eLife assessment

This study presents valuable experimental and numerical results on the motility of a magnetotactic bacterium living in sedimentary environments, particularly in environments of varying magnetic field strengths. The evidence supporting the claims of the authors is solid, although the statistical significance comparing experiments with the numerical work is weak. The study will be of interest to biophysicists interested in bacterial motility.

Reviewer #1 (Public Review):

Summary:<br /> The authors present experimental and numerical results on the motility Magnetospirillum gryphiswaldense MSR-1, a magnetotactic bacterium living in sedimentary environments. The authors manufactured microfluidic chips containing three-dimensional obstacles of irregular shape, that match the statistical features of the grains observed in the sediment via micro-computer tomography. The bacteria are furthermore subject to an external magnetic field, whose intensity can be varied. The key quantity measured in the experiments is the throughput ratio, defined as the ratio between the number of bacteria that reach the end of the microfluidic channel and the number of bacteria entering it. The main result is that the throughput ratio is non-monotonic and exhibits a maximum at magnetic field strength comparable with Earth's magnetic field. The authors rationalize the throughput suppression at large magnetic fields by quantifying the number of bacteria trapped in corners between grains.

Strengths:<br /> While magnetotactic bacteria's general motility in bulk has been characterized, we know much less about their dynamics in a realistic setting, such as a disordered porous material. The micro-computer tomography of sediments and their artificial reconstruction in a microfluidic channel is a powerful method that establishes the rigorous methodology of this work. This technique can give access to further characterization of microbial motility. The coupling of experiments and computer simulations lends considerable strength to the claims of the authors, because the model parameters (with one exception) are directly measured in the experiments.

Weaknesses:<br /> The main weakness of the manuscript pertains to the discussion of the statistical significance of the experimental throughput ratio. Especially when comparing results at zero and 50 micro Tesla. The simulations seem to predict a stronger effect than seen in the experiments. The authors do not address this discrepancy.

Reviewer #2 (Public Review):

Summary:<br /> simulation study of magnetotactic bacteria in microfluidic channels containing sediment-mimicking obstacles. The obstacles were produced based on micro-computer tomography reconstructions of bacteria-rich sediment samples. The swimming of bacteria through these channels is found experimentally to display the highest throughput for physiological magnetic fields. Computer simulations of active Brownian particles, parameterized based on experimental trajectories are used to quantify the swimming throughput in detail. Similar behavior as in experiments is obtained, but also considerable variability between different channel geometries. Swimming at strong field is impeded by the trapping of bacteria in corners, while at weak fields the direction of motion is almost random. The trapping effect is confirmed in the experiments, as well as the escape of bacteria with reducing field strength.

Strengths:<br /> This is a very careful and detailed study, which draws its main strength from the fruitful combination of the construction of novel microfluidic devices, their use in motility experiments, and simulations of active Brownian particles adapted to the experiment. Based on their results, the authors hypothesize that magnetotactic bacteria may have evolved to produce magnetic properties that are adapted to the geomagnetic field in order to balance movement and orientation in such crowded environments. They provide strong arguments in favor<br /> of such a hypothesis.

Weaknesses:<br /> Some of the issues touched upon here have been studied also in other articles. It would be good to extend the list of references accordingly and discuss the relation briefly in the text.

eLife assessment

This important study integrates microfluidic experiments and mathematical modeling to investigate how flow dynamics and biofilm growth and detachment influence each other. Using Pseudomonas aeruginosa as a model organism, the study identifies several key effects and stages in biofilm development, albeit with some weaknesses in clearly defining the setup and some of their interpretations. The comparison between experimental results and theoretical models is convincing, providing a robust analysis of the biofilm's behavior under varying flow conditions. The findings will be helpful for researchers working on biofilms and their applications.

Reviewer #1 (Public Review):

Summary:<br /> The paper investigates the interplay between fluid flow and biofilm development using Pseudomonas aeruginosa PAO1 in microfluidic channels. By combining experimental observations with mathematical modeling, the study identifies the significant impact of nutrient limitation and hydrodynamic forces on biofilm growth and detachment. The authors demonstrate that nutrient limitation drives the longitudinal distribution of biomass, while flow-induced detachment influences the maximum clogging and temporal dynamics. The study highlights that pressure buildup plays a critical role in biofilm detachment, leading to cyclic episodes of sloughing and regrowth. A stochastic model is used to describe the detachment process, capturing the apparent randomness of sloughing events. The findings offer insights into biofilm behavior during clogging and fouling, potentially relevant to infections, environmental processes, and engineering applications.

Strengths:<br /> This paper demonstrates a strong integration of experimental work and mathematical modeling, providing a comprehensive understanding of biofilm dynamics in straight microfluidic channel. The simplicity of the microchannel geometry allows for accurate modeling, and the findings have the potential to be applied to more complex geometries. The detailed analysis of nutrient limitation and its impact on biofilm growth offers valuable insights into the conditions that drive biofilm formation. The model effectively describes biofilm development across different stages, capturing both initial growth and cyclic detachment processes. While cyclic pressure buildup has been studied previously, the incorporation of a stochastic model to describe detachment events is a novel and significant contribution, capturing the complexity and randomness of biofilm behavior. Finally, the investigation of pressure buildup and its role in cyclic detachment and regrowth enhances our understanding of the mechanical forces at play, making the findings applicable to a wide range of technological and clinical contexts.

Weaknesses:<br /> The study achieves its primary goal of integrating experiments and modeling to understand the coupling between flow and biofilm growth and detachment in a microfluidic channel, but it should have highlighted the weaknesses of the methods. I list the ones that, in my opinion, are the main ones:

• The study does not consider biofilm porosity, which could significantly affect the flow and forces exerted on the biofilm. Porosity could impact the boundary conditions, such as the no-slip condition, which should be validated experimentally.<br /> • The research suggests EPS development as a stage in biofilm growth but does not probe it using lectin staining. This makes it impossible to accurately assess the role of EPS in biofilm development and detachment processes.<br /> • While the force and flow are three-dimensional, the images are taken in two dimensions. The paper does not clearly explain how the 2D images are extrapolated to make 3D assessments, which could lead to inaccuracies.<br /> • Although the findings are tested using polysaccharide-deficient mutants, the results could have been analyzed in greater detail. A more thorough analysis would help to better understand the role of matrix composition on the stochastic model of detachment.

Reviewer #2 (Public Review):

This manuscript develops well-controlled microfluidic experiments and mathematical modelling to resolve how the temporal development of P. aeruginosa biofilms is shaped by ambient flow. The experiment considers a simple rectangular channel on which a constant flow rate is applied and UV LEDs are used to confine the biofilm to a relatively small length of device. While there is often considerable geometrical complexity in confined environments and feedback between biofilm/flow (e.g. in porous media), these simplified conditions are much more amenable to analysis. A non-dimensional mathematical model that considers nutrient transport, biofilm growth and detachment is developed and used to interpret experimental data. Regimes with both gradual detachment and catastrophic sloughing are considered. The concentration of nutrients in the media is altered to resolve the effect of nutrient limitation. In addition, the role of a couple of major polysaccharide EPS components are explored with mutants, which leads results in line with previous studies.

There has been a vast amount of experimental and modelling work done on biofilms, but relatively rarely are the two linked together so tightly as in this paper. Predictions on influence of the non-dimensional Damkohler number on the longitudinal distribution of biofilm and functional dependence of flow on the maximum amount of biofilm (phi_max) are demonstrated. The study reconfirms a number of previous works that showed the gradual detachment rate of biofilms scales with the square root of the shear stress. More challenging are the rapid biofilm detachment events where a large amount of biofilm is detached at once. These events occur are identified experimentally using an automated analysis pipeline and are fitted with probability distributions. The time between detachment events was fitted with a Gamma distribution and the amplitude of the detachment events was fitted with a log-normal distribution, however, it is not clear how good these fits are. Experimental data was then used as an input for a stochastic differential equation, but the output of this model is compared only qualitatively to that of the experiments. Overall, this paper does an admirable job of developing a well-constrained experiments and a tightly integrated mathematical framework through which to interpret them. However, the new insights this provides the underlying physical/biological mechanisms are relatively limited.

eLife assessment

This important study explores how cells maintain subcellular structures in the face of constant protein turnover, focusing on neurons, whose synapses must be kept stable over long periods of time for memory storage. Using proteins from knock-in mice expressing tagged variants of the synaptic scaffold protein PSD95, nanobodies, and multiple imaging methods, there is compelling evidence that PSD95 proteins form complexes at synapses in which single protein copies are sequentially replaced over time. This happens at different rates in different synapse types and is slowest in areas where PSD95 lifetime is the longest and long-term memories are stored. While of general relevance to cell biology, these findings are of particular interest to neuroscientists because they support the hypothesis put forward by Francis Crick that stable synapses, and hence stable long-term memories, can be maintained in the face of short protein lifetimes by sequential replacement of individual subunits in synaptic protein complexes.

Joint Public Review

The present study explored the principles that allow cells to maintain complex subcellular proteinaceous structures despite the limited lifetimes of the individual protein components. This is particularly critical in the case of neurons, where the size and protein composition of synapses define synaptic strength and encode memory.

PSD95 is an abundant synapse protein that acts as a scaffold in the recruitment of transmitter receptors and other signaling proteins and is required for memory formation. The authors used super-resolution microscopy to study PSD95 super-complexes isolated from the brains of mice expressing tagged PSD variants (Halo-Tag, mEos, GFP). Their results show compellingly that a large fraction (~25%) of super-complexes contains two PSD95 copies about 13 nm apart, that there is substantial turnover of PSD95 proteins in super-complexes over a period of seven days, and that ~5-20% of the super-complexes contain new and old PSD95 molecules. This percentage is higher in synaptic fractions as compared to total brain lysates, and highest in isocortex samples (~20%). These important findings support the hypothesis put forward by Crick that sequential subunit replacement gives synaptic super-complexes long lifetimes and thus aids in memory maintenance. Overall, this is a very interesting study that provides key insights into how synaptic protein complexes are formed and maintained. On the other hand, the actual role of these PSD95 super-complexes in long-term memory storage remains unknown. Specifically, a direct correlation between PSD95 stability and memory formation remains hypothetical - but the present findings indicate important new directions for studying the mechanisms that control postsynaptic protein organisation and the maintenance of postsynaptic proteinaceous substructures.

Strengths

(1) The study employed an appropriate and validated methodology.<br /> (2) Large numbers of PSD95 super-complexes from three different mouse models were imaged and analyzed, providing adequately powered sample sizes.<br /> (3) State-of-the-art super-resolution imaging techniques (PALM and MINFLUX) were used, providing a robust, high-quality, cross-validated analysis of PSD95 protein complexes that is useful for the community.<br /> (4) The result that PSD95 proteins in dimeric complexes are on average 12.7 nm apart is useful and has implications for studies on the nanoscale organization of PSD95 at synapses.<br /> (5) The finding that postsynaptic protein complexes can continue to exist while individual components are being renewed is important for our understanding of synapse maintenance and stability.<br /> (6) The data on the turnover rate of PSD95 in super-complexes from different brain regions provide a first indication of potentially meaningful differences in the lifetime of super-complexes between brain regions.

Weaknesses

(1) The manuscript emphasizes the hypothesis that stable super-complexes, maintained through sequential replacement of subunits, might underlie the long-term storage of memory. While an interesting idea, this notion requires considerably more research. The presented experimental data are indeed consistent with this notion, but there is no evidence that these complexes are causally related to memory storage.<br /> (2) Much of the presented work is performed on biochemically isolated protein complexes. The biochemical isolation procedures rely on physical disruption and detergents that are known to alter the composition and structure of complexes in certain cases. Thus, it remains unclear how the protein complexes described in this study relate to PSD95 complexes in intact synapses.<br /> (3) Because not all GFP molecules mature and fold correctly in vitro and the PSD95-mEos mice used were heterozygous, the interpretation of the corresponding quantifications is not straightforward.<br /> (4) It was not tested whether different numbers of PSD95 molecules per super-complex might contribute to different retention times of PSD95, e.g. in synaptic vs. total-forebrain super-complexes.<br /> (5) The conclusion that the population of 'mixed' synapses is higher in the isocortex than in other brain regions is not supported by statistical analysis.<br /> (6) The validity of conclusions regarding PSD95 degradation based on relative changes in the occurrence of SiR-Halo-positive puncta is limited.

Author response:

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

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

The work is well performed and thoroughly convincing. 

However, a few points could be improved, by adjusting the manuscript: 

(1) The wording of the abstract is confusing for the casual reader. The initial impression is that the 2-copy complexes contain the majority of the PSD95 copies. This is not the case, as shown in panel cii. It would be important for the authors to explain in the abstract the exact percentage of molecules found within 2-copy complexes. 

We have now amended the abstract, making it clear that it’s not most of the complexes.  

(2) Did the authors find a sizeable population of 2-copy complexes by investigating wild-type proteins, using nanobody labeling (Figure S2)? It would be important to quantify and discuss these data. 

It was not possible to perform this analysis on the wild-type proteins. The quantification would rely on all the PSD95 molecules being bound by the antibody, which we cannot guarantee. Furthermore, the nanobody labeling would need to be stoichiometric. 

(3) The authors quote the separation value of 12.7 nm throughout their text, including the abstract. This may be somewhat misleading since the authors investigate the PSD95-GFP molecules, labeled using anti-GFP nanobodies. The large size of the two GFP molecules (~3 nm), and that of the nanobodies, will influence the readout. Two groups have already reported a separation of ~7-8 nm between neighboring PSD95 molecules in synapses, using PSD95 nanobodies, to minimize the linkage

error: https://doi.org/10.1101/2022.08.03.502284 and https://doi.org/10.1101/2023.10.18.562 700  

The difference observed here is consistent with an effect of the additional GFP moieties; the authors should cite these works (albeit they are now only provided as biorXiv pre-prints) and should mention this discrepancy, and its potential tagging-related explanation. 

We have now referenced the work and referred to this in the discussion.

(4) The authors may want to re-check the manuscript; some minor problems should be corrected, such as the mislabeling of Figure 2 and "Figure 5". 

This has now been corrected.  

Reviewer #2 (Recommendations For The Authors): 

The authors suggest that the stability of the PSD95 dimeric complex correlates with memory formation. However, the turnover experiments were conducted only on three-month-old animals, which can be considered to be at a stage of lower synaptic functionality turnover. It would be appropriate to study dimer turnover during the memory formation period at three to four weeks of age, for example in comparison to the oldest mice. 

Alternatively, it might be interesting to study the turnover in the hippocampus following exposure to a memory test. 

Whilst potentially useful, these experiments are outside of the scope of this manuscript.   

It is not clear whether the different turnover identified in various brain areas is statistically significant, as apparently no statistical analysis has been conducted. 

The findings were significant, and the SI table containing the p-values has been emphasized further in the manuscript.  

Reviewer #3 (Recommendations For The Authors): 

(1) In the last paragraph of the Results section, it could be made clearer what the nature is of the correlation between PSD95 half-life and mixed supercomplexes to understand how to interpret this correlation. In the discussion, it is concluded that stable synapses have long protein lifetimes and slow replacement of scaffolding proteins. However, this is based on the correlation of protein lifetime and mixed supercomplexes in the cortex, which does not provide any evidence that this relation is true in single synapses or is specific for stable synapses. To make this statement, the authors could for instance directly correlate the stoichiometry of supercomplexes with the protein lifetime and size of individual synapses. 

Unfortunately, we can’t directly measure the lifetime of each complex, and so it’s only possible to compare region-to-region. In doing so, we found that there was a correlation between the protein lifetime and the “mixed” population.  

(2) Some essential parts seem missing: the materials and methods and Figure 2 are not included. Also, the numbering of figures is incorrect. Both in the figure legends and the text. 

This has been added. 

(3) Figure 1a could contain more details of the experimental procedures. For example, it could be made clearer how PSD95 supercomplexes are isolated from brain homogenate. 

This is now presents in the methods. 

(4) In Figure 1c, single molecules of PSD95 are identified using PALM with a resolution of 30 nm. However, in Figure 1d it is shown that PSD95 molecules reside on average 13 nm apart, indicating that a resolution of 30 nm is not sufficient to resolve single PSD95 molecules. In addition, it would be of interest to show the distribution of fluorophore separation (assessed with MINFLUX) of only the supercomplexes with two PSD95 molecules, since only these were used to calculate the average distance. 

The 13 nm distance was measured using MINFLUX, as stated in the text. The fluorophore separation distances are shown in Figure 1dii.

(5) In the introduction, the authors could be more explicit in their explanation of memory formation and storage and how the presented study contributes to that field. 

We thank the reviewer for the suggestion, but feel that such a discussion in the introduction would detract from the main points of the manuscript.  

(6) Throughout the manuscript the authors prominently cite their own work, but relevant literature on synaptic plasticity and synapse nanostructure (EM and super-resolution studies) is lacking. 

Further references have now been added.  

(7) The results depicted in Figure 4b would be easier to interpret if a stacked histogram (including error bars) was used. 

We agree that the data could be presented in such a way, but that would prevent the results from the biological repeats, along with the variation, being presented.

eLife assessment

This important study reports that a transcription factor stimulating mRNA synthesis can stabilize its target transcripts. The convincing results demonstrate, with multiple independent approaches, co-transcriptional binding, stabilization of a family of mRNAs, and cytoplasmic activities of the transcription factor Sfp1. The results lead to the conclusion that the co-transcriptional association of Sfp1 with specific transcripts is a critical step in the stabilization of such transcripts in the cytoplasm.

Reviewer #1 (Public Review):

This manuscript builds upon the authors' previous work on the cross-talk between transcription initiation and post-transcriptional events in yeast gene expression. These prior studies identified an mRNA 'imprinting' phenomenon linked to genes activated by the Rap1 transcription factor (TF), a surprising role for the Sfp1 TF in promoting RNA polymerase II (RNAPII) backtracking, and a role for the non-essential RNAPII subunits Rpb4/7 in the regulation of mRNA decay and translation. Here the authors aimed to extend these observations to provide a more coherent picture of the role of Sfp1 in transcription initiation and subsequent steps in gene expression. They provide evidence for (1) a physical interaction between Sfp1 and Rpb4, (2) Sfp1 binding and stabilization of mRNAs derived from genes whose promoters are bound by both Rap1 and Sfp1 and (3) an effect of Sfp1 on Rpb4 binding or conformation during transcription elongation.

Author response:

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

Public Reviews:

Reviewer #2 (Public Review):

Summary:

The manuscript by Kelbert et al. presents results on the involvement of the yeast transcription factor Sfp1 in the stabilisation of transcripts whose synthesis it stimulates. Sfp1 is known to affect the synthesis of a number of important cellular transcripts, such as many of those that code for ribosomal proteins. The hypothesis that a transcription factor can remain bound to the nascent transcript and affect its cytoplasmic half-life is attractive. However, the association of Sfp1 with cytoplasmic transcripts remains to be validated, as explained in the following comments:

A two-hybrid based assay for protein-protein interactions identified Sfp1, a transcription factor known for its effects on ribosomal protein gene expression, as interacting with Rpb4, a subunit of RNA polymerase II. Classical two-hybrid experiments depend on the presence of the tested proteins in the nucleus of yeast cells, suggesting that the observed interaction occurs in the nucleus. Unfortunately, the two-hybrid method cannot determine whether the interaction is direct or mediated by nucleic acids. The revised version of the manuscript now states that the observed interaction could be indirect.

To understand to which RNA Sfp1 might bind, the authors used an N-terminally tagged fusion protein in a cross-linking and purification experiment. This method identified 264 transcripts for which the CRAC signal was considered positive and which mostly correspond to abundant mRNAs, including 74 ribosomal protein mRNAs or metabolic enzyme-abundant mRNAs such as PGK1. The authors did not provide evidence for the specificity of the observed CRAC signal, in particular what would be the background of a similar experiment performed without UV cross-linking. This is crucial, as Figure S2G shows very localized and sharp peaks for the CRAC signal, often associated with over-amplification of weak signal during sequencing library preparation.

(1) To rule out possible PCR artifacts, we used a UMI (Unique Molecular Identifier) scan. UMIs are short, random sequences added to each molecule by the 5’ adapter to uniquely tag them. After PCR amplification and alignment to the reference genome, groups of reads with identical UMIs represent only one unique original molecule. Thus, UMIs allow distinguishing between original molecules and PCR duplicates, effectively eliminating the duplicates.

(2) Looking closely at the peaks using the IGV browser, we noticed that the reads are by no means identical. Each carrying a mutation [probably due to the cross-linking] in a different position and having different length. Note that the reads are highly reproducible in two replicate.

(3) CRAC+ genes do not all fall into the category of highly transcribed genes.  On the contrary, as depicted in Figure 6A (green dots), it is evident that CRAC+ genes exhibit a diverse range of Rpb3 ChIP and GRO signals. Furthermore, as illustrated in Figure 7A, when comparing CRAC+ to Q1 (the most highly transcribed genes), it becomes evident that the Rpb4/Rpb3 profile of CRAC+ genes is not a result of high transcription levels.

(4) Only a portion of the RiBi mRNAs binds Sfp1, despite similar expression of all RiBi.

(5) The CRAC+ genes represent a distinct group with many unique features. Moreover, many CRAC+ genes do not fall into the category of highly transcribed genes.

(6) The biological significance of the 262 CRAC+ mRNAs was demonstrated by various experiments; all are inconsistent with technical flaws. Some examples are:

a) Fig. 2a and B show that most reads of CRAC+ mRNA were mapped to specific location – close the pA sites.

b) Fig. 2C shows that most reads of CRAC+ mRNA were mapped to specific RNA motif.

c) Most RiBi CRAC+ promoter contain Rap1 binding sites (p= 1.9x10-22), whereas the vast majority of RiBi CRAC- promoters do not contain Rap1 binding site. (Fig. 3C).

d) Fig. 4A shows that RiBi CRAC+ mRNAs become destabilized due to Sfp1 deletion, whereas RiBi CRAC- mRNAs do not. Fig. 4B shows similar results due to

e) Fig. 6B shows that the impact of Sfp1 on backtracking is substantially higher for CRAC+ than for CRAC- genes. This is most clearly visible in RiBi genes.

f) Fig. 7A shows that the Sfp1-dependent changes along the transcription units is substantially more rigorous for CRAC+ than for CRAC-.

g) Fig. S4B Shows that chromatin binding profile of Sfp1 is different for CRAC+ and CRAC- genes

In a validation experiment, the presence of several mRNAs in a purified SFP1 fraction was measured at levels that reflect the relative levels of RNA in a total RNA extract. Negative controls showing that abundant mRNAs not found in the CRAC experiment were clearly depleted from the purified fraction with Sfp1 would be crucial to assess the specificity of the observed protein-RNA interactions (to complement Fig. 2D).

GPP1, a highly expressed genes, is not to be pulled down by Sfp1 (Fig. 2D). GPP1 (alias RHR2) was included in our Table S2 as one of the 264 CRAC+ genes, having a low CRAC value. However, when we inspected GPP1 results using the IGV browser, we realized that the few reads mapped to GPP1 are actually anti-sense to GPP1 (perhaps they belong to the neighboring RPL34B genes, which is convergently transcribed to GPP1) (see Fig. 1 at the bottom of the document). Thus, GPP1 is not a CRAC+ gene and would now serve as a control. See  We changed the text accordingly (see page 11 blue sentences). In light of this observation, we checked other CRAC genes and found that, except for ALG2, they all contain sense reads (some contain both sense and anti-sense reads). ALG2 and GPP1 were removed leaving 262 CRAC+ genes.

The CRAC-selected mRNAs were enriched for genes whose expression was previously shown to be upregulated upon Sfp1 overexpression (Albert et al., 2019). The presence of unspliced RPL30 pre-mRNA in the Sfp1 purification was interpreted as a sign of co-transcriptional assembly of Sfp1 into mRNA, but in the absence of valid negative controls, this hypothesis would require further experimental validation. Also, whether the fraction of mRNA bound by Sfp1 is nuclear or cytoplasmic is unclear.

Further experimental validation was provided in some of our figures (e.g., Fig. 5C, Fig. 3B).

We argue that Sfp1 binds RNA co-transcriptionally and accompanies the mRNA till its demise in the cytoplasm: Co-transcriptional binding is shown in: (I) a drop in the Sfp1 ChIP-exo signal that coincides with the position of Sfp1 binding site in the RNA (Fig. 5C), demonstrating a movement of Sfp1 from chromatin to the transcript, (II) the dependence of Sfp1 RNA-binding on the promoter (Fig. 3B) and binding of intron-containing RNA. Taken together these 3 different experiments demonstrate that Sfp1 binds Pol II transcript co-transcriptionally.  Association of Sfp1 with cytoplasmic mRNAs is shown in the following experiments: (I) Figure 2D shows that Sfp1 pulled down full length RNA, strongly suggesting that these RNA are mature cytoplasmic mRNAs. (II) mRNA encoding ribosomal proteins, which belong to the CRAC+ mRNAs group are degraded by Xrn1 in the cytoplasm (Bresson et al., Mol Cell 2020). The capacity of Sfp1 to regulates this process (Fig. 4A-D) is therefore consistent with cytoplasmic activity of Sfp1. (III) The effect of Sfp1 on deadenylation (Fig. 4D), a cytoplasmic process, is also consistent with cytoplasmic activity of Sfp1. 

To address the important question of whether co-transcriptional assembly of Spf1 with transcripts could alter their stability, the authors first used a reporter system in which the RPL30 transcription unit is transferred to vectors under different transcriptional contexts, as previously described by the Choder laboratory (Bregman et al. 2011). While RPL30 expressed under an ACT1 promoter was barely detectable, the highest levels of RNA were observed in the context of the native upstream RPL30 sequence when Rap1 binding sites were also present. Sfp1 showed better association with reporter mRNAs containing Rap1 binding sites in the promoter region. Removal of the Rap1 binding sites from the reporter vector also led to a drastic decrease in reporter mRNA levels. Co-purification of reporter RNA with Sfp1 was only observed when Rap1 binding sites were included in the reporter. Negative controls for all the purification experiments might be useful.

In the swapping experiment, the plasmid lacking RapBS serves as the control for the one with RapBS and vice versa (see Bregman et al., 2011). Remember, that all these contracts give rise to identical RNA. Indeed, RabBS affects both mRNA synthesis and decay, therefore the controls are not ideal. However, see next section.

More importantly, in Fig. 3B “Input” panel, one can see that the RNA level of “construct F” was higher than the level of “construct E”. Despite this difference, only the RNA encoded by construct E was detected in the IP panel. This clearly shows that the detection of the RNA was not merely a result of its expression level.

To complement the biochemical data presented in the first part of the manuscript, the authors turned to the deletion or rapid depletion of SFP1 and used labelling experiments to assess changes in the rate of synthesis, abundance and decay of mRNAs under these conditions. An important observation was that in the absence of Sfp1, mRNAs encoding ribosomal protein genes not only had a reduced synthesis rate, but also an increased degradation rate. This important observation needs careful validation,

Indeed, we do provide validations in Fig. 4C Fig. 4D Fig. S3A and during the revision we included an  additional validation as Fig. S3B. Of note, we strongly suspect that GRO is among the most reliable approaches to determine half-lives (see our response in the first revision letter).

As genomic run-on experiments were used to measure half-lives, and this particular method was found to give results that correlated poorly with other measures of half-life in yeast (e.g. Chappelboim et al., 2022 for a comparison). As an additional validation, a temperature shift to 42{degree sign}C was used to show that , for specific ribosomal protein mRNA, the degradation was faster, assuming that transcription stops at that temperature. It would be important to cite and discuss the work from the Tollervey laboratory showing that a temperature shift to 42{degree sign}C leads to a strong and specific decrease in ribosomal protein mRNA levels, probably through an accelerated RNA degradation (Bresson et al., Mol Cell 2020, e.g. Fig 5E).

This was cited. Thank you. 

Finally, the conclusion that mRNA deadenylation rate is altered in the absence of Sfp1, is difficult to assess from the presented results (Fig. 3D).

This type of experiment was popular in the past. The results in the literature are similar to ours (in fact, ours are nicer). Please check the papers cited in our MS and a number of papers by Roy Parker.

The effects of SFP1 on transcription were investigated by chromatin purification with Rpb3, a subunit of RNA polymerase, and the results were compared with synthesis rates determined by genomic run-on experiments. The decrease in polII presence on transcripts in the absence of SFP1 was not accompanied by a marked decrease in transcript output, suggesting an effect of Sfp1 in ensuring robust transcription and avoiding RNA polymerase backtracking. To further investigate the phenotypes associated with the depletion or absence of Sfp1, the authors examined the presence of Rpb4 along transcription units compared to Rpb3. An effect of spf1 deficiency was that this ratio, which decreased from the start of transcription towards the end of transcripts, increased slightly. To what extent this result is important for the main message of the manuscript is unclear.

Suggestions: a) please clearly indicate in the figures when they correspond to reanalyses of published results.

This was done.

b) In table S2, it would be important to mention what the results represent and what statistics were used for the selection of "positive" hits. 

This was discussed in the text.

Strengths:

- Diversity of experimental approaches used.

- Validation of large-scale results with appropriate reporters.

Weaknesses:

- Lack of controls for the CRAC results and lack of negative controls for the co-purification experiments that were used to validate specific mRNA targets potentially bound by Sfp1.

- Several conclusions are derived from complex correlative analyses that fully depend on the validity of the aforementioned Sfp1-mRNA interactions.

We hope that our responses to Reviewer 2's thoughtful comments have rulled out concerns regarding the lack of controls.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Please review the text for spelling errors. While not mandatory, wig or begraph files for the CRAC results would be very useful for the readers.

Author response image 1.

A snapshot of IGV GPP1 locus showing that all the reads are anti-sense (pointing at the opposite direction of the gene (the gene arrows [white arrows over blue, at the bottom] are pointing to the right whereas the reads’ orientations are pointing to the left).

Author response:

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

The concerns raised during the review have been incorporated into the discussion of the results, and the need for further research is acknowledged in the paper. This is not possible in the present study, as the clinical project has been completed and further patients cannot be enrolled without starting a new project. We are confident that the results are scientifically valid and that the methodology was scientifically sound and up to date. They were obtained on a dataset that was obviously large enough to allow 20% of it to be set aside and a machine-learned classifier to be trained on the remaining 80%, which then assigned samples to neuropathy with an accuracy better than guessing.

Furthermore, our results are at least tentatively replicated in a completely independent data set from another patient cohort. The strengths and limitations of the study design, in particular the latter, are discussed in the necessary depth. In summary, the machine-learned results provided major hits on one side and probably unimportant lipids on the other side of the variable importance scale. Both could be verified in vitro. We are therefore confident that we have contributed to the advancement of knowledge about cancer therapy-associated neuropathy and look forward to further developments in this area.

---

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

Weaknesses Reviewer 1: 

There are a number of weaknesses in the study. The small sample size is a significant limitation of the study. Out of 31 patients, only 17 patients were reported to develop neuropathy, with significant neuropathy (grade 2/3) in only 5 patients. The authors acknowledge this limitation in the results and discussion sections of the manuscript, but it limits the interpretation of the results. Also acknowledged is the limited method used to assess neuropathy. 

We agree with the reviewer that the cohort size and assessment of neuropathy are limitations of our study as we already described in the corresponding section of the manuscript. However, occurrence and grade of the neuropathy are in line with results reported from previous studies. From these studies, the expected occurrence of neuropathy with our therapeutic regimen is around 50-70% (54.9% in our cohort), and most patients (80-90%) are expected to experience Grade 1 neuropathy after 12 weeks (13). In these studies, neuropathy is assessed by using questionnaires or by grading via NCTCTCAE as in our study. In summary, assessment and occurrence of neuropathy of our reported cohort are in line with previous reports.

Potentially due to this small number of patients with neuropathy, the machine learning algorithms could not distinguish between samples with and without neuropathy. Only selected univariate analyses identified differences in lipid profiles potentially related to neuropathy.  

The data analysis consistently followed a "mixture of experts" approach, as this seems to be the most successful way to deal with omics data. We have elaborated on this in the Methods section, including several supporting references. Regarding the quoted sentence from the results section, after rereading it, we realized that it was somewhat awkwardly worded. What we mean is now better worded in the results section, namely “Although the three algorithms detected neuropathy in new cases, unseen during training, at balanced accuracy of up to 0.75, while only the guess level of 0.5 was achieved when using permuted data for training, the 95% CI of the performance measures was not separated from guess level”. Therefore, multivariate feature selection was not considered a valid approach, since it requires that the algorithms from which the feature importance is read can successfully perform their task of class assignment (4). Therefore, univariate methods (Cohen's d, FPR, FWE) were preferred, as well as a direct hypothesis transfer of the top hits from the abovementioned day1/2 assessments to neuropathy. Classical statistics consisting of direct group comparisons using Kruskal-Wallis tests (5) were performed.” 

It was our approach to investigate the data set in an unbiased manner by different machine learning algorithms and select those lipids that the majority of the algorithms considered important for distinguishing the patient groups (majority voting). This way, the inconsistencies and limitations of a single evaluation method, such as regression analysis, that occur in some datasets, can be mitigated. 

Three sphingolipid mediators including SA1P differed between patients with and without neuropathy at the end of treatment. These sphingolipids were elevated at the end of treatment in the cohort with neuropathy, relative to those without neuropathy. However, across all samples from pre to post-paclitaxel treatment, there was a significant reduction in SA1P levels. It is unclear from the data presented what the underlying mechanism for this result would be. 

We agree with the reviewer that our study does not identify the mechanism by which paclitaxel treatment alters sphingolipid concentrations in the plasma of patients. It has been reported before that paclitaxel may increase expression and activity of serine palmitoyltransferase (SPT) which is the crucial enzyme and rate-limiting step in the denovo synthesis of sphingolipids. This may be associated with a shift towards increased synthesis of 1-deoxysphingolipids and a decrease of “classical” sphingolipids (6) and may explain the general reduction of SA1P and other sphingolipid levels after paclitaxel treatment in our study. 

It is also conceivable that paclitaxel reduces the release of sphingolipids into the plasma. Paclitaxel is a microtubule stabilizing agent (7) that may interfere with intracellular transport processes and release of paracrine mediators. 

The mechanistic details of paclitaxel involvement in sphingolipid metabolism or transport are highly interesting but identifying them is beyond the scope of our manuscript.

If elevated SA1P is associated with neuropathy development, it would be expected to increase in those who develop neuropathy from pre to post-treatment time points. 

There is a general trend of reduced plasma SA1P concentrations following paclitaxel treatment. Nevertheless, patients experiencing neuropathy exhibit significantly elevated SA1P levels post-treatment. 

It has been shown before that paclitaxel-induced neuropathic pain requires activation of the S1P1 receptor in a preclinical study (8). Moreover, a meta-analysis of genome-wide association studies (GWAS) from two clinical cohorts identified multiple regulatory elements and increased activity of S1PR1 associated with paclitaxel-induced neuropathy (9). These data imply that enhanced S1P receptor activity and signaling are key drivers of paclitaxel-induced neuropathy. It seems that both, increased levels of the sphingolipid ligands in combination with enhanced expression and activity of S1P receptors can potentiate paclitaxel-induced neuropathy in patients. This explains why also decreased SA1P concentrations after paclitaxel treatment can still enhance neuropathy via the S1PRTRPV1 axis in sensory neurons.

We added this paragraph to the discussions section of our manuscript.

Primary sensory neuron cultures were used to examine the effects of SA1P application.

SA1P application produced calcium transients in a small proportion of sensory neurons. It is not clear how this experimental model assists in validating the role of SA1P in neuropathy development as there is no assessment of sensory neuron damage or other hallmarks of peripheral neuropathy. These results demonstrate that some sensory neurons respond to SA1P and that this activity is linked to TRPV1 receptors. However, further studies will be required to determine if this is mechanistically related to neuropathy.

As we detected elevated levels of SA1P in the plasma of PIPN patients, we can assume higher concentrations in the vicinity of sensory neurons. These neurons are the main drivers for neuropathy and neuropathic pain and are strongly affected by paclitaxel in their activity (10-15). Also, TRPV1 shows altered activity patterns in response to paclitaxel treatment (16). Because of its relevance for nociception and pathological pain, TRPV1 activity is a suitable and representative readout for pathological pain states in peripheral sensory neurons (17, 18), which is why we investigated them.

We would like to point out the potency of SA1P to increase capsaicin-induced calciumtransients in sensory neurons at submicromolar concentrations. 

We also agree with the reviewer that further studies need to investigate the underlying mechanisms in more detail. We added this sentence to the final paragraph in the discussion section of our manuscript.

Weaknesses Reviewer 2: 

The article is poorly written, hindering a clear understanding of core results. While the study's goals are apparent, the interpretation of sphingolipids, particularly SA1P, as key mediators of paclitaxel-induced neuropathy lacks robust evidence. 

We agree that the relevance of SA1P as key mediator of paclitaxel-induced neuropathy might be overstated and changed the wording throughout the manuscript accordingly. However, we would like to point out the potency of this lipid to increase capsaicin-induced calcium-transients in sensory neurons at submicromolar concentrations. 

Also, the lipid signature in the plasma of PIPN patients shows a unique pattern and sphingolipids are the group that showed the strongest alterations when comparing the patient groups. We also measured eicosanoids, such as prostaglandins, linoleic acid metabolites, endocannabinoids and other lipid groups that have previously been associated with influences on pain perception or nociceptor sensitization. However, none of these lipids showed significant differences in their concentrations in patient plasma. This is why we consider sphingolipids as contributors to or markers of paclitaxel-induced neuropathy in patients.

We also revised the entire article to improve its clarity.

The introduction fails to establish the significance of general neuropathy or peripheral neuropathy in anticancer drug-treated patients, and crucial details, such as the percentage of patients developing general neuropathy or peripheral neuropathy, are omitted. This omission is particularly relevant given that only around 50% of patients developed neuropathy in this study, primarily of mild Grade 1 severity with negligible symptoms, contradicting the study's assertion of CIPN as a significant side effect. 

As we already described in the introduction, CIPN is a serious dose- and therapy-limiting side effect, which affects up to 80% of treated patients. This depends on dose and combination of chemotherapeutic agents. For paclitaxel, therapeutic doses range from 80 – 225 mg/m². As CIPN symptoms are dose-dependent, the number of PIPN patients that receive a high paclitaxel dose is higher than the number of PIPN patient receiving a low dose.

In our study, we mainly used a low dose paclitaxel, because this therapeutic regimen is the most widely used paclitaxel monotherapy. From previous studies, the expected occurrence of neuropathy with this therapeutic regimen is around 50-70%, and most patients (8090%) are expected to experience Grade 1 neuropathy after 12 weeks (1-3).

Our results are within the range reported by these studies (54.9% patients with neuropathy). Also, as we highlight in Table S1, the neuropathy symptoms persist in most cases for several years after chemotherapy, affecting quality of life of these patients which makes it far from being a negligible symptom.

We added some more information concerning PIPN in the introduction section in which we emphasize the clinical problem.

The lack of clarity in distinguishing results obtained by lipidomics using machine learning methods and conventional methods adds to the confusion. The poorly written results section fails to specify SA1P's downregulation or upregulation, and the process of narrowing down to sphingolipids and SA1P is inadequately explained. 

We have tried to keep the machine learning part in the main manuscript short and moved major parts of it to a supplement. However, as this has been claimed to have led to a lack of clarity, we have expanded the description of the data analysis and added extensive explanations and supporting references for the mixed expert approach that was used throughout the analysis. We hope this is now clear.

