Reviewer #1 (Public review):

Summary:

The aim of this paper is to develop a simple method to quantify fluctuations in the partitioning of cellular elements. In particular, they propose a flow-cytometry-based method coupled with a simple mathematical theory as an alternative to conventional imaging-based approaches.

Strengths:

The approach they develop is simple to understand and its use with flow-cytometry measurements is clearly explained. Understanding how the fluctuations in the cytoplasm partition vary for different kinds of cells is particularly interesting.

Weaknesses:

The theory only considers fluctuations due to cellular division events. This seems a large weakness because it is well known that fluctuations in cellular components are largely affected by various intrinsic and extrinsic sources of noise and only under particular conditions does partitioning noise become the dominant source of noise.

Reviewer #2 (Public review):

Summary:

The authors present a combined experimental and theoretical workflow to study partitioning noise arising during cell division. Such quantifications usually require time-lapse experiments, which are limited in throughput. To bypass these limitations, the authors propose to use flow-cytometry measurements instead and analyse them using a theoretical model of partitioning noise. The problem considered by the authors is relevant and the idea to use statistical models in combination with flow cytometry to boost statistical power is elegant. The authors demonstrate their approach using experimental flow cytometry measurements and validate their results using time-lapse microscopy. However, while I appreciate the overall goal and motivation of this work, I was not entirely convinced by the strength of this contribution. The approach focuses on a quite specific case, where the dynamics of the labelled component depend purely on partitioning. As such it seems incompatible with studying the partitioning noise of endogenous components that exhibit production/turnover. The description of the methods was partly hard to follow and should be improved. In addition, I have several technical comments, which I hope will be helpful to the authors.

Comments:

(1) In the theoretical model, copy numbers are considered to be conserved across generations. As a consequence, concentrations will decrease over generations due to dilution. While this consideration seems plausible for the considered experimental system, it seems incompatible with components that exhibit production and turnover dynamics. I am therefore wondering about the applicability/scope of the presented approach and to what extent it can be used to study partitioning noise for endogenous components. As presented, the approach seems to be limited to a fairly small class of experiments/situations.

(2) Similar to the previous comment, I am wondering what would happen in situations where the generations could not be as clearly identified as in the presented experimental system (e.g., due to variability in cell-cycle length/stage). In this case, it seems to be challenging to identify generations using a Gaussian Mixture Model. Can the authors comment on how to deal with such situations? In the abstract, the authors motivate their work by arguing that detecting cell divisions from microscopy is difficult, but doesn't their flow cytometry-based approach have a similar problem?

(3) I could not find any formal definition of division asymmetry. Since this is the most important quantity of this paper, it should be defined clearly.

(4) The description of the model is unclear/imprecise in several parts. For instance, it seems to me that the index "i" does not really refer to a cell in the population, but rather a subpopulation of cells that has undergone a certain number of divisions. Furthermore, why is the argument of Equation 11 suddenly the fraction f as opposed to the component number? I strongly recommend carefully rewriting and streamlining the model description and clearly defining all quantities and how they relate to each other.

(5) Similarly, I was not able to follow the logic of Section D. I recommend carefully rewriting this section to make the rationale, logic, and conclusions clear to the reader.

(6) Much theoretical work has been done recently to couple cell-cycle variability to intracellular dynamics. While the authors neglect the latter for simplicity, it would be important to further discuss these approaches and why their simplified model is suitable for their particular experiments.

(7) In the discussion the authors note that the microscopy-based estimates may lead to an overestimation of the fluctuations due to limited statistics. I could not follow that reasoning. Due to the gating in the flow cytometry measurements, I could imagine that the resulting populations are more stringently selected as compared to microscopy. Could that also be an explanation? More generally, it would be interesting to see how robust the results are in terms of different gating diameters.

(8) It would be helpful to show flow cytometry plots including the identified subpopulations for all cell lines, currently, they are shown only for HCT116 cells. More generally, very little raw data is shown.

(9) The title of the manuscript could be tailored more to the considered problem. At the moment it is very generic.

eLife Assessment

This study presents valuable findings suggesting that the late maturation of prefrontal cortex-based control processes enhances conceptual learning by allowing a period of less-constrained knowledge acquisition. The authors provide convincing computational evidence that delayed semantic control promotes learning without compromising representation integrity, with the strongest benefits emerging when control connections target intermediate layers of the model. However, the model's narrow scope raises concerns about scalability to more complex, real-world learning environments, and the meta-analysis, while supporting the developmental trajectory, does not directly test the model's specific predictions regarding task outcomes or error patterns.

Reviewer #1 (Public review):

Summary:

This study was motivated by the general claim that delayed development of cognitive control can be beneficial for learning, and investigated this claim in the specific domain of conceptual development. A comprehensive set of computational model simulations showed that delaying the onset of semantic control produces faster learning with only minimal effects on conceptual abstraction. The simulations also showed that control was most effective at intermediate levels between modality-specific "spokes" and the multimodal "hub". A meta-analysis of developmental data was consistent with the claim of delayed onset of semantic control: young children show substantially better semantic knowledge than the ability to constrain that knowledge to a specific task at hand.

Strengths:

The computational modelling is based on a very well-established model of semantic cognition, which means that the simulations allow exploring the specific issues under investigation here in the context of a model that accounts for a very large set of semantic cognition phenomena. The simulations are comprehensive - manipulating different parameters of the model provides important insights into how (and why) it works.

In addition to simulations exploring delayed maturation, there is an exploration of where semantic control is most effective, yielding the interesting result that control is most effective when it targets intermediate levels of semantic processing. To my knowledge, this is a novel finding and a concrete prediction for future testing.

The meta-analysis is designed in a very clever way that allows extracting evidence of semantic control from a large body of prior work. The results are quite clear and compelling in showing that semantic knowledge is acquired before children are able to use task demands to constrain the use of that knowledge.

Weaknesses:

Computational models of cognition inherently require simplification in order to focus on the mechanisms under investigation. However, it is also important to keep these simplifications in mind because they limit the generality of the inferences that can be made from the simulation results. Two aspects are important in this context:

(1) The multimodal structure was orthogonal to the surface similarity structure of the concepts to be learned. It is certainly true that multimodal structure does not perfectly mirror surface similarity, but closely related things tend to be perceptually similar. There are exceptions (whales, penguins, etc.), but they are *exceptional*, not typical. It may be that the somewhat extreme dissociation of multimodal and surface similarity structures creates demands that are not faced in natural conceptual development.

(2) Much of the benefit of delayed semantic control seems to be because the model is not penalised for activating task-irrelevant features. This blurs the distinction between being aware of a feature and making a response based on that feature. A full model that also includes a response layer could become a lot more complicated and more difficult to understand, so maybe there is an advantage to using a simpler architecture.

In addition, there is a bit of a misalignment between the model simulations and the meta-analysis. In the model, there are distinct modality-specific "spokes" and control is required in order to focus on modality/spoke in a task-appropriate way. The meta-analysis does not compare a task-defined selection of a modality; it compares the selection of taxonomic vs thematic relations, both of which are multimodal. One way to resolve this is to say that taxonomic and thematic relations are also represented in distinct sub-systems of semantic knowledge and semantic control is needed to select between them in a task-appropriate way.

This is particularly relevant to the inference at the bottom of p. 38: "taxonomic and thematic relationships ...[are]... both being encoded within the same system of representation", which seems in direct contradiction to the present results, or at least to the logic of combining these simulations with this meta-analysis. The simulations are based on semantic control being used to select/constrain the correct distinct sub-system (modality-specific spoke); the meta-analysis is based on semantic control being used to select/constrain the correct relationship type. If these two things are analogous in some way, then the relationship type has to be something like a distinct sub-system.

Reviewer #2 (Public review):

Summary:

This paper investigates the idea that the protracted maturation of the prefrontal cortex - often viewed as a developmental limitation - may actually confer advantages for conceptual learning in children. The authors focus on semantic control processes, which govern the context-sensitive application of conceptual knowledge, and are closely associated with late-developing regions of the prefrontal cortex.

Drawing on a computational model, the paper formally tests whether delayed maturation of semantic control promotes the acquisition of conceptual knowledge. The simulations demonstrate that when semantic control and anatomical connectivity mature later, conceptual learning is accelerated without compromising the integrity of the learned representations. Notably, the benefit is most apparent when control connections target intermediate layers in the computational model, suggesting a nuanced interplay between control processes and the underlying conceptual network.

To validate these computational insights in a human developmental context, the authors conduct a meta-analysis of the classic triadic matching task - a paradigm where participants decide which of two choices best matches a reference concept based on either taxonomic or thematic relations. Critically, when these relations conflict, semantic control is required to select the context-appropriate match. Results indicate that context-sensitive semantic control develops more slowly than basic conceptual knowledge, showing marked improvements between 3 and 6 years of age.

Overall, the paper argues that the delayed development of prefrontal cortex-based control processes allows for a period of less constrained learning, ultimately enhancing conceptual acquisition. The findings challenge the traditional view of late PFC maturation as solely disadvantageous and instead position it as an adaptive feature for building robust conceptual frameworks in early childhood.

Strengths:

(1) Novel Theoretical Contribution<br /> The paper offers a compelling, counterintuitive argument that a developmental lag in the maturation of control processes might be beneficial for semantic learning. This stands in contrast to the conventional framing of late prefrontal cortex (PFC) development as purely disadvantageous (e.g., a "necessary but unfortunate" constraint).

(2) Well-Grounded Computational Approach<br /> The authors propose a neural network model that is both theoretically driven (hub-and-spoke framework) and systematically tested under various conditions (different timelines for control onset, and different connectivity patterns). Their simulations replicate and extend previous findings about how insulating the multimodal hub from direct control inputs helps preserve abstract conceptual representations.

(3) Neuro-anatomical basis<br /> The paper connects its computational claims to empirical neuroanatomy, particularly the lack of direct structural connectivity between ventral ATL (the "hub") and the PFC in humans. This lends biological plausibility to the argument that control signals likely reach the ATL via intermediate regions (e.g., posterior temporal cortex).

(4) Meta-Analysis of Triadic Match-to-Sample<br /> The authors leverage decades of developmental data on conceptual matching tasks, reframing them in terms of semantic control vs. semantic representation. Their analysis nicely illustrates that children can identify semantic relationships (taxonomic or thematic) at age 2 if the task does not require them to select between conflicting semantic relations. In contrast, the ability to choose a task-relevant relation only emerges more robustly in 3-6 years. This developmental pattern aligns with the computational model's predictions.

Weaknesses:

The contribution of the paper might be considered rather specialist, and might not appeal to a broad public, which should be typical of a generalist journal. Moreover, the scope of the model is fairly narrow - its relatively small, controlled training environment raises questions about scalability to more naturalistic, high-dimensional data. Finally, the meta-analysis does not test directly the model predictions in terms of specific outcomes of the task, error patterns, or model fit, but only the developmental pattern which was an already observed phenomenon that in part motivated the hypothesis and the model itself.

Author response:

On the control of taxonomic versus thematic information. Both reviewers had questions about the relationship between the focus of the meta-analysis, the control of responses based on taxonomic versus thematic relationships, and the simulation. Both the model and the meta-analysis focus on the same mechanism, the controlled selection of task-appropriate features. In the case of the meta-analysis, this was the features and associations needed to identify the taxonomic or thematic relationships. As reviewer 1 notes, one possibility is that these kinds of structures are represented in distinct cortical regions. For instance, Mirman, Schwartz and colleagues have suggested that temporoparietal regions may preferentially support thematic knowledge while temporal regions may preferentially support taxonomic knowledge. Alternatively, they may be supported by different features instantiated within the same regions.  However, whether taxonomic and thematic relationships require access to features in different regions or not, is not crucial to the conclusions of this paper. The simulations used here happen to select features based on their inclusion in a particular sensory modality, yet they could learn to select any combination of features. Indeed, prior simulations using the Jackson et al., (2021) model show that the functional impact on learning of “deep” conceptual representations (together with controlled behaviours) is the same regardless of whether the potentiated features are localised within one spoke or distributed across spokes. Thus, the key results regarding the acquisition of semantic knowledge before the maturation of control in the current work should hold regardless of whether knowledge of taxonomic and thematic relations is localised to different anatomical regions.

On model size and scalability. Both reviewers noted the relatively small size of the model and wondered about implications for ecological validity of the simulations and scalability to larger, noisier, and potentially more systematically structured training environments. We agree this is an important direction for future research, but one that faces two nontrivial challenges. First, reviewer 1 notes that, whereas our model environment employs orthogonal structures across spokes and for the cross-modal features, perceptual structure may be better-aligned with conceptual structure for real-world experience. While we appreciate the intuition, its validity depends to a key extent on how visual information about objects is encoded. Conceptual structure is certainly not apparent, for instance, in the distance between bitmap images of objects, nor the overlap of simple feature-extraction algorithms (such as edge detection or Fourier decomposition, etc). Even in this age of deep vision models, it remains unclear how the visual system extracts and discerns perceptual similarity from retinal input (see e.g. Mukherjee & Rogers, 2025). Most successful contemporary models train neural networks to assign visual images to semantic categories, suggesting that the visual features the model learns, and thus the perceptual similarities it represents, depend on learning to generate semantic information. Therefore, it is not clear whether the similarity that people perceive amongst instances of the same class is natively apparent in the bottom-up visual input, or whether it depends on semantic/cross-modal learning and representation. It should also be noted that within our training environment, there are features in each modality that are predictive of features in other modalities, as well as some that are only predictive of features within this modality. Thus, the full cross-modality conceptual structure is not orthogonal to the information available in each sensory domain, instead there is a relationship between surface and multimodal similarity in the dataset as in the real-world environment. In general, one virtue of the small-scale modelling endeavour in the current work is that we can be very explicit about the nature of the structure apparent within and across spokes.

The second non-trivial issue concerns the nature of the mechanisms that allow for context-sensitive responding in large-scale language/vision models such as GPT 4. Such models are trained on web-scale language and vision and provide a means of simulating controlled behaviour with realistic stimuli, so might seem to provide a means of assessing scalability of current neuro-cognitive models. Large language/vision models rely, however, on transformer architectures whose relationship to hypothesized mechanisms of control in the mind and brain is unclear. In transformers, context-sensitive responding depends upon “attention” mechanisms that are fully distributed and integrated throughout the entire system—there is no distinction between control, representation, and short-term memory in the architecture. As a consequence, it is very difficult to understand why a model behaves the way it does, or to relate patterns of behaviour to hypothesised mechanisms in the human mind/brain. Yet transformers are currently the only models capable of exhibiting context-sensitive patterns of responding based on both language and vision. Scaling up neuro-cognitive models will require developing alternative architectures that preserve the critical hypothesised distinctions between representation and control while retaining the ability of transformers to learn from large-scale ecologically realistic corpora of language and images. In the meantime, small-scale simulations like those reported here provide some critical insights into aspects of architecture and maturation that may aid in this endeavour.

On including a response layer. Reviewer 1 notes that our model does not separately simulate response-generation and the selective activation of relevant feature representations. We agree that there are interesting questions about how feature-potentiation and response-generation relate to one another, and that incorporating response selection in the current model would significantly complicate the analysis. The general idea that control potentiates/suppresses task-relevant feature representations in addition to simply promoting the correct response derives from classic work by Martin and others (e.g., Martin et al., 1995) showing that, for instance, regions involved in colour perception activate more strongly in tasks requiring retrieval of colour than tasks involving retrieval of action and vice versa—results consistent with the model training/testing procedure in the current work. In general, it may be counterproductive to become aware of aspects of a concept that would be irrelevant, or even actively unhelpful in making a response, suggesting guided activation is a necessary precursor to response selection (Botvinick & Cohen, 2014). Here, we focus on this important feature potentiation step.

On the novelty of the meta-analysis. Reviewer 2 suggests the results of the meta-analysis were already known and provided motivation for the simulation. However, an important contribution of the current work is the observation that, in fact, there is little prior work on the development of semantic control. The widely known developmental delay in domain-general executive control, which did indeed motivate the study, is exclusively based on tasks requiring very different forms of executive control. Many of these involve no meaningful stimuli or require the child to completely inhibit a practiced response and generate an opposite or completely arbitrary responses, instead of requiring the child to use context to select among two or more meaningful behaviours that are equally valid in different contexts (see the introduction to Part 2). This observation, coupled with recent evidence that semantic control relies on dedicated and partially non-overlapping neural systems to executive function, illustrates the utility of the current meta-analysis: delineating the developmental trajectory of semantic control requires a task in which control is applied to the context-appropriate retrieval and manipulation of semantic knowledge, such as the triadic matching task. Moreover, the results show that semantic control, while arising later than semantic representation, nevertheless begins to mature earlier (around 2.5 years) than typical estimations of domain-general executive control (around 4). Thus, the meta-analysis contributes to our understanding of cognitive development while also testing a key prediction of the model.

eLife Assessment

The study presents valuable findings regarding the incidence and clinical impact of a mutation in a cardiac muscle protein and its association with the development of atrial fibrillation. The authors provide some convincing evidence of electrophysiological disturbances in cells with this mutation which would be of interest to cellular electrophysiologists. However, evidence supporting the conclusion that this mutation causes atrial fibrillation would benefit from more rigorous electrophysiologic approaches.

Reviewer #1 (Public review):

Summary:

Pavel et al. analyzed a cohort of atrial fibrillation (AF) patients from the University of Illinois at Chicago, identifying TTN truncating variants (TTNtvs) and TTN missense variants (TTNmvs). They reported a rare TTN missense variant (T32756I) associated with adverse clinical outcomes in AF patients. To investigate its functional significance, the authors modeled the TTN-T32756I variant using human induced pluripotent stem cell-derived atrial cardiomyocytes (iPSC-aCMs). They demonstrated that mutant cells exhibit aberrant contractility, increased activity of the cardiac potassium channel KCNQ1 (Kv7.1), and dysregulated calcium homeostasis. Interestingly, these effects occurred without compromising sarcomeric integrity. The study further identified increased binding of the titin-binding protein Four-and-a-Half Lim domains 2 (FHL2) with KCNQ1 and its modulatory subunit KCNE1 in the TTN-T32756I iPSC-aCMs.

Strengths:

This work has translational potential, suggesting that targeting KCNQ1 or FHL2 could represent a novel therapeutic strategy for improving cardiac function. The findings may also have broader implications for treating patients with rare, disease-causing variants in sarcomeric proteins and underscore the importance of integrating genomic analysis with experimental evidence to advance AF research and precision medicine.

Weaknesses:

(1) Variant Identification: It is unclear how the TTN missense variant (T32756I) was identified using REVEL, as none of the patients' parents reportedly carried the mutation or exhibited AF symptoms. Are there other TTN variants identified in the three patients carrying TTN-T32756I? Clarification on this point is necessary.

(2) Patient-Specific iPSC Lines: Since the TTN-T32756I variant was modeled using only one healthy iPSC line, it is unclear whether patient-specific iPSC-derived atrial cardiomyocytes would exhibit similar AF-related phenotypes. This limitation should be addressed.

(3) Hypertension as a Confounding Factor: The three patients carrying TTN-T32756I also have hypertension. Could the hypertension associated with this variant contribute secondarily to AF? The authors should discuss or rule out this possibility.

(4) FHL2 and KCNQ1-KCNE1 Interaction: Immunostaining data demonstrating the colocalization of FHL2 with the KCNQ1-KCNE1 (MinK) complex in TTN-T32756I iPSC-aCMs are needed to strengthen the mechanistic findings.

(5) Functional Characterization of FHL2-KCNQ1-KCNE1 Interaction: Additional functional assays are necessary to characterize the interaction between FHL2 and the KCNQ1-KCNE1 complex in TTN-T32756I iPSC-aCMs to further validate the proposed mechanism.

Reviewer #2 (Public review):

Summary:

The authors present data from a single-center cohort of African-American and Hispanic/Latinx individuals with atrial fibrillation (AF). This study provides insight into the incidences and clinical impact of missense variants in the Titin (TTN) gene in this population. In addition, the authors identified a single amino acid TTN missense variant (TTN-T32756I) that was further studied using human induced pluripotent stem cell-derived atrial cardiomyocytes (iPSC-aCMs). These studies demonstrated that the Four-and-a-Half Lim domains 2 (FHL2), has increased binding with KCNQ1 and its modulatory subunit KCNE1 in the TTN-T32756I-iPSC-aCMs, enhancing the slow delayed rectifier potassium current (Iks) and is a potential mechanism for atrial fibrillation. Finally, the authors demonstrate that suppression of FHL2 could normalize the Iks current.

Strengths:

The strengths of this manuscript/study are listed below:

(1) This study includes a previously underrepresented population in the study of the genetic and mechanistic basis of AF.<br /> (2) The authors utilize current state-of-the-art methods to investigate the pathogenicity of a specific TTN missense variant identified in this underrepresented patient population.<br /> (3) The findings of this study identify a potential therapeutic for treating atrial fibrillation.

Weaknesses:

(1) The authors do not include a non-AF group when evaluating the incidence and clinical significance of TTN missense variants in AF patients.

(2) The authors do not provide evidence that TTN-T32756I-iPSC-aCMs are arrhythmogenic only that there is an increase in the Iks current and associated action potential changes. More specifically, the authors report "compared to the WT, TTN-T32756I-iPSC-aCMs exhibited increased arrhythmic frequency" yet is it is unclear what they are referring to by "arrhythmic frequency".

(3) There seem to be discrepancies regarding the impact of the TTN-T32756I variant on mechanical function. Specifically, the authors report "both reduced contraction and abnormal relaxation in TTN-T32756I-iPSC-aCMs" yet, separately report "the contraction amplitude of the mutant was also increased . . . suggesting an increased contractile force by the TTN-T32756I-iPSC-aCMs and TTN-T32756I-iPSC-CMs exhibited similar calcium transient amplitudes as the WT."

Reviewer #3 (Public review):

Summary:

The authors describe the abnormal contractile function and cellular electrophysiology in an iPSC model of atrial myocytes with a titin missense variant. They provide contractility data by sarcomere length imaging, calcium imaging, and voltage clamp of the repolarizing current iKs. While each of the findings is separately interesting, the paper comes across as too descriptive because there is no merging of the data to support a cohesive mechanistic story/statement, especially from the electrophysiological standpoint. There is definitely not enough support for the title "A Titin Missense Variant Causes Atrial Fibrillation", since there is no strong causative evidence at all. There is some interesting clinical data regarding the variant of interest and its association with HF hospitalization, which may lead to future important discoveries regarding atrial fibrillation.

Strengths:

The manuscript is well written and there is a wide range of experimental techniques to probe this atrial fibrillation model.

Weaknesses:

(1) While the clinical data is interesting, it is extremely important to rule out heart failure with preserved EF as a confounder. HFpEF leads to AF due to increased atrial remodeling, so the fact that patients with this missense variant have increased HF hospitalizations does not necessarily directly support the variant as causative of AF. It could be that the variant is actually associated directly with HFpEF instead, and this needs to be addressed and corrected in the analyses.

(2) All of the contractility and electrophysiologic data should be done with pacing at the same rate in both control and missense variant groups, to control for the effect of cycle length on APD and calcium loading. A claim of shorter APD cannot be claimed when the firing rate of one set of cells is much faster than the other, since shorter APD is to be expected with a faster rate. Similarly, contractility is affected by diastolic interval because of the influence of SR calcium content on the myocyte power stroke. So the cells need to be paced at the same rate in the IonOptix for any direct comparison of contractility. The authors should familiarize themselves with the concept of electrical restitution.

(3) It is interesting that the firing rate of the myocytes is faster with the missense variant. This should lead to a hypothesis and investigation of abnormal automaticity or triggered activity, which may also explain the increased contractility since all these mechanisms are related to the calcium clock and calcium loading of the SR. See #2 above for suggestions on how to adequately probe calcium handling. Such an investigation into impulse initiation mechanisms would be very powerful in supporting the primary statement of the paper since these are actual mechanisms thought to cause AF.

(4) The claim of shortened APD without correcting for cycle length is problematic. However, the general concept of linking shortened APD in isolated cells alone to AF causation is more problematic. To have a setup for reentry, there must be a gradient of APD from short to long, and this can only be demonstrated at the tissue level, not really at the cellular level, so reentry should not be invoked here. If shortened APD is demonstrated with correction of the cycle length problem, restitution curves can be made showing APD shortening at different cycle lengths. If restitution is abnormal (i.e. the APD does not shorten normally in relation to the diastolic interval), this may lead to triggered activity which is an arrhythmogenic mechanism. This would also tie in well with the finding of abnormally elevated iKs current since iKs is a repolarizing current directly responsible for restitution.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

Pavel et al. analyzed a cohort of atrial fibrillation (AF) patients from the University of

Illinois at Chicago, identifying TTN truncating variants (TTNtvs) and TTN missense variants (TTNmvs). They reported a rare TTN missense variant (T32756I) associated with adverse clinical outcomes in AF patients. To investigate its functional significance, the authors modeled the TTN-T32756I variant using human induced pluripotent stem cell-derived atrial cardiomyocytes (iPSC-aCMs). They demonstrated that mutant cells exhibit aberrant contractility, increased activity of the cardiac potassium channel KCNQ1 (Kv7.1), and dysregulated calcium homeostasis. Interestingly, these effects occurred without compromising sarcomeric integrity. The study further identified increased binding of the titin-binding protein Four-and-a-Half Lim domains 2 (FHL2) with KCNQ1 and its modulatory subunit KCNE1 in the TTN-T32756I iPSCaCMs.

Strengths:

This work has translational potential, suggesting that targeting KCNQ1 or FHL2 could represent a novel therapeutic strategy for improving cardiac function. The findings may also have broader implications for treating patients with rare, disease-causing variants in sarcomeric proteins and underscore the importance of integrating genomic analysis with experimental evidence to advance AF research and precision medicine.

Weaknesses

(1) Variant Identification: It is unclear how the TTN missense variant (T32756I) was identified using REVEL, as none of the patients' parents reportedly carried the mutation or exhibited AF symptoms. Are there other TTN variants identified in the three patients carrying TTN-T32756I? Clarification on this point is necessary.  

We thank the reviewer for their insightful comment. Our study identified deleterious missense variants using a stringent REVEL score threshold of ≥0.7; however, variants with a REVEL score above 0.5 are generally considered potentially pathogenic (Ioannidis, Nilah M., et al., Am J Human Genetics 2016; 9.4: 877-885). The TTN-T32756I variant (REVEL Score: 0.58758, Supplementary Table 1) was prioritized due to its occurrence in multiple unrelated individuals within our clinical AF cohort, despite no reported family history of AF in affected individuals. While no parental inheritance was observed, the possibility of a de novo origin cannot be excluded. Furthermore, this variant is located within a region overlapping a deletion mutation recently shown to cause AF in a zebrafish model (Jiang et al., iScience, 2024;27(7):110395) supporting its potential pathogenicity. Notably, the affected individuals did not carry additional loss-of-function TTN variants. We will clarify these points in the revised manuscript.

(2) Patient-Specific iPSC Lines: Since the TTN-T32756I variant was modeled using only one healthy iPSC line, it is unclear whether patient-specific iPSC-derived atrial cardiomyocytes would exhibit similar AF-related phenotypes. This limitation should be addressed.

We acknowledge the reviewer’s concern that patient-specific iPSC lines could further validate our findings. However, due to the patients' unavailability of peripheral blood mononuclear cells (PBMCs), we utilized a healthy iPSC line and introduced the TTN-T32756I variant using CRISPR/Cas9 genome editing. This approach ensures an isogenic background, thereby minimizing genetic variability and providing a controlled system to study the direct effects of the mutation. We will acknowledge this limitation in the revised manuscript.

(3) Hypertension as a Confounding Factor: The three patients carrying TTN-T32756I also have hypertension. Could the hypertension associated with this variant contribute secondarily to AF? The authors should discuss or rule out this possibility.

We agree that hypertension is a common comorbidity in patients with AF and could contribute to disease progression. However, all three individuals carrying TTN-T32756I exhibited early-onset AF (onset before 66 years), with one case occurring as early as 36 years. This suggests a potential two-hit mechanism, where genetic predisposition and comorbidities influence disease risk. Importantly, our iPSC model isolates the genetic effects of TTN-T32756I from other factors, supporting a direct pathogenic role. We will explicitly discuss this in the revised manuscript.

(4) FHL2 and KCNQ1-KCNE1 Interaction: Immunostaining data demonstrating the colocalization of FHL2 with the KCNQ1-KCNE1 (MinK) complex in TTN-T32756I iPSC-aCMs are needed to strengthen the mechanistic findings.

We appreciate the reviewer’s suggestion and agree that additional immunostaining data would strengthen the evidence for FHL2 colocalization with the KCNQ1-KCNE1 complex in TTN-T32756I iPSC-aCMs. We will work on obtaining these additional data to validate our mechanistic findings further.

(5) Functional Characterization of FHL2-KCNQ1-KCNE1 Interaction: To further validate the proposed mechanism, additional functional assays are necessary to characterize the interaction between FHL2 and the KCNQ1-KCNE1 complex in TTN-T32756I iPSC-aCMs.

We agree with the reviewer that additional functional assays would further validate the proposed mechanism. We will perform contractility and electrophysiological experiments, such as multielectrode array (MEA) assays, to characterize better the interaction between FHL2 and the KCNQ1-KCNE1 complex in TTN-T32756I iPSC-aCMs.

Reviewer #2 (Public review):

Summary:

The authors present data from a single-center cohort of African-American and Hispanic/Latinx individuals with atrial fibrillation (AF). This study provides insight into the incidences and clinical impact of missense variants in this population in the Titin (TTN) gene. In addition, the authors identified a single amino acid TTN missense variant (TTN-T32756I) that was further studied using human induced pluripotent stem cell-derived atrial cardiomyocytes (iPSC-aCMs). These studies demonstrated that the Four-and-a-Half Lim domains 2 (FHL2) has increased binding with KCNQ1 and its modulatory subunit KCNE1 in the TTN-T32756I-iPSCaCMs, enhancing the slow delayed rectifier potassium current (Iks) and is a potential mechanism for atrial fibrillation. Finally, the authors demonstrate that suppression of FHL2 could normalize the Iks current.

Strengths:

The strengths of this manuscript/study are listed below:

(1) This study includes a previously underrepresented population in the study of the genetic and mechanistic basis of AF.

(2) The authors utilize current state-of-the-art methods to investigate the pathogenicity of a specific TTN missense variant identified in this underrepresented patient population.

(3) The findings of this study identify a potential therapeutic for treating atrial fibrillation.

Weaknesses:

(1) The authors do not include a non-AF group when evaluating the incidence and clinical significance of TTN missense variants in AF patients.

We acknowledge the limitation of not including a non-AF group in our clinical analysis. Our cohort is derived from a single-center registry of individuals with AF, and we do not have a matched cohort of non-AF controls to compare the incidence of TTN missense variants. We recognize this as a limitation and will clarify that further studies are needed to define the prevalence of TTN missense variants in broader, multiethnic cohorts that include both AF and non-AF individuals.

(2) The authors do not provide evidence that TTN-T32756I-iPSC-aCMs are arrhythmogenic, only that there is an increase in the Iks current and associated action potential changes. More specifically, the authors report that "compared to the WT, TTN-T32756I-iPSC-aCMs exhibited increased arrhythmic frequency," yet it is unclear what they are referring to by "arrhythmic frequency."

We appreciate the reviewer’s request for clarification regarding "arrhythmic frequency." In our study, this term refers to the increased spontaneous beating rate and irregular action potentials observed in TTN-T32756I iPSC-aCMs compared to WT. Our findings suggest that the AF-associated TTN-T32756I variant induces ion channel remodeling and beating abnormalities, possibly contributing to an arrhythmogenic substrate for AF. We will refine our wording in the revised manuscript to enhance clarity and precision.

(3) There seem to be discrepancies regarding the impact of the TTN-T32756I variant on mechanical function. Specifically, the authors report "both reduced contraction and abnormal relaxation in TTN-T32756I-iPSC-aCMs" yet, separately report "the contraction amplitude of the mutant was also increased … suggesting an increased contractile force by the TTN-T32756IiPSC-aCMs and TTN-T32756I-iPSC-CMs exhibited similar calcium transient amplitudes as the WT."

We thank the reviewer for pointing this out and apologize for the inconsistency. We intended to report on contraction duration and relaxation rather than contraction force alone. The increased contraction amplitude reflects altered contractile force, whereas the reduced contraction duration and impaired relaxation indicate dysfunctional contractile dynamics. We will revise the text and corresponding figures to convey these findings accurately.

Reviewer #3 (Public review):

Summary:

The authors describe the abnormal contractile function and cellular electrophysiology in an iPSC model of atrial myocytes with a titin missense variant. They provide contractility data by sarcomere length imaging, calcium imaging, and voltage clamp of the repolarizing current iKs. While each of the findings is interesting, the paper comes across as too descriptive because there is no data merging to support a cohesive mechanistic story/statement, especially from the electrophysiological standpoint. There is not enough support for the title "A Titin Missense Variant Causes Atrial Fibrillation", since there is no strong causative evidence. There is some interesting clinical data regarding the variant of interest and its association with HF hospitalization, which may lead to future important discoveries regarding atrial fibrillation.

Strengths:

The manuscript is well written, and a wide range of experimental techniques are used to probe this atrial fibrillation model.

Weaknesses

(1) While the clinical data is interesting, it is essential to rule out heart failure with preserved EF as a confounder. HFpEF leads to AF due to increased atrial remodeling, so the fact that patients with this missense variant have increased HF hospitalizations does not necessarily directly support the variant as causative of AF. It could be that the variant is associated directly with HFpEF instead, and this needs to be addressed and corrected in the analyses.

We recognize that AF and HFpEF frequently coexist and that HFpEF-related atrial remodeling could contribute to AF development. The primary aim of our cohort analysis was to explore the potential clinical significance of TTNmv. While we acknowledge the inherent limitations of retrospective observational data in establishing causality, our subsequent in vitro experiments were designed to demonstrate that TTNmv can alter the electrophysiological substrate, potentially predisposing individuals to AF.

As HFpEF is a potential confounder, it is reasonable to consider whether TTNmv may also be associated with HFpEF. However, to our knowledge, no existing literature directly links TTNmv to HFpEF. In contrast, loss-of-function TTN variants are typically associated with heart failure with reduced ejection fraction (HFrEF) and dilated cardiomyopathy, and even their role in HFrEF remains controversial. To address potential confounding, our multivariable analysis for clinical outcomes was adjusted for reduced ejection fraction, and we conducted a sensitivity analysis excluding patients with nonischemic dilated cardiomyopathy (Supplementary Table 6). We will clarify these points in the revised manuscript.

(2) All contractility and electrophysiologic data should be done with pacing at the same rate in both control and missense variant groups, to control for the effect of cycle length on APD and calcium loading. A shorter APD cannot be claimed when the firing rate of one set of cells is much faster than the other, since shorter APD is to be expected with a quicker rate. Similarly, contractility is affected by diastolic interval because of the influence of SR calcium content on the myocyte power stroke. So the cells need to be paced at the same rate in the IonOptix for any direct comparison of contractility. The authors should familiarize themselves with the concept of electrical restitution.

We appreciate the reviewer’s technical concern. iPSC-derived cardiomyocytes (iPSC-CMs) exhibit spontaneous beating due to the presence of pacemaker-like currents and the absence of I_k1, which allows for the study of intrinsic electrophysiological properties, ion channel function, and disease modeling. In our study, we utilized this unique property of iPSCCMs to test our hypothesis that TTNmvs alter electrophysiological properties through ion channel remodeling.

While iPSC-CMs with identical backgrounds are expected to show comparable electrophysiological phenotypes under the same conditions, variability due to biological and technical factors (e.g., protein expression and culture handling) can result in differences between samples. We agree with the reviewer that pacing iPSC-CMs at the same rate for action potential duration (APD) and contractility measurements will control for cycle length effects and improve the reliability and interpretability of our findings. We will incorporate this approach into our revised experimental design.

(3) It is interesting that the firing rate of the myocytes is faster with the missense variant. This should lead to a hypothesis and investigation of abnormal automaticity or triggered activity, which may also explain the increased contractility since all these mechanisms are related to the SR's calcium clock and calcium loading. See #2 above for suggestions on how to probe calcium handling adequately. Such an investigation into impulse initiation mechanisms would be compelling in supporting the primary statement of the paper since these are actual mechanisms thought to cause AF.

We agree with the reviewer that investigating abnormal automaticity or triggered activity about the increased firing rate observed with the missense variant could provide valuable insights into the mechanisms underlying AF. As these processes are closely linked to calcium handling and the calcium clock, probing calcium cycling abnormalities could strengthen our understanding of how TTNmvs contribute to AF. We will incorporate additional experiments to investigate these mechanisms, further supporting our study's central hypothesis.

(4) The claim of shortened APD without correcting for cycle length is problematic. However, linking shortened APD in isolated cells alone to AF causation is more complicated. To have a setup for reentry, there must be a gradient of APD from short to long, and this can only be demonstrated at the tissue level, not at the cellular level, so reentry should not be invoked here. If shortened APD is demonstrated with correction of the cycle length problem, restitution curves can be made showing APD shortening at different cycle lengths. If restitution is abnormal (i.e. the APD does not shorten normally in relation to the diastolic interval), this may lead to triggered activity which is an arrhythmogenic mechanism. This would also tie in well with the finding of abnormally elevated iKs current since iKs is a repolarizing current directly responsible for restitution.

We appreciate the reviewer’s insightful comment. We recognize that isolated cell studies cannot directly demonstrate reentrant circuits, and we agree that reentry should not be invoked solely based on cellular data. Our claim of shortened APD is based on observed abnormalities in APD and beating patterns, which may contribute to conditions conducive to reentry at the tissue level. We will clarify this distinction in the revised manuscript and refrain from directly linking APD shortening to reentry without tissue-level evidence.

eLife Assessment

Studying the biological roles of polyphosphates in metazoans has been a longstanding challenge to the field given that the polyP synthase has yet to be discovered in metazoans. This important study capitalizes on the sophisticated genetics available in the Drosophila system and uses a combination of methodologies to start to tease apart how polyphosphate participates in Drosophila development and in the clotting of Drosophila hemolymph. The data validating the tools are solid and well-documented and they will open up a field of research into the functional roles of polyP in a metazoan model.

Reviewer #1 (Public review):

Polymers of orthophosphate of varying lengths are abundant in prokaryotes and some eukaryotes where they regulate many cellular functions. Though they exist in metazoans, few tools exist to study their function. This study documents the development of tools to extract, measure, and deplete inorganic polyphosphates in *Drosophila*. Using these tools, the authors show:

(1) that polyP levels are negligible in embryos and larvae of all stages while they are feeding. They remain high in pupae but their levels drop in adults.

(2) that many cells in tissues such as the salivary glands, oocytes, haemocytes, imaginal discs, optic lobe, muscle, and crop, have polyP that is either cytoplasmic or nuclear (within the nucleolus).

(3) that polyP is necessary in plasmatocytes for blood clotting in Drosophila.

(4) that ployP controls the timing of eclosion.

The tools developed in the study are innovative, well-designed, tested, and well-documented. I enjoyed reading about them and I appreciate that the authors have gone looking for the functional role of polyP in flies, which hasn't been demonstrated before. The documentation of polyP in cells is convincing as its role in plasmatocytes in clotting. Its control of eclosion timing, however, could result from non-specific effects of expressing an exogenous protein in all cells of an animal. The RNAseq experiments and their associated analyses on polyP-depleted animals and controls have not been discussed in sufficient detail. In its current form, the data look to be extremely variable between replicates and I'm therefore unsure of how the differentially regulated genes were identified.

It is interesting that no kinases and phosphatases have been identified in flies. Is it possible that flies are utilising the polyP from their gut microbiota? It would be interesting to see if these signatures go away in axenic animals.

Reviewer #2 (Public review):

Summary:

The authors of this paper note that although polyphosphate (polyP) is found throughout biology, the biological roles of polyP have been under-explored, especially in multicellular organisms. The authors created transgenic Drosophila that expressed a yeast enzyme that degrades polyP, targeting the enzyme to different subcellular compartments (cytosol, mitochondria, ER, and nucleus, terming these altered flies Cyto-FLYX, Mito-FLYX, etc.). The authors show the localization of polyP in various wild-type fruit fly cell types and demonstrate that the targeting vectors did indeed result in the expression of the polyP degrading enzyme in the cells of the flies. They then go on to examine the effects of polyP depletion using just one of these targeting systems (the Cyto-FLYX). The primary findings from the depletion of cytosolic polyP levels in these flies are that it accelerates eclosion and also appears to participate in hemolymph clotting. Perhaps surprisingly, the flies seemed otherwise healthy and appeared to have little other noticeable defects. The authors use transcriptomics to try to identify pathways altered by the cyto-FLYX construct degrading cytosolic polyP, and it seems likely that their findings in this regard will provide avenues for future investigation. And finally, although the authors found that eclosion is accelerated in pupae of Drosophila expressing the Cyto-FLYX construct, the reason why this happens remains unexplained.

Strengths:

The authors capitalize on the work of other investigators who had previously shown that expression of recombinant yeast exopolyphosphatase could be targeted to specific subcellular compartments to locally deplete polyP, and they also use a recombinant polyP binding protein (PPBD) developed by others to localize polyP. They combine this with the considerable power of Drosophila genetics to explore the roles of polyP by depleting it in specific compartments and cell types to tease out novel biological roles for polyP in a whole organism. This is a substantial advance.

Weaknesses:

Page 4 of the Results (paragraph 1): I'm a bit concerned about the specificity of PPBD as a probe for polyP. The authors show that the fusion partner (GST) isn't responsible for the signal, but I don't think they directly demonstrate that PPBD is binding only to polyP. Could it also bind to other anionic substances? A useful control might be to digest the permeabilized cells and tissues with polyphosphatase prior to PPBD staining and show that the staining is lost.

In the hemolymph clotting experiments, the authors collected 2 ul of hemolymph and then added 1 ul of their test substance (water or a polyP solution). They state that they added either 0.8 or 1.6 nmol polyP in these experiments (the description in the Results differs from that of the Methods). I calculate this will give a polyP concentration of 0.3 or 0.6 mM. This is an extraordinarily high polyP concentration and is much in excess of the polyP concentrations used in most of the experiments testing the effects of polyP on clotting of mammalian plasma. Why did the authors choose this high polyP concentration? Did they try lower concentrations? It seems possible that too high a polyP concentration would actually have less clotting activity than the optimal polyP concentration.

Reviewer #3 (Public review):

Summary:

Sarkar, Bhandari, Jaiswal, and colleagues establish a suite of quantitative and genetic tools to use Drosophila melanogaster as a model metazoan organism to study polyphosphate (polyP) biology. By adapting biochemical approaches for use in D. melanogaster, they identify a window of increased polyP levels during development. Using genetic tools, they find that depleting polyP from the cytoplasm alters the timing of metamorphosis, accelerating eclosion. By adapting subcellular imaging approaches for D. melanogaster, they observe polyP in the nucleolus of several cell types. They further demonstrate that polyP localizes to cytoplasmic puncta in hemocytes, and further that depleting polyP from the cytoplasm of hemocytes impairs hemolymph clotting. Together, these findings establish D. melanogaster as a tractable system for advancing our understanding of polyP in metazoans.

Strengths:

(1) The FLYX system, combining cell type and compartment-specific expression of ScPpx1, provides a powerful tool for the polyP community.

(2) The finding that cytoplasmic polyP levels change during development and affect the timing of metamorphosis is an exciting first step in understanding the role of polyP in metazoan development, and possible polyP-related diseases.

(3) Given the significant existing body of work implicating polyP in the human blood clotting cascade, this study provides compelling evidence that polyP has an ancient role in clotting in metazoans.

Limitations:

(1) While the authors demonstrate that HA-ScPpx1 protein localizes to the target organelles in the various FLYX constructs, the capacity of these constructs to deplete polyP from the different cellular compartments is not shown. This is an important control to both demonstrate that the GTS-PPBD labeling protocol works, and also to establish the efficacy of compartment-specific depletion. While not necessary to do this for all the constructs, it would be helpful to do this for the cyto-FLYX and nuc-FLYX.

(2) The cell biological data in this study clearly indicates that polyP is enriched in the nucleolus in multiple cell types, consistent with recent findings from other labs, and also that polyP affects gene expression during development. Given that the authors also generate the Nuc-FLYX construct to deplete polyP from the nucleus, it is surprising that they test how depleting cytoplasmic but not nuclear polyP affects development. However, providing these tools is a service to the community, and testing the phenotypic consequences of all the FLYX constructs may arguably be beyond the scope of this first study.

Author response:

Our reviewers brought three things to our notice:

(1) PolyP has not been introduced as an abbreviation in the abstract.

(2) 'colorimetric' is misspelled as 'calorimetric' in the following sentence of the results section.

This method involved the digestion of polyP by recombinant S. cerevisiae exopolyphosphatase 1 (_Sc_Ppx1) followed by calorimetric measurement of the released Pi by malachite green.

(3) A reference for hNUDT3 has been deleted due to the same technical glitch from the following sentence of introduction.

Recently, biochemical experiments led to the discovery of endopolyphosphatase NUDT3, an enzyme known as a dinucleoside phosphatase.

eLife Assessment

This is an important study that examines the impact of Streptococcus pneumoniae genetics on its in vitro growth kinetics, aiming to identify potential targets for vaccines and therapeutics. The study identified significant variations in growth characteristics among capsular serotypes and lineages, linked to phylogeny and high heritability, but genome-wide association studies did not reveal specific genomic loci associated with growth features independent of the genetic background. The evidence supporting these findings is solid.

Reviewer #1 (Public review):

Summary:

This manuscript uses a diverse isolate collection of Streptococcus pneumoniae from hospital patients in the Netherlands to understand the population-level genetic basis of growth rate variation in this pathogen, which is a key determinant of S. pneumoniae within-host fitness. Previous efforts have studied this phenomenon in strain-specific comparisons, which can lack the statistical power and scope of population-level studies. The authors collected a rigorous set of in vitro growth data for each S. pneumoniae isolate and subsequently paired growth curve analysis with whole-genome analyses to identify how phylogenetics, serotype, and specific genetic loci influence in vitro growth. While there were noticeable correlations between capsular serotype and phylogeny with growth metrics, they did not identify specific loci associated with altered in vitro growth, suggesting that these phenotypes are controlled by the collective effect of the entire genetic background of a strain. This is an important finding that lays the foundation for additional, more highly-powered studies that capture more S. pneumoniae genetic diversity to identify these genetic contributions.

Strengths:

(1) The authors were able to completely control the experimental and genetic analyses to ensure all isolates underwent the same analysis pipeline to enhance the rigor of their findings.

(2) The isolate collection captures an appreciable amount of S. pneumoniae diversity and, importantly, enables disentangling the contributions of the capsule and phylogenetic background to growth rates.

(3) This study provides a population-level, rather than strain-specific, view of how genetic background influences the growth rate in S. pneumoniae. This is an advance over previous studies that have only looked at smaller sets of strains.

(4) The methods used are well-detailed and robust to allow replication and extension of these analyses. Moreover, the manuscript is very well written and includes a thoughtful and thorough discussion of the strengths and limitations of the current study.

Weaknesses:

(1) As acknowledged by the authors, the genetic diversity and sample size of this newly collected isolate set are still limited relative to the known global diversity of S. pneumoniae, which evidently limits the power to detect loci with smaller/combinatorial contributions to growth rate (and ultimately infection).

(2) The in vitro growth data is limited to a single type of rich growth medium, which may not fully reflect the nutritional and/or selective pressures present in the host.

(3) The current study does not use genetic manipulation or in vitro/in vivo infection models to experimentally test whether alteration of growth rates as observed in this study is linked to virulence or successful infection. The availability of a naturally diverse collection with phylogenetic and serotype combinations already identified as interesting by the authors provides a strong rationale for wet-lab studies of these phenotypes.

Reviewer #2 (Public review):

Summary:

The study by Chaguza et al. presents a novel perspective on pneumococcal growth kinetics, suggesting that the overall genetic background of Streptococcus pneumoniae, rather than specific loci, plays a more dominant role in determining growth dynamics. Through a genome-wide association study (GWAS) approach, the authors propose a shift in how we understand growth regulation, differing from earlier findings that pinpointed individual genes, such as wchA or cpsE, as key regulators of growth kinetics. This study highlights the importance of considering the cumulative impact of the entire genetic background rather than focusing solely on individual genetic loci.

The study emphasizes the cumulative effects of genetic variants, each contributing small individual impacts, as the key drivers of pneumococcal growth. This polygenic model moves away from the traditional focus on single-gene influences. Through rigorous statistical analyses, the authors persuasively advocate for a more holistic approach to understanding bacterial growth regulation, highlighting the complex interplay of genetic factors across the entire genome. Their findings open new avenues for investigating the intricate mechanisms underlying bacterial growth and adaptation, providing fresh insights into bacterial pathogenesis.

Strengths:

This study exemplifies a holistic approach to unraveling key factors in bacterial pathogenesis. By analyzing a large dataset of whole-genome sequences and employing robust statistical methodologies, the authors provide strong evidence to support their main findings. Which is a leap forward from previous studies focused on a relatively smaller number of strains. Their integration of genome-wide association studies (GWAS) highlights the cumulative, polygenic influences on pneumococcal growth kinetics, challenging the traditional focus on individual loci. This comprehensive strategy not only advances our understanding of bacterial growth regulation but also establishes a foundation for future research into the genetic underpinnings of bacterial pathogenesis and adaptation. The amount of data generated and corresponding approaches to analyze the data are impressive as well as convincing. The figures are convincing and comprehensible too.

Weaknesses:

Despite the strong outcomes of the GWAS approach, this study leaves room for differing interpretations. A key point of contention lies in the title, which initially gives the impression that the research addresses growth kinetics under both in vitro and in vivo conditions. However, the study is limited to in vitro growth kinetics, with the assumption that these findings are equally applicable to in vivo scenarios-a premise that is not universally valid. To more accurately reflect the study's scope and avoid potential misrepresentation, the title should explicitly specify "in vitro" growth kinetics. This clarification would better align the title with the study's actual focus and findings.

This study suggests that the entire genetic background significantly influences bacterial growth kinetics. However, to transform these predictions into established facts, extensive experimental validation is necessary. This would involve "bench experiments" focusing on generating and studying mutant variants of serotypes or strains with diverse genomic variations, such as targeted deletions. The growth phenotypes of these mutants should be analyzed, complemented by complementation assays to confirm the specific roles of the deleted regions. These efforts would provide critical empirical evidence to support the findings from the GWAS approach and enhance understanding of the genetic basis of bacterial growth kinetics.

In the discussion section, the authors state that "the influence of serotype appeared to be higher than the genetic background for the average growth rate" (lines 296-298). Alongside references 13-15, this emphasizes the important role of capsular variability, which is a key determinant of serotypes, in influencing growth kinetics. However, this raises the question: why isn't a specific locus like cps, which is central to capsule biogenesis, considered a strong influencer of growth kinetics in this study?

One plausible explanation could be the absence of "elevated signals" for cps in the GWAS analysis. GWAS relies on identifying loci with statistically significant associations to phenotypes. The lack of such signals for cps may indicate that its contribution, while biologically important, does not stand out genome-wide. This might be due to the polygenic nature of growth kinetics, where the overall genetic background exerts a cumulative effect, potentially diluting the apparent influence of individual loci like cps in statistical analyses.

Reviewer #3 (Public review):

This study provides insights into the growth kinetics of a diverse collection of Streptococcus pneumoniae, identifying capsule and lineage differences. It was not able to identify any specific loci from the genome-wide association studies (GWAS) that were associated with the growth features. It does provide a useful study linking phenotypic data with large-scale genomic population data. The methods for the large part were appropriately written in sufficient detail, and data analysis was performed with rigour. The interpretation of the results was supported by the data, although some additional explanation of the significance of e.g. ancestral state reconstruction would be useful. Efforts were made to make the underlying data fully accessible to the readers although some of the supplementary material could be formatted and explained a bit better.

eLife Assessment

This important study examines the relationship between cognition and mental health and investigates how brain, genetics, and environmental measures mediate that relationship. The methods and results are compelling and well-executed. Overall, this study will be of interest in the field of population neuroscience and in studies of mental health.

Reviewer #1 (Public review):

Summary:

This work integrates two timepoints from the Adolescent Brain Cognitive Development (ABCD) Study to understand how neuroimaging, genetic, and environmental data contribute to the predictive power of mental health variables in predicting cognition in a large early adolescent sample. Their multimodal and multivariate prediction framework involves a novel opportunistic stacking model to handle complex types of information to predict variables that are important in understanding mental health-cognitive performance associations.

Strengths:

The authors are commended for incorporating and directly comparing the contribution of multiple imaging modalities (task fMRI, resting state fMRI, diffusion MRI, structural MRI), neurodevelopmental markers, environmental factors, and polygenic risk scores in a novel multivariate framework (via opportunistic stacking), as well as interpreting mental health-cognition associations with latent factors derived from partial least squares. The authors also use a large well-characterized and diverse cohort of adolescents from the ABCD Study. The paper is also strengthened by commonality analyses to understand the shared and unique contribution of different categories of factors (e.g., neuroimaging vs mental health vs polygenic scores vs sociodemographic and adverse developmental events) in explaining variance in cognitive performance

Weaknesses:

The paper is framed with an over-reliance on the RDoC framework in the introduction, despite deviations from the RDoC framework in the methods. The field is also learning more about RDoC's limitations when mapping cognitive performance to biology. The authors also focus on a single general factor of cognition as the core outcome of interest as opposed to different domains of cognition. The authors could consider predicting mental health rather than cognition. Using mental health as a predictor could be limited by the included 9-11 year age range at baseline (where many mental health concerns are likely to be low or not well captured), as well as the nature of how the data was collected, i.e., either by self-report or from parent/caregiver report.

Reviewer #2 (Public review):

Summary:

This paper by Wang et al. uses rich brain, behaviour, and genetics data from the ABCD cohort to ask how well cognitive abilities can be predicted from mental-health-related measures, and how brain and genetics influence that prediction. They obtain an out-of-sample correlation of 0.4, with neuroimaging (in particular task fMRI) proving the key mediator. Polygenic scores contributed less.

Strengths:

This paper is characterized by the intelligent use of a superb sample (ABCD) alongside strong statistical learning methods and a clear set of questions. The outcome - the moderate level of prediction between the brain, cognition, genetics, and mental health - is interesting. Particularly important is the dissection of which features best mediate that prediction and how developmental and lifestyle factors play a role.

Weaknesses:

There are relatively few weaknesses to this paper. It has already undergone review at a different journal, and the authors clearly took the original set of comments into account in revising their paper. Overall, while the ABCD sample is superb for the questions asked, it would have been highly informative to extend the analyses to datasets containing more participants with neurological/psychiatric diagnoses (e.g. HBN, POND) or extend it into adolescent/early adult onset psychopathology cohorts. But it is fair enough that the authors want to leave that for future work.

In terms of more practical concerns, much of the paper relies on comparing r or R2 measures between different tests. These are always presented as point estimates without uncertainty. There would be some value, I think, in incorporating uncertainty from repeated sampling to better understand the improvements/differences between the reported correlations.

The focus on mental health in a largely normative sample leads to the predictions being largely based on the normal range. It would be interesting to subsample the data and ask how well the extremes are predicted.

A minor query - why are only cortical features shown in Figure 3?

eLife Assessment

This study establishes the methodology (machine vision and gaze pose estimation) and behavioral apparatus for examining social interactions between pairs of marmoset monkeys. Their results enable unrestrained social interactions under more rigorous conditions with detailed quantification of position and gaze. It has been difficult to study social interactions using artificial stimuli, as opposed to genuine interactions between unrestrained animals. This study makes an important contribution to studying social neuroscience within a laboratory setting; the approach is novel and well-executed, backed by convincing evidence.

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

One weakness that should be easily addressed is that no data is provided to directly assess how accurate the estimated head gaze is based on calibrations of the animals, for example, when they are looking at discrete locations like faces or video on a monitor. This would be useful to get an upper bound on how accurate the 3D gaze vector is estimated to be, for planned use in other studies. Although the accuracy appears sufficient for the current results, it would be difficult to know if it could be applied in other contexts where more precision might be necessary.

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

There are a few technical points in need of clarification, both in terms of the robustness of the gaze estimate, and possible confounds by gaze to non-face targets which may have relevance but are not discussed. These are relatively minor, and more suggestions than anything else.

eLife Assessment

The study describes a useful tool for assessing microglia morphology in a variety of experimental conditions. The MorphoCellSorter provides a solid platform for ranking microglia to reflect their morphology continuum and may offer new insight into changes in morphology associated with injury or disease. While the study provides an alternative approach to existing methods for measuring microglia morphology, the functional significance of the measured morphological changes were not determined.

Reviewer #1 (Public review):

The current manuscript by Bendeker et al. (2024) presents a new platform, MorphoCellSorter, for performing population wide microglial morphological analyses. This method adds to the many programs/platforms available to determine characteristics of microglial morphology; however, MorphoCellSorter is unique in that it uses Andrew's plotting to rank populations of cells together (in control and experimental groups) and present "big picture" views of how entire populations of microglia alter under different conditions. In their ranking system, Bendeker et al. (2024) use PCA to determine which of the morphological characteristics most define microglial populations, avoiding user subjective biases to determine these parameters. Compared to "expert" evaluators, MorphoCellSorter appears to perform consistently and accurately, including in different types of tissue preservation methods and in live cells, a key feature of the program. In addition, the researchers point out that this platform can be used across a wide array of imaging techniques and most microscopes that are available in a basic research lab. There are minor concerns about the platform's utility in analyzing embryonic microglia and primary microglial cultures, but overall, this platform will be another useful tool for microglial researchers to consider using in future studies. Furthermore, the method of morphological assessment aligns with the current direction of the field in identifying microglial cells in more nuanced ways.

In their current revision, the authors have done an excellent job responding to concerns and have updated the manuscript accordingly.

Reviewer #2 (Public review):

The authors introduce MorphCellSorter, an open-source tool available on GitHub, designed for automated morphometric analysis of microglia. Current understanding suggests that microglia represent a heterogeneous population, especially in non-steady adult states, better characterized as a continuum rather than distinct cell groups.

This tool was developed to classify microglia along this continuum. Using stained brain sections and microscope imaging, individual microglia are binarized and processed with MorphCellSorter, which categorizes them based on 20 morphological parameters. Notably, the tool is versatile, as it can be applied to both fluorescent and brightfield brain sections, as demonstrated by the authors. Additionally, it has been tested across various setups (both fixed and live tissues) and biological contexts (including embryonic stages, Alzheimer's disease models, stroke, and primary cell cultures), showcasing its versatility and adaptability. Overall, the study is well-conceived and could have some value in the field.

Numerous similar tools already exist, and the number is likely to grow, especially with advancements in AI. These tools have limited scientific utility as they provide descriptive rather than informative outputs. Microglial morphology varies due to external influences (such as developmental stages and injuries), but the significance of these variations remains largely hypothetical.

eLife Assessment

This manuscript represents a fundamental contribution demonstrating that fentanyl-induced respiratory depression can be reversed with a peripherally-restricted mu opioid receptor antagonist. The paper reports compelling and rigorous physiological, pharmacokinetic, and behavioral evidence supporting this major claim, and furthers mechanistic understanding of how peripheral opioid receptors contribute to respiratory depression. These findings reshape our understanding of opioid-related effects on respiration and have significant therapeutic implications given that medications currently used to reverse opioid overdose (such as naloxone) produce severe aversive and withdrawal effects via actions within the central nervous system.

Reviewer #1 (Public review):

Summary:

This paper shows that the synthetic opioid fentanyl induces respiratory depression in rodents. This effect is revised by the opioid receptor antagonist naloxone, as expected. Unexpectedly, the peripherally restricted opioid receptor antagonist naloxone methiodide also blocks fentanyl-induced respiratory depression.

Strengths:

The paper reports compelling physiology data supporting the induction of respiratory distress in fentanyl-treated animals. Evidence suggesting that naloxone methiodide reverses this respiratory depression is compelling. This is further supported by pharmacokinetic data suggesting that naloxone methiodide does not penetrate into the brain, nor is it metabolized into brain-penetrant naloxone.

Weaknesses:

The paper would be further strengthened by establishing the functional significance of the altered neural activity detected in the nTS (as measured by cFos and GcAMP/photometry) in the context of opioid-induced respiratory depression.

Reviewer #2 (Public review):

Summary:

In this article, Ruyle and colleagues assessed the contribution of central and peripheral mu opioid receptors in mediating fentanyl-induced respiratory depression using both nalaxone and nalaxone methiodide, which does not cross the blood brain barrier. Both compounds prevented and reversed fentanyl-induced respiratory depression to a comparable degree. The advantage of peripheral treatments is that they circumvent the withdrawal-like effects of nalaxone. Moreover, neurons located in the nucleus of the solitary tract are no longer activated by fentanyl when nalaxone methiodide is administered, suggesting that these responses are mediated by peripheral mu opioid receptors. The results delineate a role for peripheral mu opioid receptors in fentanyl-derived respiratory depression and identify a potentially advantageous approach to treating overdoses without inflicting withdrawal on the patients.

