancreatic islet beta cells. This is of great importance considering that controlled secretion of insulin is essential to prevent diabetes. Previously, it has been shown that KIF5B plays an essential role in insulin secretion by transporting insulin granules to the plasma membrane. High glucose activates KIF5B to increase insulin secretion resulting in cellular uptake of glucose. In order to prevent hypoglycemia, insulin secretion needs to be tightly controlled. Notably, it is known that KIF5B plays a role in MT sliding. This is important, as the authors described previously that beta cells establish a peripheral sub-membrane MT array, which is critical for withdrawal of excessive insulin granules from the secretion sites. At high glucose, the sub-membrane MT array is destabilized to allow for robust insulin secretion. Here the authors aim to answer the question how the peripheral array is formed. Based on the previously published data the authors hypothesize that KIF5B organizes the sub-membrane MT array via microtubule sliding.

General comment:<br /> This manuscript provides data that indicate that KIF5B, like in many other cells, mediates MT sliding in beta cells to establish a non-radial sub-membrane MT array. This study is based mainly on in vitro assays and one cell line. To demonstrate the importance of KIF5B in vivo/under physiological conditions, the MT pattern and directionality in beta cells within whole isolated pancreatic islets from KIF5B KO mice was analyzed in comparison to their WT littermates. While the presented effects appear often rather small, it is important to note that small changes in MT configuration can have strong effects. However, the authors provide no link to insulin secretion and glucose uptake. Finally, it remains unclear whether a KIF5B-dependent mechanism regulating microtubule sliding plays a major role in controlling insulin secretion.

Specific comments:<br /> (1) It is difficult to appreciate that there is a "peripheral sub-membrane microtubule array" as it is not well defined in the manuscript. This reviewer assumes that this is in the respective field clear. Yet, while it is appreciated that there is an increased amount of MTs close to the cytoplasmic membrane, the densities appear very variable along the membrane. Please provide a clear description in the Introduction what is meant with "peripheral sub-membrane microtubule array".<br /> (2) The authors described a "consistent presence of a significant peripheral array in the C57BL/6J control mice, while the KO counterparts exhibited a partial loss of this peripheral bundle. Specifically, the measured tubulin intensity at the cell periphery was significantly reduced in the KO mice compared to their wild-type counterparts". In vitro "control cells had convoluted non-radial MTs with a prominent sub-membrane array, typical for β cells (Fig. 2A), KIF5B-depleted cells featured extra-dense MTs in the cell center and sparse receding MTs at the periphery (Fig. 2B,C)". Please comment/discuss why in vivo there are no "extra-dense MTs in the cell center".<br /> (3) Authors should include in the Discussion a paragraph discussing the fact that small changes in MT configuration can have strong effects.

Reviewer #2 (Public review):

This elegant study provides significant and impactful insights into the factors contributing to the distinct arrangement of sub-membrane microtubules within mouse β-cells of the pancreas. The authors propose that in these cells, the motor protein KIF5B plays a crucial role in sliding existing microtubules toward the cell periphery and aligning them with one another along the plasma membrane. Furthermore, similar to other physiological features of β-cells, high glucose levels enhance this microtubule sliding process. A precise arrangement of microtubules beneath the cell membrane in β-cells is vital for the regulated secretion of pancreatic enzymes and hormones; thus, KIF5B has a significant role in pancreatic activity in both healthy conditions and diseases. The authors support their model by demonstrating that the levels of KIF5B mRNA in MIN6 cells are higher than those of other known kinesins. They show that microtubule sliding becomes less efficient when KIF5B is genetically silenced using two different short hairpin RNAs (shRNAs). Additionally, silencing of KIF5A in the same cells results in a general reorganization of microtubules throughout the cell. Specifically, while control cells exhibit a convoluted and non-radial arrangement of microtubules near the cell membrane, KIF5B-depleted cells display a sparse and less dense sub-membrane array of microtubules. Based on these findings, the authors conclude that the loss of KIF5B strongly affects the localization of microtubules to the cell periphery. Using a dominant-negative approach, the authors also demonstrate that KIF5B facilitates the sliding of microtubules by binding to cargo microtubules through the kinesin-1 tail binding domain. They present evidence suggesting that KIF5B-mediated microtubule sliding is glucose-dependent, similar to the activity levels of kinesin-1, which increase in the presence of glucose. Lastly, they show that this is glucose-dependent.

Strengths:

This study unveils a previously unexplained mechanism that regulates the specific rearrangement of microtubules beneath the cell membrane in pancreatic β-cells. The findings have significant implications because the precise regulation of the microtubule array at the secretion zone plays a critical role in controlling pancreatic function in both healthy and diseased states. The provided data supports the authors' conclusions well, and the study demonstrates the use of state-of-the-art methodologies, including quantification techniques and elegant dominant-negative experiments.

Weaknesses: None

Reviewer #1 (Public review):

Summary:

This short report shows that the transcription factor gene mirror is specifically expressed in the posterior region of the butterfly wing imaginal disk, and uses CRISPR mosaic knock-outs to show it is necessary to specify the morphological features (scales, veins, and surface) of this area.

Strengths:

The data and figures support the conclusions. The article is swiftly written and makes an interesting evolutionary comparison to the function of this gene in Drosophila. Based on the data presented, it can now be established that mirror likely has a similar selector function for posterior-wing identity in a plethora of insects.

Comments on revisions:

The revision is satisfactory. I agree with the authors that this article provides interesting insights on the evolution of insect wings. Of note, butterfly and fly wing imaginal disks differ in their mode of development: while fly wing disks grow as epithelial sacs that evaginate during metamorphosis, butterfly wing disks develop as relatively flat epithelial sheets that expand and differentiate progressively. This makes the similar role of mirror all the more interesting.

The revised text appropriately discuss how selector genes like mirror regionalize the wing during larval and pupal development. This article makes a reasonable use of CRISPR mosaic knock outs and uses contralateral controls to show the nature of the phenotypic transformations.

Reviewer #2 (Public review):

This is a short and unpretentious paper. It is an interesting area and therefore, although much of this area of research was pioneered in flies, extending basic findings to butterflies would be worthwhile. Indeed, there is an intriguing observation but it is technically flawed and these flaws are far too serious to allow us to recommend publication

The authors show that mirror is expressed at the back of the wing in butterflies (as in flies). They present some evidence that is required for the proper development of the back of the wing in butterflies (a region dubbed the vannus by the ancient guru Snodgrass). But there are problems with that evidence. First, concerning the method, using CRISP they treat embryos and the expectation is that the mirror gene will be damaged in groups of cell lineages, giving a mosaic animal in which some lines of cells are normal for mirror and others not. We do not know where the clones or patches of cells that are defective for mirror are because they are not marked. Also, we do not know what part of the wing is wildtype and what part is mutant for mirror. When the mirror mutant cells colonise the back of the wing and that butterfly survives (many butterflies fail to develop), the back of the wing is altered in some selected butterflies. This raises a second problem: we do not know whether the rear of the wing is missing or transformed. From the images the appearance of the back of the wing is clearly different from wild type, but is that due to transformation or not? And then I believe we need to know specifically what us difference between the rear of the wing and the main part. What we see is a silvery look at the back that is not present in the main part, is it the structure of the scales? We are not told. There are other problems. Mirror is only part of a group of genes in flies and in flies both iroquois and mirror are needed to make the back of the wing, the alula (Kehl et al). What is known about iro expression in butterflies?

In flies, mirror regulates a late and local expression of dpp that seems to be responsible of making the alula. What happens in butterflies? Would a study of expression of Dpp in wildtype and mirror compromised wings be useful?

Thus, I find the paper to be disappointing for a general journal as it does little more than claim what was discovered in Drosophila is at least partly true in butterflies. Also it fails to explain what the authors mean by "wing domains" and "domain specification". They are not alone, butterfly workers in general appear vague about these concepts, their vagueness allowing too much loose thinking. Since these matters are at the heart of the purpose and meaning of the work reported here, we readers need a paper containing more critical thought and information. I would like to have a better and more logical introduction and discussion.

They do define what they mean by the vannus of the wing. In flies the definition of compartments is clear and abundantly demonstrated, with gene expression and requirement being limited precisely to sets of cells that display lineage boundaries. It is true that domains of gene expression in flies, for example, of the iroquois complex, which includes mirror, can only be related to pattern with difficulty. Some recap of what is known plus the opinion of the authors on how they interpret papers on possible lineage domains in butterflies might also be useful as the reader, is no wiser about what the authors might mean at the end of it!

The references are sometimes inappropriate. The discovery of the AP compartments should not be referred to Guillen et al 1995, but to Morata and Lawrence 1975.

Comments on revisions:

Nearly all the previous criticisms remain valid and are not discussed or overcome in the revision. The authors wish to draw their conclusions and we think they can do that, but they should make clear that key evidence is lacking. Thus their conclusions are speculative. But they present them more or less as facts. This is not justified. Let us suppose that clones lacking mirror do not survive or do not develop properly in the rear part of the wing and what they are seeing is occasional damage due to incomplete regeneration or to regenerative duplication?

Many clones in flies only include parts of one surface of the wing, could this happen here and how would it affect interpretations?

The null phenotype in the wing is not known but deduced from abnormal wings which "even in mKO..... appeared to have a mutant phenotype across the entire posterior region", a nice example of circular logic.

We believe the authors should be more objective and explain that their interpretations are not solid and that they should ideally be tested by finding ways of independently marking the clones. Other clonal mosaic experiments in butterflies have been done (eg https://journals.biologists.com/dev/article/150/18/dev201868/329659/Frizzled2-receives-WntA-signaling-during-butterfly) without cell autonomous independent markers, but they are more solid as transformed spots are made visible cell by cell by scale colour changes etc.

Their deduction that "mirror acts as a selector gene necessary to define the far posterior wing domain" is a speculative hypothesis, not a deduction and the readers should be so informed.

Reviewer #3 (Public review):

Summary:

The manuscript by Chatterjee et al., examines the role of the mirror locus in patterning butterfly wings. The authors examine the pattern of mirror expression in the common buckeye butterfly, Junonia coenia and then employ CRISPR mutagenesis to generate mosaic butterflies carrying clones of mirror mutant cells. They find that mirror is expressed in a well-defined posterior sector of final-instar wing discs from both hindwings and forewings and that CRISPR-injected larvae display a loss of adult wing structures presumably derived from the mirror expressing region of hindwing primordium (the case for forewings is a bit less clear since the mirror domain is narrower than in the hindwing, but there also do seem to be some anomalies in posterior regions of forewings in adults derived from CRISPR injected larvae). The authors conclude that wings of these butterflies have at least three different fundamental wing compartments, the mirror domain, a posterior domain defined by engrailed expression, and an anterior domain expressing neither mirror or engrailed. They speculate that this most posterior compartment has been reduced to a rudiment in Drosophila and thus has not been adequately recognized as a such a primary regional specialization.