Integrating a significant portion of the discussion section into the results section could enhance clarity. An explanation of the utility of machine learning in classifying patient groups over conventional methods and the citation of original research articles, rather than relying on review articles, may also add clarity to the usefulness of the study. 

As suggested by the reviewer, we moved the relevant parts from the discussion to the results section in the revised version of our manuscript.

Reviewer #1 (Recommendations For The Authors): 

Figure 2 should be better explained or removed. In its current form, it does not add to the interpretation of the manuscript.  

As mentioned above, we have expanded the description of the ESOM/U-matrix method in the Methods section and rewritten the figure legend. In addition, we have annotated the U-matrix in the figure. The method has been reported extensively in the computer science and biomedical literature, and a more detailed description in the referenced papers would go beyond the current focus on lipidomics. However, we believe that this discussion is sufficiently detailed for the readers of this report: "… a second unsupervised approach was used to verify the agreement between the lipidomics data structure and the prior classification, implemented as self-organizing maps (SOM) of artificial neurons (19). In the special form of an “emergent” SOM (ESOM (20)), the present map consisted of 4,000 neurons arranged on a two-dimensional toroidal grid with 50 rows and 80 columns (21, 22). ESOM was used because it has been repeatedly shown to correctly detect subgroup structures in biomedical data sets comparable to the present one (20, 22, 23). The core principle of SOM learning is to adjust the weights of neurons based on their proximity to input data points. In this process, the best matching unit (BMU) is identified as the neuron closest to a given data point. The adaptation of the weights is determined by a learning rate (η) and a neighborhood function (h), both of which gradually decrease during the learning process. Finally, the groups are projected onto separate regions of the map. On top of the trained ESOM, the distance structure in the high-dimensional feature space was visualized in the form of a so-called U-matrix (24) which is the canonical tool for displaying the distance structures of input data on ESOM (21). 

The visual presentation facilitates data group separation by displaying the distances between BMUs in high-dimensional space in a color-coding that uses a geographical map analogy, where large "heights" represent large distances in feature space, while low "valleys" represent data subsets that are similar. "Mountain ranges" with "snow-covered" heights visually separate the clusters in the data. Further details about ESOM can be found in (24)."

The second patient cohort is only included in the discussion - with cohort details in the supplementary material and figures included in the main text. Perhaps these data should be removed entirely. The findings are described as trends and not statistically significant and multiple issues with this second cohort are mentioned in the discussion. 

We agree with the reviewer that including the second patient cohort in the discussion is inadequate. Of course, there are differences between the patient cohorts that do not allow direct comparison and that are highlighted in the section on limitations of the study. However, we still think it is interesting and relevant to show these data, because we used our algorithms trained on the first patient cohort to analyze the second cohort. And these data support the main results. 

We therefore moved the entire paragraph to the results section of to improve coherence of our manuscript. The passage was introduced with the subheading:  “Support of the main results in an independent second patient cohort”.

The title does not reflect the content of the paper and should be changed to better reflect the content and its significance. 

We change the title to “Machine learning and biological validation identify sphingolipids as potential mediators of paclitaxel-induced neuropathy in cancer patients” to avoid overstating the results as suggested by the Reviewer.

Further, the discussion should be modified to avoid overstating the results. 

As the reviewer suggests, we changed the wording to avoid overstating the results. 

Reviewer #2 (Recommendations For The Authors): 

Please address the absence of clear neuropathy in the majority of patients after treatment with paclitaxel in your discussion. 

As stated above, occurrence and grade of the neuropathy are in line with the results from previous studies. From these studies, the expected occurrence of neuropathy with our therapeutic regimen is around 50-70%, (the variability is due to differences in the assessment methods) and most patients (80-90%) are expected to experience Grade 1 neuropathy after 12 weeks (1-3). 

We added this information in the discussion section of the revised manuscript.

Line 65: Kindly replace review articles with original research articles for proper citation. 

We replaced the review articles with original publications, focusing on clinical observations. We added the following publications: Jensen et al., Front Neurosci 2020; Chen et al., Neurobiol Aging 2018; Igarashi et al., J Alzheimers Dis. 2011; Kim et al., Oncotarget 2017 as references 17-20 in the revised version of our manuscript.

Line 260: The mention of SA1P is introduced here without prior reference (do not use words like "again", or "see above", if it is not previously mentioned). Adjust the text for coherence.

We agree with the reviewer that the introduction of SA1P in this passage in incoherent. We replaced the sentence in line 260 with: 

The small set of lipid mediators emerging from all three methods as informative for neuropathy included the sphingolipid sphinganine-1-phosphate (SA1P), also known as dihydrosphingosine-1-phosphate (DH-S1P)…”

Lines 301-315: Consider relocating several lines from this section to the results section for improved clarity. 

We moved the lines 309-312 explaining the algorithm selection and their validation success in the corresponding results section (Lipid mediators informative for assigning postpaclitaxel therapy samples to neuropathy).

Lines 382-396: Move this content to the results section to enhance the organization and coherence of the manuscript. 

We moved the entire paragraph to the results section of our manuscript to improve coherence. The passage was introduced with the subheading:  “Support of the main results in an independent second patient cohort”.

References

(1) Barginear M, Dueck AC, Allred JB, Bunnell C, Cohen HJ, Freedman RA, et al. Age and the Risk of Paclitaxel-Induced Neuropathy in Women with Early-Stage Breast Cancer (Alliance A151411): Results from 1,881 Patients from Cancer and Leukemia Group B (CALGB) 40101. Oncologist. 2019;24(5):617-23.

(2) Mauri D, Kamposioras K, Tsali L, Bristianou M, Valachis A, Karathanasi I, et al. Overall survival benefit for weekly vs. three-weekly taxanes regimens in advanced breast cancer: A metaanalysis. Cancer Treat Rev. 2010;36(1):69-74.

(3) Budd GT, Barlow WE, Moore HC, Hobday TJ, Stewart JA, Isaacs C, et al. SWOG S0221: a phase III trial comparing chemotherapy schedules in high-risk early-stage breast cancer. J Clin Oncol. 2015;33(1):58-64.

(4) Lötsch J, and Ultsch A. Pitfalls of Using Multinomial Regression Analysis to Identify ClassStructure-Relevant Variables in Biomedical Data Sets: Why a Mixture of Experts (MOE) Approach Is Better. BioMedInformatics. 2023;3(4):869-84.

(5) Kruskal WH, and Wallis WA. Use of Ranks in One-Criterion Variance Analysis. J Am Stat Assoc. 1952;47(260):583-621.

(6) Kramer R, Bielawski J, Kistner-Griffin E, Othman A, Alecu I, Ernst D, et al. Neurotoxic 1deoxysphingolipids and paclitaxel-induced peripheral neuropathy. FASEB J. 2015;29(11):4461-72.

(7) Field JJ, Diaz JF, and Miller JH. The binding sites of microtubule-stabilizing agents. Chem Biol. 2013;20(3):301-15.

(8) Janes K, Little JW, Li C, Bryant L, Chen C, Chen Z, et al. The development and maintenance of paclitaxel-induced neuropathic pain require activation of the sphingosine 1-phosphate receptor subtype 1. J Biol Chem. 2014;289(30):21082-97.

(9) Chua KC, Xiong C, Ho C, Mushiroda T, Jiang C, Mulkey F, et al. Genomewide Meta-Analysis Validates a Role for S1PR1 in Microtubule Targeting Agent-Induced Sensory Peripheral Neuropathy. Clin Pharmacol Ther. 2020;108(3):625-34.

(10) Kawakami K, Chiba T, Katagiri N, Saduka M, Abe K, Utsunomiya I, et al. Paclitaxel increases high voltage-dependent calcium channel current in dorsal root ganglion neurons of the rat. J Pharmacol Sci. 2012;120(3):187-95.

(11) Pittman SK, Gracias NG, Vasko MR, and Fehrenbacher JC. Paclitaxel alters the evoked release of calcitonin gene-related peptide from rat sensory neurons in culture. Exp Neurol. 2013.

(12) Luo H, Liu HZ, Zhang WW, Matsuda M, Lv N, Chen G, et al. Interleukin-17 Regulates NeuronGlial Communications, Synaptic Transmission, and Neuropathic Pain after Chemotherapy.

Cell reports. 2019;29(8):2384-97 e5.

(13) Pease-Raissi SE, Pazyra-Murphy MF, Li Y, Wachter F, Fukuda Y, Fenstermacher SJ, et al. Paclitaxel Reduces Axonal Bclw to Initiate IP3R1-Dependent Axon Degeneration. Neuron. 2017;96(2):373-86 e6.

(14) Duggett NA, Griffiths LA, and Flatters SJL. Paclitaxel-induced painful neuropathy is associated with changes in mitochondrial bioenergetics, glycolysis, and an energy deficit in dorsal root ganglia neurons. Pain. 2017.

(15) Li Y, Adamek P, Zhang H, Tatsui CE, Rhines LD, Mrozkova P, et al. The Cancer Chemotherapeutic Paclitaxel Increases Human and Rodent Sensory Neuron Responses to TRPV1 by Activation of TLR4. J Neurosci. 2015;35(39):13487-500.

(16) Hara T, Chiba T, Abe K, Makabe A, Ikeno S, Kawakami K, et al. Effect of paclitaxel on transient receptor potential vanilloid 1 in rat dorsal root ganglion. Pain. 2013;154(6):882-9.

(17) Jardin I, Lopez JJ, Diez R, Sanchez-Collado J, Cantonero C, Albarran L, et al. TRPs in Pain Sensation. Front Physiol. 2017;8:392.

(18) Julius D. TRP Channels and Pain. Annual review of cell and developmental biology.

2013;29:355-84.

(19) Kohonen T. Self-Organized Formation of Topologically Correct Feature Maps. Biol Cybern. 1982;43(1):59-69.

(20) Lötsch J, Lerch F, Djaldetti R, Tegder I, and Ultsch A. Identification of disease-distinct complex biomarker patterns by means of unsupervised machine-learning using an interactive R toolbox (Umatrix). Big Data Analytics. 2018;3(1):5.

(21) Ultsch A. 2003.

(22) Lotsch J, Geisslinger G, Heinemann S, Lerch F, Oertel BG, and Ultsch A. Quantitative sensory testing response patterns to capsaicin- and ultraviolet-B-induced local skin hypersensitization in healthy subjects: a machine-learned analysis. Pain. 2018;159(1):11-24.

(23) Lötsch J, Thrun M, Lerch F, Brunkhorst R, Schiffmann S, Thomas D, et al. Machine-Learned Data Structures of Lipid Marker Serum Concentrations in Multiple Sclerosis Patients Differ from Those in Healthy Subjects. Int J Mol Sci. 2017;18(6).

(24) Lötsch J, and Ultsch A. Cham: Springer International Publishing; 2014:249-57.

eLife assessment

The manuscript presents a potentially important strategy to stimulate mammalian Müller glia to proliferate in vivo by manipulating cell cycle components. The findings are likely to appeal to retinal specialists and neuroscientists in general. However, the evidence that these cells become neurogenic is lacking/incomplete, suggesting that additional barriers exist to stimulate the regeneration of retinal neurons.

Reviewer #1 (Public Review):

Summary:

In this manuscript, Wu et al. introduce a novel approach to reactivate the Muller glia cell cycle in the mouse retina by simultaneously reducing p27Kip1 and increasing cyclin D1 using a single AAV vector. The approach effectively promotes Muller glia proliferation and reprograming without disrupting retinal structure or function. Interestingly, reactivation of the Muller glia cell cycle downregulates IFN pathway, which may contribute to the induced retinal regeneration. The results presented in this manuscript may offer a promising approach for developing Müller glia cell-mediated regenerative therapies for retinal diseases.

Strengths:

The data are convincing and supported by appropriate, validated methodology. These results are both technically and scientifically exciting and are likely to appeal to retinal specialists and neuroscientists in general.

Weaknesses:

There are some data gaps that need to be addressed.

(1) Please label the time points of AAV injection, EdU labeling, and harvest in Figure 1B.

(2) What fraction of Müller cells were transduced by AAV under the experimental conditions?

(3) It seems unusually rapid for MG proliferation to begin as early as the third day after CCA injection. Can the authors provide evidence for cyclin D1 overexpression and p27 Kip1 knockdown three days after CCA injection?

(4) The authors reported that MG proliferation largely ceased two weeks after CCA treatment. While this is an interesting finding, the explanation that it might be due to the dilution of AAV episomal genome copies in the dividing cells seems far-fetched.

Reviewer #2 (Public Review):

This manuscript by Wu, Liao et al. reports that simultaneous knockdown of P27Kip1 with overexpression of Cyclin D can stimulate Muller glia to re-enter the cell cycle in the mouse retina. There is intense interest in reprogramming mammalian muller glia into a source for neurogenic progenitors, in the hopes that these cells could be a source for neuronal replacement in neurodegenerative diseases. Previous work in the field has shown ways in which mouse Muller glia can be neurogenically reprogrammed and these studies have shown cell cycle re-entry prior to neurogenesis. In other works, typically, the extent of glial proliferation is limited, and the authors of this study highlight the importance of stimulating large numbers of Muller glia to re-enter the cell cycle with the hopes they will differentiate into neurons. While the evidence for stimulating proliferation in this study is convincing, the evidence for neurogenesis in this study is not convincing or robust, suggesting that stimulating cell cycle-reentry may not be associated with increasing regeneration without another proneural stimulus.

Below are concerns and suggestions.

Intro:

(1) The authors cite past studies showing "direct conversion" of MG into neurons. However, these studies (PMID: 34686336; 36417510) show EdU+ MG-derived neurons suggesting cell cycle re-entry does occur in these strategies of proneural TF overexpression.

(2) Multiple citations are incorrectly listed, using the authors first name only (i.e. Yumi, et al; Levi, et al;). Studies are also incompletely referenced in the references.

Figure 1:<br /> (3) When are these experiments ending? On Figure 1B it says "analysis" on the end of the paradigm without an actual day associated with this. This is the case for many later figures too. The authors should update the paradigms to accurately reflect experimental end points.

(4) Are there better representative pictures between P27kd and CyclinD OE, the EdU+ counts say there is a 3 fold increase between Figure 1D&E, however the pictures do not reflect this. In fact, most of the Edu+ cells in Figure 1E don't seem to be Sox9+ MG but rather horizontally oriented nuclei in the OPL that are likely microglia.

(5) Is the infection efficacy of these viruses different between different combinations (i.e. CyclinD OE vs. P27kd vs. control vs. CCA combo)? As the counts are shown in Figure 1G only Sox9+/Edu+ cells are shown not divided by virus efficacy. If these are absolute counts blind to where the virus is and how many cells the virus hits, if the virus efficacy varies in efficiency this could drive absolute differences that aren't actually biological.

(6) According to the Jax laboratories, mice aren't considered aged until they are over 18months old. While it is interesting that CCA treatment does not seem to lose efficacy over maturation I would rephrase the findings as the experiment does not test this virus in aged retinas.

(7) Supplemental Figure 2c-d. These viruses do not hit 100% of MG, however 100% of the P27Kip staining is gone in the P27sh1 treatment, even the P27+ cell in the GCL that is likely an astrocyte has no staining in the shRNA 1 picture. Why is this?

Figure 2<br /> (8) Would you expect cells to go through two rounds of cell cycle in such a short time? The treatment of giving Edu then BrdU 24 hours later would have to catch a cell going through two rounds of division in a very short amount of time. Again the end point should be added graphically to this figure.

Figure 3<br /> (9) I am confused by the mixing of ratios of viruses to indicate infection success. I know mixtures of viruses containing CCA or control GFP or a control LacZ was injected. Was the idea to probe for GFP or LacZ in the single cell data to see which cells were infected but not treated? This is not shown anywhere?

(10) The majority of glia sorted from TdTomato are probably not infected with virus. Can you subset cells that were infected only for analysis? Otherwise it makes it very hard to make population judgements like Figure 3E-H if a large portion are basically WT glia.

(11) Figure 3C you can see Rho is expressed everywhere which is common in studies like this because the ambient RNA is so high. This makes it very hard to talk about "Rod-like" MG as this is probably an artifact from the technique. Most all scRNA-seq studies from MG-reprogramming have shown clusters of "rods" with MG hybrid gene expression and these had in the past just been considered an artifact.

(12) It is mentioned the "glial" signature is downregulated in response to CCA treatment. Where is this shown convincingly? Figure H has a feature plot of Glul , which is not clear it is changed between treatments. Otherwise MG genes are shown as a function of cluster not treatment.

Figure 4<br /> (13) The authors should be commended for being very careful in their interpretations. They employ the proper controls (Er-Cre lineage tracing/EdU-pulse chasing/scRNA-seq omics) and were very careful to attempt to see MG-derived rods. This makes the conclusion from the FISH perplexing. The few puncta dots of Rho and GNAT in MG are not convincing to this reviewer, Rho and GNAT dots are dense everywhere throughout the ONL and if you drew any random circle in the ONL it would be full of dots. The rigor of these counts also comes into question because some dots are picked up in MG in the INL even in the control case. This is confusing because baseline healthy MG do not express RNA-transcripts of these Rod genes so what is this picking up? Taken together, the conclusion that there are Rod-like MG are based off scRNA-seq data (which is likely ambient contamination) and these FISH images. I don't think this data warrants the conclusion that MG upregulate Rod genes in response to CCA.

Figure 5<br /> (14) Similar point to above but this Glul probe seems odd, why is it throughout the ONL but completely dark through the IPL, this should also be in astrocytes can you see it in the GCL? These retinas look cropped at the INL where below is completely black. The whole retinal section should be shown. Antibodies exist to GS that work in mouse along with many other MG genes, IHC or western blots could be done to better serve this point.

Figure 6<br /> (15) Figure 6D is not a co-labeled OTX2+/ TdTomato+ cell, Otx2 will fill out the whole nucleus as can be seen with examples from other MG-reprogramming papers in the field (Hoang, et al. 2020; Todd, et al. 2020; Palazzo, et al. 2022). You can clearly see in the example in Figure 6D the nucleus extending way beyond Otx2 expression as it is probably overlapping in space. Other examples should be shown, however, considering less than 1% of cells were putatively Otx2+, the safer interpretation is that these cells are not differentiating into neurons. At least 99.5% are not.

(16) Same as above Figure 6I is not convincingly co-labeled HuC/D is an RNA-binding protein and unfortunately is not always the clearest stain but this looks like background haze in the INL overlapping. Other amacrine markers could be tested, but again due to the very low numbers, I think no neurogenesis is occurring.

(17) In the text the authors are accidently referring to Figure 6 as Figure 7.

Figure 7<br /> (18) I like this figure and the concept that you can have additional MG proliferating without destroying the retina or compromising vision. This is reminiscent of the chick MG reprogramming studies in which MG proliferate in large numbers and often do not differentiate into neurons yet still persist de-laminated for long time points.

General:<br /> (19) The title should be changed, as I don't believe there is any convincing evidence of regeneration of neurons. Understanding the barriers to MG cell-cycle re-entry are important and I believe the authors did a good job in that respect, however it is an oversell to report regeneration of neurons from this data.

(20) This paper uses multiple mouse lines and it is often confusing when the text and figures switch between models. I think it would be helpful to readers if the mouse strain was added to graphical paradigms in each figure when a different mouse line is employed.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, Wu et al. introduce a novel approach to reactivate the Muller glia cell cycle in the mouse retina by simultaneously reducing p27Kip1 and increasing cyclin D1 using a single AAV vector. The approach effectively promotes Muller glia proliferation and reprograming without disrupting retinal structure or function. Interestingly, reactivation of the Muller glia cell cycle downregulates IFN pathway, which may contribute to the induced retinal regeneration. The results presented in this manuscript may offer a promising approach for developing Müller glia cell-mediated regenerative therapies for retinal diseases.

Strengths:

The data are convincing and supported by appropriate, validated methodology. These results are both technically and scientifically exciting and are likely to appeal to retinal specialists and neuroscientists in general.

Weaknesses:

There are some data gaps that need to be addressed.

(1) Please label the time points of AAV injection, EdU labeling, and harvest in Figure 1B.

We thank the reviewer for highlighting the lack of clarity in our experimental design. We will label all experiment timelines in the figures where appropriate in the revised version.

(2) What fraction of Müller cells were transduced by AAV under the experimental conditions?

We apologize for not clearly conveying the transduction efficiency. The retinal region adjacent to the injection site, typically near the central retina, exhibits a transduction efficiency of nearly 100%. In contrast, the peripheral retina shows a lower transduction efficiency compared to the central region. We will include the quantification of AAV transduction efficiency in the revised manuscript.

The quantification of Edu+ MG or other markers was conducted in the area with the highest efficiency. 

(3) It seems unusually rapid for MG proliferation to begin as early as the third day after CCA injection. Can the authors provide evidence for cyclin D1 overexpression and p27 Kip1 knockdown three days after CCA injection?

In our pilot study, we tested the onset time of GFP expression from AAV-GFAP-GFP following intravitreal injection. We observed GFP expression in MG as early as two days post-infection. These findings will be included in the revised manuscript. Additionally, we plan to perform qPCR or Western blot analysis to confirm cyclin D1 overexpression and p27kip1 knockdown at the onset of Müller glia proliferation, which will also be included in the revised manuscript.

(4) The authors reported that MG proliferation largely ceased two weeks after CCA treatment. While this is an interesting finding, the explanation that it might be due to the dilution of AAV episomal genome copies in the dividing cells seems far-fetched.

We believe that the lack of durability in high Cyclin D1 and low p27kip1 levels in MG contributes to the cessation of their proliferation. A potential reason for the loss of high Cyclin D1 overexpression and p27kip1 knockdown during MG proliferation could be the dilution of the AAV episomal genome. However, testing this hypothesis is challenging. Instead, we plan to provide direct evidence in the revised manuscript by examining the levels of Cyclin D1 and p27kip1 in the retina treated with CCA before and after the peak of MG proliferation.

Reviewer #2 (Public Review):

This manuscript by Wu, Liao et al. reports that simultaneous knockdown of P27Kip1 with overexpression of Cyclin D can stimulate Muller glia to re-enter the cell cycle in the mouse retina. There is intense interest in reprogramming mammalian muller glia into a source for neurogenic progenitors, in the hopes that these cells could be a source for neuronal replacement in neurodegenerative diseases. Previous work in the field has shown ways in which mouse Muller glia can be neurogenically reprogrammed and these studies have shown cell cycle re-entry prior to neurogenesis. In other works, typically, the extent of glial proliferation is limited, and the authors of this study highlight the importance of stimulating large numbers of Muller glia to re-enter the cell cycle with the hopes they will differentiate into neurons. While the evidence for stimulating proliferation in this study is convincing, the evidence for neurogenesis in this study is not convincing or robust, suggesting that stimulating cell cycle-reentry may not be associated with increasing regeneration without another proneural stimulus.

Below are concerns and suggestions.

Intro:

(1) The authors cite past studies showing "direct conversion" of MG into neurons. However, these studies (PMID: 34686336; 36417510) show EdU+ MG-derived neurons suggesting cell cycle re-entry does occur in these strategies of proneural TF overexpression.

We thank the reviewer for pointing this out. We will revise the statement to "MG neurogenesis," which encompasses both direct conversion and Müller glia proliferation followed by neuronal differentiation.

(2) Multiple citations are incorrectly listed, using the authors first name only (i.e. Yumi, et al; Levi, et al;). Studies are also incompletely referenced in the references.

We apologize for the mistake with the reference. We will fix these mistakes in the revised version.

Figure 1:

(3) When are these experiments ending? On Figure 1B it says "analysis" on the end of the paradigm without an actual day associated with this. This is the case for many later figures too. The authors should update the paradigms to accurately reflect experimental end points.

We thank the reviewer for highlighting the lack of clarity in our experimental design. We will label all experiment timelines in the figures where appropriate in the revised version.

(4) Are there better representative pictures between P27kd and CyclinD OE, the EdU+ counts say there is a 3 fold increase between Figure 1D&E, however the pictures do not reflect this. In fact, most of the Edu+ cells in Figure 1E don't seem to be Sox9+ MG but rather horizontally oriented nuclei in the OPL that are likely microglia.

Thanks to the reviewer for pointing this out. We will replace the image of Cyclin D1 which a better representative image.

(5) Is the infection efficacy of these viruses different between different combinations (i.e. CyclinD OE vs. P27kd vs. control vs. CCA combo)? As the counts are shown in Figure 1G only Sox9+/Edu+ cells are shown not divided by virus efficacy. If these are absolute counts blind to where the virus is and how many cells the virus hits, if the virus efficacy varies in efficiency this could drive absolute differences that aren't actually biological.

Because the AAV-GFAP-Cyclin D1 and AAV-GFAP-Cyclin D1-p27kip1 shRNA viruses do not carry a fluorescent reporter gene, we cannot easily measure viral efficacy in the same experiment. We believe that variations in viral efficacy cannot account for the significant differences in MG proliferation for two reasons: 1) We injected the same titer for all three viruses, and 2) Viral infection efficacy is very high, approaching 100% in the central retina. Nonetheless, to rule out the possibility that the differences in MG proliferation among the Cyclin D overexpression, p27kip1 knockdown, and CCA groups are due to variations in viral efficacy, we will include the p27kip1 knockdown and Cyclin D1 overexpression efficiencies for all four groups using qPCR and/or Western blot analysis in the revised manuscript.

(6) According to the Jax laboratories, mice aren't considered aged until they are over 18months old. While it is interesting that CCA treatment does not seem to lose efficacy over maturation I would rephrase the findings as the experiment does not test this virus in aged retinas.

Thank you to the reviewer for bringing this to our attention. We will void using “aged mice” in our revised manuscript.

(7) Supplemental Figure 2c-d. These viruses do not hit 100% of MG, however 100% of the P27Kip staining is gone in the P27sh1 treatment, even the P27+ cell in the GCL that is likely an astrocyte has no staining in the shRNA 1 picture. Why is this?

For Supplementary Figure 2c-d, we focused on the central area where knockdown efficiency was high, approaching 100%. We will replace this image with one that includes both high and low Müller glia transduction efficiency regions, clearly demonstrating the complete loss of p27kip1 staining in the area of high transduction efficiency.

Figure 2

(8) Would you expect cells to go through two rounds of cell cycle in such a short time? The treatment of giving Edu then BrdU 24 hours later would have to catch a cell going through two rounds of division in a very short amount of time. Again the end point should be added graphically to this figure.

We thank the reviewer for raising this important point. While the typical cell cycle time for human cells is approximately 24 hours, we hypothesized that 24 hours would be the most likely timepoint to capture cells continuously progressing through the cell cycle. However, we acknowledge that we cannot exclude the possibility of some cells entering a second cell cycle at much later timepoints.

In the revised manuscript, we will carefully qualify our conclusion to state that the majority of MG do not immediately undergo another cell division, rather than making a definitive statement. This more cautious phrasing will better reflect the limitations of the 24-hour timepoint and allow for the potential of a small subset of cells proceeding through additional rounds of division at later stages.

Figure 3

(9) I am confused by the mixing of ratios of viruses to indicate infection success. I know mixtures of viruses containing CCA or control GFP or a control LacZ was injected. Was the idea to probe for GFP or LacZ in the single cell data to see which cells were infected but not treated? This is not shown anywhere?

The virus infection was not uniform across the entire retina. To mark the infection hotspots, we added 10% GFP virus to the mixture. Regions of the retina with low infection efficiency were removed by dissection and excluded from the scRNA-seq analysis. We apologize for not clearly explaining this methodological detail in the original text, and will update the Methods section accordingly.

(10) The majority of glia sorted from TdTomato are probably not infected with virus. Can you subset cells that were infected only for analysis? Otherwise it makes it very hard to make population judgements like Figure 3E-H if a large portion are basically WT glia.

This question is related to the last one. Since the regions with high virus infection efficiency were selectively dissected and isolated for analysis, the percentage of CCA-infected MG should constitute the majority in the scRNA-seq data.

(11) Figure 3C you can see Rho is expressed everywhere which is common in studies like this because the ambient RNA is so high. This makes it very hard to talk about "Rod-like" MG as this is probably an artifact from the technique. Most all scRNA-seq studies from MG-reprogramming have shown clusters of "rods" with MG hybrid gene expression and these had in the past just been considered an artifact.

We agree that the low levels of Rho in other MG clusters (such as quiescent, reactivated, and proliferating MG) are likely due to RNA contamination. However, the level of Rho in the rod-like MG is significantly higher than in the other clusters, indicating that this is unlikely to be solely due to contamination.

As shown in Supplementary Figure 7A-C, a cluster of MG-rod hybrid cells (cluster C4) was present in all three experimental groups at similar ratios, and this hybrid cluster was excluded from further analysis. In contrast, the rod-like Müller glia (cluster C3) were predominantly found in the CCA and CCANT groups, suggesting a genuine response to CCA treatment.

Furthermore, we will conduct Rho and Gnat1 RNA in situ hybridization on the dissociated retinal cells to further support the conclusion that rod-specific genes are upregulated in a subset of MG in the revised manuscript.

(12) It is mentioned the "glial" signature is downregulated in response to CCA treatment. Where is this shown convincingly? Figure H has a feature plot of Glul , which is not clear it is changed between treatments. Otherwise MG genes are shown as a function of cluster not treatment.

We will add box plots of several MG-specific genes to better illustrate the downregulation of the glial signature in the relevant cell cluster in the revised manuscript.

Figure 4

(13) The authors should be commended for being very careful in their interpretations. They employ the proper controls (Er-Cre lineage tracing/EdU-pulse chasing/scRNA-seq omics) and were very careful to attempt to see MG-derived rods. This makes the conclusion from the FISH perplexing. The few puncta dots of Rho and GNAT in MG are not convincing to this reviewer, Rho and GNAT dots are dense everywhere throughout the ONL and if you drew any random circle in the ONL it would be full of dots. The rigor of these counts also comes into question because some dots are picked up in MG in the INL even in the control case. This is confusing because baseline healthy MG do not express RNA-transcripts of these Rod genes so what is this picking up? Taken together, the conclusion that there are Rod-like MG are based off scRNA-seq data (which is likely ambient contamination) and these FISH images. I don't think this data warrants the conclusion that MG upregulate Rod genes in response to CCA.

We performed RNA in situ hybridization on retinal sections because we aimed to correlate cell localization with rod gene expression. We understand the reviewer’s concern that the punctate signals of Rho and GNAT1 in the ONL MG may actually originate from neighboring rods. In the revised manuscript, we will conduct RNAscope on dissociated retinal cells to avoid this issue.

Figure 5

(14) Similar point to above but this Glul probe seems odd, why is it throughout the ONL but completely dark through the IPL, this should also be in astrocytes can you see it in the GCL? These retinas look cropped at the INL where below is completely black. The whole retinal section should be shown. Antibodies exist to GS that work in mouse along with many other MG genes, IHC or western blots could be done to better serve this point.

Indeed, the GCL was cropped out in Figure 5 A-B. We have other images with all retinal layers, which we will use in the revised manuscript. Additionally, we will perform the GS antibody staining to demonstrate partial MG dedifferentiation following CCA treatment.

Figure 6

(15) Figure 6D is not a co-labeled OTX2+/ TdTomato+ cell, Otx2 will fill out the whole nucleus as can be seen with examples from other MG-reprogramming papers in the field (Hoang, et al. 2020; Todd, et al. 2020; Palazzo, et al. 2022). You can clearly see in the example in Figure 6D the nucleus extending way beyond Otx2 expression as it is probably overlapping in space. Other examples should be shown, however, considering less than 1% of cells were putatively Otx2+, the safer interpretation is that these cells are not differentiating into neurons. At least 99.5% are not.

We have additional examples of Otx2+ Tdt+ Edu+ cells, which suggest that MG neurogenesis to Otx2+ cells does occur, despite the low efficiency. We will include these images in the revised manuscript.

(16) Same as above Figure 6I is not convincingly co-labeled HuC/D is an RNA-binding protein and unfortunately is not always the clearest stain but this looks like background haze in the INL overlapping. Other amacrine markers could be tested, but again due to the very low numbers, I think no neurogenesis is occurring.

We have additional examples of HuC/D+ Tdt+ Edu+ cells, which we will show in the revised manuscript.

(17) In the text the authors are accidently referring to Figure 6 as Figure 7.

We thank the reviewer for pointing out the mistake. We will correct the mistake in the revised manuscript.

Figure 7

(18) I like this figure and the concept that you can have additional MG proliferating without destroying the retina or compromising vision. This is reminiscent of the chick MG reprogramming studies in which MG proliferate in large numbers and often do not differentiate into neurons yet still persist de-laminated for long time points.

General:

(19) The title should be changed, as I don't believe there is any convincing evidence of regeneration of neurons. Understanding the barriers to MG cell-cycle re-entry are important and I believe the authors did a good job in that respect, however it is an oversell to report regeneration of neurons from this data.

We thank the reviewer for the suggestion. We will consider changing the title in the revised manuscript.

(20) This paper uses multiple mouse lines and it is often confusing when the text and figures switch between models. I think it would be helpful to readers if the mouse strain was added to graphical paradigms in each figure when a different mouse line is employed.

We will label the mouse lines used in each experiment in the figures where appropriate.

eLife assessment

The authors provide solid evidence that any contribution of oligodendrocyte precursors to the developing cortex from the lateral ganglionic eminence is minimal in scope. The methods used support the conclusions, with some technical concerns that the authors can address with further experimentation. These are considered valuable additions to our understanding of the origins of oligodendrocytes in the forebrain during development.

Reviewer #1 (Public Review):

Summary:

In this manuscript the authors re-examine the developmental origin of cortical oligodendrocyte (OL) lineage cells using a combination of strategies, focussing on the question of whether the LGE generates cortical OL cells. The paper is interesting to myelin biologists, the methods used are appropriate and, in general, the study is well-executed, thorough, and persuasive, but not 100% convincing.

Strengths, weaknesses, and recommendations:

The first evidence presented that the LGE does not generate OLs for the cortex is that there are no OL precursors 'streaming' from the LGE during embryogenesis, unlike the MGE (Figure 1A). This in itself is not strong evidence, as they might be more dispersed. In fact, in the images shown, there is no obvious 'streaming' from the MGE either. Note that in Figure 1 there is no reference to the star that is shown in the figure.

The authors then electroporate a reporter into the LGE at E13.5 and examine the fate of the electroporated cells (Figures 1C-E). They find that electroporated cells became neurons in the striatum and in the cortex but no OLs for the cortex. There are two issues with this: first, there is no quantification, which means there might indeed be a small contribution from the LGE that is not immediately obvious from snapshot images. Second, it is unexpected to find labelled neurons in the cortex at all since the LGE does not normally generate neurons for the cortex! Electroporations are quite crude experiments as targeting is imprecise and variable and not always discernible at later stages. For example, in Figure 1D, one can see tdTOM+ cells near the AEP, as well as the striatum. Hence, IUE cannot on its own be taken as proof that there is no contribution of the LGE to the cortical OL population.

The authors then use an alternative fate-mapping approach, again with E13.5 electroporations (Figure 2). They find only a few GFP+ cells in the cortex at E18 (Figures 2C-D) and P10 (Figure 2E) and these are mainly neurons, not OL lineage cells. Again, there is no quantification.

Figure 3 is more convincing, but the experiments are incomplete. Here the authors generate triple-transgenic mice expressing Cre in the cortex (Emx1-Cre) and the MGE (Nkx2.1-Cre) as well as a strong nuclear reporter (H2B-GFP). They find that at P0 and P10, 97-98% of OL-lineage cells (SOX10+ or PDGFRA+) in the cortex are labelled with GFP (Figure 3). This is a more convincing argument that the LGE/CGE might not contribute significant numbers of OL lineage cells to the cortex, in contrast to the Kessaris et at. (2006) paper, which showed that Gsh2-Cre mice label ~50% of SOX10+ve cells in the motor cortex at P10. The authors of the present paper suggest that the discrepancy between their study and that of Kessaris et al. (2006) is based on the authors' previous observation (Zhang et al 2020) (https://doi.org/10.1016/j.celrep.2020.03.027) that GSH2 is expressed in intermediate precursors of the cortex from E18 onwards. If correct, then Kessaris et al. might have mistakenly attributed Gsh2-Cre+ lineages to the LGE/CGE when they were in fact intrinsic to the cortex. However, the evidence from Zhang et al 2020 that GSH2 is expressed by cortical intermediate precursors seems to rest solely on their location within the developing cortex; a more convincing demonstration would be to show that the GSH2+ putative cortical precursors co-label for EMX1 (by immunohistochemistry or in situ hybridization), or that they co-label with a reporter in Emx1-driven reporter mice. This demonstration should be simple for the authors as they have all the necessary reagents to hand. Without these additional data, the assertion that GSX2+ve cells in the cortex are derived from the cortical VZ relies partly on an act of faith on the part of the reader.

Note that Tripathi et al. (2011, "Dorsally- and ventrally-derived oligodendrocytes have similar electrical properties but myelinate preferred tracts." J. Neurosci. 31, 6809-6819) found that the Gsh-Cre+ OL lineage contributed only ~20% of OLs to the mature cortex, not ~50% as reported by Kessaris et al. (2006). If it is correct that these Gsh2-derived OLs are from the cortical anlagen as the current paper claims, then it would raise the possibility that the ventricular precursors of GSH2+ intermediate progenitors are not uniformly distributed through the cortical VZ but are perhaps localized to some part of it. Then the contribution of Gsh2-derived OLs to the cortical population could depend on precisely where one looks relative to that localized source. It would be a nice addition to the current manuscript if the authors could explore the distribution of their GSH2+ intermediate precursors throughout the developing cortex. In any case, Tripathi et al. (2011) should be cited.

Finally, the authors deleted Olig2 in the MGE and found a dramatic reduction of PDGFRA+ and SOX10+ cells in the cortex at E14 and E16 (Figure 4A-F). This further supports their conclusion that, at least at E16, there is no significant contribution of OLs from ventral sources other than the MGE/AEP. This does not exclude the possibility that the LGE/CGE generates OLs for the cortex at later stages. Hence, on its own, this is not completely convincing evidence that the LGE generates no OL lineage cells for the cortex.

Comments on the latest version:

The revised manuscript has addressed the issues we raised previously. The addition of the new Figure 3 supplement 1A-C demonstrating that Gsx2+ve cells in the cortex are generated from Emx1-Cre precursors is convincing, although there is nothing to prove that the GFP+, Gsh2+ double-labelled nuclei are oligodendrocyte lineage and not, for example, astrocytes. It would be helpful to include a Gsh2, Olig2 (or Gsh2, Sox10) double-label image to prove this point. Also, to make the figure more clear, the authors should also show a small area at high magnification, splitting the green and red channels so that the reader can see more clearly that all the red cells are also green.

Reviewer #2 (Public Review):

Traditional thinking has been that cortical oligodendrocyte progenitor cells (OPCs) arise in the development of the brain from the medial ganglionic eminence (MGE), lateral/caudal ganglionic eminence (LGE/CGE), and cortical radial glial cells (RGCs). Indeed a landmark study demonstrated some time ago that cortical OPCs are generated in three waves, starting with a ventral wave derived from the medial ganglionic eminence (MGE) or the anterior entopeduncular area (AEP) at embryonic day E12.5 (Nkx2.1+ lineage), followed by a second wave of cortical OLs derived from the lateral/caudal ganglionic eminences (LGE/CGE) at E15.5 (Gsx2+/Nkx2.1- lineage), and then a final wave occurring at P0, when OPCs originate from cortical glial progenitor cells (Emx1+ lineage). However, the authors challenge the idea in this paper that cortical progenitors are produced from the LGE. They have found previously that cortical glial progenitor cells were also found to express Gsx2, suggesting this may not have been the best marker for LGE-derived OPCs. They have used fate mapping experiments and lineage analyses to suggest that cortical OPCs do not derive from the LGE.