Strengths:

The strengths of the article include the intravenous delivery of all compounds, which increases the translational value of the article. The authors address both prevention and reversal of fentanyl-derived respiratory depression. The experimental design and data interpretation are rigorous and appropriate controls were used in the study. Multiple doses were screened in the study and the approaches were multipronged. The authors demonstrated activation of NTS cells using multiple techniques and the study links peripheral activation of mu opioid receptors to central activation of NTS cells. Both males and females were used in the experiments. The authors demonstrate the peripheral restriction of nalaxone methiodide.

Weaknesses:

Nalaxone is already broadly used to prevent overdoses from opioids so in some respects, the effects reported here are somewhat incremental.

Comments on the latest version:

I think the authors have adequately addressed previous critiques and I don't have any additional comments.

Reviewer #3 (Public review):

Summary

This manuscript outlines a series of very exciting and game-changing experiments examining the role of peripheral MORs in OIRD. The authors outline experiments that demonstrate a peripherally restricted MOR antagonist (NLX Methiodide) can rescue fentanyl-induced respiratory depression and this effect coincides with a lack of conditioned place aversion. This approach would be a massive boon to the OUD community, as there are a multitude of clinical reports showing that naloxone rescue post fentanyl over-intoxication is more aversive than the potential loss-of-life to the individuals involved. This important study reframes our understanding of successful overdose rescue with a potential for reduced aversive withdrawal effects.

Strengths:

Strengths include the plethora of approaches arriving at the same general conclusion, the inclusion of both sexes, and the result that a peripheral approach for OIRD rescue may side-step severe negative withdrawal symptoms of traditional NLX rescue.

Weaknesses:

All weaknesses were addressed.

eLife Assessment

In this revised work, Barzó et al. assessed the electrophysiological and anatomical properties of a large number of layer 2/3 pyramidal neurons in brain slices of human neocortex across a wide range of ages, from infancy to elderly individuals, using whole-cell patch clamp recordings and anatomical reconstructions. This large data set represents an important contribution to our understanding of how these properties change across the human lifespan, supported by convincing data and analyses. The authors have addressed the concerns raised in previous reviews. Overall, this study strengthens our understanding of how the neural properties of human cortical neurons change with age and will contribute to building more realistic models of human cortical function.

Reviewer #1 (Public review):

Summary:

The manuscript co-authored by Pál Barzó et al is very clear and very well written, demonstrating the electrophysiological and morphological properties of the human cortical layer 2/3 pyramidal cells across a wide age range, from age 1 month to 85 years using whole-cell patch clamp. To my knowledge, this is the first study that look at the cross-age differences biophysical and morphological properties of human cortical pyramidal cells. The community will also appreciate the significant effort involved in recording data from 485 cells, given the challenges associated with collecting data from human tissue. Understanding the electrophysiological properties of individual cells, which are essential for brain function, is crucial for comprehending human cortical circuits. I think this research enhances our knowledge of how biophysical properties change over time in the human cortex. I also think that by building models of human single cells at different ages using these data, we can develop more accurate representations of brain function. This, in turn, provides valuable insights into human cortical circuits and function and helps in predicting changes in biophysical properties in both health and disease.

Strengths:

The strength of this work lies in demonstrating how the electrophysiological and morphological features of human cortical layer 2/3 pyramidal cells change with age, offering crucial insights into brain function throughout life.

Comments on revisions:

Thanks to the authors for addressing my comments and providing greater clarity in the methodology. The analysis is much clearer now. I also appreciate their additional data analysis, particularly on morphology, which strengthens the paper.

Reviewer #2 (Public review):

Summary:

In this study, Barzo and colleagues aim to establish an appraisal for the development of basal electrophysiology of human layer 2/3 pyramidal cells across life and compare their morphological features at the same ages.

Strengths:

The authors have generates recordings from an impressive array of patient samples, allowing them to directly compare the same electrophysiological features as a function of age and other biological features. These data are extremely robust and well organised.

The authors group patient ages into developmentally organised bins, which are elaborated on in supplementary analysis - exemplifying the importance of determining early postnatal development on human neuron function

Weaknesses:

The author's use of (perhaps) arbitrary categorisation of spine morphology could limit the full usefulness of these data.

Overall, the authors achieve their aims by assessing the physiological and morphological properties of human L2/3 pyramidal neurons across life. Their findings have extremely important ramifications for our understanding of human brain development and implications for how different neuronal properties may influence life and disease associated with neurological conditions.

Comments on revisions:

Overall, the authors have satisfied my concerns. I fully appreciate their candour with their data and the potential limitations. I especially appreciate their supplementary data inclusions which I believe truly strengthen their conclusions and are a valuable resource for the field,

I agree whole-heartedly with the authors assertion that it is perhaps better to use the most sophisticated equipment, not always being most appropriate. However, statistical rigour should still be standard. As such, my one remaining concern relates to inappropriate replicate choice of spine morphology data in figure 6. I commend the authors inclusion of additional reconstructions and morphology data from further cells in this data set. However, to me, these still represent data from 3 cells and 1 patient/age - as to the best of my interpretation. I feel it would be more helpful to plot cell averages +/- SD for each cell - even if side-by-side with data from all spines. Likewise, it is unclear what statistical test was performed on these data and did it take into account the fact that these values are a) from 3 technical replicates per group, or b) that many of the data sets consist of many zero-values (would a categorical test be more appropriate?).

Reviewer #3 (Public review):

Summary:

To understand the specificity of age-dependent changes in the human neocortex, this paper investigated the electrophysiological and morphological characteristics of pyramidal cells in a wide age range from infants to the elderly.

The results show that some electrophysiological characteristics change with age, particularly in early childhood. In contrast, the larger morphological structures, such as the spatial extent and branching frequency of dendrites, remained largely stable from infancy to old age. On the other hand, the shape of dendritic spines is considered immature in infancy, i.e., the proportion of mushroom-shaped spines increases with age.

Strengths:

Whole-cell recordings and intracellular staining of pyramidal cells in defined areas of the human neocortex allowed the authors to compare quantitative parameters of electrophysiological and morphological properties between finely divided age groups.

They succeeded in finding symmetrical changes specific to both infants and the elderly, and asymmetrical changes specific to either infants or the elderly. The similarity of pyramidal cell characteristics between areas is unexpected.

Weaknesses:

Human L2/3 pyramidal cells are thought to be heterogeneous, as L2/3 has expanded to a high degree during the evolution from rodents to humans. However, the diversity (subtyping) is not revealed in this paper.

Comments on revisions:

I believe that the current version has been sufficiently revised based on my comments.

eLife assessment:

This study describes a new set of genetic tools for optimized Cre-mediated gene deletion in mice. The advances are substantial and will facilitate biomedical research. Although the tools have been validated using solid methodologies, the quantitative assessment of their recombination efficiency is not yet sufficiently described. Evaluating their ability to mediate the deletion of multiple alleles in a mosaic setting would also be a highly valuable addition.

Reviewer #1 (Public Review):

Summary:

Shi and colleagues report the use of modified Cre lines in which the coding region of Cre is disrupted by rox-STOP-rox or lox-STOP-lox sequences to prevent the expression of functional protein in the absence of Dre or Cre activity, respectively. The main purpose of these tools is to enable intersectional or tamoxifen-induced Cre activity with minimal or no leaky activity from the second, Cre-expressing allele. It is a nice study but lacks some functional data required to determine how useful these alleles will be in practice, especially in comparison with the figure line that stimulated their creation.

Strengths:

The new tools can reduce Cre leak in vivo.

Weaknesses:

(1) Activity of R26-loxCre line. As the authors point out, the greatest value of this approach is to accomplish a more complete Cre-mediated gene deletion using CreER transgenes that are combined with low-efficiency floxed alleles using their R26-loxCre line that is similar to the iSure Cre reported by Benedito and colleagues. The data in Figure 5 show strong activity at the Confetti locus, but the design of the newly reported R26-loxCre line lacks a WPRE sequence that was included in the iSure-Cre line to drive very robust protein expression. Thus while the line appears to have minimal leak, as the design would predict, the question of how much of a deletion increase is obtained over simple use of the CreER transgene alone is a key question for use by investigators. This is further addressed in Figure 6 where it is compared with Alb-CreER alone to recombine the Ctnnb1 floxed allele. They demonstrate that recombination frequency is clearly improved, but the western blot in Figure 6E does not look like there was a large amount of remaining b-catenin to remove. These data are certainly promising, but the most valuable experiment for such a new tool would be a head-to-head comparison with iSure (or the latest iSure version from the Benedito lab) using the same CreER and target floxed allele. At the very least a comparision of Cre protein expression between the two lines using identical CreER activators is needed.

(2) In vivo analysis of mCre activities. Why did the authors not use the same driver to compare mCre 1, 4, 7, and 10? The study in Figure 2 uses Alb-roxCre for 1 and 7 and Cdh5-roxCre for 4 and 10, with clearly different levels of activity driven by the two alleles in vivo. Thus whether mCre1 is really better than mCre4 or 10 is not clear.

(3) Technical details are lacking. The authors provide little specific information regarding the precise way that the new alleles were generated, i.e. exactly what nucleotide sites were used and what the sequence of the introduced transgenes is. Such valuable information must be gleaned from schematic diagrams that are insufficient to fully explain the approach.

Reviewer #2 (Public Review):

Summary:

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.

Strengths:

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.

Weaknesses:

The scenario where the lines would demonstrate their full potential compared to existing models has not been tested. 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. Therefore, a demonstration of the efficient deletion of multiple floxed alleles in a mosaic fashion would be a valuable addition.

In addition, a drawback of this line is the constitutive expression of Cre. When combined with the confetti line, the reporter cassette will continue flipping, potentially leading to misleading lineage tracing results. Constitutive expression of Cre is also associated with toxicity, as discussed by the authors in the introduction. These drawbacks should be acknowledged.

Reviewer #3 (Public Review):

Summary:

The authors report a new version of the iSuRe-Cre approach, which was originally developed by Rui Benedito's group in Spain (https://doi.org/10.1038/s41467-019-10239-4). Shi et al claim that their approach shows reduced leakiness compared to the iSuRe-Cre line. Shi et al elaborate strongly about the leakiness of iSuRe-Cre mice, although leakiness is rather minor according to the original publication and the senior author of the study wrote in a review a few years ago that there is no leakiness (https://doi.org/10.1016/j.jbc.2021.100509). 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.

Strengths:

The authors carefully evaluated the efficiency and leakiness of the new strains and demonstrated the applicability by marking peri-central hepatocytes in an intersectional genetics approach, amongst others. I can only find very few weaknesses in the paper, which represents the result of an enormous effort. Carefully conducted technical studies have considerable value. However, I would have preferred to see a study, which uses the wonderful new tools to address a major biological question, rather than a primarily technical report, which describes the ongoing efforts to further improve Cre and Dre recombinase-mediated recombination.

Weaknesses:

Very high levels of Cre expression may cause toxic effects as previously reported for the hearts of Myh6-Cre mice. Thus, it seems sensible to test for unspecific toxic effects, which may be done by bulk RNA-seq analysis, cell viability, and cell proliferation assays. It should also be analyzed whether the combination of R26-roxCre-tdT with the Tnni3-Dre allele causes cardiac dysfunction, although such dysfunctions should be apparent from potential changes in gene expression.

The R26-GFP or R26-tdT reporters, Alb-roxCre1-tdT, Cdh5-roxCre4-tdT, Alb-roxCre7-GFP, and Cdh5-roxCre10-GFP demonstrate no leakiness without Dre-rox recombination (Figure S1-S2). Is there any leakiness when the inducible DreER allele is introduced but no tamoxifen treatment is applied? This should be documented. The same also applies to loxCre mice.

The enhanced efficiency of loxCre and roxCre systems holds promise for reducing the necessary tamoxifen dosage, potentially reducing toxicity and side effects. In Figure 6, the author demonstrates an enhanced recombination efficiency of loxCre mice, which makes it possible to achieve efficient deletion of Ctnnb1 with a single dose of tamoxifen, whereas a conventional driver (Alb-CreER) requires five dosages. It would be very helpful to include a dose-response curve for determining the minimum dosage required in Alb-CreER; R26-loxCre-tdT; Ctnnb1flox/flox mice for efficient recombination.

In the liver panel of Figure 4F, tdT signals do not seem to colocalize with the VE-cad signals, which is odd. Is there any compelling explanation?

The authors claim that "virtually all tdT+ endothelial cells simultaneously expressed YFP/mCFP" (right panel of Figure 5D). Well, it seems that the abundance of tdT is much lower compared to YFP/mCFP. If the recombination of R26-Confetti was mainly triggered by R26-loxCre-tdT, the expression of tdT and YFP/mCFP should be comparable. This should be clarified.

In several cases, the authors seem to have mixed up "R26-roxCre-tdT" with "R26-loxCre-tdT". There are errors in #251 and #256. Furthermore, in the passage from line #278 to #301. In the lines #297 and #300 it should probably read "Alb-CreER; R26-loxCre-tdT;Ctnnb1flox/flox"" rather than "Alb-CreER;R26-tdT2;Ctnnb1flox/flox".

eLife Assessment

This is an important study that characterizes a surprising interaction between two different cytokine/hormone receptors using nanoscale resolution (dSTORM) microscopy. The study provides solid evidence that the interaction is ligand-dependent, and is mediated by the receptor-associated intracellular signalling molecule JAK2. While at present limited to growth hormone and prolactin receptors in a limited number of cell lines, there are potentially broad implications for cytokine signalling, as such JAK2-mediated interactions could occur between a range of different cytokines. Moreover, the specific hormone interactions shown in the manuscript may have significant implications for understanding how these hormones can have differential effects in breast cancer, under different conditions.

Reviewer #3 (Public review):

Summary:

The authors are interested in the relative importance of PRL versus GH and their interactive signaling in breast cancer. After examining GHR-PRLR interactions in response to ligands, they suggest that a reduction in cell surface GHR in response to PRL may be a mechanism whereby PRL can sometimes be protective against breast cancer.

Strengths:

The strengths of the study include the interesting question being addressed and the application of multiple complementary techniques, including dSTORM, which is technically very challenging, especially when using double labeling. Thus, dSTORM is used to analyze co-clustering of GHR and PRLR, and, in response to PRL, rapid internalization of GHR and increased cell surface PRLR. Conclusions from Proximity ligation assays are that some GHR and PRLR are within 40 nm (≈ 4 plasma membranes) of each other and that upon ligand stimulation, they move apart. Intact receptor knockin and knockout approaches and receptor constructs without the Jak2 binding domain demonstrate a) a requirement for the PRLR for there to be PRL- driven internalization of GHR, and b) that Jak2-PRLR interactions are necessary for stability of the GHR-PRLR colocalizations.

Weaknesses:

Although improved over the first version, the manuscript still suffers from a lack of detail, which in places makes it difficult to evaluate the data and would make it very difficult for the results to be replicated by others.

Comments on revised version:

Points for improvement of the manuscript:

(1) There is still insufficient detail about the proximity ligation assay. For example, PLAs that use reagents from Sigma (as now reported) require primary antibodies from two different species and yet both the anti-PRLR and anti-GHR used for dSTORM were mouse monoclonals. On line 356 it says that the ECD antibodies were used for microscopy and the PLA is microscopy. Were instead the ICD antibodies used for the PLA? If so, how do we know that one or more of the proteins in the very strong "non-specific" bands seen on Figure 5A are not what is being localized? Could you do a Western blot of just cell membrane proteins? There needs to be further clarity/explanation.

(2) Although the manuscript now shows a Western blot using the antibodies against intracellular regions of the receptor, a full Western blot is not provided for the antibodies against the S2 extracellular domain used for the dSTORM. While I haven't checked the papers showing characterization of the anti-GHR, I did re-check reference 70, which the authors say shows full characterization of the PRLR antibody, and this does not show a full Western (only portions of gels). How do we know that this antibody is not recognizing some other cell surface molecule, the surface expression of which increases upon stimulation of the cells with PRL? Is there only one band when blotting whole cell extracts with either the GHR or PRLR ECD antibodies so we can be sure of specificity? Figure S2 helps some, but these are different cells and the relative expression of the PRLR versus some other potential cell surface protein in these engineered cells may well be completely different.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

(1) The questions after reading this manuscript are what novel insights have been gained that significantly go beyond what was already known about the interaction of these receptors and, more importantly, what are the physiological implications of these findings? The proposed significance of the results in the last paragraph of the Discussion section is speculative since none of the receptor interactions have been investigated in TNBC cell lines. Moreover, no physiological experiments were conducted using the PRLR and GH knockout T47D cells to provide biological relevance for the receptor heteromers. The proposed role of JAK2 in the cell surface distribution and association of both receptors as stated in the title was only derived from the analysis of box 1 domain receptor mutants. A knockout of JAK2 was not conducted to assess heteromers formation.

We thank the reviewer for these comments. The novel insight is that two different cytokine receptors can interact in an asymmetric, ligand-dependent manner, such that one receptor regulates the other receptor’s surface availability, mediated by JAK2. To our knowledge this has not been reported before. Beyond our observations, there is the question if this could be a much more common regulatory mechanism and if it has therapeutic relevance. However, answering these questions is beyond the scope of this work.

Along the same line, the question regarding the biological relevance of our receptor heteromers and JAK2’s role in cell surface distribution is undoubtfully very important. Studying GHR-PRLR cell surface distributions in JAK2 knockout cells and certain TNBC cell lines as proposed by the reviewer could perhaps be insightful. However, most TNBCs down-regulate PRLR [1], so we would first have to identify TNBC cell lines that actually express PRLR at sufficiently high levels. Moreover, knocking out JAK2 is known to significantly reduce GHR surface availability [2,3], such that the proposed experiment would probably provide only limited insights.

Unfortunately, our team is currently not in the position to perform any experiments (due to lack of funding and shortage of personnel). However, to address the reviewer’s comment as much as possible, we have revised the respective paragraph of the discussion section to emphasize the speculative nature of our statement and have added another paragraph discussing shortcoming and future experiments (see revised manuscript, pages 23-24).

(1) López-Ozuna, V., Hachim, I., Hachim, M. et al. Prolactin Pro-Differentiation Pathway in Triple Negative Breast Cancer: Impact on Prognosis and Potential Therapy. Sci Rep 6, 30934 (2016). https://www.nature.com/articles/srep30934

(2) He, K., Wang, X., Jiang, J., Guan, R., Bernstein, K.E., Sayeski, P.P., Frank, S.J. Janus kinase 2 determinants for growth hormone receptor association, surface assembly, and signaling. Mol Endocrinol. 2003;17(11):2211-27. doi: 10.1210/me.2003-0256. PMID: 12920237.

(3) He, K., Loesch, K., Cowan, J.W., Li, X., Deng, L., Wang, X., Jiang, J., Frank, S.J. Janus Kinase 2 Enhances the Stability of the Mature Growth Hormone Receptor, Endocrinology, Volume 146, Issue 11, 2005, Pages 4755–4765,https://doi.org/10.1210/en.2005-0514

(2) Except for some investigation of γ2A-JAK2 cells, most of the experiments in this study were conducted on a single breast cancer cell line. In terms of rigor and reproducibility, this is somewhat borderline. The CRISPR/Cas9 mutant T47D cells were not used for rescue experiments with the corresponding full-length receptors and the box1 mutants. A missed opportunity is the lack of an investigation correlating the number of receptors with physiological changes upon ligand stimulation (e.g., cellular clustering, proliferation, downstream signaling strength).

We appreciate the reviewer’s comments. While we are confident in the reproducibility of our findings, including those obtained in the T47D cell line, we acknowledge that testing in additional cell lines would have strengthened the generalizability of our results. We also recognize that performing a rescue experiment using our T47D hPRLR or hGHR KO cells would have been valuable. Furthermore, examining physiological changes, such as proliferation rates and downstream signaling responses, would have provided additional insights. Unfortunately, these experiments were not conducted at the time, and we currently lack the resources to carry them out.

(3) An obvious shortcoming of the study that was not discussed seems to be that the main methodology used in this study (super-resolution microscopy) does not distinguish the presence of various isoforms of the PRLR on the cell surface. Is it possible that the ligand stimulation changes the ratio between different isoforms? Which isoforms besides the long form may be involved in heteromers formation, presumably all that can bind JAK2?

This is a very good point. We fully agree with the reviewer that a discussion of the results in the light of different PRLR isoforms is appropriate. We have added information on PRLR isoforms to the Introduction (see revised manuscript, page 2) and Discussion sections (see revised manuscript, pages 23-24).

(4) Changes in the ligand-inducible activation of JAK2 and STAT5 were not investigated in the T47D knockout models for the PRL and GHR. It is also a missed opportunity to use super-resolution microscopy as a validation tool for the knockouts on the single cell level and how it might affect the distribution of the corresponding other receptor that is still expressed.

We thank the reviewer for his comment. We fully agree that such additional experiments could be very valuable. We are sorry but, as already mentioned above, this is not something we are able to address at this stage due to lack of personnel and funding. However, we do hope to address these and other proposed experiments in the future.

(5) Why does the binding of PRL not cause a similar decrease (internalization and downregulation) of the PRLR, and instead, an increase in cell surface localization? This seems to be contrary to previous observations in MCF-7 cells (J Biol Chem. 2005 October 7; 280(40): 33909-33916).

It has been recently reported for GHR that not only JAK2 but also LYN binds to the box1-box2 region, creating competition that results in divergent signaling cascades and affects GHR nanoclustering [1]. So, it is reasonable to assume that similar mechanisms may be at work that regulate PRLR cell surface availability. Differences in cells’ expression of such kinases could perhaps play a role in the perceived inconsistency. Also, Lu et al. [2] studied the downregulation of the long PRLR isoform in response to PRL. All other PRLR isoforms were not detectable in MCF-7 cells. So, differences between MCF-7 and T47D may lead to this perceived contradiction.

At this stage, we can only speculate about the actual reasons for these seemingly contradictory results. However, for full transparency, we are now mentioning this apparent contradiction in the Discussion section (see page 23) and have added the references below.

(1) Chhabra, Y., Seiffert, P., Gormal, R.S., et al. Tyrosine kinases compete for growth hormone receptor binding and regulate receptor mobility and degradation. Cell Rep. 2023;42(5):112490. doi: 10.1016/j.celrep.2023.112490. PMID: 37163374.

https://www.cell.com/cell-reports/pdf/S2211-1247(23)00501-6.pdf

(2) Lu, J.C., Piazza, T.M., Schuler, L.A. Proteasomes mediate prolactin-induced receptor down-regulation and fragment generation in breast cancer cells. J Biol Chem. 2005 Oct 7;280(40):33909-16. doi: 10.1074/jbc.M508118200. PMID: 16103113; PMCID: PMC1976473.

(6) Some figures and illustrations are of poor quality and were put together without paying attention to detail. For example, in Fig 5A, the GHR was cut off, possibly to omit other nonspecific bands, the WB images look 'washed out'. 5B, 5D: the labels are not in one line over the bars, and what is the point of showing all individual data points when the bar graphs with all annotations and SD lines are disappearing? As done for the y2A cells, the illustrations in 5B-5E should indicate what cell lines were used. No loading controls in Fig 5F, is there any protein in the first lane? No loading controls in Fig 6B and 6H.

We thank the reviewer for pointing this out. We have amended Fig. 5A to now show larger crops of the two GHR and PRLR Western Blot images and thus a greater range of proteins present in the extracts. Please note that the bands in the WBs other than what is identified as GHR and PRLR are non-specific and reflect roughly equivalent loading of protein in each lane.

We also made some changes to Figures 5B-5E.

(7) The proximity ligation method was not described in the M&M section of the manuscript.

We thank the reviewer for pointing this out. We have added a description of the PL method to the Methods section.

Reviewer #1 (Recommendations for the Authors):

A final suggestion for future investigations: Instead of focusing on the heteromer formation of the GHR/PRLR which both signal all through the same downstream effectors (JAK2, STAT5), it would have been more cancer-relevant, and perhaps even more interesting, to look for heteromers between the PRLR and receptors of the IL-6 family since it had been shown that PRL can stimulate STAT3, which is a unique feature of cancer cells. If that is the case, this would require a different modality of the interaction between different JAK kinases.

We highly appreciate the reviewer’s recommendation and hope to follow up on it in the near future.

Reviewer #2 (Public Review):

(1) I could not fully evaluate some of the data, mainly because several details on acquisition and analysis are lacking. It would be useful to know what the background signal was in dSTORM and how the authors distinguished the specific signal from unspecific background fluorescence, which can be quite prominent in these experiments. Typically, one would evaluate the signal coming from antibodies randomly bound to a substrate around the cells to determine the switching properties of the dyes in their buffer and the average number of localisations representing one antibody. This would help evaluate if GHR or PRLR appeared as monomers or multimers in the plasma membrane before stimulation, which is currently a matter of debate. It would also provide better support for the model proposed in Figure 8.

We are grateful for the reviewer’s comment. In our experience, the background signal is more relevant in dSTORM when imaging proteins that are located at deeper depths (> 3 μm) above the coverslip surface. In our experiments, cells are attached to the coverslip surface and the proteins being imaged are on the cell membrane. In addition, we employed dSTORM’s TIRF (total internal reflection fluorescence) microscopy mode to image membrane receptor proteins. TIRFM exploits the unique properties of an induced evanescent field in a limited specimen region immediately adjacent to the interface between two media having different refractive indices. It thereby dramatically reduces background by rejecting fluorescence from out-of-focus areas in the detection path and illuminating only the area right near the surface.

Having said that, a few other sources such as auto-fluorescence, scattering, and non-bleached fluorescent molecules close to and distant from the focal plane can contribute to the background signal. We tried to reduce auto-fluorescence by ensuring that cells are grown in phenol-red-free media, imaging is performed in STORM buffer which reduces autofluorescence, and our immunostaining protocol includes a quenching step aside from using blocking buffer with different serum, in addition to BSA. Moreover, we employed extensive washing steps following antibody incubations to eliminate non-specifically bound antibodies. Ensuring that the TIRF illumination field is uniform helps reduce scatter. Additionally, an extended bleach step prior to the acquisition of frames to determine localizations helped further reduce the probability of non-bleached fluorescent molecules.

In short, due to the experimental design we do not expect much background. However, in the future, we will address this concern and estimate background in a subtype dependent manner. To this end we will distinguish two types of background noise: (A) background with a small change between subsequent frames, which mainly consists of auto-fluorescence and non-bleached out-of-focus fluorescent molecules; and (B) background that changes every imaging frame, which is mainly from non-bleached fluorescent molecules near the focal plane. For type (A) background, temporal filters must be used for background estimation [1]; for type (B) background, low-pass filters (e.g., wavelet transform) should be used for background estimation [2].

(1) Hoogendoorn, Crosby, Leyton-Puig, Breedijk, Jalink, Gadella, and Postma (2014). The fidelity of stochastic single-molecule super-resolution reconstructions critically depends upon robust background estimation. Scientific reports, 4, 3854. https://doi.org/10.1038/srep03854

(2) Patel, Williamson, Owen, and Cohen (2021). Blinking statistics and molecular counting in direct stochastic reconstruction microscopy (dSTORM). Bioinformatics, Volume 37, Issue 17, September 2021, Pages 2730–2737, https://doi.org/10.1093/bioinformatics/btab136

(2) Since many of the findings in this work come from the evaluation of localisation clusters, an image showing actual localisations would help support the main conclusions. I believe that the dSTORM images in Figures 1 and 2 are density maps, although this was not explicitly stated. Alexa 568 and Alexa 647 typically give a very different number of localisations, and this is also dependent on the concentration of BME. Did the authors take that into account when interpreting the results and creating the model in Figures 2 and 8?

I believe that including this information is important as findings in this paper heavily rely on the number of localisations detected under different conditions.

Including information on proximity labelling and CRISPR/Cas9 in the methods section would help with the reproducibility of these findings by other groups.

Figures 1 and 2 show Gaussian interpolations of actual localizations, not density maps. Imaging captured the fluorophores’ blinking events and localizations were counted as true localizations, when at least 5 consecutive blinking events had been observed. Nikon software was used for Gaussian fitting. In other words, we show reconstructed images based on identifying true localizations using gaussian fitting and some strict parameters to identify true fluorophore blinking. This allowed us to identify true localizations with high confidence and generate a high-resolution image for membrane receptors.

Indeed, Alexa 568 and 647 give different numbers of localization. This is dependent on the intrinsic photo-physics of the fluorophores. Specifically, each fluorophore has a different duty cycle, switching cycle, and survival fraction. However, we note that we focused on capturing the relative changes in receptor numbers over time, before and after stimulation by ligands, not the absolute numbers of surface GHR and PRLR. We are not comparing the absolute numbers of localizations or drawing comparisons for localization numbers between 568 and 647. For all these different conditions/times, the photo-physics for a particular fluorophore remains the same. This allows us to make relative comparisons.

As far as the effect of BME is concerned, the concentration of mercaptoethanol needs to be carefully optimized, as too high a concentration can potentially quench the fluorescence or affect the overall stability of the sample. However, we are using an optimized concentration which has been previously validated across multiple STORM experiments. This makes the concerns relating to the concentration of BME irrelevant to the current experimental design. Besides, the concentration of BME is maintained across all experimental conditions.

We have added information regarding PL and CRISPR/Cas9 for generating hGHR KO and hPRLR KO cells in two new subsections to the Methods section.

Reviewer #2 (Recommendations for the authors):

In the methods please include:<br /> (1) A section with details on proximity ligation assays.

We have added a description of the PL method to the Methods section.

(2) A section on CRISPR/Cas9 technology.

We have added two new sections on “Generating hGHR knockout and hPRLR knockout T47D cells” and “Design of sgRNAs for hGHR  or hPRLR knockout” to the Methods section.

(3) List the precise composition of the buffer or cite the paper that you followed.

We used the buffer recipe described in this protocol [1] and have added the components with concentrations as well as the following reference to the manuscript.

(1) Beggs, R.R., Dean, W.F., Mattheyses, A.L. (2020). dSTORM Imaging and Analysis of Desmosome Architecture. In: Turksen, K. (eds) Permeability Barrier. Methods in Molecular Biology, vol 2367. Humana, New York, NY. https://doi.org/10.1007/7651_2020_325

(4) Exposure time used for image acquisition to put 40 000 frames in the context of total imaging time and clarify why you decided to take 40 000 images per channel.

Our Nikon Ti2 N-STORM microscope is equipped with an iXon DU-897 Ultra EMCCD camera from Andor (Oxford Instruments). According to the camera’s manufacturer, this camera platform uses a back-illuminated 512 x 512 frame transfer sensor and overclocks readout to 17 MHz, pushing speed performance to 56 fps (in full frame mode). We note that we always tried to acquire STORM images at the maximal frame rate. As for the exposure time, according to the manufacturer it can be as short as 17.8 ms. We would like to emphasize that we did not specify/alter the exposure time.

See also: https://andor.oxinst.com/assets/uploads/products/andor/documents/andor-ixon-ultra-emccd-specifications.pdf

The decision to take 40,000 images per frame was based on our intention to identify the true population of the molecules of interest that are localized and accurately represented in the final reconstruction image. The total number of frames depends on the sample complexity, density of sample labeling and desired resolution. We tested a range of frames between 20,000 and 60,000 and found for our experimental design and output requirements that 40,000 frames provided the best balance between achieving maximal resolution and desired localizations to make consistent and accurate localization estimates across different stimulation conditions compared to basal controls.

(5) The lasers used to switch Alexa 568 and Alexa 647. Were you alternating between the lasers for switching and imaging of dyes? Intermittent and continuous illumination will produce very different unspecific background fluorescence.

Yes, we used an alternating approach for the lasers exciting Alexa 647 and Alexa 568, for both switching and imaging of the dyes.

(6) A paragraph with a detailed description of methods used to differentiate the background fluorescence from the signal.

We have addressed the background fluorescence under Point 1 (Public Review). We have added a paragraph in the Methods section on this issue.

(7) Minor corrections to the text:

It appears as though there is a large difference in the expression level of GHR and PRLR in basal conditions in Figure 1. This can be due to the switching properties of the dyes, which is related to the amount of BME in the buffer, or it can be because there is indeed more PRL. Would the authors be able to comment on this?

We thank the reviewer for this suggestions. According to expression data available online there is indeed more PRLR than GHR in T47D cells. According to CellMiner [1], T47D cells have an RNA-Seq gene expression level log2(FPKM + 1) of 6.814 for PRLR, and 3.587 for GHR, strongly suggesting that there is more PRLR than GHR in basal conditions, matching the reviewer’s interpretation of our images in Fig. 1 (basal). However, we would advise against using STORM images for direct comparisons of receptor expression. First, with TIRF images, we are only looking at the membrane fraction (~150 nm close to the coverslip membrane interface) that is attached to the coverslip. Secondly, as discussed above, our data represent relative cell surface receptor levels that allow for comparison of different conditions (basal vs. stimulation) and does not represent absolute quantifications. Everything is relative and in comparison to controls.

Also, BME is not going to change the level of expression. The differences in growth factor expression as estimated by relative comparison can be attributed to the actual changes in growth factors and is not an artifact of the amount of BME in the buffer or the properties of dyes. These factors are maintained across all experimental conditions and do not influence the final outcome.

(1) https://discover.nci.nih.gov/cellminer/

(8) I would encourage the authors to use unspecific binding to characterize the signal coming from single antibodies bound to the substrate. This would provide a mean number of localizations that a single antibody generates. With this information, one can evaluate how many receptors there are per cluster, which would strengthen the findings and potentially provide additional support for the model presented in Figure 8. It would also explain why the distributions of localisations per cluster in Fig. 3B look very different for hGHR and hPRLR. As the authors point out in the discussion, the results on predimerization of these receptors in basal conditions are conflicting and therefore it is important to shed more light on this topic.

We thank the reviewer for this suggestions. While we are unable to perform this experiment at this stage, we will keep it in mind for future experiments.

(9) Minor corrections to the figures:

Figure 1:

In the legend, please say what representation was used. Are these density maps or another representation? Please provide examples of actual localisations (either as dots or crosses representing the peaks of the Gaussians). Most findings of this work rely on the characterisation of the clusters of localisations and therefore it is of essence to show what the clusters look like. This could potentially go to the supplemental info to minimise additional work. It's very hard to see the puncta in this figure.

If the authors created zoomed regions in each of the images (as in Figure 3), it would be much easier to evaluate the expression level and the extent of colocalisation. Halfway through GHR 3 min green pixels become grey, but this may be the issue with the document that was created. Please check. Either increase the font on the scale bars in this figure or delete it.

As described above, Figure 1 does not show density maps. Imaging captured the fluorophores’ blinking events and localizations were counted as true localizations, when at least 5 consecutive blinking events had been observed. Nikon software was used for Gaussian fitting and smoothing.

We have generated zoomed regions. In our files (original as well as pdf) we do not see pixels become grey. We increased the font size above one of the scale bars and removed all others.

Figure 3:

In A, the GHR clusters are colour coded but PRLR are not. Are both DBSCN images? Explain the meaning of colour coding or show it as black and white. Was brightness also increased in the PRLR image? The font on the scale bars is too small. In B, right panels, the font on the axes is too small. In the figure legend explain the meaning of 33.3 and 16.7

In our document, both GHR and PRLR are color coded but the hGHR clusters are certainly bigger and therefore appear brighter than the hPRLR clusters. Both are DBSCAN images. The color coding allows to distinguish different clusters (there is no other meaning). We have kept the color-coding but have added a sentence to the caption addressing this. Brightness was increased in both images of Panel B equally. 33.3 and 16.7 are the median cluster sizes. We have added a sentence to the caption explaining this. We have increased the font on the axes in B (right panels).

Figure 4:

I struggled to see any colocalization in the 2nd and the 3rd image. Please show zoomed-in sections. In the panels B and C, the data are presented as fractions. Is this per cell? My interpretation is that ~80% of PRL clusters also contain GHR.

Is this in agreement with Figures 1 and 2? In Figure 1, PRL 3 min, Merge, colocalization seems much smaller. Could the authors give the total numbers of GHR and PRLR from which the fractions were calculated at least in basal conditions?

We have provided zoom-in views. As for panels B and C, fractions are number of clusters containing both receptors divided by the total number of clusters. We used the same strategy that we had used for calculating the localization changes: We randomly selected 4 ROIs (regions of interest) per cell to calculate fractions and then calculated the average of three different cells from independently repeated experiments. We did not calculate total numbers of GHR/PRLR. The numbers are fractions of cluster numbers.

Moreover, the reviewer interprets results in panels B and C that ~80% of PRLR clusters also contain GHR. We assume the reviewer refers to Basal state. Now, the reviewer’s interpretation is not correct for the following reason: ~80% of clusters have both receptors. How many of the remaining (~20%) clusters have only PRLR or only GHR is not revealed in the panels. Only if 100% of clusters have PRLR, we can conclude that 80% of PRLR clusters also contain GHR.

Also, while Figures 1 and 2 show localization based on dSTORM images, Figure 3 indicates and quantifies co-localization based on proximity ligation assays following DBSCAN analysis using Clus-DoC. We do not think that the results are directly comparable.

Reviewer #3 (Public Review):

(1) The manuscript suffers from a lack of detail, which in places makes it difficult to evaluate the data and would make it very difficult for the results to be replicated by others. In addition, the manuscript would very much benefit from a full discussion of the limitations of the study. For example, the manuscript is written as if there is only one form of the PRLR while the anti-PRLR antibody used for dSTORM would also recognize the intermediate form and short forms 1a and 1b on the T47D cells. Given the very different roles of these other PRLR forms in breast cancer (Dufau, Vonderhaar, Clevenger, Walker and other labs), this limitation should at the very least be discussed. Similarly, the manuscript is written as if Jak2 essentially only signals through STAT5 but Jak2 is involved in multiple other signaling pathways from the multiple PRLRs, including the long form. Also, while there are papers suggesting that PRL can be protective in breast cancer, the majority of publications in this area find that PRL promotes breast cancer. How then would the authors interpret the effect of PRL on GHR in light of all those non-protective results? [Check papers by Hallgeir Rui]

We thank the reviewer for such thoughtful comments. We have added a paragraph in the Discussion section on the limitations of our study, including sole focus on T47D and γ2A-JAK2 cells and lack of PRLR isoform-specific data. Also, we are now mentioning that these isoforms play different roles in breast cancer, citing papers by Dufau, Vonderhaar, Clevenger, and Walker labs.

We did not mean to imply that JAK2 signals only via STAT5 or by only binding the long form. We have made this point clear in the Introduction as well as in our revised Discussion section. Moreover, we have added information and references on JAK2 signaling and PRLR isoform specific signaling.

In our Discussions section we are also mentioning the findings that PRL is promoting breast cancer. We would like to point out that it is well perceivable that PRL is protective in BC by reducing surface hGHR availability but that this effect may depend on JAK2 levels as well as on expression levels of other kinases that competitively bind Box1 and/or Box2 [1]. Besides, could it not be that PRL’s effect is BC stage dependent? In any case, we have emphasized the speculative nature of our statement.

(1) Chhabra, Y., Seiffert, P., Gormal, R.S., et al. Tyrosine kinases compete for growth hormone receptor binding and regulate receptor mobility and degradation. Cell Rep. 2023;42(5):112490. doi: 10.1016/j.celrep.2023.112490. PMID: 37163374.

Reviewer #3 (Recommendations for the authors):

Points for improvement of the manuscript:

(1) Method details -

a) "we utilized CRISPR/Cas9 to generate hPRLR knockout T47D cells ......" Exactly how? Nothing is said under methods. Can we be sure that you knocked out the whole gene?

We have addressed this point by adding two new sections on “Generating hGHR knockout and hPRLR knockout T47D cells” and “Design of sgRNAs for hGHR or hPRLR knockout” to the Methods section.

b) Some of the Western blots are missing mol wt markers. How specific are the various antibodies used for Westerns? For example, the previous publications are quoted as providing characterization of the antibodies also seem to use just band cutouts and do not show the full molecular weight range of whole cell extracts blotted. Anti-PRLR antibodies are notoriously bad and so this is important.

There is an antibody referred to in Figure 5 that is not listed under "antibodies" in the methods.

We have modified Figure 5a, showing the entire gel as well as molecular weight markers. As for specificity of our antibodies, we used monoclonal antibodies Anti-GHR-ext-mAB 74.3 and Anti-PRLR-ext-mAB 1.48, which have been previously tested and used. In addition, we did our own control experiments to ensure specificity. We have added some of our many control results as Supplementary Figures S2 and S3.

We thank the reviewer for noticing the missing antibody in the Methods section. We have now added information about this antibody.

c) There is no description of the proximity ligation assay.

We have addressed this by adding a paragraph on PLA in the Methods section.

d) What is the level of expression of GHR, PRLR, and Jak2 in the gamma2A-JAK2 cells compared to the T47D cells? Artifacts of overexpression are always a worry.

γ2A-JAK2 cell series are over-expressing the receptors. That’s the reason we did not only rely on the observation in γ2A-JAK2 cell lines but also did the experiment in T47D cell lines.

e) There are no concentrations given for components of the dSTORM imaging buffer. On line 380, I think the authors mean alternating lasers not alternatively.

Thank you. Indeed, we meant alternating lasers. We are referring to [1] (the protocol we followed) for information on the imaging buffer.

(1) Beggs, R.R., Dean, W.F., Mattheyses, A.L. (2020). dSTORM Imaging and Analysis of Desmosome Architecture. In: Turksen, K. (eds) Permeability Barrier. Methods in Molecular Biology, vol 2367. Humana, New York, NY. https://doi.org/10.1007/7651_2020_325

f) In general, a read-through to determine whether there is enough detail for others to replicate is required. 4% PFA in what? Do you mean PBS or should it be Dulbecco's PBS etc., etc.?

We prepared a 4% PFA in PBS solution. We mean Dulbecco's PBS.

(2) There are no controls shown or described for the dSTORM. For example, non-specific primary antibody and second antibodies alone for non-specific sticking. Do the second antibodies cross-react with the other primary antibody? Is there only one band when blotting whole cell extracts with the GHR antibody so we can be sure of specificity?

We used monoclonal antibodies Anti-GHR-ext-mAB 74.3 and Anti-PRLR-ext-mAB 1.48 (but also tested several other antibodies). While these antibodies have been previously tested and used, we performed additional control experiments to ensure specificity of our primary antibodies and absence of non-specific binding of our secondary antibodies. We have added some of our many control results as Supplementary Figures S2 and S3.

(3) Writing/figures-

a) As discussed in the public review regarding different forms of the PRLR and the presence of other Jak2-dependent signaling

We have added paragraphs on PRLR isoforms and other JAK2-dependent signaling pathways to the Introduction. Also, we have added a paragraph on PRLR isoforms (in the context of our findings) to the Discussion section.

b) What are the units for figure 3c and d?

The figures show numbers of localizations (obtained from fluorophore blinking events). In the figure caption to 3C and 3D, we have specified the unit (i.e. counts).

c) The wheat germ agglutinin stains more than the plasma membrane and so this sentence needs some adjustment.

We thank the reviewer for this comment. We have rephrased this sentence (see caption to Fig. 4).

d) It might be better not to use the term "downregulation" since this is usually associated with expression and not internalization.

While we understand the reviewer’s discomfort with the use of the word “downregulation”, we still think that it best describes the observed effect. Moreover, we would like to note that in the field of receptorology “downregulation” is a specific term for trafficking of cell surface receptors in response to ligands. That said, to address the reviewer’s comment, we are now using the terms “cell surface downregulation” or “downregulation of cell surface [..] receptor” throughout the manuscript in order to explicitly distinguish it from gene downregulation.

e) Line 420 talks about "previous work", a term that usually indicates work from the same lab. My apologies if I am wrong, but the reference doesn't seem to be associated with the authors.

At the end of the sentence containing the phrase “previous work”, we are referring to reference [57], which has Dr. Stuart Frank as senior and corresponding author. Dr. Frank is also a co-corresponding author on this manuscript. While in our opinion, “previous work” does not imply some sort of ownership, we are happy to confirm that one of us was responsible for the work we are referencing.

Reviewing Editor's recommendations:

The reviewers have all provided a very constructive assessment of the work and offered many useful suggestions to improve the manuscript. I'd advise thinking carefully about how many of these can be reasonably addressed. Most will not require further experiments. I consider it essential to improve the methods to ensure others could repeat the work. This includes adding methods for the PLA and including detail about the controls for the dSTORM. The reviewers have offered suggestions about types of controls to include if these have not already been done.

We thank the editor for their recommendations. We have revised the methods section, which now includes a paragraph on PLA as well as on CRISPR/Cas9-based generation of mutant cell lines. We have also added information on the dSTORM buffer to the manuscript. Data of controls indicating antibody specificity (using confocal microscopy) have been added to the manuscript’s supplementary material (see Fig. S2 and S3).

I agree with the reviewers that the different isoforms of the prolactin receptor need to be considered. I think this could be done as an acknowledgment and point of discussion.

We have revised the discussions section and have added a paragraph on the different PRLR isoforms, among others.

For Figure 2E, make it clear in the figure (or at least in legend) that the middle line is the basal condition.

We thank the editor for their comment. We have made changes to Fig 2E and have added a sentence to the legend making it clear that the middle depicts the basal condition.

My biggest concern overall was the fact that this is all largely conducted in a single cell line. This was echoed by at least one of the reviewers. I wonder if you have replicated this in other breast cancer cell lines or mammary epithelial cells? I don't think this is necessary for the current manuscript but would increase confidence if available.

We thank the editor for their comment and fully agree with their assessment. Unfortunately, we have not replicated these experiments in other BC cell lines nor mammary epithelial cells but would certainly want to do so in the near future.

eLife Assessment

In their valuable study, Lee et al. explore a role for the Hippo signaling pathway, specifically wts-1/LATS and the downstream regulator yap, in age-dependent neurodegeneration and microtubule dynamics using C. elegans mechanosensory neurons as a model. The authors demonstrate that disruption of wts-1/LATS leads to age-associated morphological and functional neuronal abnormalities, linked to enhanced microtubule stabilization, and show a genetic connection between yap and microtubule stability. Overall, the study employs robust genetic and molecular approaches to reveal a convincing link between the Hippo pathway, microtubule dynamics, and neurodegeneration.

Joint Public Review:

The Lee et al. study has been revised in response to reviewer comments. It presents a valuable investigation into the role of the Hippo signaling pathway (specifically wts-1/LATS and yap) in age-dependent neurodegeneration and microtubule dynamics in C. elegans TRNs. The authors convincingly demonstrated that disruption of wts-1/LATS leads to age-associated neuronal abnormalities and enhanced microtubule stabilization, with a genetic link to yap. While the study was praised for its well-conducted and well-controlled approaches, reviewers raised concerns about the specificity of the Hippo pathway's effects to TRNs, the correlation of Hpo signaling decline in TRNs with age, and the mechanistic link between Hpo-mediated gene expression and microtubule regulation. The authors addressed the TRN specificity by suggesting the unique microtubule structure of these neurons might contribute to their susceptibility. They acknowledged the difficulty in detecting Hpo signaling decline specifically in aged TRNs but noted increased YAP-1 nuclear localization in other tissues. Importantly, the authors provided evidence suggesting that YAP-TEAD-mediated transcriptional regulation is responsible for neuronal degeneration, as loss of yap-1 or egl-44 restored the wts-1 mutant phenotype. However, the specific transcriptional targets of YAP-1 regulating microtubule stability remain unidentified, representing a key limitation. The authors also discussed the possibility of non-cell-autonomous effects of YAP-1 and offered explanations for the seemingly moderate impairment of the touch response despite structural damage. Finally, they attributed the shorter lifespan of wts-1 and wts-1; yap-1 mutants to roles of wts-1 beyond TRNs and potential synergistic effects of yap-1. Overall, the study provides significant insights into the Hippo pathway's role in neuronal aging and microtubule dynamics, while acknowledging remaining mechanistic gaps.

eLife Assessment

This important study aims to understand the function of ProSAP-interacting protein 1 (Prosapip1) in the brain. Using a conditional Prosapip1 KO mouse (floxed prosapip1 crossed with Syn1-Cre line), the authors performed analysis including protein biochemistry, synaptic physiology, and behavioral learning. Convincing evidence from this study supports a role of Prosapip 1 in synaptic protein composition, synaptic NMDA responses, LTP, and spatial memory.

Reviewer #1 (Public review):

Summary:

Summary of what author's were trying to achieve: In the manuscript by Hoisington et al., the authors utilized a novel conditional neuronal prosap2-interacting protein 1 (Prosapip1) knockout mouse to delineate the effects of both neuronal and dorsal hippocampal (dHP)-specific knockout of Prosapip1 impacts biochemical and electrophysiological neuroadaptations within the dHP that may mediate behaviors associated with this brain region.

Strengths:

(1) Methodological Strengths

a) The generation and use of a conditional neuronal knockout of Prosapip1 is a strength. These mice will be useful for anyone interested in studying or comparing and contrasting the effects of loss of Prosapip1 in different brain regions or in non-neuronal tissues.<br /> b) The use of biochemical, electrophysiological, and behavioral approaches are a strength. By providing data across multiple domains, a picture begins to emerge about the mechanistic role for Prosapip1. While questions still remain, the use of the 3 domains is a strength.<br /> c) The use of both global, constitutive neuronal loss of Prosapip1 and postnatal dHP-specific knockout of Prosapip1 help support and validate the behavioral conclusions.

(2) Strengths of the results

a) It is interesting that loss of Prosapip1 leads to specific alterations in the expression of GluN2B and PSD95 but not GluA1 or GluN2A in a post homogenization fraction that the author's term a "synaptic" fraction. Therefore, these results suggest protein-specific modulation of glutamatergic receptors within a "synaptic" fraction.<br /> b) The electrophysiological data demonstrate an NMDAR-dependent alteration in measures of hippocampal synaptic plasticity, including long-term potentiation (LTP) and NMDAR input/output. These data correspond with the biochemical data demonstrating a biochemical effect on GluN2B localization. Therefore, the conclusion that loss of Prosapip1 influences NMDAR function is well supported.<br /> c) The behavioral data suggest deficits in memory in particular novel object recognition and spatial memory, in the Prosapip1 knockout mice. These data are strongly bolstered by both the pan neuronal knockout and the dHP Cre transduction.

The authors highlight potential future studies to further the understanding of Prosapip1.

Reviewer #2 (Public review):

The authors provide valuable findings characterizing a Prosapip1 conditional knockout mouse and the effects of knockout on hippocampal excitatory transmission, NMDAR transmission, and several learning behaviors. Furthermore, the authors selectively and conditionally knockout Prosapip1 in the dorsal hippocampus and show that it is required for the same spatial learning and memory assessed in the conditional knockout mice. The study uncovers how Prosapip1 is involved PSD organization and is a functional and critical player in dorsal Hippocampal LTP via its interaction with GluN2B subunits. The study is well controlled, detailed, and data in the paper match the conclusions.

Comments on revisions:

The authors have addressed all concerns.

eLife Assessment

This valuable study investigates how the neural representation of individual finger movements changes during the early period of sequence learning. By combining a new method for extracting features from human magnetoencephalography data and decoding analyses, the authors provide incomplete evidence of an early, swift change in the brain regions correlated with sequence learning, including a set of previously unreported frontal cortical regions. The addition of more control analyses to rule out that head movement artefacts influence the findings, and to further explain the proposal of offline contextualization during short rest periods as the basis for improvement performance would strengthen the manuscript.

Reviewer #1 (Public review):

Summary:

This study addresses the issue of rapid skill learning and whether individual sequence elements (here: finger presses) are differentially represented in human MEG data. The authors use a decoding approach to classify individual finger elements, and accomplish an accuracy of around 94%. A relevant finding is that the neural representations of individual finger elements dynamically change over the course of learning. This would be highly relevant for any attempts to develop better brain machine interfaces - one now can decode individual elements within a sequence with high precision, but these representations are not static but develop over the course of learning.

Strengths:

The work follows a large body of work from the same group on the behavioural and neural foundations of sequence learning. The behavioural task is well established a neatly designed to allow for tracking learning and how individual sequence elements contribute. The inclusion of short offline rest periods between learning epochs has been influential because it has revealed that a lot, if not most of the gains in behaviour (ie speed of finger movements) occur in these so-called micro-offline rest periods.

The authors use a range of new decoding techniques, and exhaustively interrogate their data in different ways, using different decoding approaches. Regardless of the approach, impressively high decoding accuracies are observed, but when using a hybrid approach that combines the MEG data in different ways, the authors observe decoding accuracies of individual sequence elements from the MEG data of up to 94%.

Weaknesses:

A formal analysis and quantification of how head movement may have contributed to the results should be included in the paper or supplemental material. The type of correlated head movements coming from vigorous key presses aren't necessarily visible to the naked eye, and even if arms etc are restricted, this will not preclude shoulder, neck or head movement necessarily; if ICA was conducted, for example, the authors are in the position to show the components that relate to such movement; but eye-balling the data would not seem sufficient. The related issue of eye movements is addressed via classifier analysis. A formal analysis which directly accounts for finger/eye movements in the same analysis as the main result (ie any variance related to these factors) should be presented.

This reviewer recommends inclusion of a formal analysis that the intra-vs inter parcels are indeed completely independent. For example, the authors state that the inter-parcel features reflect "lower spatially resolved whole-brain activity patterns or global brain dynamics". A formal quantitative demonstration that the signals indeed show "complete independence" (as claimed by the authors) and are orthogonal would be helpful

Reviewer #2 (Public review):

Summary:

The current paper consists of two parts. The first part is the rigorous feature optimization of the MEG signal to decode individual finger identity performed in a sequence (4-1-3-2-4; 1~4 corresponds to little~index fingers of the left hand). By optimizing various parameters for the MEG signal, in terms of (i) reconstructed source activity in voxel- and parcel-level resolution and their combination, (ii) frequency bands, and (iii) time window relative to press onset for each finger movement, as well as the choice of decoders, the resultant "hybrid decoder" achieved extremely high decoding accuracy (~95%). This part seems driven almost by pure engineering interest in gaining as high decoding accuracy as possible.<br /> In the second part of the paper, armed with the successful 'hybrid decoder,' the authors asked more scientific questions about how neural representation of individual finger movement that is embedded in a sequence, changes during a very early period of skill learning and whether and how such representational change can predict skill learning. They assessed the difference in MEG feature patterns between the first and the last press 4 in sequence 41324 at each training trial and found that the pattern differentiation progressively increased over the course of early learning trials. Additionally, they found that this pattern differentiation specifically occurred during the rest period rather than during the practice trial. With a significant correlation between the trial-by-trial profile of this pattern differentiation and that for accumulation of offline learning, the authors argue that such "contextualization" of finger movement in a sequence (e.g., what-where association) underlies the early improvement of sequential skill. This is an important and timely topic for the field of motor learning and beyond.

Strengths:

Each part has its own strength. For the first part, the use of temporally rich neural information (MEG signal) has a significant advantage over previous studies testing sequential representations using fMRI. This allowed the authors to examine the earliest period (= the first few minutes of training) of skill learning with finer temporal resolution. Through the optimization of MEG feature extraction, the current study achieved extremely high decoding accuracy (approx. 94%) compared to previous works. For the second part, the finding of the early "contextualization" of the finger movement in a sequence and its correlation to early (offline) skill improvement is interesting and important. The comparison between "online" and "offline" pattern distance is a neat idea.

Weaknesses:

Despite the strengths raised, the specific goal for each part of the current paper, i.e., achieving high decoding accuracy and answering the scientific question of early skill learning, seems not to harmonize with each other very well. In short, the current approach, which is solely optimized for achieving high decoding accuracy, does not provide enough support and interpretability for the paper's interesting scientific claim. This reminds me of the accuracy-explainability tradeoff in machine learning studies (e.g., Linardatos et al., 2020). More details follow.

There are a number of different neural processes occurring before and after a key press, such as planning of upcoming movement and ahead around premotor/parietal cortices, motor command generation in primary motor cortex, sensory feedback related processes in sensory cortices, and performance monitoring/evaluation around the prefrontal area. Some of these may show learning-dependent change and others may not.

Given the use of whole-brain MEG features with a wide time window (up to ~200 ms after each key press) under the situation of 3~4 Hz (i.e., 250~330 ms press interval) typing speed, these different processes in different brain regions could have contributed to the expression of the "contextualization," making it difficult to interpret what really contributed to the "contextualization" and whether it is learning related. Critically, the majority of data used for decoder training has the chance of such potential overlap of signal, as the typing speed almost reached a plateau already at the end of the 11th trial and stayed until the 36th trial. Thus, the decoder could have relied on such overlapping features related to the future presses. If that is the case, a gradual increase in "contextualization" (pattern separation) during earlier trials makes sense, simply because the temporal overlap of the MEG feature was insufficient for the earlier trials due to slower typing speed.

Several direct ways to address the above concern, at the cost of decoding accuracy to some degree, would be either using the shorter temporal window for the MEG feature or training the model with the early learning period data only (trials 1 through 11) to see if the main results are unaffected would be some example.

Reviewer #3 (Public review):

Summary:

One goal of this paper is to introduce a new approach for highly accurate decoding of finger movements from human magnetoencephalography data via dimension reduction of a "multi-scale, hybrid" feature space. Following this decoding approach, the authors aim to show that early skill learning involves "contextualization" of the neural coding of individual movements, relative to their position in a sequence of consecutive movements. Furthermore, they aim to show that this "contextualization" develops primarily during short rest periods interspersed with skill training, and correlates with a performance metric which the authors interpret as an indicator of offline learning.

Strengths:

A strength of the paper is the innovative decoding approach, which achieves impressive decoding accuracies via dimension reduction of a "multi-scale, hybrid space". This hybrid-space approach follows the neurobiologically plausible idea of concurrent distribution of neural coding across local circuits as well as large-scale networks. A further strength of the study is the large number of tested dimension reduction techniques and classifiers.

Weaknesses:

A clear weakness of the paper lies in the authors' conclusions regarding "contextualization". Several potential confounds, which partly arise from the experimental design (mainly the use of a single sequence) and which are described below, question the neurobiological implications proposed by the authors, and provide a simpler explanation of the results. Furthermore, the paper follows the assumption that short breaks result in offline skill learning, while recent evidence, described below, casts doubt on this assumption.

Specifically:<br /> The authors interpret the ordinal position information captured by their decoding approach as a reflection of neural coding dedicated to the local context of a movement (Figure 4). One way to dissociate ordinal position information from information about the moving effectors is to train a classifier on one sequence, and test the classifier on other sequences that require the same movements, but in different positions (Kornysheva et al., Neuron 2019). In the present study, however, participants trained to repeat a single sequence (4-1-3-2-4). As a result, ordinal position information is potentially confounded by the fixed finger transitions around each of the two critical positions (first and fifth press). Across consecutive correct sequences, the first keypress in a given sequence was always preceded by a movement of the index finger (=last movement of the preceding sequence), and followed by a little finger movement. The last keypress, on the other hand, was always preceded by a ring finger movement, and followed by an index finger movement (=first movement of the next sequence). Figure 4 - supplement 2 shows that finger identity can be decoded with high accuracy (>70%) across a large time window around the time of the keypress, up to at least {plus minus}100 ms (and likely beyond, given that decoding accuracy is still high at the boundaries of the window depicted in that figure). This time window approaches the keypress transition times in this study. Given that distinct finger transitions characterized the first and fifth keypress, the classifier could thus rely on persistent (or "lingering") information from the preceding finger movement, and/or "preparatory" information about the subsequent finger movement, in order to dissociate the first and fifth keypress. Currently, the manuscript provides little evidence that the context information captured by the decoding approach is more than a by-product of temporally extended, and therefore overlapping, but independent neural representations of consecutive keypresses that are executed in close temporal proximity - rather than a neural representation dedicated to context.<br /> During the review process, the authors pointed out that a "mixing" of temporally overlapping information from consecutive keypresses, as described above, should result in systematic misclassifications and therefore be detectable in the confusion matrices in Figures 3C and 4B, which indeed do not provide any evidence that consecutive keypresses are systematically confused. However, such absence of evidence (of systematic misclassification) should be interpreted with caution, and, of course, provides no evidence of absence. The authors also pointed out that such "mixing" would hamper the discriminability of the two ordinal positions of the index finger, given that "ordinal position 5" is systematically followed by "ordinal position 1". This is a valid point which, however, cannot rule out that "contextualization" nevertheless reflects the described "mixing".