Critique: This is a very straight-forward study and the experimental results presented support the key claims that mirror is expressed in a restricted posterior section of the wing primordium and that mosaic wings from CRISPR injected larvae display loss of adult wing structures presumably derived from cells expressing mirror (or at least nearby). The major issue I have with this paper is the strong interpretation of these findings that lead the authors to conclude that mirror is acting as a high level gene akin to engrailed in defining a separate extreme posterior wing compartment. To place this claim in context, it is important in my view to consider what is known about engrailed, for which there is ample evidence to support the claim that this gene does play a very ancestral and conserved function in a defining posterior compartments of all body segments (including the wing) across arthropods.

(A) engrailed is expressed in a broad posterior domain with a sharp anterior border in all segments of virtually all arthropods examined (broad use of a very good pan-species anti-En antibody makes this case very strong).

(B) In Drosophila, marked clones of wing cells (generated during larval stages) strictly obey a straight anterior-posterior border indicating that cells in these two domains do not normally intermix, thus, supporting the claim that a clear A/P lineage compartment exists.

In my opinion, mirror does not seem to be in the same category of regulator as engrailed for the following reasons:

(1) There is no evidence that I am aware of, either from the current experiments, or others that the mirror expression domain corresponds to a clonal lineage compartment. It is also unclear from the data shown in this study whether engrailed is co-expressed with mirror in posterior most cells of J. coenia wing discs? If so, it does not seem justified to infer that mirror acts as an independent determinant of the region of the wing where it is expressed.

(2) The mirror is not only expressed in a posterior region of the wing in flies but also in the ventral region of the eye. In Drosophila, mirror mutants not only lack the alula (derived approximately from cells where mirror is expressed), but also lacks tissue derived from the ventral region of the eye disc (although this ventral tissue loss phenotype may extend beyond the cells expressing mirror).

In summary, it seems most reasonable to me to think of mirror as a transcription factor that provides important development information for a diverse set of cells in which it can be expressed (posterior wing cells and ventral eye cells) but not that it acts as a high level regulator as engrailed.

Recommendation:

While the data provided in this succinct study are solid and interesting, it is not clear to me that these findings support the major claim that mirror defines an extreme posterior compartment akin to that specified by engrailed. Minimally, the authors should address the points outlined above in their discussion section and greatly tone down their conclusion regarding mirror being a conserved selector-like gene dedicated to establishing posterior-most fates of the wing. They also should cite and discuss the original study in Drosophila describing the mirror expression pattern in the embryo and eye and the corresponding eye phenotype of mirror mutants: McNeill et al., Genes & Dev. 1997. 11: 1073-1082; doi:10.1101/gad.11.8.1073.

Reviewer #1 (Public review):

The study addresses how faces and bodies are integrated in two STS face areas revealed by fMRI in the primate brain. It is building upon recordings and analysis of the responses of large populations of neurons to three sets of images, that vary face and body positions. These sets allowed the author to thoroughly investigate invariance to position on the screen (MC HC), to pose (P1 P2), to rotation (0 45 90 135 180 225 270 315), to inversion, to possible and impossible postures (all vs straight), to presentation of head and body together or in isolation. By analyzing neuronal responses, they find that different neurons showed preferences for body orientation, or head orientation or for the interaction between the two. By using a linear support vector machine classifier, they show that the neuronal population can decode head-body angle presented across orientations, in the anterior aSTS patch (but not middle mSTS patch), except for mirror orientation. On the contrary, mSTS neurons show less invariance for head-body angle and more specialization for head or body orientation.

Strengths:

These results expand prior work on the role of Anterior STS fundus face area in face-body integration and its invariance to mirror symmetry, with a rigorous set of stimuli revealing the workings of these neuronal populations in processing individuals as a whole, in an important series of carefully designed conditions.

It also raises questions for future investigations comparing humans and monkeys expertise with upright and inverted configurations, in light of monkey-specific hanging upside-down behavior. Further, using two types of body postures (sitting, standing), they show a correlation in head-body angle between postures, suggesting that monkey orientation might be more meaningful to these neurons than precise posture.

Reviewer #2 (Public review):

Summary:

This paper investigates the neuronal encoding of the relationship between head and body orientations in the brain. Specifically, the authors focus on the angular relationship between the head and body by employing virtual avatars. Neuronal responses were recorded electrophysiologically from two fMRI-defined areas in the superior temporal sulcus and analyzed using decoding methods. They found that: (1) anterior STS neurons encode head-body angle configurations; (2) these neurons distinguish aligned and opposite head-body configurations effectively, whereas mirror-symmetric configurations are more difficult to differentiate; and (3) an upside-down inversion diminishes the encoding of head-body angles. These findings advance our understanding of how visual perception of individuals is mediated, providing a fundamental clue as to how the primate brain processes the relationship between head and body-a process that is crucial for social communication.

Strengths:

The paper is clearly written, and the experimental design is thoughtfully constructed and detailed. The use of electrophysiological recordings from fMRI-defined areas elucidated the mechanism of head-body angle encoding at the level of local neuronal populations. Multiple experiments, control conditions, and detailed analyses thoroughly examined various factors that could affect the decoding results. The decoding methods effectively and consistently revealed the encoding of head-body angles in the anterior STS neurons. Consequently, this study offers valuable insights into the neuronal mechanisms underlying our capacity to integrate head and body cues for social cognition-a topic that is likely to captivate readers in this field.

Weaknesses:

I did not identify any major weaknesses in this paper.

Reviewer #3 (Public review):

Summary:

Zafirova et al. investigated the interaction of head and body orientation in the macaque superior temporal sulcus (STS). Combining fMRI and electrophysiology, they recorded responses of visual neurons to a monkey avatar with varying head and body orientations. They found that STS neurons integrate head and body information in a nonlinear way, showing selectivity for specific combinations of head-body orientations. Head-body configuration angles can be reliably decoded, particularly for neurons in the anterior STS, suggesting a transformation of face/body orientation signals from the middle to the anterior STS. Furthermore, body inversion resulted in reduced decoding of head-body configuration angles. Compared to previous work that examined face or body alone, this study demonstrates how head and body information are integrated to compute a socially meaningful signal.

Strengths:

This work presents an elegant design of visual stimuli, with a monkey avatar of varying head and body orientations, making the analysis and interpretation straightforward. Together with several control experiments, the authors systematically investigated different aspects of head-body integration in the macaque STS. The results and analyses of the paper are convincing.

Weakness:

While this work has characterized the neural integration of head and body information in detail, it's unclear how the neural representation relates to the animal's perception. Behavioural experiments using the same set of stimuli could help address this question, but I agree that these additional experiments may be beyond the scope of the current paper.

for - book - Embracing Paradox, Evolving Language - book - review - Embracing Paradox, Evolving Language - adjacency - Lisa's conlanger - Deep Humanity BEing journeys - Indyweb - provenance - Deep Humanity - language BEing journey - author - Lisa E. Maroski - to - post - LinkedIn - Bayo Akomolafe - from 'belief' to 'apolief" - https://hyp.is/go?url=https%3A%2F%2Fwww.linkedin.com%2Fposts%2Fbayoakomolafe_i-am-against-worldview-the-term-seems-activity-7319799984663535616-fpVW%2F&group=world

new trailmark - summary to review - the word "review" may be a better trailmark word than "summary" - At this point, I will replace "summary" with "review" in the case of book or article reviews

review - Lisa's book is an insightful convergence of an important but ignored subject, the experiential intersection between language and consciousness. - Her understanding that language plays an important role in constructing our reality leads to a bold and novel proposal, especially salient at this time of global poly-meta-perma-meaning crisis. - She proposes that we individually and collectively experiment and explore creating new words and language structures that transcend the limitations of our existing language - If patterns of language usage traps us in outdated conceptual paradigms, then breaking out of these may be challenging, if not impossible, without the creation of new linguistic and language structures. - From a Stop Reset Go and Deep Humanity perpsective, Lisa's proposal for practical experimentation with constructing new languages to unleash new forms of expression is very aligned to Deep Humanity BEing journeys - As I read and annotate Lisa's book, any potential linguistic and language BEing journeys that her words inspired will be recorded for posterity

Addendum - note from journal - 2025, May 8 - reflections on Lisa's book - asynchronous communication is only one half of indyweb     - the other half is asynchronous REFLECTION AND SYNTHESIS - Effective timebinding requires both     - Annotation captures interpersonal shared ideas     - journalling captures ours own unique synthesis only emerges from asynchronous reflections of our existent associative network of ideas and the newly ingested interpersonal ones - Annotations capture the novel and newly inputted interpersonal ones     - but annotation currently only applies to hypothesis - it needs to expand to realtime meetings such as zoom calls, emails, socials media comments and socials media chats in order to be complete - Until now, there has not been a medium with sufficient set of affordances to unleash the affordances potential in language itself - While digital media has existed and rapidly developed for the past 5 decades,     - employing and leveraging it to unleash the full potential of language itself has not ever been conceived of until the concept of Indyweb arrived - Indeed, we could make the claim that the indyweb is a foundational human technology on the same order as language itself because it completes language, revealing its empty ( shunyata) quality, thereby     - uniting it with the universe itself -  From the unlimited potential of the tacit,     - the limited forms of words emerge, both are 2 sides off the same nondual coin     - and unleashing the full , unrealized potential of language - It is the provenance aspect of the indyweb that provides an automatic trail of all our learning journey, making both the     - individual and     - intertwingled collective evolution of ideas available as records for. timebinding posterity

• when we feel in a good state of health and wellbeing and absent of any disease
  • we feel when everything is within harmony in our temporary state of being alive
• Any disease shows us how the diseases-free state is so fragilely constructed
• disease-free is an and condition of many subsystems working together harmoniously -aspectualizing is creating
  • a perspective,
  • a word
  • an idea
• the greatest freedom of afforded when we are free of all perspectives
  • for that is when a new perspective can emerge
• When we cling to words and ideas, we cling to perspectives and aspects of the whole
• The teaching of one taste is the highest and most subtle teaching - equal taste - and easiest to be misinterpreted
  • because we are anchored in the world of many different tastes and of measurement and scale,
    • where some things are greater than others on our scale
• Bayo Akomolafe does some language construction - conlangering on his LinkedIn post on the derivation of the word "apolief" from "belief"

Reviewer #1 (Public review):

Summary:

Kv2 subfamily potassium channels contribute to delayed rectifier currents in virtually all mammalian neurons and are encoded by two distinct types of subunits: Kv2 alpha subunits that have the capacity to form homomeric channels (Kv2.1 and Kv2.2), and KvS or silent subunits (Kv5,6,8.9) that can assemble with Kv2.1 or Kv2.2 to form heteromeric channels with novel biophysical properties. Many neurons express both types of subunits and therefore have the capacity to make both homomeric Kv2 channels and heteromeric Kv2/KvS channels. Determining the contributions of each of these channel types to native potassium currents has been very difficult because the differences in biophysical properties are modest and there are no Kv2/KvS-specific pharmacological tools. The authors set out to design a strategy to separate Kv2 and Kv2/KvS currents in native neurons based on their observation that Kv2/KvS channels have little sensitivity to the Kv2 pore blocker RY785 but are blocked by the Kv2 VSD blocker GxTx. They clearly demonstrate that Kv2/KvS currents can be differentiated from Kv2 currents in native neurons using a two-step strategy to first selectively block Kv2 with RY785, and then block both with GxTx. The manuscript is beautifully written; takes a very complex problem and strategy and breaks it down so both channel experts and the broad neuroscience community can understand it.