Strengths:

(1) The data is high quality and very well presented, and experiments are thoughtful and elegant to address the questions being raised.

(2) The authors use two elegant approaches to lineage trace LGE derived cells, namely fate mapping of LGE-derived OPCs by combining IUE (intrauterine electroporation) with a Cre recombinase-dependent IS reporter, and Lineage tracing of LGE-derived OPCs by combining IUE with the PiggyBac transposon system. Both approaches show convincingly that labelled LGE-derived cells that enter the cortex do not express OPC markers, but that those co-labelling with oligodendrocyte markers remain in the striatum.

(3) The authors then use further approaches to confirm their findings. Firstly they lineage trace Emx1-Cre; Nkx2.1-Cre; H2B-GFP mice. Emx1-Cre is expressed in cortical RGCs and Nkx2.1-Cre is specifically expressed in MGE/AEP RGCs. They find that close to 98% of OPCs in the cortex co-label with GFP at later times, suggesting the contribution of OPCs from LGE is minimal.

(4) They use one further approach to strengthen the findings yet further. They cross Nkx2.1-Cre mice with Olig2 F/+ mice to eliminate Olig2 expression in the SVZ/VZ of the MGE/AEP (Figures 4A-B). The generation of MGE/AEP-derived OPCs is inhibited in these Olig2-NCKO conditional mice. They find that the number of cortical progenitors at E16.5 is reduced 10-fold in these mice, suggesting that LGE contribution to cortical OPCs is minimal.

Impact of Study:

The authors show elegantly and convincingly that the contribution of the LGE to the pool of cortical OPCs is minimal. The title should perhaps be that the LGE contribution is minimal rather than no contribution at all, as they are not able to rule out some small contribution from the LGE. These findings challenge the traditional belief that the LGE contributes to the pool of cortical OPCs. The authors do show that the LGE does produce OPCs, but that they tend to remain in the striatum rather than migrate into the cortex. It is interesting to wonder why their migration patterns may be different from the MGE-derived OPCs which migrate to the cortex. The functional significance of these different sources of OPCs for adult cortex in homeostatic or disease states remains unclear though.

Author response:

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

Reviewer #1 (Public Review):

Summary:

In this manuscript the authors re-examine the developmental origin of cortical oligodendrocyte (OL) lineage cells using a combination of strategies, focussing on the question of whether the LGE generates cortical OL cells. The paper is interesting to myelin biologists, the methods used are appropriate and, in general, the study is well-executed, thorough, and persuasive, but not 100% convincing.

Thank you very much for approving our paper.

Strengths, weaknesses, and recommendations:

The first evidence presented that the LGE does not generate OLs for the cortex is that there are no OL precursors 'streaming' from the LGE during embryogenesis, unlike the MGE (Figure 1A). This in itself is not strong evidence, as they might be more dispersed. In fact, in the images shown, there is no obvious 'streaming' from the MGE either. Note that in Figure 1 there is no reference to the star that is shown in the figure.

We totally agree with you. While OPC migration stream is not strong evidence to support that the LGE does not generate OPCs for the cortex, when considering our additional evidence, the absence of obvious 'streaming' from LGE to cortex provided supplementary support for this conclusion. Finally, we have removed the star in the figure.

The authors then electroporate a reporter into the LGE at E13.5 and examine the fate of the electroporated cells (Figures 1C-E). They find that electroporated cells became neurons in the striatum and in the cortex but no OLs for the cortex. There are two issues with this: first, there is no quantification, which means there might indeed be a small contribution from the LGE that is not immediately obvious from snapshot images. Second, it is unexpected to find labelled neurons in the cortex at all since the LGE does not normally generate neurons for the cortex. Electroporations are quite crude experiments as targeting is imprecise and variable and not always discernible at later stages. For example, in Figure 1D, one can see tdTOM+ cells near the AEP, as well as the striatum. Hence, IUE cannot on its own be taken as proof that there is no contribution of the LGE to the cortical OL population.

Thank you for your constructive suggestions.

(1) Following the reviewer's suggestion, we have added these statistics, please see Figure 1F.

(2) The reviewer raised a good point. We occasionally found a very small number of electroporated cells in the MGE/AEP VZ in our IUE system. Therefore, we can identify these electroporated cells in the cortex, most of them expressed the neuronal marker NeuN. We suspect these are MGE-derived cortical interneurons. It's worth noting that these electroporated cells (MGE-derived) are not glia cells. The probable reason may be that MGE/AEP generate cortical OPCs mainly before E13.5 (in this study we performed IUE at E13.5).

The authors then use an alternative fate-mapping approach, again with E13.5 electroporations (Figure 2). They find only a few GFP+ cells in the cortex at E18 (Figures 2C-D) and P10 (Figure 2E) and these are mainly neurons, not OL lineage cells. Again, there is no quantification.

Thank you very much for your suggestions. Actually, in this fate-mapping approach, the electroporated cells in the cortex is very few. We analyzed four mice, and found that all GFP positive cells (139 GFP+) did not express OLIG2, SOX10 and PDGFRA.

Figure 3 is more convincing, but the experiments are incomplete. Here the authors generate triple-transgenic mice expressing Cre in the cortex (Emx1-Cre) and the MGE (Nkx2.1-Cre) as well as a strong nuclear reporter (H2B-GFP). They find that at P0 and P10, 97-98% of OL-lineage cells (SOX10+ or PDGFRA+) in the cortex are labelled with GFP (Figure 3). This is a more convincing argument that the LGE/CGE might not contribute significant numbers of OL lineage cells to the cortex, in contrast to the Kessaris et at. (2006) paper, which showed that Gsh2-Cre mice label ~50% of SOX10+ve cells in the motor cortex at P10. The authors of the present paper suggest that the discrepancy between their study and that of Kessaris et al. (2006) is based on the authors' previous observation (Zhang et al 2020) (https://doi.org/10.1016/j.celrep.2020.03.027) that GSH2 is expressed in intermediate precursors of the cortex from E18 onwards. If correct, then Kessaris et al. might have mistakenly attributed Gsh2-Cre+ lineages to the LGE/CGE when they were in fact intrinsic to the cortex. However, the evidence from Zhang et al 2020 that GSH2 is expressed by cortical intermediate precursors seems to rest solely on their location within the developing cortex; a more convincing demonstration would be to show that the GSH2+ putative cortical precursors co-label for EMX1 (by immunohistochemistry or in situ hybridization), or that they co-label with a reporter in Emx1-driven reporter mice. This demonstration should be simple for the authors as they have all the necessary reagents to hand. Without these additional data, the assertion that GSX2+ve cells in the cortex are derived from the cortical VZ relies partly on an act of faith on the part of the reader. Note that Tripathi et al. (2011, "Dorsally- and ventrally-derived oligodendrocytes have similar electrical properties but myelinate preferred tracts." J. Neurosci. 31, 6809-6819) found that the Gsh-Cre+ OL lineage contributed only ~20% of OLs to the mature cortex, not ~50% as reported by Kessaris et al. (2006). If it is correct that these Gsh2-derived OLs are from the cortical anlagen as the current paper claims, then it would raise the possibility that the ventricular precursors of GSH2+ intermediate progenitors are not uniformly distributed through the cortical VZ but are perhaps localized to some part of it. Then the contribution of Gsh2-derived OLs to the cortical population could depend on precisely where one looks relative to that localized source. It would be a nice addition to the current manuscript if the authors could explore the distribution of their GSH2+ intermediate precursors throughout the developing cortex. In any case, Tripathi et al. (2011) should be cited.

Thank you for your constructive suggestions.

(1) We used the Emx1Cre; RosaH2B-GFP mouse and found that nearly all GSX2+ cells in the cortical SVZ are derived from the Emx1+ lineage at P0 (Please see our new Figure 3-supplement 1A-C). 

(2) According to your suggestion, we have cited this paper (Tripathi et al.) in our revised manuscript.

(3) The study conducted by Kessaris et al. (2006) revealed that roughly 50% of cortical oligodendrocytes (OLs) originate from the Gsx2 lineage (LGE/CGE-derived). In contrast, Tripathi et al. (2011) observed that Gsx2-derived OLs contribute only around 20% to the corpus callosum (CC). To investigate the reasons behind these disparate findings, we conducted three experiments. Firstly, using Emx1Cre; RosaH2B-GFP mice, we found that approximately 89% of lateral CC (LCC) OLs originate from the Emx1 lineage, with only around 11% derived from the ventral source (refer to Author response image 1A and B below). Secondly, employing Nkx2-1Cre; RosaH2B-GFP mice, we determined that approximately 11% of LCC OLs originate from the Nkx2.1 lineage (refer to pictures C and D below). Finally, we found that approximately 98.3% of lateral LCC OLs originate from both Emx1 and Nkx2.1 lineages, with only around 1.7% possibly derived from the LGE (see Author response image 1E and F below). Taken together, our results indicate that approximately 89% of LCC OLs originate from the Emx1 lineage, while 11% of LCC OLs are derived from the medial ganglionic eminence (MGE).

It is worth noting that OLs from Emx1 and Nkx2.1 lineages were equally distributed in the medial CC (mCC) (see Author response image 1G below). This finding suggests that MGE-derived OLs exhibit spatial heterogeneity in their distribution within the CC. These results provide evidence that the contribution of the lateral ganglionic eminence (LGE) and caudal ganglionic eminence (CGE) to CC OLs is minimal.

Author response image 1.

Finally, the authors deleted Olig2 in the MGE and found a dramatic reduction of PDGFRA+ and SOX10+ cells in the cortex at E14 and E16 (Figure 4A-F). This further supports their conclusion that, at least at E16, there is no significant contribution of OLs from ventral sources other than the MGE/AEP. This does not exclude the possibility that the LGE/CGE generates OLs for the cortex at later stages. Hence, on its own, this is not completely convincing evidence that the LGE generates no OL lineage cells for the cortex.

There are three reasons why we didn't analyze Olig2-NCKO mice after E16.5. 1. The expression of Nkx2.1Cre is lower within the dorsal-most region of the MGE than other Nkx2.1-expressing regions. Even at E15.5, we can still find a small number of OPCs in the lateral cortex. We speculate that these OPCs are derived from dorsal MGE. 2. Considering the possibility of incomplete recombination in Olig2 gene locus, we guess OPCs (Olig2+) in the lateral cortex are derived from MGE. Indeed, we found a few OPCs in the MGE/AEP in the Olig2-NCKO mice (Figure 4F). 3. The recent study (bioRxiv preprint doi: https://doi.org/10.1101/2024.01.23.576886) showed that the contribution of LGE/CGE to cortical OPCs is minimal, which further supporting our findings. Taken together, our results provide additional evidence supporting the limited contribution of the LGE/CGE to cortical OPCs (OLs).

Reviewer #2 (Public Review):

Traditional thinking has been that cortical oligodendrocyte progenitor cells (OPCs) arise in the development of the brain from the medial ganglionic eminence (MGE), lateral/caudal ganglionic eminence (LGE/CGE), and cortical radial glial cells (RGCs). Indeed a landmark study demonstrated some time ago that cortical OPCs are generated in three waves, starting with a ventral wave derived from the medial ganglionic eminence (MGE) or the anterior entopeduncular area (AEP) at embryonic day E12.5 (Nkx2.1+ lineage), followed by a second wave of cortical OLs derived from the lateral/caudal ganglionic eminences (LGE/CGE) at E15.5 (Gsx2+/Nkx2.1- lineage), and then a final wave occurring at P0, when OPCs originate from cortical glial progenitor cells (Emx1+ lineage). However, the authors challenge the idea in this paper that cortical progenitors are produced from the LGE. They have found previously that cortical glial progenitor cells were also found to express Gsx2, suggesting this may not have been the best marker for LGE-derived OPCs. They have used fate mapping experiments and lineage analyses to suggest that cortical OPCs do not derive from the LGE.

Strengths:

(1) The data is high quality and very well presented, and experiments are thoughtful and elegant to address the questions being raised.

(2) The authors use two elegant approaches to lineage trace LGE derived cells, namely fate mapping of LGE-derived OPCs by combining IUE (intrauterine electroporation) with a Cre recombinase-dependent IS reporter, and Lineage tracing of LGE-derived OPCs by combining IUE with the PiggyBac transposon system. Both approaches show convincingly that labelled LGE-derived cells that enter the cortex do not express OPC markers, but that those co-labelling with oligodendrocyte markers remain in the striatum.

(3) The authors then use further approaches to confirm their findings. Firstly they lineage trace Emx1-Cre; Nkx2.1-Cre; H2B-GFP mice. Emx1-Cre is expressed in cortical RGCs and Nkx2.1-Cre is specifically expressed in MGE/AEP RGCs. They find that close to 98% of OPCs in the cortex co-label with GFP at later times, suggesting the contribution of OPCs from LGE is minimal.

(4) They use one further approach to strengthen the findings yet further. They cross Nkx2.1-Cre mice with Olig2 F/+ mice to eliminate Olig2 expression in the SVZ/VZ of the MGE/AEP (Figures 4A-B). The generation of MGE/AEP-derived OPCs is inhibited in these Olig2-NCKO conditional mice. They find that the number of cortical progenitors at E16.5 is reduced 10-fold in these mice, suggesting that LGE contribution to cortical OPCs is minimal.

We thank the reviewer for summarizing the strengths of our manuscript.

Weaknesses:

(1) The authors use IUE in experiments mentioned in point 2 of 'Strengths' above (Figures 1 and 2) and claim that the reporter was delivered specifically into LGE VZ at E13.5 using this IUE. It would be nice to see some sort of time course of delivery after IUE to show the reporter is limited to LGE VZ at early times post-IUE.

Thank you very much for your suggestions. Indeed, when using IUE in our system, we occasionally found a small number of electroporated cells in the MGE/AEP VZ. Thus, we can find very few electroporated cells (MGE/AEP-derived) in the cortex and these electroporated cells are neuron (perhaps interneuron).

(2) In the experiments mentioned in point 3 of 'Strengths' (Figure 3), statistical analysis showed that only approximately 2% of OPCs were GFP-negative cells. This 2% could possibly be derived from the LGE/CGE so does not totally rule out that LGE contributes some cortical OPCs.

Thank you for your constructive suggestions. We apologize for any imprecise descriptions. Despite we suspect that this 2% may originate from MGE {Considering the possibility of incomplete recombination in Olig2 gene locus, we guess the OPCs (Olig2+) may be derived from MGE. Indeed, we found a few OPCs in the MGE/AEP in the Olig2-NCKO mice (Figure 4F)} or from the dMGE (The expression of Nkx2.1Cre is lower within the dorsal-most region of the MGE than in other Nkx2.1-expressing regions). Anyway, we have softened the assertion everywhere in our revised manuscript.

(3) In the experiments mentioned in point 4 of 'Strengths' (Figure 4), they do still find cortical OPCs at E16.5 in the Olig2-NCKO conditional mice. It is unclear whether this is due to the recombination efficiency of the CRE enzyme not being 100%, or whether there is some LGE contribution to the cortical OPCs.

This experiment alone may not provide strong evidence to support that LGE do not contribute to the cortical OPCs during development. However, when combing our other results with this result, we can confirm that the contribution of LGE to cortical OPCs is minimal. Furthermore, a recent study reported that LGE/CGE-derived OLs make minimum contributions to the neocortex and corpus callosum，which further supporting the reliability of our conclusion.

We would like to thank the reviewers and editors for their valuable comments and suggestions again.

Impact of Study:

The authors show elegantly and convincingly that the contribution of the LGE to the pool of cortical OPCs is minimal. The title should perhaps be that the LGE contribution is minimal rather than no contribution at all, as they are not able to rule out some small contribution from the LGE. These findings challenge the traditional belief that the LGE contributes to the pool of cortical OPCs. The authors do show that the LGE does produce OPCs, but that they tend to remain in the striatum rather than migrate into the cortex. It is interesting to wonder why their migration patterns may be different from the MGE-derived OPCs which migrate to the cortex. The functional significance of these different sources of OPCs for adult cortex in homeostatic or disease states remains unclear though.

Recommendations for the authors:

Reviewer #1 (Recommendations for The Authors):

(1) Change the title to e.g. 'limited contribution of the LGE to cortical oligodendrocytes'. Alternatively, It might be more useful to highlight where they come from, e.g. "Cortical oligodendrocytes originate predominantly or exclusively from the MGE and cortical VZ"

As suggested, we have changed the old title to the following: The lateral/caudal ganglionic eminence makes a limited contribution to cortical oligodendrocytes

(2) Demonstrate using lineage tracing that GSH2+ cells in the cortex are derived from the Emx1-lineage, e.g. using immunohistochemistry for GSX2 and a reporter in Emx1-Cre mice crossed to a reporter.

In our revised manuscript, we have added a new figure (Figure 3-supplement 1A-C) to demonstrate that the GSX2+ cells in the cortex are derived from the Emx1-lineage.

(3) Make it clear in their discussion that they have not explored the CGE so it is possible that this region generates some OLs.

The Emx1Cre; Nkx2.1Cre; H2B-GFP mice showed that only ~2% cortical OLs are derived from LGE/CGE. Actually, considering the efficiency of Cre enzyme recombination and the relatively low Cre activity in the dMGE of Nkx2.1Cre, the actual contribution of LGE/CGE-derived cortical OLs could be even lower than our current observation. Therefore, our results demonstrate that the LGE/CGE generate very few，possibly even no，OLs for the cortex.

(4) Soften the assertion that the LGE does not generate any OL lineage cells that reach the cortex by e.g. changing the word 'sole' to 'predominant' (line 88) and, elsewhere in the paper, leaving open the possibility that small numbers of LGE-derived OLs might enter the cortex, depending on where exactly one looks.

As suggested, we have softened the assertion everywhere in our manuscript.

(5) Lines 255-260: 'First, the time window during which the MGE generates OLs is very brief, perhaps occurring before MGE neurogenesis. The high level of SHH in the MGE allows for the production of a small population of cortical OPCs around E12.5. Subsequently, multipotent intermediate progenitors begin to express DLX transcription factors resulting in ending the generation of OPCs in the MGE'. What is the evidence that OL genesis precedes neurogenesis? If there is none (as I suspect) then this statement should be removed.

The editors raised a good point. We have no strong evidence to support that OL genesis precedes neurogenesis in MGE, thus, we removed these sentences in our manuscript.

(6) Figure 1E should show quantification of cells as a % of electroporated cells and as a % of PDGFRA+ or OLIG2+ or SOX10+ cells, so that the reader might have a clear view of the extent of labelling.

Done.

(7) Figure 4: This is interesting but incomplete. At E14.5 the authors show the presence of PDGFRA+cells in the telencephalon. However, at E16.5 they show images only of the dorsal-most region of the cortex. If the LGE/CGE begins to generate OLPs for the early cortex, they would be expected to appear near the cortico-striatal boundary, as shown in Kessaris 2006 Fig1g-h. In the current manuscript, the authors do not show these regions, or the LGE and CGE, in their images. It is essential to show PDGFRA immunolabelling at the cortico-striatal boundary and also in the LGE and CGE at E16.5 in control and Olig2 mutant mice. It is also necessary to extend this analysis to E18.5, perhaps showing PDGFRA+ cells streaming from the cortical VZ/SVZ.

There are three reasons why we didn't analyze Olig2-NCKO mice after E16.5. 1.Frankly, the expression of Nkx2.1Cre is lower within the dorsal-most region of the MGE than other Nkx2.1-expressing regions. Even at E15.5, we can still find a small number of OPCs in the lateral cortex. We guess these OPCs are derived from dMGE. 2. Considering the possibility of incomplete recombination in Olig2 gene locus, we guess OPCs (Olig2+) are derived from MGE. In fact, we found a few OPCs in the MGE/AEP in the Olig2-NCKO mice (Figure 4F). 3. The recent study (bioRxiv preprint doi: https://doi.org/10.1101/2024.01.23.576886) showed that the contribution of LGE/CGE to cortical OPCs is minimal. Taken together, our results provide additional evidence supporting the limited contribution of the LGE/CGE to cortical OPCs (OLs).

(8) Cite Tripathi et al. (2011) and mention the disparity between the findings of that paper and Kessaris et al. (2006) and possible reasons - see main review above.

Done.

eLife assessment

Shore et al. report the important effects of a heterozygous mutation in the KCNT1 potassium channel on ion currents and firing behavior of excitatory and inhibitory neurons in the cortex of KCNT1-Y777H mice. The authors provide solid evidence of physiological differences between this heterozygous mutation and their previous work with homozygotes. The reviewers appreciated the inclusion of recordings in ex vivo slices and dissociated cortical neurons, as well as the additional evidence showing an increase in persistent sodium currents in parvalbumin-positive interneurons in heterozygotes.

Reviewer #1 (Public Review):

Summary:

This manuscript reports the effects of a heterozygous mutation in the KCNT1 potassium channels on the properties of ion currents and firing behavior of excitatory and inhibitory neurons in the cortex of mice expressing KCNT1-Y777H. In humans, this mutation as well as multiple other heterozygotic mutations produce very severe early-onset seizures and produce a major disruption of all intellectual function. In contrast, in mice, this heterozygous mutation appears to have no behavioral phenotype or any increased propensity to seizures. A relevant phenotype is, however, evident in mice with the homozygous mutation, and the authors have previously published the results of similar experiments with the homozygotes. As perhaps expected, the neuronal effects of the heterozygous mutation presented in this manuscript are generally similar but markedly smaller than the previously published findings on homozygotes. There are, however, some interesting differences, particularly on PV+ interneurons, which appear to be more excitable than wild type in the heterozygotes but more excitable in the heterozygotes. This raises the interesting question, which has been explicitly discussed by the authors in the revised manuscript, as to whether the reported changes represent homeostatic events that suppress the seizure phenotype in the mouse heterozygotes or simply changes in excitability that do not reach the threshold for behavioral outcomes.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Shore et al. investigate the consequent changes in excitability and synaptic efficacy of diverse neuronal populations in an animal model of juvenile epilepsy. Using electrophysiological patch-clamp recordings from dissociated neuronal cultures, the authors find diverging changes in two major populations of inhibitory cell types, namely somatostatin (SST)- and parvalbumin (PV)-positive interneurons, in mice expressing a variant of the KCNT1 potassium channel. They further suggest that the differential effects are due to a compensatory increase in the persistent sodium current in PV interneurons in pharmacological and in silico experiments. It remains unclear why this current is selectively enhanced in PV-interneurons.

Strengths:

(1) Heterozygous KCNT1 gain of function variant was used which more accurately models the human disorder.

(2) The manuscript is clearly written, and the flow is easy to follow. The authors explicitly state the similarities and differences between the current findings and the previously published results in the homozygous KCNT1 gain of function variant.

(3) This study uses a variety of approaches including patch clamp recording, in silico modeling and pharmacology that together make the claims stronger.

(4) Pharmacological experiments are fraught with off-target effects and thus it bolsters the authors' claims when multiple channel blockers (TTX and VU170) are used to reconstruct the sodium-activated potassium current.

Reviewer #3 (Public Review):

Summary:

The present manuscript by Shore et al. entitled Reduced GABAergic Neuron Excitability, Altered Synaptic Connectivity, and Seizures in a KCNT1 Gain-of-Function Mouse Model of Childhood Epilepsy" describes in vitro and in silico results obtained in cortical neurons from mice carrying the KCNT1-Y777H gain-of-function (GOF) variant in the KCNT1 gene encoding for a subunit of the Na+-activated K+ (KNa) channel. This variant corresponds to the human Y796H variant found in a family with Autosomal Dominant Nocturnal Frontal lobe epilepsy. The occurrence of GOF variants in potassium channel encoding genes is well known, and among potential pathophysiological mechanisms, impaired inhibition has been documented as responsible for KCNT1-related DEEs. Therefore, building on a previous study by the same group performed in homozygous KI animals, and considering that the largest majority of pathogenic KCNT1 variants in humans occur in heterozygosis, the Authors have investigated the effects of heterozygous Kcnt1-Y777H expression on KNa currents and neuronal physiology among cortical glutamatergic and the 3 main classes of GABAergic neurons, namely those expressing vasoactive intestinal polypeptide (VIP), somatostatin (SST), and parvalbumin (PV), crossing KCNT1-Y777H mice with PV-, SST- and PV-cre mouse lines, and recording from GABAergic neurons identified by their expression of mCherry (but negative for GFP used to mark excitatory neurons).

The results obtained revealed heterogeneous effects of the variant on KNa and action potential firing rates in distinct neuronal subpopulations, ranging from no change (glutamatergic and VIP GABAergic) to decreased excitability (SST GABAergic) to increased excitability (PV GABAergic). In particular, modelling and in vitro data revealed that an increase in persistent Na current occurring in PV neurons was sufficient to overcome the effects of KCNT1 GOF and cause an overall increase in AP generation.

Strengths:

The paper is very well written, the results clearly presented and interpreted, and the discussion focuses on the most relevant points.<br /> The recordings performed in distinct neuronal subpopulations (both in primary neuronal cultures and, for some subpopulations, in cortical slices, are a clear strength of the paper. The finding that the same variant can cause opposite effects and trigger specific homeostatic mechanisms in distinct neuronal populations is very relevant for the field, as it narrows the existing gap between experimental models and clinical evidence.

Author response:

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

eLife assessment

Shore et al. report important effects of a heterozygous mutation in the KCNT1 potassium channel on ion currents and firing behavior of excitatory and inhibitory neurons in the cortex of KCNT1-Y777H mice. The authors provide solid evidence of physiological differences between this heterozygous mutation and their previous work with homozygotes. The reviewers appreciated the inclusion of recordings in ex vivo slices and dissociated cortical neurons, as well as the additional evidence showing an increase in persistent sodium currents (INaP) in parvalbumin-positive interneurons in heterozygotes. However, they were unclear regarding the likelihood of the increased sodium influx through INaP channels increasing sodium-activated potassium currents in these neurons.

Regarding the last sentence of the eLife assessment, we’ve added a new paragraph to the Discussion section of the paper to address this concern. Please see the response to comment 1B of Reviewer #1 below for more details. We feel that the question of whether an increase in INaP would further increase KCNT1 activity is a valid discussion point but not a limitation of the importance or rigor of the work itself.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This manuscript reports the effects of a heterozygous mutation in the KCNT1 potassium channels on the properties of ion currents and firing behavior of excitatory and inhibitory neurons in the cortex of mice expressing KCNT1-Y777H. In humans, this mutation as well as multiple other heterozygotic mutations produce very severe early-onset seizures and produce a major disruption of all intellectual function. In contrast, in mice, this heterozygous mutation appears to have no behavioral phenotype or any increased propensity to seizures. A relevant phenotype is, however, evident in mice with the homozygous mutation, and the authors have previously published the results of similar experiments with the homozygotes. As perhaps expected, the neuronal effects of the heterozygous mutation presented in this manuscript are generally similar but markedly smaller than the previously published findings on homozygotes. There are, however, some interesting differences, particularly on PV+ interneurons, which appear to be more excitable than wild type in the heterozygotes but more excitable in the heterozygotes. This raises the interesting question, which has been explicitly discussed by the authors in the revised manuscript, as to whether the reported changes represent homeostatic events that suppress the seizure phenotype in the mouse heterozygotes or simply changes in excitability that do not reach the threshold for behavioral outcomes.

Strengths and Weaknesses:

(1) The authors find that the heterozygous mutation in PV+ interneurons increases their excitability, a result that is opposite from their previous observation in neurons with the corresponding homozygous mutation. They propose that this results from the selective upregulation of a persistent sodium current INaP in the PV+ interneurons. These observations are very interesting ones, and they raised some issues in the original submission:

A) The protocol for measuring the INaP current could potentially lead to results that could be (mis)interpreted in different ways in different cells. First, neither K currents nor Ca currents are blocked in these experiments. Instead, TTX is applied to the cells relatively rapidly (within 1 second) and the ramp protocol is applied immediately thereafter. It is stated that, at this time, Na currents and INaP are fully blocked but that any effects on Na-activated K currents are minimal. In theory this would allow the pre- to post- difference current to represent a relatively uncontaminated INaP. This would, however, only work if activation of KNa currents following Na entry is very slow, taking many seconds. A good deal of literature has suggested that the kinetics of activation of KNa currents by Na influx vary substantially between cell types, such that single action potentials and single excitatory synaptic events rapidly evoke KNa currents in some cell types. This is, of course, much faster than the time of TTX application. Most importantly, the kinetics of KNa activation may be different in different neuronal types, which would lead to errors that could produce different estimates of INaP in PV+ interneurons vs other cell types.

In their revised manuscript, the authors have provided good data demonstrating that, at least for the PV and SST neurons, loss of KNa currents after TTX application is slow relative to the time course of loss of INaP, justifying the use of this protocol for these neuronal types.

B) As the authors recognize, INaP current provides a major source of cytoplasmic sodium ions for the activation. An expected outcome of increased INaP is, therefore, further activation of KNa currents, rather than a compensatory increase in an inward current that counteracts the increase in KNa currents, as is suggested in the discussion.

The authors comment in the rebuttal that, despite the fact that sodium entry through INaP is known to activate KNa channels, an increase in INaP does not necessarily imply increased KNa current. This issue should be addressed directly somewhere in the text, perhaps most appropriately in the discussion.

We’ve added the following new paragraph to the Discussion section of the manuscript to address this concern:

“As the persistent sodium current has been shown to act as a source of cytoplasmic sodium ions for KCNT1 channel activation in some neuron types (Hage & Salkoff, 2012), one might expect that the compensatory increase in INaP in YH-HET PV neurons would further increase, rather than counteract, KNa currents. Unfortunately, there is insufficient information on the relative locations of the INaP and KCNT1 channels, as well as the kinetics of sodium transfer to KCNT1 channels, among cortical neuron subtypes, and even less is known in the context of KCNT1 GOF neurons; thus, it is difficult to predict how alterations in one of these currents may affect the other. One plausible reason that increased INaP would not alter KNa currents in YH-HET PV neurons is that the particular sodium channels that are responsible for the increased INaP are not located within close proximity to the KCNT1 channels. Moreover, homeostatic mechanisms that modify the length and/or location of the sodium channel-enriched axon initial segment (AIS) in neurons in response to altered excitability are well described (Grubb & Burrone, 2010; Kuba et al., 2010); thus, it is possible that in YH-HET PV neurons, the length or location of the AIS is altered, leading to uncoupling of the sodium channels that are responsible for the increased INaP to the KCNT1 channels. Future studies will aim to further investigate potential mechanisms of neuron-type-specific alterations in NaP and KNa currents downstream of KCNT1 GOF.”  

C) The numerical simulations, in general, provide a very useful way to evaluate the significance of experimental findings. Nevertheless, while the in-silico modeling suggests that increases in INaP can increase firing rate in models of PV+ neurons, there is as yet insufficient information on the relative locations of the INaP channels and the kinetics of sodium transfer to KNa channels to evaluate the validity of this specific model.

The authors have now put in all of the appropriate caveats on this very nicely in the revised manuscript.

(2) The effects of the KCNT1 channel blocker VU170 on potassium currents are somewhat larger and different from those of TTX, suggesting that additional sources of sodium may contribute to activating KCNT1, as suggested by the authors. Because VU170 is, however, a novel pharmacological agent, it may be appropriate to make more careful statements on this. While the original published description of this compound reported no effect on a variety of other channels, there are many that were not tested, including Na and cation channels that are known to activate KCNT1, raising the possibility of off-target effects.

In the revised version, the authors have added more to the manuscript on this issue and have added a very clear discussion of this to the text (in the discussion section).

This is a very clear and thorough piece of work, and the authors are to be congratulated on this. My one remaining suggestion would be to make an explicit statement about whether increased sodium influx through INaP channels, which is thought to activate KNa channels, would be likely to increase KNa current in these neurons (see comment 1B).

Please see response to comment 1B.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Shore et al. investigate the consequent changes in excitability and synaptic efficacy of diverse neuronal populations in an animal model of juvenile epilepsy. Using electrophysiological patch-clamp recordings from dissociated neuronal cultures, the authors find diverging changes in two major populations of inhibitory cell types, namely somatostatin (SST)- and parvalbumin (PV)-positive interneurons, in mice expressing a variant of the KCNT1 potassium channel. They further suggest that the differential effects are due to a compensatory increase in the persistent sodium current in PV interneurons in pharmacological and in silico experiments. It remains unclear why this current is selectively enhanced in PV-interneurons.

Strengths:

(1) Heterozygous KCNT1 gain of function variant was used which more accurately models the human disorder.

(2) The manuscript is clearly written, and the flow is easy to follow. The authors explicitly state the similarities and differences between the current findings and the previously published results in the homozygous KCNT1 gain of function variant.

(3) This study uses a variety of approaches including patch clamp recording, in silico modeling and pharmacology that together make the claims stronger.

(4) Pharmacological experiments are fraught with off-target effects and thus it bolsters the authors' claims when multiple channel blockers (TTX and VU170) are used to reconstruct the sodium-activated potassium current.

Weaknesses:

(1) This study mostly relies on recordings in dissociated cortical neurons. Although specific WT interneurons showed intrinsic membrane properties like those reported for acute brain slices, it is unclear whether the same will be true for those cells expressing KCNT1 variants, especially when the excitability changes are thought to arise from homeostatic compensatory mechanisms. The authors do confirm that mutant SST-interneurons are hypoexcitable using an ex vivo slice preparation which is consistent with work for other KCTN1 gain of function variants (e.g. Gertler et al., 2022). However, the key missing evidence is the excitability state of mutant PV-interneurons, given the discrepant result of reduced excitability of PV cells reported by Gertler et al in acute hippocampal slices.

Reviewer #3 (Public Review):

Summary:

The present manuscript by Shore et al. entitled Reduced GABAergic Neuron Excitability, Altered Synaptic Connectivity, and Seizures in a KCNT1 Gain-of-Function Mouse Model of Childhood Epilepsy" describes in vitro and in silico results obtained in cortical neurons from mice carrying the KCNT1-Y777H gain-of-function (GOF) variant in the KCNT1 gene encoding for a subunit of the Na+-activated K+ (KNa) channel. This variant corresponds to the human Y796H variant found in a family with Autosomal Dominant Nocturnal Frontal lobe epilepsy. The occurrence of GOF variants in potassium channel encoding genes is well known, and among potential pathophysiological mechanisms, impaired inhibition has been documented as responsible for KCNT1-related DEEs. Therefore, building on a previous study by the same group performed in homozygous KI animals, and considering that the largest majority of pathogenic KCNT1 variants in humans occur in heterozygosis, the Authors have investigated the effects of heterozygous Kcnt1-Y777H expression on KNa currents and neuronal physiology among cortical glutamatergic and the 3 main classes of GABAergic neurons, namely those expressing vasoactive intestinal polypeptide (VIP), somatostatin (SST), and parvalbumin (PV), crossing KCNT1-Y777H mice with PV-, SST- and PV-cre mouse lines, and recording from GABAergic neurons identified by their expression of mCherry (but negative for GFP used to mark excitatory neurons).

The results obtained revealed heterogeneous effects of the variant on KNa and action potential firing rates in distinct neuronal subpopulations, ranging from no change (glutamatergic and VIP GABAergic) to decreased excitability (SST GABAergic) to increased excitability (PV GABAergic). In particular, modelling and in vitro data revealed that an increase in persistent Na current occurring in PV neurons was sufficient to overcome the effects of KCNT1 GOF and cause an overall increase in AP generation.

Strengths:

The paper is very well written, the results clearly presented and interpreted, and the discussion focuses on the most relevant points.

The recordings performed in distinct neuronal subpopulations (both in primary neuronal cultures and, for some subpopulations, in cortical slices, are a clear strength of the paper. The finding that the same variant can cause opposite effects and trigger specific homeostatic mechanisms in distinct neuronal populations is very relevant for the field, as it narrows the existing gap between experimental models and clinical evidence.

Weaknesses:

My main concern regarding the epileptic phenotype of the heterozygous mice investigated has been clarified in the revision, where the infrequent occurrence of seizures is more clearly stated. Also, a more detailed statistical analysis of the modeled neurons has been added in the revision.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

This is a very clear and thorough piece of work, and the authors are to be congratulated on this. My one remaining suggestion would be to make an explicit statement about whether increased sodium influx through INaP channels, which is thought to activate KNa channels, would be likely to increase KNa current in these neurons (see comment 1B).

Please see response to comment 1B.

Reviewer #2 (Recommendations For The Authors):

This revised manuscript is significantly improved and addresses most of my concerns. However, I would still recommend including the ex vivo slice recordings in mutant PV-interneurons as the authors proposed in their rebuttal. The I-V recordings using sequential TTX and VU170 blockade in WT SST and PV-interneurons that are provided in the rebuttal are interesting and may point to a preferential expression of persistent sodium currents in PV-interneurons normally. It would be helpful to readers as a supplemental figure.

As proposed in the rebuttal, we are currently recording PV neurons using ex vivo slice preparations from WT and Kcnt1-YH Het mice. We look forward to including those data in a future manuscript.

We agree with the reviewer that the differences in INaP between WT PV and SST neurons are notable. The data provided in the rebuttal were only from 5 neurons/group, and they were meant to illustrate a side-by-side comparison of TTX and VU170 subtraction methods to assess KNa currents. However, in Figure 7 of the manuscript, we performed more robust measurements of INaP and observed differences in the current between WT PV and SST neurons. Thus, we’ve added the following sentence to the Results section:

“Interestingly, the mean peak amplitude of INaP in WT PV neurons was 70% larger than that in WT SST neurons (-1.42 ± 0.16 vs. -0.85 ± 0.07 pA/pF; Fig. 7B and 7D), suggesting there may be differences in sodium channel expression, localization, or regulation inherent to each neuron type that confer their differential response to KCNT1 GOF.”

References

Grubb, M. S., & Burrone, J. (2010). Activity-dependent relocation of the axon initial segment fine-tunes neuronal excitability. Nature, 465(7301), 1070-1074. https://doi.org/10.1038/nature09160

Hage, T. A., & Salkoff, L. (2012). Sodium-activated potassium channels are functionally coupled to persistent sodium currents. J Neurosci, 32(8), 2714-2721. https://doi.org/10.1523/JNEUROSCI.5088-11.2012

Kuba, H., Oichi, Y., & Ohmori, H. (2010). Presynaptic activity regulates Na(+) channel distribution at the axon initial segment. Nature, 465(7301), 1075-1078. https://doi.org/10.1038/nature09087

eLife assessment

Goswami and colleagues used rod-specific Gls1 (the gene encoding glutaminase 1) knockout mice to investigate the role of GLS1 in photoreceptor health when GLS1 was deleted from developing or adult photoreceptor cells. This study is important as it shows the critical role of glutamine catabolism in photoreceptor cell health using in vivo model systems. The evidence supporting the authors' claims is convincing. The current manuscript would further benefit from validating the evidence with additional supporting data from IND-cKO with tamoxifen induction at adult age, testing GLS1 activity to provide glutamate for synaptic transmission, and examining metabolic crosstalk between RPE and neural retinas.

Reviewer #1 (Public Review):

Summary:

The authors show for the first time that deleting GLS from rod photoreceptors results in the rapid death of these cells. The death of photoreceptor cells could result from loss of synaptic activity because of a decrease in glutamate, as has been shown in neurons, changes in redox balance, or nutrient deprivation.