During the review process, the authors responded to my concern that training of a single sequence introduces the potential confound of "mixing" described above, which could have been avoided by training on several sequences, as in Kornysheva et al. (Neuron 2019), by arguing that Day 2 in their study did include control sequences. However, the authors' findings regarding these control sequences are fundamentally different from the findings in Kornysheva et al. (2019), and do not provide any indication of effector-independent ordinal information in the described contextualization - but, actually, the contrary. In Kornysehva et al. (Neuron 2019), ordinal, or positional, information refers purely to the rank of a movement in a sequence. In line with the idea of competitive queuing, Kornysheva et al. (2019) have shown that humans prepare for a motor sequence via a simultaneous representation of several of the upcoming movements, weighted by their rank in the sequence. Importantly, they could show that this gradient carries information that is largely devoid of information about the order of specific effectors involved in a sequence, or their timing, in line with competitive queuing. They showed this by training a classifier to discriminate between the five consecutive movements that constituted one specific sequence of finger movements (five classes: 1st, 2nd, 3rd, 4th, 5th movement in the sequence) and then testing whether that classifier could identify the rank (1st, 2nd, 3rd, etc) of movements in another sequence, in which the fingers moved in a different order, and with different timings. Importantly, this approach demonstrated that the graded representations observed during preparation were largely maintained after this cross-decoding, indicating that the sequence was represented via ordinal position information that was largely devoid of information about the specific effectors or timings involved in sequence execution. This result differs completely from the findings in the current manuscript. Dash et al. report a drop in detected ordinal position information (degree of contextualization in figure 5C) when testing for contextualization in their novel, untrained sequences on Day 2, indicating that context and ordinal information as defined in Dash et al. is not at all devoid of information about the specific effectors involved in a sequence. In this regard, a main concern in my public review, as well as the second reviewer's public review, is that Dash et al. cannot tell apart, by design, whether there is truly contextualization in the neural representation of a sequence (which they claim), or whether their results regarding "contextualization" are explained by what they call "mixing" in their author response, i.e., an overlap of representations of consecutive movements, as suggested as an alternative explanation by Reviewer 2 and myself.

Such temporal overlap of consecutive, independent finger representations may also account for the dynamics of "ordinal coding"/"contextualization", i.e., the increase in 2-class decoding accuracy, across Day 1 (Figure 4C). As learning progresses, both tapping speed and the consistency of keypress transition times increase (Figure 1), i.e., consecutive keypresses are closer in time, and more consistently so. As a result, information related to a given keypress is increasingly overlapping in time with information related to the preceding and subsequent keypresses. The authors seem to argue that their regression analysis in Figure 5 - figure supplement 3 speaks against any influence of tapping speed on "ordinal coding" (even though that argument is not made explicitly in the manuscript). However, Figure 5 - figure supplement 3 shows inter-individual differences in a between-subject analysis (across trials, as in panel A, or separately for each trial, as in panel B), and, therefore, says little about the within-subject dynamics of "ordinal coding" across the experiment. A regression of trial-by-trial "ordinal coding" on trial-by-trial tapping speed (either within-subject, or at a group-level, after averaging across subjects) could address this issue. Given the highly similar dynamics of "ordinal coding" on the one hand (Figure 4C), and tapping speed on the other hand (Figure 1B), I would expect a strong relationship between the two in the suggested within-subject (or group-level) regression. Furthermore, learning should increase the number of (consecutively) correct sequences, and, thus, the consistency of finger transitions. Therefore, the increase in 2-class decoding accuracy may simply reflect an increasing overlap in time of increasingly consistent information from consecutive keypresses, which allows the classifier to dissociate the first and fifth keypress more reliably as learning progresses, simply based on the characteristic finger transitions associated with each. In other words, given that the physical context of a given keypress changes as learning progresses - keypresses move closer together in time, and are more consistently correct - it seems problematic to conclude that the mental representation of that context changes. To draw that conclusion, the physical context should remain stable (or any changes to the physcial context should be controlled for).

A similar difference in physical context may explain why neural representation distances ("differentiation") differ between rest and practice (Figure 5). The authors define "offline differentiation" by comparing the hybrid space features of the last index finger movement of a trial (ordinal position 5) and the first index finger movement of the next trial (ordinal position 1). However, the latter is not only the first movement in the sequence, but also the very first movement in that trial (at least in trials that started with a correct sequence), i.e., not preceded by any recent movement. In contrast, the last index finger of the last correct sequence in the preceding trial includes the characteristic finger transition from the fourth to the fifth movement. Thus, there is more overlapping information arising from the consistent, neighbouring keypresses for the last index finger movement, compared to the first index finger movement of the next trial. A strong difference (larger neural representation distance) between these two movements is, therefore, not surprising, given the task design, and this difference is also expected to increase with learning, given the increase in tapping speed, and the consequent stronger overlap in representations for consecutive keypresses. Furthermore, initiating a new sequence involves pre-planning, while ongoing practice relies on online planning (Ariani et al., eNeuro 2021), i.e., two mental operations that are dissociable at the level of neural representation (Ariani et al., bioRxiv 2023).

A further complication in interpreting the results stems from the visual feedback that participants received during the task. Each keypress generated an asterisk shown above the string on the screen. It is not clear why the authors introduced this complicating visual feedback in their task, besides consistency with their previous studies. The resulting systematic link between the pattern of visual stimulation (the number of asterisks on the screen) and the ordinal position of a keypress makes the interpretation of "contextual information" that differentiates between ordinal positions difficult. During the review process, the authors reported a confusion matrix from a classification of asterisks position based on eye tracking data recorded during the task, and concluded that the classifier performed at chance level and gaze was, thus, apparently not biased by the visual stimulation. However, the confusion matrix showed a huge bias that was difficult to interpret (a very strong tendency to predict one of the five asterisk positions, despite chance-level performance). Without including additional information for this analysis (or simply the gaze position as a function of the number of astersisk on the screen) in the manuscript, this important control anaylsis cannot be properly assessed, and is not available to the public.

The authors report a significant correlation between "offline differentiation" and cumulative micro-offline gains. However, this does not address the question whether there is a trial-by-trial relation between the degree of "contextualization" and the amount of micro-offline gains - i.e., the question whether performance changes (micro-offline gains) are less pronounced across rest periods for which the change in "contextualization" is relatively low. The single-subject correlation between contextualization changes "during" rest and micro-offline gains (Figure 5 - figure supplement 4) addresses this question, however, the critical statistical test (are correlation coefficients significantly different from zero) is not included. Given the displayed distribution, it seems unlikely that correlation coefficients are significantly above zero.

The authors follow the assumption that micro-offline gains reflect offline learning. However, there is no compelling evidence in the literature, and no evidence in the present manuscript, that micro-offline gains (during any training phase) reflect offline learning. Instead, emerging evidence in the literature indicates that they do not (Das et al., bioRxiv 2024), and instead reflect transient performance benefits when participants train with breaks, compared to participants who train without breaks, however, these benefits vanish within seconds after training if both groups of participants perform under comparable conditions (Das et al., bioRxiv 2024). During the review process, the authors argued that differences in the design between Das et al. (2024) on the one hand (Experiments 1 and 2), and the study by Bönstrup et al. (2019) on the other hand, may have prevented Das et al. (2024) from finding the assumed (lasting) learning benefit by micro-offline consolidation. However, the Supplementary Material of Das et al. (2024) includes an experiment (Experiment S1) whose design closely follows the early learning phase of Bönstrup et al. (2019), and which, nevertheless, demonstrates that there is no lasting benefit of taking breaks for the acquired skill level, despite the presence of micro-offline gains.

Along these lines, the authors' claim, based on Bönstrup et al. 2020, that "retroactive interference immediately following practice periods reduces micro-offline learning", is not supported by that very reference. Citing Bönstrup et al. (2020), "Regarding early learning dynamics (trials 1-5), we found no differences in microscale learning parameters (micro-online/offline) or total early learning between both interference groups." That is, contrary to Dash et al.'s current claim, Bönstrup et al. (2020) did not find any retroactive interference effect on the specific behavioral readout (micro-offline gains) that the authors assume to reflect consolidation.

The authors conclude that performance improves, and representation manifolds differentiate, "during" rest periods (see, e.g., abstract). However, micro-offline gains (as well as offline contextualization) are computed from data obtained during practice, not rest, and may, thus, just as well reflect a change that occurs "online", e.g., at the very onset of practice (like pre-planning) or throughout practice (like fatigue, or reactive inhibition). That is, the definition of micro-offline gains (as well as offline contextualization) conflates online and "offline" processes. This becomes strikingly clear in the recent Nature paper by Griffin et al. (2025), who computed micro-offline gains as the difference in average performance across the first five sequences in a practice period (a block, in their terminology) and the last five sequences in the previous practice period. Averaging across sequences in this way minimises the chance to detect online performance changes, and inflates changes in performance "offline". The problem that "offline" gains (or contextualization) is actually computed from data entirely generated online, and therefore subject to processes that occur online, is inherent in the very definition of micro-offline gains, whether, or not, they computed from averaged performance.

A simple control analysis based on shuffled class labels could lend further support to the authors' complex decoding approach. As a control analysis that completely rules out any source of overfitting, the authors could test the decoder after shuffling class labels. Following such shuffling, decoding accuracies should drop to chance-level for all decoding approaches, including the optimized decoder. This would also provide an estimate of actual chance-level performance (which is informative over and beyond the theoretical chance level). During the review process, the authors reported this analysis to the reviewers. Given that readers may consider following the presented decoding approach in their own work, it would have been important to include that control analysis in the manuscript to convince readers of its validity.

Furthermore, the authors' approach to cortical parcellation raises questions regarding the information carried by varying dipole orientations within a parcel (which currently seems to be ignored?) and the implementation of the mean-flipping method (given that there are two dimensions - space and time - it is unclear what the authors refer to when they talk about the sign of the "average source", line 477).

eLife Assessment

This work investigates the functional difference between the most commonly expressed form of PTH, and a mutant form of PTH, identified in a patient with chronic hypocalcemia and hyperphosphatemia which characterizes hypoparathyroidism. The authors investigate the hypothesis that this mutant PTH assumes a dimeric form in vivo and serves anabolic functions in the bone. The data are compelling and the translational aspects are fundamental in understanding PTH-1 Receptor activation.

Reviewer #1 (Public review):

Summary:

In this work, the authors investigate the functional difference between the most commonly expressed form of PTH, and a novel point mutation in PTH identified in a patient with chronic hypocalcemia and hyperphosphatemia. The value of this mutant form of PTH as a potential anabolic agent for bone is investigated alongside PTH(1-84), which is a current anabolic therapy. The authors have achieved the aims of the study.

Strengths:

The work is novel, as it describes the function of a novel, naturally occurring, variant of PTH in terms of its ability to dimerise, to lead to cAMP activation, to increase serum calcium, and its pharmacological action compared to normal PTH.

Comments on revisions: No further recommendations for revisions. Acceptable as the paper stands.

[Editors' note: the original reviews are here, https://doi.org/10.7554/eLife.97579.1.sa1]

Author response:

The following is the authors’ response to the previous reviews.

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this work, the authors investigate the functional difference between the most commonly expressed form of PTH, and a novel point mutation in PTH identified in a patient with chronic hypocalcemia and hyperphosphatemia. The value of this mutant form of PTH as a potential anabolic agent for bone is investigated alongside PTH(1-84), which is a current anabolic therapy. The authors have achieved the aims of the study.

Strengths:

The work is novel, as it describes the function of a novel, naturally occurring, variant of PTH in terms of its ability to dimerise, to lead to cAMP activation, to increase serum calcium, and its pharmacological action compared to normal PTH.

Recommendations for the authors:

(1) In your response to the reviewers you included a figure. You said it was for the reviewers only. We are *not* including it here. Is that correct or should it be in the Public Reviews?

We apologize for any confusion and appreciate your thorough review. The phrase “data only for reviewers” was intended to indicate that the content was included in the revision based on reviewers’ comments, not in the main text (article). However, we acknowledge that this phrasing may be inappropriate. We are agree to make the figure included in the previous author response of the public reviews. Accordingly, we propose to revise the previous author response as follows:

- Remove "(data only for reviewers)".

-  Correct the typo from "perosteal" to "periosteal".

- “Thank you for your comment. First, we ensured that the bones sampled during the experiment showed no defects, and we carefully separated the femur bones from the mice to preserve their integrity. In the 3-point bending test, PTH treatment significantly increased the maximum load of the femur bone compared to the OVX-control group. Additionally, the maximum load in the PTH treatment group was significantly greater than that observed in the PTH dimer group. Furthermore, structural factors influencing bone strength, such as the periosteal perimeter and the endocortical bone perimeter, were also increased in the PTH treatment group compared to the PTH dimer group.”

(2) Do you mean to always have R⁰ (have a superscript) and RG (never have a superscript) or should they be shown in the same way throughout your paper?

Thank you for your thorough review. Based on previous studies that addressed the conformation of PTH1R, R⁰ is typically shown with a superscript, while RG is not (Hoare et al., 2001; Dean et al., 2006; Okazaki et al., 2008). We have followed this notation and will ensure consistency throughout our paper.

Hoare, S. R., Gardella, T. J., & Usdin, T. B. (2001). Evaluating the signal transduction mechanism of the parathyroid hormone 1 receptor: effect of receptor-G-protein interaction on the ligand binding mechanism and receptor conformation. Journal of Biological Chemistry, 276(11), 7741-7753.

Dean, T., Linglart, A., Mahon, M. J., Bastepe, M., Jüppner, H., Potts Jr, J. T., & Gardella, T. J. (2006). Mechanisms of ligand binding to the parathyroid hormone (PTH)/PTH-related protein receptor: selectivity of a modified PTH (1–15) radioligand for GαS-coupled receptor conformations. Molecular endocrinology, 20(4), 931-943.

Okazaki, M., Ferrandon, S., Vilardaga, J. P., Bouxsein, M. L., Potts Jr, J. T., & Gardella, T. J. (2008). Prolonged signaling at the parathyroid hormone receptor by peptide ligands targeted to a specific receptor conformation. Proceedings of the National Academy of Sciences, 105(43), 16525-16530.

(3) The following grammatical and fact changes and word changes are requested.

We appreciate the thoughtful review and thank you for pointing out the grammatical, factual, and word changes required. We have carefully reviewed and addressed each of these corrections to ensure the paper's accuracy and readability.

We appreciate the reviewers' detailed and constructive reviews. We have addressed all the comments to improve the quality of our paper.

eLife Assessment

Catani and colleagues provide data on antigenic properties of neuraminidase proteins of pandemic H1N1 and show that antigenic diversity of the neuraminidase from 2009 to 2020 largely falls into two groups. These antigenic groups map to two phylogenetic groups, and substitutions at positions 432 and 321 are likely associated with the antigenic change. These data and results allow useful insights into the antigenic properties of N1 influenza and the evidence supporting the conclusions is solid.

Reviewer #1 (Public review):

Summary:

In this paper, the authors have performed an antigenic assay for human seasonal N1 neuraminidase using antigens and mouse sera from 2009-2020 (with one avian N1 antigen). This shows two distinct antigen groups. There is poorer reactivity with sera from 2009-2012 against antigens from 2015-2019, and poorer reactivity with sera from 2015-2020 against antigens from 2009-2013. There is a long branch separating these two groups. However, 321 and 423 are the only two positions that are consistently different between the two groups. Therefore these are the most likely cause of these antigenic differences.

Strengths:

(1) A sensible rationale was given for the choice of sera, in terms of the genetic diversity.

(2) There were two independent batches of one of the antigens used for generating sera, which demonstrated the level of heterogeneity in the experimental process.

(3) Replicate of the Wisconsin/588/2019 antigen (as H1 and H6) is another useful measure of heterogeneity.

(4) The presentation of the data, e.g. Figure 2, clearly shows two main antigenic groups.

(5) The most modern sera are more recent than other related papers, which demonstrates that has been no major antigenic change.

Weaknesses:

(1) Issues with experimental methods<br /> As I am not an experimentalist, I cannot comment fully on the experimental methods. However, I note that BALB/c mice sera were used, whereas outbred ferret sera are typically used in influenza antigenic characterisation, so the antigenic difference observed may not be relevant in humans. Similarly, the mice were immunised with an artificial NA immunogen where the typical approach would be to infect the ferret with live virus intra-nasally.

(2) Five mice sera were generated per immunogen and then pooled, but data was not presented that demonstrated these sera were sufficiently homogenous that this approach is valid.

(3) There were no homologous antigens for most of the sera. This makes the responses difficult to interpret as the homologous titre is often used to assess the overall reactivity of a serum. The sequence of the antigens used is not described, which again makes it difficult to interpret the results.

(4) To be able to untangle the effects of the individual substitutions at 321, 386, and 432, it would have been useful to have included the naturally occurring variants at these positions, or to have generated mutants at these positions. Gao et al clearly show an antigenic difference with ferret sera correlated separately with N386K and I321V/K432E.

(5) The challenge experiments in Gao et al showed that NI titre was not a good correlate of protection, so that limits the interpretation of these results.

Issues with the computational methods

(6) The NAI titres were normalised using the ELISA results, and the motivation for this is not explained. It would be nice to see the raw values.

(7) It is not clear what value the random forest analysis adds here, given that positions 321 and 432 are the only two that consistently differ between the two groups.

(8) As with the previous N2 paper, the metric for antigenic distance (the root mean square of the difference between the titres for two sera) is not one that would be consistent when different sera are included. More usual metrics of distance are Archetti-Horsfall, fold down from homologous, or fold down from maximum.

(9) Antigenic cartography of these data is fraught. I wonder whether 2 dimensions are required for what seems like a 1-dimensional antigenic difference - certainly, the antigens, excluding the H5N1, are in a line. The map may be skewed by the high reactivity Brisbane/18 antigen. It is not clear if the column bases (normalisation factors for calculating antigenic distance) have been adjusted to account for the lack of homologous antigens. It is typical to present antigenic maps with a 1:1 x:y ratio.

Issues with interpretation

(10) Figure 2 shows the NAI titres split into two groups for the antigens, however, A/Brisbane is an outlier in the second antigenic group with high reactivity.

(11) Following Gao et al, I think you can claim that it is more likely that the antigenic change is due to K432E than I321V, based on a comparison of the amino acid change.

Appraisal:

Taking into account the limitations of the experimental techniques (which I appreciate are due to resource constraints), this paper meets its aim of measuring the antigenic relationships between 2009-2020 seasonal N1s, showing that there were two main groups. The authors discovered that the difference between the two antigenic groups was likely attributable to positions 321 and 432, as these were the only two positions that were consistently different between the two groups. They came to this finding by using a random forest model, but other simpler methods could have been used.

Impact:

This paper contributes to the growing literature on the potential benefit of NA in the influenza vaccine.

Reviewer #2 (Public review):

Summary:

In this study, Catani et al. have immunized mice with 17 recombinant N1 neuraminidases (NAs) from human isolates circulating between 2009-2020 to investigate antigenic diversity. NA inhibition (NAI) titers revealed two groups that were antigenically and phylogenetically distinct. Machine learning was used to estimate the antigenic distances between the N1 NAs and mutations at residues K432E and I321V were identified as key determinants of N1 NA antigenicity.

Strengths:

Observation of mutations associated with N1 antigenic drift.

Weaknesses:

Validation that K432E and I321V are responsible for antigenic drift was not determined in a background strain with native K432 and I321 or the restitution of antibody binding by reversion to K432 and I321 in strains that evaded sera.

eLife Assessment

The study by Chi and colleagues presents important new tools for precise genetic manipulation and lineage tracing in mice. The characterization of these new models was conducted using validated, state-of-the-art methodologies and convincingly demonstrates their ability to enhance the precision of genetic manipulation in distinct cell types. This work will be of great interest to many laboratories worldwide and will facilitate future research across various biomedical disciplines.

Reviewer #1 (Public review):

Summary:

Shi and colleagues report the use of modified Cre lines in which the coding region of Cre is disrupted by rox-STOP-rox or lox-STOP-lox sequences to prevent the expression of functional protein in the absence of Dre or Cre activity, respectively. The main purpose of these tools is to enable intersectional or tamoxifen-induced Cre activity with minimal or no leaky activity from the second, Cre-expressing allele. It is a nice study but lacks some functional data required to determine how useful these alleles will be in practice, especially in comparison with the figure line that stimulated their creation.

Strengths:

The new tools can reduce Cre leak in vivo.

Comments on revisions:

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

Reviewer #2 (Public review):

This work present 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 some 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 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.

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 a considerable value for the scientific community, justifying publication.

It seems very likely that 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 have eradicated weaknesses from the initial submission. One minor issue remains. The authors did not investigate potential toxic effects that might be caused by high level expression of a combination of "foreign" genes such as recombinases and fluorescence reporters. The authors refer to published studies about toxic effects, speculating that they can only be prevented by removing recombinases in an additional step. Although this is a valid argument, I would have appreciated to see an assessment of putative toxic effects by RNA-sequencing, since different combinations of recombinases and fluorescence reporters sometimes can generate unexpected effects. However, this minor issue does not compromise the value of this important study.

eLife Assessment

This important study examined orientation representations along the visual hierarchy during perception and working memory. The authors provide results suggesting that during working memory there is a gradient where representations are more categorical in nature later in the visual hierarchy. The evidence presented is solid, most notably a match between behavioral data, though minor weakness can be attributed to the tasks and behaviors not being designed to address this question. The findings should be of interest to a relatively broad audience, namely those interested in the relationship between sensory coding and memory.

Reviewer #1 (Public review):

Summary:

In this article, Chunharas and colleagues compared the representational differences of orientation information during a sensory task and a working memory task. By reanalyzing data from a previous fMRI study and applying representational similarity analysis (RSA), they observed that orientation information was represented differently in the two tasks: during visual perception, orientation representation resembled the veridical model, which captures the known naturalistic statistics of orientation information; whereas during visual working memory, a categorical model, which assumes different psychological distances between orientations, better explained the data, particularly in more anterior retinotopic regions. The authors suggest fundamental differences in the representational geometry of visual perception and working memory along the human retinotopic cortex.

Strengths:

Examining the differences in representational geometry between perception and working memory has important implications for the understanding of the nature of working memory. This study presents a carefully-executed reanalysis of previous data to address this question. The authors developed a novel method (model construction combined with RSA) to examine the representational geometry of orientation information under different tasks, and the control analyses provide rich, convincing support for their claims.

Weaknesses:

Although the control analyses are convincing, I still have alternative explanations for some of the results. I'm also concerned about the low sample size (n = 6 in the fMRI experiment). Overall, I think additional analyses may help to further clarify the issues and strengthen the claims.

(1) The central claim of the current study is that orientation information is represented in a veridical manner during the sensory task, and in a categorical manner during working memory. However, In the sensory task, a third type of representational geometry was observed, especially in brain regions from V3AB and beyond. These regions showed a symmetric pattern in which oblique orientations (45 and 135 degrees) appeared more similar to each other. In fact, a similar pattern can even be found in V1-V3, although the effect looked weaker. The authors raised two possible explanations for this in the discussion, one being that participants might have used verbal labels (e.g., diagonal) for both orientations, and the other being a lack of attention to orientation. Either way, this suggests that a veridical model may not be the best fit for these ROIs. How would this symmetric model explain the sensory data, in comparison to the veridical model?

(2) If the symmetric model also explains the sensory data well, I wonder whether this result challenges the authors' central claim, or instead suggests that the sensory task is not ideal for the purpose of the study. One way to address this issue might be to use the sample period of the working memory task as the perception task, as some other studies have been doing (e.g., Kwak & Curtis, 2022). This epoch of data might function as a stronger version of the attention task as the authors discussed in the discussion. What would the representational geometry look like in the sample period? I would also like to note that the current analyses used 5.6-13.6 s after stimulus onset for the memory task, which I think may reflect a mix of sample- and delay-related activity.

(3) When comparing the veridical and categorical models, it is important to first show the significance of each model before making comparisons. For instance, was the veridical model significant in different ROIs in the memory task? And was either model significant in IPS1-3 in the two tasks? I'm asking about this because the two models appear to be both significant in the memory task, whereas only the veridical model was significant in the sensory task (with overall lower correlation coefficients than the categorical model in the memory task).

(4) The current study has a low sample size of six participants. With such a small sample, it would be helpful to show results from individual participants. For example, I appreciate that Figures 2D and 3C showed individual data points, but additionally showing the representational geometry plot (i.e., Figure 1C) for each subject could better illustrate the robustness of the effect. Alternatively, the original paper from which the fMRI data were drawn actually had two fMRI experiments with similar task designs. I wonder if the authors could replicate these patterns using data from the second experiment with seven participants. This might provide even stronger support for the current findings with a more reasonable sample size.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors examined the representational geometry of orientation representations during visual perception and working memory along the visual hierarchy. Using representational similarity analysis, they found that similarity was relatively evenly distributed among all orientations during perception, while higher around oblique orientations during WM. There were some noticeable differences along the visual hierarchy. IPS showed the most pronounced oblique orientation preferences during WM but no clear patterns during perception, likely due to the different task demands for the WM orientation task and the perception contrast discrimination task. The authors proposed two models to capture the differences. The veridical model estimated the representational geometry in perception by assuming an efficient coding framework, while the categorical model estimated the pattern in WM using psychological distances to measure the differences among orientations (including estimates from a separate psychophysical study performed outside the scanner). Therefore, I think this work is valuable and advances our understanding of the transition from perception to memory.

Strengths:

The use of RSA to identify representational biases goes beyond simply relying on response patterns and helps identify how representational formats change from perception to WM. The study nicely leverages ideas about efficient coding to explain perceptual representations that are more veridical, while leaning on ideas about abstractions of percepts that are more categorical-psychological in nature (but see (1) below). Moreover, the match between memory biases of orientation and the patterns estimated with RSA were compelling (but see (2) below). I found the analyses showing how RSA and decoding (eg, cross-generalization) are associated and how/why they may differ to be particularly interesting.

Weaknesses:

(1) The idea that later visual maps (ie, IPS0) encode perceptions of orientation in a veridical form and then in a categorical form during WM is an attractive idea. However, the support is somewhat weakened by a few issues. The RSA plots in Figure 1C for IPS0 appear to show a similar pattern, but just of lower amplitude during perception. But in the model fits either for orientation statistics or estimated from the psychophysics task, the Veridical model fits best for perception and the Categorical model fits best for memory in IPS0. By my eye, the modeled RSMs in Figures 2 & 3 do not look like the observed ones in Figure 1C. Those modeled RSMs look way more categorical than the observed IPS0. They look like something in between.

(2) My biggest concern is the omission of the in-scanner behavioral data. Yes, on the one hand, they used the N=17 outside the scanner psychophysics dataset for the analyses in Figure 3. On the other hand, they do not even mention the behavioral data collected in the scanner along with the BOLD data. Those data had clear oblique effects if I recall correctly. Why use the data from the psychophysics experiment? Also, perhaps a missed opportunity; I wonder if the Veridical/Categorical models fit a single subject's RSA data matches that subject's behavioral biases. That would really be compelling if found.

The data were collected (reanalysis of published study) without consideration for the aims of the current study, and are therefore not optimized to test their goals. The biggest issue is that "The distractors are really distracting me." I'm somewhat concerned about how the distractors may have impacted the results. I honestly did not notice that the authors were using delay periods that had 11s of distractor stimuli until way into the paper. On the one hand, the "patterns" of the model fits across the ROIs appear to be qualitatively similar. That's good if you want to pool data like the authors did. But, while the authors state on line 350 "..we also confirmed that the presence of distractors during the delay did not impact the pattern of results in the memory task (Supplementary Figure 5)." When looking at Supplementary Figure 5, I noticed that there are a couple of exceptions to this. In the Gratings distractor data, V1 shows a better fit to the Veridical model, while V4 and IPS0 shows no better fit to either model. And in the Noise distractor data, neither model fits better for any ROI. At first glance, I was concerned, but then looking at the No distractor data, the pattern is identical to that of the combined data. Thus, this can be seen as a glass half full/empty issue as almost all of the ROIs show a similar pattern, but still it would concern me if I were leading this study. This gets me to my key question, why even use the distractor trials at all, where the interpretation can get dicey? For instance, the authors have shown in this exact data that the impact of distraction affects the fidelity of representations differently along the visual hierarchy (Rademaker, 2019), consistent with several other studies (eg., Bettencourt & Xu, 2016; Lorenc, 2018; Hallenbeck et al., 2022) and with one of the author's preprints (Rademaker & Serences, 2024). My guess is that without the full dataset, some of the RSA analyses are underpowered. If that is the case, I'm fine with it, but it might be nice to state that.

eLife Assessment

The songbird vocal motor nucleus HVC contains cells that project to the basal ganglia, the auditory system, or downstream vocal motor structures. In this fundamental study, the authors conduct optogenetic circuit mapping to clarify how four distinct inputs to HVC act on these distinct HVC cell types. They provide compelling evidence that all long-range projections engage inhibitory circuits in HVC and can also exhibit cell-type specific preferences in monosynaptic input strength. Understanding the HVC microcircuit at this microcircuit level is critical for informing models of song learning and production.

Reviewer #1 (Public review):

Summary:

This work tried to map the synaptic connectivity between the inputs and outputs of the song premotor nucleus, HVC in zebra finches to understand how sensory (auditory) to motor circuits interact to coordinate song production and learning. The authors optimized the optogenetic technique via AAV to manipulate auditory inputs from a specific auditory area one-by-one and recorded synaptic activity from a neuron with whole-cell recording from slice preparation with identification of the projection area by retrograde neuronal tracing. This thorough and detailed analysis provides compelling evidence of synaptic connections between 4 major auditory inputs (3 forebrain and 1 thalamic region) within three projection neurons in the HVC; all areas give monosynaptic excitatory inputs and polysynaptic inhibitory inputs, but proportions of projection to each projection neuron varied. They also find specific reciprocal connections between mMAN and Av. Taken together the authors provide the map of the synaptic connection between intercortical sensory to motor areas which is suggested to be involved in zebra finch song production and learning.

Strengths:

The authors optimized optogenetic tools with eGtACR1 by using AAV which allow them to manipulate synaptic inputs in a projection-specific manner in zebra finches. They also identify HVC cell types based on projection area. With their technical advance and thorough experiments, they provided detailed map synaptic connections.

Weaknesses:

As it is the study in brain slice, the functional implication of synaptic connectivity is limited. Especially as all the experiments were done in the adult preparation, there could be a gap in discussing the functions of developmental song learning.

Reviewer #2 (Public review):

Summary:

The manuscript describes synaptic connectivity in the Songbird cortex's four main classes of sensory neuron afferents onto three known classes of projection neurons of the pre-motor cortical region HVC. HVC is a region associated with the generation of learned bird songs. Investigators here use all male zebra finches to examine the functional anatomy of this region using patch clamp methods combined with optogenetic activation of select neuronal groups.

Strengths:

The quality of the recordings is extremely high and the quantity of data is on a very significant scale, this will certainly aid the field.

Weaknesses:

The authors could make the figures a little easier to navigate. Most of the figures use actual anatomical images but it would be nice to have this linked with a zebra finch atlas in more of a cartoon format that accompanied each fluro image. Additionally, for the most part, figures showing the labeling lack scale bar values (in um). These should be added not just shown in the legends.

The authors could make it clear in the abstract that this is all male zebra finches - perhaps this is obvious given the bird song focus, but it should be stated. The number of recordings from each neuron class and the overall number of birds employed should be clearly stated in the methods (this is in the figures, but it should say n=birds or cells as appropriate).

The authors should consider sharing the actual electrophysiology records as data.

Reviewer #3 (Public review):

Nucleus HVC is critical both for song production as well as learning and arguably, sitting at the top of the song control system, is the most critical node in this circuit receiving a multitude of inputs and sending precisely timed commands that determine the temporal structure of song. The complexity of this structure and its underlying organization seem to become more apparent with each experimental manipulation, and yet our understanding of the underlying circuit organization remains relatively poorly understood. In this study, Trusel and Roberts use classic whole-cell patch clamp techniques in brain slices coupled with optogenetic stimulation of select inputs to provide a careful characterization and quantification of synaptic inputs into HVC. By identifying individual projection neurons using retrograde tracer injections combined with pharmacological manipulations, they classify monosynaptic inputs onto each of the three main classes of glutamatergic projection neurons in HVC (RA-, Area X- and Av-projecting neurons). This study is remarkable in the amount of information that it generates, and the tremendous labor involved for each experiment, from the expression of opsins in each of the target inputs (Uva, NIf, mMAN, and Av), the retrograde labelling of each type of projection neuron, and ultimately the optical stimulation of infected axons while recording from identified projection neurons. Taken together, this study makes an important contribution to increasing our identification, and ultimately understanding, of the basic synaptic elements that make up the circuit organization of HVC, and how external inputs, which we know to be critical for song production and learning, contribute to the intrinsic computations within this critic circuit.

This study is impressive in its scope, rigorous in its implementation, and thoughtful regarding its limitations. The manuscript is well-written, and I appreciate the clarity with which the authors use our latest understanding of the evolutionary origins of this circuit to place these studies within a larger context and their relevance to the study of vocal control, including human speech. My comments are minor and primarily about legibility, clarification of certain manipulations, and organization of some of the summary figures.

eLife Assessment

This work presents important findings that the human frontal cortex is involved in a flexible, dual role in both maintaining information in short-term memory, and controlling this memory content to guide adaptive behavior and decisions. The evidence supporting the conclusions is compelling, with a well-designed task, best-practice decoding methods, and careful control analyses. The work will be of broad interest to cognitive neuroscience researchers working on working memory and cognitive control.

Reviewer #1 (Public review):

Summary:

In this manuscript, Shao et al. investigate the contribution of different cortical areas to working memory maintenance and control processes, an important topic involving different ideas about how the human brain represents and uses information when no longer available to sensory systems. In two fMRI experiments, they demonstrate that human frontal cortex (area sPCS) represents stimulus (orientation) information both during typical maintenance, but even more so when a categorical response demand is present. That is, when participants have to apply an added level of decision control to the WM stimulus, sPCS areas encode stimulus information more than conditions without this added demand. These effects are then expanded upon using multi-area neural network models, recapitulating the empirical gradient of memory vs control effects from visual to parietal and frontal cortices. Multiple experiments and analysis frameworks provide support for the authors' conclusions, and control experiments and analysis are provided to help interpret and isolate the frontal cortex effect of interest. While some alternative explanations/theories may explain the roles of frontal cortex in this study and experiments, important additional analyses have been added that help ensure a strong level of support for these results and interpretations.

Strengths:

- The authors use an interesting and clever task design across two fMRI experiments that is able to parse out contributions of WM maintenance alone along with categorical, rule-based decisions. Importantly, the second experiments only uses one fixed rule, providing both an internal replication of Experiment 1's effects and extending them to a different situation when rule switching effects are not involved across mini-blocks.

- The reported analyses using both inverted encoding models (IEM) and decoders (SVM) demonstrate the stimulus reconstruction effects across different methods, which may be sensitive to different aspects of the relationship between patterns of brain activity and the experimental stimuli.

- Linking the multivariate activity patterns to memory behavior is critical in thinking about the potential differential roles of cortical areas in sub-serving successful working memory. Figure 3's nicely shows a similar interaction to that of Figure 2 in the role of sPCS in the categorization vs. maintenance tasks. This is an important contribution to the field when we consider how a distributed set of interacting cortical areas support successful working memory behavior.

- The cross-decoding analysis in Figure 4 is a clever and interesting way to parse out how stimulus and rule/category information may be intertwined, which would have been one of the foremost potential questions or analyses requested by careful readers.

- Additional ROI analyses in more anterior regions of the PFC help to contextualize the main effects of interest in the sPCS (and no effect in the inferior frontal areas, which are also retinotopic, adds specificity). And, more explanation for how motor areas or preparation are likely not involved strengthens the takeaways of the study (M1 control analysis).

- Quantitative link via RDM-style analyses between the RNNs constructed and fMRI data.

Weaknesses:

- In the given tasks, multiple types of information codes may be present, and more detail on this possibility could always be added analytically or in discussion. However, the authors have added beneficial support to this comparison in this version of the manuscript.

- The space of possible RNN architectures and their biological feasibility could always be explored more, but links between the fMRI and RNN data provide a good foundation for this work moving forward.

Reviewer #2 (Public review):

Summary:

The author provide evidence that helps resolve long-standing questions about the differential involvement of frontal and posterior cortex in working memory. They show that whereas early visual cortex shows stronger decoding of memory content in a memorization task vs a more complex categorization task, frontal cortex shows stronger decoding during categorization tasks than memorization tasks. They find that task-optimized RNNs trained to reproduce the memorized orientations show some similarities in neural decoding to people. Together, this paper presents interesting evidence for differential responsibilities of brain areas in working memory.

Strengths:

This paper was overall strong. It had a well-designed task, best-practice decoding methods, and careful control analyses. The neural network modeling adds additional insight into the potential computational roles of different regions.

Weaknesses:

Few. The RNN-fMRI correspondence could be a little more comprehensive, but the paper contributes a compelling set of empirical findings and interpretations that can inform future research.

Author response:

The following is the authors’ response to the previous reviews.

We would like to sincerely thank the reviewers again for their insightful comments on the previous version of our manuscript. In the last round of review, the reviewers were mostly satisfied with our revision but raised a few suggestions and/or remaining concerns. We have further edited the manuscript to address these concerns.

Reviewer #1:

- An explicit, quantitative link between the RNN and fMRI data is perhaps a last point that would integrate the RNN conclusion and analyses in line with the human imaging data.

Reviewer #2:

- Few. While more could be perhaps done to understand the RNN-fMRI correspondence, the paper contributes a compelling set of empirical findings and interpretations that can inform future research.

To better align the RNN and fMRI results qualitatively, we performed an additional representational similarity analysis (RSA) on the data. Specifically, we computed the representational dissimilarity matrices (RDMs) for fMRI and RNN data separately, and calculated the correlation between the RDMs to quantify the similarity between fMRI data and different RNN models. We found that, consistent with our main claims, RNN2 generally demonstrated higher similarity with the fMRI data compared to RNN1. These results provide further support that RNN2 aligns better with human neuroimaging data. We have included this result (lines 496-505) and the corresponding figure (Figure 7) in the manuscript.

Reviewer #1:

- As Rev 2 mentions, multiple types of information codes may be present, and the response letter Figure 5 using representational similarity (RSA) gets at this question. It would strengthen the work to, at minimum, include this analysis as an extended or supplemental figure.

Following this suggestion, we have now included Response Letter Figure 5 from the previous round of review in the manuscript (lines 381-387 and Appendix 1 – figure 7).

Reviewer #1:

- To sum up the results, a possible, brief schematic of each cortical area analyzed and its contribution to information coding in WM and successful subsequent behavior may help readers take away important conclusions of the cortical circuitry involved.

Following this suggestion, we have added a schematic figure illustrating the contribution of each cortical region in our experiment to better summarize our findings (Figure 8).

We hope that these changes further clarify the issues and strengthen the key claims in our manuscript.

eLife Assessment

This study presents a fundamental finding on how levels of m6A levels are controlled, invoking a consolidated model where degradation of modified RNAs in the cytoplasm plays a primary role in shaping m6A patterns and dynamics, rather than needing active regulation by m6A erasers and other related processes. The evidence is compelling through its use of transcriptome-wide data and mechanistic modeling. Relevant for any reader with an interest in RNA metabolism, this new framework consolidates previous observations and highlights the importance of careful experimentation for evaluation m6A levels.

Reviewer #1 (Public review):

Here, the authors propose that changes in m6A levels may be predictable via a simple model that is based exclusively on mRNA metabolic events. Under this model, m6A mRNAs are "passive" victims of RNA metabolic events with no "active" regulatory events needed to modulate their levels by m6A writers, readers, or erasers; looking at changes in RNA transcription, RNA export, and RNA degradation dynamics is enough to explain how m6A levels change over time.

The relevance of this study is extremely high at this stage of the epitranscriptome field. This compelling paper is in line with more and more recent studies showing how m6A is a constitutive mark reflecting overall RNA redistribution events. At the same time, it reminds every reader to carefully evaluate changes in m6A levels if observed in their experimental setup. It highlights the importance of performing extensive evaluations on how much RNA metabolic events could explain an observed m6A change.

Reviewer #2 (Public review):

Dierks et al. investigate the impact of m6A RNA modifications on the mRNA life cycle, exploring the links between transcription, cytoplasmic RNA degradation and subcellular RNA localization. Using transcriptome-wide data and mechanistic modelling of RNA metabolism, the authors demonstrate that a simplified model of m6A primarily affecting cytoplasmic RNA stability is sufficient to explain the nuclear-cytoplasmic distribution of methylated RNAs and the dynamic changes in m6A levels upon perturbation. Based on multiple lines of evidence, they propose that passive mechanisms based on the restricted decay of methylated transcripts in the cytoplasm play a primary role in shaping condition-specific m6A patterns and m6A dynamics. The authors support their hypothesis with multiple large-scale datasets and targeted perturbation experiments. Overall, the authors present compelling evidence for their model which has the potential to explain and consolidate previous observations on different m6A functions, including m6A-mediated RNA export.

Reviewer #3 (Public review):

Summary:

This manuscript works with a hypothesis where the overall m6A methylation levels in cells is influenced by mRNA metabolism (sub-cellular localization and decay). The basic assumption is that m6A causes Mrna decay and this happens in the cytoplasm. They go on to experimentally test their model to confirm its predictions. This is confirmed by sub-cellular fractionation experiments which shows high m6A levels in the nuclear RNA. Nuclear localized RNAs have higher methylation. Using a heat shock model, they demonstrate that RNAs with increased nuclear localization or transcription, are methylated at higher levels. Their overall argument is that changes in m6A levels is rather determined by passive processes that are influenced by RNA processing/metabolism. However, it should be considered that erasers have their roles under specific environments (early embryos or germline) and are not modelled by the cell culture systems used here.

Strengths:

This is a thought-provoking series of experiments that challenge the idea that active mechanisms of recruitment or erasure are major determinants for m6A distribution and levels.

Comments on revisions:

The authors have done a good job with the revision.

eLife Assessment

This valuable study builds on previous work by the authors by presenting a potentially key method for correcting optical aberrations in GRIN lens-based microendoscopes used for imaging deep brain regions. By combining simulations and experiments, the authors provide convincing evidence showing that the obtained field of view is significantly increased with corrected, versus uncorrected microendoscopes. Because the approach described in this paper does not require any microscope or software modifications, it can be readily adopted by neuroscientists who wish to image neuronal activity deep in the brain.

Reviewer #1 (Public review):

Summary:

Sattin, Nardin, and colleagues designed and evaluated corrective microlenses that increase the useable field of view of two long (>6mm) thin (500 um diameter) GRIN lenses used in deep-tissue two-photon imaging. This paper closely follows the thread of earlier work from the same group (esp. Antonini et al, 2020; eLife), filling out the quiver of available extended-field-of-view 2P endoscopes with these longer lenses. The lenses are made by a molding process that appears practical and easy to adopt with conventional two-photon microscopes.

Simulations are used to motivate the benefits of extended field of view, demonstrating that more cells can be recorded, with less mixing of signals in extracted traces, when recorded with higher optical resolution. In vivo tests were performed in piriform cortex, which is difficult to access, especially in chronic preparations.

The design, characterization, and simulations are clear and thorough, but they do not break new ground in optical design or biological application. However, the approach shows much promise, including for applications such as miniaturized GRIN-based microscopes. Readers will largely be interested in this work for practical reasons: to apply the authors' corrected endoscopes to their own research.

Strengths:

The text is clearly written, the ex vivo analysis is thorough and well supported, and the figures are clear. The authors achieved their aims, as evidenced by the images presented, and were able to make measurements from large numbers of cells simultaneously in vivo in a difficult preparation.

The authors did a good job of addressing issues I raised in initial review, including analyses of chromaticity and the axial field of view, descriptions of manufacturing and assembly yield, explanations in the text of differences between ex vivo and in vivo imaging conditions, and basic analysis of the in vivo recordings relative to odor presentations. They have also shortened the text, reduced repetition, and better motivated their approach in the introduction.

Weaknesses:

As discussed in review and nicely simulated by the authors, the large figure error indicated by profilometry (~10 um in some cases on average) is inconsistent with the optical performance improvements observed, suggesting that those measurements are inaccurate. I see no reason to include these inaccurate measurements.

Reviewer #2 (Public review):

In this manuscript, the authors present an approach to correct GRIN lens aberrations, which primarily cause a decrease in signal-to-noise ratio (SNR), particularly in the lateral regions of the field-of-view (FOV), thereby limiting the usable FOV. The authors propose to mitigate these aberrations by designing and fabricating aspherical corrective lenses using ray trace simulations and two-photon lithography, respectively; the corrective lenses are then mounted on the back aperture of the GRIN lens.

This approach was previously demonstrated by the same lab for GRIN lenses shorter than 4.1 mm (Antonini et al., eLife, 2020). In the current work, the authors extend their method to a new class of GRIN lenses with lengths exceeding 6 mm, enabling access to deeper brain regions as most ventral region of the mouse brain. Specifically, they designed and characterized corrective lenses for GRIN lenses measuring 6.4 mm and 8.8 mm in length. Finally, they applied these corrected long micro-endoscopes to perform high-precision calcium signal recordings in the olfactory cortex.

Compared with alternative approaches using adaptive optics, the main strength of this method is that it does not require hardware or software modifications, nor does it limit the system's temporal resolution. The manuscript is well-written, the data are clearly presented, and the experiments convincingly demonstrate the advantages of the corrective lenses.

The implementation of these long corrected micro-endoscopes, demonstrated here for deep imaging in the mouse olfactory bulb, will also enable deep imaging in larger mammals such as rats or marmosets.

Comments on revisions:

The authors have clearly addressed all my comments.

Reviewer #3 (Public review):

Summary:

This work presents the development, characterization and use of new thin microendoscopes (500µm diameter) whose accessible field of view has been extended by the addition of a corrective optical element glued to the entrance face. Two microendoscopes of different lengths (6.4mm and 8.8mm) have been developed, allowing imaging of neuronal activity in brain regions >4mm deep. An alternative solution to increase the field of view could be to add an adaptive optics loop to the microscope to correct the aberrations of the GRIN lens. The solution presented in this paper does not require any modification of the optical microscope and can therefore be easily accessible to any neuroscience laboratory performing optical imaging of neuronal activity.

Strengths:

(1) The paper is generally clear and well written. The scientific approach is well structured and numerous experiments and simulations are presented to evaluate the performance of corrected microendoscopes. In particular, we can highlight several consistent and convincing pieces of evidence for the improved performance of corrected microendoscopes:

- PSFs measured with corrected microendoscopes 75µm from the centre of the FOV show a significant reduction in optical aberrations compared to PSFs measured with uncorrected microendoscopes.

- Morphological imaging of fixed brain slices shows that optical resolution is maintained over a larger field of view with corrected microendoscopes compared to uncorrected ones, allowing neuronal processes to be revealed even close to the edge of the FOV.

- Using synthetic calcium data, the authors showed that the signals obtained with the corrected microendoscopes have a significantly stronger correlation with the ground truth signals than those obtained with uncorrected microendoscopes.

(2) There is a strong need for high quality microendoscopes to image deep brain regions in vivo. The solution proposed by the authors is simple, efficient and potentially easy to disseminate within the neuroscience community.

Weaknesses:

Weaknesses that were present in the first version of the paper were carefully addressed by the authors.

eLife Assessment

This paper represents an important contribution to the field. Summarizing results from neural recording experiments in mice across ten labs, the work provides compelling evidence that basic electrophysiology features, single-neuron functional properties, and population-level decoding are fairly reproducible across labs with proper preprocessing. The results and suggestions regarding preprocessing and quality metrics may be of significant interest to investigators carrying out such experiments in their own labs.

Reviewer #1 (Public review):

The IBL here presents an important paper that aims to assess potential reproducibility issues in rodent electrophysiological recordings across labs and suggests solutions to these. The authors carried out a series of analyses on data collected across 10 laboratories while mice performed the same decision-making task, and provided convincing evidence that basic electrophysiology features, single-neuron functional properties, and population-level decoding were fairly reproducible across labs with proper preprocessing. This well-motivated large-scale collaboration allowed systematic assessment of lab-to-lab reproducibility of electrophysiological data, and the suggestions outlined in the paper for streamlining preprocessing pipelines and quality metrics will provide general guidance for the field, especially with continued effort to benchmark against standard practices (such as manual curation).

The authors have carefully incorporated our suggestions. As a result, the paper now better reflects where reproducibility is affected when using common, simple, and more complex analyses and preprocessing methods, and it is more informative-and more reflective of the field overall. We thank the reviewers for this thorough revision. We have 2 remaining suggestions on text clarification:

(1) Regarding benchmarking the automated metrics to manual curation of units: although we appreciate that a proper comparison may require a lot of effort potentially beyond the scope of the current paper; we do think that explicit discussion regarding this point is needed in the text, to remind the readers (and indeed future generations of electrophysiologists) the pros and cons of different approaches.

In addition to what the authors have currently stated (line 469-470):<br /> "Another significant limitation of the analysis presented here is that we have not been able to assess the extent to which other choices of quality metrics and inclusion criteria might have led to greater or lesser reproducibility."

Maybe also add:<br /> "In particular, a thorough comparison of automated metrics against a careful, large, manually-curated dataset, is an important benchmarking step for future studies.

(2) The authors now include in Figure 3-Figure Supplement 1 that highlight how much probe depth is adjusted by using electrophysiological features such as LFP power to estimate probe and channel depth. This plot is immensely informative for the field, as it implies that there can be substantial variability-sometimes up to 1 mm discrepancy between insertions-in depth estimation based on anatomical DiI track tips alone. Using electrophysiological features in this way for probe depth estimation is currently not standard in the field and has only been made possible with Neuropixels, which span several millimeters. These figures highlight that this should be a critical step in preprocessing pipelines, and the paper provides solid evidence for this.

Currently, this part of the figure is only subtly referenced to in the text. We think it would be helpful to explicitly reference this particular panel with discussions of its implication in the text.

Reviewer #2 (Public review):

Summary:

The authors sought to evaluate whether analyses of large-scale electrophysiology data obtained from 10 different individual laboratories are reproducible when they use standardized procedures and quality control measures. They were able to reproduce most of their experimental findings across all labs. Despite attempting to target the same brain areas in each recording, variability in electrode targeting was a source of some differences between datasets.

Strengths:

This paper gathered a standardized dataset across 10 labs and performed a host of state-of-the-art analyses on it. Their ability to assess the reproducibility of each analysis across this kind of data is an important contribution to the field.

Comments on revisions:

The authors have addressed almost all of the concerns that I raised in this revised version. The new RIGOR notebook is helpful, as are the new analyses.

This paper attributes much error in probe insertion trajectory planning to the fact that the Allen CCF and standard stereotaxic coordinate systems are not aligned. Consequently, it would be very helpful for the community if this paper could recommend software tools, procedures, or code to do trajectory planning that accounts for this.

I think it would still be helpful for the paper to have some discussion comparing/contrasting the use of the RIGOR framework with existing spike sorting statistics. They mention in their response to reviewers that this is indeed a large space of existing approaches. Most labs performing Neuropixels recordings already do some type of quality control, but these approaches are not standardized. This work is well-positioned to discuss the advantages and disadvantages of these alternative approaches (even briefly) but does not currently do so-it does not need to run any of these competing approaches to helpfully mention ideas for what a reader of the paper should do for quality control with their own data.

eLife Assessment

This study provides valuable insights into the evolutionary histories and cellular infection responses of two Salmonella Dublin genotypes. While the evidence is compelling, a more phylogenetically diverse bacterial collection would enhance the findings. This research is relevant to scientists studying Salmonella and gastroenteritis-related pathogens.

Reviewer #1 (Public review):

The manuscript consists of two separate but interlinked investigations: genomic epidemiology and virulence assessment of Salmonella Dublin. ST10 dominates the epidemiological landscape of S. Dublin, while ST74 was uncommonly isolated. Detailed genomic epidemiology of ST10 unfolded the evolutionary history of this common genotype, highlighting clonal expansions linked to each distinct geography. Notably, North American ST10 was associated with more antimicrobial resistance compared to others. The authors also performed long read sequencing on a subset of isolates (ST10 and ST74), and uncovered a novel recombinant virulence plasmid in ST10 (IncX1/IncFII/IncN). Separately, the authors performed cell invasion and cytotoxicity assays on the two S. Dublin genotypes, showing differential responses between the two STs. ST74 replicates better intracellularly in macrophage compared to ST10, but both STs induced comparable cytotoxicity levels. Comparative genomic analyses between the two genotypes showed certain genetic content unique to each genotype, but no further analyses were conducted to investigate which genetic factors likely associated with the observed differences. The study provides a comprehensive and novel understanding on the evolution and adaptation of two S. Dublin genotypes, which can inform public health measures. The methodology included in both approaches were sound and written in sufficient detail, and data analysis were performed with rigour. Source data were fully presented and accessible to readers.

Comments on revised version:

The authors have addressed all the points raised by the reviewer. The manuscript is now much enhanced in clarity and accuracy. The re-written Discussion is more relevant and brings in comparison with other invasive Salmonella serotypes.

Comments:

In light of the metadata supplied in this revision, for Australian isolates, all human cases of ST74 (n=7) were from faeces (assuming from gastroenteritis) while 18/40 of ST10 were from invasive specimen (blood and abscess). This may contradict with the manuscript's finding and discussion on different experiment phenotypes of the two STs, with ST74 showing more replication in macrophages and potentially more invasive. Thus, the reviewer suggests the authors to mention this disparity in the Discussion, and discuss possible reasons underlying this disparity. This can strengthen the author's rationale for further in vivo studies.

Reviewer #2 (Public review):

This is a comprehensive analysis of Salmonella Dublin genomes that offers insights into the global spread of this pathogen and region-specific traits that are important to understand its evolution. The phenotyping of isolates of ST10 and ST74 also offer insights into the variability that can be seen in S. Dublin, which is also seen in other Salmonella serovars, and reminds the field that it is important to look beyond lab-adapted strains to truly understand these pathogens. This is a valuable contribution to the field. The only limitation, which the authors also acknowledge, is the bias towards S. Dublin genomes from high income settings. However, there is no selection bias; this is simply a consequence of publicly available sequences.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews: 

Reviewer #1 (Public review): 

The manuscript consists of two separate but interlinked investigations: genomic epidemiology and virulence assessment of Salmonella Dublin. ST10 dominates the epidemiological landscape of S. Dublin, while ST74 was uncommonly isolated. Detailed genomic epidemiology of ST10 unfolded the evolutionary history of this common genotype, highlighting clonal expansions linked to each distinct geography. Notably, North American ST10 was associated with more antimicrobial resistance compared to others. The authors also performed long-read sequencing on a subset of isolates (ST10 and ST74) and uncovered a novel recombinant virulence plasmid in ST10 (IncX1/IncFII/IncN). Separately, the authors performed cell invasion and cytotoxicity assays on the two S. Dublin genotypes, showing differential responses between the two STs. ST74 replicates better intracellularly in macrophages compared to ST10, but both STs induced comparable cytotoxicity levels.

Comparative genomic analyses between the two genotypes showed certain genetic content unique to each genotype, but no further analyses were conducted to investigate which genetic factors were likely associated with the observed differences. The study provides a comprehensive and novel understanding of the evolution and adaptation of two S. Dublin genotypes, which can inform public health measures. 

The methodology included in both approaches was sound and written in sufficient detail, and data analysis was performed with rigour. Source data were fully presented and accessible to readers. Certain aspects of the manuscript could be clarified and extended to improve the manuscript. 

(1) For epidemiology purposes, it is not clear which human diseases were associated with the genomes included in this manuscript. This is important since S. Dublin can cause invasive bloodstream infections in humans. While such information may be unavailable for public sequences, this should be detailed for the 53 isolates sequenced for this study, especially for isolates selected to perform experiments in vitro.

Thank you for the suggestion. We have added the sample type for the 53 isolates sequenced for this study. These additional details have been added to Supplementary Tables 1, 4, 9 and 10.

(2) The major AMR plasmid in described S. Dublin was the IncC associated with clonal expansion in North America. While this plasmid is not found in the Australian isolates sequenced in this study, the reviewer finds that it is still important to include its characterization, since it carries blaCMY-2 and was sustainedly inherited in ST10 clade 5. If the plasmid structure is already published, the authors should include the accession number in the Main Results.

We have provided accessions and context for two of the IncC hybrid plasmids that have been previously reported in the literature in the Introduction. The text now reads:

“These MDR S. Dublin isolates all type as sequence type 10 (ST10), and the AMR determinants have been demonstrated to be carried on an IncC plasmid that has recombined with a virulence plasmid encoding the spvRABCD operon (12,16,18,19).  This has resulted in hybrid virulence and AMR plasmids circulating in North America including a 329kb megaplasmid with IncX1, IncFIA, IncFIB, and IncFII replicons (isolate CVM22429, NCBI accession CP032397.1) (12,16) and a smaller hybrid plasmid 172,265 bases in size with an IncX1 replicon (isolate N13-01125, NCBI accession KX815983.1) (19).”

Further characterisation of the IncA/C plasmid circulating in North America was beyond the scope of this study.

(a) The reviewer is concerned that the multiple annotations missing in  plasmid structures in Supplementary Figures 5 & 6, and  genetic content unique to ST10 and ST74 was due to insufficient annotation by Prokka. I would recommend the authors use another annotation tool, such as Bakta (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC8743544/) for plasmid annotation, and reconstruction of the pangenome described in Supplementary Figure 10. Since the recombinant virulence plasmid in ST10 is a novel one, I would recommend putting Supplementary Figure 5 as a main figure, with better annotations to show the virulence region, plasmid maintenance/replication, and possible conjugation cluster.

In the supplementary figures of the plasmids, we sought to highlight key traits on interest on the plasmids, namely plasmid replicons, antimicrobial resistance and heavy metal resistance (Supplementary Figure 5) and virulence genes (Supplementary Figure 6). The inclusion of the accessions of publicly available isolates provide for characterised plasmids such as the S. Dublin virulence plasmid (NCBI accession: CP001143). 

For the potentially hybrid plasmid with IncN/IncX1/IncFII reported in Supplementary Figure 6, we have undertaken additional analyses of the two Australian isolates to reannotate these isolates with Bakta which provides for more detailed annotations. 

We have added new text to the methods which reads as: 

“The final genome assemblies were confirmed as S. Dublin using SISTR and annotated using both Prokka v1.14.6 (69) for consistency with the draft genome assemblies and  Bakta v1.10.1 (93) which provides for more detailed annotations (Supplementary Table 13). Both Prokka and Bakta annotations were in agreement for AMR, HMR and virulence genes, with Bakta annotating between 3-7 additional CDS which were largely ‘hypothetical protein’.”

For the pangenome analysis of the seven ST74 and ten ST10 isolates, we have continued to use the Prokka annotated draft genome assemblies for input to Panaroo. 

(4) The authors are lauded for the use of multiple strains of ST10 and ST74 in the in vitro experiment. While results for ST74 were more consistent, readouts from ST10 were more heterogenous (Figure 5, 6). This is interesting as the tested ST10 were mostly clade 1, so ST10 was, as expected, of lower genetic diversity compared to tested ST74 (partly shown in Figure 1D. Could the authors confirm this by constructing an SNP table separately for tested ST10 and ST74? Additionally, the tested ST10 did not represent the phylogenetic diversity of the global epidemiology, and this limitation should be reflected in the Discussion.

In response to the reviewer’s comments, we have provided a detailed SNP table (Supplementary Table 12) to further clarify the genetic diversity within the tested ST10 and ST74 strains. 

Additionally, we have expanded on the limitation regarding the phylogenetic diversity of the ST10 isolates in the Discussion, highlighting how the strains used in the in vitro experiments may not fully represent the global epidemiological diversity of S. Dublin ST10. The new text now reads:

“This study has limitations, including a focus on ST10 isolates from clade 1, which do not represent global phylogenetic diversity. Nonetheless, our pangenome analysis identified >900 uncharacterised genes unique to ST74, offering potential targets for future research. Another limitation is the geographic bias in available genomes, with underrepresentation from Asia and South America. This reflects broader disparities in genomic research resources but may improve as public health genomics capacity expands globally.”

(5) The comparative genomics between ST10 and ST74 can be further improved to allow more interpretation of the experiments. Why were only SPI-1, 2, 6, and 19 included in the search for virulome, how about other SPIs? ST74 lacks SPI-19 and has truncated SPI-6, so what would explain the larger genome size of ST74? Have the authors screened for other SPIs using more well-annotated databases or references (S. Typhi CT18 or S. Typhimurium ST313)? The mismatching between in silico prediction of invasiveness and phenotypes also warrants a brief discussion, perhaps linked to bigger ST74 genome size (as intracellular lifestyle is usually linked with genome degradation).

Systematic screening for SPIs with detailed reporting on individual genes and known effectors is still an area of development in Salmonella comparative genomics. In our characterisation of the virulome in this S. Dublin dataset we decided to focus on SPI1, SPI-2, SPI-6 and SPI-19 as these had been identified in previous studies and were considered to be most likely linked to the invasive phenotype of S. Dublin. We thought the truncation of SPI-6 and lack of SPI-19 in ST74 compared to the ST10 isolates would provide a basis to explore genomic differences in the two genotypes, with the screening for individual genes on each SPIs reported in Supplementary Figure 7 and Supplementary Table 9.  