Strengths:

The compounds the authors use are highly selective and unlikely to have significant confounding cross-reactivity to other channel types. The authors provide strong evidence that all Kv2/KvS channels are resistant to RY785. This is a strength of the strategy - it can likely identify Kv2/KvS channels containing any of the 10 mammalian KvS subunits and thus be used as a general reagent on all types of neurons. The limitation then of course is that it can't differentiate the subtypes, but at this stage, the field really just needs to know how much Kv2/KvS channels contribute to native currents and this strategy provides a sound way to do so.

Weaknesses:

The authors are very clear about the limitations of their strategy, the most important of which is that they can't differentiate different subunit combinations of Kv2/KvS heteromers. This study is meant to be a start to understanding the roles of Kv2/KvS channels in vivo. As such, this is a minor weakness, far outweighed by the potential of the strategy to move the field through a roadblock that has existed since its inception.

The study accomplishes exactly what it set out to do: provide a means to determine the relative contributions of homomeric Kv2 and heteromeric Kv2/KvS channels to native delayed rectifier K+ currents in neurons. It also does a fabulous job laying out the case for why this is important to do.

Comments on revisions:

I liked this manuscript the first time and thought it was a great attempt to address a difficult problem, made more difficult by confusing background literature and conventions. The authors have kept all the strong points I liked from the first round and made it even stronger with their thoughtful and substantive responses to reviews. My first review was strongly supportive, and my initial short assessment/public review was written with the assumption that they would be public and the paper would be published essentially in its original form. All those points still apply so I am going to leave the initial reviews as is. The paper is a pleasure to read and a nice contribution to the field.

Reviewer #2 (Public review):

The authors used combined blockers/modulators to dissect the potassium currents mediated by inter-subunit heteromeric Kv channels. The method is robust given that the researchers know their limitations. Nevertheless, the authors elegantly tested their hypotheses, making this manuscript friendly to read despite the depth of all aspects they dealt with.

The quality of the data presented will positively impact the science involved in the study heteromeric channels, with clear developments in the field. Finally, the approach presented may unlock new studies related to these channels.

Comments on revisions:

The authors clarified all my points and beyond, specifically by adding some computational work that will also contribute to the subfield of heteromeric Kv channels.

Reviewer #2 (Public review):

Summary:

I found this an interesting manuscript describing a study investigating the role of MC4R signalling on kisspeptin neurons. The initial question is a good one. Infertility associated with MC4 mutations in humans has typically been ascribed to the consequent obesity and impaired metabolic regulation. Whether there is a direct role for MC4 in regulating the HPG axis has not been thoroughly examined. Here, the researchers have put together an elegant combination of targeted loss of function and gain of function in vivo experiments, specifically targeting MC4 expression in kisspeptin neurons. This excellent experimental design should provide compelling evidence for whether melanocortin signalling has a direct role in arcuate kisspeptin neurons to support normal reproductive function. There were definite effects on reproductive function (irregular estrous cycle, reduced magnitude of LH surge induced by exogenous estradiol). However, the magnitude of these responses and the overall effect on fertility were relatively minor. The mice lacking MC4R in kisspeptin neurons remained fertile despite these irregularities. The second part of the manuscript describes a series of electrophysiological studies evaluating the pharmacological effects of melanocortin signalling in kisspeptin cells in ex-vivo brain slides. These studies characterised interesting differential actions of melanocortins in two different populations of kisspeptin neurons. Collectively, I think the study provides novel insights into how direct actions of melanocortin signalling, via the MC4 receptor in kisspeptin neurons, contribute to the metabolic regulation of the reproductive system. Importantly, however, it is clear that other mechanisms are also at play.

Strengths:

The loss of function/gain of function experiments provide a conceptually simple but hugely informative experimental design. This is the key strength of the current paper - especially the knock-in study that showed improved reproductive function even in the presence of ongoing obesity. This is a very convincing result that documents that reproductive deficits in MC4R knockout animals (and humans with deleterious variants of the MC4R gene) can be ascribed to impaired signalling in the hypothalamic kisspeptin neurons and not necessarily simply caused as a consequence of obesity. As concluded by the authors: "reproductive impairments observed in MC4R deficient mice, which replicate many of the conditions described in humans, are largely mediated by the direct action of melanocortins via MC4R on Kiss1 neurons and not to their obese phenotype." This is important, as it might change the way such fertility problems are treated.

Limitation:

The mechanistic studies evaluating melanocortin signalling in kisppetin neurons were all completed in ovariectomized animals (with and without exogenous hormones). This reductionist approach allowed a focus on the direct actions of estradiol to regulate responses but missed an opportunity to evaluate how cyclical changes in hormones might impact the system. Such cyclical changes are fundamental to how these neurons function in vivo and may dynamically alter the way they respond to hormones and neuropeptides. However, the inclusion of gonad-intact animals would have significantly increased the complexity of experiments and can reasonably be considered outside of the scope of the present study.

Reviewer #1 (Public review):

Summary:

The authors track the motion of multiple consortia of Multicellular Magnetotactic Bacteria moving through an artificial network of pores and report a discovery of a simple strategy for such consortia to move fast through the network: an optimum drift speed is attained for consortia that swim a distance comparable to the pore size in the time it takes to align the with an external magnetic field. The authors rationalize their observations using dimensional analysis and numerical simulations. Finally, they argue that the proposed strategy could generalize to other species by demonstrating the positive correlation between the swimming speed and alignment time based on theoretical analysis and parameters derived from literature.

Strengths:

The underlying dimensional analysis and model convincingly rationalize the experimental observation of an optimal drift velocity: the optimum balances the competition between the trapping in pores at large magnetic fields and random pore exploration for weak magnetic fields.

Weaknesses:

The convex pore geometry studied here creates convex traps for cells, which I expect enhances their trapping. Natural environments may create a much smaller concentration of such traps. In this case, whether a non-monotonic dependence of the drift velocity on the Scattering number would persist is unclear.

Comments on revisions:

Thank you very much for addressing my comments. I think the revisions have improved the paper.

Reviewer #2 (Public review):

Summary:

The authors have made microfluidic arrays of pores and obstacles with a complex shape and studied the swimming of multicellular magnetotactic bacteria through this system. They provide a comprehensive discussion of the relevant parameters of this system and identify one dimensionless parameter, which they call the scattering number and which depends on the swimming speed and magnetic moment of the bacteria as well as the magnetic field and the size of the pores, as the most relevant. They measure the effective speed through the array of pores and obstacles as a function of that parameter, both in their microfluidic experiments and in simulations, with good agreement between the two. They find an optimal scattering number, which they estimate to reflect the parameters of the studied multicellular bacteria in their natural environment. They finally use this knowledge to compare different species. Despite the variability of bacteria parameters, they estimate the scattering number to be rather narrowly distributed, suggesting that their results apply to a broad range of species.

Strengths:

This is a beautiful experimental approach and the observation of an optimal scattering number (likely reflecting an optimal magnetic moment) is very convincing. The results here improve on similar previous work in two respects: On the one hand, the tracking of bacteria does not have the limitations of previous work, and on the other hand, the effective motility is quantified. Both features are enabled by choices of the experimental system: the use the multicellular bacteria which are larger than the usual single-celled magnetotactic bacteria and the design of the obstacle array which allows the quantification of transition rates due to the regular organization as well as the controlled release of bacteria into this array through a clever mechanism.

Weaknesses:

Some of the key experimental choices on which the strength of the approach is based also come at a price and impose some limitations, namely the use of a non-culturable organism and the regular, somewhat unrealistic artificial obstacle array, but the advantages of these choices outweigh the drawbacks.

Comments on revisions:

The paper has been improved with respect to presentation and content. In particular, I appreciate the new plots comparing the simulation and experiments directly and the estimate of the scattering number for different species. In my opinion, all issues raised by the reviewers have been addressed in a productive way.

Reviewer #1 (Public review):

Summary:

This manuscript reports the investigation of PriC activity during DNA replication initiation in Escherichia coli. It is reported that PriC is necessary for growth and control of DNA replication initiation under diverse conditions where helicase loading is perturbed at the chromosome origin oriC. A model is proposed where PriC loads helicase onto ssDNA at the open complex formed by DnaA at oriC. Reconstituted helicase loading assays in vitro are consistent with the model.

Strengths:

The complementary combination of genetics in vivo and reconstituted assays in vitro provide solid evidence to support the role of PriC at a replication origin.

The manuscript is well written and has a logical narrative.

The data provide new insight to how bacteria might load helicase at the replication origin when the wild-type DnaA-dependent loading pathway is perturbed.

Weakness:

It has not yet been established whether PriC localises at oriC in vivo under the conditions tested.

Reviewer #2 (Public review):

This is a great paper. Yoshida et al. convincingly show that DnaA does not exclusively do loading of the replicative helicase at the E. coli oriC, but that PriC can also perform this function. Importantly, PriC seems to contribute to helicase loading even in wt cells albeit to a much lesser degree than DnaA. On the other hand, PriC takes a larger role in helicase loading during aberrant initiation, i.e. when the origin sequence is truncated or when the properties of initiation proteins is suboptimal. Here highlighted by mutations in dnaA or dnaC.

This a major finding because it clearly demonstrates that the two roles of DnaA in the initiation process can be separated into initially forming an open complex at the DUE region by binding/nucleation onto DnaA-boxes and second in loading of the helicase. Whereas these two functions are normally assumed to be coupled, the present data clearly show that they can be separated and that PriC can perform at least part of the helicase loading provided that an area of duplex opening is formed by DnaA.<br /> This puts into questions the interpretation of a large body of previous work on mutagenesis of oriC and dnaA to find a minimal oriC/DnaA complex in many bacteria. In other words, mutants in which oriC is truncated/mutated may support initiation of replication and cell viability only in the presence of PriC. Such mutants are capable to generate single strand opening but may fail to load the helicase in absence of PriC. Similarly, dnaA mutants may generate aberrant complex on oriC that trigger strand opening but are incapable of loading DnaB unless PriC is present.