Strengths:

The strength of this manuscript is that the author shows a similar phenotype in the mice when Gls was knocked out early in rod development or the adult rod. They showed that rapid cell death is through apoptosis, and there is an increase in the expression of genes responsive to oxidative stress.

Weaknesses:

In this manuscript, the authors show a "metabolic dependency of photoreceptors on glutamine catabolism in vivo". However, there is a potential bias in their thinking that glutamine metabolism in rods is similar to cancer cells where it feeds into the TCA cycle. They should consider that as in neurons, GLS1 activity provides glutamate for synaptic transmission. The modest rescue shown by providing α-ketoglutarate in the drinking water suggests that glutamine isn't a key metabolic substrate for rods when glucose is plentiful. The ERG studies performed on the iCre-Glsflox/flox mice showed a large decrease in the scotopic b wave at saturating flashes which could indicate a decrease in glutamate at the rod synapse as stated by the authors. While EM micrographs of wt and iCre-Glsflox/flox mice were shown for the outer retina at p14, the synapse of the rods needs to be examined by EM.

The authors note that the outer segments are shorter but they do not address whether there is a decrease in the number of cones.

Rod-specific Gls ko mice with an inducible promoter were generated by crossing the Pde6g-CreERT2 and homozygous for either the WT or floxed Gls allele (IND-cKO). In Figure 3 the authors document that by western blots and antibody labeling the GLS1 expression is lost in the IND-cKO 10 days post tamoxifen. OCT images show a decrease in the thickness of the outer nuclear layer between 17 and 38 days post-TAM. Ergs should be performed on the animals at 10 and 30 days post TAM, before and after major structural changes in rod photoreceptor cells, to determine if changes in light-stimulated responses are observed. These studies could help to parse out the cause of photoreceptor cell death.

The studies in Figure 4 were all performed on iCre-Glsflox/flox and control mice at p14, why weren't the IND-cKO mice used for these studies since the findings would not be confounded by development?

In all rescue studies, the endpoint was an ONL thickness, which only addressed rod cell death. The authors should also determine whether there are small improvements in the ERG, which would distinguish the role of GLS in preventing oxidative stress.

Reviewer #2 (Public Review):

Summary:

Photoreceptor neurons are crucial for vision, and discovering pathways necessary for photoreceptor health and survival can open new avenues for therapeutics. Studies have shown that metabolic dysfunction can cause photoreceptor degeneration and vision loss, but the metabolic pathways maintaining photoreceptor health are not well understood. This is a fundamental study that shows that glutamine catabolism is critical for photoreceptor cell health using in vivo model systems.

Strengths:

The data are compelling, and the consideration of potential confounding factors (such as glutaminase 2 expression) and additional experiments to examine the synaptic connectivity and inner retina added strength to this work. The authors were also careful not to overstate their claims, but to provide solid conclusions that fit the results and data provided in their study. The findings linking asparagine supplementation and the inhibition of the integrated stress response to glutamine catabolism within the rod photoreceptor cell are intriguing and innovative. Overall, the authors provide convincing data to highlight that photoreceptors utilize various fuel sources to meet their metabolic needs, and that glutamine is critical to these cells for their biomass, redox balance, function, and survival.

Weaknesses:

Recent studies have explored the metabolic "crosstalk" that exists within the mammalian retina, where metabolites are transferred between the various retinal cells and the retinal pigment epithelium. It would be of interest to test whether the conditional knockout mice have changes in metabolism (via qPCR such as shown in Figure 4 - Supplemental Figure 1) within the retinal pigment epithelium that may be contributing to the authors' findings in the neural retina. Additionally, the authors have very compelling data to show that inhibition of eIF2a or supplementation with asparagine can delay photoreceptor death via OCT measurements in their conditional knockout mouse model (Figure 6G, H). However, does inhibition of eIF2a or asparagine adversely impact the WT retina? It would also be impactful to know whether this has a prolonged effect, or if it is short-term, as this would provide strength to potential therapeutic targeting of these pathways to maintain photoreceptor health.

Reviewer #3 (Public Review):

Summary:

The authors explored the role of GLS, a glutaminase, which is an enzyme that catalyzes the conversion of glutamine to glutamate, in rod photoreceptor function and survival. The loss of GLS was found to cause rapid autonomous death of rod photoreceptors.

Strengths:

Interesting and novel phenotype. Two types of cre-lines were rigorously used to knockout the Gls gene in rods. Both of the conditional knockouts led to a similar phenotype, i.e. rod death. Histology and ERG were carefully done to characterize the loss of rods over specific ages. A necessary metabolomic study was performed and appreciated. Some rescue experiments were performed and revealed possible mechanisms.

Weaknesses:

No major weaknesses were identified. The mechanism of GLS-loss-induced rod death seems not fully elucidated by this study but could be followed up in the future, and the same for GLS's role in cones.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors show for the first time that deleting GLS from rod photoreceptors results in the rapid death of these cells. The death of photoreceptor cells could result from loss of synaptic activity because of a decrease in glutamate, as has been shown in neurons, changes in redox balance, or nutrient deprivation. 

Strengths: 

The strength of this manuscript is that the author shows a similar phenotype in the mice when Gls was knocked out early in rod development or the adult rod. They showed that rapid cell death is through apoptosis, and there is an increase in the expression of genes responsive to oxidative stress. 

We thank the reviewer for their time reviewing the manuscript and their comments regarding the potential mechanism(s) by which rod photoreceptors rapidly degenerate upon knockout of GLS.

Weaknesses: 

In this manuscript, the authors show a "metabolic dependency of photoreceptors on glutamine catabolism in vivo". However, there is a potential bias in their thinking that glutamine metabolism in rods is similar to cancer cells where it feeds into the TCA cycle. They should consider that as in neurons, GLS1 activity provides glutamate for synaptic transmission. The modest rescue shown by providing α-ketoglutarate in the drinking water suggests that glutamine isn't a key metabolic substrate for rods when glucose is plentiful. The ERG studies performed on the iCre-Glsflox/flox mice showed a large decrease in the scotopic b wave at saturating flashes which could indicate a decrease in glutamate at the rod synapse as stated by the authors. While EM micrographs of wt and iCre-Glsflox/flox mice were shown for the outer retina at p14, the synapse of the rods needs to be examined by EM. 

We agree with the reviewer that in the presence of sufficient glucose, it appears a lack of GLS-driven glutamine (Gln) catabolism does not drastically alter the levels of TCA cycle metabolites or mitochondrial function as we demonstrated in Figure 4, and supplementation with alpha-ketoglutarate improved outer nuclear layer thickness by only a small amount as observed in Figure 5e. Hence, as we stated in the Results and Discussion, at least in the mouse where Gls is selectively deleted from rod photoreceptors by crossing Glsfl/fl mice with Rho-Cre mice (Glsfl/fl; Rho-Cre+, cKO), Gln’s role in supporting the TCA cycle is not the major mechanism by which rod photoreceptors utilize Gln to suppress apoptosis.

With regards to GLS-driven Gln catabolism providing glutamate (Glu) for synaptic transmission, we again agree with the reviewer that Glu is an important excitatory neurotransmitter, but it is also a key metabolite necessary for the synthesis of glutathione, amino acids, and proteins. As noted and discussed at length in the manuscript, a lack of GLS-driven Gln catabolism in rod photoreceptors leads to reduced levels of oxidized glutathione (Figure 4D) possibly signaling an overall reduction in the biosynthesis of glutathione as Glu is directly and indirectly responsible for its synthesis. Furthermore, Gln and GLS-derived Glu play a central role in the biosynthesis of several nonessential amino acids and proteins. To this end, we see a reduction in the level of Glu, which is the product of the GLS reaction and further confirms the loss of GLS function. We also noted a significant decrease in aspartate (Asp), which can be constructed from the carbons and nitrogens of Gln as discussed at length in the manuscript (Figure 6A). Finally, we noted a significant decrease in global protein synthesis in the cKO retina as compared to the wild-type animal as well (Figure 6E). Therefore, the data suggest that GLS-driven Gln catabolism is critical for amino acid metabolism and protein synthesis and to some degree redox balance; although, the small but statistically significant changes in oxidized glutathione, NADP/NADPH, and redox gene expression may not fully account for the rapid and complete photoreceptor degeneration observed. Future studies are necessary to shed light on the role of redox imbalance in this novel transgenic mouse model.

Glu also plays a role in synaptic transmission, and we considered this scenario as described in Figure 1 – figure supplement 5. Here, the synaptic connectivity between photoreceptors and the inner retina did not demonstrate significant differences in the labeling of photoreceptor synaptic membranes in the outer plexiform layer nor alterations in the labeling of a key protein (Bassoon) in ribbon synapses. These data suggest that the synaptic connectivity between photoreceptors and second-order neurons was unaltered at P14 in the cKO retina, which is the time just prior to rapid photoreceptor degeneration. We agree, though, that to obtain greater insight into the alterations in the ribbon synapse, EM images can be examined. The EM images shown in Figure 1 – figure supplement 4 are from P21 and will be utilized to assess the ribbon synapse for the revised version of the article.

With regards to the ERG changes noted in Figure 2, we agree with the reviewer that a large decrease was noted in the scotopic b-wave at P21 and P42 in the cKO. However, an even larger reduction in the scotopic a-wave was noted at these ages as well. In animal models that disrupt photoreceptor synaptic function (Dick et al. Neuron. 2003; Johnson et al. J Neuroscience. 2007; Haeseleer et al. Nature Neuroscience. 2004; Chang et al. Vis Neurosci. 2006), a more negative ERG pattern is typically observed with the b-wave altered to a much larger degree than the a-wave. Additionally, in these models that disrupt photoreceptor synaptic transmission, the overall structure of the retina with respect to thickness is maintained (Dick et al. Neuron. 2003) or noted to have modest changes in the outer plexiform layer within the first two months of age with the outer nuclear layer not significantly altered until 8-10 months of age (Haeseleer et al. Nature Neuroscience. 2004). In contrast, a rapid decline in the outer nuclear layer thickness was observed in the cKO retina after P14 likely contributing to the ERG changes noted in Figure 2.  Also, Gln is catabolized to Glu primarily by GLS as suggested by the approximately 50% reduction in Glu levels in the cKO retina (Figure 6A), but other enzymes are also capable of catabolizing Gln to Glu, so Glu levels in the rod photoreceptors are unlikely to be zero. Coupling this with the fact that rods are equipped with a self-sufficient Glu recollecting system at their synaptic terminals (Hasegawa et al. Neuron. 2006; Winkler et al. Vis Neurosci. 1999) and that GLS activity is at least two-fold higher in the photoreceptor inner segments, which support energy production and metabolism, than any other layer in the retina (Ross et al. Brain Res. 1987) suggests that altered synaptic transmission secondary to reduced levels of Glu likely does not account in full for the rapid and robust photoreceptor degeneration observed in the cKO retina.

The authors note that the outer segments are shorter but they do not address whether there is a decrease in the number of cones. 

The number of cones will be assessed and provided in the revised version of the article.

Rod-specific Gls ko mice with an inducible promoter were generated by crossing the Pde6g-CreERT2 and homozygous for either the WT or floxed Gls allele (IND-cKO). In Figure 3 the authors document that by western blots and antibody labeling the GLS1 expression is lost in the IND-cKO 10 days post tamoxifen. OCT images show a decrease in the thickness of the outer nuclear layer between 17 and 38 days post-TAM. Ergs should be performed on the animals at 10 and 30 days post TAM, before and after major structural changes in rod photoreceptor cells, to determine if changes in light-stimulated responses are observed. These studies could help to parse out the cause of photoreceptor cell death. 

We agree with the reviewer that the IND-cKO is a useful tool to help parse out the cause of photoreceptor cell death in this model as well as shed light on the role of GLS-driven Gln catabolism in photoreceptor synaptic transmission as discussed at length above. Hence, ERG analyses will be provided for these animals in the revised version of the article.

The studies in Figure 4 were all performed on iCre-Glsflox/flox and control mice at p14, why weren't the IND-cKO mice used for these studies since the findings would not be confounded by development? 

To gain further insight into the role of GLS-driven Gln catabolism in the maintenance of rod photoreceptors as compared to their development/maturation, we will provide ERG and targeted metabolomic analyses of the IND-cKO retina in the revised version of the article.

In all rescue studies, the endpoint was an ONL thickness, which only addressed rod cell death. The authors should also determine whether there are small improvements in the ERG, which would distinguish the role of GLS in preventing oxidative stress. 

Optical coherence tomography (OCT) provides a sensitive in vivo method to detect small changes in retinal thickness without potential artifacts incurred through histological processing. Considering the Gls cKO retina demonstrates significant and rapid photoreceptor degeneration, we wanted to assess pathways that may be critical to photoreceptor survival downstream of GLS-driven Gln catabolism using rescue experiments with pharmacologic treatment or metabolite supplementation. That said, disruption of GLS-driven Gln catabolism may also significantly alter rod photoreceptor function beyond that which is secondary to photoreceptor cell death. As such, changes in ERG will be examined and provided in the revised version of the article for certain rescue experiments that demonstrated a robust change in ONL thickness.

Reviewer #2 (Public Review): 

Summary: 

Photoreceptor neurons are crucial for vision, and discovering pathways necessary for photoreceptor health and survival can open new avenues for therapeutics. Studies have shown that metabolic dysfunction can cause photoreceptor degeneration and vision loss, but the metabolic pathways maintaining photoreceptor health are not well understood. This is a fundamental study that shows that glutamine catabolism is critical for photoreceptor cell health using in vivo model systems. 

Strengths: 

The data are compelling, and the consideration of potential confounding factors (such as glutaminase 2 expression) and additional experiments to examine the synaptic connectivity and inner retina added strength to this work. The authors were also careful not to overstate their claims, but to provide solid conclusions that fit the results and data provided in their study. The findings linking asparagine supplementation and the inhibition of the integrated stress response to glutamine catabolism within the rod photoreceptor cell are intriguing and innovative. Overall, the authors provide convincing data to highlight that photoreceptors utilize various fuel sources to meet their metabolic needs, and that glutamine is critical to these cells for their biomass, redox balance, function, and survival. 

We greatly appreciate the reviewer’s thoughtful comments and time spent reviewing this manuscript.

Weaknesses: 

Recent studies have explored the metabolic "crosstalk" that exists within the mammalian retina, where metabolites are transferred between the various retinal cells and the retinal pigment epithelium. It would be of interest to test whether the conditional knockout mice have changes in metabolism (via qPCR such as shown in Figure 4 - Supplemental Figure 1) within the retinal pigment epithelium that may be contributing to the authors' findings in the neural retina. Additionally, the authors have very compelling data to show that inhibition of eIF2a or supplementation with asparagine can delay photoreceptor death via OCT measurements in their conditional knockout mouse model (Figure 6G, H). However, does inhibition of eIF2a or asparagine adversely impact the WT retina? It would also be impactful to know whether this has a prolonged effect, or if it is short-term, as this would provide strength to potential therapeutic targeting of these pathways to maintain photoreceptor health. 

We agree with the reviewer that metabolic communication in the outer retina is crucial to the function and survival of both photoreceptors and RPE. We will perform qRT-PCR on the eyecups of these mice to assess any changes in the expression of metabolic genes. This data will be provided in the revised manuscript.

We have data demonstrating systemic treatment with ISRIB does not adversely impact the anatomy of the wild-type retina; this data will be included in the revised manuscript as a supplement to Figure 6. Additionally, we have recent data to suggest that the effect of ISRIB extends beyond P21 in the cKO mouse. This data will be included in the revised manuscript.

Reviewer #3 (Public Review): 

Summary: 

The authors explored the role of GLS, a glutaminase, which is an enzyme that catalyzes the conversion of glutamine to glutamate, in rod photoreceptor function and survival. The loss of GLS was found to cause rapid autonomous death of rod photoreceptors. 

Strengths: 

Interesting and novel phenotype. Two types of cre-lines were rigorously used to knockout the Gls gene in rods. Both of the conditional knockouts led to a similar phenotype, i.e. rod death. Histology and ERG were carefully done to characterize the loss of rods over specific ages. A necessary metabolomic study was performed and appreciated. Some rescue experiments were performed and revealed possible mechanisms. 

We thank the reviewer for their comments and appreciation of the methods utilized herein to address the role of GLS-driven Gln catabolism in rod photoreceptors.

Weaknesses: 

No major weaknesses were identified. The mechanism of GLS-loss-induced rod death seems not fully elucidated by this study but could be followed up in the future, and the same for GLS's role in cones.

We agree with the reviewer that the downstream metabolic and molecular mechanisms by which Gln catabolism impacts rod photoreceptor health are not fully elucidated. Defining these mechanisms will advance our understanding of photoreceptor metabolism and identify therapeutic targets promoting photoreceptor resistance to stress. Future studies are underway to uncover these mechanisms. Additionally, while outside the scope of the current manuscript, we have generated mice lacking GLS in cone photoreceptors specifically and are currently elucidating the role of GLS in cone photoreceptor metabolism, function, and survival. These results will be published in a separate manuscript.

eLife assessment

This study is a potentially important contribution to the field of protein biosynthesis pathways and their link to aging, especially regarding the thorough analysis of variation in measures expected to correlate with elongation rate in old and new daughter cells derived from old and new mother cells. However, the imaging results, analysis, and methodologies are incomplete, as in its current form several key questions remain unanswered.

Reviewer #1 (Public Review):

The research by Lin Chao, Chun Kuen Chen, Chao Shi, and Camilla U. Rang addresses the asymmetric distribution of ribosomes in single E. coli cells during aging by time-lapse microscopy, as well as its correlation to protein misfolding. The presented research is an important contribution to the field of protein biosynthesis pathways and their link to aging, especially in regard to the thorough analysis of variation in cells elongation rate in old and new daughter cells derived from old and new mother cells.

Comments on current version:

I thank the authors for their thoughtful responses. Yet the centrality of protein aggregate distribution analysis to this manuscript requires further evidence to support the link to ribosome asymmetrical distribution and aging.

The authors suggest this is beyond the scope of this study. This then requires a major revising of the study, as in its current form, it is one of its main claims.

Author response:

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

Response to reviewers

A general comment was that this study left several key questions unanswered, in particular the causal mechanism for the reported ribosomal distributions.  We have been interested in the evolution of asymmetric bacterial growth and aging for many years. However, a motivational difference is that we are more interested in the evolutionary process, and evolution by natural selection works on the phenotype.  Thus, we wanted to start with the phenotype closest to fitness, appropriately defined for the conditions, work downwards.  We examined first the asymmetry of elongation rates in single cells, then gene products, and now ribosomes.  As we have pointed out, our demonstration of ribosomal asymmetry shows that the phenomenon was not peculiar and unique to the gene products we examined.  Rather, the asymmetry is acting higher up in the metabolic network and likely affecting all genes.  We find such conceptual guidance to be important.  In the ideal world, of course we would have liked to have worked out the causal mechanisms in one swoop.  In a less than ideal situation, it is a subjective decision as where to stop.  We believe that the publication of this manuscript is more than appropriate at this juncture.  We work at the interface of evolutionary theory and microbiology.  Our results could appeal to both fields.  If we attract new researchers, progress could be accelerated.  Could the delay caused by publishing only completed stories slow the rate of discovery?  These questions are likely as old as science (e.g., https://telliamedrevisited.wordpress.com/2021/01/28/how-not-to-write-a-response-to-reviewers/).

We present below our response to specific comments by reviewers.  We have not added a new discussion of papers suggested by Reviewer #1 because we feel that the speculations would have been too unfocused.  We were already criticized for speculation in the Discussion about a link between aggregate size and ribosomal density.

Respond to Major comments by Reviewer #1.

a) Fig. 1 only shows 2 divisions (rather than 3 as per Rev1) to avoid an overly elaborate figure.  We have added text to the figure legend that the old and new poles and daughters in the subsequent 3, 4, 5, 6, and 7 generations can be determined by following the same notations and tracking we presented for generations 1 and 2 in Fig. 1.  For example, if we know the old and new poles of any of the four daughters after 2 divisions (as in Fig. 1), and allow that daughter to elongate, become a mother, and divide to produce 2 “grand-daughters”, the polarity of the grand-daughters can also be determined.

b) Because division times were normalized and analyzed as quartiles, the raw values were never used.  Rather than annotating unused values, we have provided the mean division times in the Material and Methods section on normalization to provide representative values.

c) We did not quantify in our study the changes over generations for three reasons.  First, the sample sizes for the first generations (cohorts of 1, 2, 4, and 8 cells) are statistically small.  Second, and most importantly, cells on an agar pad in a microscope slide, despite being inoculated as fresh exponentially growing cells, experience a growth lag, as all cells transferred to a new physiological condition.  Thus, to be safe, we do not collect data from cohorts 1, 2, 4, and 8 to ensure that our cells are as much as possible physiologically uniform.  Lastly, as we noted in the Material and Methods they also slow down after 7 generations (128 cells).  Thus, we have collected ribosome and length measurements primarily from cohorts 16, 32, 64, and 128.  Measurable cells from the 128 cohort are actually rare because a colony with that many cells often starts to form double layers, which are not measurable.  Most of our measurements came from the 16, 32, and 64 cohorts, in which case a time series would not be meaningful.  Some of these details were not included in our manuscript but have been added to the Material and Methods (Microscopy and time-lapse movies).  For these reasons we have not added a time series as requested by the reviewer.

d) We have added the additional figure as requested, but as a supplement rather than in the main article (Supplemental Materials Fig. S1).  This figure showed the normalized density of ribosomes along the normalized length of old and new daughters.  The density was continuous rather than quartiles.  This figure was included in the original manuscript, but readers recommended that it be removed because the all the analyzed data had been done with quartiles.  Readers felt mislead and confused.

eLife assessment

This valuable manuscript reports on the relationship between GTP hydrolysis parameters and kinase activity of LRRK2, which is associated with Parkinson's disease. The authors provide a detailed accounting of the catalytic efficiency of the ROC GTPase domain of pathogenic variants of LRRK2, in comparison with the wild-type enzyme. The authors propose that phosphorylation of T1343 inhibits kinase activity and influences monomer-dimer transitions, but the experimental evidence is currently incomplete.

Reviewer #1 (Public Review):

Summary:

This study presents careful biochemical experiments to understand the relationship between LRRK2 GTP hydrolysis parameters and LRRK2 kinase activity. The authors report that incubation of LRRK2 with ATP increases the KM for GTP and decreases the kcat. From this they suppose an autophosphorylation process is responsible for enzyme inhibition. LRRK2 T1343A showed no change, consistent with it needing to be phosphorylated to explain the changes in G-domain properties. The authors propose that phosphorylation of T1343 inhibits kinase activity and influences monomer-dimer transitions.

Strengths:

The strengths of the work are the very careful biochemical analyses and interesting results for wild type LRRK2.

Weaknesses:

The conclusions related to the involvement of a monomer-dimer transition are to this reviewer, premature and an independent method needs to be utilized to bolster this aspect of the story.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This study presents careful biochemical experiments to understand the relationship between LRRK2 GTP hydrolysis parameters and LRRK2 kinase activity. The authors report that incubation of LRRK2 with ATP increases the KM for GTP and decreases the kcat. From this they suppose an autophosphorylation process is responsible for enzyme inhibition. LRRK2 T1343A showed no change, consistent with it needing to be phosphorylated to explain the changes in G-domain properties. The authors propose that phosphorylation of T1343 inhibits kinase activity and influences monomer-dimer transitions.

Strengths:

Strengths of the work are the very careful biochemical analyses and interesting result for wild type LRRK2.

Weaknesses:

The conclusions related to involvement of a monomer-dimer transition are to this reviewer, premature and an independent method needs to be utilized to bolster this aspect of the story.

The monomer-dimer transition has been described in detail in our recent preprint Guaitoli et al., 2023 (doi: 10.1101/2023.08.11.549911). Where we in addition to mass-photometry have used blue-native page. Furthermore, to better elucidate the mechanistic impact of the phosphorylation, we have provided AlphaFold3 models. As the new AlphaFold version allows to consider PTMs as well as small molecules, we compared the models of the GDP vs the GTP-state of pT1343 LRRK2. Interestingly, the AF3 model suggests, that the phosphate of the pT1343 is orientated inwards thereby substituting the gamma phosphate (see Supplementary Figure 5). This finding is in well agreement with MD simulations published recently (Stormer et al., 2023, doi: 10.1042/BCJ20230126). As we are determining GTP hydrolysis in a multi turnover situation, the pT1343 might hamper the hydrolysis by competing with GTP re-binding. Final models have been deposited on Zenodo (https://doi.org/10.5281/zenodo.11242230).

Reviewer #2 (Public Review):

As discussed in the original review, this manuscript is an important contribution to a mechanistic understanding of LRRK2 kinase. Kinetic parameters for the GTPase activity of the ROC domain have been determined in the absence/presence of kinase activity. A feedback mechanism from the kinase domain to GTP/GDP hydrolysis by the ROC domain is convincingly demonstrated through these kinetic analyses. However, a regulatory mechanism directly linking the T1343 phosphosite and a monomer/dimer equilibrium is not fully supported. The T1343A mutant has reduced catalytic activity and can form similar levels of dimer as WT. The revised manuscript does point out that other regulatory mechanisms can also play a role in kinase activity and GTP/GDP hydrolysis (Discussion section). The environmental context in cells cannot be captured from the kinetic assays performed in this manuscript, and the introduction contains some citations regarding these regulatory factors. This is not a criticism, the detailed kinetics here are rigorous, but it is simply a limitation of the approach. Caveats concerning effects of membrane localization, Rab/14-3-3 proteins, WD40 domain oligomers, etc... should be given more prominence than a brief (and vague) allusion to 'allosteric targeting' near the end of the Discussion.

We thank the reviewer for the evaluation of the manuscript and suggestions made. With respect to the mentioned caveats regarding the complex regulation of LRRK2 in its native cellular environment by effectors, localization and effector binding, we have revised the discussion, accordingly. We nevertheless, want to emphasize that the phospho-null mutant T1343A leads to an increase in Rab10 phosphorylation in cells, demonstrating a relevance of this regulatory mechanism under near physiological conditions (shown in Figure 6). In addition, to further elucidate the molecular mechanisms of the p-loop phosphorylation at T1343, we have performed AlphaFold3 modelling allowing to include phosphoresidues (see comment above, Supplemental Figure 5).

Specific comments

(1) The revised version is better organized with respect to the significance of monomer/dimer equilibrium and the relevance of the GTP-binding region of ROC domain that encompasses the T1343 phospho-site. The relevance of monomers/dimers of LRRK2 from previous studies is better articulated and readers are able to follow the reasoning for the various mutations.

We thank the reviewer for the positive feedback. 

(2) As a suggestion I would change the following on page 6 to clarify for readers: "...would show no change in kcat and KM values upon in vitro ATP treatment" to:

"...would show no change in kcat and KM values for GTP hydrolysis upon in vitro

ATP treatment"

(3) The levels of dimer in WT (+ATP) and T1343A (+/- ATP) are the same, about 40-45%. These data are cited when the authors state that ATP-induced monomerization is 'abolished' (page 6). My suggestion is to re-phrase this conclusion for consistency with data (Fig 5). For example, one can state that 'ATP incubation does not affect the percentage of dimer for the T1343A variant of LRRK2'. This would be similar to the authors' description of these data on page 8 - 'no difference in dimer formation upon ATP treatment'.

We thank the reviewer for the suggestions. We revised the manuscript accordingly. Changes have been highlighted in the version provided for reviewing purposes.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Minor revisions

-change 'Although functional work on LRRK2 has been made significant progress...' to 'Although there is significant progress toward functional characterization of LRRK2...'

-change 'exact mechanisms' to 'precise mechanisms', and similarly 'exact interplay' to 'precise interplay'

-change 'On a contrary' to 'On the contrary' in Discussion

-change remained to be unchanged' to 'remains unchanged', page 8

We thank the reviewer for having noticed this. We have revised the manuscript accordingly.

eLife assessment

This study provides valuable new insights into insect cognition and problem-solving in bumblebees. The authors present convincing evidence that bumblebees lack causal understanding in a string-pulling task, and find support for bumblebees instead using image-matching for this task.

Reviewer #1 (Public Review):

Summary:

In this paper the researchers aimed to address whether bees causally understand string-pulling through a series of experiments. I first briefly summarize what they did:

- In experiment 1, the researchers trained bees without string and then presented them with flowers in the test phase that either had connected or disconnected strings, to determine what their preference was without any training. Bees did not show any preference.

- In experiment 2, bees were trained to have experience with string and then tested on their choice between connected vs. disconnected string.

- Experiment 3 was similar except that instead of having one option which was an attached string broken in the middle, the string was completely disconnected from the flower.

- In experiment 4, bees were trained on green strings and tested on white strings to determine if they generalize across color.

- In experiment 5, bees were trained on blue strings and tested on white strings.

- In experiment 6, bees were trained where black tape covered the area between the string and the flower (i.e. so they would not be able to see/ learn whether it was connected or disconnected).

- In experiments 2-6, bees chose the connected string in the test phase.

- In experiment 7, bees were trained as in expt 3 and then tested where string was either disconnected or coiled i.e. still being 'functional' but appearing different.

- In experiment 8, bees were trained as before and then tested on string that was in a different coiled orientation, either connected or disconnected.

- In experiments 7 and 8 the bees showed no preference.

Strengths:

I appreciate the amount of work that has gone into these experiments and think they are a nice, thorough set of experiments. I enjoyed reading the paper and felt that it was overall well-written and clear. I think experiment 1 shows that bees do not have an untrained understanding of the function of the string in this context. The rest of the experiments indicate that with training, bees have a preference for unbroken over broken string and likely use visual cues learned during training to make this choice. They also show that as in other contexts, bees readily generalize across different colors.

The 'weaknesses' that I previously listed were dealt with by the authors in the revised version of the manuscript. I think the only point that we disagreed on was relating to the ecological relevance of the task to the bees.

Here is my previous comment:

I think the paper would be made stronger by considering the natural context in which the bee performs this behavior. Bees manipulate flowers in all kinds of contexts, and scrabble with their legs to achieve nectar rewards. Rather than thinking that it is pulling a string, my guess would be that the bee learns that a particular motor pattern within their usual foraging repertoire (scrabbling with legs), leads to a reward. I don't think this makes the behavior any less interesting - in fact, I think considering the behavior through an ecological lens can help make better sense of it.

The authors disagreed, writing the following:

"Here we respectfully disagree. The solving of Rubik s cube by humans could be said to be version of finger movements naturally required to open nuts or remove ticks from fur, but this is somewhat beside the point: it s not the motor<br /> sequences that are of interest, but the cognition involved. A general approach in work on animal intelligence and cognition is to deliberately choose paradigms that are outside the animals daily routines this is what we have done here, in asking whether there is means end comprehension in bee problem solving. Like comparable studies on this question in other animals, the experiments are designed to probe this question, not one of ecological validity."

I think the difference would be that humans know that they are doing a rubik's cube whereas I do not think that the bee knows that it is pulling string- I think the bee thinks that it is foraging on a flower. Therefore, I stand by my statement that I think it's worth considering what the bee is experiencing in this task and how it relates to what it would be doing while foraging. I think that as animal cognition researchers we can design tasks that are distinct from what the animal would naturally encounter to ask specific questions about what they are thinking- but that we can never remove the ecological context since the animal will always be viewing the task through that lens. However, I think this may be a philosophical difference in opinion and I am happy with the manuscript as it stands.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this paper, the researchers aimed to address whether bees causally understand string-pulling through a series of experiments. I first briefly summarize what they did:

- In experiment 1, the researchers trained bees without string and then presented them with flowers in the test phase that either had connected or disconnected strings, to determine what their preference was without any training. Bees did not show any preference.

- In experiment 2, bees were trained to have experience with string and then tested on their choice between connected vs. disconnected string.

- experiment 3 was similar except that instead of having one option which was an attached string broken in the middle, the string was completely disconnected from the flower.

- In experiment 4, bees were trained on green strings and tested on white strings to determine if they generalize across color.

- In experiment 5, bees were trained on blue strings and tested on white strings.

- In experiment 6, bees were trained where black tape covered the area between the string and the flower (i.e. so they would not be able to see/ learn whether it was connected or disconnected).

- In experiments 2-6, bees chose the connected string in the test phase.

- In experiment 7, bees were trained as in experiment 3 and then tested where the string was either disconnected or coiled i.e. still being 'functional' but appearing different.

- In experiment 8, bees were trained as before and then tested on a string that was in a different coiled orientation, either connected or disconnected.

- In experiments 7 and 8 the bees showed no preference.

Strengths:

I appreciate the amount of work that has gone into this study and think it contains a nice, thorough set of experiments. I enjoyed reading the paper and felt that overall it was well-written and clear. I think experiment 1 shows that bees do not have an untrained understanding of the function of the string in this context. The rest of the experiments indicate that with training, bees have a preference for unbroken over broken string and likely use visual cues learned during training to make this choice. They also show that as in other contexts, bees readily generalize across different colors.

Weaknesses:

(1) I think there are 2 key pieces of information that can be taken from the test phase - the bees' first choice and then their behavior across the whole test. I think the first choice is critical in terms of what the bee has learned from the training phase - then their behavior from this point is informed by the feedback they obtain during the test phase. I think both pieces of information are worth considering, but their behavior across the entire test phase is giving different information than their first choice, and this distinction could be made more explicit. In addition, while the bees' first choice is reported, no statistics are presented for their preferences.

We agree with the reviewer that the first choice is critical in terms of what the bumblebees have learned from the training phase. We analyzed the bees’ first choice in Table 1, and we added the tested videos. The entire connected and disconnected strings were glued to the floor, the bees were unable to move either the connected or disconnected strings, and avoid learning behavior during the tests. We added the data of bee's each choice in the Supplementary table.

(2) It seemed to me that the bees might not only be using visual feedback but also motor feedback. This would not explain their behavior in the first test choice, but could explain some of their subsequent behavior. For example, bees might learn during training that there is some friction/weight associated with pulling the string, but in cases where the string is separated from the flower, this would presumably feel different to the bee in terms of the physical feedback it is receiving. I'd be interested to see some of these test videos (perhaps these could be shared as supplementary material, in addition to the training videos already uploaded), to see what the bees' behavior looks like after they attempt to pull a disconnected string.

We added supplementary videos of testing phase. As noted in General Methods, both connected and disconnected strings were glued to the floor to prevent the air flow generated by flying bumblebees’ wings from changing the position of the string during the testing phase. The bees were unable to move either the connected or disconnected strings during the tests, and only attempted to pull them. Therefore, the difference in the friction/weight of pulling the both strings cannot be a factor in the test.

(3) I think the statistics section needs to be made clearer (more in private comments).

We changed the statistical analysis section as suggested by the reviewer.

(4) I think the paper would be made stronger by considering the natural context in which the bee performs this behavior. Bees manipulate flowers in all kinds of contexts and scrabble with their legs to achieve nectar rewards. Rather than thinking that it is pulling a string, my guess would be that the bee learns that a particular motor pattern within their usual foraging repertoire (scrabbling with legs), leads to a reward. I don't think this makes the behavior any less interesting - in fact, I think considering the behavior through an ecological lens can help make better sense of it.

Here we respectfully disagree. The solving of Rubik’s cube by humans could be said to be version of finger-movements naturally required to open nuts or remove ticks from fur, but this is somewhat beside the point: it’s not the motor sequences that are of interest, but the cognition involved. A general approach in work on animal intelligence and cognition is to deliberately choose paradigms that are outside the animals’ daily routines-this is what we have done here, in asking whether there is means-end comprehension in bee problem solving. Like comparable studies on this question in other animals, the experiments are designed to probe this question, not one of ecological validity.

Reviewer #2 (Public Review):

Summary:

The authors wanted to see if bumblebees could succeed in the string-pulling paradigm with broken strings. They found that bumblebees can learn to pull strings and that they have a preference to pull on intact strings vs broken ones. The authors conclude that bumblebees use image matching to complete the string-pulling task.

Strengths:

The study has an excellent experimental design and contributes to our understanding of what information bumblebees use to solve a string-pulling task.

Weaknesses:

Overall, I think the manuscript is good, but it is missing some context. Why do bumblebees rely on image matching rather than causal reasoning? Could it have something to do with their ecology? And how is the task relevant for bumblebees in the wild? Does the test translate to any real-life situations? Is pulling a natural behaviour that bees do? Does image matching have adaptive significance?

We appreciate the valuable comment from the reviewer. Our explanation, which we have now added to the manuscript, is as follows:

“Different flower species offer varying profitability in terms of nectar and pollen to bumblebees; they need to make careful choices and learn to use floral cues to predict rewards (Chittka, 2017). Bumblebees can easily learn visual patterns and shapes of flower (Meyer-Rochow, 2019); they can detect stimuli and discriminate between differently coloured stimuli when presented as briefly as 25 ms (Nityananda et al., 2014). In contrast, causal reasoning involves understanding and responding to causal relationships. Bumblebees might favor, or be limited to, a visual approach, likely due to the efficiency and simplicity of processing visual cues to solve the string-pulling task. ”

As above, it worth noting that our work is not designed as an ecological study, but one about the question of whether causal reasoning can explain how bees solve a string-pulling puzzle. We have a cognitive focus, in line with comparable studies on other animals. We deliberately chose a paradigm that is to some extent outside of the daily challenges of the animal.

Reviewer #3 (Public Review):

Summary:

This paper presents bees with varying levels of experience with a choice task where bees have to choose to pull either a connected or unconnected string, each attached to a yellow flower containing sugar water. Bees without experience of string pulling did not choose the connected string above chance (experiment 1), but with experience of horizontal string pulling (as in the right-hand panel of Figure 4) bees did choose the connected string above chance (experiments 2-3), even when the string colour changed between training and test (experiments 4-5). Bees that were not provided with perceptual-motor feedback (i.e they could not observe that each pull of the string moved the flower) during training still learned to string pull and then chose the connected string option above chance (experiment 6). Bees with normal experience of string pulling then failed to discriminate between connected and unconnected strings when the strings were coiled or looped, rather than presented straight (experiments 7-8).

Weaknesses:

The authors have only provided video of some of the conditions where the bees succeeded. In general, I think a video explaining each condition and then showing a clip of a typical performance would make it much easier to follow the study designs for scholars. Videos of the conditions bees failed at would be highly useful in order to compare different hypotheses for how the bees are solving this problem. I also think it is highly important to code the videos for switching behaviours. When solving the connected vs unconnected string tasks, when bees were observed pulling the unconnected string, did they quickly switch to the other string? Or did they continue to pull the wrong string? This would help discriminate the use of perceptual-motor feedback from other hypotheses.

We added the test videos as suggested by the reviewer, and we added the data for each bee's choice. However, both connected and disconnected strings were glued to the floor, and therefore perceptual-motor feedback was equal and irrelevant between the choices during the test.

The experiments are also not described well, for my below comments I have assumed that different groups of bees were tested for experiments 1-8, and that experiment 6 was run as described in line 331, where bees were given string-pulling training without perceptual feedback rather than how it is described in Figure 4B, which describes bees as receiving string pulling training with feedback.

We now added figures of Experiment 6 and 7 in the Figure 1B, and we mentioned that different groups of bees were tested for Experiments 1-9.