We have expanded upon the mismatching of the in silico prediction of invasiveness and phenotypes in the Discussion. We now explore the increased genome size and intracellular replication of the ST74 population. We hypothesise that invasiveness has not been studied as thoroughly in zoonotic iNTS as much as human adapted iNTS and S. Typhi, and the increased genome content may be required for survival in different host species. The new text now reads:

“Our phenotypic data demonstrated a striking difference in replication dynamics between ST10 and ST74 populations in human macrophages. ST74 isolates replicated significantly over 24 hours, whereas ST10 isolates were rapidly cleared after 9 hours of infection. ST74 induced significantly less host cell death during the early-mid stage of macrophage infection, supported by limited processing and release of IL-1ß at 9 hpi. While NTS are generally potent inflammasome activators (60), most supporting data come from laboratory-adapted S. Typhimurium strains. Our findings suggest that ST74 isolates may employ immune evasion mechanisms to avoid host recognition and activation of cell death signaling in early infection stages. Similar trends have been observed with S. Typhimurium ST313, which induces less inflammasome activation than ST19 during murine macrophage infection (61). This could facilitate increased replication and dissemination at later stages of infection. Consistent with this, we observed comparable cytotoxicity between ST10 and ST74 isolates at 24 hpi, suggesting ST74 induces cell death via alternative mechanisms once intracellular bacterial numbers are unsustainable. Further research is needed to identify genomic factors underpinning these observations.”

(6) On the epidemiology scale, ST10 is more successful, perhaps due to its ongoing adaptation to replication inside GI epithelial cells, favouring shedding. ST74 may tend to cause more invasive disease and less transmission via fecal shedding. The presence of T6SS in ST10 also can benefit its competition with other gut commensals, overcoming gut colonization resistance. The reviewer thinks that these details should be more clearly rephrased in the Discussion, as the results highly suggested different adaptations of two genotypes of the same serovar, leading to different epidemiological success.

We thank the reviewer for highlighting that we could rephrase this important point. We have added additional text in the Discussion to better interpret the differences in the two genotypes of S. Dublin and how this relates to difference epidemiological success. The new text now reads:

“While machine learning predicted lower invasiveness for ST74 compared to ST10, the increased genomic content of ST74 may support higher replication in macrophages. We speculate that increased intracellular replication could enhance systemic dissemination, though this requires in vivo validation. Invasiveness of S. enterica is often linked to genome degradation (4,62–64). However, this is mostly based on studies of human-adapted iNTS (ST313) and S. Typhi, leaving open the possibility that the additional genomic content of ST74 supports survival in diverse host species. An uncharacterised virulence factor may underlie this replication advantage. Collectively, these findings highlight phenotypic differences between S. Dublin populations ST10 and ST74. Enhanced intra-macrophage survival of ST74 could promote invasive disease, whereas the prevalence of ST10 may relate to better intestinal adaptation and enhanced faecal shedding. In vivo models are needed to test this hypothesis. Interestingly, the absence of SPI-19 in ST74, which encodes a T6SS, may reflect adaptation to enhanced replication in macrophages. SPI-19 has been linked to intestinal colonisation in poultry (23,56) and mucosal virulence in mice (56). It’s possible that the efficient replication of ST74 in macrophages might compensate for the absence of SPI-19, relying instead on phagocyte uptake via M cells or dendritic cells. The larger pangenome of ST74 compared to ST10 could further enhance survival within hosts. These findings highlight important knowledge gaps in zoonotic NTS host-pathogen interactions and drivers of emerging invasive NTS lineages with broad host ranges.”

Reviewer #2 (Public review): 

This is a comprehensive analysis of Salmonella Dublin genomes that offers insights into the global spread of this pathogen and region-specific traits that are important to understanding its evolution. The phenotyping of isolates of ST10 and ST74 also offers insights into the variability that can be seen in S. Dublin, which is also seen in other Salmonella serovars, and reminds the field that it is important to look beyond lab-adapted strains to truly understand these pathogens. This is a valuable contribution to the field. The only limitation, which the authors also acknowledge, is the bias towards S. Dublin genomes from high-income settings. However, there is no selection bias; this is simply a consequence of publically available sequences.

Reviewer #1 (Recommendations for the authors): 

(1) The Abstract did not summarize the main findings of the study. The authors should rewrite to highlight the key findings in genomic epidemiology (low AMR generally, novel plasmid of which Inc type, etc.) and the in vitro experiments. The findings clearly illustrate the differing adaptations of the two genotypes. Suggest to omit 'economic burden' and 'livestock' as this study did not specifically address them.

We agree with the Reviewer and have re-written the abstract to directly reflect the major outcomes of the research. We have also deleted wording such as ‘livestock’, ‘economic burden’ and ‘One Health’ as we did not specifically address these issues as highlighted by the Reviewer. 

(2) Figure 2: The MCC tree should include posterior support in major internal nodes. The current colour scheme is also confusing to readers (columns 1, 2). Suggest to revise and include additional key information as columns: major AMR genes (blaCMY-2, strAB, floR) and mer locus, so this info can be visualized in the main figure. 

Thank you for your valuable feedback. We have revised Figure 2 with the MCC tree to include posterior support on the internal nodes. We have also amended the figure legend to explain the additional coloured internal nodes. We have also amended the heatmap in Figure 2 to include additional white space between the columns to make it easier for the readers to distinguish. We didn’t change the colours in this figure as we have used the same colours throughout for the different traits reported in this study. Further, we chose to keep the AMR profiles reported in Figure 2 at the susceptible, resistant or MDR. This was done to convey the overview of the AMR profiles, and we provide detail in the AMR and HMR determinants in the Supplementary Figures and Tables. 

(3) The manuscript title is not informative, as it did not study the 'dynamics' of the two genotypes. Suggest to revise the study title along the lines of main results.

Thank you for the feedback on the title. We have amended this to better reflect the main findings of the study, and it now reads as “Distinct adaptation and epidemiological success of different genotypes within Salmonella enterica serovar Dublin”

(4) The co-occurrence of AMR and heavy metal resistance genes (like mer) are quite common in Salmonella and E. coli. This is not a novel finding. The reviewer would suggest shortening the details related to heavy metal resistance in Results and Discussion, to make the writing more streamlined. 

In line with the Reviewer comments, we have shortened the details in the Results and Discussion on the co-occurrence of AMR and HMR.  

(5) L185: missing info after n=82. 

This has been revised to now read as “n=82 from Canada”. 

(6) I think Vi refers to the capsular antigen, not flagelle. Please double-check this.

Thank you for highlighting this mistake. We have revised all instances.

(7) L252-253: which statistic was used to state 'no association'. Also, there is no evidence presented to support 'no fitness cost associated with resistance and virulence."

We have removed this sentence.

(8) 320: Figure 6F is a scatterplot, not PCA. Please confirm. 

The reviewer is correct, this is in fact a scatterplot. We have amended the figure legend and text.

(9) For Discussion, it would be helpful to compare the phenotype findings with that of other invasive Salmonella like Typhi or Typhimurium ST313.

Thank you for noting this, we had alluded to findings from ST313 but have now expanded include some further comparisons to S. Typhimurium ST313 and added references for these within the Discussion. The additional text now reads:

“Similar trends have been observed with S. Typhimurium ST313, which induces less inflammasome activation than ST19 during murine macrophage infection (61). This could facilitate increased replication and dissemination at later stages of infection.”

"Invasiveness of S. enterica is often linked to genome degradation (4,62–64).

However, this is mostly based on studies of human-adapted iNTS (ST313) and S. Typhi, leaving open the possibility that the additional genomic content of ST74 supports survival in diverse host species. An uncharacterised virulence factor may underlie this replication advantage.”

(10) L440: no evidence for "successful colonization" of ST74. Actually, the findings suggested otherwise.

Thank you for picking this up, we have amended the sentence to better reflect the findings. The amended text now reads as:

“It’s possible that the efficient replication of ST74 in macrophages might compensate for the absence of SPI-19, relying instead on phagocyte uptake via M cells or dendritic cells. The larger pangenome of ST74 compared to ST10 could further enhance survival within hosts.”

(11) L460-461: The data did not show an increasing trend of iNTS related to S. Dublin.

Thank you for identifying this. This sentence has been revised accordingly and now reads as:

“While the data did not indicate an increasing trend of iNTS associated with S. Dublin, the potential public health risk of this pathogen suggests it may still warrant considering it a notifiable disease, similar to typhoid and paratyphoid fever.”

(12) L465: Data were not analyzed explicitly in the context of animal vs. human. Suggest omitting 'One Health' from the conclusion.

Thank you for the suggestion. We have omitted “One Health” from the conclusion

(13) L500: Was the alignment not checked for recombination using Gubbins? The approach here is inconsistent with the method described in the subtree selected for BEAST analysis (L546).

We have now applied Gubbins to the phylogenetic tree constructed using IQTREE, and the methods and results have been updated accordingly.

(14) What was the output of Tempest? Correlation or R2 value? 

We have now included the R2 value from Tempest and reported this in the manuscript. 

(15) L556: marginal likelihood to allow evaluation of the best-fit model. Please rephrase to state this clearly.

We have rephrased this in the manuscript to state this clearly.

eLife Assessment

This valuable study reports that epididymal proteins are required for embryogenesis after fertilization. The data presented are generally supportive of the conclusion and considered solid. This work will be of interest to reproductive biologists and andrologists.

Reviewer #1 (Public review):

Summary:

The main observation that the sperm from CRISP proteins 1 and 3 KO lines are post-fertilization less developmentally competent is convincing. The data showing progressive acquisition of the sperm defects during epididymal transport and the exchange fluid studies showing the altered epididymal environment are important. However, the molecular characterization of the mechanism(s) that leads to these defects requires additional studies.

Strengths:

The generation of these double mutant mice is valuable for the field. Moreover, the fact that the double mutant line of Crisp 1 and 3 is phenotypically different from the Crisp 1 and 4 line suggests different functions of these epididymis proteins. The methods used to demonstrate that developmental defects are largely due to post-fertilization defects are also a considerable strength. The initial characterization that these sperm have altered intracellular Ca2+ levels, and increased rates of DNA fragmentation are valuable. The increase fragmentation of control sperm DNA when exposed to mutant epididymal fluid is significant and an excellent platform for future studies.

Weaknesses:

The study is mechanistically incomplete because evidence of how these proteins alter the environment is not shown. What are the target(s) of these proteins that result in increased Ca2+?

Reviewer #2 (Public review):

Summary:

The study highlights the role of CRISP1 and CRISP3, two epididymal proteins, in early embryo development through DNA integrity. The authors demonstrate that C1/C3 DKO sperm exhibit defects in the DNA integrity, probably due to Ca2+ dysregulation in the epididymis. However, direct evidence for this mechanism requires further experiments. The finding of the involvement of the epididymal environment in embryogenesis is significant, but some results on sperm fertilizing ability of C1/C3 DKO mice were similar to the previous report. Thus, this point raises concern about the perspective of novelty.

Strengths:

The authors demonstrate that CRISP1 and CRISP3 regulate Ca2+ in the epididymal fluid, and loss of CRISP1 and CRISP3 disrupts Ca2+ regulation in the epididymal fluid, leading to sperm DNA fragmentation and impaired embryonic development after fertilization. This proposed mechanism is both novel and intriguing, offering valuable insights into the epididymal control of sperm quality.

Weaknesses:

The evidence supporting the mechanism of CRISP1 and CRISP3 in calcium regulation within epididymis and its contribution to the sperm DNA damage remains limited.

Major comments:

The data provided in this manuscript (Figure 2A and B) appear to overlap with data in previously published paper (PMID:33037689), despite differences in the duration of in vivo fertilization after mating. The results in both studies show similar findings, raising concerns about potential data redundancy.

As shown in Figure 6A, while wild-type sperm were exposed to the epididymal fluid of C1/C3 DKO mice, the wild-type sperm exhibited DNA fragmentation. Additionally, when wild-type sperm were exposed to the epididymal fluid of wild-type mice with 10 mM Ca2+, DNA fragmentation is still observed. Therefore, the authors conclude that the DNA fragmentation in C1/C3 DKO sperm is due to the increased level of the Ca2+. However, the connection between the DNA damage in wild-type sperm exposed to the epididymal fluid of C1/C3 DKO mice and the increased levels of Ca2+ remains unclear. To clarify this, it is suggested that intracellular calcium levels in the wild type sperm should be analyzed before and after exposure to the epididymal fluid of C1/C3 DKO mice (or before and after adding 10 mM Ca2+ into wild-type fluid). Furthermore, the author should explain detailed information on epididymal fluid collection, because Ca2+ levels vary between different sections of the epididymis.

In lines 321-323, the authors mention the selection system of the female reproductive tract that only allows high-quality sperm to reach the eggs (Cummins and Yanagimachi 1982), but this paper is not listed in the bibliography. It is important to ensure proper referencing.

The discussion section is too long and difficult to follow well because there is redundancy of the results in many parts. It is recommended to shorten it by focusing only on relevant and important information.

Author response:

The following is the authors’ response to the previous reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The main observation that the sperm from CRISP proteins 1 and 3 KO lines are postfertilization less developmentally competent is convincing. However, the molecular characterization of the mechanism that leads to these defects and the temporal appearance of the defects requires additional studies.

We thank the reviewer for the valuable comments. As requested, additional experiments were carried out to analyze both the molecular mechanisms and the temporal appearance of the observed defects. Our results showed that DNA integrity defects appear during epididymal maturation and/or storage (see Figure 5B), that the epididymal fluid contributes to sperm DNA fragmentation defects (See Figure 6A) and that these defects seem not to be due to an increase in oxidative stress (Figure 5C) but rather to a dysregulation in Ca²⁺ homeostasis within the epididymis (Figure 6A,B).

Strengths:

The generation of these double mutant mice is valuable for the field. Moreover, the fact that the double mutant line of Crisp 1 and 3 is phenotypically different from the Crisp 1 and 4 line suggests different functions of these epididymis proteins. The methods used to demonstrate that developmental defects are largely due to post-fertilization defects are also a considerable strength. The initial characterization of these sperm has altered intracellular Ca²⁺ levels, and increased rates of DNA fragmentation are valuable.

We thank the reviewer for the positive comments on our work.

Weaknesses:

The study is mechanistically incomplete because there is no direct demonstration that the absence of these proteins alters the epididymal environment and fluid, wherein during the passage through the epididymis the sperm become affected. Also, a direct demonstration of how the proteins in question cause or lead to DNA damage and increased Ca²⁺ requires further characterization.

The new experiments included in the revised version (see Figure 6A) showed that exposure of control WT sperm to epididymal fluid form mutant mice leads to an increase in sperm DNA fragmentation levels, confirming that the absence of CRISP1 and CRISP3 alters the epididymal fluid wherein the sperm become affected. In addition, new observations showing that WT sperm exposed to WT epididymal fluid in the presence of Ca²⁺ also exhibit higher DNA fragmentation levels (Figure 6A) together with the finding that mutant sperm exhibit higher intracellular Ca²⁺ levels (Figure 6B) but no higher levels of ROS, strongly support a dysregulation in Ca²⁺ homeostasis within the epididymis and sperm as the main responsible for DNA integrity defects.

Reviewer #2 (Public Review):

The authors showed that CRISP1 and CRISP3, secreted proteins in the epididymis, are required for early embryogenesis after fertilization through DNA integrity in cauda epididymal sperm. This paper is the first report showing that the epididymal proteins are required for embryogenesis after fertilization. However, some data in this paper (Table 1 and Figure 2A) are overlapped in a published paper (Curci et al., FASEB J, 34,15718-15733, 2020; PMID: 33037689). Furthermore, the authors did not address why the disruption of CRISP1/3 leads to these phenomena (the increased level of the intracellular Ca²⁺ level and impaired DNA integrity in sperm) with direct evidence. Therefore, if the authors can address the following comments to improve the paper's novelty and clarification, this paper may be worthwhile to readers.

We thank the reviewer for the constructive comments. Regarding the data included in Table 1 and Figure 2A, it is important to note that Table 1 includes data on embryo development corresponding to C1/C4 DKO mice not published before in which the data on embryo development corresponding to C1/C3 DKO was used as simultaneous control. Figure 2A showed in vivo fertilization results at short times after mating (4h instead of 18 h) that have been neither reported before.

Regarding studies to address why the disruption of CRISP1 and CRISP3 leads to defects in DNA integrity and Ca²⁺ levels, we have carried out new experiments showing that mutant sperm do not exhibit higher levels of ROS (see Figure 5C), not favoring oxidative stress as the mechanism underlying mutant sperm defects. In addition, we found that DNA integrity defects develop during epididymal transit (Figure 5B) and that exposure of WT sperm to epididymal fluid from mutant mice leads to an increase in sperm DNA fragmentation levels (Figure 6A), confirming that the absence of CRISP1 and CRISP3 alters the epididymal fluid. Finally, our new results showing that WT sperm exposed to WT epididymal fluid in the presence of Ca²⁺ also exhibit higher DNA fragmentation levels (Figure 6A) together with the higher intracellular Ca²⁺ levels detected in mutant sperm (Figure 6B) strongly support a dysregulation in Ca²⁺ homeostasis within the epididymis and sperm as the main responsible for DNA integrity defects.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Overall comments:

This manuscript investigates the mechanisms whereby the absence of the epididymal CRISP proteins 1 and 3 (Cysteine-Rich Secretory Proteins) causes infertility and lower embryo developmental rates. This strain's infertility seems to have a post-fertilization origin because the rates of in vivo fertilization are like the controls, but the development to the blastocyst stage is decreased. The results of this study show that (1) mutant sperm viability, progressive motility, and morphology are normal;

(2) in vivo fertilization rates are comparable to controls, but embryo development is reduced;

(3) in vitro fertilization studies found reduced fertilization rates and activation rates even in zona-free studies;

(4) additional functional studies showed increased rates of DNA fragmentation and elevated Ca²⁺ levels in mutant sperm.

The results presented are credible and hint that the epididymis might play a role before and after fertilization and directly affect embryo development. However, the study is mechanistically incomplete, as there is no direct demonstration that the absence of these proteins alters the epididymal environment and fluid, wherein the passage through the epididymis the sperm become functionally defective, and whether mutant or control epididymal fluid or purified CRISP proteins can change, either reduce or overcome, respectively, the developmental competence of the control or mutant sperm and induce functional changes in the counterpart sperm. In summary, the main observation that the sperm from CRISP proteins 1 and 3 KO lines are post-fertilization less developmentally competent is significant and important, but the molecular characterization of the defects and the temporal appearance of defects requires additional studies.

Specific comments:

(1) Introduction.

It is too long. The description of the function of the epididymis should be reduced. The functional properties of the Crisp genes should also be substantially shortened.

As requested, the Introduction has been revised and descriptions of the epididymis and CRISP have been shortened

(2) Results.

• Lines 140 to 142. Remove these initial lines. Start directly addressing the results of the C1/C3 strain, which is the mutant under consideration here. Referring to the C1/C4 results detracts from the focus of the study.

As suggested by the reviewer, lines 140 to 142 have been removed.

• Table 1. Move the two-cell embryo line to the top of the Table and place the Blastocyst line below it. This organization is the conventional method to present this type of data.

As suggested, the order of the lines in Table 1 has been modified to align with the conventional presentation method.

• Figures 1 and 2A and B data are solid and support the notion that enough sperm reach the site of fertilization, and that the sperm are defective in their capacity to support embryo development. Figures 2C and D have interesting data, although additional information would strengthen these results. The authors concluded that the sperm were defective in the epididymis. Where in the epididymis? These sperm were all from the cauda. Could the authors collect sperm from the upper portion of the cauda, or midportion, and compare if the defects manifest gradually?

We appreciate this interesting and appropriate comment from the reviewer. In this regard, all the studies in our work were carried out using sperm from the whole cauda epididymis, the reason why we could not answer where defective sperm appear in the epididymis. In view of this, we have now conducted a comparative DNA fragmentation analysis between caput and cauda sperm from both genotypes. Our findings indicate that while cauda mutant sperm showed once again higher DNA fragmentation levels than controls, caput sperm exhibited levels of DNA damage not significantly different between genotypes. These results confirm that defects in DNA appear following sperm passage through the epididymal caput, supporting the hypothesis that defects in DNA fragmentation manifest during sperm transit through the epididymis and /or during storage in the cauda. These results have been included in the revised version of the manuscript (see lines 235-240/Figure 5B of the revised version)

• Figure 3 displays the results of in vitro fertilization, either COCs A-C or zona-free fertilization D-F. The results are important and differ from those produced by fertilization in vivo. The authors indicate that these confirm that the in vivo conditions overcome in vitro defects. However, this study never addresses the reason behind it. Is there less expression of proteins related to these functions, or the function of some proteins is compromised? The authors should advance a hypothesis or a rationale to explain these results.

As indicated by the reviewer, our results showed differences between the fertilization rates observed for mutant mice under in vivo and in vitro conditions, as previously observed for all our single and multiple KO models (Da Ros et al., 2008; PMID: 18571638, Brukman et al., 2016; PMID: 26786179, Weigel Muñoz, 2018; PMID: 29481619, Ernesto et al., 2015; PMID: 26416967, Carvajal et al,. 2018; PMID: 30510210) and also reported by other groups (Okabe et al., 2007; PMID: 17558467). In this regard, it has been well established that, although millions of sperm are ejaculated into the female tract, only a few (approximately one per oocyte) reach the fertilization site (i.e. the ampulla) (Cummins and Yanagimachi, 1982; doi:10.1002/mrd.1120050304). This efficient selection system by the female reproductive tract leads to the arrival of only the best sperm at the fertilization site, even in males with reproductive deficiencies, thereby “masking” sperm defects that can be detected under in vitro conditions due to the competition between good and bad quality sperm for the egg. Thus, although we can not exclude other mechanisms to explain the commonly observed differences between in vivo and in vitro fertilization rates, our rationale is that the natural and efficient sperm selection process that takes place within the female reproductive tract masks sperm defects that can, otherwise, be detected under the competitive in vitro conditions. This explanation is now included in the discussion of the revised version of the manuscript (see lines 320-325).

• Data in Figures 4 and 5 support the interpretation of the authors. However, it is necessary to establish the level of oxidative stress in the mutant sperm vs. the controls. Also, a question to explore is for how long does the sperm need to reside in that mutant environment to start undergoing the DNA fragmentation reported?

In response to the valuable request from the reviewer regarding the level of oxidative stress in sperm, we have analyzed reactive oxygen species (ROS) levels in mutant and control epididymal sperm. Our results showed that ROS levels in mutant sperm were not higher than those observed in the control group, supporting the idea that mechanisms other than oxidative stress may be leading to the increased DNA fragmentation observed in mutant sperm. These results are now included in the revised version of the manuscript (see Figure 5C).

Regarding the question on how long the sperm need to reside in the mutant environment to undergo DNA fragmentation, recent experiments carried out in response to this reviewer in which we analyzed DNA fragmentation in caput sperm led us to conclude that DNA fragmentation develops during epididymal transit and/or storage in the cauda. While these observations do not precisely define the time within the epididymis that sperm require for exhibiting DNA fragmentation, our additional new in vitro experiments analyzing the effect of epididymal fluids on sperm DNA integrity showed that exposure of WT sperm to DKO fluid for only 1 hr already leads to an increase in DNA fragmentation (see Figure 6A of the revised manuscript), suggesting that sperm do not need long periods within the mutant environment to be affected.

(3) The length of the Discussion section should be shortened, especially by not recapitulating data presented in the Results section.

As requested by the reviewer, sections recapitulating results have been modified.

Minor comments:

(1) The sentence in lines 171 and 172 is unclear, "However, despite the short time after mating, once again, the in vivo fertilized eggs corresponding to the mutant group exhibited clear defects to reach the blastocyst stage in vitro compared to controls." What do the authors mean by short time? It is the expected time, correct?

It is well established that after copulatory plug formation, most oocytes are fertilized within 2 to 8 hours, with fertilization rates that increase over time: 0–5% at 1.5 hours post-mating; 40% at 4 hours post-mating and more than 90% at 7 hs after mating (Muro et al., 2016; PMID: 26962112, La Spina et al., 2016; PMID: 26872876). In order to examine whether the embryo development defects observed for mutant mice were due to a delayed arrival of sperm to the ampulla, we decided to analyze the percentage of fertilized eggs recovered from the ampulla at “short times” (4 hs) after mating to avoid the possibility that the prolonged stay of sperm within the female tract corresponding to the usual “overnight mating” schedule could be giving defective sperm enough time to reach the ampulla and, finally, fertilize the eggs (i.e. delayed fertilization). Our results showed that, despite the expected lower fertilization rates observed for both control and mutant males when analyzed just 4 hs after mating, the fertilized eggs corresponding to the mutant group were still exhibiting clear defects to develop into blastocysts compared to controls, not favoring the idea that embryo development defects were due to a delayed fertilization. The sentence in lines “171 and 172” has been modified in the revised version of the manuscript to better explain this conclusion (see lines 152-155 of the revised version).

(2) Line 177. Mutant epididymal sperm already carry defects leading to embryo development failure. Under this subheading, the authors compare within the same female the ability of mutant and control sperm delivered into different horns to support fertilization and embryo development. They show that the embryo development induced by mutant sperm is diminished vs. controls under very similar conditions, confirming the previous results of post-fertilization failure. The data also answers the question raised by the authors of whether the fertilization defects appear during or after epididymal transit; the interpretation of the results is the functional defects in the sperm are present before the transport into the female tract. Important unaddressed questions are, could these defects begin even earlier before arriving at the cauda? Did the authors try to incubate the mutant sperm with the epididymal fluid of WT mice to examine if the sperm defects could be rescued? The opposite experiment could also be performed, where WT sperm are incubated with the epididymal fluid of mutant mice, and the treated sperm examined for altered Ca²⁺ levels or DNA fragmentation.

First of all, we would like to clarify that our question about whether the fertilization defects appear “during or after epididymal transit” was in fact referring to whether defects appear during epididymal maturation or later on, at the moment of ejaculation. In this regard, our in vivo and in vitro fertilization studies allowed us to conclude that defects were already present in epididymal sperm without excluding the possibility that additional defects could appear at the vas deferens or at the moment of ejaculation due to the contribution of seminal plasma secretions.

Regarding whether sperm defects could appear even earlier before arriving to the cauda, we have now analyzed DNA fragmentation defects in caput vs cauda both mutant and control sperm observing differences between genotypes only for cauda sperm. Based on these observations, we conclude that DNA integrity defects appear within the epididymis after sperm passage through the caput either when sperm reach the corpus or the cauda epididymis, or during their storage within the cauda region.

Also, as suggested by the reviewer, we incubated in vitro WT sperm with epididymal fluid from DKO mice (and vice versa) and then analyzed DNA fragmentation levels. Results showed that exposure of control sperm to the mutant epididymal fluid for 1 hr significantly increased DNA fragmentation levels. When mutant sperm (exhibiting higher levels of DNA fragmentation than control sperm), were exposed to epididymal fluid from WT mice, no differences between groups were observed. Together, these results confirm both that the epididymal fluid from mutant mice contributes to the higher DNA fragmentation levels detected in mutant sperm, and that normal epididymal fluid would not be able to rescue the DNA fragmentation present in mutant cells. These results are now included in the revised version of the manuscript (see Figure 6A).

(3) Lines 203 to 216. In these paragraphs the authors indicate "that mutant sperm had a lower percentage of fertilization and lower rates of blastocysts (Figure 3D, E), indicating that defects in egg coat penetration were not responsible for embryo development failure. Later, they indicated that a few eggs fertilized by mutant sperm failed to activate. It is shown that Ca²⁺ oscillations are normal, indicating that the defects lie elsewhere. Could the authors propose a mechanism based on their sperm DNA defects?

As described in the Result and Discussion sections of the original manuscript, we decided to investigate the existence of possible defects in sperm DNA fragmentation based on evidence indicating that delays in early embryo development may result from the time taken by the egg to repair damaged paternal DNA (Esbert et al., 2018; PMID: 30259705, Newman et al., 2022; PMID: 34954800, Nguyen et al., 2023; PMID: 37658763). In this regard, it is known that time is needed before the first embryonic cell division for activation of the egg DNA repairing machinery (Martin et al., 2019; PMID: 30541031, Newman et al., 2022; PMID: 34954800) and that increased sperm DNA damage may necessitate more time for repair by the oocyte (Martin et al., 2019; PMID: 30541031, Newman et al., 2022; PMID: 34954800). Based on this, we decided to examine possible DNA damage in sperm. Our finding that, in fact, sperm DNA fragmentation was clearly increased in mutant sperm led us to propose that delays in early embryo development in our mutant colonies may result from the time required by the egg to repair sperm DNA fragmentation.

(4) The demonstration that C1/C3 sperm have abnormal rates of DNA fragmentation and Ca²⁺ levels is significant. Additional studies would strengthen the findings reported here. For example, what are the levels of oxidative stress in these sperm? Are there other changes related to oxidative stress? Performing a TUNNEL assay will strengthen the notion of DNA damage demonstrated here with the chromatin dispersion assay.

As mentioned previously, we analyzed oxidative stress by evaluating ROS levels in control and mutant sperm observing no differences between genotypes. These results have been included in the revised version of the manuscript (See Figure 5C). We appreciate the suggestion of performing TUNNEL assay for future studies.

Reviewer #2 (Recommendations For The Authors):

Major comments:

(1) There are some reports small RNAs gained during the epididymal transition of sperm are essential for embryonic development (e.g., Conine et al., Dev Cell, 46, 470480, 2018; PMID: 30057276), suggesting that the luminal changes in Crisp1/3 double KO (dKO) epididymis lead to the phenotype in this study. In fact, there is no evidence whether CRISP1/CRISP3 secreted from an epididymis exists in cauda epididymal sperm and directly controls the observed phenomena. Also, the authors wrote there is no strong evidence to exclude the possible role of small RNA in Crisp1/3 dKO sperm (lines 370-372). Therefore, it is at least necessary to measure small RNA abundance in dKO mice.

As mentioned by the reviewer and as cited in our manuscript, there is a report indicating that the small RNAs gained during epididymal transit may play a role in embryonic development (Conine et al., 2018; PMID: 30057276). However, the need of small RNAs for embryonic development still remains a topic of debate (Wang et al. 2020; PMCID: PMC7799177). In this regard, clear evidence indicating that sperm DNA fragmentation is associated with embryo development defects together with the increase in sperm DNA fragmentation levels observed in mutant sperm support sperm DNA damage as one of the causes leading to the observed phenotype in our mutant mice. Moreover, recent experiments carried out in response to Reviewer 1 comments revealed that exposure of control sperm to epididymal fluid from mutant mice significantly increases DNA fragmentation levels, confirming that the absence of CRISP1 and CRISP3 proteins in epididymal fluid contributes to sperm DNA damage in mutant sperm. Finally, whereas oxidative stress might also lead to embryo development impairment as mentioned in our original manuscript, recent evaluation of ROS levels in control and mutant sperm carried out in response to Reviewer 1’s comments did not show higher ROS levels in mutant sperm. Thus, although as mentioned in the manuscript, we do not exclude the possibility that small RNAs may also contribute to embryo development defects, our observations support DNA fragmentation and a dysregulation in Ca²⁺ homeostasis within the epididymis and sperm as the main responsible for embryo development failure in our mutant males. The experiments using epididymal fluid (Figure 6A) and those evaluating ROS levels (Figure 5C) have been included in the revised version of the manuscript and discussed accordingly.

(2) Lines 245-248 and 354-374: According to Figure 5C, the intracellular Ca²⁺ level significantly increased in Crisp1/3 dKO sperm compared to control. The author hypothesized that this increase could destroy sperm DNA integrity, causing defects in early embryogenesis. However, the authors did not show the direct evidence.

Specifically, as CRISP1 inhibits CatSper (line 95), the authors believed the increased Ca²⁺ level in Crisp1/3 dKO sperm was observed. Crisp1/3 dKO and Crisp1/4 dKO mice share the disruption of Crisp1, but the phenotype is totally different. Thus, the authors should also examine the CatSper activity in Crisp1/3 dKO sperm.

We appreciate the reviewer's insightful comments. In this regard, whereas C1/C3 and C1/C4 DKO colonies shares the disruption of Crisp1, the intracellular Ca²⁺ levels in these two colonies are different as no increase in sperm intracellular Ca²⁺ was detected in Crisp C1/C4 DKO mice. Thus, this difference in intracellular Ca²⁺ levels might explain the different embryo development phenotype observed in our two DKO colonies. In this regard, our results revealed that sperm intracellular Ca²⁺ levels are different depending on the Crisp gene being deleted. Whereas the lack of Crisp1 did not affect intracellular sperm Ca²⁺ levels (Weigel Munoz et al, 2018; PMID: 29481619), there was an increase in Ca²⁺ levels in CRISP2 KO sperm (Brukman et al., 2016; PMID: 26786179) and a decrease in sperm when Crisp4 was deleted (Carvajal 2019, Ph.D Thesis). Thus, although the ability of CRISP3 to regulate sperm Ca²⁺ channels has not yet been reported, the existence of functional compensations between homologous CRISP members (Curci et al., 2020; PMID: 33037689) makes it complicated to draw straightforward conclusions based on the behavior of each individual protein in Ca²⁺ regulation. In fact, while the lack of CRISP1 and CRISP4 does not affect sperm Ca²⁺ concentration (Carvajal 2019, Ph.D Thesis), the simultaneous lack of CRISP1 and CRISP3 produced an increase in Ca²⁺ levels and the lack of the four CRISP proteins showed a decrease in the intracellular levels of the cation after capacitation (Curci et al, 2020). Based on these observations, we conclude that the absence of CRISP1 may or may not lead to altered intracellular Ca²⁺ levels depending on the other simultaneously-deleted gene/s.

The authors make a hypothesis that the increased Ca²⁺ level may lead to damaged DNA integrity by citing a published paper (lines 360-363). In the published paper, the authors examined the influence of the luminal fluid of the epididymis and vas deference on sperm chromatin fragmentation (Gawecka et al., 2015). However, they did not mention the increased DNA fragmentation in epididymal sperm when these sperm were incubated with Ca²⁺ or Mn2+. So, the authors' hypothesis is over discussion. Thus, the correlation between the intracellular Ca²⁺ level and DNA integrity in sperm is still unclear. So, the authors should show why the increased Ca²⁺ level leads to DNA fragmentation with direct evidence.

We appreciate the reviewer’s comment regarding the work by Gawecka et al., (2015), and the opportunity to clarify the proposed mechanism underlying our observations. In the above mentioned paper, the authors reported that when mouse epididymal or vas deferens sperm were incubated with divalent cations (Ca²⁺ and Mn²⁺) in the presence of luminal fluid, they were induced to degrade their DNA in a process termed sperm chromatin fragmentation (SCF). The fact that both the ejaculated and epididymal mutant sperm used in our studies had been exposed to epididymal fluid lacking CRISP proteins known to regulate sperm Ca²⁺ channels, opened the possibility that changes in Ca²⁺ levels within the epididymal fluid and/or sperm could be responsible for the higher DNA fragmentation levels observed in mutant cells. In this regard, it is important to note that, as requested by Reviewer 1, we performed additional in vitro experiments in which WT epididymal sperm were exposed to mutant or WT epididymal fluid in the presence or absence of Ca²⁺ and DNA fragmentation analyzed at the end of incubation. Results showed a significant increase in DNA fragmentation in WT sperm exposed to either mutant epididymal fluid or WT fluid in the presence of Ca²⁺ (Figure 6A). We believe these observations together with the higher intracellular Ca²⁺ levels detected in DKO sperm (Figure 6B) provides strong evidence supporting changes in Ca²⁺ homeostasis in the epididymis and sperm as the main responsible for the observed sperm DNA integrity defects. This could be mediated by the activation of Ca²⁺-dependent nucleases present within the epididymal fluid and/or sperm cells as previously suggested (Shaman et al., 2006; PMID: 16914690, Sotolongo et al., 2005; PMID: 15713834, Boaz et al., 2008; PMID: 17879959, Dominguez and Ward, 2009; PMID: 19938954). These observations have now been included and discussed in the revised version of the manuscript (see lines 245-265 and 427-439).

Minor Comments:

(3) Standards for measuring rates should be clarified, such as two-cell rates are determined by dividing the number of two-cell embryos by the total number of eggs.

As requested, standards for measuring rates have now been clarified in the corresponding figure legends

eLife Assessment

This study provides valuable information on a novel gene that regulates meiotic progression in both male and female meiosis. The evidence supporting the conclusions of the authors is solid. This study will be of interest to developmental and reproductive biologists.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors investigate the role of BEND2, a novel regulator of meiosis, in both male and female fertility. Huang et al have created a mouse model where the full-length BEND2 transcript is depleted but the truncated BEND2 version remains. This mouse model is fertile, and the authors used it to study the role of BEND2 on both male and female meiosis. Overall, the full-length BEND2 appears dispensable for male meiosis. The more interesting phenotype was observed in females. Females exhibit a lower ovarian reserve suggesting that full-length BEND2 is involved in the establishment of the primordial follicle pool.

Strengths:

The authors generated a mouse model that enabled them to study the role of BEND2 in meiosis. The role of BEND2 in female fertility is novel and enhances our knowledge of genes involved in the establishment of the primordial follicle pool.

Weaknesses highlighted previously:

The manuscript extensively explores the role of BEND2 in male meiosis; however, a more interesting result was obtained from the study of female mice.

Reviewer #2 (Public review):

In their manuscript entitled "BEND2 is a crucial player in oogenesis and reproductive aging", the authors present their findings that full-length BEND2 is important for repair of meiotic double strand break repair in spermatocytes, regulation of LINE-1 elements in spermatocytes, and proper oocyte meiosis and folliculogenesis in females. The manuscript utilizes an elegant system to specifically ablate the full-length form of BEND2 which has been historically difficult to study due to its location on the X chromosome and male sterility of global knockout animals.

The authors have been extremely responsive to reviewer critiques and have presented strong data and appropriate conclusions, making it an excellent addition to the field.

Reviewer #3 (Public review):

Huang et al. investigated the phenotype of Bend2 mutant mice which expressed truncated isoform. Bend2 deletion in male showed fertility and this enabled them to analyze the BEND2 function in females. They showed that Bend2 deletion in females showed decreasing follicle number which may lead to loss of ovarian reserve.

Strengths:

They found the truncated isoform of Bend2 and the depletion of this isoform showed decreasing follicle number at birth.

Weaknesses highlighted previously:

The authors showed novel factors that impact ovarian reserve. Although the number of follicles and conception rate are reduced in mutant mice, the in vitro fertilization rate is normal and follicles remain at 40 weeks of age. It is difficult to know how critical this is when applied to the human case.

[Editors' note: We thank the authors for considering the previous recommendations and suggested corrections.]

Author response:

The following is the authors’ response to the previous reviews.

Public Reviews:

Reviewer #1 (Public review): 

Summary: 

In this manuscript, the authors investigate the role of BEND2, a novel regulator of meiosis, in both male and female fertility. Huang et al have created a mouse model where the full-length BEND2 transcript is depleted but the truncated BEND2 version remains. This mouse model is fertile, and the authors used it to study the role of BEND2 on both male and female meiosis. Overall, the full-length BEND2 appears dispensable for male meiosis. The more interesting phenotype was observed in females. Females exhibit a lower ovarian reserve suggesting that full-length BEND2 is involved in the establishment of the primordial follicle pool. 

Strengths: 

The authors generated a mouse model that enabled them to study the role of BEND2 in meiosis. The role of BEND2 in female fertility is novel and enhances our knowledge of genes involved in the establishment of the primordial follicle pool. 

Weaknesses: 

The manuscript extensively explores the role of BEND2 in male meiosis; however, a more interesting result was obtained from the study of female mice. 

We sincerely appreciate the reviewer’s thoughtful evaluation of our work and recognition of the strengths of our study. We are especially grateful for the acknowledgment of the novelty of our findings regarding the role of BEND2 in female fertility. While we extensively characterized the e ects of BEND2 depletion in male meiosis, we agree that the phenotype observed in females provides particularly interesting insights into the establishment of the primordial follicle pool. 

Reviewer #2 (Public review): 

In their manuscript entitled "BEND2 is a crucial player in oogenesis and reproductive aging", the authors present their findings that full-length BEND2 is important for repair of meiotic double strand break repair in spermatocytes, regulation of LINE-1 elements in spermatocytes, and proper oocyte meiosis and folliculogenesis in females. The manuscript utilizes an elegant system to specifically ablate the full-length form of BEND2 which has been historically di icult to study due to its location on the X chromosome and male sterility of global knockout animals. 

The authors have been extremely responsive to reviewer critiques and have presented strong data and appropriate conclusions, making it an excellent addition to the field. 

We are truly grateful for the reviewer’s thoughtful review and recognition of the key contributions of our study. We appreciate the acknowledgment of how our model overcomes the challenges in studying BEND2 and the importance of our findings in both male and female meiosis. We also value the reviewer’s encouraging comments on our responsiveness to their feedback and the quality of our data and conclusions.

Reviewer #3 (Public review): 

Huang et al. investigated the phenotype of Bend2 mutant mice which expressed truncated isoform. Bend2 deletion in male showed fertility and this enabled them to analyze the BEND2 function in females. They showed that Bend2 deletion in females showed decreasing follicle number which may lead to loss of ovarian reserve. 

Strengths: 

They found the truncated isoform of Bend2 and the depletion of this isoform showed decreasing follicle number at birth. 

Weaknesses: 

The authors showed novel factors that impact ovarian reserve. Although the number of follicles and conception rate are reduced in mutant mice, the in vitro fertilization rate is normal and follicles remain at 40 weeks of age. It is difficult to know how critical this is when applied to the human case. 

We greatly appreciate the reviewer’s comments and recognition of the strengths of our work. We are grateful for their acknowledgment of our findings related to the truncated isoform of Bend2 and its e ect on ovarian reserve. We also agree that, although our study provides important insights, we are still far from directly applying these results to human clinical scenarios. There is much further research needed before these findings can be translated. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):: 

The authors have addressed all concerns both editorially and experimentally. This is a very nice manuscript, and I congratulate the authors on their work. 

We sincerely appreciate your kind words and thoughtful review. Your feedback has been invaluable in improving our manuscript, and we are grateful for your time and effort. Thank you for your support and encouragement!

Reviewer #2 (Recommendations for the authors):: 

In Figure 3, graphs in panels C & D have typos in the early zygotene column where it reads "zyotene". 

We appreciate your careful review and for pointing out the typos in Figure 4, which has been corrected in the new version of the manuscript. 

Reviewer #3 (Recommendations for the authors): 

・Since there are two isoforms of Bend2, and the authors depleted one isoform, this is not suitable to use "full length" in the titles and in the manuscripts. 

We respectfully disagree with the reviewer’s comment. In our mouse model, we specifically remove the full-length isoform of Bend2. Therefore, we consider it appropriate to refer to it as such in the manuscript. Our results indicate that the full-length isoform is not required to complete meiotic prophase in males but is indispensable for setting up the ovarian reserve in females. We appreciate the reviewer’s input and are happy to clarify this point further if needed.

・Is there any reason why authors used 7 month old females for in vitro fertilization? It may not be recognized as aged mice but it seems a bit old to perform IVF especially when the ovarian reserve in mutant mice is decreased. If there is any reason, please clarify it. In addition, since the authors added IVF data, which showed similar fertilization ratio between control and mutant, the authors need to discuss why the litter size was decreased in mutant mice. It may be to strong to conclude "subfertility". 

We used 7-month-old females for IVF because this falls within the age range of the samples analyzed for ovarian reserve, with the oldest females being 8 months old. Regarding the apparent discrepancy between IVF results and litter size, we addressed this in the discussion section of the manuscript: 'Interestingly, our mutant oocyte quality analysis suggests that mature oocytes from mutant females are equally competent to develop into a blastocyst as control ones. These data suggest that the subfertility observed in Bend2 mutants may be due to errors in later developmental stages, such as implantation or organogenesis.' We appreciate the reviewer’s feedback and hope this clarification helps.

eLife Assessment

This important study shows that a very slow (infraslow) oscillation occurs in voltage recordings from the dentate gyrus of the adult mouse. The authors suggest that it is related to sleep stage and serotonin acting at one type of serotonin receptor in the dentate gyrus. The results are significant because they suggest new insight into how a slow oscillation affects memory through serotonin receptors in the dentate gyrus. Convincing data are provided to support the claims.

Reviewer #1 (Public review):

Turi, Teng and the team used state of the art techniques to provide convincing evidence on the infraslow oscillation of DG cells during NREM sleep, and how serotonergic innervation modulates hippocampal activity pattern during sleep and memory. First, they showed that the glutamatergic DG cells become activated following an infraslow rhythm during NREM sleep. In addition, the infraslow oscillation in the DG is correlated with rhythmic serotonin release during sleep. Finally, they found that specific knockdown of 5-HT receptors in the DG impairs the infraslow rhythm and memory, suggesting that serotonergic signaling is crucial for regulating DG activity during sleep. Given that the functional role of infraslow rhythm still remains to be studied, their findings deepen our understanding on the role of DG cells and serotonergic signaling in regulating infraslow rhythm, sleep microarchitecture and memory.

Reviewer #2 (Public review):

Summary:

The authors investigated DG neuronal activity at the population and single cell level across sleep/wake periods. They found an infraslow oscillation (0.01-0.03 Hz) in both granule cells (GC) and mossy cells (MC) during NREM sleep. The important findings are:

(1) The antiparallel temporal dynamics of DG neuron activities and serotonin neuron activities/extracellular serotonin levels during NREM sleep<br /> (2) The GC Htr1a-mediated GC infraslow oscillation.

Strengths:

(1) The combination of polysomnography, Ca-fiber photometry, two-photon microscopy and gene depletion is technically sound. The coincidence of microarousals and dips in DG population activity is convincing. The dip in activity in upregulated cells is responsible for the dip at the population level.

(2) DG GCs express excitatory Htr4 and Htr7 in addition to inhibitory Htr1a, but deletion of Htr1a is sufficient to disrupt DG GC infraslow oscillation, supporting the importance of Htr1a in DG activity during NREM sleep.

Weaknesses from the original round of review:

(1) The current data set and analysis are insufficient to interpret the observation correctly [...].

(2) It is acceptable that DG Htr1a KO induces the reduced freezing in the CFC test (Fig. 6E, F), but it is too much of a stretch that the disruption of DG ISO causes impaired fear memory. There should be a correlation.

(3) It is necessary to describe the extent of AAV-Cre infection. The authors injected AAV into the dorsal DG (AP -1.9 mm), but the histology shows the ventral DG (Supplementary Fig. 4), which reduces the reliability of this study.

Comments on revisions:

Thank you for the clarification of the detection criteria and the quantification of the specific events. This reviewer can now follow the authors' interpretation.

Author response:

The following is the authors’ response to the previous reviews.

Public Reviews:

Reviewer #1 (Public review):

Turi, Teng and the team used state-of-the-art techniques to provide convincing evidence on the infraslow oscillation of DG cells during NREM sleep, and how serotonergic innervation modulates hippocampal activity pattern during sleep and memory. First, they showed that the glutamatergic DG cells become activated following an infraslow rhythm during NREM sleep. In addition, the infraslow oscillation in the DG is correlated with rhythmic serotonin release during sleep. Finally, they found that specific knockdown of 5-HT receptors in the DG impairs the infraslow rhythm and memory, suggesting that serotonergic signaling is crucial for regulating DG activity during sleep. Given that the functional role of infraslow rhythm still remains to be studied, their findings deepen our understanding on the role of DG cells and serotonergic signaling in regulating infraslow rhythm, sleep microarchitecture and memory.

Reviewer #2 (Public review):

Summary:

The authors investigated DG neuronal activity at the population and single cell level across sleep/wake periods. They found an infraslow oscillation (0.01-0.03 Hz) in both granule cells (GC) and mossy cells (MC) during NREM sleep. The important findings are 1) the antiparallel temporal dynamics of DG neuron activities and serotonin neuron activities/extracellular serotonin levels during NREM sleep, and 2) the GC Htr1a-mediated GC infraslow oscillation.

Strengths:

(1) The combination of polysomnography, Ca-fiber photometry, two-photon microscopy and gene depletion is technically sound. The coincidence of microarousals and dips in DG population activity is convincing. The dip in activity in upregulated cells is responsible for the dip at the population level.

(2) DG GCs express excitatory Htr4 and Htr7 in addition to inhibitory Htr1a, but deletion of Htr1a is sufficient to disrupt DG GC infraslow oscillation, supporting the importance of Htr1a in DG activity during NREM sleep.

Weaknesses:

(1) The current data set and analysis are insufficient to interpret the observation correctly.<br /> a. In Fig 1A, during NREM, the peaks and troughs of GC population activities seem to gradually decrease over time. Please address this point.

b. In Fig 1F, about 30% of Ca dips coincided with MA (EMG increase) and 60% of Ca dips did not coincide with EMG increase. If this is true, the readers can find 8 Ca dips which are not associated with MAs from Fig 1E. If MAs were clustered, please describe this properly.<br /> c. In Fig 1F, the legend stated the percentage during NREM. If the authors want to include the percentage of wake and REM, please show the traces with Ca dips during wake and REM. This concern applies to all pie charts provided by the authors.

d. In Fig 1C, please provide line plots connecting the same session. This request applies to all related figures.

e. In Fig 2C, the significant increase during REM and the same level during NREM are not convincing. In Fig 2A, the several EMG increasing bouts do not appear to be MA, but rather wakefulness, because the duration of the EMG increase is greater than 15 seconds. Therefore, it is possible that the wake bouts were mixed with NREM bouts, leading to the decrease of Ca activity during NREM. In fact, In Fig 2E, the 4th MA bout seems to be the wake bout because the EMG increase lasts more than 15 seconds.

f. Fig 5D REM data are interesting because the DRN activity is stably silenced during REM. The varied correlation means the varied DG activity during REM. The authors need to address it.

g. In Fig 6, the authors should show the impact of DG Htr1a knockdown on sleep/wake structure including the frequency of MAs. I agree with the impact of Htr1a on DG ISO, but possible changes in sleep bout may induce the DG ISO disturbance.

(2) It is acceptable that DG Htr1a KO induces the reduced freezing in the CFC test (Fig. 6E, F), but it is too much of a stretch that the disruption of DG ISO causes impaired fear memory. There should be a correlation.

(3) It is necessary to describe the extent of AAV-Cre infection. The authors injected AAV into the dorsal DG (AP -1.9 mm), but the histology shows the ventral DG (Supplementary Fig. 4), which reduces the reliability of this study.

Responses to weaknesses mentioned above have been addressed in the first revision.

Comments on revisions:

In the first revision, I pointed out the inappropriate analysis of the EEG/EMG/photometry data and gave examples. The authors responded only to the points raised and did not seem to see the need to improve the overall analysis and description. In this second revision, I would like to ask the authors to improve them. The biggest problem is that the detection criteria and the quantification of the specific event are not described at all in Methods and it is extremely difficult to follow the statement. All interpretations are made by the inappropriate data analysis; therefore, I have to say that the statement is not supported by the data.

Please read my following concerns carefully and improve them.

(1) The definition of the event is critical to the detection of the event and the subsequent analysis. In particular, the authors explicitly describe the definition of MA (microarousal), the trough and peak of the population level of intracellular Ca concentrations, or the onset of the decline and surge of Ca levels.

(1-1) The authors categorized wake bouts of <15 seconds with high EMG activity as MA (in Methods). What degree of high EMG is relevant to MA and what is the lower limit of high EMG? In Fig 1E, there are some EMG spikes, but it was unclear which spike/wave (amplitude/duration) was detected as MA-relevant spike and which spike was not detected. In Fig 2E, the 3rd MA coincides with the EMG spike, but other EMG spikes have comparable amplitude to the 3rd MA-relevant EMG spike. Correct counting of MA events is critical in Fig 1F, 2F, 4C.

We have added more information about the MA definition in Methods, including EMG amplitude. Furthermore, we have re-analyzed MA and MA-related calcium signals in Fig1 and Fig2. Fig-S1 shows the traces of EMG aptitude for all MA events show in Fig1G and Fig2G.

(1-2) Please describe the definition of Ca trough in your experiments. In Fig 1G, the averaged trough time is clear (~2.5 s), so I can acknowledge that MA is followed by Ca trough. However, the authors state on page 4 that "30% of the calcium troughs during NREM sleep were followed by an MA epoch". This discrepancy should be corrected.

We apologize for the misleading statement. We meant 30% of ISO events during NERM sleep. We have corrected this. To detect the calcium trough of ISO, we first calculated a moving baseline (blue line in Fig-S2 below) by smoothing the calcium signals over 60 s, then set a threshold (0.2 standard deviation from the moving baseline) for events of calcium decrease, and finally detected the minimum point (red dots in Fig-S2) in each event as the calcium trough. We have added these in Methods.

(1-3) Relating comment 1-2, I agree that the latency is between MA and Ca through in page 4, as the authors explain in the methods, but, in Fig 1G, t (latency) is labeled at incorrect position. Please correct this.

We are sorry for the mistake in describing the latency in the Methods. The latency was defined as the time difference between the onset of calcium decline (see details below in 1-4) and the onset of the MA. We have corrected this in the revised manuscript. Thus, the labeling in Fig1G was correct.

(1-4) The authors may want to determine the onset of the decline in population Ca activity and the latency between onset and trough (Fig 1G, latency t). If so, please describe how the onset of the decline is determined. In Fig 1G, 2G, S6, I can find the horizontal dashed line and infer that the intersection of the horizontal line and the Ca curve is considered the onset. However, I have to say that the placement of this horizontal line is super arbitrary. The results (t and Drop) are highly dependent on the position of horizontal line, so the authors need to describe how to set the horizontal line.

Indeed, we used the onset of calcium decline to calculate the latency as mentioned above. First, we defined the baseline (dashed line in Fig1G) by calculating the average of calcium signals in the10s window before the MA (from -15s to -5s in Fig1G). The onset of calcium decline is defined as the timepoint where calcium decrease was larger than 0.05 SD from this baseline. We have added these in Methods.

(1-5) In order to follow Fig 1F correctly, the authors need to indicate the detection criteria of "Ca dip (in legend)". Please indicate "each Ca dip" in Fig 1E. As a reader, I would like to agree with the Ca dip detection of this Ca curve based on the criteria. Please also indicate "each Ca dip" in Fig 2E and 2F. In the case of the 2nd and 3rd MAs, do they follow a single Ca dip or does each MA follow each Ca dip? This chart is highly dependent on the detection criteria of Ca dip.

We have indicated each ca dip in Fig 1 and Fig 2.

As I mentioned above, most of the quantifications are not based on the clear detection criteria. The authors need to re-analyze the data and fix the quantification. Please interpret data and discuss the cellular mechanism of ISO based on the re-analyzed quantification.

As suggested, we have re-analyzed the MA and MA-related photometry signals. Accordingly, parts of Fig1 and Fig2 have been revised. Although there are some small changes, the main results and conclusions remain unchanged.

Reviewer #3 (Public review):

Summary:

The authors employ a series of well-conceived and well-executed experiments involving photometric imaging of the dentate gyrus and raphe nucleus, as well as cell-type specific genetic manipulations of serotonergic receptors that together serve to directly implicate serotonergic regulation of dentate gyrus (DG) granule (GC) and mossy cell (MC) activity in association with an infra slow oscillation (ISO) of neural activity has been previously linked to general cortical regulation during NREM sleep and microarousals.

Strengths:

There are a number of novel and important results, including the modulation of dentage granule cell activity by the infraslow oscillation during NREM sleep, the selective association of different subpopulations of granule cells to microarousals (MA), the anticorrelation of raphe activity with infraslow dentate activity.

The discussion includes a general survey of ISOs and recent work relating to their expression in other brain areas and other potential neuromodulatory system involvement, as well as possible connections with infraslow oscillations, micro arousals, and sensory sensitivity.

Weaknesses:

- The behavioral results showing contextual memory impairment resulting from 5-HT1a knockdown are fine, but are over-interpreted. The term memory consolidation is used several times, as well as references to sleep-dependence. This is not what was tested. The receptor was knocked down, and then 2 weeks later animals were found to have fear conditioning deficits. They can certainly describe this result as indicating a connection between 5-HT1a receptor function and memory performance, but the connection to sleep and consolidation would just be speculation. The fact that 5-HT1a knockdown also impacted DG ISOs does not establish dependency. Some examples of this are:

– The final conclusion asserts "Together, our study highlights the role of neuromodulation in organizing neuronal activity during sleep and sleep-dependent brain functions, such as memory.", but the reported memory effects (impairment of fear conditioning) were not shown to be explicitly sleep-dependent.

– Earlier in the discussion it mentions "Finally, we showed that local genetic ablation of 5-HT1a receptors in GCs impaired the ISO and memory consolidation". The effect shown was on general memory performance - consolidation was not specifically implicated.

– The assertion on page 9 that the results demonstrate "that the 5-HT is directly acting in the DG to gate the oscillations" is a bit strong given the magnitude of effect shown in Fig. 6D, and the absence of demonstration of negative effect on cortical areas that also show ISO activity and could impact DG activity (see requested cortical sigma power analysis).

– Recent work has shown that abnormal DG GC activity can result from the use of the specific Ca indicator being used (GCaMP6s). (Teng, S., Wang, W., Wen, J.J.J. et al. Expression of GCaMP6s in the dentate gyrus induces tonic-clonic seizures. Sci Rep 14, 8104 (2024). https://doi.org/10.1038/s41598-024-58819-9). The authors of that study found that the effect seemed to be specific to GCaMP6s and that GCaMP6f did not lead to abnormal excitability. Note this is of particular concern given similar infraslow variation of cortical excitability in epilepsy (cf Vanhatalo et al. PNAS 2004). While I don't think that the experiments need to be repeated with a different indicator to address this concern, you should be able to use the 2p GCaMP7 experiments that have already been done to provide additional validation by repeating the analyses done for the GCaMP6s photometry experiments. This should be done anyway to allow appropriate comparison of the 2p and photometry results.

– While the discussion mentions previous work that has linked ISOs during sleep with regulation of cortical oscillations in the sigma band, oddly no such analysis is performed in the current work even though it is presumably available and would be highly relevant to the interpretation of a number of primary results including the relationship between the ISOs and MAs observed in the DG and similar results reported in other areas, as well as the selective impact of DG 5-HT1a knockdown on DG ISOs. For example, in the initial results describing the cross correlation of calcium activity and EMG/EEG with MA episodes (paragraph 1, page 4), similar results relating brief arousals to the infraslow fluctuation in sleep spindles (sigma band) have been reported also at .02 Hz associated with variation in sensory arousability (cf. Cardis et al., "Cortico-autonomic local arousals and heightened somatosensory arousability during NREMS of mice in neuropathic pain", eLife 2021). It would be important to know whether the current results show similar cortical sigma band correlations. Also, in the results on ISO attenuation following 5-HT1 knockdown on page 7 (fig. 6), how is cortical EEG affected? is ISO still seen in EEG but attenuated in DG?

– The illustrations of the effect of 5-HT1a knockdown shown in Figure 6 are somewhat misleading. The examples in panels B and C show an effect that is much more dramatic than the overall effect shown in panel D. Panels B and C do not appear to be representative examples. Which of the sample points in panel D are illustrated in panels B, C? it is not appropriate to arbitrarily select two points from different animals for comparison, or worse, to take points from the extremes of the distributions. If the intent is to illustrate what the effect shown in D looks like in the raw data, then you need to select examples that reflect the means shown in panel D. It is also important to show the effect on cortical EEG, particularly in sigma band to see if the effects are restricted to the DG ISOs. It would also be helpful to show that MAs and their correlations as shown in Fig 1 or G as well as broader sleep architecture are not affected.

– On page 9 of the results it states that GCs and MCs are upregulated during NREM and their activity is abruptly terminated by MAs through a 5-HT mediated mechanism. I didn't see anything showing the 5-HT dependence of the MA activity correlation. The results indicate a reduction in ISO modulation of GC activity but not the MA correlated activity. I would like to see the equivalent of Fig 1,2 G panels with the 5-HT1a manipulation.

Responses to Revewer#3 have been addressed in the first revision. 

Reviewer #1 (Recommendations for the authors):

Minor comment: Several recent publications from different laboratories have shown rhythmic release of norepinephrine (NE) (~0.03 Hz) in the medial prefrontal cortex, the thalamus, and in the locus coeruleus (LC) of the mouse during sleep-wake cycles-> Please add "preoptic area" here

We have added the citation.

Reviewer #2 (Recommendations for the authors):

Minor

(1) (abstract, page 2 line 9) what kind of "increased activity" did the authors find?

Increased activity compared to that during wakefulness. We have added this.

(2) (result, page 4) please define first, early, and late stage of NREM sleep in the methods.

We have added these in the Methods.

(3) (result, page 6) please define "the risetime of the phasic increase".

It refers to the latency between the increase of 5-HT and the MA onset. We have clarified this in the text.

(4) (supplement Fig 3 legend) please reword "5-HT events" and "5-HT signals" because these are ambiguous.

We have defined the events in the legend.

(5) (Fig 5A) please replace the picture without bubbles.