In the present work, the sequence of experiments presented is logical and the manuscript is clearly written and easy to follow. The very last part regarding PriC in cSDR replication does not add much to the story and may be omitted.

I have a few specific questions/comments

The partial complementation of the dnaC2 strain by PriC seems quite straightforward since this particular mutation leads to initiation arrest at the open complex stage and this sets the stage for PriC to load the helicase. The situation is somewhat different for dnaA46. Why is this mutation partly complemented by PriC at 37C? DnaA46 binds neither ATP nor ADP, yet it functions in initiation at permissive temperature. At nonpermssive temperature, it binds oriC as well but does not lead to initiation. Does the present data imply that the true initiation defect of DnaA46 lies in helicase loading? The authors need to comment on this in the text.

Relating to the above. In Fig. 3 it is shown that the pFH plasmid partly complement dnaA46 in a PriC dependent manner. Again, it would be nice to know the nature of the DnaA46 protein defect. It would be interesting to see how a pING1-dnaA46 plasmid performs in the experiment presented in Fig. 3.

Reviewer #3 (Public review):

Summary:

At the abandoned replication fork, loading of DnaB helicase requires assistance from PriABC, repA, and other protein partners, but it does not require replication initiator protein, DnaA. In contrast, nucleotide-dependent DnaA binding at the specific functional elements is fundamental for helicase loading, leading to the DUE region's opening. However, the authors questioned in this study that in case of impeding replication at the bacterial chromosomal origins, oriC, a strategy similar to an abandoned replication fork for loading DnaB via bypassing the DnaA interaction step could be functional. The study by Yoshida et al. suggests that PriC could promote DnaB helicase loading on the chromosomal oriC ssDNA without interacting with the DnaA protein. The conclusions drawn supported by the evidence provided are compelling.

Strengths:

Understanding the mechanism of how DNA replication restarts via reloading the replisomes onto abandoned DNA replication forks is crucial. Notably, this knowledge becomes crucial to understanding how bacterial cells maintain DNA replication from a stalled replication fork when challenging or non-permissive conditions prevail. This critical study combines experiments to address a fundamental question of how DnaB helicase loading could occur when replication initiation impedes at the chromosomal origin, leading to replication restart.

Reviewer #1 (Public review):

Summary:

This paper focuses on understanding how covalent inhibitors of peroxisome proliferator-activated receptor-gamma (PPARg) show improved inverse agonist activities. This work is important because PPARg plays essential roles in metabolic regulation, insulin sensitization, and adipogenesis. Like other nuclear receptors, PPARg, is a ligand-responsive transcriptional regulator. Its important role, coupled with its ligand-sensitive transcriptional activities, makes it an attractive therapeutic target for diabetes, inflammation, fibrosis, and cancer. Traditional non-covalent ligands like thiazolininediones (TZDs) show clinical benefit in metabolic diseases, but utility is limited by off-target effects and transient receptor engagement. In previous studies, the authors characterized and developed covalent PPARg inhibitors with improved inverse agonist activities. They also showed that these molecules engage unique PPARg ligand binding domain (LBD) conformations whereby the c-terminal helix 12 penetrates into the orthosteric binding pocket to stabilize a repressive state. In the nuclear receptor superclass of proteins, helix 12 is an allosteric switch that governs pharmacologic responses, and this new conformation was highly novel. In this study, the authors did a more thorough analysis of how two covalent inhibitors, SR33065 and SR36708 influence the structural dynamics of PPARg LBD.

Strengths:

(1) The authors employed a compelling integrated biochemical and biophysical approach.

(2) The cobinding studies are unique for the field of nuclear receptor structural biology, and I'm not aware of any similar structural mechanism described for this class of proteins.

(3) Overall, the results support their conclusions.

(4) The results open up exciting possibilities for the development of new ligands that exploit the potential bidirectional relationship between the covalent versus non-covalent ligands studied here.

Weaknesses:

(1) The major weakness in this work is that it is hard to appreciate what these shifting allosteric ensembles actually look like on the protein structure. Additional graphical representations would really help convey the exciting results of this study.

Reviewer #2 (Public review):

Summary:

The authors use ligands (inverse agonists, partial agonists) for PPAR, and coactivators and corepressors, to investigate how ligands and cofactors interact in a complex manner to achieve functional outcomes (repressive vs. activating).

Strengths:<br /> The data (mostly biophysical data) are compelling from well-designed experiments. Figures are clearly illustrated. The conclusions are supported by these compelling data. These results contribute to our fundamental understanding of the complex ligand-cofactor-receptor interactions.

Weaknesses:

This is not the weakness of this particular paper, but the general limitation in using simplified models to study a complex system.

Reviewer #1 (Public review):

Summary:

This manuscript by Harris and Gallistel investigates how the rate of learning and strength of conditioned behavior post learning depend on the various temporal parameters of Pavlovian conditioning. They replicate results from Gibbon and Balsam (1981) in rats to show that the rate of learning is proportional to the ratio between the cycle duration and the cue duration. They further show that the strength of conditioned behavior post learning is proportional to the cue duration, and not the above ratio. The overall findings here are interesting, provide context to many conflicting recent results on this topic, and are supported by reasonably strong evidence. Nevertheless, there are some major weaknesses in the evidence presented for some of the stronger claims in the manuscript.

Strengths:

This manuscript has many strengths including a rigorous experimental design, several different approaches to data analysis, careful consideration of prior literature, and a thorough introduction and discussion. The central claim-that animals track the rates of events in their environment, and that the ratio of two rates determine the rate of learning-is supported with solid evidence.

Weaknesses:

Despite the above major strengths, some key aspects of the paper need major improvement. These are listed below.

(1) A key claim made here is that the same relationship (including the same parameter) describes data from pigeons by Gibbon and Balsam (1981) and the rats in this study. I think the evidence for this claim is weak as presented here. First, the exact measure used for identifying trials to criterion makes a big difference in Fig 3. As best as I understand, the authors do not make any claims about which of these approaches is the "best" way. Second, the measure used for identifying trials to criterion in Fig 1 appears different from any of the criteria used in Fig 3. If so, to make the claim that the quantitative relationship is one and the same in both datasets, the authors need to use the same measure of learning rate on both datasets and show that the resultant plots are statistically indistinguishable. Currently, the authors simply plot the dots from the current dataset on the plot in Fig 1 and ask the readers to notice the visual similarity. This is not at all enough to claim that both relationships are the same. In addition to the dependence of the numbers on the exact measure of learning rate used, the plots are in log-log axis. Slight visual changes can mean a big difference in actual numbers. For instance, between Fig 3 B and C, the highest information group moves up only "slightly" on the y-axis but the difference is a factor of 5. The authors need to perform much more rigorous quantification to make the strong claim that the quantitative relationships obtained here and in Gibbon and Balsam 1981 are identical.

(2) Another interesting claim here is that the rates of responding during ITI and the cue are proportional to the corresponding reward rates with the same proportionality constant. This too requires more quantification and conceptual explanation. For quantification, it would be more convincing to calculate the regression slope for the ITI data and the cue data separately and then show that the corresponding slopes are not statistically distinguishable from each other. Conceptually, I am confused why the data used to the test the ITI proportionality come from the last 5 sessions. Specifically, if the model is that animals produce response rates during the ITI (a period with no possible rewards) based on the overall rate of rewards in the context, wouldn't it be better to test this before the cue learning has occurred? Before cue learning, the animals would presumably only have attributed rewards in the context to the context and thus, produce overall response rates in proportion to the contextual reward rate. After cue learning, the animals could technically know that the rate of rewards during ITI is zero. Why wouldn't it be better to test the plotted relationship for ITI before cue learning has occurred? Further, based on Fig 1, it seems that the overall ITI response rate reduces considerably with cue learning. What is the expected ITI response rate prior to learning based on the authors' conceptual model? Why does this rate differ pre and post cue learning? Finally, if the authors' conceptual framework predicts that ITI response rate after cue learning should be proportional to contextual reward rate, why should the cue response rate be proportional to cue reward rate instead of cue reward rate plus contextual reward rate?

(3) I think there was a major conceptual disconnect between the gradual nature of learning shown in Figs 7 and 8 and the information theoretic model proposed by the authors. To the extent that I understand the model, the animals should simply learn the association once the evidence crosses a threshold (nDKL > threshold) and then produce behavior in proportion to the expected reward rate. If so, why should there be a gradual component of learning as shown in these figures? In terms of the proportional response rule to rate of rewards, why is it changing as animals go from 10% to 90% of peak response? I think the manuscript would be much strengthened if these results are explained within the authors' conceptual framework. If these results are not anticipated by the authors' conceptual framework, please do explicitly state this in the manuscript.

(4) I find the idea stated in the Conclusion section that any model considering probability of reinforcement cannot be correct because it doesn't have temporal units to be weak. I think the authors might mean that existing models based on probability do not work and not that no possible model can work. For any point process, the standard mathematical treatment of continuous time is to compute the expected count of events as p*dt where p is the probability of occurrence of the event in that time bin and dt is an infinitesimal time bin. There is obviously a one-to-one mapping between probability of an event in a point process and its rate. Existing models use an arbitrary time bin/trial and thus, I get the authors' argument in the discussion. However, I think their conclusion is overstated.

(5) The discussion states that the mutual information defined in equation 1 does not change during partial reinforcement. I am confused by this. The mean delay between reinforcements increases in inverse proportion to the probability of reinforcement, but doesn't the mean delay between cue and next reinforcement increase by more than this amount (next reinforcement is greater than or equal to the cue-to-cue interval away from the cue for many trials)? Why is this ratio invariant to partial reinforcement?

Comments on revisions:

Update following revision

(1) This point is discussed in more detail in the attached file, but there are some important details regarding the identification of the learned trial that require more clarification. For instance, isn't the original criterion by Gibbon et al. (1977) the first "sequence of three out of four trials in a row with at least one response"? The authors' provided code for the Wilcoxon signed rank test and nDkl thresholds looks for a permanent exceeding of the threshold. So, I am not yet convinced that the approaches used here and in prior papers are directly comparable. Also, there's still no regression line fitted to their data (Fig 3's black line is from Fig 1, according to the legends). Accordingly, I think the claim in the second paragraph of the Discussion that the old data and their data are explained by a model with "essentially the same parameter value" is not yet convincing without actually reporting the parameters of the regression. Related to this, the regression for their data based on my analysis appears to have a slope closer to -0.6, which does not support strict timescale invariance. I think that this point should be discussed as a caveat in the manuscript.

(2) The authors report in the response that the basis for the apparent gradual/multiple step-like increases after initial learning remains unclear within their framework. This would be important to point out in the actual manuscript. Further, the responses indicating the fact that there are some phenomena that are not captured by the current model would be important to state in the manuscript itself.

(3) There are several mismatches between results shown in figures and those produced by the authors' code, or other supplementary files. As one example, rat 3 results in Fig 11 and Supplementary Materials don't match and neither version is reproduced by the authors' code. There are more concerns like this, which are detailed in the attached review file.