The authors suggest the bees' performance is best explained by what they term 'image matching'. However, experiment 6 does not seem to support this without assuming retroactive image matching after the problem is solved. The logic of experiment 6 is described as "This was to ensure that the bees could not see the familiar "lollipop shape" while pulling strings....If the bees prefer to pull the connected strings, this would indicate that bees memorize the arrangement of strings-connected flowers in this task." I disagree with this second sentence, removing perceptual feedback during training would prevent bees memorising the lollipop shape, because, while solving the task, they don't actually see a string connected to a yellow flower, due to the black barrier. At the end of the task, the string is now behind the bee, so unless the bee is turning around and encoding this object retrospectively as the image to match, it seems hard to imagine how the bee learns the lollipop shape.

We agree with the reviewer that while solving the task in the last step during training, the bees don't actually see a string connected to a yellow flower, due to the black barrier. Since the full shape is only visible after the pulling is completed and this requires the bee to “check back” on the entire display after feeding, to basically conclude “ this is the shape that I need to be looking for later”.

Another possibility is that bumblebees might remember the image of the “lollipop shape” while training the bees in the first step, in which the “lollipop shape” was directly presented to the bumblebee in the early step of the training.

We added the experiment suggested by the reviewer, and the result showed that when a green table was placed behind the string to obscure the “lollipop shape” at any point during the training phase, the bees were unable to identify the connected string. The result further supports that bumblebees learn to choose the connected string through image matching.

Despite this, the authors go on to describe image matching as one of their main findings. For this claim, I would suggest the authors run another experiment, identical to experiment 6 but with a black panel behind the bee, such that the string the bee pulls behind itself disappears from view. There is now no image to match at any point from the bee's perspective so it should now fail the connectivity task.

Strengths:

Despite these issues, this is a fascinating dataset. Experiments 1 and 2 show that the bees are not learning to discriminate between connected and unconnected stimuli rapidly in the first trials of the test. Instead, it is clear that experience in string pulling is needed to discriminate between connected and unconnected strings. What aspect of this experience is important? Experiment 6 suggests it is not image matching (when no image is provided during problem-solving, but only afterward, bees still attend to string connectivity) and casts doubt on perceptual-motor feedback (unless from the bee's perspective, they do actually get feedback that pulling the string moves the flower, video is needed here). Experiments 7 and 8 rule out means-end understanding because if the bees are capable of imagining the effect of their actions on the string and then planning out their actions (as hypotheses such as insight, means-end understanding and string connectivity suggest), they should solve these tasks. If the authors can compare the bees' performance in a more detailed way to other species, and run the experiment suggested, this will be a highly exciting paper

We appreciate the valuable comment from the reviewer. We compared the bees' performance to other species, and conducted the experiment as suggested by the reviewer.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Smaller comments:

Line 64: is the word 'simple' needed here? It could also be explained by more complex forms of associative learning, no?

We deleted “simple”.

Methods:

Line 230: was it checked that this was high-contrast for the bees?

We added the relevant reference in the revised manuscript.

Line 240: how much sucrose solution was present in the flowers?

We added 25 microliters sucrose solution in the flowers. We added the information in the revised manuscript.

Line 266: check grammar.

We checked the grammar as follows: “During tests, both strings were glued to the floor of the arena to prevent the air flow generated by flying bumblebees’ wings from changing the position of the string.”

Statistical analysis:

- What does it mean that "Bees identity and colony were analyzed with likelihood ratio tests"?

Bees identity and colony was set as a random variable. We changed the analysis methods in the revised manuscript, and results of the all the experiments did not changed.

- Line 359: do you mean proportion rather than percentage?

We mean the percentage.

- "the number of total choices as weights" - this should be explained further. This is the number of choices that each bee made? What was the variation and mean of this number? If bees varied a lot in this metric, it might make more sense to analyze their first choice (as I see you've done) and their first 10 choices or something like that - for consistency.

This refers to the total number of choices made by each bumblebee. We added the mean and standard error of each bee’s number of choices in Table 1. Some bees pulled the string fewer than 10 times; we chose to include all choices made by each bee.

- More generally I think the first test is more informative than the subsequent choices, since every choice after their first could be affected by feedback they are getting in that test phase. Or rather, they are telling you different things.

All the bees were tested only once, however, you might be referring to the first choice. We used Chi-square test to analyze the bumblebees’ first choices in the test. It is worth noting that both connected and disconnected strings were glued to the floor. The bees were unable to move either the connected or disconnected strings during the tests, and only attempted to pull them. Therefore,the feedback from pulling either the connected or disconnected strings is the same.

- Line 362: I think I know what you mean, but this should be re-phrased because the "number of" sounds more appropriate for a Poisson distribution. I think what you are testing is whether each individual bee chose the connected or the disconnected string - i.e. a 0 or 1 response for each bee?

We agree with the reviewer that each bee chose the connected or the disconnected string - i.e. a 0 or 1 response for each bee, but not the number. We clarify this as: “The total number of the choices made by each bee was set as weights.” 

- Line 364-365: here and elsewhere, every time you mention a model, make it clear what the dependent and independent variables are. i.e. for the mixed model, the 'bee' is the random factor? Or also the colony that the bee came from? Were these nested etc?

We clarify this in the revised manuscript. The bee identity and colony is the random factor in the mixed model.

- Line 368: "Latency to the first choice of each bee was recorded" - why? What were the hypotheses/ predictions here?

The latency to the first choice was intended to see if the bumblebees were familiarizing with the testing pattern. A shorter delay time might indicate that the bumblebees were more familiar with the pattern.

- Line 371: "Multiple comparisons among experiments were.." - do you mean 'within' experiments? It seems that treatments should not be compared between different experiments.

We mean multiple comparisons among different experiments; we clarify this in the revised manuscript.

Results

Experiment 1: From the methods, it sounded like you both analyzed the bees' first choice and their total no. of choices, but in the results section (and Figure 1) I only see the data for all choices combined here.

In table 1 and in the text you report the number of bees that chose each option on their first choice, but there are no statistical results associated with these results. At the very least, a chi square or binomial test could be run.

Line 138: "Interestingly, ten out of fifteen bees pulled the connected string in their first choice" - this is presented like it is a significant majority of bees, but a chi-square test of 10 vs 5 has a p-value = 0.1967

We used the Chi square test to analyzed of the bees’ first choice. We also added the analyzed data in the Table 1.

Line 143: "It makes sense because the bees could see the "lollipop shape" once they pulled it out from the table." - this feels more like interpretation (i.e. Discussion) rather than results.

We moved the sentence to the discussion.

Line 162: again this feels more like interpretation/ conjecture than results.

We removed the sentence in the results.

Line 184: check grammar.

We checked the grammar. We changed “task” to “tasks”.

Figures

I really appreciated the overview in Figure 5 - though I think this should be Figure 1? Even if the methods come later in eLife, I think it would be nice to have that cited earlier on (e.g. at the start of the results) to draw the reader's attention to it quickly, since it's so helpful. It also then makes the images at the bottom of what is currently Figure 1 make more sense. I also think that the authors could make it clearer in Figure 5 which strings are connected vs disconnected in the figure (even if it means exaggerating the distance more than it was in real life). I had to zoom in quite a bit to see which were connected vs. not. Alternatively, you could have an arrow to the string with the words "connected" "disconnected" the first time you draw it - and similar labels for the other string conditions.

We appreciate the valuable comment from the reviewer. We changed Figure 5 to Figure 2, and Figure 4 to Figure 1. We cited the Figures at the start of the results. We also changed the gap distance between the disconnected strings. Additionally, we added arrows to indicate “connected” and “disconnected” strings in the Figure.

Figure 1 - I think you could make it clearer that the bars refer to experiments (e.g. have an x-axis with this as a label). Also, check the grammar of the y-axis.

We added the experiments number in the Figures. Additionally, we checked the grammar of the y-axis. We changed “percentages” to “parentage”. 

I also think it's really helpful to see the supplementary videos but I think it would be nice to see some examples of the test phase, and not just the training examples.

We added Supplementary videos of the testing phase.

Reviewer #2 (Recommendations For The Authors):

Below are also some minor comments:

L40: "approaches".

We changed “approach” to “approaches”.

L42: but likely mainly due to sampling bias of mammals and birds.

We changed the sentence as follows: String pulling is one of the most extensively used approaches in comparative psychology to evaluate the understanding of causal relationships (Jacobs & Osvath, 2015), with most research focused on mammals and birds, where a food item is visible to the animal but accessible only by pulling on a string attached to the reward (Taylor, 2010; Range et al., 2012; Jacobs & Osvath, 2015; Wakonig et al., 2021).

L64: remove "in this study"

We removed “in this study”.

L64: simple associative learning of what? Isn't your image matching associative too?

We removed “ simple”.

L97: remove "a" before "connected".

We removed “a” before “connected”.

L136-138: but maybe they could still feel the weight of the flower when pulling?

Because both strings were glued to the floor in the test phase, the feedback was the same and therefore irrelevant. This information is noted in the General Methods.

L161: what are these numbers?

We removed the latency in the revised manuscript.

L167/ Table 1: I realise that the authors never tried slanted strings to check if bumblebees used proximity as a cue. Why?

This was simply because we wanted to focus on whether bumblebees could recognize the connectivity of the string.

Discussion: Why did you only control for colour of the string? What if you had used strings with different textures or smells? Unclear if the authors controlled for "bumblebee smell" on the strings, i.e., after a bee had used the string, was the string replaced by a new one or was the same one used multiple times?

We used different colors to investigate featural generalization of the visual display of the string connected to the flower in this task. We controlled for color because it is a feature that bumblebees can easily distinguish.

Both the flowers and the strings were used only once, to prevent the use of chemosensory cues. We clarify this in the revised manuscript.

L182: since what?

We deleted “since” in the revised manuscript.

L182-188: might be worth mentioning that some crows and parrots known for complex cognition perform poorly on broken strings (e.g., https://doi.org/10.1098/rspb.2012.1998 ; https://doi.org/10.1163/1568539X-00003511 ; https://doi.org/10.1038/s41598-021-94879-x ) and Australian magpies use trial and error (https://doi.org/10.1007/s00265-023-03326-6).

We added the following sentences as suggested by the reviewer: “It is worth noting that some crows and parrots known for complex cognition perform poorly on the broken string task without perceptual feedback or learning. For example, New Caledonian crows use perceptual feedback strategies to solve the broken string-pulling task, and no individual showed a significant preference for the connected string when perceptual feedback was restricted (Taylor et al., 2012). Some Australian magpies and African grey parrots can solve the broken string task, but they required a high number of trials, indicating that learning plays a crucial role in solving this task (Molina et al., 2019; Johnsson et al., 2023).”

L193: maybe expand on this to put the task into a natural context?

We added the following sentences as suggested by the reviewer:

“Different flower species offer varying profitability in terms of nectar and pollen to bumblebees; they need to make careful choices and learn to use floral cues to predict rewards (Chittka, 2017). Bumblebees can easily learn visual patterns and shapes of flower (Meyer-Rochow, 2019); they can detect stimuli and discriminate between differently coloured stimuli when presented as briefly as 25 ms (Nityananda et al., 2014). In contrast, causal reasoning involves understanding and responding to causal relationships. Bumblebees might favor, or be limited to, a visual approach, likely due to the efficiency and simplicity of processing visual cues to solve the string-pulling task. ”

L204: is causal understanding the same as means-end understanding?

Means-end understanding is expressed as goal-directed behavior, which involves the deliberate and planned execution of a sequence of steps to achieve a goal. Includes some understanding of the causal relationship (Jacobs & Osvath, 2015; Ortiz et al., 2019). .

L235: this is a very big span of time. Why not control for motivation? Cognitive performance can vary significantly across the day (at least in humans).

Bumblebee motivation is understood to be rather consistent, as those that were trained and tested came to the flight arena of their own volition and were foragers looking to fill their crop load each time to return it to the colony.

L232: what is "(w/w)" ? This occurs throughout the manuscript.

“w/w” represents the weight-to-weight percentage of sugar.

L250: this sentence sounds odd. "containing in the central well.." ?? Perhaps rephrase? Unclear what central well refers to? Did the flowers have multiple wells?

We rephrased the sentence as follows: For each experiment, bumblebees were trained to retrieve a flower with an inverted Eppendorf cap at the center, containing 25 microliters of 50% sucrose solution, from underneath a transparent acrylic table

L268: why euthanise?

The reason for euthanizing the bees is that new foragers will typically only become active after the current ones were removed from the hive.

L270: chemosensory cues answer my concern above. Maybe make it clear earlier.

We moved this sentence earlier in the result.

L273: did different individuals use different pulling strategies? Do you have the data to analyse this? This has been done on birds and would offer a nice comparison.

We analyzed the string-pulling strategies among different individuals, and provided Supplementary Table 1 to display the performances of each individual in different string-pulling experiments.

L365: unclear why both models. Would be nice to see a GLM output table.

The duration of pulling different kinds of strings were first tested with the Shapiro-Wilk test to assess data normality. The duration data that conforms to a normal distribution was compared using linear mixed-effects models (LMM), while the data that deviates from normality were examined with a generalized linear-mixed model (GLMM). We added a GLM and GLMM output table in the revised manuscript.

L377: should be a space between the "." and "This".

We added a space between the “.” and “This”.

L383-390: some commas and semicolons are in the wrong places.

We carefully checked the commas and semicolons in this sentence.

Reviewer #3 (Recommendations For The Authors):

Minor comments

Line 32: seems to be missing a word, suggest "the bumblebees' ability to distinguish".

we added “the” in the revised manuscript.

Line 47: it would be good to reference other scholars here, this is the central focus of all work in comparative psychology.

We added the reference in the revised manuscript.

Line 50-61: I think the string-pulling literature could be described in more detail here, with mention of perceptual-motor feedback loops as a competing hypothesis to means-end understanding (see Taylor et al 2010, 2012). It seems a stretch to suggest that "String-pulling studies have directly tested means-end comprehension in various species", when perceptual-motor feedback is a competing hypothesis that we have positive evidence for in several species.

We mentioned the perceptual-motor feedback in the introduction as follow:

“Multiple mechanisms can be involved in the string-pulling task, including the proximity principle, perceptual feedback and means-end understanding (Taylor et al., 2012; Wasserman et al., 2013; Jacobs & Osvath, 2015; Wang et al., 2020). The principle of proximity refers to animals preferring to pull the reward that is closest to them (Jacobs & Osvath, 2015). Taylor et al. (2012) proposed that the success of New Caledonian crows in string-pulling tasks is based on a perceptual-motor feedback loop, where the reward gradually moves closer to the animal as they pull the strings. If the visual signal of the reward approaching is restricted, crows with no prior string-pulling experience are unable to solve the broken string task (Taylor et al., 2012).

However, when a green table was placed behind the string to obscure the “lollipop” structure during the training, the bees could not see the “lollipop” during the initial training stage or after pulling the string from under the table. In this situation, the bees were unable to identify the connected string, further proving that bumblebees chose the connected string based on image matching.

Line 68: suggest remove 'meticulously'.

We removed “meticulously”.

Line 99: This is an exciting finding, can the authors please provide a video of a bee solving this task on its first trial?

We added videos in the supplementary materials.

Line 133: perceptual-motor feedback loops should be introduced in the introduction.

We introduced perceptual-motor feedback loops in the revised manuscript.

Line 136: please clarify the prior experience of these bees, it is not clear from the text.

We clarified the prior experience of these bees as follow: Bumblebees were initially attracted to feed on yellow artificial flowers, and then trained with transparent tables covered by black tape (S7 video) through a four-step process.

Line 138: from the video it is not possible to see the bee's perspective of this occlusion. Do the authors have a video or image showing the feedback the bees received? I think this is highly important if they wish to argue that this condition prevents the use of both image matching and a perceptual-motor feedback loop.

We prevented the use of image matching: the bees were unable to see the flower moving towards them above the table during the training phase in this condition. But the bees may receive visual image both after pulling the string out from the table and in the initial stages of training in this condition.

Line 147: please clarify what experience these bees had before this test.

We added the prior experience of bumblebees before training as follow: We therefore designed further experiments based on Taylor et al. (2012) to test this hypothesis. Bumblebees were first trained to feed on yellow artificial, and then trained with the same procedure as Experiment 2, but the connected strings were coiled in the test.

Line 155: This is a highly similar test to that used in Taylor et al 2012, have the authors seen this study?

We mentioned the reference in the revised manuscript as follows: We therefore designed further experiments based on Taylor et al. (2012) to test this hypothesis.

Line 183: This sentence needs rewriting "Since the vast majority of animals, including dogs 183 (Osthaus et al., 2005), cats (Whitt et al., 2009), western scrub-jays (Hofmann et al.,2016) and azure-winged magpies (Wang et al., 2019) are failing in such tasks spontaneously".

We changed the sentence as suggested by the reviewer as follow:  Some animals, including dogs (Osthaus et al., 2005), cats (Whitt et al., 2009), western scrub-jays (Hofmann et al., 2016) and azure-winged magpies (Wang et al., 2019) fail in such task spontaneously.

Line 186: "complete comprehension of the functionality of strings is rare" I am not sure the evidence in the current literature supports any animal showing full understanding, can the authors explain how they reach this conclusion?

We wished to say that few animal species could distinguish between connected and disconnected strings without trial and error learning. We revised the sentence as follows:

It is worth noting that some crows and parrots known for complex cognition perform poorly on broken string task without perceptual feedback or learning. For example, New Caledonian crows use perceptual feedback strategies to solve broken string-pulling task, and no individual showed a significant preference for the connected string when perceptual feedback is restricted (Taylor et al., 2012). Some Australian magpies and African grey parrots can solve the broken string task, but it required a high number of trials, indicating that learning plays a crucial role in solving this task (Molina et al., 2019; Johnsson et al., 2023).

Line 190: the authors need to clarify which part of their study provides positive evidence for this conclusion.

We added the evidence for this conclusion as follows: Our findings suggest that bumblebees with experience of string pulling prefer the connected strings, but they failed to identify the interrupted strings when the string was coiled in the test.

Line 265: was the far end of the string glued only?

The entire string was glued to the floor, not just the far ends of the string.

eLife assessment

This study reports important results and new insights into humoral immune responses to Plasmodium falciparum sexual stage proteins. The experiments are based on the use of target-agnostic memory B cell sorting and screening approaches as well as several state-of-the-art technologies. The authors present compelling evidence that one antibody, B1E11K, is cross-reactive with multiple proteins containing glutamate-rich repeats through homotypic interactions, a process similar to what has been observed for Plasmodium circumsporozoite protein repeat-directed antibodies.

Reviewer #2 (Public Review):

This manuscript by Amen, Yoo and Fabra-Garcia et al describes a human monoclonal antibody B1E11K, targeting EENV repeats which are present in parasite antigens such as Pfs230, RESAs and Pf11.1. The authors isolated B1E11K using an initial target agnostic approach for antibodies that would bind gamete/gametocyte lysate which they made 14 mAbs. Following a suite of highly appropriate characterization methods from Western blotting of recombinant proteins to native parasite material, use of knockout lines to validate specificity, ITC, peptide mapping, SEC-MALS, negative stain EM and crystallography, the authors have built a compelling case that B1E11K does indeed bind EENV repeats. In addition, using X-ray crystallography they show that two B1E11K Fabs bind to a 16 aa RESA repeat in a head-to-head conformation using homotypic interactions and provide a separate example from CSP, of affinity-matured homotypic interactions.

The authors have addressed most of our previous comments in their revised manuscript.

One of the main conclusions in the paper is the binding of B1E11K to RESAs which are blood stage antigens that are exported to the infected parasite surface. In the future, it would be interesting to understand if B1E11K mAb binds to the red cell surface of infected blood stage parasites to understand its cellular localization in those stages.

Materials and Methods:<br /> PBMC sampling: While the authors have provided clarification that they obtained informed consent from the PBMC donor, they have not added the ethics approval codes in this section.

Reviewer #3 (Public Review):

The manuscript from Amen et al reports the isolation and characterization of human antibodies that recognize proteins expressed at different sexual stages of Plasmodium falciparum. The isolation approach was antigen agnostic and based on the sorting, activation, and screening of memory B cells from a donor whose serum displays high transmission-reducing activity. From this effort, 14 antibodies were produced and further characterized. The antibodies displayed a range of transmission-reducing activities and recognized different Pf sexual stage proteins. However, none of these antibodies had substantially higher TRA than previously described antibodies.

The authors then performed further characterization of antibody B1E11K, which was unique in that it recognized multiple proteins expressed during sexual and asexual stages. Using protein microarrays, B1E11K was shown to recognize glutamate-rich repeats, following an EE-XX-EE pattern. An impressive set of biophysical experiments were performed to extensively characterize the interactions of B1E11K with various repeat motifs and lengths. Ultimately, the authors succeeded in determining a 2.6 A resolution crystal structure of B1E11K bound to a 16AA repeat-containing peptide. Excitingly, the structure revealed that two Fabs bound simultaneously to the peptide and made homotypic antibody-antibody contacts. This had only previously been observed before with antibodies directed against CSP repeats.

Overall I found the manuscript to be very well written. Strengths of the manuscript include the target-agnostic screening approach and the thorough characterization of antibodies. The demonstration that B1E11K is cross-reactive to multiple proteins containing glutamate-rich repeats, and that the antibody recognizes the repeats via homotypic interactions, similar to what has been observed for CSP repeat-directed antibodies, should be of interest to many in the field.

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review):

Summary: 

In this paper, the authors used target agnostic MBC sorting and activation methods to identify B cells and antibodies against sexual stages of Plasmodium falciparum. While they isolated some Mabs against PFs48/45 and PFs230, two well-known candidates for "transmission blocking" vaccines, these antibodies' efficacies, as measured by TRA, did not perform as well as other known antibodies. They also isolated one cross-reactive mAb to proteins containing glutamic acid-rich repetitive elements, that express at different stages of the parasite life cycle. They then determined the structure of the Fab with the highest protein binder they could determine through protein microarray, RESA, and observed homotypic interactions. 

Strengths: 

-  Target agnostic B cell isolation (although not a novel methodology). 

-  New cross-reactive antibody with some "efficacy" (TRA) and mechanism (homotypic interactions) as demonstrated by structural data and other biophysical data. 

Weaknesses: 

The paper lacks clarity at times and could benefit from more transparency (showing all the data) and explanations. 

We have added the oocyst count data from the SMFA experiments as Supplementary Table 2, and ELISA binding curves underlying Figure 4B as Supplementary Figure 5.

In particular: 

- define SIFA 

- define TRAbs 

We have carefully gone through the manuscript and have introduced abbreviations at first use, removed unnecessary abbreviations and removed unnecessary jargon to increase readability.

- it is not possible to read the Figure 6B and C panels. 

We regret that the labels in Supplementary Figures 6 and 7 were of poor quality and have now included higher resolution images to solve this issue.

Reviewer #2 (Public Review): 

This manuscript by Amen, Yoo, Fabra-Garcia et al describes a human monoclonal antibody B1E11K, targeting EENV repeats which are present in parasite antigens such as Pfs230, RESAs, and 11.1. The authors isolated B1E11K using an initial target agnostic approach for antibodies that would bind gamete/gametocyte lysate which they made 14 mAbs. Following a suite of highly appropriate characterization methods from Western blotting of recombinant proteins to native parasite material, use of knockout lines to validate specificity, ITC, peptide mapping, SEC-MALS, negative stain EM, and crystallography, the authors have built a compelling case that B1E11K does indeed bind EENV repeats. In addition, using X-ray crystallography they show that two B1E11K Fabs bind to a 16 aa RESA repeat in a head-to-head conformation using homotypic interactions and provide a separate example from CSP, of affinity-matured homotypic interactions. 

There are some minor comments and considerations identified by this reviewer, These include that one of the main conclusions in the paper is the binding of B1E11K to RESAs which are blood stage antigens that are exported to the infected parasite surface. It would have been interesting if immunofluorescence assays with B1E11K mAb were performed with blood-stage parasites to understand its cellular localization in those stages. 

In the current manuscript, we provide multiple lines of evidence that B1E11K binds (with high affinity) to repeats that are present in RESAs, i.e. through micro-array studies, in vitro binding experiments such as Western blot, ELISA and BLI, and through X-ray crystallography studies on B1E11k – repeat peptide complexes. Taken together, we think we provide compelling evidence that B1E11k binds to repeats present in RESA proteins. We do agree that studies on the function of this mAb against other stages of the parasite could be of interest, but as our manuscript focuses on the sexual stage of the parasite, we feel that this is beyond scope of the current work. However, this line of inquiry will be strongly considered in follow up studies.   

Reviewer #3 (Public Review): 

The manuscript from Amen et al reports the isolation and characterization of human antibodies that recognize proteins expressed at different sexual stages of Plasmodium falciparum. The isolation approach was antigen agnostic and based on the sorting, activation, and screening of memory B cells from a donor whose serum displays high transmission-reducing activity. From this effort, 14 antibodies were produced and further characterized. The antibodies displayed a range of transmission-reducing activities and recognized different Pf sexual stage proteins. However, none of these antibodies had substantially lower TRA than previously described antibodies. 

The authors then performed further characterization of antibody B1E11K, which was unique in that it recognized multiple proteins expressed during sexual and asexual stages. Using protein microarrays, B1E11K was shown to recognize glutamate-rich repeats, following an EE-XX-EE pattern. An impressive set of biophysical experiments was performed to extensively characterize the interactions of B1E11K with various repeat motifs and lengths. Ultimately, the authors succeeded in determining a 2.6 A resolution crystal structure of B1E11K bound to a 16AA repeat-containing peptide. Excitingly, the structure revealed that two Fabs bound simultaneously to the peptide and made homotypic antibody-antibody contacts. This had only previously been observed with antibodies directed against CSP repeats. 

Overall I found the manuscript to be very well written, although there are some sections that are heavy on field-specific jargon and abbreviations that make reading unnecessarily difficult. For instance, 'SIFA' is never defined. 

We have carefully gone through the manuscript and have introduced abbreviations at first use, removed unnecessary abbreviations and removed unnecessary jargon to increase readability.

Strengths of the manuscript include the target-agnostic screening approach and the thorough characterization of antibodies. The demonstration that B1E11K is cross-reactive to multiple proteins containing glutamate-rich repeats, and that the antibody recognizes the repeats via homotypic interactions, similar to what has been observed for CSP repeat-directed antibodies, should be of interest to many in the field. 

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Figure 1 - why only gametes ELISA and Spz or others?  

The volumes of the single B cell supernatants were too small to screen against multiple antigens/parasite stages. As we aimed to isolate antibodies against the sexual stages of the parasite, our assay focused on this stage and supernatants were not tested against other stages. Furthermore, we screened for reactivity against gametes as TRA mAbs likely target gametes rather than other forms of sexual stage parasites.

Figure 2 A 

(a) Wild type (WT) and Pfs48/45 knock-out (KO) gametes.

(b) I am a bit confused about what GMT is vs Pfs48/45 

We have changed the column titles in Figure 2A to “wild-type gametes” and “Pfs48/45 knockout gametes” to improve clarity.  

(c) Binding is high % why is it red? 

We chose to present the results in a heatmap format with a graded color scale, from strong binders in red to weak binders in green. It has now been clarified in the legend of the figure. 

Please state acronyms clearly 

TRA - transmission reducing activity 

SMFA - standard membrane feeding assay 

We have added the full terms to clarify the acronyms.

1123- VRC01 (not O1)

We have corrected this.

Figure 2 C bottom panels, clarify which ones are TRAbs (Assuming the Mabs with over 80% TRA at 500 ug/ml) (right gel) and the ones that are not (left gel)? 

In the Western blot in Figure 2c, we have marked the antibodies with >80% TRA with an asterisk.

Furthermore, we have replaced ‘TRAbs’ by ‘mAbs with >80% TRA at 500 µg/mL’ in the figure legend.

ITC show the same affinity of the Fab to the 2 peptides but not the ELISA, not the BLI/SPR would be more appropriate. Any potential explanation?  

The way binding affinity is determined across various techniques can result in slight differences in determined values. For instance, ELISAs utilize long incubation times with extensive washing steps and involve a spectroscopic signal, isothermal titration calorimetry (ITC) uses calorimetric signal at different concentration equilibriums to extract a KD, and BLI determines kinetic parameters for KD determination. Discrepancies in binding affinities between orthologous techniques have indeed been observed previously in the context of peptide-antibody binding (e.g. PMID: 34788599).

Despite this, regardless of technique, the relative relationships in all three sets of data is the same - higher binding affinity is observed to the longer P2 peptide. This is the main takeaway of the section. As the reviewer suggests, BLI is likely the most appropriate readout here and is the only value explicitly mentioned in the main text. We primarily use ITC to support our proposed binding stoichiometry which is important to substantiate the SEC-MALS and nsEM data in Figure 4H-I. We added the following sentences to help reinforce these points: “The determined binding affinity from our ITC experiments (Table 1) differed from our BLI experiments (Fig. 4D and 4E), which can occur when measuring antibody-peptide interactions. Regardless, our data across techniques all trend toward the same finding in which a stronger binding affinity is observed toward the longer RESA P2 (16AA) peptide.”

Figure 5C - would be helpful to have the peptide sequence above referring to what is E1, E2 etc... 

We added two panels (Figure 5C-D) showcasing the binding interface that shows the peptide numbering in the context of the overall complex. We hope that this will help better orient the reader. 

Figure S4 - maybe highlight in different colors the EENVV, EEIEE, Etc, etc 

Repeats found in the sequence of the various proteins in Figure S4 have now been highlighted with different colors.

Line 163 - why 14 mabs if 11 wells? Isn't it 1 B cell per well? The authors should explain right away that some wells have more than 1 B cell and some have 1 HC, 1LC, and 1 KC. 

We agree that this was somewhat confusing and have modified the text which now reads: “We obtained and cloned heavy and light chain sequences for 11 out of 84 wells. For three wells we obtained a kappa light chain sequence and for five wells a lambda light chain sequence. For three wells we obtained both a lambda and kappa light chain sequence suggesting that either both chains were present in a single B cell or that two B cells were present in the well. For all 14 wells we retrieved a single heavy chain sequence. Following amplification and cloning, 14 mAbs, from 11 wells, were expressed as full human IgG1s (Table S1) (Dataset S1).”

Line 166-167 - were they multiple HC (different ones) as well when Lambda and kappa were present?

This is not clear at first. 

We clarified this point in the text, see also comment above.

Line 177 - expressed Pfs48/45 and Pfs230, is it lacking both or just Pfs48/45 (as stated on line 172)? 

Pfs48/45 binds to the gamete surface via a GPI anchor, while Pfs230 is retained to the surface through binding to Pfs48/45. Hence, the Pfs48/45 knockout parasite will therefore also lack surfacebound Pfs230. We have added a sentence to the Results clarifying this: “The mAbs were also tested for binding to Pfs48/45 knock-out female gametes, which lack surface-bound Pfs48/45 and Pfs230”.

Show the ELISA data used to calculate EC50 in Figure 3. 

ELISA binding curves are now shown as Figure S5.

Line 313-315 - what if you reverse, capture the Fab (peptide too small even if biotinylated?) 

As anticipated by the Reviewer, immobilizing the Fab and dipping into peptide did not yield appreciable signal for kinetic analysis and thus the experiment from this setup is not reported. 

Line 341 - add crystal structure 

This has now been added.

There is a bit too much speculation in the discussion. For e.g. "The B1C5L and B1C5K mAbs were shown to recognize Domain 2 of Pfs48/45 and exhibited moderate potency, as previously described for Abs with such specificity (27). These 2 mAbs were isolated from the same well and shared the same heavy chain; their three similar characteristics thus suggest that their binding is primarily mediated by the heavy chain". Actual data will reinforce this statement. 

As B1C5L and B1C5K recognized domain 2 of Pfs48/45 with similar affinity, this strongly suggests that binding is mediated though the heavy chain. Structural analysis could confirm this statement, but this is out of the scope of this study.  

Reviewer #2 (Recommendations For The Authors): 

Figure 1: This figure provides a description of the workflow. To make it more relevant for the paper, the authors could add relevant numbers as the workflow proceeds. 

(a) For example, how many memory B cells were sorted, how many supernatants were positive, and then how many mAbs were produced? These numbers can be attached to the relevant images in the workflow. 

We modified the figure to include the numbers. 

(b) For the "Supernatant screening via gamete extract ELISA", please change to "Supernatant screening via gamete/gametocyte extract ELISA". 

We modified the statement as suggested. 

Line 155: The manuscript states that 84 wells reacted with gamete/gametocyte lysate. The following sentence states that "Out of the 21 supernatants that were positive...". Can the authors provide the summary of data for all 84 wells or why focus on only 21 supernatants? 

We screened all supernatants against gamete lysate, and only a subset against gametocyte lysate. In total, we found 84 positive supernatants that were reactive to at least one of the two lysates. 21 of those 84 positive were screened against both lysates. We have modified the text to clarify the numbers:

“After activation, single cell culture supernatants potentially containing secreted IgGs were screened in a high-throughput 384-well ELISA for their reactivity against a crude Pf gamete lysate (Fig. S1B). A subset of supernatants was also screened against gametocyte lysate (S1C). In total, supernatants from 84 wells reacted with gamete and/or gametocyte lysate proteins, representing 5.6% of the total memory B cells. Of the 21 supernatants that were screened against both gamete and gametocyte lysates, six recognized both, while nine appeared to recognize exclusively gamete proteins, and six exclusively gametocyte proteins.”

Please note that all 84 positive wells were taken forward for B cell sequencing and cloning. 

Line 171: SIFA is introduced for the first time and should be completely spelled out.

We have corrected this. 

Figure 2: 

(a) In Figure 2A, can you change the column title from "% pos KO GMT" to "% pos Pfs48/45 KO GMT"?

We have changed the column titles.  

(b) In Figure 2B, the SMFA results have been converted to %TRA. Can the authors please provide the raw data for the oocyst counts and number of mosquitoes infected in Supplementary Materials? 

We have added oocyst count data in Table S2, to which we refer in the figure legend. 

(c) For Figure 2F, the authors do have other domains to Pfs230 as described in Inklaar et al, NPJ Vaccines 2023. An ELISA/Western to the other domains could identify the binding site for B2C10L, though we appreciate this is not the central result of this manuscript. 

We thank the reviewer for this suggestion. We are indeed planning to identify the target domain of B2C10L using the previously described fragments, but agree with the reviewer that this not the focus of the current manuscript and decided to therefore not include it in the current report.

Line 116: The word sporozoites appears in subscript and should be corrected to be normal text. 

We have corrected this.

Line 216: Typo "B1E11K" 

We have corrected this.

Materials and Methods: 

(a) PBMC sampling: Please add the ethics approval codes in this section. 

Donor A visited the hospital with a clinical malaria infection and provided informed consent for collection of PBMCs. We have modified the method section to clarify this. 

“Donor A had lived in Central Africa for approximately 30 years and reported multiple malaria infections during that period. At the time of sampling PBMCs, Donor A had recently returned to the Netherlands and visited the hospital with a clinical malaria infection. After providing informed consent, PBMCs were collected, but gametocyte prevalence and density were not recorded.”

(b) Gamete/Gametocyte extract ELISA: Can the authors please provide the concentration of antibodies used for the positive and negative controls (TB31F, 2544, and 399) 

We have added the concentrations for these mAbs in the methods section.

Recombinant Pfs48/45 and Pfs230 ELISA: Please state the concentration or molarity used for the coating of recombinant Pfs48/45 and Pfs230CMB. 

We have added the concentrations, i.e. 0.5 µg/mL, to the methods section.

Western Blotting: The protocol states that DTT was added to gametocyte extracts (Line 594), but Western Blots in Figures 2 and 3 were performed in non-reducing conditions. Please confirm whether DTT was added or not. 

Thank you for noting this. We did not use DTT for the western blots and have removed this line from the methods section.

Reviewer #3 (Recommendations For The Authors): 

Below are a few minor comments to help improve the manuscript. 

(1) In Figure 4E, are the BLI data fit to a 1:1 binding model? The fits seem a bit off, and from ITC and X-ray studies it is known that 2 Fabs bind 1 peptide. The second Fab should presumably have higher affinity than the first Fab since the second Fab will make interactions with both the peptide and the first Fab. It may be better to fit the BLI data to a 2:1 binding model. 

The 2:1 (heterogeneous ligand) model assumes that there are two different independent binding sites. However, the second binding event described is dependent on the first binding event and thus this model also does not accurately reflect the system. Given that there is not an ideal model to fit, we instead are careful about the language used in the main text to describe these results. Additionally, we also include a sentence to the results section to ensure that the proper findings/interpretations are highlighted: “…our data all trend toward the same finding in which a stronger binding affinity is observed toward the longer RESA P2 (16AA) peptide.”

(2) The sidechain interactions shown in Figures 5C and D could probably be improved. The individual residues are just 'floating' in space, causing them to lack context and orientation. 

We added two panels (Fig. 5C-D) showcasing the binding interface that shows the peptide numbering in the context of the overall complex. We hope that this will help orient the reader.  

(3) The percentage of Ramachandran outliers should be listed in Table 2. Presumably, the value is 0.2%, but this is omitted in the current table. 

Table 2 has been modified to include the requested information explicitly.

eLife assessment

The ThermoMaze represents a valuable tool to control the rest/exploration states of an animal. The data, collected and analyzed using solid and validated methodology, demonstrate its use in addressing previously elusive questions. This will facilitate future work with more in-depth analysis of place cell activity to further support for some of the claims.

Reviewer #1 (Public Review):

Summary:

This manuscript introduced a new behavioral apparatus to regulate the animal's behavioral state naturally. It is a thermal maze where different sectors of the maze can be set to different temperatures; once the rest area of the animal is cooled down, it will start searching for a warmer alternative region to settle down again. They recorded with silicon probes from the hippocampus in the maze and found that the incidence of SWRs was higher at the rest areas and place cells representing a rest area were preferentially active during rest-SWRs as well but not during non-REM sleep.

Strengths:

The maze can have many future applications, e.g., see how the duration of waking immobility can influence learning, future memory recall, or sleep reactivation. It represents an out-of-the-box thinking to study and control less-studies aspects of the animals' behavior.

Weaknesses:

The impact is only within behavioral research and hippocampal electrophysiology.

Author response:

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

Reviewer #1 (Public Review):

This manuscript introduced a new behavioral apparatus to regulate the animal's behavioral state naturally. It is a thermal maze where different sectors of the maze can be set to different temperatures; once the rest area of the animal is cooled down, it will start searching for a warmer alternative region to settle down again. They recorded with silicon probes from the hippocampus in the maze and found that the incidence of SWRs was higher at the rest areas and place cells representing a rest area were preferentially active during rest-SWRs as well but not during non-REM sleep.

We thank the reviewer for carefully reading our manuscript and providing useful and constructive comments.

Strengths:

The maze can have many future applications, e.g., see how the duration of waking immobility can influence learning, future memory recall, or sleep reactivation. It represents an out-of-the-box thinking to study and control less-studies aspects of the animals' behavior.

Weaknesses:

The impact is only within behavioral research and hippocampal electrophysiology.

We agree with this assessment but would like to add that the intersection of electrophysiological recordings in behaving animals is a very large field. Behavioral thermoregulation is a hotly researched area also by investigators using molecular tools as well. The ThermoMaze can be used for juxtacellular/intracellular recordings in behaving animals. Restricting the animal’s movement during these recordings can improve the length of recording time and recorded single unit yield in these experiments. 

Moreover, the fact that animals can sleep within the task can open up new possibilities to compare the role of sleep in learning without having to move the animal from a maze back into its home cage. The cooling procedure can be easily adapted to head-fixed virtual reality experiments as well.

I have only a few questions and suggestions for future analysis if data is available.