We have replaced the image in Fig5A.

eLife Assessment

This important manuscript proposes a dual behavioral/computational approach to assess emotional regulation in humans. The authors present solid evidence for the idea that emotional distancing (as routinely used in clinical interventions for e.g. mood and anxiety disorders) enhances emotional control.

Reviewer #1 (Public review):

Summary:

Using sequences of short videos to elicit emotional changes in participants, Malamud & Huys demonstrate how a brief, controlled emotion regulation intervention (distancing) can effectively alter subsequent emotion ratings. The authors employ latent state-space models to capture the trajectories of emotion ratings, leveraging tools from control theory to quantify the intervention's impact on emotion dynamics.

Strengths:

The experiment is well-designed and tailored to the computational modeling approach advanced in the paper. It also relies on a selection of stimuli that were previously validated. Within the constraints of a controlled experiment, the intervention successfully implements a relatively common tool of psychotherapeutic treatment, ensuring its clinical relevance.

The computational modeling is grounded in the well-established framework of dynamical systems and control theory. This foundation offers a conceptually clear formalization along with powerful quantification tools that go beyond previous more data-driven approaches.

Overall, the study presents a coherent approach that bridges concepts from clinical psychology and computational theories, providing a timely stepping stone toward advancing quantified, evidence-based psychological interventions targetting emotion control.

Weaknesses:

A primary limitation of this study, acknowledged by the authors, is its reliance on self-reports of participants' emotional states. Although considerable effort was made to minimize expectation effects, further research is needed to confirm that the observed behavioral changes reflect genuine alterations in emotional states. Additionally, the generalizability of the findings to long-term remediation strategies remains an open question.

Second, the statistical analysis, particularly the computational approach, sometimes lacks sufficient detail and refinement. While I will not elaborate on specific points here, one notable issue is the interpretation of the intrinsic matrix (A). The model-free analysis reveals correlations between emotions at a given time or within an emotional state across time points. However, it does not provide evidence to support lagged interactions across states that would justify non-diagonal elements in A. The other result concerning the dynamics matrix only highlights a trend in the dominant eigenvalue, which is difficult to interpret in isolation. The absence of a statistically significant group x intervention interaction furthermore makes this finding a little compelling. This weakens the study's conclusions about the importance of intrinsic dynamics, as claimed in the title.

Finally, to avoid potential misunderstandings of their work, the authors should be more careful about their use of terms pertaining to the control theory and take the time to properly define them. For example, the "controllability" of emotional states can either denote that those states are more changeable (control theory definition), or, conversely, more tightly regulated (common interpretation, as used in the abstract). This is true for numerous terms (stability, sensitivity, Gramian, etc.) for which no clear definition nor references are provided. Readers unfamiliar with the framework of control theory will likely be at a loss without more guidance.

Reviewer #2 (Public review):

Summary:

In this well-conceived and timely study, the authors assess the controllability of emotions in a quantitative way using the framework of control theory. They use a controlled distancing intervention halfway through an emotion rating task where emotion-inducing short videos from a validated database are shown and find that the intervention enables a better controllability of externally induced emotions in the experimental group.

Strengths:

It is a highly original idea to address the external controllability of emotions using the formal framework of control theory. It is also a very propitious approach to take what could be called a 'micro-therapeutic' perspective which looks at the immediate effect of an intervention instead of the 'macro-therapeutic' mid- or long-term effect of a whole course of therapy.

Weaknesses:

Acquiring data online inevitably gives rise to selection and self-selection effects. This needs to be acknowledged clearly. Exacerbating this, participant remuneration seems low at an amount below the minimum or living wage in Western countries (do the authors know where their participants came from?).

Another concern is that the intervention does not simply take place before the second block begins but is ongoing during the whole of the second block in that it is integrated into the phrasing of the task on each trial. It is therefore somewhat misleading to speak of a period 'after the intervention', and it would have been interesting to assess the effect of this by including a third group where the phrasing does not change, but the floating leaves intervention takes place.

As mentioned in the Limitations section, observation noise was assumed and not estimated. While this is understandable in this case, the effect of this assumption could have been assessed by simulation with varying levels of observation (and process) noise.

Relatedly, the reliance on formal model comparison is unfortunate since the outcome of such comparisons is easily influenced by slight changes to assumptions such as noise levels. An alternative approach would have been to develop a favoured model based on its suitability to address the research question and its ability, established by simulation, to distill relevant changes of behaviour into reliable parameter estimates.

The statistical analyses clearly show the limitations of classical statistical testing with highly complex models of the kind the authors (commendably) use. Hunting for statistically significant interactions in a multivariate repeated-measures design relying on inputs from time series-derived point estimates is a difficult proposition. While the authors make the best of the bad situation they create by using null-hypothesis significance testing, a more promising approach would have been to estimate parameters using a sampler like Stan or PyMC and then draw conclusions based on posterior predictive simulations.

Reviewer #3 (Public review):

Summary:

The manuscript takes a dynamical systems perspective on emotion regulation, meaning that rather than a simplistic model conceptualising regulation as applying to a single emotion (e.g. regulation of sadness), emotion regulation could cause a shift in the dynamics of a whole system of emotions (which are linked mathematically to one another). This builds on the idea that there are 'attractor states' of emotions between which people transition, governed by both the system's intrinsic characteristics (e.g. temporal autocorrelation of a particular emotion/person) and external driving forces (having a stressful week). Conceptually this is a very useful advance because it is very unlikely that emotions are elicited (or reduced) singly, without affecting other emotions. This paper is a timely implementation of these ideas in the context of psychotherapeutic intervention, distancing, which participants were trained (randomised) to perform while watching emotion-inducing videos.

The authors' main conclusion is that distancing both stabilises specific emotional patterns and reduces the impact of external video clips. I would consider these results strong and believable, and to have the potential to impact models of emotion regulation as well as the field's broader views on the mechanisms of psychological therapies.

Strengths:

This paper has very many strengths: I would especially note the authors' very-well-matched active control condition and the robustness of their model comparison approach. One feature of the authors' approach is that they explicitly add noise - not what you typically see in an emotion time-series analysis - which allows participants to make errors in their own subjective ratings (a reasonable thing to assume); this noise can then be smoothed during filtering. In their model comparison approach, they explicitly test whether a true dynamical system explains emotion change/emotion regulation effect on emotions - demonstrating that both intrinsic dynamics and external inputs were needed to explain subjective emotion. Powerfully, they also used this approach to test the differential effects of the treatment groups (see below).

The main result seems quite robust statistically. Verifying the effects of the distancing intervention on emotion, the authors found an interaction between time (pre- to post-intervention) and intervention group (distancing vs. relaxation) suggesting that distancing (but not relaxation) reduced ratings of almost all emotions. Participants allocated to the distancing intervention also showed decreased variability of emotion ratings compared to those in the relaxation intervention (though note this interaction was not significant).

Using a model comparison approach, the authors then demonstrated that whilst the control group was best explained by a model that did not change its dynamics of emotions, the active intervention (distancing) group was best explained by a model that captured both changing emotion dynamics and a changing input weights (influence of the videos) - results confirmed in follow-up analyses. This is convincing evidence that emotion regulation strategies may specifically affect the dynamics of emotions - both their relationships to one another and their susceptibility to changes evoked by external influences.

The authors also perform analyses that suggest their result is not attributable to a demand effect (finding that participants were quicker during the control intervention, which one would expect if they had already decided how to respond in advance of the emotion question). I personally also think a demand effect is unlikely given the robustness of their control intervention (which participants would be just as likely to interpret as mental health-enhancing training as distancing), and I am convinced by the notion that demand effects would be unlikely to elicit their more specific effects on the dynamic quality of emotions.

Weaknesses:

An interesting but perhaps at present slightly confusing aspect of their described results relates to the 'controllability' of emotions, which they define as their susceptibility to external inputs. Readers should note this definition is (as I understand it) quite distinct from, and sometimes even orthogonal to, concepts of emotional control in the emotion literature, which refer to intentional control of emotions (by emotion regulation strategies such as distancing). The authors also use this second meaning in the discussion. Because of the centrality of control/controllability (in both meanings) to this paper, at present it is key for readers to bear these dual meanings in mind for juxtaposed results that distancing "reduces controllability" while causing "enhanced emotional control".

As above the authors use an active control - a relaxation intervention - which is extremely closely matched with their active intervention (and a major strength). However, there was an additional difference between the groups (as I currently understand it): "in the group allocated to the distancing intervention, the phrasing of the question about their feelings in the second video block reminded participants about the intervention, stating: "You observed your emotions and let them pass like the leaves floating by on the stream." I do wonder if the effects of distancing also have been partially driven by some degree of reappraisal (considered a separate emotion regulation strategy) since this reminder might have evoked retrospective changes in ratings.

Not necessarily a weakness, but an unanswered question is exactly how distancing is producing these effects. As the authors point out, there is a possibility that eye-movement avoidance of the more emotionally salient aspects of scenes could be changing participants' exposure to the emotions somewhat. Not discussed by the authors, but possibly relevant, is the literature on differences between emotion types on oculomotor avoidance, which could have contributed to differential effects on different emotions.

Author response:

Reviewer 1:

A primary limitation of this study, acknowledged by the authors, is its reliance on self-reports of participants’ emotional states. Although considerable effort was made to minimize expectation effects, further research is needed to confirm that the observed behavioral changes reflect genuine alterations in emotional states.

Thank you very much for raising this point. We fully agree that self-reported emotional states are inherently subjective and that the ramifications of this need to be clarified in the manuscript. However, we would suggest that the focus on self-report may be a strength rather than a limitation. First, the regularities and rules underlying and determining emotional self-report are of primary importance and interest in their own right, and the work presented here does, we believe, shed light on a rich structure present in multivariate timeseries of subjective self-reports and their response to external inputs. Second, there is no clear definition of what a ”genuine emotion state” might be; particularly if there is a discrepancy with self-reported emotions.

Additionally, the generalizability of the findings to long-term remediation strategies remains an open question.

Yes, we agree that what we have described is limited to a short-term intervention and change.

Whether these changes bear on longer-term changes remains to be assessed. Furthermore, the mechanisms or processes that would support such a maintenance are of substantial interest, and will be the focus of future work.

Second, the statistical analysis, particularly the computational approach, sometimes lacks sufficient detail and refinement. While I will not elaborate on specific points here, one notable issue is the interpretation of the intrinsic matrix (A). The model-free analysis reveals correlations between emotions at a given time or within an emotional state across time points. However, it does not provide evidence to support lagged interactions across states that would justify non-diagonal elements in A. The other result concerning the dynamics matrix only highlights a trend in the dominant eigenvalue, which is difficult to interpret in isolation. The absence of a statistically significant group x intervention interaction furthermore makes this finding a little compelling. This weakens the study’s conclusions about the importance of intrinsic dynamics, as claimed in the title.

We appreciate the reviewer’s detailed feedback on the statistical analysis and interpretation of the intrinsic dynamics matrix. It is true that the model-free analysis as presented focuses on within-state correlations and that we have not provided such model-free evidence for lagged interactions across states. We do note that the model comparison suggested that the intervention caused changes in the full A matrix. This would be unlikely if there had not been meaningful cross-emotion lagged effects. Similarly, inference of the A matrix could have revealed a diagonal matrix, and we preferred not to impose such an assumption a priori, as it is very restrictive. Nevertheless, in the absence of a statistically significant group x intervention interaction, the findings regarding the A matrix are less compelling than those related to the control analyses. While this is likely due to a lack of statistical power, these are important points which we will consider in more detail in the revision.

Finally, to avoid potential misunderstandings of their work, the authors should be more careful about their use of terms pertaining to the control theory and take the time to properly define them. For example, the ”controllability” of emotional states can either denote that those states are more changeable (control theory definition), or, conversely, more tightly regulated (common interpretation, as used in the abstract). This is true for numerous terms (stability, sensitivity, Gramian, etc.) for which no clear definition nor references are provided. Readers unfamiliar with the framework of control theory will likely be at a loss without more guidance.

Thank you for this point. We recognize the potential for misunderstanding due to the dual usage of terms such as ”controllability” and will improve the clarity to avoid any misunderstanding.

Reviewer 2:

Acquiring data online inevitably gives rise to selection and self-selection effects. This needs to be acknowledged clearly. Exacerbating this, participant remuneration seems low at an amount below the minimum or living wage in Western countries (do the authors know where their participants came from?).

Thank you for this point. We certainly agree that different experimental settings can induce different biases, and this is no different for online settings. However, online tasks such as the one used here, have become accepted, and there is now a substantial literature showing that in-lab effects are often well-replicated in online settings (Gillan and Rutledge, 2021) . For the current study, it is not clear that an inperson setting may not induce comparably complex biases, e.g. to do with differences between experimenters. All participants were from the UK. Remuneration rates were comparable to other experimental settings, in keeping with other online studies, UK living wage recommendations, and ultimately determined according to institutional ethical guidance.

Another concern is that the intervention does not simply take place before the second block begins but is ongoing during the whole of the second block in that it is integrated into the phrasing of the task on each trial. It is therefore somewhat misleading to speak of a period ’after the intervention’, and it would have been interesting to assess the effect of this by including a third group where the phrasing does not change, but the floating leaves intervention takes place.

Thank you for this point. We acknowledge that the phrasing of the emotion question in the second block may have influenced the observed effects. Including a third group without the reminder would have provided valuable insights and is an important consideration for future studies. We will acknowledge this limitation.

As mentioned in the Limitations section, observation noise was assumed and not estimated. While this is understandable in this case, the effect of this assumption could have been assessed by simulation with varying levels of observation (and process) noise.

Thank you for this comment. We would like to clarify that both observation noise and process noise were estimated in the analyses. We will ensure this is emphasized better in the revised version to avoid future misunderstandings.

Relatedly, the reliance on formal model comparison is unfortunate since the outcome of such comparisons is easily influenced by slight changes to assumptions such as noise levels. An alternative approach would have been to develop a favoured model based on its suitability to address the research question and its ability, established by simulation, to distill relevant changes of behaviour into reliable parameter estimates.

We agree that model comparison alone is insufficient. This is why we have also included extensive simulations, including posterior predictive checks, and have followed established best-practice procedures (Wilson and Collins, 2019). We have focused on a relatively simple model space to avoid overfitting to the dataset, and hence reduce the risk of spurious findings. While we agree that outcomes will be influenced by underlying assumptions, this would persist with the suggested approach of relying on a favoured model. Simulations themselves rely on predefined structures and noise specifications, which inherently shape parameter recovery and inference. Relying only on a favoured model might risk model misspecification, whereby the model may not actually capture the data, and the parameters intended to capture the intervention effect could be confounded. We will clarify the reasoning behind our approach in the revised version.

The statistical analyses clearly show the limitations of classical statistical testing with highly complex models of the kind the authors (commendably) use. Hunting for statistically significant interactions in a multivariate repeated-measures design relying on inputs from time seriesderived point estimates is a difficult proposition. While the authors make the best of the bad situation they create by using null-hypothesis significance testing, a more promising approach would have been to estimate parameters using a sampler like Stan or PyMC and then draw conclusions based on posterior predictive simulations.

This comment raises several interesting points. First, we agree that the value of classical test on individual parameters within such complex situations is limited. This is why our main focus is on global measures like model comparison. Our use of the classical tests is more to support the understanding of the nature of the data, i.e. they have a more descriptive aim. We will hope to clarify this further in the revision. Second, in terms of sampling, we would like to emphasize that the Kalman filter is both efficient and analytical tractable, making it well-suited to our data and research question. It may have been possible to use sampling to obtain posterior distributions rather than point estimates. However, we did not judge this to be worth the (substantial) additional computational cost.

Reviewer 3:

An interesting but perhaps at present slightly confusing aspect of their described results relates to the ’controllability’ of emotions, which they define as their susceptibility to external inputs. Readers should note this definition is (as I understand it) quite distinct from, and sometimes even orthogonal to, concepts of emotional control in the emotion literature, which refer to intentional control of emotions (by emotion regulation strategies such as distancing). The authors also use this second meaning in the discussion. Because of the centrality of control/controllability (in both meanings) to this paper, at present it is key for readers to bear these dual meanings in mind for juxtaposed results that distancing ”reduces controllability” while causing ”enhanced emotional control”.

We fully agree with the reviewer’s observation that ”controllability” can be interpreted in different ways. we will revise the text to ensure consistent usage and explicitly state the distinction between the control theory definition of controllability and its interpretation in the emotion regulation literature.

As above the authors use an active control - a relaxation intervention - which is extremely closely matched with their active intervention (and a major strength). However, there was an additional difference between the groups (as I currently understand it): ”in the group allocated to the distancing intervention, the phrasing of the question about their feelings in the second video block reminded participants about the intervention, stating: ”You observed your emotions and let them pass like the leaves floating by on the stream.” I do wonder if the effects of distancing also have been partially driven by some degree of reappraisal (considered a separate emotion regulation strategy) since this reminder might have evoked retrospective changes in ratings.

We appreciate this substantial point. While our study was designed to isolate the effects of distancing, we acknowledge that elements of reappraisal may also have influenced the results. We will discuss this in the revised version. Additionally, as noted in our response to Reviewer 2, including a third group without the reminder could have provided valuable information, and we consider this to be an important direction for future research.

Not necessarily a weakness, but an unanswered question is exactly how distancing is producing these effects. As the authors point out, there is a possibility that eye-movement avoidance of the more emotionally salient aspects of scenes could be changing participants’ exposure to the emotions somewhat. Not discussed by the authors, but possibly relevant, is the literature on differences between emotion types on oculomotor avoidance, which could have contributed to differential effects on different emotions.

Thank you very much for these suggestions. It is very true that different emotions can elicit different patterns of oculomotor avoidance, which could have contributed to our observed effects. Research suggests that emotions such as disgust are associated with visual avoidance (Armstrong et al., 2014; Dalmaijer et al., 2021), whereas anxiety and other negative emotions exhibited increased attentional bias after fear conditioning (Kelly and Forsyth, 2009; Pischek-Simpson et al., 2009). It would be very interesting to repeat the experiment with eye-tracking to examine these possibilities. What would be particularly interesting to examine is whether a distancing intervention induces multiple, emotionally-specific behaviours, or not.

References

Armstrong, T., McClenahan, L., Kittle, J., and Olatunji, B. O. (2014). Don’t look now! Oculomotor avoidance as a conditioned disgust response. Emotion (Washington, D.C.), 14(1):95–104.

Dalmaijer, E. S., Lee, A., Leiter, R., Brown, Z., and Armstrong, T. (2021). Forever yuck: Oculomotor avoidance of disgusting stimuli resists habituation. Journal of Experimental Psychology. General, 150(8):1598– 1611.

Gillan, C. M. and Rutledge, R. B. (2021). Smartphones and the Neuroscience of Mental Health. Annual Review of Neuroscience, 44(Volume 44, 2021):129–151. Publisher: Annual Reviews.

Kelly, M. M. and Forsyth, J. P. (2009). Associations between emotional avoidance, anxiety sensitivity, and reactions to an observational fear challenge procedure. Behaviour Research and Therapy, 47(4):331–338. Place: Netherlands Publisher: Elsevier Science.

Pischek-Simpson, L. K., Boschen, M. J., Neumann, D. L., and Waters, A. M. (2009). The development of an attentional bias for angry faces following Pavlovian fear conditioning. Behaviour Research and Therapy, 47(4):322–330.

Wilson, R. C. and Collins, A. G. (2019). Ten simple rules for the computational modeling of behavioral data. eLife, 8:e49547. Publisher: eLife Sciences Publications, Ltd.

eLife Assessment

This important study has modified ChIP-seq and 4C-seq procedures with a urea step and shows that this drastically changes the pattern of chromatin interactions observed for SATB1 but not other proteins (CTCF, Jarid2, Suz12, Ezh2). Multiple controls make the data convincing. The findings shed new light on the role of SATB1 in genome organization and will be of interest to those who study chromosome structure and nuclear organization.

Reviewer #1 (Public review):

Summary:

The nuclear protein SATB-1 was originally identified as a protein of the 'nuclear matrix', an aggregate of nuclear components that arose upon extracting nuclei with high salt. While the protein was assumed to have a global function in chromatin organization, it has subsequently been linked to a variety of pathological conditions, notably cancer. The mapping of the factor by conventional ChIP procedures showed strong enrichment in active, accessible chromatin, suggesting a direct role in gene regulation, perhaps in enhancer-promoter communication. These findings did not explain why SATB-1-chromatin interaction resisted the 2 M salt extraction during early biochemical fractionation of nuclei.

The authors, who have studied SATB-1 for many years, now developed an unusual variation of the ChIP procedure, in which they purify crosslinked chromatin by centrifugation through 8 M urea. Remarkably, while they lose all previously mapped signals for SATB-1 in active chromatin, they now gain many binding events in silent regions of the genome, represented by lamin-associated domains (LADs).

SATB-1 had previously been shown by the authors and others to bind to DNA with special properties, termed BUR (for 'base-unpairing regions'). BURs are AT-rich and apparently enriched in equally AT-rich LADs. The 'urea-ChIP' pattern is essentially complementary to the classical ChIP pattern. The authors now speculate that the previously known SATB-1 binding pattern, which does not overlap BURs particularly well, is due to indirect chromatin binding, whereas they consider the urea-ChIP profile that fits better to the BUR distribution on the chromosome to be due to direct binding.

Building on the success with urea-ChIP the authors adapted the 4C-procedure of chromosome conformation mapping to work with urea-purified chromatin. The data suggest that BUR-bound SATB-1 in heterochromatin mediates long-distance interaction with loci in active chromatin. They close with a model, whereby SATB-1 tethers active chromatin to the nuclear lamina. Because cell type-specific differences are observed, they suggest that the SATB-1 interactions are functionally relevant.

Strengths:

Given the unusual finding of essentially mutually exclusive 'standard ChIP' and 'urea-ChIP' profiles for SATB-1, the authors conducted many appropriate controls. They showed that all SATB-1 peaks in urea-ChIP and 96% of peaks in standard-ChIP represent true signals, as they are not observed in a SATB-1 knockout cell line. They also show that urea-ChIP and standard ChIP yield similar profiles for CTCF. The data appear reproducible, judged by at least two replicates and triangulation. The SATB-1 KO cells provide a nice control for the specificity of signals, including those that arise from their elaborately modified 4C protocol.

Weaknesses:

The weaknesses mainly relate to missing qualifier statements and overinterpretations. I also found some aspects of the model not yet well supported by the data.

(1) Under high urea conditions the BUR elements should be rendered single-stranded, and one wonders whether this has any effect on the procedure. The authors should alert the reader of these circumstances.

(2) An important conclusion is that urea-ChIP reveals direct DNA binding events, whereas standard ChIP shows indirect binding (which is stripped off by urea). I do not yet see any evidence for direct binding. It cannot be excluded, for example, that the binding is RNA-mediated. The authors mention in passing that urea-ChIP material still contains (specific!) RNA. Given that this is a new procedure, the authors should document the RNA content of urea-ChIP and RNase-treat their samples prior to ChIP to monitor an RNA contribution.

(3) An important aspect of the model is that SATB-1 tethers active genes to inactive LADs. However, in the 4C experiment the BUR elements used to anchor the looping are both in the accessible, active chromatin domain.

Reviewer #2 (Public review):

Summary:

The report by Kohwi-Shigematsu et al. describes the key observation that SATB1 binds directly to so-called BUR elements. This is in contrast to several other reports describing SATB1 binding to promoters and enhancers. This discrepancy is explained by the authors to depend on the features of the ChIP technique being used. Urea-ChIP, innovated by the authors, strips off protein-protein interactions that are maintained in conventional ChIP. The authors convincingly make the case that SATB1 and the key genome organiser CTCF co-localize by conventional ChIP but not urea ChIP, as particularly evident in Figure 2A. SATB1 controls long-range interactions in thymocytes and the expression of gene clusters. This feature is independent of TADs, as the knockdown of SATB1 expression does not affect the TAD patterns.

Strengths:

A new and innovative adaptation of the urea ChIP-seq technique has enabled the authors to reveal a new aspect of SATB1 binding to the genome. The authors provide a wealth of data to reinforce their claims. This report thus sheds new light on SATB1 function, which is particularly important given its role in metastasising cancer cells.

Weaknesses:

No weaknesses were identified by this reviewer.

eLife Assessment

This important study investigates the different mechanisms that provide instructions for a missing body part to regenerate its appropriate identity. The authors use two species of planarians to identify a key role for bodywide canonical Wnt gradients in controlling the outcome of regeneration. The study provides convincing evidence for variable regeneration efficiency among planarian species that will be of interest to developmental biologists interested in regeneration. However, some of the results are over-interpreted and the additional experiments could provide better support for the authors' claims.

Reviewer #1 (Public review):

Summary:

In the manuscript entitled 'A comparative analysis of planarian regeneration specificity reveals tissue polarity contributions of the axial cWnt signalling gradient.' Cleland et al. study the robustness of regenerating a head or a tail in the proper position in two different planarian species (S. mediterranea and G. sinensis). The authors find that the expression of notum, a Wnt inhibitor that is triggered after any cut, shows different dynamics of expression in both planarian species, being more symmetrical in the species that display a higher number of double-headed or Janus heads (G. sinenesis), which they refer to a less robust regeneration. The authors claim that the reduced robustness of G. sinensis regeneration is partially explained by this anterior-posterior symmetric expression of notum, since in S. mediterranea, which shows a 'robust regeneration' it appears asymmetric. So, the first claim of the manuscript is that the symmetry in notum expression could underlie the poor robustness of regenerating a head/tail in small bipolar regenerating planarian fragments.

Then, they analyse the role of a proposed tail-to-head cWnt signalling gradient during the regeneration of heads and tails in the same planarian species. To do so they develop an antibody that allows the quantification of b-catenin activity along the AP axis, together with a pharmacological approach that reduces the pre-existent cWnt gradient without affecting the wound-induced. Through this strategy the authors can demonstrate the slope of the b-catenin activity, which is a very nice result, and that it changes according to the size of the animal. Furthermore, they are able to demonstrate that by reducing the cWnt signalling in the pre-existent tissue, there is an increase in the number of double-headed regenerates (Janus heads) and that it depends on the body size and on the decreasing steepness of the cWnt gradient. This result relies on G. sinensis species since the drug is not so effective in S. mediterranea. Thus, the authors' second claim is that the slope of the cWnt gradient may contribute to head-tail regeneration specificity in planarians.

To conclude, it is proposed that regeneration of the correct identity in each wound depends on multiple cues acting in parallel and that their species-specificity provides variations in the regenerative capability of the different planarian species.

The study has great potential to have a high impact on the regeneration community, since the opportunity to compare mechanisms between close species provides the framework for understanding the essential mechanism of regeneration.

Strengths:

The project has several strengths. The authors are able to reproduce the Janus heads phenotypes described by Morgan TH by analysing different planarian species. This is of great importance in the planarian field, because with the current model species, S. mediterranea, this could not be reproduced. So, these results demonstrate that small planarian fragments do make errors during regeneration, giving rise to double-headed animals, which supports the well-known hypothesis that it exists an anteroposterior gradient underlying anteroposterior identity during regeneration. However, and importantly, it does not occur in all planarian species. So, there are differences between planarian species in the robustness of regeneration and may be in the mechanisms that drive this regeneration. The finding of different behaviours and gene expressions in different planarian species is very interesting and promising in the field of regeneration.

A second strength of the study is the demonstration of the b-catenin1 slope in planarians and how it changes with the animal size, and also the establishment of a method to decrease it in the pre-existent tissue but not in the wound. This strategy allows us to examine specifically the role of the pre-existent cWnt signal, demonstrating that it does have a role in the decision of making head or tail during regeneration, which was an essential question in the field of planarians and animal regeneration.

Weaknesses:

(1) The finding that notum, which is the main head determinant identified in planarians, has a different dynamic in both planarian species is very suggestive. However, the different dynamics of notum expression during regeneration, which is the basis of the subsequent rationale, is not properly demonstrated, nor is its correlation with the robustness in regenerating a proper head/tail identity. Main concerns regarding this point:

a) The authors observe that 'In regenerating S. mediterranea 2 mm trunk pieces cut from 6 mm animals, notum expression was induced predominantly at anterior-facing wounds as early as 6 h post-amputation (Figure 2A), as previously reported (Petersen and Reddien 2011)'. However, in the graphics in Figures 2B and C, the expression of notum at 6h is shown as symmetric. It definitely does not agree with the in situ, with the text, or with the published data. How was it measured? It should be corrected and explained since it is the basis of the subsequent rationale.

b) Then, when measuring notum in G. sinensis the authors conclude: 'Strikingly and in sharp contrast to S. mediterranea, the number of notum expressing cells was nearly identical between anterior and posterior wounds without any discernible A/P asymmetry at any of the examined time points (Figures 2E-F)'. However, in the in situ results of 12 h regenerating G. sinensis, there is a clear difference in notum expression between anterior and posterior wounds. Is it not representative of the image? Again, how exactly the measurements were performed? Are dots or pixels quantified? It is not explained in the text. This is a crucial result that has to be consistent.

c) A more general weakness of this part of the manuscript is that even if the authors demonstrate that in G. sinensis the expression of notum is symmetrical in contrast to S. mediterranea, this is just an observation of 1 species that has symmetrical notum and regenerates less robustly than 1 species that has asymmetrical expression and regenerates more robustly. If they for instance look at the expression of wnt1, maybe they also see differences between both species that could be linked to their different regeneration properties (related to this, see below the comment on wnt1 expression). That is to say, comparing 1 to 1 species cannot give any cause-effect evidence.<br /> Furthermore, the authors rely on the fact that notum inhibition rescues the wild-type phenotype to conclude that is the symmetric expression of notum that underlies the appearance of Janus heads. This is what can be read in the results: 'Significantly, the rescue of wild-type regenerates by notum(RNAi) suggests that the symmetric G. sinensis notum expression contributes to the formation of double-heads and thus to reduced regeneration specificity'; and in the Summary: We found that the reduced regeneration robustness of G. sinensis was partially explained by wound site-symmetric expression of the head determinant notum, which is highly anterior-specific in S. mediterranea.' However, notum RNAi decreases notum in both wounds, so it does not produce an asymmetric expression (at least this is not shown). So, it does not link the symmetry or asymmetry of notum with the appearance of Janus heads.

d) If the authors want to maintain the claim that the symmetry of notum is one of the reasons that explain the increase in Janus head phenotype in G. sinensis, there are several possibilities to test it. For instance:

i) Analyse notum expression in different planarian species and relate its symmetry or asymmetry with the appearance of Janus heads. If the claim is true, the species that are more robust should show more asymmetric expression of notum. This would sustain strongly the first claim, and would really be a breakthrough in the field of regeneration.

ii) Another possibility is a more in-depth analysis of notum expression in the species of the study. If the authors show that larger fragments show fewer Janus heads, and also that it depends on the anteroposterior level of the fragments, they could try to relate the rate of Janus heads with the degree of asymmetry in notum expression in both wounds. For instance, they could analyze notum expression in bipolar regenerating fragments along the anteroposterior axis in both species; it should be more symmetric in G sinenesis, in all fragments, according to Figure 2 L. Or they could analyze notum expression in bipolar regenerating fragments of different sizes, mainly in 1 or 2 mm fragments of big planarians, since they are the fragments analyzed that form or not the Janus heads. In G sinensis the expression of notum should be more symmetrical than in S. mediterranea in these fragments.

iii) The authors could design an experiment to demonstrate that the symmetry in the expression of notum affects the rate of Janus heads. The experiment that the authors show is the rescue of the Janus heads in G. sinensis after notum RNAi. However, notum RNAi suppresses notum in both wounds, thus not making them asymmetric. Furthermore, the rescue could be explained by the posteriorizing effect that notum RNAi has in planarians, as reported by several authors. A possibility could be to inhibit APC, which increases notum expression in S. mediterranea (Petersen and Reddien 2011). If APC RNAi in G. sinenesis produces an increase in notum in both wounds and the rate of Janus heads is not rescued, then it would support the hypothesis that notum symmetry is the cause of the Janus heads. However, if it produces an increase of notum in an asymmetric manner, then the Janus phenotype should be rescued.

(2) The second weakness of the study is related to the methodology used to support the second claim, that the slope of bcatenin1 activity has a role in the decision of regeneration - a head and a tail in the correct tip. The main concerns relate to the specificity of the anti-bcatenin1 antibody and to the broad effect of C59 in the secretion of all Wnts.

a) Raising an antibody against beta-catenin1 that allows the quantification by western blot is a strength of the study, since beta-catenin1 is the key element of the cWnt pathway, and their levels are directly associated with the activation of the pathway. Since this is one of the tools that support the second claim of the study, a characterization of the antibody and additional tests to prove its specificity are required. The authors show a Western blot in which the band intensity decreases after beta-catenin1 inhibition in both species. Further analysis should be shown:<br /> i) Demonstration that the intensity of the band increases after APC or Axin inhibition.<br /> ii) Does the antibody work in immunohistochemistry? It would provide further evidence of the specificity of a nuclear signal could be demonstrated.<br /> iii) Explanation and discussion of the protocol used to analyse the levels of b-catenin1 activity along the anteroposterior axis is required. It has been reported that beta-catenin1 is highly expressed and required in the brain in planarians, and also in the pharynx, and in the sexual organs (Hill and Petersen 2015, Sureda-Gomez et al 2016). How is it then explained the anterior-to-posterior gradient of expression of beta-catenin1 seen in this study in both species? Has the pharynx been removed before the protein extraction? What about the beta-catenin1 activity demonstrated in the brain? Why is it not reflected in the western blot analysis using the antibody? This point should be clarified.

b) The second tool used in the second part of the manuscript is the drug C59, which inhibits Porcupine, a protein required for palmitoylation and secretion of Wnts. Because Porcupine could be required for the secretion of all Wnts, the phenotype obtained with the drug could be the sum of the inhibition of cWNT signal (wnt1 for instances) and non-canonical WNT (as wnt5). This is in fact the phenotype resulting after the inhibition of Wntless in planarians (Adell et al. 2009), which is also required for the secretion of Wnts. Thus, in the phenotypes resulting from C59 treatment the analysis of the nervous system and posterior/anterior markers is required. Looking at the in vivo phenotype it appears that in fact the drug is affecting both canonical and no canonical pathways since the animal with protrusions in the lateral part (Figure 4B-double head, or Supplementary Figure 3A) is very similar to the one reported after Wntless inhibition. In case the phenotypes observed also show non-canonical Wnt inhibition, this should be clearly shown and discussed.

The above-mentioned weaknesses are the most important concerns about the present manuscript. However, there are other concerns related to a further analysis of the phenotypes and the analysis of additional Wnt elements as wnt1, which are essential to complete the study and are directly discussed with the authors.

Reviewer #2 (Public review):

Summary:

This study identifies a key role for bodywide canonical Wnt gradients in controlling the outcome of regeneration within planarians, likely acting in parallel to injury-induced cues that also use tissue asymmetry to control this process. In S. Mediterranea a central part of this decision process is the asymmetric expression of the Wnt inhibitor notum specifically at injury sites facing in the anterior direction to promote head formation and inhibit tail formation through regulation of canonical Wnt signaling pathways. Leveraging classic studies by T.H. Morgan over a century ago, which found that amputated thin transverse fragments occasionally incorrectly regenerate 2 heads rather than a head and a tail in a species of Girardia planarians, this study identifies a closely related species G. Sinensis which undergoes errors to regeneration specificity under similar challenges. Morgan had proposed that his results might arise from the use of a "gradient of materials" providing axis information across the body axis such that small tissue fragments are too narrow to interpret gradient differences, leading to head/tail polarity defects in regeneration. The authors show very convincingly that this species of planaria undergoes notum expression after injury, but unlike in S. Mediterranea, this occurs symmetrically at the onset of regeneration. Using RNAi, they show notum participates in the regeneration of mispolarized heads (though interestingly apparently not in normal head regeneration unlike in Smeds, at least under these conditions). G. Sinensis planarians, like many organisms, have abundant expression of Wnt genes posteriorly. To test whether this gradient of Wnts may participate in the regeneration distinct from any Wnt signals activated after injury, the authors use chemical inhibition to reduce Wnt signaling prior to injury and then alleviate inhibition following injury by removal of the drug and confirming successful washout of the drug using mass spec. They also raise a new antibody that can detect beta-catenin-1 in this species in order to monitor the body-wide cWnt gradient after these treatments, and correlate this with outcomes on the head/tail regeneration decision. Using this approach, they find that homeostatic inhibition of porcupine (required for Wnt secretion) could dampen the cWnt/beta-catenin gradient and increase the incidence of inappropriate head regeneration at posterior-facing wounds. In addition, they find that the cWnt gradient is less steep in larger animals that also concurrently have a higher incidence of mistakes in regeneration specificity. Together, the paper presents compelling experiments and analysis to support the conclusion that cWnt gradients are an important determinant of head/tail identity determination decisions in G. Sinensis, and thereby proposes a plausible model that the notum asymmetry present in S. Mediterranea could act in parallel to support the higher regeneration robustness observed in that species.

Strengths:

This is a great paper, an instant classic. It addresses an enduring problem that Morgan and others initiated more than a century ago and brings a new synthesis of ideas to clarify an important mechanism. I also like the term "regeneration specificity" which can provide a nice unification and generalization of ideas that other authors have variously described as regeneration patterning or regeneration polarity. The work is a tour de force that creatively builds new tools and observations to leverage a new model of planarian species for unraveling general mechanisms of regeneration decision-making. The experiments are rigorously conducted and I find the overall data to be quite compelling. I have some comments for the authors to consider below for drawing out the interpretation and also clarifying the underlying mechanism.

Comments:

(1) The G. Sinesis species showed accurate head/tail specificity in 2mm thick fragments but was strongly impaired at 1 mm thick. I am assuming that outcomes of pieces greater than 2mm would make similarly robust head/tail choices, implying a rather sharp transition occurring between 1 and 2 mm. In that case, in the gradient model, are there theoretical reasons to predict that polarity outcomes would decline sharply rather than gradually as size thickness decreases? I think the muscle fibers themselves are thought to have lengths on the order of 200 microns, so I wonder what could account for the characteristic length of less than 1mm here? From the lab's prior analysis of beta-cat gradient, is this perhaps the minimal length where a difference in bcat protein levels can be detected? This is not essential to resolve in this draft (in my view), just a very interesting question arising from the present study. Relatedly, it seems that the slope of cWnt at the wound site itself might not be enough information for polarity because at a highly granular level, this should be identical at posterior-facing wounds from trunk fragments versus thin transverse fragments obtained at the same AP position, yet trunk fragments succeed at regeneration specificity whereas thin transverse fragments fail.

(2) The paper nicely shows strong evidence that notum expression is definitely symmetric at the first occurrence of its expression by 6 hours in D. Sinensis, and this is a really important result of the paper. At 12 hours, it does look to me in the FISH experiments that there is more persistence of expression at the anterior-facing wound versus the posterior-facing wounds (Fig 2D), although the methods for quantification in Fig2E/F do not show a difference in expression at the two wound sites at this time point. Could this difference arise from differences in the perdurance or timing of early wound-induced signaling at the two wound sites that was perhaps too subtle to detect in the quantification methods used? Or perhaps these images do not represent the population? On a related note, the quantification method seems to fail to show that in 6h Smeds, notum expression is indeed asymmetric. Probably the issue here is not the data in the FISH images themselves which strongly support the author's interpretations, but rather a deficiency or limitation of the quantification method used, which should be resolved so that the conclusions from the single FISH images can be interpreted robustly. For example, some authors have used a method of counting notum+ cells and I wonder if this could provide better quantitative information here.

(3) Given that the double-headed phenotype is observed from thin transverse fragments, ideally, the symmetry of notum could be established to occur in those types of fragments as well. This experiment would clarify that notum is expressed at posterior-facing wounds in the very same types of fragments that undergo the highest levels of mistakes in regeneration specificity.

(4) Is wnt1 expressed symmetrically at wound sites in this species? It seems there are cases like acoels where wound-induced Wnt activation can occur asymmetrically but through preferential expression of Wnts at posterior-facing wounds, rather than notum. It would be interesting to know although I also think the work the authors already have done in this study itself already constitutes a very comprehensive advance and could be the subject of future work.

(5) I agree that notum is relatively much more strongly expressed at the far posterior region in D. Senesis than in Smeds, but it does seem from the RNAseq data it also has some locally enriched expression at the anterior pole. Because the RNAseq analysis involves scaling expression across the regions for each gene, it is difficult to know if the anterior expression is relatively lower or perhaps even about the same level of expression as the anterior pole expression of this gene in Smeds. Though not essential to make the desired arguments, in situs on notum in the intact animals would be helpful to clarify this. Relatedly it would be fascinating to know whether D. Senesis notum undergoes anterior-pole expression around the 72 hour or similar timepoint as in Smeds.

(6) The assessment of beta-catenin gradients was done through protein extractions from whole tissue fragments. However, it has been shown in other planarian species that beta-catenin can have strong tissue-specific expression in, for example, the pharynx, brain, and reproductive systems. Some supporting evidence or argument should be presented to clarify the interpretation that the graded expression observed by western blotting cannot be fully explained by this kind of tissue-specific expression of beta-catenin rather than representing a true signaling gradient as interpreted by the authors. For example, if this antibody could be used in immunostaining, this could support the beta-catenin signaling gradient. Alternatively, information about the location of the pharynx or any other posterior reproductive tissues in D. Sinensis could be calibrated with respect to the fragment bins used for the gradient--perhaps a portion of the C59-dependent body-wide gradient measured here occurs fully within tail tissue that lacks other regionalized tissue that could be a potential additional source of beta-catenin. Further discussion and interpretation, or additional experiments, should be included to rule out alternative confounding sources of beta-catenin in order to clarify the interpretation of the western blot as representing a beta-catenin signaling gradient.

(7) I find the analysis in Figure 5 to be quite compelling for showing the importance of cWnt/Bcat gradients in contributing to head/tail determination, and I also think that the author's discussion of the limitations of the approach are well articulated and considered. Based on prior literature, it also seems very likely that there is a third redundantly acting component to regeneration specificity, which is the amplification of small differences in cWnt in a directional-dependent manner early in the regeneration process (24-72 hours in Smeds). This would explain why post-amputation with porcupine inhibitor in D. Sinensis caused 100% penetrant defects in regeneration specificity while the pre-treatment paradigm caused a weaker effect (25-40% for larger animals). In Smeds, it is known already that delivery of dsRNAs against beta-catenin-1, wnt1, and notum only after injury caused polarity defects, and thus all three genes certainly have a function relevant for head/tail after injury (Petersen and Reddien 2008, 2009, 2011- please note these experiments were reported in the text of these studies and not in individual figures). This evidence, combined with extensive FISH and complementary RNAi studies in the field, strongly suggests that some combination of the 6-18h injury-induced phase but also very likely the subsequent "pole-specific phase" of wnt1 expression is likely to be important for driving or enacting the tail fate program and is therefore a component of the regeneration specificity mechanism described here.

(8) Prior work has also demonstrated roles for Wnt genes expressed in gradients to participate in regeneration specificity. In particular, inhibition of the wntP-2/wnt11-5 gene, which is expressed in an animal-wide gradient, strongly enhanced the effects of inhibition of wnt1, which is the earliest wound-activated Wnt gene, to cause 100% penetrant posterior head regeneration phenotypes in S. mediterranea (Petersen and Reddien 2009). These observations are complementary to the present study by implicating Wnts expressed in bodywide gradients in the process of regeneration decision-making. Given that this study also showed that wnt1 is necessary for new wntP-2 expression during the wound-induced early phase and that wnt1 activation does not require beta-catenin for its expression, collectively suggest a more complex process involved in gradient detection and the involvement of wound signals likely beyond only autoregulation of the cWnt gradient or notum asymmetry mechanisms. Although this paper is cited already, framing the present study more fully in context with this and other relevant prior work would be helpful to contextualize the advance for the field.

Reviewer #3 (Public review):

Summary:

In this study, the authors revisit the hypothesis of gradient-based polarity specification during planarian regeneration proposed over a century ago, but here they apply molecular techniques and a valuable comparative approach. By using a comparative analysis with classic and modern planarian model organisms, the authors have identified variable molecular mechanisms that different planarian species utilize to ensure that the proper tissues are regenerated following wounding.

Strengths:

The comparative approach of using 2 different planarian species allowed the study to elucidate different molecular mechanisms that planarians utilize in re-establishing anterior-posterior axis polarity during regeneration. Without this comparative approach, the mystery of T.H. Morgan's data classic studies that demonstrate mistakes in this axis re-polarization would remain unanswered. Furthermore, the use of both a modern molecular model species and another more classical planarian species, which the authors have fully developed with molecular tools and techniques, sheds light on the diversity of genetic processes that closely related species seem to utilize in regeneration. To dissect the role of a long-hypothesized canonical cWnt signaling gradient, the authors developed a novel strategy using chemical genetics to titer this gradient, which led to phenotypes with enhanced aberrant axis polarity re-establishment. Together these experimental approaches establish a well-supported initial model for explaining the molecular mechanisms that different planarian species utilize to allow for proper regeneration of lost tissues.

Weaknesses:

While pharmacological perturbation of signaling pathways could produce off-target effects, the authors provide well-documented evidence that canonical Wnt signaling is altered with drug treatment. The correlation between altered cWnt signaling gradients and the incidence of double-headed regeneration is strong, but it is not clear that the axial cWnt signaling gradient is the ultimate cause of the modified regeneration polarity. However, the model established here and supported by considerable data provides a useful alternative to the mechanism of notum upregulation that has been well-documented in the Schmidtea mediterranea, the workhouse model in planarian research. Throughout the manuscript, the authors suggest that Girardia sinensis lost the ability to upregulate notum at anterior-facing wounds, but until additional planarian species are evaluated, it remains plausible (and equally parsimonious) that S. mediterranea could have innovated a novel strategy to re-establish axis-polarity through asymmetric notum expression.

The study is very well-designed with considerable confirmation of results, especially in the novel use of the pharmacological inhibitor C59. This study is invaluable in its comparative approach, finding that well-established molecular processes may not explain similar developmental outcomes for different species; this corroborates the need to study additional model organisms and how an evolutionary approach to the study of development is imperative.

eLife Assessment

This valuable study reports a potential connection between the seminal microbiome and sperm quality/male fertility. The data are generally convincing. This study will be of interest to clinicians and biomedical researchers who work on microbiome and male fertility.

Reviewer #1 (Public review):

Summary:

The authors analyzed the bacterial colonization of human sperm using 16S rRNA profiling. Patterns of microbiota colonization were subsequently correlated with clinical data, such as spermiogram analysis, presence of reactive oxygen species (ROS), and DNA fragmentation. The authors identified three main clusters dominated by Streptococcus, Prevotella, and Lactobacillus & Gardnerella, respectively, which aligns with previous observations. Specific associations were observed for certain bacterial genera, such as Flavobacterium and semen quality. Overall, it is a well-conducted study that further supports the importance of the seminal microbiota.

Strengths:

- The authors performed the analysis on 223 samples, which is the largest dataset in semen microbiota analysis so far

- Inclusion of negative controls to control contaminations.

- Inclusion of a positive control group consisting of men with proven fertility.

[Editors' note: the authors addressed the concerns raised in the previous round of review.]

Author response:

The following is the authors’ response to the previous reviews.

Discussion: Could the authors discuss more the findings about Flavobacterium? Has it ever been associated with the urogenital tract?

Page 13-14, line 252-268:

‘The genus Flavobacterium was defined in 1923 to encompass gram-negative, non-spore-forming rods, of yellow pigment (44). The inclusiveness of this definition resulted in a collective of heterogenous species. By 1984 the genus had been restricted to those that were also non-motile and non-gliding (44). More recently, with an increase in genomic profiling, many species previously considered to be of genus Flavobacterium have been reclassified to genus Chryseobacterium, Cytophaga, and Weeksella (45). Increasing numbers of Flavobacterium species are being discovered such as gondwanense, Collinsii, branchiarum, branchiicola, salegens and scophthalmum (46) (47) (48). The allocation of Flavobacterium aquatile to this genus remains controversial due to its motility (49). Flavobacterium species are widely distributed in the environment including soil, fresh water and saltwater habitats (50) (51).  There are many reports of pathogenic infections of Flavobacterium species in fish, however human infections are rare (48).  A handful of case reports have described opportunistic infections to include pneumonia, urinary tract infection, peritonitis and meningitis (52) (53) (54) (55). Flavobacterium lindanitolerans and Flavobacterium ceti have been isolated as causative agents in some (56) (54). Case reports also describe Flavobacterium odoratum as a causative agent in urinary tract infection, most often in the immunocompromised or those with indwelling devices (57) (58) (59). However, this was one of many species previously of genus Flavobacterium reclassified, in this case to genus Myroides (60). Notably in our sample participants were asymptomatic of urinary tract infection’. 

What is the relative abundance of Flavobacterium in the present study: this type of bacterium has been previously associated with contaminations (PMID: 25387460, 30497919).

Page 13, line 244-247:

‘The Flavobacterium genus taxon we identified as significantly associated with abnormal semen quality and sperm morphology was present in 36.28% of the samples, with a mean relative abundance of 1.15% in those samples. This information and the mention of previous findings of Flavibacterium in contamination studies have been added to the discussion’.

Figure 1: Increase the size of panel A.

Amended.

Figure 3: Can the authors indicate the relative abundance of each genus/species by the size of the node?

Co-occurrence network figure has been modified to display relative abundance of nodes.

Supplementary data: I don't see anywhere the decontam plots.

Decontam plots as suggested in the package vignette https://benjjneb.github.io/decontam/vignettes/decontam_intro.html have been added in the GitHub repository. For practical purposes, the plot corresponding to the frequency testing only display a random subset (n=15) of the total taxa (n=82) flagged by this test as contaminants. The. .csv files with the outputs of each filter are available in the same directory

Line 12: Check the sentence

Line 15: Genera in italics

Line 33: Change "overall quality of the spermatozoa" to "overall semen quality"

Lines 18-20: Rephrase

Line 87: 28F-Borrelia

Line 134: "Seminal microbiota" or "Composition of the seminal microbiota"

Line 159: "These included ... genera"

Line 166: "Of note, Flavobacterium genus was..."

Lines 187-188: Check sentence

Thank you, these have been amended

eLife Assessment

This compelling study introduces a set of novel genetically encoded tools for the selective and reversible ablation of excitatory and inhibitory synapses. These new tools enable selective and efficient ablation of excitatory synapses, and photoactivatable and chemically inducible methods for inhibitory synapse ablation in specific cell types, providing valuable methods for disrupting neural circuits. This approach holds broad potential for investigating the roles of specific synaptic input onto genetically determined cells.

Reviewer #1 (Public review):

Summary:

This work is a continuation of a previous paper from the Arnold group, where they engineered GFE3, which allows to specifically ablate inhibitory synapses. Here, the authors generate 3 different actuators:

(1) An excitatory synapse ablator.<br /> (2) A photoactivatable inhibitory synapse ablator.<br /> (3) A chemically inhibitory synapse ablator.

Following initial engineering, the authors present characterization and optimization data to showcase that these new tools allow one to specifically ablate synapses, without toxicity and with specificity. Furthermore, they showcase that these manipulations are reversible.

Altogether, these new tools would be important for the neuroscience community.

Strengths:

The authors convincingly demonstrate the engineering, optimization and characterization of these new probes. The main novelty here is the new excitatory synapse ablator, which has not been shown yet and thus could be a valuable tool for neuroscientists.

Weaknesses:

The authors have convincingly demonstrated the use of these tools in cultured neurons. The biggest weakness is the limited information given for the use of these tools for in vivo studies. The authors provide one example of the use of these new tool to study retinal circuits, and show evidence that the excitatory synapse ablator reduces synaptic transmission in retinal slices. Still, more work will be required to use this tool in intact neuronal circuits. It remains unclear if it would be trivial to characterize how well these tools express and operate in vivo. This could be substantially different and present some limitations as to the utility of these tools.

Reviewer #2 (Public review):

Summary:

This study introduces a set of genetically encoded tools for the selective and reversible ablation of excitatory and inhibitory synapses. Previously, the authors developed GFE3, a tool that efficiently ablates inhibitory synapses by targeting an E3 ligase to the inhibitory scaffolding protein Gephyrin via GPHN.FingR, a recombinant, antibody-like protein (Gross et al., 2016). Building on this work, they now present three new ablation tools: PFE3, which targets excitatory synapses, and two new versions of GFE3-paGFE3 and chGFE3-that are photoactivatable and chemically inducible, respectively. These tools enable selective and efficient synapse ablation in specific cell types, providing valuable methods for disrupting neural circuits. This approach holds broad potential for investigating the roles of specific synaptic input onto genetically determined cells.

Strengths:

The primary strength of this study lies in the rational design and robust validation of each tool's effectiveness, building on previous work by the authors' group (Gross et al., 2016). Each tool serves distinct research needs: PFE3 enables efficient degradation of PSD-95 at excitatory synapses, while paGFE3 and chGFE3 allow for targeted degradation of Gephyrin, offering spatiotemporal control over inhibitory synapses via light or chemical activation. These tools are efficiently validated through robust experiments demonstrating reductions in synaptic markers (PSD-95 and Gephyrin) and confirming reversibility, which is crucial for transient ablation. By providing tools with both optogenetic and chemical control options, this study broadens the applicability of synapse manipulation across varied experimental conditions, enhancing the utility of E3 ligase-based approaches for synapse ablation.

Weaknesses:

While this study provides valuable tools and addresses many critical points for varidation, examining potential issues with specificity and background ubiquitination in further detail could strengthen the paper. For PFE3, the study demonstrates reductions in both PSD-95 and GluA1. In their previous work, GFE3 selectively reduced Gephyrin without affecting major Gephyrin interactors or other PSD proteins. Clarifying whether PFE3 affects additional PSD proteins beyond GluA1 would be important for accurately interpreting results in experiments using PFE3. Additionally, further insight into PFE3's impact on inhibitory synapses would be valuable to assess the excitatory specificity and potential for circuit-level applications. For paGFE3 and chGFE3, the E3 ligase (RING domain of Mdm2) is overexpressed and thus freely diffusible within the cell as a separate construct. Although the authors show that Gephyrin is not significantly reduced without light or chemical activation, it remains possible that other proteins, particularly non-synaptic proteins, could be ubiquitinated due to the presence of freely diffusing E3 ligase in cytosol. Addressing these points would clarify the strengths and limitations of tools, providing users with valuable information.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews

Reviewer #1:

The biggest concern in this regard is: that almost all the characterization is performed in cultured dissociated neurons…

While it is true that most of the characterization done in this paper was in cultured neurons, we verified that PFE3 mediates functional ablation of excitatory synapses in vivo (Fig. 3). Furthermore, the GPHN.FingR-XIAP (GFE3), a protein very similar to the complex formed following activation of paGFE3 and chGFE3, has been extensively tested by us and others in vivo(1-4).

Reviewer #2:

For paGFE3 and chGFE3, the E3 ligase (RING domain of Mdm2) is overexpressed throughout cells as a separate construct. Although the authors show that Gephyrin is not significantly reduced without light or chemical activation, it remains possible that other proteins could be ubiquitinated due to the overexpressed E3 domain.

In our previous paper(1), we tested neurons under 3 conditions: 1. expressing a construct similar to PBP-E3, consisting of a FingR with a randomized binding domain fused to the same XIAP ring domain used in paGFE3 and chGFE3 (RAND-E3). 2. expressing GPHN.FingR. 3. not expressing any exogenous proteins (control neurons). In each case, we found that expression of a variety of excitatory and inhibitory synaptic proteins was not significantly different when exposed to either of these exogenous proteins compared with control neurons.

Recommendations for the authors:

(1)  Can the authors use the tools to show the ablation of endogenous PSD95 without FingR overexpression?

The experiments described in Fig. 3 are an example of this type of experiment. Furthermore, the PSD-95.FingR was extensively tested and has been used in dozens of studies without any indication that its expression alters cellular function or morphology. Note also that the transcriptional regulation system of PSD-95.FingR limits the expression such that there is virtually no background, so it is not really being overexpressed.

(2) I am missing some control experiments for the excitatory synapses ablator- can the authors show that cells transfected with the plasmid and no DOX, show similar numbers of synapses as neurons without transfection?

We have added an experiment comparing cells expressing PSD-95.FingR alone, and others expressing PFE3 with no Dox. We found that the two types of cells express amounts of PSD-95 that are not significantly different (Fig. S2L).

(3) I am not quite sure how they used paired statistics on staining since they could only stain the cell at the end of the experiment. Are the comparisons performed on different cells?

These experiments were done on the same cells. However, the methods of labeling were different- the initial counting of synapses was done, so we agree with the reviewer that it would be best not to use a paired analysis. Accordingly, we have changed Figs. 1F and 2D.

eLife Assessment

The paper describes a novel approach for inferring features of synaptic networks from recordings of individual cells within the network. The paper will be a valuable contribution to those studying central pattern generators, including those involved in respiration. However, the theoretical approach to drawing inferences regarding the underlying synaptic currents is incomplete as it relies on unsupported simplifying assumptions.

Reviewer #1 (Public review):

Summary:

The paper develops a phase method to obtain the excitatory and inhibitory afferents to certain neuron populations in the brainstem. The inferred contributions are then compared to the results of voltage clamp and current clamp experiments measuring the synaptic contributions to post-I, aug-E and ramp-I neurons.

Strengths:

The electrophysiology part of the paper is sound and reports novel features with respect to earlier work by JC Smith et al 2012, Paton et al 2022 (and others) who have mapped circuits of the respiratory central pattern generator. Measurements on ramp-I neurons, late-I neurons and two types of post-I neurons in Fig.2 besides measurements of synaptic inputs to these neurons in Fig.5 are to my knowledge new.

Weaknesses:

The phase method for inferring synaptic conductances fails to convince. The method rests on many layers of assumptions and the inferred connections in Fig.4 remain speculative. To be convincing, such method ought to be tested first on a model CPG with known connectivity to assess how good it is at inferring known connections back from the analysis of spatio-temporal oscillations. For biological data, once the network connectivity has been inferred as claimed, the straightforward validation is to reconstruct the experimental oscillations (Fig.2) noting that Rybak et al (Rybak, Paton Schwaber J. Neurophysiol. 77, 1994 (1997)) have already derived models for the respiratory neurons.

The transformation from time to phase space, unlike in the Kuramoto model, is not justified here (L.94) and is wrong. The underpinning idea that "the synaptic conductances depend on the cycle phase and not on time explicitly" is flawed because synapses have characteristic decay times and delays to response which remain fixed when the period of network oscillations increases. Synaptic properties depend on time and not on phase in the network. One major consequence relevant to the present identification of excitatory or inhibitory behaviour, is that it cannot account for change in behaviour of inhibitory synapses - from inhibitory to excitatory action - when the inhibitory decay time becomes commensurable to the period of network oscillations (Wang & Buzsaki Journal of Neuroscience 16, 6402 (1996), van Vreeswijk et al. J. Comp. Neuroscience 1,313 (1994), Borgers and Kopell Neural Comput. 15, 2003). In addition, even small delays in the inhibitory synapse response relative to the pre-synaptic action potential also produce in-phase synchronization (Chauhan et al., Sci. Rep. 8, 11431 (2018); Borgers and Kopell, Neural Comput. 15, 509 (2003)). The present assumption are way too simplistic because you cannot account for these commensurability effects with a single parameter like the network phase. There is therefore little confidence that this model can reliably distinguish excitatory from inhibitory synapses when their dynamics properties are not properly taken into account.

L..82, Eq.1 makes extremely crude assumptions that the displacement current (CdV/dt) is negligible and that the ion channel currents are all negligible. Vm(t) is also not defined. The assumption that the activation/inactivation times of all ion channels are small compared to the 10-20ms decay time of synaptic currents is not true in general. Same for the displacement current. The leak conductance is typically g~0.05-0.09ms/cm^2 while C~1uF/cm^2. Therefore the ratio C/g leak is in the 10-20ms range - the same as the typical docking neurotransmitter time in synapses.

Models of brainstem CPG circuits have been known to exist for decades: JC Smith et al 2012, Paton et al 2022, Bellingham Clin. Exp. Pharm. And Physiol. 25, 847 (1998); Rubin et al., J. Neurophysiol. 101, 2146 (2009) among others. The present paper does not discuss existing knowledge on respiratory networks and gives the impression of reinventing the wheel from scratch. How will this paper add to existing knowledge?

Comments on revisions:

The authors have done a good job at revising the manuscript to put this work into the context of earlier work on brainstem central pattern generators.

I still believe the case for the method is not as convincing as it would have been if the method had been validated first on oscillations produced by a known CPG model. Why would the inference of synaptic types from the model CPG voltage oscillations be predetermined? Such inverse problems are quite complicated and their solution is often not unique or sufficiently constrained. Recovering synaptic weights (or CPG parameters) from limited observations of a highly nonlinear system is not warranted (Gutenkunst et al., Universally sloppy parameter sensitivities in systems biology models, PLoS Comp. Biol. 2007; www.doi.org/10.1371/journal.pcbi.0030189) especially when using surrogate biological models like Hodgkin-Huxley models.