Reviewer #2 (Public review):

A long-standing debate in the field of Pavlovian learning relates to the phenomenon of timescale invariance in learning i.e. that the rate at which an animal learns about a Pavlovian CS is driven by the relative rate of reinforcement of the cue (CS) to the background rate of reinforcement. In practice, if a CS is reinforced on every trial, then the rate of acquisition is determined by the relative duration of the CS (T) and the ITI (C = inter-US-interval = duration of CS + ITI), specifically the ratio of C/T. Therefore, the point of acquisition should be the same with a 10s CS and a 90s ITI (T = 10; C = 90 + 10 = 100, C/T = 100/10 = 10) and with a 100s CS and a 900s ITI (T = 100; C = 900 + 100 = 1000, C/T = 1000/100 = 10). That is to say, the rate of acquisition is invariant to the absolute timescale as long as this ratio is the same. This idea has many other consequences, but is also notably different from more popular prediction-error based associative learning models such as the Rescrola-Wagner model. The initial demonstrations that the ratio C/T predicts the point of acquisition across a wide range of parameters (both within and across multiple studies) was conducted in Pigeons using a Pavlovian autoshaping procedure. What has remained under contention is whether or not this relationship holds across species, particularly in the standard appetitive Pavlovian conditioning paradigms used in rodents. The results from rodent studies aimed at testing this have been mixed, and often the debate around the source of these inconsistent results focuses on the different statistical methods used to identify the point of acquisition for the highly variable trial-by-trial responses at the level of individual animals.<br /> The authors successfully replicate same effect found in pigeon autoshaping paradigms decades ago (with almost identical model parameters) in a standard Pavlovian appetitive paradigm in rats. They achieve this through a clever change the experimental design, using a convincingly wide range of parameters across 14 groups of rats, and by a thorough and meticulous analysis of these data. It is also interesting to note that the two author's have published on opposing sides of this debate for many years, and as a result have developed and refined many of the ideas in this manuscript through this process.

Main findings

(1) The present findings demonstrate that the point of initial acquisition of responding is predicted by the C/T ratio.

(2) The terminal rates of responding to the CS appears to be related to the reinforcement rate of the CS (T; specifically, 1/T) but not its relation to the reinforcement rate of the context (i.e. C or C/T). In the present experiment, all CS trials were reinforced so it is also the case that the terminal rate of responding was related to the duration of the CS.

(3) An unexpected finding was that responding during the ITI was similarly related to the rate of contextual reinforcement (1/C). This novel finding suggests that the terminal rate of responding during the ITI and the CS are related to their corresponding rates of reinforcement. This finding is surprising as it suggests that responding during the ITI is not being driven by the probability of reinforcement during the ITI.

(4) Finally, the authors characterised the nature of increased responding from the point of initial acquisition until responding peaks at a maximum. Their analyses suggest that nature of this increase was best described as linear in the majority of rats, as opposed to the non-linear increase that might be predicted by prediction error learning models (e.g. Rescorla-Wagner). However, more detailed analyses revealed that these changes can be quite variable across rats, and more variable when the CS had lower informativeness (defined as C/T).

Strengths and Weaknesses:

There is an inherent paradox regarding the consistency of the acquisition data from Gibbon & Balsam's (1981) meta-analysis of autoshaping in pigeons, and the present results in magazine response frequency in rats. This consistency is remarkable and impressive, and is suggestive of a relatively conserved or similar underlying learning principle. However, the consistency is also surprising given some significant differences in how these experiments were run. Some of these differences might reasonably be expected to lead to differences in how these different species respond. For example:

- The autoshaping procedure commonly used in the pigeons from these data were pretrained to retrieve rewards from a grain hopper with an instrumental contingency between head entry into the hopper and grain availability. During Pavlovian training, pecking the key light also elicited an auditory click feedback stimulus, and when the grain hopper was made available the hopper was also illuminated.

- In the present experimental procedure, the rats were not given contextual exposure to the pellet reinforcers in the magazine (e.g. a magazine training session is typically found in similar rodent procedures). The Pavlovian CS was a cue light within the magazine itself.

These design features in the present rodent experiment are clearly intentional. Pretraining with the reinforcer in the testing chambers would reasonably alter the background rate of reinforcement (parameter), so it make sense not to include this but differs from the paradigm used in pigeons. Having the CS inside the magazine where pellets are delivered provides an effective way to reduce any potential response competition between CS and US directed responding and combines these all into the same physical response. This makes the magazine approach response more like the pecking of the light stimulus in the pigeon autoshaping paradigm. However, the location of the CS and US is separated in pigeon autoshaping, raising questions about why the findings across species are consistent despite these differences.

Intriguingly, when the insertion of a lever is used as a Pavlovian cue in rodent studies, CS directed responding (sign-tracking) often develops over training such that eventually all animals bias their responding towards the lever than towards the US (goal-tracking at the magazine). However, the nature of this shift highlights the important point that these CS and US directed responses can be quite distinct physically as well as psychologically. Therefore, by conflating the development of these different forms of responding, it is not clear whether the relationship between C/T and the acquisition of responding describes the sum of all Pavlovian responding or predominantly CS or US directed responding.

Another interesting aspect of these findings is that there is a large amount of variability that scales inversely with C/T. A potential account of the source of this variability is related to the absence of preexposure to the reward pellets. This is normally done within the animals' homecage as a form of preexposure to reduce neophobia. If some rats take longer to notice and then approach and finally consume the reward pellets in the magazine, the impact of this would systematically differ depending on the length of the ITI. For animals presented with relatively short CSs and ITIs, they may essentially miss the first couple of trials and/or attribute uneaten pellets accumulating in the magazine to the background/contextual rate of reinforcement. What is not currently clear is whether this was accounted for in some way by confirming when the rats first started retrieving and consuming the rewards from the magazine.

While the generality of these findings across species is impressive, the very specific set of parameters employed to generate these data raise questions about the generality of these findings across other standard Pavlovian conditioning parameters. While this is obviously beyond the scope of the present experiment, it is important to consider that the present study explored a situation with 100% reinforcement on every trial, with a variable duration CS (drawn form a uniform distribution), with a single relatively brief CS (maximum of 122s) CS and a single US. Again, the choice of these parameters in the present experiment is appropriate and very deliberately based on refinements from many previous studies from the authors. This includes a number of criteria used to define magazine response frequency that includes discarding specific responses (discussed and reasonably justified clearly in the methods section). Similarly, the finding that terminal rates of responding are reliably related to 1/T is surprising, and it is not clear whether this might be a property specific to this form of variable duration CS, the use of a uniform sampling distribution, or the use of only a single CS. However, it is important to keeps these limitations in mind when considering some of the claims made in the discussion section of this manuscript that go beyond what these data can support.

The main finding demonstrating the consistent findings across species is presented in Figure 3. In the analysis of these data, it is not clear why the correlations between C, T, and C/T and the measure of acquisition in Figure 3A were presented as r values, whereas the r2 values were presented in the discussion of Figure 3B, and no values were provided in discussing Figure 3C. The measure of acquisition in Figure 3A is based on a previously established metric, whereas the measure in Figure 3B employs the relatively novel nDKL measure that is argued to be a better and theoretically based metric. Surprisingly, when r and r2 values are converted to the same metric across analyses, it appears that this new metric (Figure 3B) does well but not as well as the approach in Figure 3A. This raises questions about why a theoretically derived measure might not be performing as well on this analysis, and whether the more effective measure is either more reliable or tapping into some aspect of the processes that underlie acquisition that is not accounted for by the nDKL metric. Unfortunately, the new metric is discussed and defined at great length but its utility is not considered.<br /> An important analysis issue that is unclear in the present manuscript is exactly how the statistics were run (how the model was defined, were individual subjects or group medians used, what software was used etc...). For example, it is not clear whether the analyses conducted in relation to Figure 3 used the data from individual rats or the group medians. Similarly, it appears that each rat contributes four separate data points, and a single regression line was fit to all these data despite the highly likely violation of the assumption independent observations (or more precisely, the assumption of uncorrelated errors) in this analysis. Furthermore, it is claimed that the same regression line fit the IT and CS period data in this figure, however this<br /> If the data in figure 3 were analyzed with log(ITI) or log(C/ITI) i.e. log(C/(T-C)), would this be a better fit for these data? Is it the case that the ratio of C/T the best predictor of the trial/point of acquisition, or is it the case that another metric related to reinforcement rates provides a better fit?

Based on the variables provided in Supplementary file 3, containing the acquisition data, I was unable to reproduce the values reported in the analysis of Figure 3.<br /> In relation to Figure 3: I am curious about whether the authors would be able to comment on whether the individual variability in trials to acquisition would be expected to scale differently based on C/T, or C, or (if a less restricted range was used) T?<br /> It is not clear why Figure 3C is presented but not analyzed, and why the data presented in Figure 4 to clarify the spread of the distribution of the data observed across the plots in Figure 3 uses the data from Figure 3C. This would seem like the least representative data to illustrate the point of Figure 4. It also appears to my eye that the data actually plotted in Figure 4 correspond to Figure 3A and 3B rather than the odds 10:1 data indicated in text.

What was the decision criteria used to decide on averaging the final 5 conditioning sessions as terminal responding for the analyses in Figure 5? This is an oddly specific number. Was this based on consistency with previous work, or based on the greatest number of sessions where stable data for all animals could be extracted?<br /> In the analysis corresponding to Figures 7-8: If I understand the description of this analysis correctly, for each rat the data are the cumulative response data during the CS, starting from the trial on which responding to the CS > ITI (t = 1), and ending at the trial on which CS responding peaked (maximum over 3 session moving average window; t = end). This analysis does not seem to account for changes (decline) in the ITI response rates over this period of acquisition, and it is likely that responding during the ITI is still declining after t=1. Are the 4 functions that were fit to these data to discriminate between different underlying generative processes still appropriate on total CS responding instead of conditional CS responding after accounting for changes in baseline response rates during ITI?

Page 27, Procedure, final sentence: The magazine responding during the ITI is defined as the 20s period immediately before CS onset. The range of ITI values (Table 1) always starts as low as 15s in all 14 groups. Even in the case of an ITI on a trial that was exactly 20s, this would also mean that the start of this period overlaps with the termination of the CS from the previous trial and delivery (and presumably consumption) of a pellet. Please indicate if the definition of the ITI period was modified on trials where the preceding ITI was <20s, and if any other criteria were used to define the ITI.

Were the rats exposed to the reinforcers/pellets in their home cage prior to acquisition? Please indicate whether rats where pre-exposed to the reward pellets in their home cages e.g. as is often done to reduce neophobia. Given the deliberate absence of a magazine-training phase, this information is important when assessing the experienced contingency between the CS and the US.