Comment-1: Could you observe a relationship between the duration of immobility and the preferred SWR activation of place cells coding for the current (SWR) location of the animal? In the cited O'Neill et al. paper, they found that the 'spatial selectivity' of SWR activity gradually diminished within a 2-5min period, and after about 5min, SWR activity was no longer influenced by the current location of the animal. Of course, I can imagine that overall, animals are more alert here, so even over more extended immobility periods, SWRs may recruit place cells coding for the current location of the animal.

We thank the reviewer for raising this question, which is a fundamental issue that we attempted to address using the ThermoMaze. First, we indeed observed persistent place-specific firing of CA1 neurons for up to around 5 minutes, which was the maximal duration of each warm spot epoch, as shown by the decoding analysis (based on firing rate map templates constructed during SPW-Rs) in Figure 5C and D. However, we did not observe above-chance-level decoding of the current position of the animal during sharp-wave ripples using templates constructed during theta, which aligns with previous observation that CA1 neurons during “iSWRs” (15–30 s time windows surrounding theta oscillations) did not show significant differences in their peak firing rate inside versus outside the place field (O’Neil et al., 2006). We reasoned that this could be potentially explained by a different (although correlated, see Figure 5E) neuronal representation of space during theta and during awake SPW-R.

Comment-2: Following the logic above, if possible, it would be interesting to compare immobility periods on the thermal maze and the home cage beyond SWRs, as it could give further insights into differences in rest states associated with different alertness levels. E.g., power spectra may show a stronger theta band or reduced delta band compared to the home cage.

If we are correct the Reviewer would like to know whether the brain state of the animal was similar in the ThermoMaze (warm spot location) and in the home cage during immobility. A comparison of the time-evolved power spectra shows similar changes from walking to immobility in both situations without notable differences. This analysis was performed on a subset of animals (n = 17 sessions in 7 mice) that were equipped with an accelerometer (home cage behavior was not monitored by video). We detected rest epochs that lasted at least 2 seconds during wakefulness in both the home cage and ThermoMaze. Using these time points we calculated the event-triggered power spectra for the delta and theta band (±2 s around the transition time) and found no difference between the home cage and ThermoMaze (Suppl. Fig. 4D).

Prompted by the Reviewer’s question, we further quantified the changes in LFP in the two environments. We did not find any significant change in the frequencies between 1-40 Hz during Awake periods, but we did find higher delta power (1-4 Hz) in some animals in the ThermoMaze (Suppl. Fig. 4A, B). 

We have also quantified the delta and theta power spectra in the few cases, when the warm spot was maintained, and the animal fell asleep. The time-resolved spectra classified the brain state as NREM, similar to sleeping in the home cage. Both delta and theta power were higher in the ThermoMaze following Awake-NREM transitions (±30 seconds around the transition, Suppl. Fig. 4C). It might well be that immobility/sleep outside the mouse’s nest might reflect some minor (but important) differences but our experiments with only a single camera recording do not have the needed resolution to reveal minor differences in posture.

We added these results to the revised Supplementary material (Suppl. Fig. 4).

Comment-3: Was there any behavioral tracking performed on naïve animals that were placed the first time in the thermal maze? I would expect some degree of learning to take place as the animal realizes that it can find another warm zone and that it is worth settling down in that area for a while. Perhaps such a learning effect could be quantified.

Unfortunately, we did not record videos during the first few sessions in the ThermoMaze. Typically, we transferred a naïve animal into the ThermoMaze for an hour on the first day to acclimatize them to the environment. This was performed without video analysis. In addition, because the current version of the maze is relatively small (20 x 20 cm), the animal usually walked around the edges of the maze before settling down at a heated warm spot. It appeared to us that there was only a very weak drive to learn the sequence and location of the warm spot, and therefore we did not quantified learning in the current experiment. We agree with the reviewer that in future studies, it will be interesting to explore whether the ThermoMaze could be adapted to a land-version of the Morris water maze by increasing the size of the maze and performing more controlled behavioral training and testing.

Comment-4: There may be a mislabeling in Figure 6g because the figure does not agree with the result text - the figure compares the population vector similarly of waking SWR vs sleep SWRs to exploration vs waking SWR and exploration vs sleep SWRs.

We thank the reviewer for raising the point, we have updated the labels accordingly.

Reviewer #2 (Public Review):

In this manuscript, Vöröslakos and colleagues describe a new behavioural testing apparatus called ThermoMaze, which should facilitate controlling when a mouse is exploring the environment vs. remaining immobile. The floor of the apparatus is tiled with 25 plates, which can be individually heated, whereas the rest of the environment is cooled. The mouse avoids cooled areas and stays immobile on a heated tile. The authors systematically changed the location of the heated tile to trigger the mouse's exploratory behaviours. The authors showed that if the same plate stays heated longer, the mouse falls into an NREM sleep state. The authors conclude their apparatus allows easy control of triggering behaviours such as running/exploration, immobility and NREM sleep. The authors also carried out single-unit recordings of CA1 hippocampal cells using various silicone probes. They show that the location of a mouse can be decoded with above-chance accuracy from cell activity during sharp wave ripples, which tend to occur when the mouse is immobile or asleep. The authors suggest that consistent with some previous results, SPW-Rs encode the mouse's current location and any other information they may encode (such as past and future locations, usually associated with them).

We thank the reviewer for carefully reading our manuscript and providing useful and constructive comments.

Strengths:

Overall, the apparatus may open fruitful avenues for future research to uncover the physiology of transitions from different behavioural states such as locomotion, immobility, and sleep. The setup is compatible with neural recordings. No training is required.

Weaknesses:

I have a few concerns related to the authors' methodology and some limitations of the apparatus's current form. Although the authors suggest that switching between the plates forces animal behaviour into an exploratory mode, leading to a better sampling of the enclosure, their example position heat maps and trajectories suggest that the behaviour is still very stereotypical, restricted mostly to the trajectories along the walls or the diagonal ones (between two opposite corners). This may not be ideal for studying spatial responses known to be affected by the stereotypicity of the animal's trajectories. Moreover, given such stereotypicity of the trajectories mice take before and after reaching a specific plate, it may be that the stable activity of SWR-P ripples used for decoding different quadrants may be representing future and/or past trajectories rather than the current locations suggested by the authors. If this is the case, it may be confusing/misleading to call such activity ' place-selective firing', since they don't necessarily encode a given place per se (line 281).

We agree with the reviewer that the current version of the ThermoMaze does not necessarily motivate the mice to sample the entire maze during warm spot transitions. However, we did show correlational evidence that neuronal firing during awake sharp-wave ripples is place-selective. Both firing rate ratios and population vectors of CA1 neurons showed a reliable correlation between those during movement and awake sharp-wave ripples (Figure 5 E and F), indicating that spatial coding during movement persists into awake SWR-P state. This finding rejects the hypothesis that neuronal firing during ripples throughout the Cooling sub-session encodes past/future trajectories, which could be explained by a lack of goal-directed behavior in order to perform the task. We hope to test whether such place-specific firing during ripples can be causally involved in maintaining an egocentric representation of space in a future study.

Besides, we have attempted to motivate the animal to visit the center of the maze during the Cooling sub-session. Moving the location of warm spots from the corners can shape the animals’ behavior and promote more exploration of the environment as we show in Suppl. Fig. 5. We agree with the Reviewer that the current size of the ThermoMaze poses these limitations. However, an example future application could be to warm the floor of a radial-arm maze by heating Peltier elements at the ends of maze arms and center in an otherwise cold room, allowing the experimenter to induce ambulation in the 1-dimensional arms, followed by extended immobility and sleep at designated areas.

Another main study limitation is the reported instability of the location cells in the Thermomaze. This may be related to the heating procedure, differences in stereotypical sampling of the enclosure, or the enclosure size (too small to properly reveal the place code). It would be helpful if the authors separate pyramidal cells into place and non-place cells to better understand how stable place cell activity is. This information may also help to disambiguate the SPW-R-related limitations outlined above and may help to solve the poor decoding problem reported by the authors (lines 218-221).

The ThermoMaze is a relatively small enclosure (20 x 20 cm) compared to typical 2D arenas (60 x 60 cm) used in hippocampal spatial studies. Due to the small environment, one possibility is that CA1 neurons encode less spatial information and only a small number of place cells could be found. Therefore, we identified place cells in each sub-session. We found 40.90%, 45.32%, and 41.26% of pyramidal cells to be place cells in the Pre-cooling, Cooling, and Post-cooling sub-sessions, respectively. Furthermore, we found on average 17.36% of pyramidal neurons pass the place cell criteria in all three sub-sessions in a daily session. Therefore, the strong decorrelation of spatial firing maps across sub-sessions cannot be explained by poor recording quality or weak neuronal encoding of spatial information but is potentially due to changes in environmental conditions.

Some additional points/queries:

Comment-1: Since the authors managed to induce sleeping on the warm pads during the prolonged stays, can they check their hypothesis that the difference in the mean ripple peak frequency (Fig. 4D) between the home cage and Thermomaze was due to the sleep vs. non-sleep states?

In response to the reviewer’s comment, we compared the ripple peak frequency that occurred during wakefulness and NREM epochs in the home cage and ThermoMaze (n = 7 sessions in 4 mice). We found that the peak frequency of the awake ripples was higher compared to both home cage and ThermoMaze NREM sleep (one-way ANOVA with Tukey’s posthoc test, ripple frequencies were: 171.63 ± 11.69, 172.21 ± 11.86, 168.19 ± 11.10 and 168.26 ± 11.08 Hz mean±SD for home cage awake, ThermoMaze awake, home cage NREM and ThermoMaze NREM conditions, p < 0.001 between awake and NREM states). We added this quantification to the revised manuscript.

Author response image 1.

NREM sleep either in home cage or in ThermoMaze affects ripple mean peak frequency similarly.

Comment-2: How many cells per mouse were recorded? How many of them were place cells? How many place cells at the same time on average? What are the place field size, peak, and mean firing rate distributions in these various conditions? It would be helpful if they could report this.

For each animal on a given day, the average number of cells recorded was 57.5, which depended on the electrodes and duration after implantation. We first applied peak firing rate and spatial information thresholds to identify place cells in each sub-session (see more details in the revised Methods section for place cell definition). We found 40.90%, 45.32%, and 41.26% of pyramidal cells to be place cells in the Pre-cooling, Cooling, and Post-cooling sub-sessions respectively. Furthermore, we found on average 17.36% of pyramidal neurons pass the place cell criteria in all three sub-sessions in a daily session.

For place cells identified in each sub-session, their place fields size is on average 61.03, 79.86, and 57.51 cm2 (standard deviation = 60.13, 69.98, and 49.64 cm2; Pre-cooling, Cooling, and Post-cooling correspondingly). A place field was defined to be a contiguous region of at least 20 cm2 (20 spatial bins) in which the firing rate was above 60% of the peak firing rate of the cell in the maze (Roux and Buzsaki et al., 2017). A place field also needs to contain at least one bin above 80% of the peak firing rate in the maze. With such definition, the average place field peak firing rate is 5.84, 5.22, and 6.48 Hz (standard deviation = 5.11, 4.65, and 5.83 Hz) and the average mean firing rate within the place fields is 4.54, 4.05, and 5.07 Hz (standard deviation = 4.00, 3.60, and 4.60).

We would like to point out that these values depend strongly on the definition of place fields, which vary widely across studies. We reason that the ThermoMaze paradigm induced place field remapping which has been reported to occur upon changes in the environment such as visual cues (Leutgeb et al., 2009). We hypothesize that temperature gradient is an important aspect among the environmental cues, thus remapping is expected. Overall, we did not aim for biological discoveries in the first presentation of the ThermoMaze. Instead, our limited goal was the detailed description of the method and its validation for behavioral and physiological experiments.

References

(1) Mizuseki K, Royer S, Diba K, Buzsáki G. Activity dynamics and behavioral correlates of CA3 and CA1 hippocampal pyramidal neurons. Hippocampus. 2012 Aug;22(8):1659-80. doi: 10.1002/hipo.22002. Epub 2012 Feb 27. PMID: 22367959; PMCID: PMC3718552.

(2) Skaggs WE,McNaughton BL,Gothard KM,Markus EJ. 1993. An information-theoretic approach to deciphering the hippocampal code. In: SJ Hanson, JD Cowan, CL Giles, editors. Advances in Neural Information Processing Systems, Vol. 5. San Francisco, CA: Morgan Kaufmann. pp 1030–1037.

(3) Roux L, Hu B, Eichler R, Stark E, Buzsáki G. Sharp wave ripples during learning stabilize the hippocampal spatial map. Nat Neurosci. 2017 Jun;20(6):845-853. doi: 10.1038/nn.4543. Epub 2017 Apr 10. PMID: 28394323; PMCID: PMC5446786.

(4) Markus, E.J., Barnes, C.A., McNaughton, B.L., Gladden, V.L. & Skaggs, W.E. Spatial information content and reliability of hippocampal CA1 neurons: effects of visual input. Hippocampus 4, 410–421 (1994).

eLife assessment

Based on analyses of retinae from genetically modified mice, and from wild-type ground squirrel and macaque, employing microscopic imaging, electrophysiology, and pharmacological manipulations, this valuable study on the role of Cav1.4 calcium channels in cone photoreceptor cells (i) shows that the expression of a Cav1.4 variant lacking calcium conductivity supports the development of cone synapses beyond what is observed in the complete absence of Cav1.4, and (ii) indicates that the cone pathway can partially operate even without calcium flux through Cav1.4 channels, thus preserving behavioral responses under bright light. The evidence for the function of Cav1.4 protein in synapse development is convincing and in agreement with a closely related earlier study by the same authors on rod photoreceptors. The mechanism of compensation of Cav1.4 loss by Cav3 remains unclear but appears to involve post-transcriptional processes. As congenital Cav1.4 dysfunction can cause stationary night blindness, this work relates to a wide range of neuroscience topics, from synapse biology to neuro-ophthalmology.

Public Review (Joint Version of all Reviewers)

Cav1.4 calcium channels control voltage-dependent calcium influx at photoreceptor synapses, and congenital loss of Cav1.4 function causes stationary night blindness CSNB2. Based on a broad portfolio of methodological approaches - genetic mouse models, immunolabeling and microscopic imaging, serial block-face-SEM, ERGs, and electrophysiology - the authors show that cone photoreceptor synapse development is strongly perturbed in the absence of Cav1.4 protein, and that expression of a nonconducting Cav1.4 channel mitigates these perturbations. Further data indicate that Cav3 channels are present, which, according to the authors, may compensate for the loss of Cav1.4 calcium currents and thus maintain cone synaptic transmission. These data, which are in agreement with a similar study by the same authors on rod photoreceptor synapses, help to explain what functional defects exactly cause CSNB2 and why it is accompanied by only mild visual impairment.

The strengths of the present study are its conceptual and experimental soundness, the broad spectrum of cutting-edge methodological approaches pursued, and the convincing differential analysis of mutant phenotypes. Weaknesses mainly concern the fact that the mechanism by which Cav3 channels might partially compensate for the loss of Cav1.4 calcium currents remains unclear.

Author response:

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

Intro. 

47-48 rewrite sentence

This sentence has been rewritten as: Photoreceptor synapses are specialized with a vesicle-associated ribbon organelle and postsynaptic neurites of horizontal and bipolar cells that invaginate deep within the terminal

Results 

Major comment. Lines 100-103 

The new rod data presented here looks like an n = 1. Neither the Results section nor Supp Fig S1, describe the number of cells used. Nor do the authors offer a statistical description with averages, etc.. In addition, the single traces are much improved over their previous study (Maddox et al eLife 2020), but the authors have not described any new approach or trick that improved their rod Ica. Neither Methods section nor Supp section describes the procedure for patching rods (solutions, or Vh which is critical for assessing T-type currents). 

Suggestion, if more data exists, then present it. Otherwise, drop the argument. 

The recording methodology for recording rods was like that for cones and this has been clarified in the Methods section (lines 725-752). Averaged data (n= at least 5 per group) and statistical analyses have been added to Fig.S1 (renamed Figure 2-Figure Supplement 1), and clearly show that no Ca2+ currents are present in the KI rods.

Supp Fig S2. The legend needs to be fixed. Conversion to PDF file may have created these formatting errors. 

This has been corrected (renamed Figure 3-Figure Supplement 2).

Fig 8 a. The position of the light stimulus bar in the KO panel appears to be out of place, shifted too far to the left. 

This has been corrected.

Major comments. 219-221 

The use of Fluo3-AM is not properly stated here. The text reads "cone pedicles filled with the Ca2+ indicator Fluo3". The wording used could be wrongly interpreted as: whole-cell filling of the cones via patch electrode. However, the Methods section describes bathing the retina in Fluo3-AM, which presumably fills PRs, HCs tips, Mueller glia and bpc dendrites. The Results section should acknowledge that the retina was loaded with Fluo3-AM. 

The cell types, and their processes (Muellers, HCs, bpc, PRs), present in a cone pedicle ROI will likely contribute to the Fluo3 readout of Ca2+ in the OPL, because 1) the EM images in Fig 7 highlight how interdigitated the processes are with the presynapse, 2) all express Cav channels, and many if not all express L-Type Cavs in their processes (glia, HC, on-bcs and PRs), and 3) all are depolarized with the addition of high extracellular KCl. The inclusion of Isradipine will inhibit L-type Cavs on pre- and post-synaptic targets, failing to specifically isolate PR Ca2+. Furthermore, Glu Receptor blockers are used here, which would be a great idea if the cones were stimulated with light; however, KCl bypasses the excitatory synaptic pathway and depolarizes all processes within the ROI. Hence, all cellular parts in the ROI will potentially contribute to Fluo3-Ca2+ signals. 

Suggestions for presentation of these findings. Ultimately your conclusion is suitable " 233 to 234...... Taken together, our results suggest that Cav3 channels nominally support Ca2+ signals and synaptic transmission in cones of G369i KI mice". The dramatic reduction in Fluo3-Ca2+ signals in the OPL G369i retinas (Fig 9) is a valuable finding for the following reasons: 1) the results do not show a clear compensation from intracellular stores that could potentially supersede the T-type currents in the G369i (which is an argument you make), and 2) there is a massive loss of Ca2+ influx in the OPL of G369i retinas. Since G369i is specific to the PRs, and only cones are present in the mutant G369i, the loss of Fluo3-Ca2+ signal in the mutant ROI reflects in large part loss of cone Fluo3-Ca2+ signals. Your findings illustrate the severity of the mutation, which has also been addressed in the various electro-physio sections of the MS. 

Figure 9 also needs to be more clear about 1) the loading of the cells with AM-dye, and 2) the presence of glia, HCs and bc dendrites in the PNA demarcated ROIs. 

We regret that we did not make this more clear, but our Fluo 3 loading protocol of whole retina followed by vertical slicing allowed for loading primarily of photoreceptors in the portion of the outer retina that we imaged. We clarified this with the following edit to the text (lines 220-226):

“To test if the diminished HC light responses correlated with lower presynaptic Ca2+ signals in G369i KI cones, we performed 2-photon imaging of vertical slices prepared from whole retina that was incubated  with the Ca2+ indicator Fluo3-AM and  Alexa-568-conjugated peanut agglutinin (PNA) to demarcate regions of interest (ROIs) corresponding to cone pedicles. With this approach Fluo3 fluorescence was detected only in photoreceptors and ganglion cells and not inner retinal cell-types (e.g., horizontal cells, bipolar cells, Mueller cell soma). Thus, Ca2+ signals reported by Fluo3 fluorescence near PNA-labeling originated primarily from cones.”

We also note that given the considerably larger volume of the cone pedicle relative to the postsynaptic neurites of horizontal and bipolar cells, as well as neighboring glia, it seems unlikely that the latter would contribute significantly to the isradipine-sensitive Ca2+ signal measured in the ROI above the PNA labeling. Moreover, to our knowledge the contribution of Cav1 L-type channels to postsynaptic Ca2+ signals in the dendritic tips of horizontal cells and bipolar cells has not been demonstrated.

Author response:

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

Reviewer #1 (Public Review):

Major shortcomings include the unusual normalization strategies used for many experiments and the lack of quantification/statistical analyses for several experiments. Because of these omissions, it is difficult to conclude that the data justify the conclusions. The significance of the data presented is overstated, as many of the experiments presented confirm/support previously published work. The study provides a modest advance in the understanding of the complex issue of SHH membrane extraction.

Major shortcomings include the unusual normalization strategies used for many experiments and the lack of quantification/statistical analysis for several experiments.

This statement is not correct for the revised manuscript: The normalization strategies used are clearly described in the manuscript and are not unusual. Each experiment is now statistically analyzed.

The significance of the data presented is overstated, as many of the experiments presented confirm/support previously published work.

As reviewer 2 correctly points out, there are many competing models for Hedgehog release. Our study cannot possibly support them all - the reviewer's statement is therefore misleading. In fact, our careful biochemical analysis of the mechanistics of Dispatched- mediated Shh export supports only two of them: The model of proteolytic processing of Shh lipid anchors (shedding) and the model of lipoprotein-mediated Shh transport. In contrast, our study does not support the predominant model of Dispatched-mediated extraction of dual-lipidated Shh and delivery to Scube2, which is currently thought to act as a soluble Shh chaperone. We also do not support Dispatched function in Shh endocytic recycling and cytoneme loading, or any of the other models such as exosome-mediated or micelle Shh transport.

Reviewer #2 (Public Review):

A novel and surprising finding of the present study is the differential removal of Shh N- or C- terminal lipid anchors depending on the presence of HDL and/or Disp. In particular, the identification of a non-palmitoylated but cholesterol-modified Shh variant that associates with lipoproteins is potentially important. The authors use RP-HPLC and defined controls to assess the properties of processed forms of Shh, but their precise molecular identity remains to be defined. One caveat is the heavy reliance on overexpression of Shh in a single cell line. The authors detect Shh variants that are released independently of Disp and Scube2 in secretion assays, but these are excluded from interpretation as experimental artifacts. Therefore, it would be important to demonstrate key findings in cells that endogenously secrete Shh.

We would like to respond as follows:

The authors use RP-HPLC and defined controls to assess the properties of processed forms of Shh, but their precise molecular identity remains to be defined.

This is the original reviewers statement regarding our original manuscript submission. We believe that the biochemical and functional data presented in the VOR clearly describe the molecular identity of solubilized Shh: it is monolipidated, lipoprotein-associated, and highly biologically active in two established Shh bioassays.

One caveat is the heavy reliance on overexpression of Shh in a single cell line.

As stated by reviewer 1, the strength of our work is the use of a bicistronic SHH-Hhat system to consistently generate doubly lipidated ligand to determine the amount and lipidation status of SHH released into cell culture media. This unique system therefore eliminates the artifacts of protein overexpression. We have also added two other cell lines to our VOR that produce the same results (including Panc1 cells that endogenously produce Shh, Supplementary Figure 1).

The authors detect Shh variants that are released independently of Disp and Scube2 in secretion assays, but these are excluded from interpretation as experimental artifacts.

As the reviewer correctly points out, these variants are released independently of Disp and Scube2, both of which are known as essential release factors in vivo. These variants are therefore by definition experimental artifacts. The forms we have included in our analysis are the alternative forms that are clearly dependent on Dispatched and Scube2 for their release - as shown in the first figure in the manuscript, and in pretty much every other figure after that.

---

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

Reviewer #1 (Public Review):

Key shortcomings include the unusual normalization strategies used for many experiments and the lack of quantification/statistical analyses for several experiments.

In the updated version of the paper, we have addressed all of this reviewer's criticisms. Most importantly, we have performed several additional experiments to address the concern that unusual normalization strategies were used in our paper and that quantification and statistical analyses were lacking for several experiments. We have now analyzed the full set of release conditions for Shh and engineered proteins from Disp-expressing n.t. control cells and Disp-/- cells both in the presence and absence of Scube2 (Figure 1A'-D', Figure 2E added to the paper, Figure 3B'-D', Figure 5C and Figure S2F-H). Previously, we had only quantified protein release from n.t. controls and Disp-/- cells in the presence but not in the absence of Scube2 under serum-depleted conditions. Quantifications of serum-free protein release and Shh release under conditions ranging from 0.05% FCS to 10% FCS were completely missing from the earlier versions of the manuscript, but have now been added to our paper. In addition, we have reanalyzed all of the data sets in the above figures, as well as Figures 2C and S1B, to address the issue of "unusual normalization strategies": unlike previous assays in which the highest amount of protein detected in the media was set to 100% and all other proteins in that experiment were expressed relative to that value, we now directly compare the relative amounts of cellular and corresponding solubilized proteins as a method to quantify release without the need for data normalization (Figs. 1A'-D', 2C,E, 3B'-D', E, 5C, Fig. S1B, S2F-H).

We have also repeated the qPCR analyses in C3H10T1/2 cells and now show that the same Shh/C25AShh activities can be observed when using another Shh responsive cell line, NIH3T3 cells (Fig. 4B, 6B, fig. S5B).

We would like to point out that if the criticism refers to the presentation of our RP-HPLC and SEC data, the normalization of the strongest eluted protein signal to 100% for all proteins tested is necessary to put their behavior in a clearer relationship. This is because only the relative positions of protein elution, and not their amounts, are important in these experiments.

The significance of the data provided is overstated because many of the presented experiments confirm/support previously published work.

To mitigate the first reviewer's comment that the significance of the data presented is overstated, we now clearly distinguish between our novel results and the known aspect of Hh release on lipoproteins throughout our paper. We now clearly describe what is new and important in our paper: First, contrary to the general perception in the field, Disp and Scube2 are not sufficient to solubilize Shh, casting doubt on the currently accepted model that Scube2 accepts dual-lipidated Shh from Disp and transports it to the receptor Ptch. Second, lipoproteins shift dual Shh processing to N-terminal peptide processing only to generate different soluble Hh forms with different activities (as shown in Figure 4C). Third, and again contrary to popular belief, this new release mode does not inactivate Shh, as we now show in two established cellular assays for Hh biofunction (Figures 4A-C, 5B'', 6B and S5C-G). Fourth, and most importantly, we show that spatiotemporally controlled, Disp-, Scube2- and HDL-mediated Shh release absolutely requires dual lipidation of the membrane-associated Shh precursor prior to its release. This finding (as shown in Figures 1 and S2) changes the interpretation of previously published in vivo data that have long been interpreted as evidence for the requirement of dual Shh lipidation for full receptor binding and activation.

The study provides a modest advance in our understanding of the complex issue of Shh membrane extraction.

Although we agree that our results integrate our novel observations into previously established concepts of Hh release and trafficking, we also hope that our data cast well-founded doubt on the current view that the issue of Hh release and trafficking is largely resolved by the model of Disp-mediated Shh hand-over to Scube2 and then to Ptch, which requires interactions with both Shh lipids. Our data show that this is clearly not the case in the presence of lipoproteins. Thus, the significance of our data is that models of Shh lipid-regulated signaling to Ptch obtained using the dual-lipidated Shh precursor prior to its Disp- and Scube2-mediated conversion into a delipidated or monolipidated, HDL-associated soluble ligand are likely to describe a non-physiological interaction. Instead, our work describes a highly bioactive soluble ligand with only one lipid still attached, which has not been described before in the literature. The in vivo endpoint analyses presented in Fig. S8 suggest that this new protein variant is likely to play an important role during development.

Reviewer #2 (Public Review):

The precise molecular identity (of the released Shh) remains to be defined.

We would like to respond that the direct comparison of soluble proteins and their well-defined double-lipidated precursors side-by-side in the same experiment, as shown in our paper, determines all relevant molecular changes in the Shh release process. Most importantly, we show by SDS-PAGE and RP-HPLC that HDL restricts Shh processing to the N-terminus and that the absence of HDL results in double processing of Shh during its release. We also show by SEC that the C-terminus binds the protein to HDL. In addition, the fly experiments confirm the requirement for N-terminal Hh processing, but not for processing of the C-terminal peptide, and suggest that the N-terminal Cardin-Weintraub sequence replaced by the functionally blocking tag represents the physiological cleavage site.

It would be important to demonstrate key findings in cells that secrete Shh endogenously.

We now confirm the key findings of our study in Panc1 cells that endogenously produce and secrete Shh: As shown in Fig. S1D, we find that soluble proteins are processed but retain the C-cholesterol, which we now directly confirm by RP-HPLC (Fig. S4F-H). The in vivo analyses shown in Fig. S8 suggest that the key finding - that N-terminal but not C-terminal Hh shedding is required for release - can be supported, at least in the fly: here, Hh variants impaired in their ability to be processed N-terminally strongly repress the endogenous protein, whereas the same protein impaired in its ability to be processed C-terminally does not.

The authors detect Shh variants that are expressed independently of Disp and Scube2 in secretion assays, but are excluded from interpretation as experimental artifacts.

We agree with the reviewer's criticism that the amounts of Shh released independently of Disp and Scube2 in secretion assays were not quantified and analyzed statistically to justify their proposed status as not physiologically relevant. We now show that these forms are indeed secretion artifacts (Fig. 3E and Fig. S2F-H show quantification of the lower electrophoretic mobility protein fraction (i.e., the "top" band representing the double-lipidated soluble protein fraction)) because this fraction is released independently of Disp and Scube2.

eLife assessment

This study uses a deep neural network approach to challenge the role of spatially selective neurons like place, head or border cells for position decoding. The findings are important as they suggest that such functional cell types may emerge naturally from object recognition in complex visual environments, but are neither necessary, nor particularly critical for position decoding. However, direct evidence supporting this conclusion remains incomplete.

Author response:

We thank the reviewers for their engagement and constructive comments. This provisional response aims to clarify key misconceptions, address major criticisms, and outline our revision plans.

A primary concern of the reviewers appears to be our model's limitations in addressing a broad range of empirical findings. This, however, misinterprets our core contribution. Our work centers on a cautionary tale that before advocating for newly discovered cell types and their purported special roles in spatial cognition—an approach prevalent in the field—such claims must be tested against alternative (null) hypotheses that may contradict intuitive expectations. We present such an alternative hypothesis regarding spatial cells and their assumed privileged roles. We show that key findings in the field - spatial “cell types”,  arise in a set of null models without spatial grounding (including untrained variants) despite the models not being a model for spatial processing, and we also found that they had no privileged role for representing spatial information.

Our proposal is not a new model attempting to explain the brain, and therefore we do not aim to capture every empirical finding. Indeed, we would not expect an object recognition model (and its untrained variant) with no explicit spatial grounding to account for all phenomena in spatial cognition. This underscores our key point: if there exists a basic, spatially agnostic model that can explain certain degrees of empirical findings using criteria from the literature (i.e. place, head-direction and border cells), what implications does this have for the more complex theories and models proposed as underlying mechanisms of special cell types?

Regarding concerns about the limited scope and generalizability of our setting, we will clarify that we considered multiple DNN architectures, both trained and untrained, on multiple decoding tasks (position, head direction, and nearest-wall distance). We plan to extend our experiments further as detailed in the revision plan below.

Further, there was a methodological concern about using a linear decoder on a fixed DNN for spatial decoding tasks being a form of "hacking". However, linear readout is standard practice in neuroscience to characterize information available in a neural population. Moreover, our tests on untrained networks also showed spatial decoding capabilities, suggesting it's not solely due to the linear readout.

For our full revision plan:

(1) We will revise the manuscript to better reflect these above points, clarifying our paper's stance and improving the writing to reduce misconceptions.

(2) We will address individual public reviews in more detail.

(3) We intend to address key reviewer recommendations, focusing on better situating our work within the broader context of the existing literature whilst emphasizing the null hypothesis perspective.

(4) In general, we will consider additional aspects of the literature and conduct new experiments to strengthen the relevance of our work to existing work. We highlight a number of potential experiments which we believe can address reviewer concerns:

a. Blurring the visual inputs to DNNs to match rodent perception.

b. Vary environmental settings to verify whether our findings are more

generalizable (which we predict to be the case).

c. Vary the environment to assess remapping effects, which will strengthen the

connection of our work to the literature.

Reviewer #1 (Public Review):

Summary:<br /> This study investigated spatial representations in deep feedforward neural network models (DDNs) that were often used in visual tasks. The authors create a three-dimensional virtual environment, and let a simulated agent randomly forage in a smaller two-dimensional square area. The agent "sees" images of the room within its field of view from different locations and heading directions. These images were processed by DDNs. Analyzing model neurons in DDNs, they found response properties similar to those of place cells, border cells and head direction cells in various layers of deep nets. A linear readout of network activity can recover key spatial variables. In addition, after removing neurons with strong place/border/head direction selectivity, one can still decode these spatial variables from the remaining neurons in the DNNs. Based on these results, the authors argue that that the notion of functional cell types in spatial cognition is misleading.

Strengths:<br /> This paper contains interesting and original ideas, and I enjoy reading it. Most previous studies (e.g., Banino, Nature, 2018; Cueva & Wei, ICLR, 2018; Whittington et al, Cell, 2020) using deep network models to investigate spatial cognition mainly relied on velocity/head rotation inputs, rather than vision (but see Franzius, Sprekeler, Wiskott, PLoS Computational Biology, 2007). Here, the authors find that, under certain settings, visual inputs alone may contain enough information about the agent's location, head direction and distance to the boundary, and such information can be extracted by DNNs. If confirmed, this is potentially an interesting and important observation.

Weaknesses:<br /> While the findings reported here are interesting, it is unclear whether they are the consequence of the specific model setting, and how well they would generalize. Furthermore, I feel the results are over-interpreted. There are major gaps between the results actually shown and the claim about the "superfluousness of cell types in spatial cognition". Evidence directly supporting the overall conclusion seems to be weak at the moment.

Major concerns:

(1) The authors reported that, in their model setting, most neurons throughout the different layers of CNNs show strong spatial selectivity. This is interesting and perhaps also surprising. It would be useful to test/assess this prediction directly based on existing experimental results. It is possible that the particular 2-d virtual environment used is special. The results will be strengthened if similar results hold for other testing environments.

In particular, examining the pictures shown in Fig. 1A, it seems that local walls of the 'box' contain strong oriented features that are distinct across different views. Perhaps the response of oriented visual filters can leverage these features to uniquely determine the spatial variable. This is concerning because this is a very specific setting that is unlikely to generalize.

(2) Previous experimental results suggest that various function cell types discovered in rodent navigation circuits persist in dark environments. If we take the modeling framework presented in this paper literally, the prediction would be that place cells/head direction cells should go away in darkness. This implies that key aspects of functional cell types in the spatial cognition are missing in the current modeling framework. This limitation needs to be addressed or explicitly discussed.

(3) Place cells/border cell/ head direction cells are mostly studied in the rodent's brain. For rodents, it is not clear whether standard DNNs would be good models of their visual systems. It is likely that rodent visual system would not be as powerful in processing visual inputs as the DNNs used in this study.

(4) The overall claim that those functional cell types defined in spatial cognition are superfluousness seems to be too strong based on the results reported here. The paper only studied a particular class of models, and arguably, the properties of these models have a major gap to those of real brains. Even though, in the DNN models simulated in this particular virtual environment, (i) most model neurons have strong spatial selectivity; (ii) removing model neurons with the strongest spatial selectivity still retain substantial spatial information, why this is relevant to the brain? The neural circuits may operate in a very different regime. Perhaps a more reasonable interpretation of the results would be: these results raise the possibility that those strongly selective neurons observed in the brain may not be essential for encoding certain features, as something like this is observed in certain models. It is difficult to draw definitive conclusions about the brain based on the results reported.

Reviewer #2 (Public Review):

Summary:<br /> The authors aim at challenging the relevance of cell populations with characteristic selectivity for specific aspects of navigation (e.g. place cells, head direction and border cells) in the processing of spatial information. Their claim is that such cells naturally emerge in any system dealing with the estimation of position in an environment, without the need for a special involvement of these cells in the computations. In particular the work shows how when provided with spatial error signals, networks designed for invariant object recognition spontaneously organize the activity in their hidden layers into a mixture of spatially selective cells, some of them passing classification criteria for place, head direction or border cells. Crucially, these cells are not necessary for position decoding, nor are they the most informative when it comes to the performance of the network in reconstructing spatial position from visual scenes. These results lead the authors to claim that focusing on the classification of specific cell types is hindering rather than helping advancement in the understanding of spatial cognition. In fact they claim that the attention should rather be pointed at understanding highly-dimensional population coding, regardless of its direct interpretability or its appeal to human observers.

Strengths:<br /> Methodologically the paper is consistent and convincingly support the author claims regarding the role of cell types in coding for spatial aspects of cognition. It is also interesting how the authors leverage on established machine learning systems to provide a sort of counter-argument to the use of such techniques to establish a parallel between artificial and biological neural representations. In the recent past similar applications of artificial neural networks to spatial navigation have been directed at proving the importance of specific neural substrates (take for example Banino et al. 2018 for grid cells), while in this case the same procedure is used to unveil them as epiphenomena, so general and unspecific to be of very limited use in understanding the actual functioning of the neural system. I am quite confident that this stance regarding the role of place cells and co. could gather large sympathy and support in the greater part of the neuroscience community, or at least among the majority of theoretical neuroscientists with some interest in the hippocampus and higher cognition.

Weaknesses:<br /> My criticism of the paper can be articulated in three main points:<br /> - What about grid cells? Grid cells are notably not showing up in the analyses of the paper. But they surely can be considered as the 'mother' of all tailored spatial cells of the hippocampal formation. Are they falling outside the author's assessment of the importance of this kind of cells? Some discussion of the place grid cells occupy in the vision of the authors would greatly help.<br /> - The network used in the paper is still guided by a spatial error signal, and the network is trained to minimize spatial decoding error. In a sense, although object classfication networks are not designed for spatial navigation, one could say that the authors are in some way hacking this architecture and turning it into a spatial navigation one through learning. I wonder if their case could be strengthened by devising a version of their experiment based on some form of self-supervised or unsupervised learning.<br /> - The last point is more about my perception of the community studying hippocampal functions, rather than being directed at the merits of the paper itself. My question is whether the paper is fighting an already won battle. That is whether the focus on the minute classification of response profiles of cells in the hippocampus is in fact already considered an 'old' approach, very useful for some initial qualitative assessments but of limited power when asked to provide deeper insight into the functioning of hippocampal computations (or computations of any other brain circuit).

Reviewer #3 (Public Review):

Summary:<br /> In this paper, the authors demonstrate the inevitably of the emergence of some degree of spatial information in sufficiently complex systems, even those that are only trained on object recognition (i.e. not "spatial" systems). As such, they present an important null hypothesis that should be taken into consideration for experimental design and data analysis of spatial tuning and its relevance for behavior.

Strengths:<br /> The paper's strengths include the use of a large multi-layer network trained in a detailed visual environment. This illustrates an important message for the field: that spatial tuning can be a result of sensory processing. While this is a historically recognized and often-studied fact in experimental neuroscience, it is made more concrete with the use of a complex sensory network. Indeed, the manuscript is a cautionary tale for experimentalists and computational researchers alike against blindly applying and interpreting metrics without adequate controls.

Weaknesses:<br /> However, the work has a number of significant weaknesses. Most notably: the degree and quality of spatial tuning is not analyzed to the standards of evidence historically used in studies of spatial tuning in the brain, and the authors do not critically engage with past work that studies the sensory influences of these cells; there are significant issues in the authors' interpretation of their results and its impact on neuroscientific research; the ability to linearly decode position from a large number of units is not a strong test of spatial information, nor is it a measure of spatial cognition; and the authors make strong but unjustified claims as to the implications of their results in opposition to, as opposed to contributing to, work being done in the field.