In p.2, the edited section refers to the interspike interval being much smaller than the period of the network. More important is to mention the relationship between the decay time of inhibitory synapses and the period of the network.

Reviewer #2 (Public review):

Summary:

By measuring intracellular changes in membrane voltage from a single neuron of the medulla the authors describe a method for determining the balance of excitatory and inhibitory synaptic drive onto a single neuron within this important brain region.

Strengths:

This data-driven approach to exploring neural circuits is well described and could be valuable in identifying microcircuits that generate rhythms. Importantly, perhaps, this inference method could enable microcircuits to be studied without the need for time consuming anatomical tracing or other more involved electrophysiological techniques. Therefore, I definitely can see the value in developing an approach of this type.

Weaknesses:

There are many assumptions that need to be accepted in order to successfully apply this technique and I was pleased to see that several of these assumption have been explored by the authors in this study.

For example, this approach involves assuming the reversal potential that is associated with the different permeant ions that underlie the excitation and inhibition as well as the application of Ohms law to estimate the contribution of excitation and inhibitory conductance. My first concern was that this approach relies on a linear I-V relationship between the measured voltage and the estimated reversal potential. However, open rectification is a feature of any I-V relationship generated by asymmetric distributions of ions (see the GHK current equation) and will therefore be a particular issue for the inhibition resulting from asymmetrical Cl- ion gradients across GABA-A receptors. The mixed cation conductance that underlies most synaptic excitation will also generate a non-linear I-V relationship due to the inward rectification associated with polyamine block of AMPA receptors. The authors present evidence that over most of the voltage range examined the I-V relationship is linear and this is a helpful addition.

This approach has similarities to earlier studies undertaken in the visual cortex that estimated the excitatory and inhibitory synaptic conductance changes that contributed to membrane voltage changes during receptive field stimulation. However, these approaches also involved the recording of transmembrane current changes during visual stimulation that were undertaken in voltage-clamp at various command voltages to estimate the underlying conductance changes. Molkov et al have attempted to essentially deconvolve the underlying conductance changes without this information and I am concerned that this simply may not be possible.

The current balance equation (1) cited in this study is based upon the parallel conductance model developed by Hodgkin & Huxley. One key element of the HH equations is the inclusion of an estimate of the capacitive current generated due to the change in voltage across the membrane capacitance. While the present study takes into account the impact of membrane capacitance, a deeper discussion on how variations in capacitance across different neuron types might affect inference accuracy would be useful. Differences in capacitance could introduce variability in inferred conductances, potentially influencing model predictions.

Studies using acute slicing preparations to examine circuit effects have often been limited to the study of small microcircuits - especially feedforward and feedback interneuron circuits. It is widely accepted that any information gained from this approach will always be compromised by the absence of patterned afferent input from outside the brain region being studied. In this study, descending control from the Pons and the neocortex will not be contributing much to the synaptic drive and ascending information from respiratory muscles will also be absent completely. This may not have been such a major concern if this study was limited to demonstrating the feasibility of a methodological approach. However, this limitation does need to be considered when using an approach of this type to speculate on the prevalence of specific circuit motifs within the medulla (Figure 4). Therefore, I would argue that some discussion of this limitation should be included in this manuscript.

eLife Assessment

This neuroimaging and electrophysiology study in a small cohort of congenital cataract patients with sight recovery aims to characterize the effects of early visual deprivation on excitatory and inhibitory balance in visual cortex. While contrasting sight-recovery with visually intact controls suggested the existence of persistent alterations in Glx/GABA ratio and aperiodic EEG signals, it provided incomplete evidence supporting claims about the effects of early deprivation itself. The reported data were considered valuable, given the rare study population. However, methodological limitations will likely restrict usefulness to scientists working in this particular subfield.

Reviewer #1 (Public review):

Summary

In this human neuroimaging and electrophysiology study, the authors aimed to characterise effects of a period of visual deprivation in the sensitive period on excitatory and inhibitory balance in the visual cortex. They attempted to do so by comparing neurochemistry conditions ('eyes open', 'eyes closed') and resting state, and visually evoked EEG activity between ten congenital cataract patients with recovered sight (CC), and ten age-matched control participants (SC) with normal sight. First, they used magnetic resonance spectroscopy to measure in vivo neurochemistry from two locations, the primary location of interest in the visual cortex, and a control location in the frontal cortex. Such voxels are used to provide a control for the spatial specificity of any effects because the single-voxel MRS method provides a single sampling location. Using MR-visible proxies of excitatory and inhibitory neurotransmission, Glx and GABA+ respectively, the authors report no group effects in GABA+ or Glx, no difference in the functional conditions 'eyes closed' and 'eyes open'. They found an effect of group in the ratio of Glx/GABA+ and no similar effect in the control voxel location. They then perform multiple exploratory correlations between MRS measures and visual acuity and report a weak positive correlation between the 'eyes open' condition and visual acuity in CC participants. The same participants then took part in an EEG experiment. The authors selected two electrodes placed in the visual cortex for analysis and report a group difference in an EEG index of neural activity, the aperiodic intercept, as well as the aperiodic slope, considered a proxy for cortical inhibition. Control electrodes in the frontal region did not present with the same pattern. They report an exploratory correlation between the aperiodic intercept and Glx in one out of three EEG conditions.

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

Strengths of study

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

Limitations

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

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

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

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

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

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

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

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

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

The updated document has addressed this caveat.

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

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

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

This caveat has been addressed in the revised manuscript.

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

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

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

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

Comments on revisions:

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

In their second revision, the authors pointed to justifications for their analyses, careful interpretation and tempered claims to clarify their response to the initial feedback. However, my assessment of the first revision has not been changed after the second revision, because there were no further modifications of their responses to my feedback.

Reviewer #2 (Public review):

Summary:

The study examined 10 congenitally blind patients who recovered vision through the surgical removal of bilateral dense cataracts, measuring neural activity and neuro chemical profiles from the visual cortex. The declared aim is to test whether restoring visual function after years of complete blindness impacts excitation/inhibition balance in the visual cortex. The manuscript reports precious behavioural, electrophysiological and magnetic resonance data from a rare population. Although the findings are useful for stimulating further research in the field, they only provide incomplete support to the authors' claims.

The main claim is that sight recovery impacts the excitation/inhibition balance in the visual cortex; however, the paradigm does not allow to distinguish the effects of sight recovery from those of visual deprivation (i.e. in patients who were born blind but recovered vision after several months/years vs. patients who were born blind and never recovered vision); moreover, the link between electrophysiological findings and cortical excitation/inhibition is tentative and its interpretation remains speculative.

Strengths:

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

Weaknesses:

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

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

Conclusions:

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

Comments on revisions:

The authors' revisions did not substantially alter the manuscript. As such, my assessment above remains unaltered.

Reviewer #3 (Public review):

Summary:

This manuscript examines the impact of congenital visual deprivation on the excitatory/inhibitory (E/I) ratio in the visual cortex using Magnetic Resonance Spectroscopy (MRS) and electroencephalography (EEG) in individuals whose sight was restored. Ten individuals with reversed congenital cataracts were compared to age-matched, normally sighted controls, assessing the cortical E/I balance and its interrelationship and to visual acuity. The study reveals that the Glx/GABA ratio in the visual cortex and the intercept and aperiodic signal are significantly altered in those with a history of early visual deprivation, suggesting persistent neurophysiological changes despite visual restoration. First of all, I would like to disclose that I am not an expert in congenital visual deprivation, nor in MRS. My expertise is in EEG (particularly in the decomposition of periodic and aperiodic activity) and statistical methods. Second, although the authors addressed some of my concerns on the previous version of this manuscript, major concerns and flaws remain in terms of methodological and statistical approaches along with the (over) interpretation of the results.

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

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

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

Several points require clarification or improvement:

(4) Correlation Methods: The manuscript does not specify whether the reported correlation analyses are based on Pearson or Spearman correlation.<br /> This has been addressed in the final revision

(5) Confidence Intervals: Include confidence intervals for correlations to represent the uncertainty associated with these estimates.<br /> This has been addressed in the final revision

(6) Permutation Statistics: Given the small sample size, I recommend using permutation statistics, as these are exact tests and more appropriate for small datasets.

(7) Adjusted P-Values: Ensure that reported Bonferroni corrected p-values (e.g., p > 0.999) are clearly labeled as adjusted p-values where applicable.<br /> This has been addressed in the final revision

(8) Figure 2C<br /> Figure 2C still lacks crucial information that the correlation between Glx/GABA ratio and visual acuity was computed solely in the control group (as described in the rebuttal letter). Why was this analysis restricted to the control group? Please provide a rationale.

(9 3.4) Interpretation of Aperiodic Signal<br /> Relying on previous studies to interpret the aperiodic slope as a proxy for excitation/inhibition (E/I) does not make the interpretation more robust.

(10) Additionally, the authors state:<br /> "We cannot think of how any of the exploratory correlations between neurophysiological measures and MRS measures could be accounted for by a difference e.g. in skull thickness."

(11) This could be addressed directly by including skull thickness as a covariate or visualizing it in scatterplots, for instance, by representing skull thickness as the size of the dots.

(12 3.5) Problems with EEG Preprocessing and Analysis<br /> Downsampling: The decision to downsample the data to 60 Hz "to match the stimulation rate" is problematic. This choice conflates subsequent spectral analyses due to aliasing issues, as explained by the Nyquist theorem. While the authors cite prior studies (Schwenk et al., 2020; VanRullen & MacDonald, 2012) to justify this decision, these studies focused on alpha (8-12 Hz), where aliasing is less of a concern compared of analyzing aperiodic signal. Furthermore, in contrast, the current study analyzes the frequency range from 1-20 Hz, which is too narrow for interpreting the aperiodic signal asE/I. Typically, this analysis should include higher frequencies, spanning at least 1-30 Hz oreven 1-45 Hz (not 20-40 Hz).

(13) Baseline Removal: Subtracting the mean activity across an epoch as a baseline removal step is inappropriate for resting-state EEG data. This preprocessing step undermines the validity of the analysis. The EEG dataset has fundamental flaws, many of which were pointed out in the previous review round but remain unaddressed. In its current form, the manuscript falls short of standards for robust EEG analysis.

(14) The authors mention: "The EEG data sets reported here were part of data published earlier (Ossandón et al.,2023; Pant et al., 2023)." Thus, the statement "The group differences for the EEG assessments corresponded to those of a larger sample of CC individuals (n=38) " is a circular argument and should be avoided."<br /> The authors addressed this comment and adjusted the statement. However, I do not understand, why the full sample published earlier (Ossandón et al., 2023) was not used in the current study?

Comments on revisions:

The current version of the manuscript is almost unchanged compared to the last version. Unfortunately, I observed that the authors have not adequately addressed most of my previous suggestions; rather, they provided justifications for not incorporating them.

Given this, I do not see the need to modify my initial assessment.

eLife Assessment

van Vliet and colleagues show a useful correlation between internal states of a convolutional neural network (CNN) trained on visual word stimuli with three specific components of evoked MEG potentials during reading in humans. The findings are solid, though quantitative evidence that model can produce any of the phenomena that the human visual system is known to have (e.g., feedback connections, sensitivity to word frequency), or that it has comparable performance to human behaviour (i.e., similar task accuracy with a comparable pattern of mistakes) would make the conclusions much stronger.

Reviewer #2 (Public review):

van Vliet and colleagues present results of a study correlating internal states of a convolutional neural network trained on visual word stimuli with evoked MEG potentials during reading.

In this study, a standard deep learning image recognition model (VGG-11) trained on a large natural image set (ImageNet) that begins illiterate but is then further trained on visual word stimuli, is used on a set of predefined stimulus images to extract strings of characters from "noisy" words, pseudowords and real words. This methodology is used in hopes of creating a model which learns to apply the same nonlinear transforms that could be happening in different regions of the brain - which would be validated by studying the correlations between the weights of this model and neural responses. Specifically, the aim is that the model learns some vector embedding space, as quantified by the spread of activations across a layer's weights (L2 Norm prior to ReLu Activation Function), for the different kinds of stimuli, that creates a parameterized decision boundary that is similar to amplitude changes at different times for a MEG signal. More importantly, the way that the stimuli are ordered or ranked in that space should be separable to the degree we see separation in neural activity. This study does show that the layer weights corresponding to five different broad classes of stimuli do statistically correlate with three specific components in the ERP. However, I believe there are fundamental theoretical issues that limit the implications of the results of this study.

As has been shown over many decades, there are many potential computational algorithms, with varied model architectures, that can perform the task of text recognition from an image. However, there is no evidence presented here that this particular algorithm has comparable performance to human behavior (i.e. similar accuracy with a comparable pattern of mistakes). This is a fundamental prerequisite before attempting to meaningfully correlate these layer activations to human neural activations. Therefore, it is unlikely that correlating these derived layer weights to neural activity provides meaningful novel insights into neural computation beyond what is seen using traditional experimental methods.

One example of a substantial discrepancy between this model and neural activations is that, while incorporating frequency weighting into the training data is shown to slightly increase neural correlation with the model, Figure 7 shows that no layer of the model appears directly sensitive to word frequency. This is in stark contrast to the strong neural sensitivity to word frequency seen in EEG (e.g. Dambacher et al 2006 Brain Research), fMRI (e.g. Kronbichler et al 2004 NeuroImage), MEG (e.g. Huizeling et al 2021 Neurobio. Lang.), and intracranial (e.g. Woolnough et al 2022 J. Neurosci.) recordings. Figure 7 also demonstrates that late stages of the model show a strong negative correlation with font size, whereas later stages of neural visual word processing are typically insensitive to differences in visual features, instead showing sensitivity to lexical factors.

Another example of the mismatch between this model and visual cortex is the lack of feedback connections in the model. Within visual cortex there are extensive feedback connections, with later processing stages providing recursive feedback to earlier stages. This is especially evident in reading, where feedback from lexical level processes feeds back to letter level processes (e.g. Heilbron et al 2020 Nature Comms.). This feedback is especially relevant for reading of words in noisy conditions, as tested in the current manuscript, as lexical knowledge enhances letter representation in visual cortex (the word superiority effect). This results in neural activity in multiple cortical areas varying over time, changing selectivity within a region at different measured time points (e.g. Woolnough et al 2021 Nature Human Behav.), which in the current study is simplified down to three discrete time windows, each attributed to different spatial locations.

The presented model needs substantial further development to be able to replicate, both behaviorally and neurally, many of the well-characterized phenomena seen in human behavior and neural recordings that are fundamental hallmarks of human visual word processing. Until that point it is unclear what novel contributions can be gleaned from correlating low dimensional model weights from these computational models with human neural data.

The revised version of this manuscript has not addressed these concerns.

Reviewer #3 (Public review):

Summary:

The authors investigate the extent to which the responses of different layers of a vision model (VGG-11) can be linked to the cascade of responses (namely, type-I, type-II and N400) in the human brain when reading words. To achieve maximal consistency between, they add noisy-activations to VGG and finetune it on a character recognition task. In this setup, they observe various similarities between the behavior of VGG and the brain when presented with various transformations of the words (added noise, font modification etc).

Strengths:<br /> - The paper is well written and well presented<br /> - The topic studied is interesting.<br /> - The fact that the response of the CNN on unseen experimental contrasts such as adding noise correlated with previous results on the brain is compelling.

Weaknesses:<br /> - The paper is rather qualitative in nature. In particular, the authors show that some resemblance exists between the behavior of some layers and some parts of the brain, but it is hard to quantitively understand how strong the resemblences are in each layer, and the exact impact of experimental settings such as the frequency balancing (which seems to only have a very moderate effect according to figure 5)<br /> - The experiments only consider a rather outdated vision model (VGG)

Comments on revisions:

After rebuttal, the authors significantly strengthened their results. I now find the paper much more convincing, and thank the author for their careful consideration of the reviewers' suggestions.

Author response:

The following is the authors’ response to the original reviews.

We thank the reviewers for their efforts. They have pointed out several shortcomings and made very helpful suggestions. Based on their feedback, we have substantially revised the manuscript and feel the paper has been much improved because of it.

Notable changes are:

(1) As our model does not contain feed-back connections, the focus of the study is now more clearly communicated to be on feed-forward processes only, with appropriate justifications for this choice added to the Introduction and Discussion sections. Accordingly, the title has been changed to include the term “feed-forward”.

(2) The old Figure 5 has been removed in favor of reporting correlation scores to the right of the response profiles in other figures.

(3) We now discuss changes to the network architecture (new Figure 5) and fine-tuning of the hyperparameters (new Figure 6) in the main text instead of only the Supplementary Information.

(4) The discussion on qualitative versus quantitative analysis has been extended and given its own subsection entitled “On the importance of experimental contrasts and qualitative analysis of the model”.

Below, we address each point that the reviewers brought up in detail and outline what improvements we have made in the revision to address them.

Reviewer #1 (Public Review):

Summary:

This study trained a CNN for visual word classification and supported a model that can explain key functional effects of the evoked MEG response during visual word recognition, providing an explicit computational account from detection and segmentation of letter shapes to final word-form identification.

Strengths:

This paper not only bridges an important gap in modeling visual word recognition, by establishing a direct link between computational processes and key findings in experimental neuroimaging studies, but also provides some conditions to enhance biological realism.

Weaknesses:

The interpretation of CNN results, especially the number of layers in the final model and its relationship with the processing of visual words in the human brain, needs to be further strengthened.

We have experimented with the number of layers and the number of units in each layer. In the previous version of the manuscript, these results could be found in the supplementary information. For the revised version, we have brought some of these results into the main text and discuss them more thoroughly.

We have added a figure (Figure 5 in the revised manuscript) showing the impact of the number of convolution and fully-connected layers on the response profiles of the layers, as well as the correlation with the three MEG components.

We discuss the figure in the Results section as follows:

“Various variations in model architecture and training procedure were evaluated. We found that the number of layers had a large impact on the response patterns produced by the model (Figure 5). The original VGG-11 architecture defines 5 convolution layers and 3 fully connected layers (including the output layer). Removing a convolution layer (Figure 5, top row), or removing one of the fully connected layers (Figure 5, second row), resulted in a model that did exhibit an enlarged response to noisy stimuli in the early layers that mimics the Type-I response. However, such models failed to show a sufficiently diminished response to noisy stimuli in the later layers, hence failing to produce responses that mimic the Type-II or N400m, a failure which also showed as low correlation scores.

Adding an additional convolution layer (Figure 5, third row) resulted in a model where none of the layer response profiles mimics that of the Type-II response. The Type-II response is characterized by a reduced response to both noise and symbols, but an equally large response to consonant strings, real and pseudo words. However, in the model with an additional convolution layer, the consonant strings evoked a reduced response already in the first fully connected layer, which is a feature of the N400m rather than the Type-II. These kind of subtleties in the response pattern, which are important for the qualitative analysis, generally did not show quantitatively in the correlation scores, as the fully connected layers in this model correlate as well with the Type-II response as models that did show a response pattern that mimics the Type-II.

Adding an additional fully connected layer (Figure 5, fourth row) resulted in a model with similar response profiles and correlation with the MEG components as the original VGG-11 architecture (Figure 5, bottom row) The N400m-like response profile is now observed in the third fully connected layer rather than the output layer. However, the decrease in response to consonant strings versus real and pseudo words, which is typical of the N400m, is less distinct than in the original VGG-11 architecture.”

And in the Discussion section:

“In the model, convolution units are followed by pooling units, which serve the purpose of stratifying the response across changes in position, size and rotation within the receptive field of the pooling unit. Hence, the effect of small differences in letter shape, such as the usage of different fonts, was only present in the early convolution layers, in line with findings in the EEG literature (Chauncey et al., 2008; Grainger & Holcomb, 2009; Hauk & Pulvermüller, 2004). However, the ability of pooling units to stratify such differences depends on the size of their receptive field, which is determined by the number of convolution-and-pooling layers. As a consequence, the response profiles of the subsequent fully connected layers was also very sensitive to the number of convolution-and-pooling layers. The optimal number of such layers is likely dependent on the input size and pooling strategy. Given the VGG-11 design of doubling the receptive field after each layer, combined with an input size of 225×225 pixels, the optimal number of convolution-andpooling layers for our model was five, or the model would struggle to produce response profiles mimicking those of the Type-II component in the subsequent fully connected layers (Figure 5).”

Reviewer #1 (Recommendations For The Authors):

(1) The similarity between CNNs and human MEG responses, including type-I (100ms), type-II (150ms), and N400 (400ms) components, looks like separately, lacking the sequential properties among these three components. Is the recurrent neural network (RNN), which can be trained to process and convert a sequential data input into a specific sequential data output, a better choice?

When modeling sequential effects, meaning that the processing of the current word is influenced by the word that came before it, such as priming and top-down modulations, we agree that such a model would indeed require recurrency in its architecture. However, we feel that the focus of modeling efforts in reading has been overwhelmingly on the N400 and such priming effects, usually skipping over the pixel-to-letter process. So, for this paper, we were keen on exploring more basic effects such as noise and symbols versus letters on the type-I and type-II responses. And for these effects, a feed-forward model turns out to be sufficient, so we can keep the focus of this particular paper on bottom-up processes during single word reading, on which there is already a lot to say.

To clarify our focus on feed-forward process, we have modified the title of the paper to be:

“Convolutional networks can model the functional modulation of the MEG responses associated with feed-forward processes during visual word recognition” furthermore, we have revised the Introduction to highlight this choice, noting:

“Another limitation is that these models have primarily focused on feed-back lexicosemantic effects while oversimplifying the initial feed-forward processing of the visual input.

[…]

For this study, we chose to focus on modeling the early feed-forward processing occurring during visual word recognition, as the experimental setup in Vartiainen et al. (2011) was designed to demonstrate.

[…]

By doing so, we restrict ourselves to an investigation of how well the three evoked components can be explained by a feed-forward CNN in an experimental setting designed to demonstrate feed-forward effects. As such, the goal is not to present a complete model of all aspects of reading, which should include feed-back effects, but rather to demonstrate the effectiveness of using a model that has a realistic form of input when the aim is to align the model with the evoked responses observed during visual word recognition.”

And in the Discussion section:

“In this paper we have restricted our simulations to feed-forward processes. Now, the way is open to incorporate convolution-and-pooling principles in models of reading that simulate feed-back processes as well, which should allow the model to capture more nuance in the Type-II and N400m components, as well as extend the simulation to encompass a realistic semantic representation.”

(2) There is no clear relationship between the layers that signal needs to traverse in the model and the relative duration of the three components in the brain.

While some models offer a tentative mapping between layers and locations in the brain, none of the models we are aware of actually simulate time accurately and our model is no exception.

While we provide some evidence that the three MEG components are best modeled with different types of layers, and the type-I becomes somewhere before type-II and N400m is last in our model, the lack of timing information is a weakness of our model we have not been able to address. In our previous version, this already was the main topic of our “Limitations of the model” section, but since this weakness was pointed out by all reviewers, we have decided to widen our discussion of it:

“One important limitation of the current model is the lack of an explicit mapping from the units inside its layers to specific locations in the brain at specific times. The temporal ordering of the components is simulated correctly, with the response profile matching that of the type-I occurring the layers before those matching the type-II, followed by the N400m. Furthermore, every component is best modeled by a different type of layer, with the type-I best described by convolution-and-pooling, the type-II by fully-connected linear layers and the N400m by a one-hot encoded layer. However, there is no clear relationship between the number of layers the signal needs to traverse in the model to the processing time in the brain. Even if one considers that the operations performed by the initial two convolution layers happen in the retina rather than the brain, the signal needs to propagate through three more convolution layers to reach the point where it matches the type-II component at 140-200 ms, but only through one more additional layer to reach the point where it starts to match the N400m component at 300-500 ms. Still, cutting down on the number of times convolution is performed in the model seems to make it unable to achieve the desired suppression of noise (Figure 5). It also raises the question what the brain is doing during the time between the type-II and N400m component that seems to take so long. It is possible that the timings of the MEG components are not indicative solely of when the feed-forward signal first reaches a certain location, but are rather dictated by the resolution of feed-forward and feedback signals (Nour Eddine et al., 2024).”

See also our response to the next comment of the Reviewer, in which we dive more into the effect of the number of layers, which could be seen as a manipulation of time.

(3) I am impressed by the CNN that authors modified to match the human brain pattern for the visual word recognition process, by the increase and decrease of the number of layers. The result of this part was a little different from the author’s expectation; however, the author didn’t explain or address this issue.

We are glad to hear that the reviewer found these results interesting. Accordingly, we now discuss these results more thoroughly in the main text.

We have moved the figure from the supplementary information to the main text (Figure 5 in the revised manuscript). And describe the results in the Results section:

“Various variations in model architecture and training procedure were evaluated. We found that the number of layers had a large impact on the response patterns produced by the model (Figure 5). The original VGG-11 architecture defines 5 convolution layers and 3 fully connected layers (including the output layer). Removing a convolution layer (Figure 5, top row), or removing one of the fully connected layers (Figure 5, second row), resulted in a model that did exhibit an enlarged response to noisy stimuli in the early layers that mimics the Type-I response. However, such models failed to show a sufficiently diminished response to noisy stimuli in the later layers, hence failing to produce responses that mimic the Type-II or N400m, a failure which also showed as low correlation scores.

Adding an additional convolution layer (Figure 5, third row) resulted in a model where none of the layer response profiles mimics that of the Type-II response. The Type-II response is characterized by a reduced response to both noise and symbols, but an equally large response to consonant strings, real and pseudo words. However, in the model with an additional convolution layer, the consonant strings evoked a reduced response already in the first fully connected layer, which is a feature of the N400m rather than the Type-II. These kind of subtleties in the response pattern, which are important for the qualitative analysis, generally did not show quantitatively in the correlation scores, as the fully connected layers in this model correlate as well with the Type-II response as models that did show a response pattern that mimics the Type-II.

Adding an additional fully connected layer (Figure 5, fourth row) resulted in a model with similar response profiles and correlation with the MEG components as the original VGG-11 architecture (Figure 5, bottom row) The N400m-like response profile is now observed in the third fully connected layer rather than the output layer. However, the decrease in response to consonant strings versus real and pseudo words, which is typical of the N400m, is less distinct than in the original VGG-11 architecture.”

We also incorporated these results in the Discussion:

“However, the ability of pooling units to stratify such differences depends on the size of their receptive field, which is determined by the number of convolution-andpooling layers. This might also explain why, in later layers, we observed a decreased response to stimuli where text was rendered with a font size exceeding the receptive field of the pooling units (Figure 8). Hence, the response profiles of the subsequent fully connected layers was very sensitive to the number of convolution-and-pooling layers. This number is probably dependent on the input size and pooling strategy. Given the VGG11 design of doubling the receptive field after each layer, combined with an input size of 225x225 pixels, the optimal number of convolution-and-pooling layers for our model was five, or the model would struggle to produce response profiles mimicking those of the type-II component in the subsequent fully connected layers (Figure 5).

[…]

A minimum of two fully connected layers was needed to achieve this in our case, and adding more fully connected layers would make them behave more like the component (Figure 5).”

(4) Can the author explain why the number of layers in the final model is optimal by benchmarking the brain hierarchy?

We have incorporated the figure describing the correlation between each model and the MEG components (previously Figure 5) with the figures describing the response profiles (Figures 4 and 5 in the revised manuscript and Supplementary Figures 2-6). This way, we (and the reader) can now benchmark every model qualitatively and quantitatively.

As we stated in our response to the previous comment, we have added a more thorough discussion on the number of layers, which includes the justification for our choice for the final model. The benchmark we used was primarily whether the model shows the same response patterns as the Type I, Type II and N400 responses, which disqualifies all models with fewer than 5 convolution and 3 fully connected layers. Models with more layers also show the proper response patterns, however we see that there is actually very little difference in the correlation scores between different models. Hence, our justification for sticking with the original VGG11 architecture is that it produces the qualitative best response profiles, while having roughly the same (decently high) correlation with the MEG components. Furthermore, by sticking to the standard architecture, we make it slightly easier to replicate our results as one can use readily available pre-trained ImageNet weights.

As well as always discussing the correlation scores in tandem with the qualitative analysis, we have added the following statement to the Results:

“Based on our qualitative and quantitative analysis, the model variant that performed best overall was the model that had the original VGG11 architecture and was preinitialized from earlier training on ImageNet, as depicted in the bottom rows of Figure 4 and Figure 5.”

Reviewer #2 (Public Review):

As has been shown over many decades, many potential computational algorithms, with varied model architectures, can perform the task of text recognition from an image. However, there is no evidence presented here that this particular algorithm has comparable performance to human behavior (i.e. similar accuracy with a comparable pattern of mistakes). This is a fundamental prerequisite before attempting to meaningfully correlate these layer activations to human neural activations. Therefore, it is unlikely that correlating these derived layer weights to neural activity provides meaningful novel insights into neural computation beyond what is seen using traditional experimental methods.

We very much agree with the reviewer that a qualitative analysis of whether the model can explain experimental effects needs to happen before a quantitative analysis, such as evaluating model-brain correlation scores. In fact, this is one of the intended key points we wished to make.

As we discuss at length in the Introduction, “traditional” models of reading (those that do not rely on deep learning) are not able to recognize a word regardless of exact letter shape, size, and (up to a point) rotation. In this study, our focus is on these low-level visual tasks rather than high-level tasks concerning semantics. As the Reviewer correctly states, there are many potential computational algorithms able to perform these visual task at a human level and so we need to evaluate the model not only on its ability to mimic human accuracy but also on generating a comparable pattern of mistakes. In our case, we need a pattern of behavior that is indicative of the visual processes at the beginning of the reading pipeline. Hence, rather than relying on behavioral responses that are produced at the very end, we chose the evaluate the model based on three MEG components that provide “snapshots” of the reading process at various stages. These components are known to manifest a distinct pattern of “behavior” in the way they respond to different experimental conditions (Figure 2), akin to what to Reviewer refers to as a “pattern of mistakes”. The model was first evaluated on its ability to replicate the behavior of the MEG components in a qualitative manner (Figure 4). Only then do we move on to a quantitative correlation analysis. In this manner, we feel we are in agreement with the approach advocated by the Reviewer.

In the Introduction, we now clarify:

“Another limitation is that these models have primarily focused on feed-back lexicosemantic effects while oversimplifying the initial feed-forward processing of the visual input.

[…]

We sought to construct a model that is able to recognize words regardless of length, size, typeface and rotation, as well as humans can, so essentially perfectly, whilst producing activity that mimics the type-I, type-II, and N400m components which serve as snapshots of this process unfolding in the brain.

[…]

These variations were first evaluated on their ability to replicate the experimental effects in that study, namely that the type-I response is larger for noise embedded words than all other stimuli, the type-II response is larger for all letter strings than symbols, and that the N400m is larger for real and pseudowords than consonant strings. Once a variation was found that could reproduce these effects satisfactorily, it was further evaluated based on the correlation between the amount of activation of the units in the model and MEG response amplitude.”

To make this prerequisite more clear, we have removed what was previously Figure 5, which showed the correlation between the various models the MEG components out of the context of their response patterns. Instead, these correlation values are now always presented next to the response patterns (Figures 4 and 5, and Supplementary Figures 2-6 in the revised manuscript). This invites the reader to always consider these metrics in relation to one another.

One example of a substantial discrepancy between this model and neural activations is that, while incorporating frequency weighting into the training data is shown to slightly increase neural correlation with the model, Figure 7 shows that no layer of the model appears directly sensitive to word frequency. This is in stark contrast to the strong neural sensitivity to word frequency seen in EEG (e.g. Dambacher et al 2006 Brain Research), fMRI (e.g. Kronbichler et al 2004 NeuroImage), MEG (e.g. Huizeling et al 2021 Neurobio. Lang.), and intracranial (e.g. Woolnough et al 2022 J. Neurosci.) recordings. Figure 7 also demonstrates that the late stages of the model show a strong negative correlation with font size, whereas later stages of neural visual word processing are typically insensitive to differences in visual features, instead showing sensitivity to lexical factors.

We are glad the reviewer brought up the topic of frequency balancing, as it is a good example of the importance of the qualitative analysis. Frequency balancing during training only had a moderate impact on correlation scores and from that point of view does not seem impactful. However, when we look at the qualitative evaluation, we see that with a large vocabulary, a model without frequency balancing fails to properly distinguish between consonant strings and (pseudo)words (Figure 4, 5th row). Hence, from the point of view of being able to reproduce experimental effects, frequency balancing had a large impact. We now discuss this more explicitly in the revised Discussion section:

“Overall, we found that a qualitative evaluation of the response profiles was more helpful than correlation scores. Often, a deficit in the response profile of a layer that would cause a decrease in correlation on one condition would be masked by an increased correlation in another condition. A notable example is the necessity for frequency-balancing the training data when building models with a vocabulary of 10 000. Going by correlation score alone, there does not seem to be much difference between the model trained with and without frequency balancing (Figure 4A, fifth row versus bottom row). However, without frequency balancing, we found that the model did not show a response profile where consonant strings were distinguished from words and pseudowords (Figure 4A, fifth row), which is an important behavioral trait that sets the N400m component apart from the Type-II component (Figure 2D). This underlines the importance of the qualitative evaluation in this study, which was only possible because of a straightforward link between the activity simulated within a model to measurements obtained from the brain, combined with the presence of clear experimental conditions.”

It is true that the model, even with frequency balancing, only captures letter- and bigramfrequency effects and not the word-frequency effects that we know the N400m is sensitive to. Since our model is restricted to feed-forward processes, this finding adds to the evidence that frequency-modulated effects are driven by feed-back effects as modeled by Nour Eddine et al. (2024, doi:10.1016/j.cognition.2024.105755). See also our response to the next comment by the Reviewer where we discuss feed-back connections. We have added the following to the section about model limitations in the revised Discussion:

“The fact that the model failed to simulate the effects of word-frequency on the N400m (Figure 8), even after frequency-balancing of the training data, is additional evidence that this effect may be driven by feed-back activity, as for example modeled by Nour Eddine et al. (2024).”

Like the Reviewer, we initially thought that later stages of neural visual word processing would be insensitive to differences in font size. When diving into the literature to find support for this claim, we found only a few works directly studying the effect of font size on evoked responses, but, surprisingly, what we did find seemed to align with our model. We have added the following to our revised Discussion:

“The fully connected linear layers in the model show a negative correlation with font size. While the N400 has been shown to be unaffected by font size during repetition priming (Chauncey et al., 2008), it has been shown that in the absence of priming, larger font sizes decrease the evoked activity in the 300–500 ms window (Bayer et al., 2012; Schindler et al., 2018). Those studies refer to the activity within this time window, which seems to encompass the N400, as early posterior negativity (EPN). What possibly happens in the model is that an increase in font size causes an initial stronger activation in the first layers, due to more convolution units receiving input. This leads to a better signal-to-noise ratio (SNR) later on, as the noise added to the activation of the units remains constant whilst the amplitude of the input signal increases. A better SNR translates ultimately in less co-activation of units corresponding to orthographic neighbours in the final layers, hence to a decrease in overall layer activity.”

Another example of the mismatch between this model and the visual cortex is the lack of feedback connections in the model. Within the visual cortex, there are extensive feedback connections, with later processing stages providing recursive feedback to earlier stages. This is especially evident in reading, where feedback from lexical-level processes feeds back to letter-level processes (e.g. Heilbron et al 2020 Nature Comms.). This feedback is especially relevant for the reading of words in noisy conditions, as tested in the current manuscript, as lexical knowledge enhances letter representation in the visual cortex (the word superiority effect). This results in neural activity in multiple cortical areas varying over time, changing selectivity within a region at different measured time points (e.g. Woolnough et al 2021 Nature Human Behav.), which in the current study is simplified down to three discrete time windows, each attributed to different spatial locations.

We agree with the Reviewer that a full model of reading in the brain must include feed-back connections and share their sentiment that these feed-back processes play an important role and are a fascinating topic to study. The intent for the model presented in our study is very much to be a stepping stone towards extending the capabilities of models that do include such connections.

However, there is a problem of scale that cannot be ignored.

Current models of reading that do include feedback connections fall into the category we refer to in the paper as “traditional models” and all only a few layers deep and operate on very simplified inputs, such as pre-defined line segments, a few pixels, or even a list of prerecognized letters. The Heilbron et al. 2020 study that the Reviewer refers to is a good example of such a model. (This excellent and relevant work was somehow overlooked in our literature discussion in the Introduction. We thank the Reviewer for pointing it out to us.) Models incorporating realistic feed-back activity need these simplifications, because they have a tendency to no longer converge when there are too many layers and units. However, in order for models of reading to be able to simulate cognitive behavior such as resolving variations in font size or typeface, or distinguish text from non-text, they need to operate on something close to the pixel-level data, which means they need many layers and units.

Hence, as a stepping stone, it is reasonable to evaluate a model that has the necessary scale, but lacks the feed-back connections that would be problematic at this scale, to see what it can and cannot do in terms of explaining experimental effects in neuroimaging studies. This was the intended scope of our study. For the revision, we have attempted to make this more clear.

We have changed the title to be:

“Convolutional networks can model the functional modulation of the MEG responses associated with feed-forward processes during visual word recognition” and added the following to the Introduction:

“The simulated environments in these models are extremely simplified, partly due to computational limitations and partly due to the complex interaction of feed-forward and feed-back connectivity that causes problems with convergence when the model grows too large. Consequently, these models have primarily focused on feed-back lexico-semantic effects while oversimplifying the initial feed-forward processing of the visual input. 

[…]

This rather high level of visual representation sidesteps having to deal with issues such as visual noise, letters with different scales, rotations and fonts, segmentation of the individual letters, and so on. More importantly, it makes it impossible to create the visual noise and symbol string conditions used in the MEG study to modulate the type-I and type-II components. In order to model the process of visual word recognition to the extent where one may reproduce neuroimaging studies such as Vartiainen et al. (2011), we need to start with a model of vision that is able to directly operate on the pixels of a stimulus. We sought to construct a model that is able to recognize words regardless of length, size, typeface and rotation with very high accuracy, whilst producing activity that mimics the type-I, type-II, and N400m components which serve as snapshots of this process unfolding in the brain. For this model, we chose to focus on the early feed-forward processing occurring during visual word recognition, as the experimental setup in the MEG study was designed to demonstrate, rather than feed-back effects

[…]

By doing so, we restrict ourselves to an investigation of how well the three evoked components can be explained by a feed-forward CNN in an experimental setting designed to demonstrate feed-forward effects. > As such, the goal is not to present a complete model of all aspects of reading, which should include feed-back effects, but rather to demonstrate the effectiveness of using a model that has a realistic form of input when the aim is to align the model with the evoked responses observed during visual word recognition.”

And we have added the following to the Discussion section:

“In this paper we have restricted our simulations to feed-forward processes. Now, the way is open to incorporate convolution-and-pooling principles in models of reading that simulate feed-back processes as well, which should allow the model to capture more nuance in the Type-II and N400m components, as well as extend the simulation to encompass a realistic semantic representation. A promising way forward may be to use a network architecture like CORNet (Kubilius et al., 2019), that performs convolution multiple times in a recurrent fashion, yet simultaneously propagates activity forward after each pass. The introduction of recursion into the model will furthermore align it better with traditional-style models, since it can cause a model to exhibit attractor behavior (McLeod et al., 2000), which will be especially important when extending the model into the semantic domain.

Furthermore, convolution-and-pooling has recently been explored in the domain of predictive coding models (Ororbia & Mali, 2023), a type of model that seems particularly well suited to model feed-back processes during reading (Gagl et al., 2020; Heilbron et al., 2020; Nour Eddine et al., 2024).”

We also would like to point out to the Reviewer that we did in fact perform a correlation between the model and the MNE-dSPM source estimate of all cortical locations and timepoints (Figure 7B). Such a brain-wide correlation map confirms that the three dipole groups are excellent summaries of when and where interesting effects occur within this dataset.

The presented model needs substantial further development to be able to replicate, both behaviorally and neurally, many of the well-characterized phenomena seen in human behavior and neural recordings that are fundamental hallmarks of human visual word processing. Until that point, it is unclear what novel contributions can be gleaned from correlating low-dimensional model weights from these computational models with human neural data.

We hope that our revisions have clarified the goals and scope of this study. The CNN model we present in this study is a small but, we feel, essential piece in a bigger effort to employ deep learning techniques to further enhance already existing models of reading. In our revision, we have extended our discussion where to go from here and outline our vision on how these techniques could help us better model the phenomena the reviewer speaks of. We agree with the reviewer that there is a long way to go, and we are excited to be a part of it.

In addition to the changes described above, we now end the Discussion section as follows: 

“Despite its limitations, our model is an important milestone for computational models of reading that leverages deep learning techniques to encompass the entire computational process starting from raw pixels values to representations of wordforms in the mental lexicon. The overall goal is to work towards models that can reproduce the dynamics observed in brain activity observed during the large number of neuroimaging experiments performed with human volunteers that have been performed over the last few decades. To achieve this, models need to be able to operate on more realistic inputs than a collection of predefined lines or letter banks (for example: Coltheart et al., 2001; Heilbron et al., 2020; Laszlo & Armstrong, 2014; McClelland & Rumelhart, 1981; Nour Eddine et al., 2024). We have shown that even without feed-back connections, a CNN can simulate the behavior of three important MEG evoked components across a range of experimental conditions, but only if unit activations are noisy and the frequency of occurrence of words in the training dataset mimics their frequency of use in actual language.”

Reviewer #3 (Public Review):

The paper is rather qualitative in nature. In particular, the authors show that some resemblance exists between the behavior of some layers and some parts of the brain, but it is hard to quantitively understand how strong the resemblances are in each layer, and the exact impact of experimental settings such as the frequency balancing (which seems to only have a very moderate effect according to Figure 5).

The large focus on a qualitative evaluation of the model is intentional. The ability of the model to reproduce experimental effects (Figure 4) is a pre-requisite for any subsequent quantitative metrics (such as correlation) to be valid. The introduction of frequency balancing is a good example of this. As the reviewer points out, frequency balancing during training has only a moderate impact on correlation scores and from that point of view does not seem impactful. However, when we look at the qualitative evaluation, we see that with a large vocabulary, a model without frequency balancing fails to properly distinguish between consonant strings and (pseudo)words (Figure 4, 5th row). Hence, from the point of view of being able to reproduce experimental effects, frequency balancing has a large impact.

That said, the reviewer is right to highlight the value of quantitative analysis. An important limitation of the “traditional” models of reading that do not employ deep learning is that they operate in unrealistically simplified environments (e.g. input as predefined line segments, words of a fixed length), which makes a quantitative comparison with brain data problematic. The main benefit that deep learning brings may very well be the increase in scale that makes more direct comparisons with brain data possible. In our revision we attempt to capitalize on this benefit more. The reviewer has provided some helpful suggestions for doing so in their recommendations, which we discuss in detail below.

We have added the following discussion on the topic of qualitative versus quantitative analysis to the Introduction:

“We sought to construct a model that is able to recognize words regardless of length, size, typeface and rotation, as well as humans can, so essentially perfectly, whilst producing activity that mimics the type-I, type-II, and N400m components which serve as snapshots of this process unfolding in the brain.

[…]

These variations were first evaluated on their ability to replicate the experimental effects in that study, namely that the type-I response is larger for noise embedded words than all other stimuli, the type-II response is larger for all letter strings than symbols, and that the N400m is larger for real and pseudowords than consonant strings. Once a variation was found that could reproduce these effects satisfactorily, it was further evaluated based on the correlation between the amount of activation of the units in the model and MEG response amplitude.”

And follow this up in the Discussion with a new sub-section entitled “On the importance of experimental contrasts and qualitative analysis of the model”

The experiments only consider a rather outdated vision model (VGG).

VGG was designed to use a minimal number of operations (convolution-and-pooling, fullyconnected linear steps, ReLU activations, and batch normalization) and rely mostly on scale to solve the classification task. This makes VGG a good place to start our explorations and see how far a basic CNN can take us in terms of explaining experimental MEG effects in visual word recognition. However, we agree with the reviewer that it is easy to envision more advanced models that could potentially explain more. In our revision, we expand on the question of where to go from here and outline our vision on what types of models would be worth investigating and how one may go about doing that in a way that provides insights beyond higher correlation values.

We have included the following in our Discussion sub-sections on “Limitations of the current model and the path forward”:

“The VGG-11 architecture was originally designed to achieve high image classification accuracy on the ImageNet challenge (Simonyan & Zisserman, 2015). Although we have introduced some modifications that make the model more biologically plausible, the final model is still incomplete in many ways as a complete model of brain function during reading.

[…]

In this paper we have restricted our simulations to feed-forward processes. Now, the way is open to incorporate convolution-and-pooling principles in models of reading that simulate feed-back processes as well, which should allow the model to capture more nuance in the Type-II and N400m components, as well as extend the simulation to encompass a realistic semantic representation. A promising way forward may be to use a network architecture like CORNet (Kubilius et al., 2019), that performs convolution multiple times in a recurrent fashion, yet simultaneously propagates activity forward after each pass. The introduction of recursion into the model will furthermore align it better with traditional-style models, since it can cause a model to exhibit attractor behavior (McLeod et al., 2000), which will be especially important when extending the model into the semantic domain. Furthermore, convolution-and-pooling has recently been explored in the domain of predictive coding models (Ororbia & Mali, 2023), a type of model that seems particularly well suited to model feed-back processes during reading (Gagl et al., 2020; Heilbron et al., 2020; Nour Eddine et al., 2024).”

Reviewer #3 (Recommendations For The Authors):

(1) The method used to select the experimental conditions under which the behavior of the CNN is the most brain-like is rather qualitative (Figure 4). It would have been nice to have a plot where the noisyness of the activations, the vocab size and the amount of frequency balancing are varied continuously, and show how these three parameters impact the correlation of the model layers with the MEG responses.

We now include this analysis (Figure 6 in the revised manuscript, Supplementary Figures 47) and discuss these factors in the revised Results section:

“Various other aspects of the model architecture were evaluated which ultimately did not lead to any improvements of the model. The response profiles can be found in the supplementary information (Supplementary Figures 4–7) and the correlations between the models and the MEG components are presented in Figure 6. The vocabulary of the final model (10 000) exceeds the number of units in its fullyconnected layers, which means that a bottleneck is created in which a sub-lexical representation is formed. The number of units in the fully-connected layers, i.e. the width of the bottleneck, has some effect on the correlation between model and brain (Figure 6A), and the amount of noise added to the unit activations less so (Figure 6B). We already saw that the size of the vocabulary, i.e. the number of wordforms in the training data and number of units in the output layer of the model, had a large effect on the response profiles (Figure 4). Having a large vocabulary is of course desirable from a functional point of view, but also modestly improves correlation between model and brain (Figure 6C). For large vocabularies, we found it beneficial to apply frequency-balancing of the training data, meaning that the number of times a word-form appears in the training data is scaled according to its frequency in a large text corpus. However, this cannot be a one-to-one scaling, since the most frequent words occur so much more often than other words that the training data would consist of mostly the top-ten most common words, with less common words only occurring once or not at all. Therefore, we decided to scale not by the frequency 𝑓 directly, but by 𝑓𝑠, where 0 < 𝑠 < 1, opting for 𝑠 = 0.2 for the final model (Figure 6D).”

(2) It is not clear which layers exactly correspond to which of the three response components. For this to be clearer, it would have been nice to have a plot with all the layers of VGG on the x-axis and three curves corresponding to the correlation of each layer with each of the three response components.

This is a great suggestion that we were happy to incorporate in the revised version of the manuscript. Every figure comparing the response patterns of the model and brain now includes a panel depicting the correlation between each layer of the model and each of the three MEG components (Figures 4 & 5, Supplementary Figures 2-5). This has given us (and now also the reader) the ability to better benchmark the different models quantitatively, adding to our discussion on qualitative to quantitative analysis.

(3) It is not clear to me why the authors report the correlation of all layers with the MEG responses in Figure 5: why not only report the correlation of the final layers for N400, and that of the first layers for type-I?

We agree with the reviewer that it would have been better to compare the correlation scores for those layers which response profile matches the MEG component. While the old Figure 5 has been merged with Figure 4, and now provides the correlations between all the layers and all MEG components, we have taken the Reviewer’s advice and marked the layers which qualitatively best correspond to each MEG component, so the reader can take that into account when interpreting the correlation scores.

(4) The authors mention that the reason that they did not reproduce the protocol with more advanced vision models is that they needed the minimal setup capable of yielding the desired experiment effect. I am not fully convinced by this and think the paper could be significantly strengthened by reporting results for a vision transformer, in particular to study the role of attention layers which are expected to play an important role in processing higher-level features.

We appreciate and share the Reviewer’s enthusiasm in seeing how other model architectures would fare when it comes to modeling MEG components. However, we regard modifying the core model architecture (i.e., a series of convolution-and-pooling followed by fully-connected layers) to be out of scope for the current paper.

One of the key points of our study is to create a model that reproduces the experimental effects of an existing MEG study, which necessitates modeling the initial feed-forward processing from pixel to word-form. For this purpose, a convolution-and-pooling model was the obvious choice, because these operations play a big role in cognitive models of vision in general. In order to properly capture all experimental contrasts in the MEG study, many variations of the CNN were trained and evaluated. This iterative design process concluded when all experimental contrasts could be faithfully reproduced.

If we were to explore different model architectures, such as a transformer architecture, reproducing the experimental contrasts of the MEG study would no longer be the end goal, and it would be unclear what the end goal should be. Maximizing correlation scores has no end, and there are a nearly endless number of model architectures one could try. We could bring in a second MEG study with experimental contrasts that the CNN cannot explain and a transformer architecture potentially could and set the end goal to explain all experimental effects in both MEG studies. But even if we had access to such a dataset, this would almost double the length of the paper, which is already too long.

eLife Assessment

Hardly anything is known about the genetic basis and mechanism of male-killing. Recently, a gene called oscar, in the bacterium Wolbachia, was implicated in killing male corn borer moths by interfering with moth genes that control sex determination and proper dosage of sex-specific genes. In this paper, the authors show that a distantly related oscar gene in another strain of Wolbachia kills male tea tortrix moths in a similar mechanism. This valuable study cements our understanding of the sophisticated way that Wolbachia kills male moths and butterflies (Lepidoptera) so early in their development. The conclusions are supported by solid evidence.

Reviewer #1 (Public review):

Summary:

Insects and their relatives are commonly infected with microbes that are transmitted from mothers to their offspring. A number of these microbes have independently evolved the ability to kill the sons of infected females very early in their development; this male killing strategy has evolved because males are transmission dead-ends for the microbe. A major question in the field has been to identify the genes that cause male killing and to understand how they work. This has been especially challenging because most male-killing microbes cannot be genetically manipulated. This study focuses on a male-killing bacterium called Wolbachia. Different Wolbachia strains kill male embryos in beetles, flies, moths, and other arthropods. This is remarkable because how sex is determined differs widely in these hosts. Two Wolbachia genes have been previously implicated in male-killing by Wolbachia: oscar (in moth male-killing) and wmk (in fly male-killing). The genomes of some male-killing Wolbachia contain both of these genes, so it is a challenge to disentangle the two.

This paper provides strong evidence that oscar is responsible for male-killing in moths. Here, the authors study a strain of Wolbachia that kills males in a pest of tea, Homona magnanima. Overexpressing oscar, but not wmk, kills male moth embryos. This is because oscar interferes with masculinizer, the master gene that controls sex determination in moths and butterflies. Interfering with the masculinizer gene in this way leads the (male) embryo down a path of female development, which causes problems in regulating the expression of genes that are found on the sex chromosomes.

Strengths:

The authors use a broad number of approaches to implicate oscar, and to dissect its mechanism of male lethality. These approaches include: a) overexpressing oscar (and wmk) by injecting RNA into moth eggs, b) determining the sex of embryos by staining female sex chromosomes, c) determining the consequences of oscar expression by assaying sex-specific splice variants of doublesex, a key sex determination gene, and by quantifying gene expression and dosage of sex chromosomes, using RNASeq, and d) expressing oscar along with masculinizer from various moth and butterfly species, in a silkmoth cell line. This extends recently published studies implicating oscar in male-killing by Wolbachia in Ostrinia corn borer moths, although the Homona and Ostrinia oscar proteins are quite divergent. Combined with other studies, there is now broad support for oscar as the male-killing gene in moths and butterflies (i.e. order Lepidoptera).

Reviewer #2 (Public review):

Wolbachia are maternally transmitted bacteria that can manipulate host reproduction in various ways. Some Wolbachia induce male killing (MK), where the sons of infected mothers are killed during development. Several MK-associated genes have been identified in Homona magnanima, including Hm-oscar and wmk-1-4, but the mechanistic links between these Wolbachia genes and MK in the native host are still unclear.

In this manuscript, Arai et al. show that Hm-oscar is the gene responsible for Wolbachia-induced MK in Homona magnanima. They provide evidence that Hm-Oscar functions through interactions with the sex determination system. They also found that Hm-Oscar disrupts sex determination in male embryos by inducing female-type dsx splicing and impairing dosage compensation. Additionally, Hm-Oscar suppresses the function of Masc. The manuscript is well-written and presents intriguing findings. The results support their conclusions regarding the diversity and commonality of MK mechanisms, contributing to our understanding of the mechanisms and evolutionary aspects of Wolbachia-induced MK.

Author response:

The following is the authors’ response to the previous reviews.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Insects and their relatives are commonly infected with microbes that are transmitted from mothers to their offspring. A number of these microbes have independently evolved the ability to kill the sons of infected females very early in their development; this male killing strategy has evolved because males are transmission dead-ends for the microbe. A major question in the field has been to identify the genes that cause male killing and to understand how they work. This has been especially challenging because most male-killing microbes cannot be genetically manipulated. This study focuses on a male-killing bacterium called Wolbachia. Different Wolbachia strains kill male embryos in beetles, flies, moths, and other arthropods. This is remarkable because how sex is determined differs widely in these hosts. Two Wolbachia genes have been previously implicated in male-killing by Wolbachia: oscar (in moth male-killing) and wmk (in fly male-killing). The genomes of some male-killing Wolbachia contain both of these genes, so it is a challenge to disentangle the two.

This paper provides strong evidence that oscar is responsible for male-killing in moths. Here, the authors study a strain of Wolbachia that kills males in a pest of tea, Homona magnanima. Overexpressing oscar, but not wmk, kills male moth embryos. This is because oscar interferes with masculinizer, the master gene that controls sex determination in moths and butterflies. Interfering with the masculinizer gene in this way leads the (male) embryo down a path of female development, which causes problems in regulating the expression of genes that are found on the sex chromosomes.

We would like to thank you for evaluating our manuscript.

Strengths:

The authors use a broad number of approaches to implicate oscar, and to dissect its mechanism of male lethality. These approaches include: a) overexpressing oscar (and wmk) by injecting RNA into moth eggs, b) determining the sex of embryos by staining female sex chromosomes, c) determining the consequences of oscar expression by assaying sex-specific splice variants of doublesex, a key sex determination gene, and by quantifying gene expression and dosage of sex chromosomes, using RNASeq, and d) expressing oscar along with masculinizer from various moth and butterfly species, in a silkmoth cell line. This extends recently published studies implicating oscar in male-killing by Wolbachia in Ostrinia corn borer moths, although the Homona and Ostrinia oscar proteins are quite divergent. Combined with other studies, there is now broad support for oscar as the male-killing gene in moths and butterflies (i.e. order Lepidoptera). So an outstanding question is to understand the role of wmk. Is it the master male-killing gene in insects other than Lepidoptera and if so, how does it operate?

We would like to thank you for evaluating our manuscript. Our data demonstrated that Oscar homologs play important roles in male-killing phenotypes in moths and butterflies; however, the functional relevance of wmk remains uncertain. As you noted, whether wmk acts as a male-killing gene in insects such as flies and beetles—or even in certain lepidopteran species—requires further investigation using diverse insect models, which we are eager to explore in future research.

Weaknesses:

I found the transfection assays of oscar and masculinizer in the silkworm cell line (Figure 4) to be difficult to follow. There are also places in the text where more explanation would be helpful for non-experts.

Thank you for your suggestion. We have revised the section on the cell-based experiment. Further, we revised the manuscript to make it accessible to a broader audience. We believe these revisions have significantly improved the clarity and comprehensiveness of our manuscript.

Reviewer #2 (Public review):

Summary:

Wolbachia are maternally transmitted bacteria that can manipulate host reproduction in various ways. Some Wolbachia induce male killing (MK), where the sons of infected mothers are killed during development. Several MK-associated genes have been identified in Homona magnanima, including Hm-oscar and wmk-1-4, but the mechanistic links between these Wolbachia genes and MK in the native host are still unclear.

In this manuscript, Arai et al. show that Hm-oscar is the gene responsible for Wolbachia-induced MK in Homona magnanima. They provide evidence that Hm-Oscar functions through interactions with the sex determination system. They also found that Hm-Oscar disrupts sex determination in male embryos by inducing female-type dsx splicing and impairing dosage compensation. Additionally, Hm-Oscar suppresses the function of Masc. The manuscript is well-written and presents intriguing findings. The results support their conclusions regarding the diversity and commonality of MK mechanisms, contributing to our understanding of the mechanisms and evolutionary aspects of Wolbachia-induced MK.

We would like to thank you for evaluating our manuscript.

Comments on revisions:

The authors have already addressed the reviewer's concerns.

We would like to thank you for evaluating our manuscript.

Reviewer #3 (Public review):

Summary:

Overall, this is a clearly written manuscript with nice hypothesis testing in a non-model organism that addresses the mechanism of Wolbachia-mediated male killing. The authors aim to determine how five previously identified male-killing genes (encoded in the prophage region of the wHm Wolbachia strain) impact the native host, Homona magnanima moths. This work builds on the authors' previous studies in which

(1) they tested the impact of these same wHm genes via heterologous expression in Drosophila melanogaster

(2) also examined the activity of other male-killing genes (e.g., from the wFur Wolbachia strain in its native host: Ostrinia furnacalis moths).

Advances here include identifying which wHm gene most strongly recapitulates the male-killing phenotype in the native host (rather than in Drosophila), and the finding that the Hm-Oscar protein has the potential for male-killing in a diverse set of lepidopterans, as inferred by the cell-culture assays.

We would like to thank you for evaluating our manuscript.

Strengths:

Strengths of the manuscript include the reverse genetics approaches to dissect the impact of specific male-killing loci, and use of a "masculinization" assay in Lepidopteran cell lines to determine the impact of interactions between specific masc and oscar homologs.

We would like to thank you for evaluating our manuscript.

Weaknesses:

It is clear from Figure 1 that the combinations of wmk homologs do not cause male killing on their own here. While I largely agree with the author's conclusions that oscar is the primary MK factor in this system, I don't think we can yet rule out that wmk(s) may work synergistically or interactively with oscar in vivo. This might be worth a small note in the discussion. (eg at line 294 'indicating that wmk likely targets factors other than masc." - this could be downstream of the impacts of oscar; perhaps dependent on oscar-mediated impacts on masc first).

We sincerely appreciate your suggestion. Whilst wmk genes themselves did not exhibit apparent lethal effects on the native host, as you noted, we cannot entirely rule out the possibility that wmk may be involved in male-killing actions, either directly or indirectly assisting the function of Hb-oscar. Following your suggestion, we have added a brief note in the discussion section regarding the interpretation of wmk functions.

“In addition, Katsuma et al. (2022) reported that the wmk homologs encoded by wFur did not affect the masculinizing function of masc in vitro, indicating that wmk likely targets factors other than masc. Whilst we cannot rule out the possibility that wmk may work synergistically or interactively with oscar in vivo—potentially acting downstream of oscar’s impact—our results strongly suggested that Wolbachia strains have acquired multiple MK genes through evolution.” (lines 287-292)

Regarding the perceived male-bias in Figure 2a: I think readers might be interpreting "unhatched" as "total before hatching". You could eliminate ambiguity by perhaps splitting the bars into male and female, and then within a bar, coloring by hatched versus unhatched. But this is a minor point, and I think the updated text helps clarify this.

Thank you for your suggestion. We have accordingly revised the figure 2a. In addition, we have included more detailed information in the first sentence of the section Males are killed mainly at the embryonic stage.

“The sex of hatched larvae (neonates) and the remaining unhatched embryos was determined by the presence or absence of W chromatin, a condensed structure of the female-specific W chromosome observed during interphase.” (lines 171-173)

The new Figure 4b looks to be largely redundant with the oscar information in Figure 1a.

Thank you for your suggestion. We have removed Figure 4b due to its overlap with Figure 1a and have incorporated relevant figure legends into the Figure 1a legend.

Updated statistical comparisons for the RNA-seq analysis are helpful. However these analyses are based on single libraries (albeit each a pool of many individuals), so this is still a weaker aspect of the manuscript.

Thank you for your suggestion. As you noted, the use of single libraries (due to the limited number of available individuals, though each includes approximately 50 males and females) may be a potential limitation of this study. However, as demonstrated in the qPCR assay for the Z-linked gene provided in the previous revision, we believe that our data and conclusion—that Wolbachia/ Hb-oscar disrupts dosage compensation by causing the overexpression of Z-linked genes—are well-supported and robust.