For all the analyses, please provide the exact models that were fit and the software used. For example, it is not necessarily clear to the reader (particularly in the absence of degrees of freedom) that the model fits discussed in Figure 3 are fit on the individual subject data points or the group medians. Similarly, in Figure 6 there is no indication of whether a single regression model was fit to all the plotted data or whether tests of different slopes for each of the conditions were compared. With regards to the statistics in Figure 6, depending on how this was run, it is also a potential problem that the analyses does not correct for the potentially highly correlated multiple measurements from the same subjects i.e. each rat provides 4 data points which are very likely not to be independent observations.

A number of sections of the discussion are speculative or not directly supported by the present experimental data (but may well be supported by previous findings that are not the direct focus of the present experiment). For example, Page 19, Paragraph 2: this entire paragraph is not really clearly explained and is presenting an opinion rather than a strong conclusion that follows directly from the present findings. Evidence for an aspect of RET in the present paper (i.e. the prediction of time scale invariance on the initial point of acquisition, but not necessarily the findings regarding the rate of terminal acquisition) - while supportive - does not necessarily provide unconditional evidence for this theory over all the alternatives.

Similarly, the Conclusion section (Page 23) makes the claim that "the equations have at most one free parameter", which may be an oversimplification that is conditionally true in the narrow context of the present experiment where many things were kept constant between groups and run in a particular way to ensure this is the case. While the equations do well in this narrow case, it is unlikely that additional parameters would not need to be added to account for more general learning situations. To clarify, I am not contending that this kind of statement is necessarily untrue, merely that it is being presented in a narrow context and may require a deeper discussion of much more of the literature to qualify/support properly - and the discussion section of the present experiment/manuscript may not be the appropriate place for this.

- Consider taking advantage of an "Ideas and Speculation" subsection within the Discussion that is supported by eLife [ https://elifesciences.org/inside-elife/e3e52a93/elife-latest-including-ideas-and-speculation-in-elife-papers ]. This might be more appropriate to qualify the tone of much of the discussion from page 19 onwards.

It seems like there are entire analyses and new figures being presented in the discussion e.g. Page 20: Information-Theoretic Contingency. These sections might be better placed in the methods section or a supplementary section/discussion.

Reviewer #1 (Public review):

The manuscript by Zhang et al describes the use of a protein language model (pLM) to analyse disordered regions in proteins, with a focus on those that may be important in biological phase separation. While the paper is relatively easy to read overall, my main comment is that the authors could perhaps make it clearer which observations are new, and which support previous work using related approaches. Further, while the link to phase separation is interesting, it is not completely clear which data supports the statements made, and this could also be made clearer.

Major comments:

(1) With respect to putting the work in a better context of what has previously been done before, this is not to say that there is not new information in it, but what the authors do is somewhat closely related to work by others. I think it would be useful to make those links more directly. Some examples:

(1a) Alderson et al (reference 71) analysed in detail the conservation of IDRs (via pLDDT, which is itself related to conservation) to show, for example, that conserved residues fold upon binding. This analysis is very similar to the analysis used in the current study (using ESM2 as a different measure of conservation). Thus, the approach (pages 7-8) described as "This distinction allows us to classify disordered regions into two types: "flexible disordered" regions, which show high ESM2 scores and greater mutational tolerance, and "conserved disordered" regions, which display low ESM2 scores, indicating varying levels of mutational constraint despite a lack of stable folding." is fundamentally very similar to that used by Alderson et al. Thus, the result that "Given that low ESM2 scores generally reflect mutational constraint in folded proteins, the presence of region a among disordered residues suggests that certain disordered amino acids are evolutionarily conserved and likely functionally significant" is in some ways very similar to the results of that paper.

(1b) Dasmeh et al (https://doi.org/10.1093/genetics/iyab184), Lu et al (https://doi.org/10.1371/journal.pcbi.1010238) and Ho & Huang (https://doi.org/10.1002/pro.4317) analysed conservation in IDRs, including aromatic residues and their role in phase separation

(1c) A number of groups have performed proteomewide saturation scans using pLMs, including variants of the ESM family, including Meier (reference 89, but cited about something else) and Cagiada et al (https://doi.org/10.1101/2024.05.21.595203) that analysed variant effects in IDRs using a pLM. Thus, I think statements such as "their applicability to studying the fitness and evolutionary pressures on IDRs has yet to be established" should possibly be qualified.

(2) On page 4, the authors write, "The conserved residues are primarily located in regions associated with phase separation." These results are presented as a central part of the work, but it is not completely clear what the evidence is.

(3) It would be useful with an assessment of what controls the authors used to assess whether there are folded domains within their set of IDRs.

Reviewer #2 (Public review):

This manuscript uses the ESM2 language model to map the evolutionary fitness landscape of intrinsically disordered regions (IDRs). The central idea is that mutational preferences predicted by these models could be useful in understanding eventual IDR-related behavior, such as disruption of otherwise stable phases. While ESM2-type models have been applied to analyze such mutational effects in folded proteins, they have not been used or verified for studying IDRs. Here, the authors use ESM2 to study membraneless organelle formation and the related fitness landscape of IDRs.

Through this, their key finding in this work is the identification of a subset of amino acids that exhibit mutation resistance. Their findings reveal a strong correlation between ESM2 scores and conservation scores, which if true, could be useful for understanding IDRs in general. Through their ESM2-based calculations, the authors conclude that IDRs crucial for phase separation frequently contain conserved sequence motifs composed of both so-called sticker and spacer residues. The authors note that many such motifs have been experimentally validated as essential for phase separation.

Unfortunately, I do not believe that the results can be trusted. ESM2 has not been validated for IDRs through experiments. The authors themselves point out its little use in that context. In this study, they do not provide any further rationale for why this situation might have changed. Furthermore, they mention that experimental perturbations of the predicted motifs in in vivo studies may further elucidate their functional importance, but none of that is done here. That some of the motifs have been previously validated does not give any credibility to the use of ESM2 here, given that such systems were probably seen during the training of the model.

I believe that the authors should revamp their whole study and come up with a rigorous, scientific protocol where they make predictions and test them using ESM2 (or any other scientific framework).

Reviewer #3 (Public review):

Summary:

This is a very nice and interesting paper to read about motif conservation in protein sequences and mainly in IDRs regions using the ESM2 language model. The topic of the paper is timely, with strong biological significance. The paper can be of great interest to the scientific community in the field of protein phase transitions and future applications using the ESM models. The ability of ESM2 to identify conserved motifs is crucial for disease prediction, as these regions may serve as potential drug targets. Therefore, I find these findings highly significant, and the authors strongly support them throughout the paper. The work motivates the scientific community towards further motif exploration related to diseases.

Strengths:

(1) Revealing conserved regions in IDRs by the ESM-2 language model.

(2) Identification of functionally significant residues within protein sequences, especially in IDRs.

(3) Findings supported by useful analyses.

Weaknesses:

(1) Lack of examples demonstrating the potential biological functions of these conserved regions

(2) Very limited discussion of potential future work and of limitations.

Reviewer #1 (Public review):

Summary:

Systemic and partial Tcf7l2 repression is effective in protecting cancer mice from cachexia-induced death. Hence, this is a promising treatment strategy for cancer patients suffering from cachexia.

Strengths:

The method is well-designed and clearly explained.

Weaknesses:

(1) Abbreviations should be mentioned in full terms for the first time.

(2) Relatively old or even very old references in the Introduction and Discussion.

(3) The result section contains discussion with references, as well.

(4) The number of mice in individual groups is relatively small (3 mice in some groups).

Reviewer #2 (Public review):

Summary:

This study by Leong and colleagues examines the role of the TCF7L2 transcription factor in the Wnt signaling pathway as a regulator of colon/small intestinal cancers and cachexia. Investigators utilize a Tet off repressor genetic system in mice under Dox regulation to silence TCF7L2. Results show DSS-treated APCMin/+ mice lose body weight that can be rapidly rescued by Dox treatment and suppression of TCF7L2 expression. Reduction of TCF7L2 rescues features of cachexia, including body weight, gastrocnemius muscle and adipose mass, as well as molecular markers of cachexia such as the E3 Ub ligases, MuRF1, and Atrogin-1. The most significant finding in the study is that loss of TCF7L2 reduces but does not eliminate tumor progression, as tumors go from adenomas to adenocarcinomas over time while mice are treated with Dox, yet cachexia persists. This implies that TCF7L2 has a direct effect on cachexia. Overall, the study provides insight into the role of TCFL2 in the development of intestinal cancers and muscle atrophy in cachexia.

Strengths:

The study uses an elegant genetic mouse model to provide significant new insight into the role of TCFL2 in colon and small intestinal cancers. In addition, the authors describe the role of TCF7L2 as a regulator of muscle wasting in cachexia. This, too, can be viewed as a new finding for the cachexia field.

Weaknesses:

However, in its current form, the study lacks sufficient data to support the authors' claim regarding the relevance of TCF7L2 as a regulator of cachexia.

Reviewer #1 (Public review):

This is a very elegant and convincing study. Using systematic screening of actin tail formation in two bacterial strains and employing a panel of CRISPR-CAS ko cell lines, the authors identify a novel dynamin-related GTPase GVIN, which forms an oligomeric coat around an intracellular Burkholderia strain. The bacterial O-antigen LPS layer is required for the formation of the GVIN coat, which disturbs the polar localization of the bacterial actin-polymerizing BimA protein.

I am not an expert in infection studies, but the experiments appear to be of high quality, the figures are well prepared, and clean and statistically significant results are provided. I have no criticism of the presented approaches.

The identification of a novel GBP1-independent pathway targeting intracellular bacteria is not only of fundamental importance for the immunity field but also of high interest to researchers in other areas, for example, evolutionary or structural biologists.

Reviewer #2 (Public review):

Summary:

The authors wanted to investigate how cells defend against intracellular pathogens, such as Shigella and Burkholderia species, that co-opt the host actin machinery to spread from cell-to-cell. Previous work has identified IFNg-inducible GTPase of the Guanylate Binding Protein (GBP) family in cytosolic defence against Gram-negative bacteria. By forming a coat around Shigella, human GBP1 suppresses actin-based motility by displacing IcsA, which is the actin-polymerising virulence factor present at bacterial poles. In addition, GBP1 recruits the cytosolic LPS-sensor, caspase-4, to the bacterial surface, which results in the removal of bacterial replicative niches via pyroptotic cell death. Here, they followed up their finding that GBP1 can reduce actin-based motility of Shigella in HeLa cells and, surprisingly, fails to do so during Burkholderia infection. In contrast, in T24 bladder epithelial cells, GBP1 is competent in blocking Burkholderia actin-tails. They therefore wanted to identify the GBP1-independent factor that blocks actin-based motility in IFNg-treated cells that is absent in HeLa cells.