The first weakness is that the degree and quality of spatial tuning that emerges in the network is not analyzed to the standards of evidence that have been used in studies of spatial tuning in the brain. Specifically, the authors identify place cells, head direction cells, and border cells in their network and their conjunctive combinations. However, these forms of tuning are the most easily confounded by visual responses, and it's unclear if their results will extend to forms of spatial tuning that are not. Further, in each case, previous experimental work to further elucidate the influence of sensory information on these cells has not been acknowledged or engaged with.

For example, consider the head direction cells in Figure 3C. In addition to increased activity in some directions, these cells also have a high degree of spatial nonuniformity, suggesting they are responding to specific visual features of the environment. In contrast, the majority of HD cells in the brain are only very weakly spatially selective, if at all, once an animal's spatial occupancy is accounted for (Taube et al 1990, JNeurosci). While the preferred orientation of these cells are anchored to prominent visual cues, when they rotate with changing visual cues the entire head direction system rotates together (cells' relative orientation relationships are maintained, including those that encode directions facing AWAY from the moved cue), and thus these responses cannot be simply independent sensory-tuned cells responding to the sensory change) (Taube et al 1990 JNeurosci, Zugaro et al 2003 JNeurosci, Ajbi et al 2023).

As another example, the joint selectivity of detected border cells with head direction in Figure 3D suggests that they are "view of a wall from a specific angle" cells. In contrast, experimental work on border cells in the brain has demonstrated that these are robust to changes in the sensory input from the wall (e.g. van Wijngaarden et al 2020), or that many of them are not directionally selective (Solstad et al 2008).

The most convincing evidence of "spurious" spatial tuning would be the emergence of HD-independent place cells in the network, however, these cells are a small minority (in contrast to hippocampal data, Thompson and Best 1984 JNeurosci, Rich et al 2014 Science), the examples provided in Figure 3 are significantly more weakly tuned than those observed in the brain, and the metrics used by the authors to quantify place cell tuning are not clearly defined in the methods, but do not seem to be as stringent as those commonly used in real data. (e.g. spatial information, Skaggs et al 1992 NeurIPS).

Indeed, the vast majority of tuned cells in the network are conjunctively selective for HD (Figure 3A). While this conjunctive tuning has been reported, many units in the hippocampus/entorhinal system are *not* strongly hd selective (Muller et al 1994 JNeurosci, Sangoli et al 2006 Science, Carpenter et al 2023 bioRxiv). Further, many studies have been done to test and understand the nature of sensory influence (e.g. Acharya et al 2016 Cell), and they tend to have a complex relationship with a variety of sensory cues, which cannot readily be explained by straightforward sensory processing (rev: Poucet et al 2000 Rev Neurosci, Plitt and Giocomo 2021 Nat Neuro). E.g. while some place cells are sometimes reported to be directionally selective, this directional selectivity is dependent on behavioral context (Markus et al 1995, JNeurosci), and emerges over time with familiarity to the environment (Navratiloua et al 2012 Front. Neural Circuits). Thus, the question is not whether spatially tuned cells are influenced by sensory information, but whether feed-forward sensory processing alone is sufficient to account for their observed turning properties and responses to sensory manipulations.

These issues indicate a more significant underlying issue of scientific methodology relating to the interpretation of their result and its impact on neuroscientific research. Specifically, in order to make strong claims about experimental data, it is not enough to show that a control (i.e. a null hypothesis) exists, one needs to demonstrate that experimental observations are quantitatively no better than that control.

Where the authors state that "In summary, complex networks that are not spatial systems, coupled with environmental input, appear sufficient to decode spatial information." what they have really shown is that it is possible to decode *some degree* of spatial information. This is a null hypothesis (that observations of spatial tuning do not reflect a "spatial system"), and the comparison must be made to experimental data to test if the so-called "spatial" networks in the brain have more cells with more reliable spatial info than a complex-visual control.

Further, the authors state that "Consistent with our view, we found no clear relationship between cell type distribution and spatial information in each layer. This raises the possibility that "spatial cells" do not play a pivotal role in spatial tasks as is broadly assumed." Indeed, this would raise such a possibility, if 1) the observations of their network were indeed quantitatively similar to the brain, and 2) the presence of these cells in the brain were the only evidence for their role in spatial tasks. However, 1) the authors have not shown this result in neural data, they've only noticed it in a network and mentioned the POSSIBILITY of a similar thing in the brain, and 2) the "assumption" of the role of spatially tuned cells in spatial tasks is not just from the observation of a few spatially tuned cells. But from many other experiments including causal manipulations (e.g. Robinson et al 2020 Cell, DeLauilleon et al 2015 Nat Neuro), which the authors conveniently ignore. Thus, I do not find their argument, as strongly stated as it is, to be well-supported.

An additional weakness is that linear decoding of position is not a strong test, nor is it a measure of spatial cognition. The ability to decode position from a large number of weakly tuned cells is not surprising. However, based on this ability to decode, the authors claim that "'spatial' cells do not play a privileged role in spatial cognition". To justify this claim, the authors would need to use the network to perform e.g. spatial navigation tasks, then investigate the network's ability to perform these tasks when tuned cells were lesioned.

Finally, I find a major weakness of the paper to be the framing of the results in opposition to, as opposed to contributing to, the study of spatially tuned cells. For example, the authors state that "If a perception system devoid of a spatial component demonstrates classically spatially-tuned unit representations, such as place, head-direction, and border cells, can "spatial cells" truly be regarded as 'spatial'?" Setting aside the issue of whether the perception system in question does indeed demonstrate spatially-tuned unit representations comparable to those in the brain, I ask "Why not?" This seems to be a semantic game of reading more into a name then is necessarily there. The names (place cells, grid cells, border cells, etc) describe an observation (that cells are observed to fire in certain areas of an animal's environment). They need not be a mechanistic claim (that space "causes" these cells to fire) or even, necessarily, a normative one (these cells are "for" spatial computation). This is evidenced by the fact that even within e.g. the place cell community, there is debate about these cells' mechanisms and function (eg memory, navigation, etc), or if they can even be said to serve only a single function. However, they are still referred to as place cells, not as a statement of their function but as a history-dependent label that refers to their observed correlates with experimental variables. Thus, the observation that spatially tuned cells are "inevitable derivatives of any complex system" is itself an interesting finding which *contributes to*, rather than contradicts, the study of these cells. It seems that the authors have a specific definition in mind when they say that a cell is "truly" "spatial" or that a biological or artificial neural network is a "spatial system", but this definition is not stated, and it is not clear that the terminology used in the field presupposes their definition.

In sum, the authors have demonstrated the existence of a control/null hypothesis for observations of spatially-tuned cells. However, 1) It is not enough to show that a control (null hypothesis) exists, one needs to test if experimental observations are no better than control, in order to make strong claims about experimental data, 2) the authors do not acknowledge the work that has been done in many cases specifically to control for this null hypothesis in experimental work or to test the sensory influences on these cells, and 3) the authors do not rigorously test the degree or source of spatial tuning of their units.

eLife assessment

This important study examined the complexity of emergent dynamics of large-scale neural network models after perturbation (perturbational complexity index, PCI) and used it as a measurement of consciousness to account for previous recordings of humans at various anesthetized levels. The evidence supporting the conclusion is solid and constitutes a unified framework for different observations related to consciousness. There are many fields that would be interested in this study, including cognitive neuroscience, psychology, complex systems, neural networks, and neural dynamics.

Reviewer #1 (Public Review):

Summary:

This paper attempts to measure the complex changes of consciousness in the human brain as a whole. Inspired by the perturbational complexity index (PCI) from classic research, authors introduce simulation PCI (𝑠𝑃𝐶𝐼) of a time series of brain activity as a measure of consciousness. They first use large-scale brain network modeling to explore its relationship with the network coupling and input noise. Then the authors verify the measure with empirical data collected in previous research.

Strengths:

The conceptual idea of the work is novel. The authors measure the complexity of brain activity from the perspective of dynamical systems. They provide a comparison of the proposed measure with four other indexes. The text of this paper is very concise, supported by experimental data and theoretical model analysis.

Weaknesses:

(1) Consciousness is a network phenomenon. The measure defined by the authors is to consider the maximal sPCI across the nodes stimulated. This measure is based on the time series of one node. The measure may be less effective in quantifying the ill relationship between nodes. This may contribute to the less predictive power of anesthesia (Figure 4b).

(2) One of the focuses of the work is the use of a dynamic model of brain networks. The explanation of the model needs to be in more detail.

(3) The equations should be checked. For example, there should be no max on the left side of the first equation on page 13.

(4) The quality of the figures should be improved.

(5) Figure 4 should be discussed and analyzed more in the text.

(6) The usage of the terms PCI and sPCI should be distinguished.

Reviewer #2 (Public Review):

Summary:

Breyton and colleagues analysed the emergent dynamics from a neural mass model, characterised the resultant complexity of the dynamics, and then related these signatures of complexity to datasets in which individuals had been anaesthetised with different pharmacological agents. The results provide a coherent explanation for observations associated with different time series metrics, and further help to reinforce the importance of modelling when integrating across scientific studies.

Strengths:

* The modelling approach was clear, well-reasoned, and explicit, allowing for direct comparison to other work and potential elaboration in future studies through the augmentation with richer neurobiological detail.

* The results serve to provide a potential mechanistic basis for the observation that the Perturbational Complexity Index changes as a function of the consciousness state.

Weaknesses:

* Coactivation cascades were visually identified, rather than observed through an algorithmic lens. Given that there are numerous tools for quantifying the presence/absence of cascades from neuroimaging data, the authors may benefit from formalising this notion.

* It was difficult to tell, graphically, where the model's operating regime lay. Visual clarity here will greatly benefit the reader.

eLife assessment

This is a conceptually appealing study in which the authors identify genes whose function is important for the development of inhibitory (GABA) neurons, and then demonstrate that a diet rich in ketone body β-hydroxybutyrate partially suppresses specific mutant phenotypes. The authors provide compelling evidence that features methods, data and analyses more rigorous than the current state-of-the-art. Conceptually, this is evidence of a rescue of a developmental defect with dietary metabolic intervention, linking, in an elegant way, the underpinning genetic mechanisms with novel metabolic pathways that could be used to circumvent the defects.

Reviewer #1 (Public Review):

Summary

This interesting study, which has greatly improved in the current revised version, explores the mechanism behind an increased susceptibility of daf-18/PTEN mutant nematodes to paralyzing drugs that exacerbate cholinergic transmission. The authors use state-of-the-art genetics and neurogenetics coupled with locomotor behavior monitoring and neuroanatomical observations using gene expression reporters to show that the susceptibility occurs due to low levels of DAF-18/PTEN in developing inhibitory GABAergic neurons early during larval development (specifically, during the larval L1 stage). DAF-18/PTEN is convincingly shown to act cell-autonomously in these cells upstream of the PI3K-PDK-1-AKT-DAF-16/FOXO pathway, consistent with its well-known role as an antagonist of this conserved signaling pathway. The authors exclude a role for the TOR pathway in this process and present evidence implicating selectivity towards-developing GABAergic neurons of the ventral nerve cord in comparison to excitatory cholinergic neurons. Finally, the authors show that a diet supplemented with a ketogenic body, β-hydroxybutyrate, which also counteracts the PI3K-PDK-1-AKT pathway, promoting DAF-16/FOXO activity, partially rescues the proper development (morphology and function) of GABAergic neurons in daf-18/PTEN mutants, but only if the diet is provided early during larval development. This strongly suggests that the critical function of DAF-18/PTEN in developing inhibitory GABAergic neurons is to prevent excessive PI3K-PDK-1-AKT activity during this critical and particularly sensitive period of their development in juvenile L1 stage worms. Whether or not the sensitivity of GABAergic neurons to DAF-18/PTEN function is a defining and widespread characteristic of this class of neurons in C. elegans and other animals, or rather a particularity of the early developmental stage of the GABAergic neurons investigated remains to be determined.

Strengths:

The study reports interesting and important findings, advancing the knowledge of how daf-18/PTEN and the PI3K-PDK-1-AKT pathway can influence neurodevelopment, and providing a valuable paradigm to study the selectivity of gene activities towards certain neurons. It also defines a solid paradigm to study the potential of dietary interventions (such as ketogenic diets) or other drug treatments to counteract (prevent or revert?) neurodevelopment defects and stimulate DAF-16/FOXO activity.

Weaknesses:

The fact that other non-GABAergic C. elegans neurons (i.e., AIY and HSN neurons) are also sensitive to DAF-18/PTEN activity during development suggests that the particular sensitivity observed in the GABAergic ventral nerve cord neurons in this study could be unrelated to their neurotransmitter class (GABAergic) per se, but rather to some other neuronal property (a critical period of plasticity or activity-based wiring?) that these neurons share with the AIY and HSN neurons, and not with the other surveyed ventral nerve cord neurons (the excitatory cholinergic neurons). The relevance of this possibility within the framework of understanding the role of DAF-18/PTEN in E/I imbalance across clades is not fully clear at this stage.

Reviewer #2 (Public Review):

Summary:

Disruption of the excitatory/inhibitory (E/I) balance have been reported in Autism Spectrum disorders (ASD) to which PTEN mutations have been associated. Giunti et al choose to explore the impact of PTEN mutations on the balance between E/I signaling using as a platform the C. elegans neuromuscular system where both cholinergic (E) and GABAergic (I) motor neurons regulate muscle contraction and relaxation. Mutations in daf-18/PTEN specifically affect morphologically and functionally the GABAergic (I) system, while leaving the cholinergic (E) system unaffected. The study further reveals that the observed defects in the GABAergic system in daf-18/PTEN mutants are attributed to reduced activity of DAF-16/FOXO during development.<br /> Moreover, ketogenic diets (KGDs), known for their effectiveness in disorders associated with E/I imbalances such as epilepsy and ASD, are found to induce DAF-16/FOXO during early development. Supplementation with β-hydroxybutyrate in the nematode at early developmental stages proves to be both necessary and sufficient to correct the effects on GABAergic signaling in daf-18/PTEN mutants.

Strengths:

The authors combined pharmacological, behavior and optogenetic experiments to show the GABAergic signaling impairment at the C. elegans neuromuscular junction in DAF-18/PTEN and DAF-16/FOXO mutants. Moreover, by studying the neuron morphology, they point towards neurodevelopmental defects in the GABAergic motoneurons involved in locomotion. Using the same set of experiments, they demonstrate that a ketogenic diet can rescue the inhibitory defect in the daf-18/PTEN mutant at an early stage.

Weaknesses:

The morphological experiments hint towards a pre-synaptic defect to explain the GABAergic signaling impairment, but it would have also been interesting to check the post-synaptic part of the inhibitory neuromuscular junctions such as the GABA receptor clusters to assess if the impairment is only presynaptic or both post and presynaptic. Moreover, analysing post-synaptic functionality in-depth using electrophysiology would be beneficial too.<br /> Nevertheless, this question alone could be entirely the subject of another paper and is not essential to the primary message of the paper.

Conclusion:

Giunti et al provide fundamental insights into the connection between PTEN mutations and neurodevelopmental defects through DAF-16/FOXO and shed light on the mechanisms through which ketogenic diets positively impact neuronal disorders characterized by E/I imbalances.

Reviewer #3 (Public Review):

Summary:

This is a conceptually appealing study by Giunti et al in which the authors identify a role for PTEN/daf-18 and daf-16/FOXO in the development of inhibitory GABA neurons, and then demonstrate that a diet rich in ketone body β-hydroxybutyrate partially suppresses the PTEN mutant phenotypes. The authors use three assays to assess their phenotypes: 1) pharmacological assays (with levamisole and aldicarb); 2) locomotory assays and 3) cell morphological assays. These assays are carefully performed and the article is clearly written. While neurodevelopmental phenotypes had been previously demonstrated for PTEN/daf-18 and daf-16/FOXO (in other neurons), and while KB β-hydroxybutyrate had been previously shown to increase daf-16/FOXO activity (in the context of aging), this study is significant because it demonstrates the importance of KB β-hydroxybutyrate and DAF-16 in the context of neurodevelopment. Conceptually, and to my knowledge, this is the first evidence I have seen of a rescue of a developmental defect with a dietary metabolic intervention, linking, in an elegant way, the underpinning genetic mechanisms with novel metabolic pathways that could be used to circumvent the defects.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This interesting study explores the mechanism behind an increased susceptibility of daf-18/PTEN mutant nematodes to paralyzing drugs that exacerbate cholinergic transmission. The authors use state-of-theart genetics and neurogenetics coupled with locomotor behavior monitoring and neuroanatomical observations using gene expression reporters to show that the susceptibility occurs due to low levels of DAF-18/PTEN in developing inhibitory GABAergic neurons early during larval development (specifically, during the larval L1 stage). DAF-18/PTEN is convincingly shown to act cell-autonomously in these cells upstream of the PI3K-PDK-1-AKT-DAF-16/FOXO pathway, consistent with its well-known role as an antagonist of this conserved signaling pathway. The authors exclude a role for the TOR pathway in this process and present evidence implicating selectivity towards developing GABAergic neurons. Finally, the authors show that a diet supplemented with a ketogenic body, β-hydroxybutyrate, which also counteracts the PI3K-PDK-1-AKT pathway, promoting DAF-16/FOXO activity, partially rescues the proper development (morphology and function) of GABAergic neurons in daf-18/PTEN mutants, but only if the diet is provided early during larval development. This strongly suggests that the critical function of DAF18/PTEN in developing inhibitory GABAergic neurons is to prevent excessive PI3K-PDK-1-AKT activity during this critical and particularly sensitive period of their development in juvenile L1 stage worms. Whether or not the sensitivity of GABAergic neurons to DAF-18/PTEN function is a defining and widespread characteristic of this class of neurons in C. elegans and other animals, or rather a particularity of the unique early-stage GABAergic neurons investigated remains to be determined.

Strengths:

The study reports interesting and important findings, advancing the knowledge of how daf-18/PTEN and the PI3K-PDK-1-AKT pathway can influence neurodevelopment, and providing a valuable paradigm to study the selectivity of gene activities towards certain neurons. It also defines a solid paradigm to study the potential of dietary interventions (such as ketogenic diets) or other drug treatments to counteract (prevent or revert?) neurodevelopment defects and stimulate DAF-16/FOXO activity.

Weaknesses:

(1) Insufficiently detailed methods and some inconsistencies between Figure 4 and the text undermine the full understanding of the work and its implications.

The incomplete methods presented, the imprecise display of Figure 4, and the inconsistency between this figure and the text, make it presently unclear what are the precise timings of observations and treatments around the L1 stage. What exactly do E-L1 and L1-L2 mean in the figure? The timing information is critical for the understanding of the implications of the findings because important changes take place with the whole inhibitory GABAergic neuronal system during the L1 stage into the L2 stage. The precise timing of the events such as neuronal births and remodelling events are welldescribed (e.g., Figure 2 in Hallam and Jin, Nature 1998; Fig 7 in Mulcahy et al., Curr Biol, 2022). Likewise, for proper interpretation of the implication of the findings, it is important to describe the nature of the defects observed in L1 larvae reported in Figure 1E - at present, a representative figure is shown of a branched commissure. What other types of defects, if any, are observed in early L1 larvae? The nature of the defects will be informative. Are they similar or not to the defects observed in older larvae?

We thank the reviewer for highlighting these areas for improvement. We have updated and clarified the timing of observation in the text, figures, and methodology section accordingly.

All experiments were conducted using age-synchronized animals. Gravid worms were placed on NGM plates and removed after two hours. The assays were then carried out on animals that hatched from the eggs laid during this specific timeframe.

Regarding the detailed timings outlined in the original Figure 4 (now Figure 5 in the revised version), we provided the following information in the revised version: For experiments involving continuous exposure to βHB throughout development, the gravid worms were placed on NGM plates containing the ketone body and removed after two hours. Therefore, this exposure covered the ex-utero embryonic development period up to the L4-Young adult stage when the experiments were conducted.

In experiments involving exposure at different developmental stages as those depicted in Figure 4 of the original version, (now Figure 5, revised version), animals were transferred between plates with and without βHB as required. We exposed daf-18/PTEN mutant animals to βHB-supplemented diets for 18-hour periods at different developmental stages (Figure 5A, revised version). The earliest exposure occurred during the 18 hours following egg laying, covering ex-utero embryonic development and the first 8-9 hours of the L1 stage. The second exposure period encompassed the latter part of the L1 stage, the entire L2 stage, and most of the L3 stage. The third exposure spanned the latter part of the L3 stage (~1-2 hours), the entire L4 stage, and the first 6-7 hours of the adult stage.

All this information has been conveniently included in Figure 5, text (Page13, lines 259-276), and in methodology (Page 4, Lines 85-90, Revised Methods and Supplementary information) of the revised manuscript.

In response to the reviewer's suggestion, we have also included photos of daf-18 worms at the L1 stage (30 min/1h post-hatching). Defects are already present at this early stage, such as handedness and abnormal branching commissures, which are also observed in adult worm neurons (see Supplementary Figure 4, revised version). 

These defects manifest in DD neurons shortly after larval birth. The prevalence of animals with errors is higher in L4 worms (when both VDs and DDs are formed) compared to early L1s (Figures 3 C-E and Supplementary Figure 4, revised version). This suggests that defects in VD neurons also occur in daf-18 mutants. Indeed, when we analyzed the neuronal morphology of several wild-type and daf-18 mutant animals, we found defects in the commissures corresponding to both DD and VD neurons (Supplementary Figure 3, revised version). 

These data are now included in the revised version (Results (Page 10, lines 177-196), Discussion (Pages 14-16), Main Figure 3, and Supplementary Figures 3, 4 and 7 revised version)

(2) The claim of proof of concept for a reversal of neurodevelopment defects is not fully substantiated by data.

The authors state that the work "constitutes a proof of concept of the ability to revert a neurodevelopmental defect with a dietary intervention" (Abstract, Line 56), however, the authors do not present sufficient evidence to distinguish between a "reversal" or prevention of the neurodevelopment defect by the dietary intervention. This clarification is critical for therapeutic purposes and claims of proof-of-concept. From the best of my understanding, reversal formally means the defect was present at the time of therapy, which is then reverted to a "normal" state with the therapy. On the other hand, prevention would imply an intervention that does not allow the defect to develop to begin with, i.e., the altered or defective state never arises. In the context of this study, the authors do not convincingly show reversal. This would require showing "embryonic" GABAergic neuron defects or showing convincing data in newly hatched L1 (0-1h), which is unclear if they do so or not, as I have failed to find this information in the manuscript. Again, the method description needs to be improved and the implications can be very different if the data presented in Figure 2D-E regard newly born L1 animals (0-1h) or L1 animals at say 5-7h after hatching. This is critical because the development of the embryonically-born GABAergic DD neurons, for instance, is not finalized embryonically. Their neurites still undergo outgrowth (albeit limited) upon L1 birth (see DataS2 in Mulcahy et al., Curr Biol 2022), hence they are susceptible to both committing developmental errors and to responding to nutritional interventions to prevent them. In contrast to embryonic GABAergic neurons, embryonic cholinergic neurons (DA/DB) do not undergo neurite outgrowth post-embryonically (Mulcahy et al., Curr Biol 2022), a fact which could provide some mechanistic insight considering the data presented. However, neurites from other post-embryonically-born neurons also undergo outgrowth postembryonically, but mostly during the second half of the L1 stage following their birth up to mid-L2, with significant growth occurring during the L1-L2 transition. These are the cholinergic (VA/VB and AS neurons) and GABAergic (VD) neurons. The fact that AS neurons undergo a similar amount of outgrowth as VD neurons is informative if VD neurons are or are not susceptible to daf-18/PTEN activity. Independently, DD neurons are still quite unique on other aspects (see below), which could also bring insight into their selective response.

Finally, even adjusting the claim to "constitutes a proof-of-concept of the ability of preventing a neurodevelpmental defect with a dietary intervention" would not be completely precise, because it is unclear how much this work "constitutes a proof of concept". This is because, unless I misunderstood something, dietary interventions are already applied to prevent neurodevelopment defects, such as when folic acid supplementation is recommended to pregnant women to prevent neural tube defects in newborns.

Thank you very much for pointing out this issue and highlighting the need to further investigate the ameliorative capacity of βHB on GABAergic defects in daf-18 mutants. In the revised version, we have included experiments to address this point.

Our microscopy analyses strongly indicate that the development of DD neurons is affected, with errors observed as early as one-hour post-hatching (Main Figure 3, and Supplementary Figures  4 and 7, revised version). Additionally, based on the position of the commissures in L4s, our results strongly suggest that VD neurons are also affected (Supplementary Figure 3, revised version). Both, the frequency of animals with errors and the number of errors per animal are higher in L4s compared to L1 larvae (Main Figures 3,  and Supplementary Figure 4 and 7, revised version). It is very likely that the errors in VD neurons, which are born in the late L1 stage, are responsible for the higher frequency of defects observed in L4 animals. 

As the reviewer noted, GABAergic DD neurons, which are born embryonically, do not complete their development during the embryonic stages. Some defects in DD neurons may arise during the postembryonic period. Following the reviewer's suggestion, we analyzed L1 larvae at different times before the appearance of VDs (1 hour post-hatching and 6 hours post-hatching). We did not observe an increase in error prevalence, suggesting that DD defects in daf-18 mutants are mostly embryonic (Supplementary Fig 4B, Revised Version). 

Our findings suggest that βHB's enhancement is not due to preventive effects in DDs, as defects persist in newly hatched larvae regardless of βHB presence (Supplementary Figure 7, revised version), and postembryonic DD growth does not introduce new errors (Supplementary Figure 4, revised version). This lack of preventive effect could be due to βHB's limited penetration into the embryonic environment. Unlike early L1s, significant improvement occurs in L4s upon βHB early exposure (Supplementary Figure 7, revised version). This could be explained by a reversing effect on malformed DD neurons and/or a protective influence on VD neuron development. While we cannot rule out the first option, even if all errors in DDs in L1 were repaired (which is very unlikely), it wouldn't explain the level of improvement in L4 (Supplementary Figure 7, revised version). Therefore, we speculate that VDs may be targeted by βHB. The notion that exposure to βHB during early L1 can ameliorate defects in neurons primarily emerging in late L1s (VDs) is intriguing. We may hypothesize that residual βHB or a metabolite from prior exposure could forestall these defects in VD neurons. Notably, βHB has demonstrated a capacity for long-lasting effects through epigenetic modifications (Reviewed in He et al, 2023, https://doi.org/10.1016%2Fj.heliyon.2023.e21098). More work is needed to elucidate the underlying fundamental mechanisms regarding the ameliorating effects of βHB supplementation. We have now discussed these possibilities under discussion (Page 17, lines 369-383, revised version).

We agree with the reviewer that the term "reversal" is not accurate, and we have avoided using this terminology throughout the text. Furthermore, in the title, we have decided to change the word "rescue" to "ameliorate," as our experiments support the latter term but not the former. Additionally, the reviewer is correct that folic acid administration to pregnant women is already a metabolic intervention to prevent neural tube defects. In light of this, we have avoided claiming this as proof of concept in the revised manuscript 

(3) The data presented do not warrant the dismissal of DD remodeling as a contributing factor to the daf-18/PTEN defects.

Inhibitory GABAergic DD neurons are quite unique cells. They are well-known for their very particular property of remodeling their synaptic polarity (DD neurons switch the nature of their pre- and postsynaptic targets without changing their wiring). This process is called DD remodeling. It starts in the second half of the L1 stage and finishes during the L2 stage. Unfortunately, the fact that the authors find a specific defect in early GABAergic neurons (which are very likely these unique DD neurons) is not explored in sufficient detail and depth. The facts that these neurons are not fully developed at L1, that they still undergo limited neurite growth, and that they are poised for striking synaptic plasticity in a few hours set them apart from the other explored neurons, such as early cholinergic neurons, which show a more stable dynamics and connectivity at L1 (see Mulcahy et al., Curr Biol 2022).

The authors use their observation that daf-18/PTEN mutants present morphological defects in GABAergic neurons prior to DD remodeling to dismiss the possibility that the DAF-18/PTEN-dependent effects are "not a consequence of deficient rearrangement during the early larval stages". However, DD remodeling is just another cell-fate-determined process and as such, its timing, for instance, can be affected by mutations in genes that affect cell fates and developmental decisions, such as daf-18 and daf-16, which affect developmental fates such as those related with the dauer fate. Specifically, the authors do not exclude the possibility that the defects observed in the absence of either gene could be explained by precocious DD remodeling. Precocious DD remodeling can occur when certain pathways, such as the lin-14 heterochronic pathway, are affected. Interestingly, lin-14 has been linked with daf16/FOXO in at least two ways: during lifespan determination (Boehm and Slack, Science 2005) and in the

L1/L2 stages via the direct negative regulation of an insulin-like peptide gene ins-33 (Hristova et al., Mol Cell Bio 2005). It is likely that the prevention of DD dysfunction requires keeping insulin signaling in check (downregulated) in DD neurons in early larval stages, which seems to coincide with the critical timing and function of daf-18/PTEN. Hence, it will be interesting to test the involvement of these genes in the daf-18/daf-16 effects observed by the authors.

This is another interesting point raised by the reviewer. We have demonstrated that defects manifest in early L1 (30 min-1 hour post-hatching) which corresponds to a pre-remodeling time in wild-type worms.

We acknowledge the possibility of early remodeling in specific mutants as pointed out by the reviewer.

However, the following points suggest that the effects of these mutations may extend beyond the particularity of DD remodeling: i) Our experiments also show defects in VD neurons in daf-18 mutants (Supplementary Figure 3, revised version), as discussed in our previous response. These neurons do not undergo significant remodeling during their development. ii) DAF-18 and DAF-16 deficiencies produce neurodevelopmental alteration on other Non-Remodeling Neurons: Severe neurite defects in neurons that are nearly fully formed at larval hatching, such as AIY in daf-18 and daf-16 mutants, have been previously reported (Christensen et al., 2011). Additionally, the migration of another neuron, HSN, is severely affected in these mutants (Kennedy et al., 2013). iii) To the best of our knowledge, DD remodeling only alters synaptic polarity without forming new commissures or significant altering the trajectory of the formed ones. Thus, it is unlikely (though not impossible) for remodeling defects to cause the observed commissural branching and handedness abnormalities in DD neurons. Therefore, we think that the impact of daf-18 mutations on GABAergic neurons is not primarily linked to DD remodeling but extends to various neuron types. It is intriguing and requires further exploration in the future, the apparent resilience of cholinergic motor neurons to these mutations. This resilience is not limited to daf18/PTEN animals since mutants in certain genes expressed in both neuron types (such as neuronal integrin ina-1 or eel-1, the C. elegans ortholog of HUWE1) alter the function or morphology of GABAergic neurons but not cholinergic motor neurons (Kowalski, J. R. et al. Mol Cell Neurosci 2014; Oliver, D. et al. J Dev Biol (2019); Opperman, K. J. et al. Cell Rep 2017). These points are discussed in the manuscript (Discussion, page 15, lines 311-322, revised version) and reveal the existence of compensatory or redundant mechanisms in these excitatory neurons, rendering them much more resistant to both morphological and functional abnormalities.

Discussion on the impact of the work on the field and beyond:

The authors significantly advance the field by bringing insight into how DAF-18/PTEN affects neurodevelopment, but fall short of understanding the mechanism of selectivity towards GABAergic neurons, and most importantly, of properly contextualizing their findings within the state-of-the-art C. elegans biology.

For instance, the authors do not pinpoint which type of GABAergic neuron is affected, despite the fact that there are two very well-described populations of ventral nerve cord inhibitory GABAergic neurons with clear temporal and cell fate differences: the embryonically-born DD neurons and the postembryonically-born VD neurons. The time point of the critical period apparently defined by the authors (pending clarifications of methods, presentation of all data, and confirmation of inconsistencies between the text and figures in the submitted manuscript) could suggest that DAF-18/PTEN is required in either or both populations, which would have important and different implications. An effect on DD neurons seems more likely because an image is presented (Figure 2D) of a defect in an L1 daf-18/PTEN mutant larva with 6 neurons (which means the larva was processed at a time when VD neurons were not yet born or expressing pUnc-47, so supposedly it is an image of a larva in the first half of the L1 stage (0-~7h?)). DD neurons are also likely the critical cells here because the neurodevelopment errors are partially suppressed when the ketogenic diet is provided at an "early" L1 stage, but not later (e.g., from L2-L3, according to the text, L2-L4 according to the figure? ).

Thank you for this insightful input. As previously mentioned, we conducted experiments in this revision to clarify the specificity of GABAergic errors in daf-18/PTEN mutants, in particular, whether they affect DDs, VDs, or both. Our results suggest that commissural defects are not limited to DD neurons but also occur in VD neurons (Supplementary Figure 3). Regarding the effect of βHB, our findings suggest that VD neurons are targets of βHB action. As mentioned in the previous response and the discussion section (Page 17, lines 369-383, revised version), we might speculate that lingering βHB or a metabolite from prior exposure could mitigate these defects in VD neurons that are born in Late L1s-Early L2s. Additionally, βHB has been noted for its capacity to induce long-term epigenetic changes. Therefore, it could act on precursor cells of VD neurons, with the resulting changes manifesting during VD development independently of whether exposure has ceased. All these possibilities are now discussed in the manuscript.

Acknowledging that our work raises several questions that we aim to address in the future, we believe our manuscript provides valuable information regarding how the PI3K pathway modulates neuronal development and how dietary interventions can influence this process.

This study brings important contributions to the understanding of GABAergic neuron development in C. elegans, but unfortunately, it is justified and contextualized mostly in distantly-related fields - where the study has a dubious impact at this stage rather than in the central field of the work (post-embryonic development of C. elegans inhibitory circuits) where the study has stronger impact. This study is fundamentally about a cell fate determination event that occurs in a nutritionally-sensitive

developmental stage (post-embryonic L1 larval stage) yet the introduction and discussion are focused on more distantly related problems such as excitatory/inhibitory (E/I) balance, pathophysiology of human diseases, and treatments for them. Whereas speculation is warranted in the discussion, the reduced indepth consideration of the known biology of these neurons and organisms weakens the impact of the study as redacted. For instance, the critical role of DAF-18/PTEN seems to occur at the early L1 larval stage, a stage that is particularly sensitive to nutritional conditions. The developmental progression of L1 larvae is well-known to be sensitive to nutrition - eg, L1 larvae arrest development in the absence of food, something that is explored in nematode labs to synchronize animals at the L1 stage by allowing embryos to hatch into starvation conditions (water). Development resumes when they are exposed to food. Hence, the extensive postembryonic developmental trajectory that GABAergic neurons need to complete is expected to be highly susceptible to nutrition. Is it? The sensitivity towards the ketogenic diet intervention seems to favor this. In this sense, the attribution of the findings to issues with the nutrition-sensitive insulin-like signaling pathway seems quite plausible, yet this possibility seems insufficiently considered and discussed.

We greatly appreciate the reviewer's emphasis on the sensitivity of the L1 stage to nutritional status. As the reviewer points out, C. elegans adjusts its development based on food availability, potentially arresting development in L1 in the absence of food. It is therefore reasonable that both the completion of DD neuron trajectories and the initial development steps of VD neurons are particularly sensitive to dietary modulation of the insulin pathway, in which both DAF-18 and DAF-16 play roles. This important point has also been included in the discussion (Page 18, lines 384-407, revised version).

Finally, the fact that imbalances in excitatory/inhibitory (E/I) inputs are linked to Autism Spectrum Disorders (ASD) is used to justify the relevance of the study and its findings. Maybe at this stage, the speculation would be more appropriate if restricted to the discussion. In order to be relevant to ASD, for instance, the selectivity of PTEN towards inhibitory neurons should occur in humans too. However, at present, the E/I balance alteration caused by the absence of daf-18/PTEN in C. elegans could simply be a coincidence due to the uniqueness of the post-embryonic developmental program of GABAergic neurons in C. elegans. To be relevant, human GABAergic neurons should also pass through a unique developmental stage that is critically susceptible to the PI3K-PDK1-AKT pathway in order for DAF18/PTEN to have any role in determining their function. Is this the case? Hence, even in the discussion, where the authors state that "this study provides universally relevant information on.... the mechanisms underlying the positive effects of ketogenic diets on neuronal disorders characterized by GABA dysfunction and altered E/I ratios", this claim seems unsubstantiated as written particularly without acknowledging/mentioning the criteria that would have to be fulfilled and demonstrated for this claim to be true.

Our results suggest that defects in GABAergic neurons are not limited to DDs, which, as the reviewer rightly notes, are quite unique in their post-embryonic development primarily due to the synaptic remodeling process they undergo. These defects also extend to VD neurons, which do not exhibit significant developmental peculiarities once they are born. Therefore, we think that the defects are not specific to the developmental program of DD neurons but are more related to all GABAergic motoneurons. Additionally, the observation of defects in non-GABAergic neurons in C. elegans daf-18 mutants supports the hypothesis that the role of daf-18 is not limited to DD neurons (Christensen et al., 2011; Kennedy et al., 2013).

In mammals, Pten conditional knockout (cKO) animals have been extensively studied for synaptic connectivity and plasticity, revealing an imbalance between synaptic excitation and inhibition (E/I balance) (Reviewed in Rademacher and Eickholt, 2019, Cold Spring Harbor Perspect Med, https://doi.org/10.1101%2Fcshperspect.a036780). This imbalance is now widely accepted as a key pathological mechanism linked to the development of ASD-related behavior (Lee et al, 2017; Biological Psychiatry, https://doi.org/10.1016/j.biopsych.2016.05.011) . The importance of PTEN in the development of GABAergic neurons in mammals is well-documented. For instance, embryonic PTEN deletion from inhibitory neurons impacts the establishment of appropriate numbers of parvalbumin and somatostatin-expressing interneurons, indicating a central role for PTEN in inhibitory cell development (Vogt et al, 2015, Cell Rep, https://doi.org/10.1016%2Fj.celrep.2015.04.019). Additionally, conditional PTEN knockout in GABAergic neurons is sufficient to generate mice with seizures and autism-related behavioral phenotypes (Shin et al, 2021, Molecular Brain, https://doi.org/10.1186%2Fs13041-02100731-8). Moreover, while mice in which PV GABAergic neurons lacked both copies of Pten experienced seizures and died, heterozygous animals (PV-Pten+/−) showed impaired formation of perisomatic inhibition (Baohan et al, 2016, Nature Comm, OI: 10.1038/ncomms12829). Therefore, there is substantial evidence in mammals linking PTEN mutations to neurodevelopmental disorders in general and affecting GABAergic neurons in particular. Hence, we believe that the role of daf-18/PTEN in GABAergic development could be a more widespread phenomenon across the animal kingdom rather than a specific process unique to C. elegans.

Beyond the points discussed, we have addressed the reviewer's comment regarding the last sentence of the abstract. We have revised it to more cautiously frame the relationship between our findings, ASD, and mammalian neurodevelopmental disorders.

Reviewer #2 (Public Review):

Summary:

Disruption of the excitatory/inhibitory (E/I) balance has been reported in Autism Spectrum Disorders

(ASD), with which PTEN mutations have been associated. Giunti et al choose to explore the impact of PTEN mutations on the balance between E/I signaling using as a platform the C. elegans neuromuscular system where both cholinergic (E) and GABAergic (I) motor neurons regulate muscle contraction and relaxation. Mutations in daf-18/PTEN specifically affect morphologically and functionally the GABAergic (I) system, while leaving the cholinergic (E) system unaffected. The study further reveals that the observed defects in the GABAergic system in daf-18/PTEN mutants are attributed to reduced activity of DAF-16/FOXO during development.