The new information on masc similarity is useful (Fig 4d) - if the authors could please include a heatmap legend for the colors, that would be helpful. Also, please avoid green and red in the same figure when key for interpretation.

Thank you for your suggestion. We have accordingly included a heatmap legend and revised the colors.

Figure 1A "helix-turn-helix" is misspelled. ("tern").

We have revised.

Recommendations for the authors:

Comments from the reviewing editor: I would suggest you address the comments of the reviewer on the revised version.

We have further revised the manuscript to address all the questions, comments and suggestions provided by the reviewers. We believe that the resulting revisions have significantly enhanced the quality and comprehensiveness of our manuscript.

Reviewer #1 (Recommendations for the authors):

Thank you for revising this manuscript. I have a few last recommendations:

- Line 214: re: 'Statistical data are available in the supplementary data file', it would be more helpful to add a few words here that actually summarize the statistical results

We would like to thank you for your suggestion. We have revised the sentence to describe the overview of the statistical results.

“RNA-seq analysis revealed that, in Hm-oscar-injected embryos, Z-linked genes (homologs on the B. mori chromosomes 1 and 15) were more expressed in males than in females (Fig. 3a), which was not observed in the GFP-injected group (Fig. 3b). Similarly, as previously reported by Arai et al. (2023a), high levels of Z-linked gene expression were also observed in wHm-t-infected males, but not in NSR males (Fig. 3c,d). The high (i.e., doubled) Z-linked gene expression in both Hm-oscar-expressed and wHm-t-infected males was further confirmed by quantification of the Z-linked Hmtpi gene (Fig. 3e). These trends were statistically supported, with all data available in the supplementary data file.” (lines 205-213)

- Figure 1 legend: do you mean 'bridged' instead of 'brigged'?

We have accordingly revise, thank you for the suggestion.

eLife Assessment

The authors have developed a biosensor for programmed cell death. They use this biosensor to provide cell death measurements in a specific early development time. The findings useful in a specific context; however, the application of this biosensor is incomplete as it does not take into account existing literature and is missing controls.

Joint Public Review:

Summary:

Jia and colleagues developed a fluorescence resonance energy transfer (FRET)-based biosensor to study programmed cell death in the zebrafish spinal cord. They applied this tool to study death of zebrafish spinal motor neurons.

Strengths:

Their analysis shows that the tool is a useful biosensor of motor neuron apoptosis in living zebrafish and can reveal which part of the neuron undergoes caspase activation first.

Weaknesses:

As far as it is possible to tell, the authors focus on death of motor neurons innervating axial muscles. Previous work from over 30 years ago revealed that only a small number of these motor neurons die early in development. So this is not new, although following the cells and learning details of their apoptosis is new. Most of the work on motor neuron death in tetrapods was carried out on limb innervating motor neurons. Zebrafish have paired pectoral and pelvic fins, homologs of tetrapod paired limbs. These fins are innervated by distinct sets of motor neurons in zebrafish, as they are in tetrapods. However, the authors have not focused on these particular motor neurons, and thus have not made a fair comparison with tetrapods. In fact, they do not tell us which spinal levels they observed or whether they have been consistent from animal to animal. Pelvic fins emerge much later than pectoral fins in zebrafish, so it is possible that the time frame during which the authors imaged motor neuron death does not include motor neurons innervating pelvic fins.

Author response:

The following is the authors’ response to the previous reviews.

Reviewer 1:

(1) The results do not support the conclusions. The main "selling point" as summarized in the title is that the apoptotic rate of zebrafish motorneurons during development is strikingly low (~2% ) as compared to the much higher estimate (~50%) by previous studies in other systems. The results used to support the conclusion are that only a small percentage (under 2%) of apoptotic cells were found over a large population at a variety of stages 24-120hpf. This is fundamentally flawed logic, as a short-time window measure of percentage cannot represent the percentage on the long-term. For example, at any year under 1% of human population die, but over 100 years >99% of the starting group will have died. To find the real percentage of motorneurons that died, the motorneurons born at different times must be tracked over long term, or the new motorneuron birth rate must be estimated. Similar argument can be applied to the macrophage results.<br />

In the revised manuscript (revised Figure 4), we extended the observation time window as long as possible, from 24 hpf to 240 hpf. After 240 hpf, the transparency of zebrafish body decreased dramatically, which made optical imaging quite difficult.

We are confident that this 24-240 hpf time window covers the major time window during which motor neurons undergo programmed cell death during zebrafish early development. We chose the observation time window based on the following two reasons: 1) Previous studies showed that although the time windows of motor neuron death vary in chick (E5-E10), mouse (E11.5-E15.5), rat (E15-E18), and human (11-25 weeks of gestation), the common feature of these time windows is that they are all the developmental periods when motor neurons contact with muscle cells. The contact between zebrafish motor neurons and muscle cells occurs before 72 hpf, which is included in our observation time window. 2) Most organs of zebrafish form before 48-72 hpf, and they complete hatching during 48-72 hpf. Food-seeking and active avoidance behaviors also start at 72 hpf, indicating that motor neurons are fully functional at 72 hpf.

Previous studies in zebrafish have shown that the production of spinal cord motor neurons largely ceases before 48 hpf, and then the motor neurons remain largely constant until adulthood (doi: 10.1016/j.celrep.2015.09.050; 10.1016/j.devcel.2013.04.012; 10.1007/BF00304606; 10.3389/fcell.2021.640414). Our observation time window covers the major motor neuron production process. Therefore, we believe that neurogenesis will not affect our findings and conclusions.

Although we are confident that 240 h tracking is long enough to measure the motor neuron death rate, several sentences have been added in the discussion part, “In our manuscript, we tracked the motor neuron death in live zebrafish until 240 hpf, which was the longest time window we could achieve. But there was still a possibility that zebrafish motor neurons might die after 240 hpf.”

We agreed that the “2%” description might not be very accurate. Thus, we have revised our title to “Zebrafish live imaging reveals a surprisingly small percentage of spinal cord motor neurons die during early development.”

(2) The conclusion regarding timing of axon and cell body caspase activation and apoptosis timing also has clear issues. The ~minutes measurement are too long as compared to the transport/diffusion timescale between the cell body and the axon, caspase activity could have been activated in the cell body and either caspase or the cleaved sensor move to the axon in several seconds. The authors' results are not high frequency enough to resolve these dynamics. Many statements suggest oversight of literature, for example, in abstract "however, there is still no real-time observation showing this dying process in live animals.".

Real-time imaging of live animals is quite challenging in the field. Currently, using confocal microscopy, we can only achieve minute-scale tracking. In the future, with more advanced imaging techniques, the sensor fish in the present study may provide us with more detailed information on motor neuron death. We have removed “real-time” from our revised manuscript. We also revised the mentioned sentence in the abstract.

(3) Many statements should use more scholarly terms and descriptions from the spinal cord or motorneuron, neuromuscular development fields, such as line 87 "their axons converged into one bundle to extend into individual somite, which serves as a functional unit for the development and contraction of muscle cells"

We have removed this sentence.

(4) The transgenic line is perhaps the most meaningful contribution to the field as the work stands. However, mnx1 promoter is well known for its non-specific activation - while the images do suggest the authors' line is good, motorneuron markers should be used to validate the line. This is especially important for assessing this population later as mnx1 may be turned off in mature neurons. The author's response regarding mnx1 specificity does not mitigate the original concern.

The mnx1 promoter has been widely used to label motor neurons in transgenic zebrafish. Previous studies have shown that most of the cells labeled in the mnx1 transgenic zebrafish are motor neurons. In this study, we observed that the neuronal cells in our sensor zebrafish formed green cell bodies inside of the spinal cord and extended to the muscle region, which is an important morphological feature of the motor neurons.

Furthermore, a few of those green cell bodies turned into blue apoptotic bodies inside the spinal cord and changed to blue axons in the muscle regions at the same time, which strongly suggests that those apoptotic neurons are not interneurons.

In fact, no matter what method is used, such as using antibodies to stain specific markers to label motor neurons, 100% specificity cannot be achieved. More importantly, although the mnx1 promoter might have labeled some interneurons, this will not affect our major finding that only a small percentage of spinal cord motor neurons die during the early development of zebrafish.

Reviewer 2:

(1) Title: The 50% figure of motor neurons dying through apoptosis during early vertebrate development is not precisely accurate. In papers referenced by the authors, there is a wide distribution of percentages of motor neurons that die depending on the species and the spinal cord region. In addition, the authors did not examine limb-innervating motor neurons, which are the ones best studied in motor neuron programmed cell death in other species. Thus, a better title that reflects what they actually show would be something like "A surprisingly small percentage of early developing zebrafish motor neurons die through apoptosis in non-limb innervating regions of the spinal cord."

In fish, there are no such structures as limbs, although fins may be evolutionarily related to limbs. In our manuscript, we studied the naturally occurring motor neuron death in the whole spinal cord during the early stage of zebrafish development. The death of motor neurons in limb-innervating motor neurons has been extensively studied in chicks and rodents, as it is easy to undergo operations such as amputation. However, previous studies have shown this dramatic motor neuron death occurs not only in limb-innervating motor neurons but also in other spinal cord motor neurons (doi: 10.1006/dbio.1999.9413).

We have revised our title to “Zebrafish live imaging reveals a surprisingly small percentage of spinal cord motor neurons die during early development.”

(2) lines 18-19: "embryonic stage of vertebrates" is very broad, since zebrafish are also vertebrates; it would be better to be more specific

lines 25-26: The authors should be more specific about which animals have widespread neuronal cell death.

We have revised our manuscript accordingly.

(3) lines 98-99; 110-111; 113; 122-123; 140-141: A cell can undergo apoptosis. But an axon, which is only part of a cell, cannot undergo apoptosis. Especially since the axon doesn't have a separate nucleus, and the definition of apoptosis usually includes nuclear fragmentation. A better subheading would describe the result, which is that caspase activation is seen in both the cell body and the axon.

We have revised the subheadings and related words in the manuscript accordingly. In the introduction, we also revised the expression of the third aim from “Which part of a neuron (cell body vs. axon) will die first?” to “Which part of a neuron (cell body vs. axon) will degrade first?”.

(4) lines 159-160; 178-179: This is an oversimplification of the literature. The authors should spell out which populations of motor neuron have been examined and say something about the similarities and difference in motor neuron death.

We have revised it accordingly.

(5) lines 200; 216: The authors did not observe macrophages engulfing motor neurons. But that does not mean that they cannot. Making the conclusion stated in this subheading would require some kind of experiment, not just observations.

We did observe few colocalizations of macrophages and dead motor neurons.  To more accurately express these data, in the revised manuscript, we used “colocalization” to replace “engulfment.” The subheading has been revised to “Most dead motor neurons were not colocalized with macrophages.” Accordingly, panel C of Figure 5 has also been revised.

(6) lines 234-246: The authors seem to have missed the point about VaP motor neuron death, which was two-fold. First, VaP death has been previously described, thus it could serve as a control for the work in this paper, especially since the conditions underlying VaP death and survival have been experimentally tested. Second, they should acknowledge that previous work showed that at least some motor neuron death in zebrafish differs from that described in chick and rodents. This conclusion came from work showing that death of VaP is independent of limitations in muscle innervation area, suggesting it is not coupled to muscle-derived neurotrophic factors.

Figures: The authors should say which level of the spinal cord they examined in each figure.

We have compared our findings with previous findings in the revised manuscript. The death of VaP motor neurons is not related to neurotrophic factors, but the death of other motor neurons may be related to neurotrophic factors, which needs further study and evidence. Our study examined the overall motor neuron apoptosis regardless of the causes and locations. To avoid misunderstanding, in the revised manuscript, we removed the data and words related to neurotrophic factors.

We also extended the observation time window as long as possible, from 24 hpf to 240 hpf (revised Figure 4). After 240 hpf, the transparency of zebrafish body decreased dramatically, which made the optical imaging quite difficult.

eLife Assessment

It is known from model organisms that genes' effects on traits are often modulated by environmental variables, but similar gene-by-environment (GxE) interactions have been difficult to detect using statistical analyses of genomic data, e.g., in humans. This study introduces a new framework to estimate gene-by-environment effects, treating it as a bias-variance tradeoff problem. The authors convincingly show that greater statistical power can be achieved in detecting GxE if an underlying model of polygenic GxE is assumed. This polygenic amplification model is a truly novel view with fundamental promise for the detection of GxE in genomic datasets, especially with continued development to detect more complex signals of amplification.

Reviewer #1 (Public review):

Experiments in model organisms have revealed that the effects of genes on heritable traits are often mediated by environmental factors -- so-called gene-by-environment (or GxE) interactions. In human genetics, however, where indirect statistical approaches must be taken to detect GxE, limited evidence has been found for pervasive GxE interactions. The present manuscript argues that the failure of statistical methods to detect GxE may be due to how GxE is modelled (or not modelled) by these methods.

The authors show, via re-analysis of an existing dataset in Drosophila, that a polygenic 'amplification' model can parsimoniously explain patterns of differential genetic effects across environments. (Work from the same lab had previously shown that the amplification model is consistent with differential genetic effects across the sexes for a number of traits in humans.) The parsimony of the amplification model allows for powerful detection of GxE in scenarios in which it pertains, as the authors show via simulation.

Before the authors consider polygenic models of GxE, however, they present a very clear analysis of a related question around GxE: When one wants to estimate the effect of an individual allele in a particular environment, when is it better to stratify one's sample by environment (reducing sample size, and therefore increasing the variance of the estimator) versus using the entire sample (including individuals not in the environment of interest, and therefore biasing the estimator away from the true effect specific to the environment of interest)? Intuitively, the sample-size cost of stratification is worth paying if true allelic effects differ substantially between the environment of interest and other environments (i.e., GxE interactions are large), but not worth paying if effects are similar across environments. The authors quantify this trade-off in a way that is both mathematically precise and conveys the above intuition very clearly. They argue on its basis that, when allelic effects are small (as in highly polygenic traits), single-locus tests for GxE may be substantially underpowered.

The paper is an important further demonstration of the plausibility of the amplification model of GxE, which, given its parsimony, holds substantial promise for the detection and characterization of GxE in genomic datasets. However, the empirical and simulation examples considered in the paper (and previous work from the same lab) are somewhat "best-case" scenarios for the amplification model, with only two environments and with these environments amplifying equally the effects of only a single set of genes. It would be an important step forward to demonstrate the possibility of detecting amplification in more complex scenarios, with multiple environments each differentially modulating the effects of multiple sets of genes. This could be achieved via simulations similar to those presented in the current manuscript.

Comments on revisions:

The authors have (with reasonable justification) said that my main recommendations for strengthening the conclusions of the paper are beyond its scope, and they have thoughtfully responded to my (and the other reviewer's) other comments. The paper is now more clearly written---in particular, the connection between the single-locus bias-variance tradeoff calculations and the polygenic results is much more transparent than before. Given that the authors have (again, with fair justification) chosen not to address my major comment, my broad assessment of the paper is unchanged---I think it is an important contribution to a critical topic---and I have no further comments for its improvement (though I note an issue with figure referencing in the captions of Supplementary Figs S2 and S3).

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Experiments in model organisms have revealed that the effects of genes on heritable traits are often mediated by environmental factors---so-called gene-by-environment (or GxE) interactions. In human genetics, however, where indirect statistical approaches must be taken to detect GxE, limited evidence has been found for pervasive GxE interactions. The present manuscript argues that the failure of statistical methods to detect GxE may be due to how GxE is modelled (or not modelled) by these methods.

The authors show, via re-analysis of an existing dataset in Drosophila, that a polygenic ‘amplification’ model can parsimoniously explain patterns of differential genetic effects across environments. (Work from the same lab had previously shown that the amplification model is consistent with differential genetic effects across the sexes for several traits in humans.) The parsimony of the amplification model allows for powerful detection of GxE in scenarios in which it pertains, as the authors show via simulation.

Before the authors consider polygenic models of GxE, however, they present a very clear analysis of a related question around GxE: When one wants to estimate the effect of an individual allele in a particular environment, when is it better to stratify one’s sample by environment (reducing sample size, and therefore increasing the variance of the estimator) versus using the entire sample (including individuals not in the environment of interest, and therefore biasing the estimator away from the true effect specific to the environment of interest)? Intuitively, the sample-size cost of stratification is worth paying if true allelic effects differ substantially between the environment of interest and other environments (i.e., GxE interactions are large), but not worth paying if effects are similar across environments. The authors quantify this trade-off in a way that is both mathematically precise and conveys the above intuition very clearly. They argue on its basis that, when allelic effects are small (as in highly polygenic traits), single-locus tests for GxE may be substantially underpowered.

The paper is an important further demonstration of the plausibility of the amplification model of GxE, which, given its parsimony, holds substantial promise for the detection and characterization of GxE in genomic datasets. However, the empirical and simulation examples considered in the paper (and previous work from the same lab) are somewhat “best-case” scenarios for the amplification model, with only two environments, and with these environments amplifying equally the effects of only a single set of genes. It would be an important step forward to demonstrate the possibility of detecting amplification in more complex scenarios, with multiple environments each differentially modulating the effects of multiple sets of genes. This could be achieved via simulations similar to those presented in the current manuscript.

Reviewer #2 (Public Review):

Summary:

Wine et al. describe a framework to view the estimation of gene-context interaction analysis through the lens of bias-variance tradeoff. They show that, depending on trait variance and context-specific effect sizes, effect estimates may be estimated more accurately in context-combined analysis rather than in context-specific analysis. They proceed by investigating, primarily via simulations, implications for the study or utilization of gene-context interaction, for testing and prediction, in traits with polygenic architecture. First, the authors describe an assessment of the identification of context-specificity (or context differences) focusing on “top hits” from association analyses. Next, they describe an assessment of polygenic scores (PGSs) that account for context-specific effect sizes, showing, in simulations, that often the PGSs that do not attempt to estimate context-specific effect sizes have superior prediction performance. An exception is a PGS approach that utilizes information across contexts. Strengths:

The bias-variance tradeoff framing of GxE is useful, interesting, and rigorous. The PGS analysis under pervasive amplification is also interesting and demonstrates the bias-variance tradeoff.

Weaknesses:

The weakness of this paper is that the first part -- the bias-variance tradeoff analysis -- is not tightly connected to, i.e. not sufficiently informing, the later parts, that focus on polygenic architecture. For example, the analysis of “top hits” focuses on the question of testing, rather than estimation, and testing was not discussed within the bias-variance tradeoff framework. Similarly, while the PGS analysis does demonstrate (well) the bias-variance tradeoff, the reader is left to wonder whether a bias-variance deviation rule (discussed in the first part of the manuscript) should or could be utilized for PGS construction.

We thank the editors and the reviewers for their thoughtful critique and helpful suggestions throughout. In our revision, we focused on tightening the relationship between the analytical single variant bias-variance tradeoff derivation and the various empirical analyses that follow.

We improved discussion of our scope and what is beyond our scope. For example, our language was insufficiently clear if it suggested to the editor and reviewers that we are developing a method to characterize polygenic GxE. Developing a new method that does so (let alone evaluating performance across various scenarios) is beyond the scope of this manuscript.

Similarly, we clarify that we use amplification only as an example of a mode of GxE that is not adequately characterized by current approaches. We do not wish to argue it is an omnibus explanation for all GxE in complex traits. In many cases, a mixture of polygenic GxE relationships seems most fitting (as observed, for example, in Zhu et al., 2023, for GxSex in human physiology).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

MAJOR COMMENT

The amplification model is based on an understanding of gene networks in which environmental variables concertedly alter the effects of clusters of genes, or modules, in the network (e.g., if an environmental variable alters the effect of some gene, it indirectly and proportionately alters the effects of genes downstream of that gene in the network---or upstream if the gene acts as a bottleneck in some pathway). It is clear in this model that (i) multiple environmental variables could amplify distinct modules, and (ii) a single environmental variable could itself amplify multiple separate modules, with a separate amplification factor for each module.

However, perhaps inspired by their previous work on GxSex interactions in humans, the authors’ focus in the present manuscript is on cases where there are only two environments (“control” and “high-sugar diet” in the Drosophila dataset that they reanalyze, and “A” and “B” in their simulations [and single-locus mathematical analysis]), and they consider models where these environments amplify only a single set of genes, i.e., with a single amplification factor. While it is of course interesting that a single-amplification-factor model can generate data that resemble those in the Drosophila dataset that the authors re-analyze, most scenarios of amplification GxE will presumably be more complex. It seems that detecting amplification in these more complex scenarios using methods such as the authors do in their final section will be correspondingly more difficult. Indeed, in the limit of sufficiently many environmental variables amplifying sufficiently many modules, the scenario would resemble one of idiosyncratic single-locus GxE which, as the authors argue, is very difficult to detect. That more complex scenarios of amplification, with multiple environments separately amplifying multiple modules each, might be difficult to detect statistically is potentially an important limitation to the authors’ approach, and should be tested in their simulations.

We agree that characterizing GxE when there is a mixture of drivers of context-dependency is difficult. Developing a method that does so across multiple (and perhaps not pre-defined) contexts is of high interest to us but beyond the scope of the current manuscript

We note that for GxSex, modeling this mixture does generally improve phenotypic prediction, and more so in traits where we infer amplification as a major mode of GxE.

MINOR COMMENTS

Lines 88-90: “This estimation model is equivalent to a linear model with a term for the interaction between context and reference allele count, in the sense that context-specific allelic effect estimators have the same distributions in the two models.”

Does this equivalence require the model with the interaction term also to have an interaction term for the intercept, i.e., the slope on a binary variable for context (since the generative model in Eq. 1 allows for context-specific intercepts)?

It does require an interaction term for the intercept. This is e_i (and its effect beta_E) in Eq. S2 (line 70 of the supplement).

Lines 94-96: Perhaps just a language thing, but in what sense does the estimation model described in lines 92-94 “assume” a particular distribution of trait values in the combined sample? It’s just an OLS regression, and one can analyze its expected coefficients with reference to the generative model in Eq. 1, or any other model. To say that it “assumes” something presupposes its purpose, which is not clear from its description in lines 92-94.

We corrected “assume” to “posit”.

Lines 115-116: It should perhaps be noted that the weights wA and wB need not sum to 1.

Indeed; it is now explicitly stated.

Lines 154-160: I think the role of r could be made even clearer by also discussing why, when VA>>VB, it is better to use the whole-sample estimate of betaA than the sample-A-specific estimate (since this is a more counterintuitive case than the case of VA<<VB discussed by the authors).

This is addressed in lines 153-154, stating: “Typically, this (VA<<VB) will also imply that the additive estimator is greatly preferable for estimating β_B , as β_B will be extremely noisy”

Line 243 and Figure 4 caption: The text states that the simulated effects in the high-sugar environment are 1.1x greater than those in the control environment, while the caption states that they are 1.4x greater.

We have corrected the text to be consistent with our simulations.

TYPOS/WORDING

Line 14: “harder to interpret” --> “harder-to-interpret”

Line 22: We --> we

Line 40: “as average effect” -> “as the average effect”?

Line 57: “context specific” --> “context-specific”

Line 139: “re-parmaterization” --> “re-parameterization”

Lines 140, 158, 412: “signal to noise” --> “signal-to-noise”

Figure 3C,D: “pule rate” --> “pulse rate”

The caption of Figure 3: “conutinous” --> “continuous”

Line 227: “a variant may fall” --> “a variant may fall into”

Line 295: “conferring to more GxE” --> “conferring more GxE” or “corresponding to more GxE”? This is very pedantic, but I think “bias-variance” should be “bias--variance” throughout, i.e., with an en-dash rather than a hyphen.

We have corrected all of the above typos.

Reviewer #2 (Recommendations For The Authors):

(This section repeats some of what I wrote earlier).

- First polygenic architecture part: the manuscript focuses on “top hits” in trying to identify sets of variants that are context-specific. This “top hits” approach seems somewhat esoteric and, as written, not connected tightly enough to the bias-variance tradeoff issue. The first section of the paper which focuses on bias-variance trade-off mostly deals with estimation. The “top hits” section deals with testing, which introduces additional issues that are due to thresholding. Perhaps the authors can think of ways to make the connection stronger between the bias-variance tradeoff part to the “top hits” part, e.g., by introducing testing earlier on and/or discussion estimation in addition to testing in the “top hits” part of the manuscript. The second polygenic architecture part: polygenic scores that account for interaction terms. Here the authors focused (well, also here) on pervasive amplification in simulations. This part combines estimation and testing (both the choice of variants and their estimated effects are important). In pervasive amplification the idea is that causal variants are shared, the results may be different than in a model with context-specific effects and variant selection may have a large impact. Still, I think that these simulations demonstrate the idea developed in the bias-variance tradeoff part of the paper, though the reader is left to wonder whether a bias-variance decision rule should or could be utilized for PGS construction.

In both of these sections we discuss how the consideration of polygenic GxE patterns alters the conclusions based on the single-variant tradeoff. In the “top hits” section, we show that single-variant classification itself, based on a series of marginal hypothesis tests alone, can be misleading. The PGS prediction accuracy analysis shows that both approaches are beaten by the polygenic GxE estimation approach. Intuitively, this is because the consideration of polygenic GxE can mitigate both the bias and variance, as it leverages signals from many variants.

We agree that the links between these sections of the paper were not sufficiently clear, and have added signposting to help clarify them (lines 176-180; lines 275-277; lines 316-321).

- Simulation of GxDiet effects on longevity: the methods of the simulation are strange, or communicated unclearly. The authors’ report (page 17) poses a joint distribution of genetic effects (line 439), but then, they simulated effect estimates standard errors by sampling from summary statistics (line 445) rather than simulated data and then estimating effect and effect SE. Why pose a true underlying multivariate distribution if it isn’t used?

We rewrote the Methods section “Simulation of GxDiet effects on longevity in Drosophila to make our simulation approach clearer (lines 427-449). We are indeed simulating the true effects from the joint distribution proposed. However, in order to mimic the noisiness of the experiment in our simulations, we sample estimated effects from the true simulated effects, with estimation noise conferring to that estimated in the Pallares et al. dataset (i.e., sampling estimation variances from the squares of empirical SEs).

- How were the “most significantly associated variants” selected into the PGS in the polygenic prediction part? Based on a context-specific test? A combined-context test of effect size estimates?

For the “Additive” and “Additive ascertainment, GxE estimation” models (red and orange in Fig. 5, respectively), we ascertain the combined-context set. For the “GxE” and “polygenic GxE” (green and blue in Fig. 5, respectively) models, we ascertain in a context-specific test. We now state this explicitly in lines 280-288 and lines 507-526.

- As stated, I find the conclusion statement not specific enough in light of the rest of the manuscript. “the consideration of polygenic GxE trends is key” - this is very vague. What does it mean “to consider polygenic GxE trends” in the context of this paper? I can’t tell. “The notion that complex trait analyses should combine observations at top associated loci” - I don’t think the authors really refer to combining “observations”, rather perhaps combine information from top associated loci. But this does not represent the “top hits” approach that merely counts loci by their testing patterns. “It may be a similarly important missing piece...” What does “it” refer to? The top loci? What makes it an important missing piece?

We rewrote the conclusion paragraph to address these concerns (lines 316-321).

eLife Assessment

This important study reports numerous attempts to replicate reports on transgenerational inheritance of a learned behavior – pathogen avoidance – in C. elegans. While the authors observe parental effects that are limited to a single generation (also called intergenerational inheritance), the authors failed to find evidence for transmission over multiple generations, or transgenerational inheritance. The experiments presented are meticulously described, making for compelling evidence that in the authors' hands transgenerational inheritance cannot be observed. There remains the possibility that different assay setups explain the failure to reproduce previous observations, although the authors present data suggesting that details of the assay are not that significant. There also remains the possibility that differences in culture conditions or lab environment explain the failure to reproduce previous observations, with updates to the paper having further reduced the probability that this applies here. Even if this were the case, it would imply that the original experimental paradigm was dependent on a very specific context. Given the prominence of the original reports of transgenerational inheritance, the present study is of broad interest to anyone studying genetics, epigenetics, or learned behavior.

[As also pointed out by the authors of this study, the authors of the original reports have provided a response on bioRxiv (DOI: https://doi.org/10.1101/2025.01.21.634111).]

Reviewer #1 (Public review):

Summary:

The authors report an inability to reproduce a transgenerational memory of avoidance of the pathogen PA14 in C. elegans. Instead, the authors demonstrate intergenerational inheritance for a single F1 generation, in embryos of mothers exposed to OP50 and PA14, where embryos isolated from these mothers by bleaching are capable of remembering to avoid PA14 in a manner that is dependent on systemic RNAi proteins sid-1 and sid-2. This could reflect systemic sRNAs generated by neuronal daf-7 signaling that are transmitted to F1 embryos. The authors note that transgenerational memory of PA14 was reported by the Murphy group at Princeton, but that environmental or strain variation (worms or bacteria) might explain the single generation of inheritance observed at Harvard. The Hunter group tried different bacterial growth conditions and different worm growth temperatures for independent PA14 strains, which they show to be strongly pathogenic. However, the authors could not reproduce a transgenerational effect at Harvard. This paper honestly alters expectations and indicates that the model that avoidance of PA14 is remembered for multiple generations is not robust enough to be replicated in all laboratories.

Overall, this paper that demonstrates that one model for transgenerational inheritance in C. elegans is not robust. The author do demonstrate an avoidance memory for F1 embryos that could be a maternal effect, and the authors confirm that this is mediated by a systemic small RNA response. There are several points in the manuscript where a more positive tone might be helpful.

Strengths:

The authors note that the high copy number daf-7::GFP transgene used by the Murphy group displayed variable expression and evidence for somatic silencing or transgene breakdown in the Hunter lab, as confirmed by the Murphy group. The authors nicely use single copy daf-7::GFP to show that neuronal daf-7::GFP is elevated in F1 but not F2 progeny with regards to memory of PA14 avoidance, speaking to an intergenerational phenotype.

The authors nicely confirm that sid-1 and sid-2 are generally required for intergenerational avoidance of F1 embryos of moms exposed to PA14. However, these small RNA proteins did not affect daf-7::GFP elevation in the F1 progeny. This result is unexpected given previous reports that daf-7::GFP is not elevated in F1 progeny of sid mutants.

The authors studied antisense small RNAs that change in Murphy data sets, identifying 116 mRNAs that might be regulated by sRNAs in response to PA14. The authors show that the maco-1 gene, putatively targeted by piRNAs according to the Kaletsky 2020 paper, displays few siRNAs that change in response to PA14. The authors conclude that the P11 ncRNA of PA14, which was proposed to promote interkingdom RNA communication by the Murphy group, may not affect maco-1 expression in C. elegans, although they did not formally demonstrate this. The authors define 8 genes based on their analysis of sRNAs and mRNAs that might promote resistance to PA14, but they do not further characterize these genes' role in pathogen avoidance. Others might wish to consider following up on these genes and their possible relationship with P11.

Weaknesses:

This very thorough and interesting manuscript is at times pugnacious.

Please explain more clearly what is High Growth media for E. coli in the text and methods, conveying why it was used by the Murphy lab, and if Normal Growth or High Growth is better for intergenerational heritability assays.

Comments on revisions:

The authors have done a reasonable job cordially revising this manuscript, and the authors have addressed most reviewer concerns. It is likely that the P11 gene was in some of the PA14 Pseudomonas strains tested, as one was kindly provided by the Murphy group.

Reviewer #2 (Public review):

This paper examines the reproducibility of results reported by the Murphy lab regarding transgenerational inheritance of a learned avoidance behavior in C. elegans. It has been well established by multiple labs that worms can learn to avoid the pathogen pseudomonas aeruginosa (PA14) after a single exposure. The Murphy lab has reported that learned avoidance is transmittable to 4 generations and dependent on a small RNA expressed by PA14 that elicits the transgenerational silencing of a gene in C. elegans. The Hunter lab now reports that although they can reproduce inheritance of the learned behavior by the first generation (F1), they cannot reproduce inheritance in subsequent generations.

This is an important study that will be useful for the community. Although they fail to identify a "smoking gun", the study examine several possible sources for the discrepancy, and their findings will be useful to others interested in using these assays. The preference assay appears to work in their hands in as much as they are able to detect the learned behavior in the P0 and F1 generations, suggesting that the failure to reproduce the transgenerational effect is not due to trivial mistakes in the protocol. The authors provide a full protocol and highlight key deviations from the Murphy lab protocol. The authors provide good evidence that no single protocol modification was sufficient on its own to explain the divergent results. It remains possible that protocol differences affected the assay cumulatively or that other uncontrolled factors were responsible. Nevertheless, the authors provide good evidence that the trans-generational effect reported by the Murphy lab lacks experimental robustness, calling into question its ecological relevance in the wild.

Reviewer #3 (Public review):

Summary:

It has been previously reported in many high-profile papers, that C. elegans can learn to avoid pathogens. Moreover, this learned pathogen avoidance can be passed on to future generations - up to the F5 generation in some reports. In this paper, Gainey et al. set out to replicate these findings. They successfully replicated pathogen avoidance in the exposed animals, as well as a strong increase in daf-7 expression in ASI neurons in F1 animals, as determined by a daf-7::GFP reporter construct. However, they failed to see strong evidence for pathogen avoidance or daf-7 overexpression in the F2 generation. The failure of replication is the major focus of this work.<br /> Given their failure to replicate these findings, the authors embark on a thorough test of various experimental confounders that may have impacted their results. They also re-analyze the small RNA sequencing and mRNA sequencing data from one of the previously published papers and draw some new conclusions, extending this analysis.

Strengths:

• The authors provide a thorough description of their methods, and a marked-up version of a published protocol that describes how they adapted the protocol to their lab conditions. It should be easy to replicate the experiments.

• The authors test source of bacteria, growth temperature (of both C. elegans and bacteria), and light/dark husbandry conditions. They also supply all their raw data, so that sample size for each testing plate can be easily seen (in the supplementary data). None of these variations appears to have a measurable effect on pathogen avoidance in the F2 generation, with all but one of the experiments failing to exhibit learned pathogen avoidance.

• The small RNA seq and mRNA seq analysis is well performed and extends the results shown in the original paper. The original paper did not give many details of the small RNA analysis, which was an oversight. Although not a major focus of this paper, it is a worthwhile extension on the previous work.

• It is rare that negative results such as these are accessible. Although the authors were unable to determine the reason that their results differ from those previously published, it is important to document these attempts in detail, as has been done here. Behavioral assays are notoriously difficult to perform and public discourse around these attempts may give clarity to the difficulties faced by a controversial field.

Weaknesses:

• Although the "standard" conditions have been tested over multiple biological replicates, many of the potential confounders that may have altered the results have been tested only once or twice. For example, changing the incubation temperature to 25{degree sign}C was tested in only two biological replicates (Exp 5.1 and 5.2) - and one of these experiments actually resulted in apparent pathogen avoidance inheritance in the F2 generation (but not in the F1). An alternative pathogen source was tested in only one biological replicate (Exp 3). Given the variability observed in the F2 generation, increasing biological replicates would have added to the strengths of the report.

• A key difference between the methods used here and those published previously, is an increase in the age of the animals used for training - from mostly L4 to mostly young adults. I was unable to find a clear example of an experiment when these two conditions were compared, although the authors state that it made no difference to their results.

• The original paper reports a transgenerational avoidance effect up to the F5 generation. Although in this work the authors failed to see avoidance in the F2 generation, it would have been prudent to extend their tests for more generations in at least a couple of their experiments to ensure that the F2 generation was not an aberration (although this reviewer acknowledges that this seems unlikely to be the case).

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

[…] Overall, this is an important paper that demonstrates that one model for transgenerational inheritance in C. elegans is not reproducible. This is important because it is not clear how many of the reported models of transgenerational inheritance reported in C. elegans are reproducible. The authors do demonstrate a memory for F1 embryos that could be a maternal effect, and the authors confirm that this is mediated by a systemic small RNA response. There are several points in the manuscript where a more positive tone might be helpful.

We would like to correct the statement made in the second to last sentence. The demonstration of an F1 response to PA14 was first reported by Moore et al., (2019) and then by Pereira et al., (2020) using a different behavioral assay. We merely confirmed these results in our hands, and confirmed the observation, first reported by Kaletsky et al., (2020), that sid-1 and sid-2 are required for this F1 response; although we did find that sid-1 and sid-2 are not required for the PA14-induced increase in daf-7p::gfp expression in ASI neurons in the F1 progeny of trained adults, which had not been addressed in the published work.

Yes, the intergenerational F1 response could be a maternal effect, but the in utero F1 embryos and their precursor germ cells were directly exposed to PA14 metabolites and toxins (non-maternal effect) as well as any parental response, whether mediated by small RNAs, prions, hormones, or other unknown information carriers. While the F1 aversion response does require sid-1 and sid-2, we would not presume that the substrate is therefore an RNA molecule, particularly because the systemic RNAi response supported by sid-1 and sid-2 is via long double-stranded RNA. To date, no evidence suggests that either protein transports small RNAs, particularly single-stranded RNAs.

Strengths:

The authors note that the high copy number daf-7::GFP transgene used by the Murphy group displayed variable expression and evidence for somatic silencing or transgene breakdown in the Hunter lab, as confirmed by the Murphy group. The authors nicely use single copy daf-7::GFP to show that neuronal daf-7::GFP is elevated in F1 but not F2 progeny with regards to the memory of PA14 avoidance, speaking to an intergenerational phenotype.

The authors nicely confirm that sid-1 and sid-2 are generally required for intergenerational avoidance of F1 embryos of moms exposed to PA14. However, these small RNA proteins did not affect daf-7::GFP elevation in the F1 progeny. This result is unexpected given previous reports that single copy daf-7::GFP is not elevated in F1 progeny of sid mutants. Because the Murphy group reported that daf-7 mutation abolishes avoidance for F1 progeny, this means that the sid genes function downstream of daf-7 or in parallel, rather than upstream as previously suggested.

The published report (Moore et al., 2019) shows only multicopy daf-7p::gfp results and does not address the daf-7p::gfp response in sid-1 or sid-2 mutants. Thus, our discovery that systemic RNAi, exogenous RNAi, and heritable RNAi mutants don’t disrupt elevated daf-7p::gfp in ASI neurons in the F1 progeny of PA14 trained P0’s is only unexpected with respect to the published models (Moore et al., 2019, Kaletsky et al., 2020).

The authors studied antisense small RNAs that change in Murphy data sets, identifying 116 mRNAs that might be regulated by sRNAs in response to PA14. Importantly, the authors show that the maco-1 gene, putatively targeted by piRNAs according to the Kaletsky 2020 paper, displays few siRNAs that change in response to PA14. The authors conclude that the P11 ncRNA of PA14, which was proposed to promote interkingdom RNA communication by the Murphy group, is unlikely to affect maco-1 expression by generating sRNAs that target maco-1 in C. elegans. The authors define 8 genes based on their analysis of sRNAs and mRNAs that might promote resistance to PA14, but they do not further characterize these genes' role in pathogen avoidance. The Murphy group might wish to consider following up on these genes and their possible relationship with P11.

Weaknesses:

This very thorough and interesting manuscript is at times pugnacious.

We reiterate that we never claimed that Moore et al., (2019) did not obtain their reported results. We simply stated that we could not replicate their results using the published methods and then failed in our search to identify variable(s) that might account for our results. In revising the manuscript, we have striven to make clear, unmuddied statements of facts and state that future investigations may provide independent evidence that supports the original claims and explains our divergent results.

Please explain more clearly what is High Growth media for E. coli in the text and methods, conveying why it was used by the Murphy lab, and if Normal Growth or High Growth is better for intergenerational heritability assays.

We added the standard recipes and the following explanations in the methods section to the revised text.

“NG plates minimally support OP50 growth, resulting in a thin lawn that facilitates visualization of larvae and embryos. HG plates (8X more peptone) support much higher OP50 growth, resulting in a thick bacterial lawn that supports larger worm populations.”

We have also included the following text in our presentation and discussion of the effects of growth conditions on worm choice in PA14 vs OP50 choice assays.

“Furthermore, because OP50 pathogenicity is enhanced by increased E. coli nutritive conditions (Garsin et al., 2003, Shi et al., 2006), the growth of F1-F4 progeny on High Growth (HG) plates (Moore et al., 2019; 2021b), which contain 8X more peptone than NG plates and therefore support much higher OP50 growth levels, immediately prior to the F1-F4 choice assays may further contribute to OP50 aversion among the control animals.”

We don’t know enough to claim that HG or NG media is better than the other for intergenerational assays, but they are different. Thus, switching between the two in a multigenerational experiment likely introduces unknown variability.

Reviewer #2 (Public Review):

This paper examines the reproducibility of results reported by the Murphy lab regarding transgenerational inheritance of a learned avoidance behavior in C. elegans. It has been well established by multiple labs that worms can learn to avoid the pathogen pseudomonas aeruginosa (PA14) after a single exposure. The Murphy lab has reported that learned avoidance is transmittable to 4 generations and dependent on a small RNA expressed by PA14 that elicits the transgenerational silencing of a gene in C. elegans. The Hunter lab now reports that although they can reproduce inheritance of the learned behavior by the first generation (F1), they cannot reproduce inheritance in subsequent generations.

This is an important study that will be useful for the community. Although they fail to identify a "smoking gun", the study examines several possible sources for the discrepancy, and their findings will be useful to others interested in using these assays. The preference assay appears to work in their hands in as much as they are able to detect the learned behavior in the P0 and F1 generations, suggesting that the failure to reproduce the transgenerational effect is not due to trivial mistakes in the protocol. An obvious reason, however, to account for the differing results is that the culture conditions used by the authors are not permissive for the expression of the small RNA by PA14 that the MUrphy lab identified as required for transgenerational inheritance. It would seem prudent for the authors to determine whether this small RNA is present in their cultures, or at least acknowledge this possibility.

We thank the reviewer for raising this issue and have added the following statement to this effect in the revised manuscript.

“We note that previous bacterial RNA sequence analysis identified a small non-coding RNA called P11 whose expression correlates with bacterial growth conditions that induce heritable avoidance (Kaletsky et al., 2020). Critically, C. elegans trained on a PA14 ΔP11 strain (which lacks this small RNA) still learn to avoid PA14, but their F1 and F2-F4 progeny fail to show an intergenerational or transgenerational response (Figure 3L in Kaletsky et al., 2020). The fact that we observed an intergenerational (F1) avoidance response is evidence that our PA14 growth conditions induce P11 expression.”

We believe that this addresses the concern raised here.

The authors should also note that their protocol was significantly different from the Murphy protocol (see comments below) and therefore it remains possible that protocol differences cumulatively account for the different results.

As suggested below, we have added to the supplemental documents the protocol we followed for the aversion assay. In our view, this document shows that our adjustments to the core protocol were minor. Furthermore, where possible, these adjustments were explicitly tested in side-by-side experiments for both the aversion assay and the daf-7p::gfp expression assay and presented in the manuscript.

To discover the source(s) of discrepancy between our results and the published results we subsequently introduced variations to this core protocol to exclude likely variables (worm and bacteria growth temperatures, assay conditions, worm handling methods, bacterial culture and storage conditions, and some minor developmental timing issues). Again, where possible, the effect of variations was tested in side-by-side experiments for both the aversion assay and the daf-7p::gfp expression assay and were presented in or have now been added to the manuscript.

It remains possible that we misunderstood the published Murphy lab protocols, but we were highly motivated to replicate the results so we could use these assays to investigate the reported RNAi-pathway dependent steps, thus we read every published version with extreme care.

Reviewer #3 (Public Review):

[…] Strengths:

(1) The authors provide a thorough description of their methods, and a marked-up version of a published protocol that describes how they adapted the protocol to their lab conditions. It should be easy to replicate the experiments.

As noted above in response to a suggestion by reviewer #2, we have replaced the annotated published protocol with the protocol that we followed. This will aid other groups' attempts to replicate our experimental conditions.

(2) The authors test the source of bacteria, growth temperature (of both C. elegans and bacteria), and light/dark husbandry conditions. They also supply all their raw data, so that the sample size for each testing plate can be easily seen (in the supplementary data). None of these variations appears to have a measurable effect on pathogen avoidance in the F2 generation, with all but one of the experiments failing to exhibit learned pathogen avoidance.

We note that the parallel analysis of daf-7p::gfp expression in ASI neurons was also tested for several of these conditions and also failed to replicate the published findings.

(3) The small RNA seq and mRNA seq analysis is well performed and extends the results shown in the original paper. The original paper did not give many details of the small RNA analysis, which was an oversight. Although not a major focus of this paper, it is a worthwhile extension of the previous work.

(4) It is rare that negative results such as these are accessible. Although the authors were unable to determine the reason that their results differ from those previously published, it is important to document these attempts in detail, as has been done here. Behavioral assays are notoriously difficult to perform and public discourse around these attempts may give clarity to the difficulties faced by a controversial field.

Thank you for your support. Choosing to pursue publication of these negative results was not an easy decision, and we thank members of the community for their support and encouragement.

Weaknesses:

(1) Although the "standard" conditions have been tested over multiple biological replicates, many of the potential confounders that may have altered the results have been tested only once or twice. For example, changing the incubation temperature to 25{degree sign}C was tested in only two biological replicates (Exp 5.1 and 5.2) - and one of these experiments actually resulted in apparent pathogen avoidance inheritance in the F2 generation (but not in the F1). An alternative pathogen source was tested in only one biological replicate (Exp 3). Given the variability observed in the F2 generation, increasing biological replicates would have added to the strengths of the report.

We agree that our study was not exhaustive in our exploration of variables that might be interfering with our ability to detect F2 avoidance. We also note that some of these variables also failed (with many more independent experiments) to induce elevated daf-7p::gfp expression in ASI neurons in F2 progeny. Our goal was not to show that variation in some growth or assay condition would generate reproducible negative results, but the exploration was designed to tweak conditions to enable detection of a robust F2 response. Given the strength of the data presented in Moore et al., (2019) we expected that adjustment of the problematic variable would produce positive results apparent in a single replicate, which could then be followed up. If we had succeeded, then we would have documented the conditions that enabled robust F2 inheritance and would have explored molecular mechanisms that support this important but mysterious process.

(2) A key difference between the methods used here and those published previously, is an increase in the age of the animals used for training - from mostly L4 to mostly young adults. I was unable to find a clear example of an experiment when these two conditions were compared, although the authors state that it made no difference to their results.

We can state firmly that the apparent time delay did not affect P0 learned avoidance (new Figure S1) or, as documented in Table S1, daf-7p::gfp expression in ASI neurons. In our experience, training mostly L4’s on PA14 frequently failed to produce sufficient F1 embryos for both F1 avoidance assays or daf-7p::gfp measurements in ASI neurons and collection of F2 progeny. Indeed, in early attempts to detect heritable PA14 aversion, trained P0 and F1 progeny were not assayed in order to obtain sufficient F2’s for a choice assay. These animals failed to display aversion, but without evidence of successful P0 training or an F1 intergenerational response this was deemed a non-fruitful trouble-shooting approach. We have added supplemental Figure S1 which presents P0 choice assay results from experiments using younger trained animals that failed to produce sufficient F1’s to continue the inheritance experiments.

The different timing at the start of training between the two protocols may reflect the age of the recovered bleached P0 embryos. It is reasonable to assume that bleaching day 1 adults vs day 2 or 3 adults from the P-1 population could shift the average age of recovered P0 embryos by several hours. The Murphy protocol only states that P0 embryos were obtained by bleaching healthy adults. Regardless, if the hypothesis entertained here is true, that a several hour difference in larval/adult age during 24 hours of training affects F2 inheritance of learned aversion but does not affect P0 learned avoidance, then we would argue that this paradigm for heritable learned avoidance, as described in Moore et al., (2019, 2021), is not sufficiently robust for mechanistic investigations.

(3) The original paper reports a transgenerational avoidance effect up to the F5 generation. Although in this work the authors failed to see avoidance in the F2 generation, it would have been prudent to extend their tests for more generations in at least a couple of their experiments to ensure that the F2 generation was not an aberration (although this reviewer acknowledges that this seems unlikely to be the case).

We would point out that we also failed to robustly replicate the F2 response in the daf-7p::gfp expression assays. An F2-specific aberration that affects two different assays seems quite unlikely, and it remains unclear how we would interpret a positive result in F3 and F4 generations without a positive result in the F2 generation. Were we to further extend these investigations, we believe that exploration of additional culture conditions would warrant higher priority than extension of our results to the F3 and F4 generations.

Reviewing Editor Comments:

The reviewers' suggestions for improving the manuscript were mostly minor, to change the wording in some places and to add some more explanation regarding the methods.

What should be highlighted in the section on OP50 growth conditions is that the initial preference for PA14 in the Murphy lab has also been observed by multiple other labs (Bargmann, Kim, Zhang, Abbalay). The fact that this preference was not observed by the Hunter lab is one of several indicators of subtle differences in the environment that might add up to explain the differences in results.

We agree that subtle known and unknown differences in OP50 and PA14 culture conditions can have measurable effects on the detection of PA14 attraction/aversion relative to OP50 attraction/aversion that could obscure or create the appearance of heritable effects between generations. We have added (see below) to the text a fuller description of the variability in the initial or naive preference observed in different laboratories using similar or variant 2-choice assays and culture conditions. It is worth emphasizing that direct comparison of the OP50 growth conditions specified in Moore et al., (2021) frequently revealed a much larger effect on the naïve choice index than is reported between labs (Figure 4).  

“Naïve (OP50 grown) worms often show a bias towards PA14 in choice assays (Zhang et al., 2005; Ha et al., 2010; Moore et al., 2019; Pereira et al., 2020; Lalsiamthara and Aballay, 2022). This response, rather than representing an innate attraction to PA14, likely reflects the context of the worm's recent growth on OP50, a mild C. elegans pathogen (Garigan et al., 2002; Garsin et al., 2003; Shi et al., 2006). Thus, the naïve worms presented with a choice between a recently experienced mild pathogen (OP50) and a novel food choice (PA14) initially choose the novel food instead of the known mild pathogen (OP50 aversion).

In line with our results, some other groups have also reported higher naïve choice index scores (Lee et al., 2017). This variability in naïve choice may reflect differences in growth conditions of either the OP50 or PA14 bacteria. In addition, we note that among the studies that show naïve worm attraction to Pseudomonas (OP50 aversion) there are extensive methodological differences from the methods in Moore et al., (2019; 2021b), including differences in bacterial growth temperature, incubation time, whether the bacteria is diluted or concentrated prior to placement on the choice plates, the concentration of peptone in the choice plates, the length of the choice assay, and the inclusion of sodium azide in the choice assays (Zhang et al., 2005; Ha et al., 2010; Moore et al., 2019; Pereira et al 2020; Lalsiamthara and Aballay, 2022). Thus, the cause of the variability across published reports is not clear.”

Overall, an emphasis on the absence of robustness of the reported results, rather than failure to reproduce them (which can always have many reasons), is appropriate.

We agree that an emphasis on robustness is appropriate and have modified the text throughout the manuscript to shift the emphasis to absence of robustness. This includes a change to the manuscript title, which is now, “Reported transgenerational responses to Pseudomonas aeruginosa in C. elegans are not robust”

A significant experimental addition would be some attempts to determine whether the bacterial PA14 pathogen in the authors' lab produces the P11 small RNA, which has been proposed to have a causal role in initiating the previously reported transgenerational inheritance.

We acknowledge in the revised manuscript that a subsequent publication (Kaletsky et al., 2020) identified a correlation between PA14 training conditions that induced transgenerational memory and the expression of P11, a P. aeruginosa small non-coding RNA (see our response above to Reviewer #2’s similar query). While testing for the presence of P11 in Harvard culture conditions would be an important assay in any study whose purpose was to investigate the proposed P11-mediated mechanism underlying the transgenerational responses reported by the Murphy Lab, our goal was rather to replicate the robust transgenerational (F2) responses to PA14 training and then to investigate in more detail how sid-1 and sid-2 contribute to transgenerational epigenetic inheritance. Neither sid-1 nor sid-2 are predicted to transport small RNAs or single-stranded RNAs, thus testing for the presence of P11 is less relevant to our goals. Regardless, we note that Figure 3L in Kaletsky et al., (2020) showed that PA14 ΔP11 bacteria failed to induce an F1 avoidance response. Thus, the fact that we observed F1 avoidance implies that our culture conditions successfully induced P11 expression.

Reviewer #1 (Recommendations For The Authors):

The abstract could be more positive by concluding that 'We conclude that this example of transgenerational inheritance lacks robustness but instead reflects an example of small RNA-mediated intergenerational inheritance.'

As recommended, we have added additional clarifying information to the abstract and moderated the conclusion sentence.

“We did confirm that the dsRNA transport proteins SID-1 and SID-2 are required for the intergenerational (F1) inheritance of pathogen avoidance, but not for the F1 inheritance of elevated daf-7 expression. Furthermore, our reanalysis of RNA seq data provides additional evidence that this intergenerational inherited PA14 response may be mediated by small RNAs.”

“We conclude that this example of transgenerational inheritance lacks robustness, confirm that the intergenerational avoidance response, but not the elevated daf-7p::gfp expression in F1 progeny, requires sid-1 and sid-2, and identify candidate siRNAs and target genes that may mediate this intergenerational response.”

Differential expression of sRNAs or mRNAs might be better understood quantitatively by presenting data in scatterplots (Reed and Montgomery 2020) rather than in volcano plots.

We agree and have modified Figure 6A and 6B.

This statement in the main text might be unnecessary, as it affects the tenor of the conclusion of this significant manuscript. 'We note that none of the raw data for the published figures and unpublished replicate experiments . . . this hampered our ability to fully compare'.

We have rewritten this paragraph to focus on our goal: to identify the source of the discrepancy between our results and the published results. We considered discarding this statement but ultimately decided that our inability to directly compare our data to that of previously published work is a shortcoming of our study that deserves to be acknowledged and explained.

“Ideally, we would have compared our results with the published results (Moore et al., 2019), to possibly identify additional experimental parameters for further investigation; for example, a quantitative comparison of naïve choice in the P0 and F1 generations could help to determine the role of bacterial growth in the choice assay response. However, none of the raw data for the published figures and unpublished replicate experiments (Moore et al., 2019) were available on the publisher’s website or provided upon request to the corresponding author. In the absence of a quantitative comparison, it remains possible that an explanation for the discrepancies between our results and those of Moore et al., (2019) has been overlooked.”

The final sentence of the Discussion could be tempered and more positive by stating 'Thus independent reproducibility is of paramount concern, and we have tried to be completely transparent as a model for how heritability research should be conducted within the C. elegans community'.

Thank you. The suggested sentence nicely captures our intention. We now use it, almost verbatim, as our final sentence.

“Thus, independent reproducibility is of paramount concern, and we have tried to be completely transparent as a model for how heritability research should be presented within the C. elegans community.”

Reviewer #2 (Recommendations For The Authors):

Specific comments:

(1) Protocol: It is difficult to assess from the Methods the exact protocol used by the authors to assay food preference. The annotated Murphy protocol is not sufficient. The authors should provide their own protocol - a detailed lab-ready protocol where every step is outlined, and any steps that deviate from the Murphy lab protocol are called out.

Thank you for this excellent suggestion. We now include a protocol that documents the precise steps, timings, and controls that we followed (S1_aversion_protocol). We also include footnotes to both explain the reasons behind particular steps and to document known differences to the published protocol. Given the thoroughness of this suggested approach, we have thus removed the annotated version of Moore et al., (2021) from the revised submission.

(2) The authors imply in the methods that, unlike the Murphy lab, they did NOT use azide in the assay, and instead used 4oC to "freeze" the worms in place - It is not clear whether this method was used throughout all their assays and whether this could be a source of the difference. This change is NOT indicated in the annotated Murphy lab STAR Protocol they provide in the supplement.

We apologize for the lack of clarity. Concerned that azide may be interfering with our ability to detect heritable silencing we tested and then used cold-induced rigor to preserve worm choice in some choice assay results. This was not a change to the core protocol, but a variation used in some assays to determine whether azide could reduce our ability to detect heritable behavioral responses to PA14 exposure. As Moore et al., (2021) show, too much azide can affect measurement of worm choice. Too little or ineffective azide also can affect measurement of worm choice. Azide also affects bacteria (both OP50 and PA14), which could affect the production of molecules that attract or repel worms, much like performing the assay in light vs dark conditions can influence the measured choice index.

In our hands, cold-induced rigor worked well and within biological replicates was indistinguishable from azide (Figure S10). Thus, we include those results in our analysis and now indicate in Tables 2 and S2 and in Figures 1 and 3 which experiments used which method. As suggested, we now provide a detailed protocol that includes a note describing our precise method for cold-induced rigor.

Also, the number of worms used in each assay needs to be specified (same or different from Murphy protocol?), and whether any worms were "censored" as in the Murphy protocol, and if so on what basis.

While we published the exact number of worms scored in each assay (on each plate) it is unknown how this might compare to the results published in Moore et al., (2019), as the number of animals in the presented choice assays (either per plate or per choice) were not reported. Details on censoring, when to exclude data, and additional criteria to abandon an in-progress experiment are now detailed in the protocol (S1_aversion_protocol)

(3) Several instances in the text cite changes in the protocol as producing "no meaningful differences" without referring to a specific experiment that supports that statement (for example, line 399 regarding azide).

We now include data and methods comparing azide and cold-induced rigor (Supplemental document S1_aversion_protocol, Supplemental Figure S10), and data showing the P0 choice index for 48-52 hour post-bleach L4/young adults (Supplemental Figure S1), in addition to the previously noted absence of effects due to differences in embryo bleaching protocols (Figures 2, 3 and Tables 1, 2, S1, and S2).

(4) If the authors want to claim the irreproducibility of the Murphy lab results, they should use the exact protocol used by the Murphy lab in its entirety. It is not sufficient to show that individual changes do not affect the outcome, since the protocol they use appears to include SEVERAL changes which could cumulatively affect the results. If the authors do not want to do this, they should at least acknowledge and summarize in their discussion ALL their protocol changes.

We acknowledge these minor differences between the protocols we followed and the published methods but disagree that they invalidate our results. We transparently present the effect of known minimal protocol changes. We also present analysis of possible invalidating variations (number of animals in a choice assay). We emphasize that in our hands both measures of TEI, the choice assay and measurement of daf-7p::gfp in ASI neurons, failed to replicate the published transgenerational results.

If the protocol is sensitive to how animals are counted, whether bleached embryos are mixed gently or vigorously or a few hours difference in age at training, then in our view this TEI paradigm is not robust.

See also our response to reviewer #3’s public reviews above.

(5) The authors acknowledge that "non-obvious growth culture differences" could account for the different results. In this respect, the Murphy lab has proposed that the transgenerational effect requires a small RNA expressed in PA14. The authors should check that this RNA is expressed in the cultures they grow in their lab and use for their experiments. This could potentially identify where the two protocols diverge.

The bacterial culture conditions and worm training procedures described in Moore et al., (2019) successfully produced trained P0 animals that transmitted a PA14 aversion response to their F1 progeny. In a subsequent publication (Kaletsky et al., 2020), the Murphy lab showed a correlation between the culture conditions that induce heritable avoidance and the expression of P11, a P. aeruginosa small non-coding RNA. As mentioned above in response to Reviewer #2’s public review and the Reviewing Editor’s comments to authors, the Murphy lab showed that PA14 ΔP11 bacteria fail to induce an F1 avoidance response (Figure 3L in Kaletsky et al., (2020)). Thus, the fact that we observed F1 avoidance implies that our culture conditions successfully induced P11 expression. We believe that this addresses the concern raised here. Furthermore, if P11 is not reliably expressed in pathogenic PA14, then the published model is unlikely to be relevant in a natural environment. Again, we thank the reviewer for raising this issue and have added this information to the revised manuscript (see above response to Reviewer #2’s Public Reviews).

(6) Legend to Figure 1: please clarify which experiments were done with which PA14 isolates especially for A-C. What is the origin of the N2 strain used here?

These details from Tables 2 and S2 have been added to Figure 1 panels A-C and Figure 3. Bristol N2, obtained from the CGC (reference 257), was used for aversion experiments.

(7) Growth conditions: "These young adults produced comparable P0 and F1 results (Figure 1, Figure 2, and Figure 3)." It is not clear from the text what specific figure panels need to be compared to examine the effect of the variables described in the text. Please indicate which figure panels should be compared (lines 70-95).

The information for the daf-7p::gfp expression experiments displayed in Figure 1 and Figure 2 is presented in Table 1 and Table S1. The data for P0 aversion training using younger animals is now presented in Figure S1.

Reviewer #3 (Recommendations For The Authors):

While overall I found this easy to follow and well-written, I think the clarity of the figures could be improved by incorporating some of the information from S2 into Figure 3. Besides the figure label listing the experiment (Exp1, Exp2, etc) it would be helpful to add pertinent information about the experiment. For example Exp 1.1 (light, 20{degree sign}C), Exp1.2 (dark, 20{degree sign}C), Exp 5 (25{degree sign}C, light), etc.

Thank you for the suggestion. These details from Tables 2 and S2 have been added to Figures 1 A-C, and 3.