Major strengths and weaknesses of the methods and results:

The authors report a second IFNg-dependent pathway involving the protein product of the gene GVIN1, which was previously thought to be a pseudogene. GVIN1 (GTPase, very large interferon inducible 1) is thus the first human member of this family of ~250 kDa putative GTPases to be demonstrated to be functional and have potential antimicrobial roles. The discovery that GVIN1 is indeed functional, forms coats on Burkholderia in an LPS O-antigen-dependent manner, and limits actin-dependent motility are the main strengths of this paper. The authors use CRISPR/Cas9-based knockouts in HeLa and T24 cells, and complement them to demonstrate that GBP1 and GVIN1 are both required to inhibit actin-based motility.

An appraisal of whether the authors achieved their aims and whether the results support their conclusions:

The authors achieved their main goals through well-planned experiments and unbiased screens. They succeeded in finding the factor that blocks actin-based motility independently of GBP1. This is driven by GVIN1, which coats bacteria and limits actin-tail formation by reducing the expression of BimA through currently unknown mechanisms. Further, they found that an O-antigen mutant can escape coating by GVIN1, indicating the requirement for these polysaccharides in GVIN1-dependent bacterial sensing. However, the authors have not investigated whether GVIN1, which has two GTPase-domains, does indeed have GTPase activity and whether GVIN1 and GBP1 together completely block cell-to-cell spread by Burkholderia and thereby restrict bacterial numbers over the infection time course. They also do not show whether GBP1 and GVIN1 target the same bacterial cell or different populations of bacteria.

A discussion of the likely impact of the work on the field, and the utility of the methods and data to the community:

This work uncovers the antimicrobial actions of a member of yet another family of IFNg-induced GTPases, which potentially acts against other intracellular pathogens. GVIN1 appears to operate independently and in parallel to GBP1, pointing to the breadth and complexity of the IFNg-inducible GTPase families.

Reviewer #3 (Public review):

Summary:

Here, Guo et al. (2025) propose that the IFN-induced GTPase GVIN1 forms a coat on cytosolic Burkholderia thailandensis, blocking actin tail formation through a mechanism analogous to GBP1-mediated restriction of Shigella motility.

Their study was prompted by the intriguing observation that IFNγ priming and GBP1 coat formation fail to inhibit B. thailandensis actin-based motility in HeLa cells, yet IFNγ restricts the motility of Burkholderia in T24 cells. Further investigation revealed that IFNγ restricts B. thailandensis motility in T24 cells via both GBP1-dependent and -independent mechanisms, suggesting that HeLa cells lack a critical GBP1 co-factor required to inhibit actin tail formation.

To identify the GBP1-independent mechanism, the authors performed an siRNA screen of interferon-stimulated genes (ISGs) and identified GVIN1, a large IFN-induced GTPase, as essential for restricting B. thailandensis motility. To identify the GBP1-independent mechanism, perform a knock-down screen for ISGs and find that the loss of GVIN, a very large IFN-induced GTPase, results in higher actin tail-positive B. thailandensis in T24 cells. They further demonstrate that GVIN forms coats on the surface of B. thailandensis, which prevent the polar localization of BimA and thus actin tail formation. In summary, the data reveal two independent IFNγ-induced pathways that restrict bacterial motility: one GBP1-dependent and the other GVIN1-dependent, each relying on distinct host co-factors.

Global assessment:

This is a well-executed study that convincingly demonstrates how GVIN1 restricts the actin-based motility of B. thailandensis through the assembly of coatomers. The results are clearly described, the manuscript is easy to follow, and the data are overall compelling and well presented. I have only a few suggestions on how the manuscript could be further improved.

Reviewer #1 (Public review):

Summary:

This manuscript describes a novel magnetic steering technique to target human adipose derived mesenchymal stem cells (hAMSC) or induce pluripotent stem cells to the TM (iPSC-TM). The authors show delivery of the stem cells lowered IOP, increased ouflow facility, and increased TM cellularity.

Strengths:

The technique is novel and shows promise as a novel therapeutic to lower in IOP in glaucoma. hAMSC are able to lower IOP below baseline as well as increase outflow facility above baseline with no tumorigenicity. These data will have a positive impact on the field and will guide further research using hAMSC in glaucoma models.

Weaknesses:

The transgenic mouse model of glaucoma the authors used did not show ocular hypertensive phenotypes as previously reported; therefore, the Tg-MYOCY437H model should be used with caution in the future. However, the results presented here clearly show magnetically steered cell therapy as a viable treatment strategy to lower intraocular pressure even from baseline. Future studies are needed to demonstrate the effects in ocular hypertensive eyes.

Reviewer #2 (Public review):

This observational study investigates the efficacy of intracameral injected human stems cells as a means to re-functionalize the trabecular meshwork for the restoration of intraocular pressure homeostasis. Using a murine model of glaucoma, human adipose-derived mesenchymal stem cells are shown to be biologically safer and functionally superior at eliciting a sustained reduction in intraocular pressure (IOP). The authors conclude that the use of magnetically-steered human adipose-derived mesenchymal stem cells has potential for long-term treatment of ocular hypertension in glaucoma.

Comments on revisions: Previously noted concerns have been thoughtfully and sincerely considered by the authors and are now clearly addressed in the revised manuscript. No further concerns/comments.

Reviewer #1 (Public review):

The authors attempted to replicate previous work showing that counterconditioning leads to more persistent reduction of threat responses, relative to extinction. They also aimed to examine the neural mechanisms underlying counterconditioning and extinction. They achieved both of these aims, and were able to provide some additional information, such as how counterconditioning impacts memory consolidation. Having a better understanding of which neural networks are engaged during counterconditioning may provide novel pharmacological targets to aid in therapies for traumatic memories. It will be interesting to follow up by examining the impact of varying amounts of time between acquisition and counterconditioning phases, to enhance replicability to real world therapeutic settings.

Major strengths

• This paper is very well written and attempts to comprehensively assess multiple aspects counterconditioning and extinction processes. For instance, the addition of memory retrieval tests is not core to the primary hypotheses, but provides additional mechanistic information on how episodic memory is impacted by counterconditioning. This methodical approach is commonly seen in animal literature, but less so in human studies.

• The Group x Cs-type x Phase repeated measure statistical tests with 'differentials' as outcome variables are quite complex, however the authors have generally done a good job of teasing out significant F test findings with post hoc tests and presenting the data well visually. It is reassuring that there is convergence between self-report data on arousal and valence and the pupil dilation response. Skin conductance is a notoriously challenging modality, so it is not too concerning that this was placed in the supplementary materials. Neural responses also occurred in logical regions with regards to reward learning.

• Strong methodology with regards to neuroimaging analysis, and physiological measures.

• The authors are very clear on documenting where there were discrepancies from their pre-registration and providing valid rationales for why.

Major Weaknesses

• The statistics showing that counterconditioning prevents differential spontaneous recovery are the weakest p values of the paper (and using one tailed tests, although this is valid due to directions being pre-hypothesised). This may be due to relatively small number of participants and some variability in responses.

Reviewer #2 (Public review):

Summary:

The present study sets out to examine the impact of counterconditioning (CC) and extinction on conditioned threat responses in humans, particularly looking at neural mechanisms involved in threat memory suppression. By combining behavioral, physiological, and neuroimaging (fMRI) data, the authors aim to provide a clear picture of how CC might engage unique neural circuits and coding dynamics, potentially offering a more robust reduction in threat responses compared to traditional extinction.

Strengths:

One major strength of this work lies in its thoughtful and unique design - integrating subjective, physiological, and neuroimaging measures to capture the variouse aspects of counterconditiong (CC) in humans. Additionally, the study is centered on a well-motivated hypothesis and the findings have potentials for improving the current understanding of pathways associated with emotional and cognitive control.

The data presentation is systematic, and the results on behavioral and physiological measures fit well with the hypothesized outcomes. The neuroimaging results also provide strong support for distinct neural mechanisms underlying CC versus extinction.

Weaknesses:

Overall, this study is a well-conducted and thought-provoking investigation into counterconditioning, with strong potential to advance our understanding of threat modulation mechanisms. Two minor weaknesses concern the scope and decisions regarding analysis choices. First, while the findings are solid, the topic of counterconditioning is relatively niche and may have limited appeal to a broader audience. Expanding the discussion to connect counterconditioning more explicitly to widely studied frameworks in emotional regulation or cognitive control would enhance the paper's accessibility and relevance to a wider range of readers. This broader framing could also underscore the generalizability and broader significance of the results. In addition, detailed steps in the statistical procedures and analysis parameters seem to be missing. This makes it challenging for readers to interpret the results in light of potential limitations given the data modality and/or analysis choices.

Comments on revisions: My previous concerns and questions have been sufficiently addressed.

Reviewer #3 (Public review):

In this manuscript, Wirz et al use neuroimaging (fMRI) to show that counterconditioning produces a longer lasting reduction in fear conditioning relative to extinction and appears to rely on the nucleus accumbens rather than the ventromedial prefrontal cortex. These important findings are supported by convincing evidence and will be of interest to researchers across multiple subfields, including neuroscientists, cognitive theory researchers, and clinicians.

In large part, the authors achieved their aims of giving a qualitative assessment of the behavioural mechanisms of counterconditioning versus extinction, as well as investigating the brain mechanisms. The results support their conclusions and give interesting insights into the psychological and neurobiological mechanisms of the processes that underlie the unlearning, or counteracting, of threat conditioning.

Strengths:

* Clearly written with interesting psychological insights<br /> * Excellent behavioural design, well-controlled and tests for a number of different psychological phenomena (e.g. extinction, recovery, reinstatement, etc).<br /> * Very interesting results regarding the neural mechanisms of each process.<br /> * Good acknowledgement of the limitations of the study.

Weaknesses:

* I am not sure that the memories tested were truly episodic<br /> * Twice as many female participants than males

Comments on revisions: I have no remaining concerns

Reviewer #1 (Public review):

Summary:

Audio et al. present an interesting study examining cerebral blood volume (CBV) across cortical areas and layers in non-human primates (NHPs) using high-resolution MRI. While with contrast agents are frequently employed to improve fMRI sensitivity in NHP research, its application for characterizing baseline CBV distribution is less common. This study quantifies large-vessel distribution as well as regional and laminar CBV variations, comparing them with other metrics.

Strengths:

(1) Noninvasive mapping of relative cerebral blood volume is novel for non-human primates.<br /> (2) A key finding was the observation of variations in CBV across regions; primary sensory cortices had high CBV, whereas other higher areas had low CBV.<br /> (3) The measured relative CBV values correlated with previously reported neuronal and receptor densities, potentially providing valuable physiological insights.