Citations

• Moore, R.S., Kaletsky, R., and Murphy, C.T. (2019). Piwi/PRG-1 Argonaute and TGF-beta Mediate Transgenerational Learned Pathogenic Avoidance. Cell 177, 1827-1841 e1812.

• Moore, R.S., Kaletsky, R., and Murphy, C.T. (2021). Protocol for transgenerational learned pathogen avoidance behavior assays in Caenorhabditis elegans. STAR Protoc 2, 100384.

• Kaletsky, R., Moore, R.S., Vrla, G.D., Parsons, L.R., Gitai, Z., and Murphy, C.T. (2020). C. elegans interprets bacterial non-coding RNAs to learn pathogenic avoidance. Nature 586, 445-451.

• Pereira, A.G., Gracida, X., Kagias, K., and Zhang, Y. (2020). C. elegans aversive olfactory learning generates diverse intergenerational effects. J Neurogenet 34, 378-388.

eLife Assessment

This work investigates ZC3H11A as a cause of high myopia through the analysis of human data and experiments with genetic knockout of Zc3h11a in mouse, providing a useful model of myopia. The evidence supporting the conclusion is still incomplete in the revised manuscript as the concerns raised in the previous review were not fully addressed. The article will benefit from further strengthening the genetic analysis, full presentation of human phenotypic data, and explaining the reasons why there was no increased axial length in mice with myopia. The work will be of interest to ophthalmologists and researchers working on myopia.

Reviewer #2 (Public review):

Summary:

The authors reported that mutations were identified in the ZC3H11A gene in four adolescents from 1015 high myopia subjects in their myopia cohort. They further generated Zc3h11a knockout mice utilizing the CRISPR/Cas9 technology.

Comments on revisions:

Chong Chen and colleagues revised the manuscript; however, none of my suggestions from the initial review have been sufficiently addressed.

(1) I indicated that the pathogenicity and novelty of the mutation need to be determined according to established guidelines and databases. However, the conclusion was still drawn without sufficient justification.<br /> (2) The phenotype of heterozygous mutant mice is too weak to support the gene's contribution to high myopia. The revised manuscript does not adequately address these discrepancies. Furthermore, no explanation was provided for why conditional gene deletion was not used to avoid embryonic lethality, nor was there any discussion on tissue- or cell-specific mechanistic investigations.<br /> (3) The title, abstract, and main text continue to misrepresent the role of the inflammatory intracellular PI3K-AKT and NF-κB signaling cascade in inducing high myopia. No specific cell types have been identified as contributors to the phenotype. The mice did not develop high myopia, and no relationship between intracellular signaling and myopia progression has been demonstrated in this study.

Reviewer #3 (Public review):

Chen et al have identified a new candidate gene for high myopia, ZC3H11A, and using a knock-out mouse model, have attempted to validate it as a myopia gene and explain a potential mechanism. They identified 4 heterozygous missense variants in highly myopic teenagers. These variants are in conserved regions of the protein, and predicted to be damaging, but the only evidence the authors provide that these specific variants affect protein function is a supplement figure showing decreased levels of IκBα after transfection with overexpression plasmids (not specified what type of cells were transfected). This does not prove that these mutations cause loss of function, in fact it implies they have a gain-of-function mechanism. They then created a knock-out mouse. Heterozygotes show myopia at all ages examined but increased axial length only at very early ages. Unfortunately, the authors do not address this point or examine corneal structure in these animals. They show that the mice have decreased B-wave amplitude on electroretinogram (a sign of retinal dysfunction associated with bipolar cells), and decreased expression of a bipolar cell marker, PKCα. On electron microscopy, there are morphologic differences in the outer nuclear layer (where bipolar, amacrine, and horizontal cell bodies reside). Transcriptome analysis identified over 700 differentially expressed genes. The authors chose to focus on the PI3K-AKT and NF-κB signaling pathways and show changes in expression of genes and proteins in those pathways, including PI3K, AKT, IκBα, NF-κB, TGF-β1, MMP-2 and IL-6, although there is very high variability between animals. They propose that myopia may develop in these animals either as a result of visual abnormality (decreased bipolar cell function in the retina) or by alteration of NF-κB signaling. These data provide an interesting new candidate variant for development of high myopia, and provide additional data that MMP2 and IL6 have a role in myopia development. For this revision, none of my previous suggestions have been addressed.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

Chen and colleagues investigated ZC3H11A as a potential cause of high myopia (HM) in humans through the analysis of exome sequencing in 1,015 adolescents and experiments involving Zc3h11a knock-out mice. The authors showed four possibly pathogenic missense variants in four adolescents with HM. After that, the authors presented the phenotypic features of Zc3h11a knock-out mice, the result of RNA-sequencing, and a comparison of mRNA and protein levels of the functional candidates between wild-type and Zc3h11a knock-out mice. Based on their observations, the authors concluded that ZC3H11A protein contributes to the early onset of myopia.

The strengths of this manuscript include: (1) successful identification of characteristic ophthalmic phenotypes in Zc3h11a knock-out mice, (2) demonstration of biological features related to myopia, such as PI3K-AKT and NF-kB pathways, and (3) inclusion of supporting human genetic data in individuals with HM. On the other hand, the weaknesses of this paper appear to be: (1) the lack of robust evidence from their genomic analysis, and (2) insufficient evidence to support phenotypic similarity between humans with ZC3H11A mutations and Zc3h11a knock-out mice. Given that the biological mechanisms of high myopia are not fully understood, the identification of a novel gene is valuable. As described in the manuscript, it is worth noting that the previous study using myopic mouse model has implicated the role of ZC3H11A in the etiology of myopia (Fan et al. Plos Genet 2012).

Thank you very much for your valuable suggestions.

Specific comments:

(1) I am concerned about the certainty of similarity in phenotypes between individuals with ZC3H11A mutation and Zc3h11a knock-out mice. A crucial point would be that there are no statistical differences in axial lengths (ALs) between wild-type and Zc3h11a knock-out mice at 8W and 10W, even though ALs in the individuals with ZC3H11A mutation were long. I would also like to note that the phenotypic information of these individuals is not available in the manuscript, although the authors indicated the suppressed b-wave amplitude in Zc3h11a knock-out mice. Considering that the authors described that "Detailed ophthalmic examinations were performed (lines: 321-323)", the detailed clinical features of these individuals should be included in the manuscript.

Thank you for your valuable comments. The axial length in Zc3h11a Het-KO mice were found to be significantly greater than in WT littermates at weeks 4 and 6 (Independent samples t-test, p<0.05; Figure 2A and B). Although no significant differences were observed at other time points, there was still some degree of increase in these parameters. We continued to measure corneal curvature and found no significant differences between the two groups. Therefore, the difference in refraction may be due to the small size of the mouse eye. A 1 D change in refraction corresponds to only a 5-6 μm change in AL(1). However, the SD-OCT resolution used in this study is relatively low (theoretical resolution of 6 μm)(2, 3), so the small changes measured in vitreous cavity depth and AL may not be statistically significant. Additionally, some studies have shown that axial lengths reported in frozen sections are longer than those measured in vivo for age-matched mice(1, 4). Another possible explanation is that the curvature and refractive power of the lens have changed. These hypotheses provide a reasonable explanation for the mismatch between changes in refraction and ocular length parameters.

Reference

(1) Schmucker C, Schaeffel F. A paraxial schematic eye model for the growing C57BL/6 mouse. Vision research 44, 1857-1867 (2004).

(2) Yuan Y, Chen F, Shen M, Lu F, Wang J. Repeated measurements of the anterior segment during accommodation using long scan depth optical coherence tomography. Eye & contact lens 38, 102-108 (2012).

(3) Shen M, et al. SD-OCT with prolonged scan depth for imaging the anterior segment of the eye. Ophthalmic Surgery, Lasers and Imaging Retina 41, S65-S69 (2010).

(4) Schmucker C, Schaeffel F. In vivo biometry in the mouse eye with low coherence interferometry. Vision research 44, 2445-2456 (2004).

Additionally, regarding the “detailed ophthalmic examinations”, due to our patients were selected from a myopia screening cohort of over one million (children and adolescents myopia survey [CAMS] program), and ophthalmic examination only includes semi-annual refractive error measurements (a total of 5 times, with refractive error being the average of the three maximum values) and only one axial length measurement. The inappropriate description of “Detailed clinical features” has been removed.

(2) The term "pathogenic variant" should be used cautiously. Please clarify the pathogenicity of the reported variants in accordance with the ACMG guideline.

Thank you for your valuable comments. Four missense mutations in the ZC3H11A gene (c.412G>A, p.V138I; c.128G>A, p.G43E; c.461C>T, p.P154L; and c.2239T>A, p.S747T) were identified in the 1015 HM patients aged from 15 to 18 years. All of the identified mutations exhibited very low frequencies or does not exist in the Genome Aggregation Database (gnomAD) and Clinvar, and using pathogenicity prediction software SIFT, PolyPhen2, and CADD, most of them display high pathogenicity levels. Among them, c.412G>A, c.128G>A and c.461C>T were located in or around a domain named zf-CCCH_3 (Figure 1A and B). Furthermore, all of the mutation sites were located in highly conserved amino acids across different species (Figure 1C). Four mutations resulted in a higher degree of conformational flexibility and altered the negative charge at the corresponding sites (Figure 1D and E). Meanwhile, through transfection of overexpression mutant plasmids, it was found that compared to the wild-type, the mRNA expression levels of IκBα in the nucleus of all four mutant types (ZC3H11A^V138I, ZC3H11A^G43E, ZC3H11A^P154L and ZC3H11A^S747T) were significantly reduced (Supplement Figure 3). According to the ACMG guidelines, the above mutations can be classified as “Pathogenic Moderate”.

(3) The genetic analysis does not fully support the claim that ZC3H11A is causative for HM. While the authors showed the rare allele frequencies and high CADD scores (> 20) of the identified variants, these were insufficient to establish causality. A helpful way to assess the causality would be performing a segregation analysis. An alternative approach is to show significant association by performing a gene-level association test. Assessing the pathogenicity of the variants using various prediction software, such as SIFT, PolyPhen2, and REVEL may also provide additional supportive evidence.

Thank you for your valuable comments. We have addad the pathogenicity of the variants using various prediction software, such as SIFT, PolyPhen2, CADD, and the population variation databases, such as Genome Aggregation Database (gnomAD_AF) and ClinVar. Meanwhile, through transfection of overexpression mutant plasmids, it was found that compared to the wild-type, the mRNA expression levels of IκBα in the nucleus of all four mutant types (ZC3H11A^V138I, ZC3H11A^G43E, ZC3H11A^P154L and ZC3H11A^S747T) were significantly reduced (Supplement Figure 3).

(4) As shown in Figure 2, significant differences in refraction were observed from 4 weeks to 10 weeks. Nevertheless, no differences were observed in AL, anterior/vitreous chamber depth, and lens depth. The author should experimentally clarify what factors contribute to the observed difference in refraction.

Thank you for your valuable comments. The existing data show significant differences in refraction between 4 and 10 weeks, with the AL and vitreous cavity depth of Het mice being longer than those of WT mice at 4 and 6 weeks. Although no significant differences were observed at other time points, there was still some degree of increase in these parameters. We continued to measure corneal curvature and found no significant differences between the two groups. Therefore, the difference in refraction may be due to the small size of the mouse eye. A 1 D change in refraction corresponds to only a 5-6 μm change in AL(1). However, the SD-OCT resolution used in this study is relatively low (theoretical resolution of 6 μm)(2, 3), so the small changes measured in vitreous cavity depth and AL may not be statistically significant. Additionally, some studies have shown that axial lengths reported in frozen sections are longer than those measured in vivo for age-matched mice(1, 4). Another possible explanation is that the curvature and refractive power of the lens have changed. These hypotheses provide a reasonable explanation for the mismatch between changes in refraction and ocular length parameters.

Reference

(1) Schmucker C, Schaeffel F. A paraxial schematic eye model for the growing C57BL/6 mouse. Vision research 44, 1857-1867 (2004).

(2) Yuan Y, Chen F, Shen M, Lu F, Wang J. Repeated measurements of the anterior segment during accommodation using long scan depth optical coherence tomography. Eye & contact lens 38, 102-108 (2012).

(3) Shen M, et al. SD-OCT with prolonged scan depth for imaging the anterior segment of the eye. Ophthalmic Surgery, Lasers and Imaging Retina 41, S65-S69 (2010).

(4) Schmucker C, Schaeffel F. In vivo biometry in the mouse eye with low coherence interferometry. Vision research 44, 2445-2456 (2004).

(5) The gene names should be italicized throughout the manuscript.

Thank you for your valuable comments. The gene names have been italicized throughout the manuscript.

(6) Table 1: providing chromosomal positions and rs numbers (if available) would be helpful for readers.

Thank you for your valuable comments. We have provided the chromosome positions and rs number (if available) of each mutation in Table 1.

(7) Figure 5b, c, and d: the results of pathway analysis and GO enrichment analysis are difficult to interpret due to the small font size. It would be preferable to present these results in tables. Moreover, the authors should set a significant threshold in the enrichment analyses.

Thank you for your valuable comments. We have adjusted the font size of the image. In the retina transcriptome analysis, we have set Fold change (FC) of at least two and a P value < 0.05 as thresholds to analyze differentially expressed genes (DEGs). The GO terms and KEGG pathways enrichment analysis selected the top 20 with the most significant differences or the highest number of enriched genes for display.

Reviewer #2 (Public Review):

Summary: Chong Chen and colleagues reported that mutations were identified in the ZC3H11A gene in four adolescents from 1015 high myopia subjects in their myopia cohort. They further generated Zc3h11a knockout mice utilizing the CRISPR/Cas9 technology. They analyzed the heterozygotes knockout mice compared to control littermates and found refractive error changes, electrophysiological differences, and retinal inflammation-related gene expression differences. They concluded that ZC3H11A may play a role in the early onset of myopia by regulating inflammatory responses.

Strengths:

Data were shown from both clinical cohort and animal models.

Weaknesses:

Their findings are interesting and important, however; they need to resolve several points to make the current conclusion.

(1) They described the ZC3H11A gene as a pathogenic variant for high myopia. It should be classified as pathogenic according to the guidelines of the American College of Medical Genetics and Genomics (Richards et al., Genet Med 17(5):405-24, 2015). The modes of inheritance for the families need to be shown. They also described identifying the gene as a "new" candidate. It should be checked in databases such as gnomAD and ClinVar, and any previous publications and be declared as a novel variant.

Thank you for your valuable comments. Four missense mutations in the ZC3H11A gene (c.412G>A, p.V138I; c.128G>A, p.G43E; c.461C>T, p.P154L; and c.2239T>A, p.S747T) were identified in the 1015 HM patients aged from 15 to 18 years. All of the identified mutations exhibited very low frequencies or does not exist in the Genome Aggregation Database (gnomAD) and Clinvar, and using pathogenicity prediction software SIFT, PolyPhen2, and CADD, most of them display high pathogenicity levels. Among them, c.412G>A, c.128G>A and c.461C>T were located in or around a domain named zf-CCCH_3 (Figure 1A and B). Furthermore, all of the mutation sites were located in highly conserved amino acids across different species (Figure 1C). Four mutations resulted in a higher degree of conformational flexibility and altered the negative charge at the corresponding sites (Figure 1D and E). Meanwhile, through transfection of overexpression mutant plasmids, it was found that compared to the wild-type, the mRNA expression levels of IκBα in the nucleus of all four mutant types (ZC3H11A^V138I, ZC3H11A^G43E, ZC3H11A^P154L and ZC3H11A^S747T) were significantly reduced (Supplement Figure 3). According to the ACMG guidelines, the above mutations can be classified as “Pathogenic Moderate”.

Unfortunately, our patients are part of the MAGIC project (aged 15 years or older), a cohort consists of thousands of individuals with HM (patients from the children and adolescents myopia survey [CAMS] program) who have undergone WES, and their parents' relevant information was not collected for performing a segregation analysis.

(2) The phenotypes of the heterozygote mice are weak overall. The het mice showed mild to moderate myopic refractive shifts from 4 to 10 weeks of age. However, this cannot be explained by other ocular biometrics such as anterior chamber depth or lens thickness. Some differences are found between het and WT littermates in axial length and vitreous chamber depth but disappear after 8 weeks old. Furthermore, the early differences are not enough to explain the refractive error changes. They mentioned that they did not use homozygotes because of the embryonic lethality. I would strongly suggest employing conditional knockout systems to analyze homozygotes. This will also be able to identify the causative tissues/cells because they assume bipolar cells are functional. The cells in the retinal pigment epithelium and choroid are also important to contribute to myopia development.

Thank you for your valuable comments. The existing data show significant differences in refraction between 4 and 10 weeks, with the AL and vitreous cavity depth of Het mice being longer than those of WT mice at 4 and 6 weeks. Although no significant differences were observed at other time points, there was still some degree of increase in these parameters. We continued to measure corneal curvature and found no significant differences between the two groups. Therefore, the difference in refraction may be due to the small size of the mouse eye. A 1 D change in refraction corresponds to only a 5-6 μm change in AL(1). However, the SD-OCT resolution used in this study is relatively low (theoretical resolution of 6 μm)(2, 3), so the small changes measured in vitreous cavity depth and AL may not be statistically significant. Additionally, some studies have shown that axial lengths reported in frozen sections are longer than those measured in vivo for age-matched mice(1, 4). Another possible explanation is that the curvature and refractive power of the lens have changed. These hypotheses provide a reasonable explanation for the mismatch between changes in refraction and ocular length parameters.

Reference

(1) Schmucker C, Schaeffel F. A paraxial schematic eye model for the growing C57BL/6 mouse. Vision research 44, 1857-1867 (2004).

(2) Yuan Y, Chen F, Shen M, Lu F, Wang J. Repeated measurements of the anterior segment during accommodation using long scan depth optical coherence tomography. Eye & contact lens 38, 102-108 (2012).

(3) Shen M, et al. SD-OCT with prolonged scan depth for imaging the anterior segment of the eye. Ophthalmic Surgery, Lasers and Imaging Retina 41, S65-S69 (2010).

(4) Schmucker C, Schaeffel F. In vivo biometry in the mouse eye with low coherence interferometry. Vision research 44, 2445-2456 (2004).

The drawback is that, we did not conduct relevant research on homozygous knockout mice. The first reason is that our patient's mutation pattern is heterozygous mutation (Heterozygous knockout mice can better simulate human phenotypes). The second reason is that homozygous knockout mice are lethal, and we did not use the conditional knockout mouse model for further research. At the same time, we limited the pathway of myopia to the recognized and classical retina-sclera pathway, and did not study other pathways such as retinal pigment epithelium and choroid.

(3) Their hypothesis regarding inflammatory gene changes and myopic development is not logical. Are the inflammatory responses evoked from bipolar cells? Did the mice show an accumulation of inflammatory cells in the inner retina? Visible retinal inflammation is not generally seen in either early-onset or high-myopia human subjects. Can this be seen in the actual subjects in the cohort? To me, this is difficult to adapt the retina-to-sclera signaling they mentioned in the discussion so far. Egr-1 may be examined as described.

Thank you for your valuable comments. We have removed the hypothesis regarding inflammatory gene changes and myopic development. At present, the explanation is based solely on the correlation of signal pathways, the theoretical basis comes from the reference literature:

“Lin et al., Role of Chronic Inflammation in Myopia Progression: Clinical Evidence and Experimental Validation. EBioMedicine, 2016 Aug:10:269-81, Figure 7.”

Reviewer #3 (Public Review):

Chen et al have identified a new candidate gene for high myopia, ZC3H11A, and using a knock-out mouse model, have attempted to validate it as a myopia gene and explain a potential mechanism. They identified 4 heterozygous missense variants in highly myopic teenagers. These variants are in conserved regions of the protein, but the authors provide no evidence that these specific variants affect protein function. They then created a knock-out mouse. Heterozygotes show myopia at all ages examined but increased axial length only at very early ages. Unfortunately, the authors do not address this point or examine corneal structure in these animals. They show that the mice have decreased B-wave amplitude on electroretinogram (a sign of retinal dysfunction associated with bipolar cells), and decreased expression of a bipolar cell marker, PKCa. They do not address, however, whether there are fewer bipolar cells, or simply decreased expression of the marker protein. On electron microscopy, there are morphologic differences in the outer nuclear layer (where bipolar, amacrine, and horizontal cell bodies reside). Transcriptome analysis identified over 700 differentially expressed genes. The authors chose to focus on the PI3K-AKT and NF-kB signaling pathways and show changes in the expression of genes and proteins in those pathways, including PI3K, AKT, IkBa, NF-kB, TGF-b1, MMP-2, and IL-6, although there is very high variability between animals. They propose that myopia may develop in these animals either as a result of visual abnormality (decreased bipolar cell function in the retina) or by alteration of NF-kB signaling. These data provide an interesting new candidate variant for the development of high myopia, and provide additional data that MMP2 and IL6 have a role in myopia development, but do not support the claim of the title that myopia is caused by an inflammatory reaction.

Thank you for your valuable comments. Four missense mutations in the ZC3H11A gene (c.412G>A, p.V138I; c.128G>A, p.G43E; c.461C>T, p.P154L; and c.2239T>A, p.S747T) were identified in the 1015 HM patients aged from 15 to 18 years. All of the identified mutations exhibited very low frequencies or does not exist in the Genome Aggregation Database (gnomAD) and Clinvar, and using pathogenicity prediction software SIFT, PolyPhen2, and CADD, most of them display high pathogenicity levels. Among them, c.412G>A, c.128G>A and c.461C>T were located in or around a domain named zf-CCCH_3 (Figure 1A and B). Furthermore, all of the mutation sites were located in highly conserved amino acids across different species (Figure 1C). Four mutations resulted in a higher degree of conformational flexibility and altered the negative charge at the corresponding sites (Figure 1D and E). Meanwhile, through transfection of overexpression mutant plasmids, it was found that compared to the wild-type, the mRNA expression levels of IκBα in the nucleus of all four mutant types (ZC3H11A^V138I, ZC3H11A^G43E, ZC3H11A^P154L and ZC3H11A^S747T) were significantly reduced (Supplement Figure 3). According to the ACMG guidelines, the above mutations can be classified as “Pathogenic Moderate”.

The existing data show significant differences in refraction between 4 and 10 weeks, with the AL and vitreous cavity depth of Het mice being longer than those of WT mice at 4 and 6 weeks. Although no significant differences were observed at other time points, there was still some degree of increase in these parameters. We continued to measure corneal curvature and found no significant differences between the two groups. Therefore, the difference in refraction may be due to the small size of the mouse eye. A 1 D change in refraction corresponds to only a 5-6 μm change in AL(1). However, the SD-OCT resolution used in this study is relatively low (theoretical resolution of 6 μm)(2, 3), so the small changes measured in vitreous cavity depth and AL may not be statistically significant. Additionally, some studies have shown that axial lengths reported in frozen sections are longer than those measured in vivo for age-matched mice(1, 4). Another possible explanation is that the curvature and refractive power of the lens have changed. These hypotheses provide a reasonable explanation for the mismatch between changes in refraction and ocular length parameters.

To evaluate the change in the number of a specific type of retinal cells, the most commonly used experimental method involves staining with antibodies specific to the target cell type, followed by fluorescence microscopy. The fluorescence intensity or the number of cells can be analyzed semi-quantitatively to assess the changes in the specific cell type in the retina. For example, in retinal degenerative models, rhodopsin-specific staining is used to identify the loss of rod cells. In our study, we selected PCK-α as a marker protein for bipolar cells to assess their number. Additionally, transmission electron microscopy (TEM) was used to observe damage to the cell morphology in the inner nuclear layer (INL) of Het mice, where bipolar cell bodies are located. Based on both sets of data, we conclude that bipolar cells have indeed undergone structural damage and a reduction in number.

Reference

(1) Schmucker C, Schaeffel F. A paraxial schematic eye model for the growing C57BL/6 mouse. Vision research 44, 1857-1867 (2004).

(2) Yuan Y, Chen F, Shen M, Lu F, Wang J. Repeated measurements of the anterior segment during accommodation using long scan depth optical coherence tomography. Eye & contact lens 38, 102-108 (2012).

(3) Shen M, et al. SD-OCT with prolonged scan depth for imaging the anterior segment of the eye. Ophthalmic Surgery, Lasers and Imaging Retina 41, S65-S69 (2010).

(4) Schmucker C, Schaeffel F. In vivo biometry in the mouse eye with low coherence interferometry. Vision research 44, 2445-2456 (2004).

We have removed the hypothesis regarding inflammatory gene changes and myopic development. At present, the explanation is based solely on the correlation of signal pathways, the theoretical basis comes from the reference literature:

“Lin et al., Role of Chronic Inflammation in Myopia Progression: Clinical Evidence and Experimental Validation. EBioMedicine, 2016 Aug:10:269-81, Figure 7.”

eLife Assessment

This study follows up on Arimura et al's powerful new method MagIC-Cryo-EM for imaging native complexes at high resolution. Using a clever design embedding protein spacers between the antibody and the nucleosomes purified, thereby minimizing interference from the beads, the authors concentrate linker histone variant H1.8 containing nucleosomes. From these samples, the authors obtain convincing atomic structures of the H1.8 bound chromatosome purified from interphase and metaphase cells, finding a NPM2 chaperone bound form exists as well. Caveats previously noted have been addressed nicely in the revision, strengthening the overall conclusions. This is an important new tool in the arsenal of single molecule biologists, permitting a deep dive into structure of native complexes, and will be of high interest to a broad swathe of scientists studying native macromolecules present at low concentrations in cells.

Reviewer #1 (Public review):

Summary:

In this manuscript, Arimura et al describe MagIC-Cryo-EM, an innovative method for immune-selective concentrating of native molecules and macromolecular complexes for Cryo-EM imaging and single-particle analysis. Typically, Cryo-EM imaging requires much larger concentrations of biomolecules than those that are feasible to achieve by conventional biochemical fractionation. This manuscript is meticulously and clearly written and the new technique is likely to become a great asset to other electron microscopists and chromatin researchers.

Strengths:

Previously, Arimura et al. (Mol. Cell 2021) isolated from Xenopus extract and resolved by Cryo-EM a sub-class of native nucleosomes conjugated containing histone H1.8 at the on-dyad position, similar to that previously observed by other researchers with reconstituted nucleosomes. Here they sought to analyze immuno-selected nucleosomes aiming to observe specific modes of H1.8 positioning (e.g. on-dyad and off-dyad) and potentially reveal structural motifs responsible for the decreased affinity of H1.8 for the interphase chromatin compared to metaphase chromosomes. The main strength of this work is a clever and novel methodological design, in particular the engineered protein spacers to separate captured nucleosomes from streptavidin beads for clear imaging. The authors provide a detailed step-by-step description of MagIC-Cryo-EM procedure including nucleosome isolation, preparation of GFP nanobody attached magnetic beads, optimization of the spacer length, concentration of the nucleosomes on graphene grids, data collection and analysis, including their new DUSTER method to filter-out low signal particles. This tour de force methodology should facilitate the consideration of MagIC-Cryo-EM by other electron microscopists, especially for analysis of native nucleosome complexes.<br /> In pursuit of biologically important new structures, the immune-selected H1.8-containing nucleosomes were solved at about 4A resolution; their structure appears to be very similar to the previously determined structure of H1.8-reconstituted nucleosomes. There were no apparent differences between the metaphase and interphase complexes suggesting that the on-dyad and off-dyad positioning does not explain the differences in H1.8 - nucleosome binding. However, they were able to identify and solve complexes of H1.8-GFP with histone chaperone NPM2 in a closed and open conformation providing mechanistic insights for H1-NPM2 binding and the reduced affinity of H1.8 to interphase chromatin as compared to metaphase chromosomes.

MagIC technique still has certain limitations resulting from formaldehyde fixation, use of bacterial-expressed recombinant H1.8-GFP, and potential effects of magnetic beads and/or spacer on protein structure, which are explicitly discussed in the text. Notwithstanding these limitations, MagIC-Cryo-EM is expected to become a great asset to other electron microscopists and biochemists studying native macromolecular complexes.

Comments on revisions:

In the revision, Arimura et al. have constructively addressed the reviewer's concerns, by discussing possible limitations and including additional information on proteomic analysis and H1.8-NPM2 structures.<br /> The revised manuscript and rebuttal letter strengthen my initial opinion that this paper describes an innovative method for immune-selective concentrating of native molecules and macromolecular complexes thus enabling Cryo-EM imaging and structural analysis of native nucleosome complexes at low concentration. This manuscript is meticulously and clearly written and may become a great asset to other electron microscopists and chromatin researchers

Reviewer #2 (Public review):

Summary:

The authors present a straightforward and convincing demonstration of a reagent and workflow that they collectively term "MagIC-cryo-EM", in which magnetic nanobeads combined with affinity linkers are used to specifically immobilize and locally concentrate complexes that contain a protein-of-interest. As a proof of concept, they localize, image, and reconstruct H1.8-bound nucleosomes reconstructed from frog egg extracts. The authors additionally devised an image-processing workflow termed "DuSTER", which increases the true positive detections of the partially ordered NPM2 complex. The analysis of the NPM2 complex {plus minus} H1.8 was challenging because only ~60 kDa of protein mass was ordered. Overall, single-particle cryo-EM practitioners should find this study useful.

Strengths:

The rationale is very logical and the data are convincing.

Weaknesses:

I have seen an earlier version of this study at a conference. The conference presentation was much easier to follow than the current manuscript. It is as if this manuscript had undergone review at another journal and includes additional experiments to satisfy previous reviewers. Specifically, the NPM2 results don't seem to add much to the main story (MagIC-cryo-EM) and read more like an addendum. The authors could probably publish the NPM2 results separately, which would make the core MagIC results (sans DusTER) easier to read.

Comments on revisions:

The authors have addressed my concerns. Congratulations!

eLife Assessment

The formation of the Z-ring at the time of bacterial cell division interests researchers working towards understanding cell division across all domains of life. The manuscript by Jasnin et al reports the cryoET structure of toroid assembly formation of FtsZ filaments driven by ZapD as the cross linker. The findings are important and have the potential to open a new dimension in the field, but the evidence to support these exciting claims is currently incomplete, mostly because of the suboptimal "resolution of the toroids", so in the absence of additional experiments, the interpretations would need to be toned down.

Reviewer #1 (Public review):

Summary:

The major result in the manuscript is the observation of the higher order structures in a cryoET reconstruction that could be used for understanding the assembly of toroid structures. The cross-linking ability of ZapD dimers result in bending of FtsZ filaments to a constant curvature. Many such short filaments are stitched together to form a toroid like structure. The geometry of assembly of filaments - whether they form straight bundles or toroid like structures - depends on the relative concentrations of FtsZ and ZapD.

Strengths:

In addition to a clear picture of the FtsZ assembly into ring-like structures, the authors have carried out basic biochemistry and biophysical techniques to assay the GTPase activity, the kinetics of assembly, and the ZapD to FtsZ ratio.

Weaknesses:

The discussion does not provide an overall perspective that correlates the cryoET structural organisation of filaments with the biophysical data. The current version has improved in terms of addressing this weakness and clearly states the lacuna in the model proposed based on the technical limitations.

Future scope of work includes the molecular basis of curvature generation and how molecular features of FtsZ and ZapD affect the membrane binding of the higher order assembly.

Reviewer #3 (Public review):

Summary:

Previous studies have analyzed the binding of ZapD to FtsZ and provided images of negatively stained toroids and straight bundles, where FtsZ filaments are presumably crosslinked by ZapD dimers. Toroids without ZapD have also been previously formed by treating FtsZ with crowding agents. The present study is the first to apply cryoEM tomography, which can resolve the structure of the toroids in 3D. This shows a complex mixture of filaments and sheets irregularly stacked in the Z direction and spaced radially. The most important interpretation would be to distinguish FtsZ filaments from ZapD crosslinks, This is less convincing. The authors seem aware of the ambiguity: "However, we were unable to obtain detailed structural information about the ZapD connectors due to the heterogeneity and density of the toroidal structures, which showed significant variability in the conformations of the connections between the filaments in all directions." Therefore, the reader may assume that the crosslinks identified and colored red are only suggestions, and look for their own structural interpretations. But readers should also note some inconsistencies in stoichiometry and crosslinking arrangements that are detailed under "weaknesses."

Strengths.

This is the first cryoEM tomography to image toroids and straight bundles of FtsZ filaments bound to ZapD. A strength is the resolution, which. at least for the straight bundles. is sufficient to resolve the ~4.5 nm spacing of ZapD dimers attached to and projecting subunits of an FtsZ filament. Another strength is the pelleting assay to determine the stoichiometry of ZapD:FtsZ (although this also leads to weaknesses of interpretation).

Weaknesses

The stoichiometry presents some problems. Fig. S5 uses pelleting to convincingly establish the stoichiometry of ZapD:FtsZ. Although ZapD is a dimer, the concentration of ZapD is always expressed as that of its subunit monomers. Fig. S5 shows the stoichiometry of ZapD:FtsZ to be 1:1 or 2:1 at equimolar or high concentrations of ZapD. Thus at equimolar ZapD, each ZapD dimer should bridge two FtsZ's, likely forming crosslinks between filaments. At high ZapD, each FtsZ should have it's own ZapD dimer. However, this seems contradicted by later statements in Discussion and Results. (1) "At lower concentrations of ZapD, .. toroids are the most prominent structures, containing one ZapD dimer for every four to six FtsZ molecules." Shouldn't it be one ZapD dimer for every two FtsZ? (2) "at the high ZapD concentration...a ZapD dimer binds two FtsZ molecules connecting two filaments." Doesn't Fig. S5 show that each FtsZ subunit has its own ZapD dimer? And wouldn't this saturate the CTD sites with dimers and thus minimize crosslinking?

A major weakness is the interpretation of the cryoEM tomograms, specifically distinguishing ZapD from FtsZ. The distinction of crosslinks seems based primarily on structure: long continuous filaments (which often appear as sheets) are FtsZ, and small masses between filaments are ZapD. The density of crosslinks seems to vary substantially over different parts of the figures. More important, the density of ZapD's identified and colored red seem much lower than the stoichiometry detailed above. Since the mass of the ZapD monomer is half that of FtsZ, the 1:1 stoichiometry in toroids means that 1/3 of the mass should be ZapD and 2/3 FtsZ. However, the connections identified as ZapD seem much fewer than the expected 1/3 of the mass. The authors conclude that connections run horizontally, diagonally and vertically, which implies no regularity. This seems likely, but as I would suggest that readers need to consider for themselves what they would identify as a crosslink.

In contrast to the toroids formed at equimolar FtsZ and ZapD, thin bundles of straight filaments are assembled in excess ZapD. Here the stoichiometry is 2:1, which would mean that every FtsZ should have a bound ZapD DIMER. The segmentation of a single filament in Fig. 5e seems to agree with this, showing an FtsZ filament with spikes emanating like a picket fence, with a 4.5 nm periodicity. This is consistent with each spike being a ZapD dimer, and every FtsZ subunit along the filament having a bound ZapD dimer. But if each FtsZ has its own dimer, this would seem to eliminate crosslinking. The interpretative diagram in Fig. 6, far right, which shows almost all ZapD dimers bridging two FtsZs on opposite filaments, would be inconsistent with this 2:1 stoichiometry.

In the original review I suggested a control that might help identify the structures of ZapD in the toroids. Popp et al (Biopolymers 2009) generated FtsZ toroids that were identical in size and shape to those here, but lacking ZapD. These toroids of pure FtsZ were generated by adding 8% polyvinyl chloride, a crowding agent. The filamentous substructure of these toroids in negative stain seemed very similar to that of the ZapD toroids here. CryoET of these toroids lacking ZapD might have been helpful in confirming the identification of ZapD crosslinks in the present toroids. However, the authors declined to explore this control.

Finally, it should be noted that the CTD binding sites for ZapD should be on the outside of curved filaments, the side facing the membrane in the cell. All bound ZapD should project radially outward, and if it contacted the back side of the next filament, it should not bind (because the CTD is on the front side). The diagram second to right in Fig. 6 seems to incorporate this abortive contact.

eLife Assessment

Combining experimental and computation approaches, this manuscript provides convincing evidence for a post-transcriptional mechanism that provides robust control over the protein expression level of RecB in E. coli. In addition to uncovering how DNA damage drives higher levels of RecB protein, this work also reveals important tenets for how broader mechanisms that suppress noise and underlie responsive tuning of protein levels can be achieved.

Reviewer #1 (Public review):

Summary:

In this study the authors use an elegant set of single-molecule experiments to assess the transcriptional and post-transcriptional regulation of RecB. The question stems from a previous observation from the same lab, that RecB protein levels are low and not induced under DNA damage. The authors first show that recB transcript levels are low and have a short half-live. They further show that RecB levels are likely regulated via translational control. They provide evidence for low noise in RecB protein levels across cells and show that the translation of the mRNA increases under double-strand break conditions. Authors identify Hfq binding sites in the recbcd operon and show that Hfq regulates the levels of RecB protein without changing the mRNA levels. They suggest that RecB translation is directly controlled by Hfq binding to mRNA, as mutating one of the binding sites has a direct effect on RecB protein levels.

The implication of Hfq in regulation of RecB translation is important, and suggests mechanisms of cellular response to DNA damage that are beyond the canonically studied mechanisms (such as transcriptional regulation by LexA). Data are clearly presented and the writing is direct and easy to follow. Overall, the study is well-designed and provides novel insights into the regulation of RecB, that is part of the complex required to process break ends.

Comments on revisions:

All my comments are addressed - I congratulate the authors on this excellent work.

Reviewer #2 (Public review):

Summary:

The authors carry out a careful and rigorous quantitative analysis of RecB transcript and protein levels at baseline and in response to DNA damage. Using single-molecule FISH and Halo-tagging in order to achieve sensitive measurements, they provide evidence that enhanced RecB protein levels in response to DNA damage are achieved through a post-transcriptional mechanism mediated by the La-like RNA binding protein, Hfq. In terms of biological relevance, the authors suggest that this mechanism provides a way to control the optimum level of RecB expression as both deletion and over-expression are deleterious. In addition, the proposed mechanism provides a new framework for understanding how transcriptional noise can be suppressed at the protein level.

Strengths:

Strengths of the manuscript include the rigorous approaches and orthogonal evidence to support the core conclusions, for example, the evidence that altering either Hfq or its recognition sequence on the RNA similarly enhance the protein to RNA ratio of RecB. The writing is clear and the experiments are well-controlled. The modeling approaches provide essential context to interpret the data, particularly given the small numbers of molecules per cell. The interpretations are careful and well supported. The findings

Weaknesses:

Future studies (and possibly new experimental tools) will be needed to provide further insight into the relevance of the findings to more subtle changes in RecB levels than that occurring in response to extensive DNA damage.

Reviewer #3 (Public review):

Summary:

The work by Kalita et al. reports regulation of RecB expression by Hfq protein in E.coli cell. RecBCD is an essential complex for DNA repair and chromosome maintenance. The expression level needs to be regulated at low level under regular growth conditions but upregulated upon DNA damage. Through quantitative imaging, the authors demonstrate that recB mRNAs and proteins are expressed at low level under regular conditions. While the mRNA copy number demonstrates high noise level due to stochastic gene expression, the protein level is maintained at a lower noise level compared to expected value. Upon DNA damage, the authors claim that the recB mRNA concentration is decreased, however RecB protein level is compensated by higher translation efficiency. Through analyzing CLASH data on Hfq, they identified two Hfq binding sites on RecB polycistronic mRNA, one of which is localized at the ribosome binding site (RBS). Through measuring RecB mRNA and protein level in the ∆hfq cell, the authors conclude that binding of Hfq to the RBS region of recB mRNA suppresses translation of recB mRNA. This conclusion is further supported by the same measurement in the presence of Hfq sequestrator, the sRNA ChiX, and the deletion of the Hfq binding region on the mRNA.

Strengths:

(1) The manuscript is well-written and easy to understand.<br /> (2) While there are reported cases of Hfq regulating translation of bound mRNAs, its effect on reducing translation noise is relatively new.<br /> (3) The imaging and analysis are carefully performed with necessary controls.

Comments on revisions:

The authors have addressed my previous concerns.

eLife Assessment

In this detailed study, Cohen and Ben-Shaul characterized Accessory Olfactory Bulb (AOB) cell responses to various conspecific urine samples in female mice across the estrous cycle. The authors found that AOB cell responses varied depending on the strain and sex of the sample, but no clear differences were observed between estrous and non-estrous females. These findings provide convincing evidence that the AOB functions as a stable sensory relay, without directly modulating responses based on reproductive state, which supports the role of downstream brain regions in integrating reproductive state. Overall, this study provides valuable insights for researchers in the fields of olfaction and social neuroscience.

Reviewer #1 (Public review):

Summary:

In this detailed study, Cohen and Ben-Shaul characterized the AOB cell responses to various conspecific urine samples in female mice across the estrous cycle. The authors found that AOB cell responses vary with the strains and sexes of the samples. Between estrous and non-estrous females, no clear or consistent difference in responses was found. The cell response patterns, as measured by the distance between pairs of stimuli, are largely stable. When some changes do occur, they are not consistent across strains or male status. The authors concluded that AOB detects the signals without interpreting them. Overall, this study will provide useful information for scientists in the field of olfaction.

Strengths:

The study uses electrophysiological recording to characterize the responses of AOB cells to various urines in female mice. AOB recording is not trivial as it requires activation of VNO pump. The team uses a unique preparation to activate the VNO pump with electric stimulation, allowing them to record AOB cell responses to urines in anesthetized animals. The study comprehensively described the AOB cell responses to social stimuli and how the responses vary (or not) with features of the urine source and the reproductive state of the recording females. The dataset could be a valuable resource for scientists in the field of olfaction.

Weaknesses:

(1) The figures could be better labeled.

(2) For Figure 2E, please plot the error bar. Are there any statistics performed to compare the mean responses?

(3) For Figure 2D, it will be more informative to plot the percentage of responsive units.

(4) Could the similarity in response be explained by the similarity in urine composition? The study will be significantly strengthened by understanding the "distance" of chemical composition in different urine.

(5) If it is not possible for the authors to obtain these data first-hand, published data on MUPs and chemicals found in these urines may provide some clues.

(6) It is not very clear to me whether the female overrepresentation is because there are truly more AOB cells that respond to females than males or because there are only two female samples but 9 male samples.

(7) If the authors only select two male samples, let's say ICR Naïve and ICR DOM, combine them with responses to two female samples, and do the same analysis as in Figure 3, will the female response still be overrepresented?

(8) In Figure 4B and 4C, the pairwise distance during non-estrus is generally higher than that during estrus, although they are highly correlated. Does it mean that the cells respond to different urines more distinctively during diestrus than in estrus?

(9) The correlation analysis is not entirely intuitive when just looking at the figures. Some sample heatmaps showing the response differences between estrous states will be helpful.

Reviewer #2 (Public review):

Summary:

Many aspects of the study are carefully done, and in the grand scheme this is a solid contribution. I have no "big-picture" concerns about the approach or methodology. However, in numerous places the manuscript is unnecessarily vague, ambiguous, or confusing. Tightening up the presentation will magnify their impact.

Strengths:

(1) The study includes urine donors from males of three strains each with three social states, as well as females in two states. This diversity significantly enhances their ability to interpret their results.

(2) Several distinct analyses are used to explore the question of whether AOB MCs are biased towards specific states or different between estrus and non-estrus females. The results of these different analyses are self-reinforcing about the main conclusions of the study.

(3) The presentation maintains a neutral perspective throughout while touching on topics of widespread interest.

Weaknesses:

(1) Introduction:<br /> The discussion of the role of the VNS and preferences for different male stimuli should perhaps include Wysocki and Lepri 1991

(2) Results:<br /> a) Given the 20s gap between them, the distinction between sample application and sympathetic nerve trunk stimulation needs to be made crystal clear; in many places, "stimulus application" is used in places where this reviewer suspects they actually mean sympathetic nerve trunk stimulation.<br /> b) There appears to be a mismatch between the discussion of Figure 3 and its contents. Specifically, there is an example of an "adjusted" pattern in 3A, not 3B.<br /> c) The discussion of patterns neglects to mention whether it's possible for a neuron to belong to more than one pattern. For example, it would seem possible for a neuron to simultaneously fit the "ICR pattern" and the "dominant adjusted pattern" if, e.g., all ICR responses are stronger than all others, but if simultaneously within each strain the dominant male causes the largest response.

(3) Discussion:<br /> a) The discussion of chemical specificity in urine focuses on volatiles and MUPs (citation #47), but many important molecules for the VNS are small, nonvolatile ligands. For such molecules, the corresponding study is Fu et al 2015.<br /> b) "Following our line of reasoning, this scarcity may represent an optimal allocation of resources to separate dominant from naïve males": 1 unit out of 215 is roughly consistent with a single receptor. Surely little would be lost if there could be more computational capacity devoted to this important axis than that? It seems more likely that dominance is computed from multiple neuronal types with mixed encoding.

(4) Methods:<br /> a) Male status, "were unambiguous in most cases": is it possible to put numerical estimates on this? 55% and 99% are both "most," yet they differ substantially in interpretive uncertainty.<br /> b) Surgical procedures and electrode positioning: important details of probes are missing (electrode recording area, spacing, etc).<br /> c) Stimulus presentation procedure: Are stimuli manually pipetted or delivered by apparatus with precise timing?<br /> d) Data analysis, "we applied more permissive criteria involving response magnitude": it's not clear whether this is what's spelled out in the next paragraph, or whether that's left unspecified. In either case, the next paragraph appears to be about establishing a noise floor on pattern membership, not a "permissive criterion."<br /> e) Data analysis, method for assessing significance: there's a lot to like about the use of pooling to estimate the baseline and the use of an ANOVA-like test to assess unit responsiveness.<br /> But:<br /> i) for a specific stimulus, at 4 trials (the minimum specified in "Stimulus presentation procedure") kruskalwallis is questionable. They state that most trials use 5, however, and that should be okay.<br /> ii) the methods statement suggests they are running kruskalwallis individually for each neuron/stimulus, rather than once per neuron across all stimuli. With 11 stimuli, there is a substantial chance of a false-positive if they used p < 0.05 to assess significance. (The actual threshold was unstated.) Were there any multiple comparison corrections performed? Or did they run kruskalwallis on the neuron, and then if significant assess individual stimuli? (Which is a form of multiple-comparisons correction.)

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this detailed study, Cohen and Ben-Shaul characterized the AOB cell responses to various conspecific urine samples in female mice across the estrous cycle. The authors found that AOB cell responses vary with the strains and sexes of the samples. Between estrous and non-estrous females, no clear or consistent difference in responses was found. The cell response patterns, as measured by the distance between pairs of stimuli, are largely stable. When some changes do occur, they are not consistent across strains or male status. The authors concluded that AOB detects the signals without interpreting them. Overall, this study will provide useful information for scientists in the field of olfaction.

Strengths:

The study uses electrophysiological recording to characterize the responses of AOB cells to various urines in female mice. AOB recording is not trivial as it requires activation of VNO pump. The team uses a unique preparation to activate the VNO pump with electric stimulation, allowing them to record AOB cell responses to urines in anesthetized animals. The study comprehensively described the AOB cell responses to social stimuli and how the responses vary (or not) with features of the urine source and the reproductive state of the recording females. The dataset could be a valuable resource for scientists in the field of olfaction.

Weaknesses:

(1) The figures could be better labeled.

Figures will be revised to provide more detailed labeling.

(2) For Figure 2E, please plot the error bar. Are there any statistics performed to compare the mean responses?

We did not perform statistical comparisons (between the mean rates across the population). We will add this analysis and the corresponding error bars. 

(3) For Figure 2D, it will be more informative to plot the percentage of responsive units.

We will do it.

(4) Could the similarity in response be explained by the similarity in urine composition? The study will be significantly strengthened by understanding the "distance" of chemical composition in different urine.

We agree. As we wrote in the Discussion: “Ultimately, lacking knowledge of the chemical space associated with each of the stimuli, this and all the other ideas developed here remain speculative.”

A better understanding of the chemical distance is an important aspect that we aim to include in our future studies. However, this is far from trivial, as it is not chemical distance per se (which in itself is hard to define), but rather the “projection” of chemical space on the vomeronasal receptor neurons array. That is, knowledge of the chemical composition of the stimuli, lacking full knowledge of which molecules are vomeronasal system ligands, will only provide a partial picture. Despite these limitations, this is an important analysis which we would have done had we access to this data.

(5) If it is not possible for the authors to obtain these data first-hand, published data on MUPs and chemicals found in these urines may provide some clues.

Measurements about some classes of molecules may be found for some of the stimuli that we used here, but not for all. We are not aware of any single dataset that contains this information for any type of molecules (e.g., MUPs) across the entire stimulus set that we have used. More generally, pooling results from different studies has limited validity because of the biological and technical variability across studies. In order to reliably interpret our current recordings, it would be necessary to measure the urinary content of the very same samples that were used for stimulation. Unfortunately, we are not able to conduct this analysis at this stage.

(6) It is not very clear to me whether the female overrepresentation is because there are truly more AOB cells that respond to females than males or because there are only two female samples but 9 male samples.

It is true that the number of neurons fulfilling each of the patterns depends on the number of individual stimuli that define it. However, our measure of “over-representation” aims to overcome this bias, by using bootstrapping to reveal if the observed number of patterns is larger than expected by chance. We also note that more generally, the higher frequency of responses to female, as compared to male stimuli, is obtained in other studies by others and by us, also when the number of male and female stimuli is matched (e.g., Bansal et al BMC Biol 2021, Ben-Shaul et al, PNAS 2010, Hendrickson et al, JNS, 2008).

(7) If the authors only select two male samples, let's say ICR Naïve and ICR DOM, combine them with responses to two female samples, and do the same analysis as in Figure 3, will the female response still be overrepresented?

We believe that the answer is positive, but we can, and will perform this analysis to check.

(8) In Figure 4B and 4C, the pairwise distance during non-estrus is generally higher than that during estrus, although they are highly correlated. Does it mean that the cells respond to different urines more distinctively during diestrus than in estrus?

This is an important observation. For the Euclidean distance there might be a simple explanation as the distance depends on the number of units (and there are more units recorded in non-estrus females). However, this simple explanation does not hold for the correlation distance. A higher distance implies higher discrimination during the non-estrus stage, but our other analyses of sparseness and the selectivity indices do not support this idea. We note that absolute values of distance measures should generally be interpreted cautiously, as they may depend on multiple factors including sample size. Also, a small number of non-selective units could increase the correlation in responses among stimuli, and thus globally shift the distances. For these reasons, we focus on comparisons, rather than the absolute values of the correlation distances. In the revised manuscript, we will note and discuss this important observation.

(9) The correlation analysis is not entirely intuitive when just looking at the figures. Some sample heatmaps showing the response differences between estrous states will be helpful.

If we understand correctly, the idea is to show the correlation matrices from which the values in 4B and 4C are taken. We can and will do this, probably as a supplementary figure.

Reviewer #2 (Public review):

Summary:

Many aspects of the study are carefully done, and in the grand scheme this is a solid contribution. I have no "big-picture" concerns about the approach or methodology. However, in numerous places the manuscript is unnecessarily vague, ambiguous, or confusing. Tightening up the presentation will magnify their impact.

We will revise the text with the aim of tightening the presentation.

Strengths:

(1) The study includes urine donors from males of three strains each with three social states, as well as females in two states. This diversity significantly enhances their ability to interpret their results.

(2) Several distinct analyses are used to explore the question of whether AOB MCs are biased towards specific states or different between estrus and non-estrus females. The results of these different analyses are self-reinforcing about the main conclusions of the study.

(3) The presentation maintains a neutral perspective throughout while touching on topics of widespread interest.

Weaknesses:

(1) Introduction:

The discussion of the role of the VNS and preferences for different male stimuli should perhaps include Wysocki and Lepri 1991

Agreed. we will refer to this work in our discussion.

(2) Results:

a) Given the 20s gap between them, the distinction between sample application and sympathetic nerve trunk stimulation needs to be made crystal clear; in many places, "stimulus application" is used in places where this reviewer suspects they actually mean sympathetic nerve trunk stimulation.

In this study, we have considered both responses that are triggered by sympathetic trunk activation, and those that occur (as happens in some preparations) immediately following stimulus application (and prior to nerve trunk stimulation). An example of the latter Is provided in the second unit shown in Figure 1D (and this is indicated also in the figure legend). In our revision, we will further clarify this confusing point.

b) There appears to be a mismatch between the discussion of Figure 3 and its contents. Specifically, there is an example of an "adjusted" pattern in 3A, not 3B.

True. Thanks for catching this error. We will correct this.

c) The discussion of patterns neglects to mention whether it's possible for a neuron to belong to more than one pattern. For example, it would seem possible for a neuron to simultaneously fit the "ICR pattern" and the "dominant adjusted pattern" if, e.g., all ICR responses are stronger than all others, but if simultaneously within each strain the dominant male causes the largest response.

This is true. In the legend to Figure 3B, we actually write: “A neuron may fulfill more than one pattern and thus may appear in more than one row.”, but we will discuss this point in the main text as well.

(3) Discussion:

a) The discussion of chemical specificity in urine focuses on volatiles and MUPs (citation #47), but many important molecules for the VNS are small, nonvolatile ligands. For such molecules, the corresponding study is Fu et al 2015.

We fully agree. We will expand our discussion and refer to Fu et al.

b) "Following our line of reasoning, this scarcity may represent an optimal allocation of resources to separate dominant from naïve males": 1 unit out of 215 is roughly consistent with a single receptor. Surely little would be lost if there could be more computational capacity devoted to this important axis than that? It seems more likely that dominance is computed from multiple neuronal types with mixed encoding.

We agree, and we are not claiming that dominance, nor any other feature, is derived using dedicated feature selective neurons.  Our discussion of resource allocation is inevitably speculative. Our main point in this context is that a lack of overrepresentation does not imply that a feature is not important. We will revise our discussion to better clarify our view of this issue.

(4) Methods:

a) Male status, "were unambiguous in most cases": is it possible to put numerical estimates on this? 55% and 99% are both "most," yet they differ substantially in interpretive uncertainty.

This sentence is actually misleading and irrelevant. Ambiguous cases were not considered as dominant for urine collection. We only classified mice as dominant if they were “won” in the tube test and exhibited dominant behavior in the subsequent observation period in the cage. We will correct the wording in the revised manuscript.

b) Surgical procedures and electrode positioning: important details of probes are missing (electrode recording area, spacing, etc).

True. We will add these details.

c) Stimulus presentation procedure: Are stimuli manually pipetted or delivered by apparatus with precise timing?

They are delivered manually. We will clarify this as well.

d) Data analysis, "we applied more permissive criteria involving response magnitude": it's not clear whether this is what's spelled out in the next paragraph, or whether that's left unspecified. In either case, the next paragraph appears to be about establishing a noise floor on pattern membership, not a "permissive criterion."

True, the next paragraph is not the explanation for the more permissive criteria. The more permissive criteria involving response magnitude are actually those described in Figure 3A and 3B. The sentence that was quoted above merely states that before applying those criteria, we had also searched for patterns defined by binary designation of neurons as responsive, or not responsive, to each of the stimuli (this is directly related to the next comment below). Using those binary definitions, we obtained a very small number of neurons for each pattern and thus decided to apply the approach actually used and described in the manuscript.

e) Data analysis, method for assessing significance: there's a lot to like about the use of pooling to estimate the baseline and the use of an ANOVA-like test to assess unit responsiveness.

But:

i) for a specific stimulus, at 4 trials (the minimum specified in "Stimulus presentation procedure") kruskalwallis is questionable. They state that most trials use 5, however, and that should be okay.

The number of cases with 4 trials is truly a minority, and we will provide the exact numbers in our revision.

ii) the methods statement suggests they are running kruskalwallis individually for each neuron/stimulus, rather than once per neuron across all stimuli. With 11 stimuli, there is a substantial chance of a false-positive if they used p < 0.05 to assess significance. (The actual threshold was unstated.) Were there any multiple comparison corrections performed? Or did they run kruskalwallis on the neuron, and then if significant assess individual stimuli? (Which is a form of multiple-comparisons correction.)

First, we indeed failed to mention that our criterion was 0.05. We will correct that in our revision. We did not apply any multiple comparison measures. We consider each neuron-stimulus pair as an independent entity, and we are aware that this leads to a higher false positive rate. On the other hand, applying multiple comparisons would be problematic, as we do not always use the same number of stimuli in different studies. Applying multiple comparison corrections would lead to different response criteria across different studies. Notably, most, if not all, of our conclusions involve comparisons across conditions, and for this purpose we think that our procedure is valid. We do not attach any special meaning to the significance threshold, but rather think of it as a basic criterion that allows us to exclude non-responsive neurons, and to compare frequencies of neurons that fulfill this criterion.

eLife Assessment

Pinho et al use in vivo calcium imaging and chemogenetic approaches to examine the involvement of hippocampal sub-regions across the different stages of a sensory preconditioning task in mice. They find convincing evidence for sensory preconditioning in male mice. They also find that, in these mice, CaMKII-positive neurons in the dorsal hippocampus: (1) encode the audio-visual association that forms in stage 1 of the task, and (2) retrieve/express sensory preconditioned fear to the auditory stimulus at test. These findings are supported by evidence that ranges from incomplete to convincing. The study will be valuable to researchers in the field of learning and memory.

Reviewer #1 (Public review):

Summary:

The study by Pinho et al. presents a novel behavioral paradigm for investigating higher-order conditioning in mice. The authors developed a task that creates associations between light and tone sensory cues, driving mediated learning. They observed sex differences in task acquisition, with females demonstrating faster-mediated learning compared to males. Using fiber photometry and chemogenetic tools, the study reveals that the dorsal hippocampus (dHPC) plays a central role in encoding mediated learning. These findings are crucial for understanding how environmental cues, which are not directly linked to positive/negative outcomes, contribute to associative learning. Overall, the study is well-designed, with robust results, and the experimental approach aligns with the study's objectives.

Strengths:

(1) The authors develop a robust behavioral paradigm to examine higher-order associative learning in mice.

(2) They discover a sex-specific component influencing mediated learning, with females exhibiting enhanced learning abilities.

(3) Using fiber photometry and chemogenetic techniques, the authors identify the dorsal hippocampus but not the ventral hippocampus, which plays a crucial for encoding mediated learning.

Weaknesses:

(1) The study would be strengthened by further elaboration on the rationale for investigating specific cell types within the hippocampus.

(2) The analysis of photometry data could be improved by distinguishing between early and late responses, as well as enhancing the overall presentation of the data.

(3) The manuscript would benefit from revisions to improve clarity and readability.

Reviewer #2 (Public review):

Summary:

Pinho et al. developed a new auditory-visual sensory preconditioning procedure in mice and examined the contribution of the dorsal and ventral hippocampus to learning in this task. Using photometry they observed activation of the dorsal and ventral hippocampus during sensory preconditioning and conditioning. Finally, the authors combined their sensory preconditioning task with DREADDs to examine the effect of inhibiting specific cell populations (CaMKII and PV) in the DH on the formation and retrieval/expression of mediated learning.

Strengths:

The authors provide one of the first demonstrations of auditory-visual sensory preconditioning in male mice. Research on the neurobiology of sensory preconditioning has primarily used rats as subjects. The development of a robust protocol in mice will be beneficial to the field, allowing researchers to take advantage of the many transgenic mouse lines. Indeed, in this study, the authors take advantage of a PV-Cre mouse line to examine the role of hippocampal PV cells in sensory preconditioning.

Weaknesses:

(1) The authors report that sensory preconditioning was observed in both male and female mice. However, their data only supports sensory preconditioning in male mice. In female mice, both paired and unpaired presentations of the light and tone in stage 1 led to increased freezing to the tone at test. In this case, fear to the tone could be attributed to factors other than sensory preconditioning, for example, generalization of fear between the auditory and visual stimulus.

(2) In the photometry experiment, the authors report an increase in neural activity in the hippocampus during both phase 1 (sensory preconditioning) and phase 2 (conditioning). In the subsequent experiment, they inhibit neural activity in the DH during phase 1 (sensory preconditioning) and the probe test, but do not include inhibition during phase 2 (conditioning). It was not clear why they didn't carry forward investigating the role of the hippocampus during phase 2 conditioning. Sensory preconditioning could occur due to the integration of the tone and shock during phase two, or retrieval and chaining of the tone-light-shock memories at test. These two possibilities cannot be differentiated based on the data. Given that we do not know at which stage the mediate learning is occurring, it would have been beneficial to additionally include inhibition of the DH during phase 2.

(3) In the final experiment, the authors report that inhibition of the dorsal hippocampus during the sensory preconditioning phase blocked mediated learning. While this may be the case, the failure to observe sensory preconditioning at test appears to be due more to an increase in baseline freezing (during the stimulus off period), rather than a decrease in freezing to the conditioned stimulus. Given the small effect, this study would benefit from an experiment validating that administration of J60 inhibited DH cells. Further, given that the authors did not observe any effect of DREADD inhibition in PV cells, it would also be important to validate successful cellular silencing in this protocol.