Weaknesses:

(1) A weakness of this manuscript is that the quantification of CBV with postprocessing approaches to remove susceptibility effects from pial and penetrating vessels is not fully validated, especially on a laminar scale.<br /> (2) High-resolution MRI with a critical sampling frequency estimated from previous studies (Weber 2008, Zheng 1991) was performed to separate penetrating vessels. However, this approach depends on multiple factors, including spatial resolution, contrast agent dosage, and data processing methods. This raises concerns about the generalizability of these findings to other experimental setups or populations.<br /> (3) Baseline R2* is sensitive to baseline R2, vascular volume, iron content, and susceptibility gradients. Additionally, it is sensitive to imaging parameters; higher spatial resolution tends to result in lower R2* values (closer to the R2 value). Although baseline R2* correlates with several physiological parameters, drawing direct physiological inferences from it remains challenging.<br /> (4) CBV-weighted deltaR2*, which depends on both CBV and contrast agent dose, correlates with various metrics (cytoarchitectural parcellation, myelin/receptor density, cortical thickness, CO, cell-type specificity, etc.). While such correlations may be useful for exploratory analyses, all comparisons depend on measurement accuracy. A fundamental question remains whether CBV-weighted ΔR2* can provide reliable and biologically meaningful insights into these metrics, particularly in diseased or abnormal brain states.

Reviewer #2 (Public review):

Summary:

This manuscript presents a new approach for non-invasive, MRI-based, measurements of cerebral blood volume (CBV). Here, the authors use ferumoxytol, a high-contrast agent and apply specific sequences to infer CBV. The authors then move to statistically compare measured regional CBV with known distribution of different types of neurons, markers of metabolic load and others. While the presented methodology captures and estimated 30% of the vasculature, the authors corroborated previous findings regarding lack of vascular compartmentalization around functional neuronal units in the primary visual cortex.

Strengths:

Non-invasive methodology geared to map vascular properties in vivo.

Implementation of a highly sensitive approach for measuring blood volume.

Ability to map vascular structural and functional vascular metrics to other types of published data.

Weaknesses:

The key issue here is the underlying assumption about the appropriate spatial sampling frequency needed to captures the architecture of the brain vasculature. Namely, ~7 penetrating vessels / mm2 as derived from Weber et al 2008 (Cer Cor). The cited work, begins by characterizing the spacing of penetrating arteries and ascending veins using vascular cast of 7 monkeys (Macaca mulatta, same as in the current paper). The ~7 penetrating vessels / mm2 is computed by dividing the total number of identified vessels by the area imaged. The problem here is that all measurements were made in a "non-volumetric" manner and only in V1. Extrapolating from here to other brain areas is therefore not possible without further exploration with independent methodologies.

Please note that these are comments on the revised version.

Reviewer #1 (Public review):

Summary:

This study explores how heterozygosity for specific neurodevelopmental disorder-associated Trio variants affects mouse behavior, brain structure, and synaptic function, revealing distinct impacts on motor, social, and cognitive behaviors linked to clinical phenotypes. Findings demonstrate that Trio variants yield unique changes in synaptic plasticity and glutamate release, highlighting Trio's critical role in presynaptic function and the importance of examining variant heterozygosity in vivo.

Strengths:

This study generated multiple mouse lines to model each Trio variant, reflecting point mutations observed in human patients with developmental disorders. The authors employed various approaches to evaluate the resulting behavioral, neuronal morphology, synaptic function, and proteomic phenotypes.

Reviewer #2 (Public review):

Summary:

The authors generated three mouse lines harboring ASD, Schizophrenia, and Bi-polar-associated variants in the TRIO gene. Anatomical, behavioral, physiological, and biochemical assays were deployed to compare and contrast the impact of these mutations in these animals. In this undertaking the authors sought to identify and characterize the cellular and molecular mechanisms responsible for ASD, Schizophrenia, and Bi-polar disorder development.

Strengths:

The establishment of TRIO dysfunction in the development of ASD, Schizophrenia, and Bi-polar disorder is very recent and of great interest. Disorder-specific variants have been identified in the TRIO gene, and this study is the first to compare and contrast the impact of these variants in vivo in preclinical models. The impact of these mutations was carefully examined using an impressive host of methods. The authors achieved their goal of identifying behavioral, physiological, and molecular alterations that are disorder/variant specific. The impact of this work is extremely high given the growing appreciation of TRIO dysfunction in a large number of brain-related disorders. This work is very interesting in that it begins to identify the unique and subtle ways brain function is altered in ASD, Schizophrenia, and Bi-polar disorder.

Weaknesses:

(1) Most assays were performed in older animals and perhaps only capture alterations that result from homeostatic changes resulting from prodromal pathology that may look very different.

(2) Identification of upregulated (potentially compensating) genes in response to these disorder specific Trio variants is extremely interesting. However, a functional demonstration of compensation is not provided.

(3) There are instances where data is not shown in the manuscript. See "data not shown". All data collected should be provided even if significant differences are not observed.

I consider weaknesses 1 and 2 minor. While they would very interesting to explore, these experiments might be more appropriate for a follow up study. The missing data in 3 should be provided in the supplemental material.

Revised Manuscript:

All of my above concerns were well addressed by the authors in the revised submission.

Reviewer #2 (Public review):

Summary:

This manuscript is about using different analytical approaches to allow ancestry adjustments to GWAS analyses amongst admixed populations. This work is a follow-on from the recently published ITHGC multi-population GWAS (https://doi.org/10.7554/eLife.84394), with the focus on the admixed South African populations. Ancestry adjustment models detected a peak of SNPs in the class II HLA DPB1, distinct from the class II HLA DQA1 loci signficant in the ITHGC analysis.

Strengths:

Excellent demonstration of GWAS analytical pipelines in highly admixed populations. Particularly the utility of ancestry adjustment to improve study power to detect novel associations. Further confirmation of the importance of the HLA class II locus in genetic susceptibility to TB.

Weaknesses:

Limited novelty compared to the group's previous existing publications and the body of work linking HLA class II alleles with TB susceptibility in South Africa or other African populations. This work includes only ~100 new cases and controls from what has already been published. High resolution HLA typing has detected significant signals in both the DQA1 and DPB1 regions identified by the larger ITHGC and in this GWAS analysis respectively (Chihab L et al. HLA. 2023 Feb; 101(2): 124-137).<br /> Despite the availability of strong methods for imputing HLA from GWAS data (Karnes J et Plos One 2017), the authors did not confirm with HLA typing the importance of their SNP peak in the class II region. This would have supported the importance of this ancestry adjustment versus prior ITHGC analysis.

The populations consider active TB and healthy controls (from high-burden presumed exposed communities) and do not provide QFT or other data to identify latent TB infection.

Important methodological points for clarification and for readers to be aware of when reading this paper:

(1) One of the reasons cited for the lack of African ancestry-specific associations or suggestive peaks in the ITHGC study was the small African sample size. The current association test includes a larger African cohort and yields a near-genome-wide significant threshold in the HLA-DPB1 gene originating from the KhoeSan ancestry. Investigation is needed as to whether the increase in power is due to increased African samples and not necessarily the use of the LAAA model as stated on lines 295 and 296?

Authors response - The Manhattan plot in Figure 3 includes the results for all four models: the traditional GWAS model (GAO), the admixture mapping model (LAO), the ancestry plus allelic (APA) model and the LAAA model. In this figure, it is evident that only the LAAA model identified the association peak on chromosome 6, which lends support the argument that the increase in power is due to the use of the LAAA model and not solely due to the increase in sample size.<br /> Reviewer comment - This data supports the authors conclusions that increase power is related to the LAAA model application rather than simply increase sample size.

(2) In line 256, the number of SNPs included in the LAAA analysis was 784,557 autosomal markers; the number of SNPs after quality control of the imputed dataset was 7,510,051 SNPs (line 142). It is not clear how or why ~90% of the SNPs were removed. This needs clarification.

Authors response:<br /> In our manuscript (line 194), we mention that "...variants with minor allele frequency (MAF) < 1% were removed to improve the stability of the association tests." A large proportion of imputed variants fell below this MAF threshold and were subsequently excluded from this analysis.

Reviewers additional comment: The authors should specify the number of SNPs in the dataset before imputation and indicate what proportion of the 784,557 remaining SNPs were imputed. Providing this information might help the reader better understand the rationale behind the imputation process.

(3) The authors have used the significance threshold estimated by the STEAM p-value < 2.5x10-6 in the LAAA analysis. Grinde et al. (2019 implemented their significance threshold estimation approach tailored to admixture mapping (local ancestry (LA) model), where there is a reduction in testing burden. The authors should justify why this threshold would apply to the LAAA model (a joint genotype and ancestry approach).

Authors response: We describe in the methods (line 189 onwards) that the LAAA model is an extension of the APA model. Since the APA model itself simultaneously performs the null global ancestry only model and the local ancestry model (utilised in admixture mapping), we thus considered the use of a threshold tailored to admixture mapping appropriate for the LAAA model.

Reviewers additional comment: While the LAAA model is an extension of the APA model, the authors describe the LAAA test as 'models the combination of the minor allele and the ancestry of the minor allele at a specific locus, along with the effect of this interaction,' thus a joint allele and ancestry effects model. Grinde et al. (2019) proposed the significance threshold estimation approach, STEAM, specifically for the LA approach, which tests for ancestry effects alone and benefits from the reduced testing burden. However, it remains unclear why the authors found it appropriate to apply STEAM to the LAAA model, a joint test for both allele and ancestry effects, which does not benefit from the same reduction in testing burden.

(4) Batch effect screening and correction (line 174) is a quality control check. This section is discussed after global and local ancestry inferences in the methods. Was this QC step conducted after the inferencing? If so, the authors should justify how the removed SNPs due to the batch effect did not affect the global and local ancestry inferences or should order the methods section correctly to avoid confusion.

Authors response: The batch effect correction method utilised a pseudo-case-control comparison which included global ancestry proportions. Thus, batch effect correction was conducted after ancestry inference. We excluded 36 627 SNPs that were believed to have been affected by the batch effect. We have amended line 186 to include the exact number of SNPs excluded due to batch effect.<br /> The ancestry inference by RFMix utilised the entire merged dataset of 7 510 051 SNPs. Thus, the SNPs removed due to the batch effect make up a very small proportion of the SNPs used to conduct global and local ancestry inferences (less than 0.5%). As a result, we do not believe that the removed SNPs would have significantly affected the global and local ancestry inferences. However, we did conduct global ancestry inference with RFMix on each separate dataset as a sanity check. In the tables below, we show the average global ancestry proportions inferred for each separate dataset, the average global ancestry proportions across all datasets and the average global ancestry proportions inferred using the merged dataset. The SAC and Xhosa cohorts are shown in two separate tables due to the different number of contributing ancestral populations to each cohort. The differences between the combined average global ancestry proportions across the separate cohorts does not differ significantly to the global ancestry proportions inferred using the merged dataset.

This is an excellent response and should remain accessible to readers for clarifying this issue.

Comments on revisions:

Thank you for addressing my other recommendations to authors. These have all been satisfactorily addressed.