Moreover, ketogenic diets (KGDs), known for their effectiveness in disorders associated with E/I imbalances such as epilepsy and ASD, are found to induce DAF-16/FOXO during early development. Supplementation with β-hydroxybutyrate in the nematode at early developmental stages proves to be both necessary and sufficient to correct the effects on GABAergic signaling in daf-18/PTEN mutants.

Strengths:

The authors combined pharmacological, behavioral, and optogenetic experiments to show the

GABAergic signaling impairment at the C. elegans neuromuscular junction in DAF-18/PTEN and DAF-

16/FOXO mutants. Moreover, by studying the neuron morphology, they point towards

neurodevelopmental defects in the GABAergic motoneurons involved in locomotion. Using the same set of experiments, they demonstrate that a ketogenic diet can rescue the inhibitory defect in the daf18/PTEN mutant at an early stage.

Weaknesses:

The morphological experiments hint towards a pre-synaptic defect to explain the GABAergic signaling impairment, but it would have also been interesting to check the post-synaptic part of the inhibitory neuromuscular junctions such as the GABA receptor clusters to assess if the impairment is only presynaptic or both post and presynaptic.

Moreover, all observations done at the L4 stage and /or adult stage don't discriminate between the different GABAergic neurons of the ventral nerve cord, ie the DDs which are born embryonically and undergo remodeling at the late L1 stage, and VDs which are born post-embryonically at the end of the L1 stage. Those additional elements would provide information on the mechanism of action of the FOXO pathway and the ketone bodies.

Thank you for your insightful suggestions. 

This is an initial study that serves as a cornerstone, demonstrating the sensitivity of GABAergic neuron development to alterations in the PI3K pathway and how these alterations can be mitigated by a dietary intervention with a ketone body. While we have determined that the transcription factor DAF-16/FOXO is essential in the neurodevelopmental process and is the target of ketone bodies to alleviate defects, there are still underlying mechanisms to be elucidated. This is only the first step that opens many avenues for further investigation, including the study of post-synaptic partners.

While our current study primarily focuses on neuronal alterations without delving into potential postsynaptic effects, we do plan to investigate this aspect in future research. This includes examining GABAergic receptors as well as cholinergic receptors, as exacerbation of cholinergic signaling cannot be ruled out. To conduct a comprehensive study of post-synaptic structure and functionality, we would need strains with fluorescent markers for both pre- and post-synaptic components (such as rab-3, unc-49, unc29, acr-16 fusion to GFP or mCherry). Unfortunately, most of these strains are not currently available in our laboratory. Unlike the US or Europe, acquiring these strains from the C. elegans CGC repository in Argentina is challenging due to common customs delays, which require significant time and resources to navigate. Discussions at the Latin American C. elegans conference with CGC administrators, such as Ann Rougvie, have been initiated to address this issue, but a solution has not been reached yet.  Additionally, to analyze post-synaptic functionality in-depth, studying the response to perfusion with various agonists using electrophysiology would be beneficial. We are in the process of acquiring the capability to conduct electrophysiology experiments in our laboratory, but progress is slow due to limited funding.

While we believe these experiments are very informative, they will require a considerable amount of time due to our current circumstances. We consider them non-essential to the primary message of the paper, which focuses on neuronal developmental defects leading to functional alterations in daf-18/PTEN mutants and the novel finding that these can be mitigated by supplementing food with hydroxybutyrate. We will study the structure and functionality of the post-synapse in our future projects and also plan to extend this investigation to mutants with deficiencies in genes closely related to neurodevelopmental defects, such as neuroligin, neurexin, or shank-3, which have been implicated in synaptic architecture.

We also agree that discriminating between DD and VD neurons provides significant insights into the neurodevelopmental phenomena dependent on the FOXO pathway and the action of βHB. In this revised version, we present evidence that not only DD neurons are affected but also VD neurons (see

Supplementary Figure 3, revised version). This allows us to suggest that daf-18 affects the development of GABAergic neurons regardless of whether they are born embryonically (DDs) or post-embryonically (VDs) (see also our response to the previous reviewer). We hope to distinguish the defects observed in each type of neuron in future studies. For this, we would need to use strains specifically marked in one neuronal type or another, which, for the same reasons mentioned earlier, would take a considerable amount of time under current conditions. 

Conclusion:

Giunti et al provide fundamental insights into the connection between PTEN mutations and neurodevelopmental defects through DAF-16/FOXO and shed light on the mechanisms through which ketogenic diets positively impact neuronal disorders characterized by E/I imbalances.  

Reviewer #3 (Public Review):

Summary:

This is a conceptually appealing study by Giunti et al in which the authors identify a role for PTEN/daf-18 and daf-16/FOXO in the development of inhibitory GABA neurons, and then demonstrate that a diet rich in ketone body β-hydroxybutyrate partially suppresses the PTEN mutant phenotypes. The authors use three assays to assess their phenotypes: (1) pharmacological assays (with levamisole and aldicarb); (2) locomotory assays and (3) cell morphological assays. These assays are carefully performed and the article is clearly written. While neurodevelopmental phenotypes had been previously demonstrated for PTEN/daf-18 and daf-16/FOXO (in other neurons), and while KB β-hydroxybutyrate had been previously shown to increase daf-16/FOXO activity (in the context of aging), this study is significant because it demonstrates the importance of KB β-hydroxybutyrate and DAF-16 in the context of neurodevelopment. Conceptually, and to my knowledge, this is the first evidence I have seen of a rescue of a developmental defect with dietary metabolic intervention, linking, in an elegant way, the underpinning genetic mechanisms with novel metabolic pathways that could be used to circumvent the defects.

Strengths:

What their data clearly demonstrate, is conceptually appealing, and in my opinion, the biggest contribution of the study is the ability of reverting a neurodevelopmental defect with a dietary intervention that acts upstream or in parallel to DAF-16/FOXO.

Weaknesses:

The model shows AKT-1 as an inhibitor of DAF-16, yet their studies show no differences from wildtype in akt-1 and akt-2 mutants. AKT is not a major protein studied in this paper, and it can be removed from the model to avoid confusion, or the result can be discussed in the context of the model to clarify interpretation.

Thank you very much for the suggestion. We agree with the reviewer's appreciation that the study of AKT's action itself is too limited in this study to draw conclusions that would allow its inclusion in the proposed model. Therefore, following the reviewer's suggestion, we have removed this protein from our model

When testing additional genes in the DAF-18/FOXO pathway, there were no significant differences from wild-type in most cases. This should be discussed. Could there be an alternate pathway via DAF-18/DAF16, excluding the PI3K pathway or are there variations in activity of PI3K genes during a ketogenic diet that are hard to detect with current assays?

Thank you for bringing up this point. Our pharmacological experiments indeed demonstrate that all mutants associated with an exacerbation of the PI3K pathway, which typically inhibits nuclear translocation and activity of the transcription factor DAF-16, lead to imbalances in E/I

(excitation/inhibition) that manifest as hypersensitivity to cholinergic drugs. This includes the gain of function of pdk-1 and the loss of function of daf-18 and daf-16 itself. In our subsequent experiments, we demonstrate that this exacerbation of the PI3K pathway leads to errors in the neurodevelopment of GABAergic neurons, which explains the hypersensitivity to aldicarb and levamisole.

As the reviewer remarks, it is intriguing why mutants inhibiting this pathway do not show differences in their sensitivity to cholinergic drugs compared to wild-type animals. We can speculate, for instance, that during neurodevelopment, there is a critical period where the PI3K pathway must remain with very low activity (or even deactivated) for proper development of GABAergic neurons. This could explain why there are no differences in sensitivity to cholinergic drugs between mutants that inhibit the PI3K pathway and the wild type. The PI3K pathway depends on insulin-like signals, which are in turn positively modulated by molecules associated with the presence of food. Interestingly, larval stage 1 is particularly sensitive to nutritional status, being able to completely arrest development in the absence of food. Therefore, dietary intervention with BHB may generate a signal of dietary restriction (as seen in mammals) and, as a consequence of this dietary restriction, the PI3K pathway is inhibited, resulting in increased DAF-16 activity. This could restore the proper neurodevelopment of GABAergic neurons. However, this is mere speculation, and further deeper experiments (than the pharmacology ones we performed here) with mutants in different genes within the PI3K pathway may shed light on this point.

Following the reviewer's suggestion, this point has been discussed in the revised version of the manuscript. (Discussion Page 18, Lines 384-407).

The consequence of SOD-3 expression in the broader context of GABA neurons was not discussed. SOD3 was also measured in the pharynx but measuring it in neurons would bolster the claims.

SOD-3 is a known target of DAF-16. Previous studies have shown that βHB induces SOD-3 expression through the induction of DAF-16 (Edwards et al, 2014, Aging,

https://doi.org/10.18632%2Faging.100683). The highest levels of SOD-3 expression are typically observed in the pharynx or intestine (DeRosa et al, 2019 https://doi.org/10.1038/s41586-019-1524-5;  Zheng et al., 2021, PNAS, https://doi.org/10.1073/pnas.2021063118), and it is often used as a measure of general upregulation of DAF-16. Therefore, we used this parameter as a measure of βHB upregulating systemic DAF-16 activity.  While we agree with the reviewer that observing variations in SOD-3 expression in neurons would further support our conclusions, unfortunately, we did not detect measurable signals of SOD-3 in motor neurons in either the control condition or the daf-18 background even upon stress or BHB-exposure. This may be because SOD-3 is a minor target of DAF-16 in these neurons, or its modulation may not correspond to the timing of fluorescence measurements (L4-adults).

Despite this, our genetic experiments and neuron-specific rescue experiments lead us to conclude that DAF-16 must act autonomously in GABAergic neurons to ensure proper neurodevelopment.

If they want to include AKT-1, seeing its effect on SOD-3 expression could be meaningful to the model.

Thank you for this suggestion. We believe that even measuring SOD-3 levels in akt mutant backgrounds would still provide limited information to give it a predominant value in our work. Additionally, to have a complete understanding of the total role of AKT, it would be necessary to measure it in a double mutant background of akt-1; akt-2, and these double mutants generate 100 % dauers even at 15C (Oh et al., PNAS 2005, https://doi.org/10.1073/pnas.0500749102; Quevedo et al., Current Biology 2007, http://dx.doi.org/10.1016/j.cub.2006.12.038; Gatzi et al., PLOS ONE 2014,

https://doi.org/10.1371/journal.pone.0107671), greatly complicating the execution of these experiments. Therefore, following the first advice of this reviewer, we have decided to modify our model by excluding AKT.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

⁃ Please include earlier in the main text the rationale for using unc-25 as a control/reference already when mentioning Figure 1A.

Thank you for pointing out the need to reference this control earlier. We have included the following paragraph in the description of Figure 1 (Page 5, line 71, revised version):

“Hypersensitivity to cholinergic drugs is typical of animals with an increased E/I ratio in the neuromuscular system, such as mutants in unc-25 (the C. elegans orthologue for glutamic acid decarboxylase, an essential enzyme for synthesizing GABA). While daf-18/PTEN mutants become paralyzed earlier than wild-type animals, their hypersensitivity to cholinergic drugs is not as severe as that observed in animals completely deficient in GABA synthesis, such unc-25 null mutants (Figures 1B and 1C) indicating a less pronounced imbalance between excitatory and inhibitory signals.”

⁃ Please discuss the greater sensitivity of pdk-1(gf) animals to levamisole than to aldicarb.

Thank you for bringing up this subtle point.  We understand that the reviewer is referring to the paralysis curve in response to aldicarb in pdk-1(gf), which is closer to unc-25 than the curve for levamisole (in both cases, they are more sensitive than the wild type). Therefore, pdk-1(gf) animals seem to be more sensitive to aldicarb than to levamisole. These results are now shown in Figure 1D (revised version).

The PI3K pathway does not only act in neurons but also in muscles. Gain of function in pdk-1 has been shown to modulate muscle protein degradation (Szewczyk et al, EMBO Journal, 2008. https://doi.org/10.1038/sj.emboj.7601540). In contrast,  no effect on protein degradation has been reported for null mutants in this gene. Several studies have demonstrated that protein degradation levels can differentially affect receptor subunits, particularly acetylcholine receptors (Reviewed in Crespi et al, Br J Pharmacol, 2018). C. elegans is characterized by a wide repertoire of AChR subunits, and there are at least two subtypes of ACh receptors in muscles (one multimeric sensitive to levamisole and one homomeric (ACR-16) insensitive to levamisole) (Richmond et al, 1999 Nature Neuroscience http://dx.doi.org/10.1038/12160; Touroutine D, JBC 2005 https://doi.org/10.1074/jbc.M502818200).

Interestingly, acr-16 null mutants are hypersensitive to aldicarb (Zeng et al, JCB, 2023, https://doi.org/10.1083/jcb.202301117) while the electrophysiological response to levamisole in this mutant remains similar to that of wild-type (Tourorutine et al, 2005). Therefore, it may be that the gain of function in pdk-1 induces a change in the expression of AChR subtypes in muscle that differentially affect sensitivity to levamisole and ACh. This is purely speculative, and there may be many other explanations. While it would be interesting to explore this difference further, it goes far beyond the scope of this study. The cholinergic drug sensitivity assay is purely exploratory and allowed us to delve into the GABAergic and cholinergic signals in daf-18 mutants. In this sense, the hypersensitivity of pdk-1(gf) to both drugs supports the idea that an increase in PI3K signaling leads to an increased E/I ratio.

⁃ Please explain the rationale to perform akt-1 and akt-2 assays separated. Why not test doublemutants? Has their lack of redundancy been determined?.  

Our pharmacological assays are conducted at the L4 larval stage, making it impossible to analyze the potential redundancy of akt-1 and akt-2 in sensitivity to levamisole and aldicarb. This impossibility arises because the akt-1;akt-2 double mutant exhibits nearly 100% arrest as dauer even at 15°C, as reported in several prior studies (Oh et al., PNAS 2005, https://doi.org/10.1073/pnas.0500749102; Quevedo et al., Current Biology 2007, http://dx.doi.org/10.1016/j.cub.2006.12.038; Gatzi et al., PLOS ONE 2014, https://doi.org/10.1371/journal.pone.0107671). While the increased dauer arrest in the double mutant compared to the single mutants might suggest redundant functions in dauer entry, there are also reports indicating the absence of redundancy in other processes, such as vulval development (Nakdimon et al., PLOS Genetics 2012, https://doi.org/10.1371%2Fjournal.pgen.1002881).

The complete Dauer arrest likely underlies why other studies focusing on the role of the PI3K pathway in neurodevelopment utilize both mutants separately (Christensen et al, Development 2011,

https://doi.org/10.1242/dev.069062). While determining the potential redundancy of these genes is not feasible for this assay, we utilized various mutants of the pathway (age-1, pdk-1, daf-18, daf-16 and daf16;daf-18 in addition to the akt-s) that support the conclusion, which is that exacerbating the PI3K pathway activity makes animals hypersensitive to cholinergic drugs.

In response to the reviewer's concern, we have added a sentence in the text explaining the impossibility of performing the assay in the akt-1;akt-2 double mutant (Page 6, lines90-92) 

Figure 1C and D (This applies to all similarly presented bar figures). Please show data points and dispersion (preferably data, median+- 25-75% or average+-SD). 

Thank you. Done

⁃ Line 112 -maybe "and resumes"? 

Thank you. Done (Line 126, revised version)

⁃ Figure 1E and F. Please present mean +-SD (not SEM) of fluctuations. Please change slightly the tones so that the dispersion is easier to distinguish on the "blue light on" box.

Thank you for the suggestion. We have adjusted the tones as recommended to enhance the visualization of the "blue light on" box. For visualization purposes, we present the shading of the standard error of the mean (SEM), as is usual in these types of optogenetic experiments where traces of animal length variations are measured (Liewald et al, Nature Methods, 2008, doi: 10.1038/nmeth.1252; Schulstheis et al, J. Neurophysiology, 2011, doi: 10.1152/jn.00578.2010; Koopman et al, BMC Biology 2021, https://doi.org/10.1186/s12915-021-01085-2; Seidhenthal et al, Micro Publication Biology, 2022, https://doi.org/10.17912%2Fmicropub.biology.000607 ).

For the revised version, we have also included bar graphs for each optogenetic experiment, representing the mean of the length average of each worm measured from the first second after the blue light was turned on until the second before the light was turned off (in the graph, this corresponds to the period between seconds 6 and 9 of the traces). These graphs include the standard deviation and the corresponding significance levels. All of this has been included in the new legend (Figure 2D, 2E, 4E-J).

⁃ Figure 1A&1B & Supplementary Figure 1D x Supplementary Figure 1E&1F. What is the difference between these experiments? Whereas the unc-25 mutants paralyze in the same amount of time, the WT animals paralyze ~1 h later in Supplementary Figure 1E-1F in response to either drug. Please revise experimental conditions to see if anything can be learned eg, maybe this is a nutritional response from experiments done at different timepoints? Maybe different food recipes affected sensitivity to paralysis?

Thank you for pointing this out. While the experiments with daf-18 (in both alleles) and daf-16 were conducted at the beginning of this project (2019-2020), the assays with the other mutants in the PI3K and mTOR pathways were performed years later. Changes in the reagents used (agar, peptone, cholesterol, etc.) to grow the worms have occurred, potentially altering the animals' response directly or through the nutritional quality of the bacteria they grow on. In addition, the difference may be attributed to the fact that experiments at the project's outset were conducted by one author, while more recent experiments were carried out by another. The goal is to quantify paralysis in non-responsive worms after touch stimulation. The force of this probing or the thickness of the hair used for touching can be slightly operator-dependent and can lead to variable responses. In addition, always the presence of wild-type and unc-25 strain is included as internal control in every experiment. Nevertheless, despite this userdependent variation, the experiments were always conducted blindly (except for unc-25, whose uncoordinated phenotype is easily identifiable), thus we trust in the outcomes.

⁃ Supplementary Figure 1G - Length and Width appear to be switched in both left and right panels - please revise and include a description of N and of statistics depicted. 

Unfortunately, we don't see the switching error that the reviewer mentioned. In the left panel, we demonstrate that optogenetic activation of GABAergic neurons leads to an increase in length without modifying the width of the animal. Therefore, we conclude that the increase in area, as observed in our Fiji macro for optogenetic response analysis, is due to an increase in the animal's length. In the cholinergic activation shown in the right panel, the animal shortens (decreasing length) without modifying the width, resulting in the reduction of the total body area. 

We have included information about N (sample size) and the statistical test used in the legends as suggested. These graphs are now shown as Figures 2F and G, revised version.

⁃ Supplementary Figure 1G legend lines 779-780. Please describe the post-hoc test applied following ANOVA to obtain the denoted p values. This applies to all datasets where ANOVA or Krusal-Wallis tests were applied.

Following reviewer´s suggestion, all the post-hoc tests applied after ANOVA or Kruskal-Wallis analysis were included in the legend of each figure and Materials and Methods (statistical analysis section).

⁃ Line 174 maybe "arises *from* the hyperactivation" instead of *for*?.

Corrected. Thank you. Line 190, revised version.

⁃ Supplementary Figure 4. On line 816 it says n=40-90, but please check the n of the daf-18, daf-16 samples, which seem to have less than 40 animals.

We understand that the reviewer is referring to Supplementary Figure 3 from the original version (now Supplementary Figure 5 in the revised version). We have now included the number of observations below each data point cloud to clearly indicate the sample size for each condition

⁃ Supplementary Figure 4 - please state what are the bars on the graphs. Please state which post-hoc test was performed after Kruskal-Wallis and present at least the p values obtained between treated controls and each genotype. Alternatively, present the whole truth table in supplementary daita.

We understand that the reviewer is referring to Supplementary Figure 3 from the original version (now Supplementary Figure 5 in the revised version). There was an error in the original legend (thank you for bringing this to our attention) since the statistics were not performed using Kruskall-Wallis in this case, but rather each treated condition was compared to its own untreated control using Mann-Whitney test. We have now added the p-values to the graph. All raw data for this figure, as well as for all other figures, are available in Open Science Framework (https://osf.io/mdpgc/?view_only=3edb6edf2298421e94982268d9802050).

⁃ Please cite the figure panels in order: eg, Figure 3E is mentioned in the text after panels Figure 3F-K.

Done. We have rearranged the figures to adapt them to the text order (Figure 4, revised version)

⁃ Figure 4 - line 610 please revise "(n=20-30 (n: 20-25 animals per genotype/trial)."

Thank you. Corrected.

⁃ Figure 4 - there appears to be an inconsistency in the figure with the text (lines 223-225). In figures it says E-L1, but in the text, it says "solely in L1". Does E-L1 include the whole L1 stage? If not- E-L1 can be interpreted only as during the embryonic stage, hence, no exposure to betaHB due to the impermeable chitin eggshell. Then there is L1-L2, which should cover the L1 stage and the L2 or something else. Please revise. The text mentions L2-L3 or L3-L4 and these categories are not in the figures. This clarification is key for the interpretation of the results. The precise developmental time of the exposures is not defined either in the methods or in the figures. Please provide precise times relative to hours and/or molts and revise the text/figure for consistency.

The reviewer is entirely correct in pointing out the lack of relevant data regarding the exposure time to βHB. We have now clarified the information For the revised version, we have adjusted the nomenclature of each exposure period to precisely reflect the developmental stages involved.

For the experiments involving continuous exposure to βHB throughout development, the NGM plate contained the ketone body. Therefore, the exposure encompassed, in principle, the ex-utero embryonic development period up to L4-Young adults (E-L4/YA, in Figure 5A) when the experiments were conducted. Since it could be a restriction to drug penetration through the chitin shell of the eggs (see Supplementary Figure 7), we can ensure βHB exposure from hatching.

In experiments involving exposure at different developmental stages as those depicted in Figure 4 of the original version, (now Figure 5), animals were transferred between plates with and without βHB as required. We exposed daf-18/PTEN mutant animals to βHB-supplemented diets for 18-hour periods at different developmental stages (Figure 5A). The earliest exposure occurred during the 18 hours following egg laying, covering ex-utero embryonic development and the first 8-9 hours of the L1 stage (This period is called E-L1, in figure 5 revised version). The second exposure period encompassed the latter part of the L1 stage, the entire L2 stage, and most of the L3 stage (L1-L3). The third exposure spanned the latter part of the L3 stage (~1-2 hours), the entire L4 stage, and the first 6-7 hours of the adult stage (L3-YA).

All this information has been conveniently included in Figure 5 (and its legend), text (Page 13, lines 259276), and Material and Methods of the revised manuscript.

⁃ Some methods are not sufficiently well described. Specifically, how the animals were exposed to treatments and how stages were obtained for each experiment. Was synchronization involved? If so, in which experiments and how exactly was it performed?

As mentioned in previous responses all the experiments were performed in age-synchronized animals. We include the following sentence in Materials and Methods (C. elegans culture and maintenance section): “All experiments were conducted on age-synchronized animals. This was achieved by placing gravid worms on NGM plates and removing them after two hours. The assays were performed on the animals hatched from the eggs laid in these two hours”.

Reviewer #2 (Recommendations For The Authors):

Major points

(1) To complete the study on the GABAergic signaling at the NMJs, it would be interesting to assess the status of the post-synaptic part of the synapse such as the GABAR clustering. It would also tell if the impairment is only presynaptic or both post and presynaptic.

Thank you for your insightful suggestion. We agree that exploring post-synaptic elements can shed light on whether the impairment is solely presynaptic or involves both pre and post-synaptic components.

While our current study primarily focuses on neuronal alterations without delving into potential postsynaptic effects, we do plan to investigate this aspect in the future. This includes not only examining GABAergic receptors but also exploring cholinergic receptors, as exacerbation of cholinergic signaling cannot be ruled out. To conduct a comprehensive study of post-synaptic structure and functionality, we would need strains with fluorescent markers for both pre and post-synaptic components (rab-3, unc-49, unc-29, acr-16 driving GFP or mCherry). However, most of these strains are not currently available in our laboratory. Unlike the US or Europe, acquiring these strains from the C. elegans CGC repository in Argentina is challenging due to common customs delays, requiring significant time and resources to navigate. Discussions at the Latin American C. elegans conference with CGC administrators, such as Ann Rougvie, have been initiated to address this issue, but a solution has not been reached yet. 

Additionally, to analyze post-synaptic functionality in-depth, studying the response to perfusion with various agonists using electrophysiology would be beneficial. We are in the process of acquiring the capability to conduct electrophysiology experiments in our laboratory, but progress is slow due to limited funding.

While we believe these experiments are very informative, they will require a considerable amount of time due to our current circumstances. We consider them non-essential to the primary message of the paper, which focuses on neuronal morphological defects leading to functional alterations in daf-18/PTEN mutants.

We will include these experiments in our future projects, also planning to extend this investigation to mutants with deficiencies in genes closely related to neurodevelopmental defects, such as neuroligin, neurexin, or shank-3, which have been implicated in synaptic architecture.

(2) The author always referred to unc-47 promoter or unc-17 promoter, never specifying where those promoters are driving the expression (and in the Materials & Methods, no information on the corresponding sequence). Depending on the promoters they may not only be expressed in the motoneurons involved in locomotion (VA, VB, DA, DB, VD, and DD), but they could also be expressed in other neurons which could be of importance for the conclusions of the optogenetic assays but also the daf-18 expression in GABAergic neurons.

We appreciate the reviewer's insight regarding the broader expression patterns of the unc-17 and unc-47 promoters in all cholinergic and GABAergic neurons, respectively. The strains expressing constructs with these promoters were obtained from the CGC or other labs and have been widely used in previous papers (Liewald et al, Nature Methods, https://www.nature.com/articles/nmeth.1252 (2008); Byrne, A. B. et al. Neuron 81, 561-573, doi:10.1016/j.neuron.2013.11.019 (2014).

Regarding the optogenetic assays, the readout utilized (body length elongation or contraction) is primarily associated with the activity of cholinergic and GABAergic motor neurons and has been used in numerous studies to measure motor neuron functionality (Liewald et al, Nature Methods, https://www.nature.com/articles/nmeth.1252 (2008);Hwang, H. et al. Sci Rep 6, 19900, doi:10.1038/srep19900 (2016); Schultheis et al,  . J Neurophysiol 106, 817-827, doi:10.1152/jn.00578.2010 (2011); Koopman, M., Janssen, L. & Nollen, E. A. BMC Biol 19, 170, doi:10.1186/s12915-021-01085-2 (2021);). It has previously been established that the shortening observed after optogenetic activation of the unc-17 promoter, while active in various interneurons, depends on the activity of cholinergic motor neurons (Liewald et al., Nature Methods, https://www.nature.com/articles/nmeth.1252 (2008)). This was demonstrated by examining transgenic worms expressing ChR2-YFP from another cholinergic, motoneuronspecific but weaker promoter, Punc-4. They observed contraction and coiling upon illumination, albeit to a milder degree.

In terms of GABAergic neurons, only 3 do not directly synapse to body wall muscles (AVL, PDV, and RIS) and are primarily involved in defecation. Of the 23 GABAergic motor neurons, 19 are Dtype motoneurons, while the remaining 4 innervate head muscles (Pereira et al, eLife 2015, https://doi.org/10.7554/eLife.12432). It is therefore expected that while there may be some contribution from these latter neurons to the elongation after optogenetic activation in animals containing punc-47::ChR2, the main contribution should be from the D-type neurons. Additionally, while there may be some influence on D-type neuron development due to daf-18 rescue in neurons like RME, DVB or AVL, the most direct explanation for the rescue is that daf-18 acts autonomously in D-type cells.  Additionally, we have pharmacological and behavioral assays that support the findings of optogenetics and enable us to reach final conclusions.

(3) DD neurons are born during embryogenesis and newborn L1s have neurites even though less than at a later stage. If possible, it would be interesting to take a look at them to see if βHB has an effect or not. It will corroborate the hypothesis that βHB action is prevented by the impermeable eggshell on a system that can respond at a later stage. Moreover, using a specific DD, DA, and DB promoter, it would be possible to check if there is a difference in the morphological defects between embryonic and post-embryonic neurons.

This is a very interesting point raised by the reviewer. We conducted experiments to analyze the morphology of GABAergic neurons in animals exposed to βHB only during the ex-utero embryonic development (in their laid egg state). We observed that this incubation was not sufficient to rescue the defects in GABAergic neurons (Supplementary Figure 7, revised version). As reported by other authors and discussed in our paper, the chitinous eggshell might act as an impermeable barrier to most drugs. However, we cannot rule out that incubation during this period is necessary but not sufficient to mitigate the defects. We have included these experiments in Supplementary Figure 7 and in the text (Page 13, lines 272-276)

Additionally, we analyzed confocal images where, based on their position, we could identify and assess errors in DD (embryonic) and VD (Post-embryonic) neurons (Supplementary Figure 3, revised version). These experiments show that the effects are observed in both types of neurons, and we did not observe any differential alterations in neuronal morphology between the two types of neurons.

Minor points

(1)   Expression of daf-18/PTEN in muscle or hypodermis, could it ensure a proper development? It could give insights into the action mechanism of βHB.

The reviewer's observation is indeed very intriguing. Previous studies from the Grishok lab (Kennedy et al, 2013) have demonstrated that the expression of daf-18 or daf-16 in extraneuronal tissues, specifically in the hypodermis, can rescue migratory defects in the serotoninergic neuron HSN in daf-18 or daf-16 null mutants of C. elegans. Clearly, this could also be an option for rescuing the morphological and functional defects of GABAergic motoneurons.

However, the fact that the expression of daf-18 in GABAergic neurons rescues these defects strongly suggests an autonomous effect. In this regard, autonomous effects of DAF-18 or DAF-16 on neurodevelopmental defects have also been reported in interneurons in C. elegans (Christensen et al, 2011). This is included in the discussion (Page 15, lines 330-335)

(2) Re-organise the introduction. The paragraph on ketogenic diets (lines 35-38) is not logically linked.

Following reviewer´s suggestion we have reorganized the introduction and changed the order of explanation regarding the significance of ketogenic diets, linking it with their proven effectiveness in alleviating symptoms of diseases with E/I imbalance (Lines 23-60, revised version)

(3) Incorporate titles in the result section to guide the reader.

Done. Thank you

(4) Systematically add PTEN or FOXO when daf-18 or daf-16 are mentioned (for example lines 69, 84, 85).

Done. Thank you  

(5) Strain lists: lines 646 to 653: some information is missing on the different transgenes used in this study (integrated (Is) or extrachromosomal (Ex) with their numbers).

Thank you for bringing this to our attention. We have now included all the information regarding the different transgenes used in this study, including whether they are integrated (Is) or extrachromosomal (Ex) and their respective numbers. This information can be found in the revised version of the manuscript (Materials and Methods, C. elegans culture and maintenance section highlighted in yellow).

Reviewer #3 (Recommendations For The Authors):

In Figure 1, some experiments were done with the unc-25 control while others, such as the optogenetic experiments, were done without those controls.

Thank you for pointing this out. In the optogenetic experiments, we waited for the worm to move forward for 5 seconds at a sustained speed before exposing it to blue light to standardize the experiment, as the response can vary if the animal is in reverse, going forward, or stationary. Due to the severity of the uncoordinated movement in unc-25 mutants, achieving this forward movement before exposure is very difficult. Additionally, this lack of coordination prevents these animals from performing the escape response tests, as they barely move. Therefore, we limited the use of this severe GABAergic-deficient control to pharmacological or post-prodding shortening experiments.

eLife assessment

The authors are interested in the developmental origin of the neurons of the cerebellar nuclei. In this valuable study, they identify a population of neurons with a specific complement of markers that originate in a distinct location from where cerebellar nuclear precursor cells have been thought to originate that show distinct developmental properties. The discovery of a new germinal zone giving rise to a new population of neurons is an exciting finding, and it enriches our understanding of cerebellar development. The claims are reasonably well supported by the solid evidence because the authors use a wide range of technical approaches, including transgenic mice that allow them to disentangle the influence of distinct developmental organisers.

Reviewer #1 (Public Review):

Summary:

The authors are interested in the developmental origin of the neurons of the cerebellar nuclei. They identify a population of neurons with a specific complement of markers originating in a distinct location from where cerebellar nuclear precursor cells have been thought to originate that show distinct developmental properties. The cerebellar nuclei have been well studied in recent years to understand their development through an evolutionary lens, which supports the importance of this study. The discovery of a new germinal zone giving rise to a new population of CN neurons is an exciting finding, and it enriches our understanding of cerebellar development, which has previously been quite straightforward, where cerebellar inhibitory cells arise from the ventricular zone and the excitatory cells arise from the rhombic lip.

Strengths:

One of the strengths of the manuscript is that the authors use a wide range of technical approaches, including transgenic mice that allow them to disentangle the influence of distinct developmental organizers such at ATOH.<br /> Their finding of a novel germinal zone and a novel population of CN neurons is important for developmental neuroscientists, cerebellar neuroscientists.

Weaknesses:

One important question raised by this work is what do these newly identified cells eventually become in the adult cerebellum. Are they excitatory or inhibitory? Do they correspond to a novel cell type or perhaps one of the cell classes that have been recently identified in the cerebellum (e.g. Fujita et al., eLife, 2020)? Understanding this would significantly bolster the impact of this manuscript.

The major weakness of the manuscript is that it is written for a very specialized reader who has a strong background in cerebellar development, making it hard to read for eLife's general audience. It's challenging to follow the logic of some of the experiments as well as to contextualize these findings in the field of cerebellar development.

Reviewer #2 (Public Review):

Summary:

Canonically cerebellar neurons are derived from 2 primary germinal zones within the anterior hindbrain (dorsal rhombomere 1). This manuscript identifies an important, previously underappreciated origin for a subset of early cerebellar nuclei neurons - likely the mesencephalon. This is an exciting finding.

Strengths:

The authors have identified a novel early population of cerebellar neurons with likely novel origin in the midbrain. They have used multiple assays to support their conclusions, including immunohistochemistry and in situ analyses of a number of markers of this population which appear to stream from the midbrain into the dorsal anterior cerebellar anlage.

The inclusion of Otx2-GFP short term lineage analyses and analysis of Atoh1 -/- animals also provide considerable support for the midbrain origin of these neurons as streams of cells seem to emanate from the midbrain. However, without live imaging there remains the possibility that these streams of cells are not actually migrating and rather, gene expression is changing in static cells. Hence the authors have conducted midbrain diI labelling experiments of short term and long term cultured embryos showing di-labelled cells in the developing cerebellum. These studies confirm migration of cells from the midbrain into the early cerebellum.

The authors have appropriately responded to review issues, replacing panels in figures and updating legends and text. They have also appropriately noted the limitations of their work.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

Additional experiments to characterize what this novel cell type becomes in older animals would be ideal to strengthen the manuscript, but the authors should at least address this in the Discussion.

The manuscript could be significantly improved if the authors included, for example, a timeline and/or cartoon contextualizing these cells relative to the formation of other CN neurons and their locations, perhaps as a summary figure at the end. Furthermore, the logic of each figure could be enhanced if the authors graphically show - again, perhaps with a schematic/cartoon - the question being tested for each figure. Furthermore, making the figure titles less descriptive and more explanatory would also help a reader follow the logic of the experiments.

These are indeed valid and important questions for our research, and understanding the distribution, fate, and connectivity of this new cell type in the cerebellar nuclei postnatally is a focus of ongoing investigation in our lab. To address these questions, we are currently utilizing SNCA-GFP mice, a project led by a PhD student in my lab. While this work will be the subject of a full-length research paper, we do add a sentence to the paper concerning a recent report about the presence of SNCA neurons in the adult CN.  We have included a reference to the postnatal expression of SNCA (“In adult mice, postnatal expression of SNCA has been reported in medial CN neurons. PMID: 32639229”.) on page 8 of our manuscript (highlighted in yellow). In addition, we have included a cartoon as a summary figure (Fig. 9) illustrating the origin of cerebellar nuclei from the caudal and rostral ends in both Atoh1+/+ and Atoh1-/- mice. Thank you once again, we have revised and improved the Fig. titles accordingly.

Reviewer #2 (Recommendations For The Authors):

Figure 3:

(1) If most SNCA+ cells are OTX2+ based on the IHCs, why are there so many SNCA+ Otx2- cells in the sort?

In each group, 350,000 cells were sorted. Due to the relatively small population size of this subset of cerebellar nuclei neurons, the sorting procedure could not perfectly mirror our immunohistochemistry results. In each group, 350,000 cells were sorted. Due to the relatively small population size of this subset of cerebellar nuclei neurons, the sorting procedure could not perfectly mirror our immunohistochemistry results. However, it is noteworthy that a portion of sorted cells expressed SNCA or Otx2 while a smaller population co-expressed both Otx2 and SNCA in the cerebellar primordium.

(2) Panel 3F: FACS graphs - the resolution of the figures is too poor on the PDF to read any of the text of these graphs. What are the axes?

We thank the reviewer for this comment. In the revision a high resolution of the FACS graph has replaced the lower quality graph in panel 3F. This clearly identifies the axes and text for this panel.

Figure 4:

(1) Arrowheads are making a subset of + cerebellar cells -Why? Not defined in the legend.

The population of cells indicated by the arrowheads are now defined in the legend. We have added the statement “Examples of Otx2 expressing cells are indicated by arrowheads in panels B, D, E, and F.”

(2) The orientation of panels E and F is unclear - please provide low mag panel insets.

An orientation marker (ie, (r-c and d-v; rostral caudal and dorsal ventral, respectively)) has been added to panel A, which applies to all panels, including panels E and F. Furthermore, the isthmus is noted with an “i” to provide further orientation.

(3) G - and throughout the paper - whisker plots (not simple box plots) are required. Also, it is unclear from the methods how Otx2+ cells were counted - how many embryos/age? The description of 10 sections across 3 slides is incomplete. Are these cells distributed equally across the mediolateral axis of the anlage? Where are comparable M/L sections compared across ages? Is the increase in # across time because these cells are proliferative or are more migrating into the anlage?

The plot has been replaced with whisker plots. A more detailed description of the Method used has been on page 15; “To assess the number of OTX2-positive cells, we conducted immunohistochemistry (IHC) labeling on slides containing serial sections from embryonic days 12, 13, 14, and 15 (n=3 at each timepoint). Under the microscope, we systematically counted OTX2-positive cells within the cerebellar primordium. This analysis encompassed a minimum of 10 sections, spread across at least 3 slides, ensuring comprehensive coverage of OTX2 expression along the mediolateral axis of the cerebellar primordium. For each slide, the counts of OTX2-positive cells from all sections were cumulatively calculated to determine the total number of positive cells per slide. Subsequently, statistical analysis was employed to compare the results obtained different developmental time points.”

Figure 5:

The use of confocal microscopy creates clear data re Otx2-GFP expression, but I cannot understand the origin of the panels. How do they relate to E/F and H/I? Different sections?

In Figure 5, panels A-D display Otx2 expressing cells in the cerebellar primordium of Otx2-GFP transgenic mice, whereas panels E-J depict RNAscope fluorescence in situ hybridization (FISH) for the Otx2 probe in wild type mice. These represent complementary approaches to map Otx2+ cells in the developing cerebellum. This is made clear in a revised legend in Fig 5.

Figure 6:

The justification for the in-culture experiments, particularly the long (4 and 21DIV) times is unclear and needs to be strengthened or the in vitro data should be removed.

Thank you for the respected reviewer’s comment. The E-H panels, show the co-expression of SNCA and p75NTR, highlight a significant role in the differentiation of specific neuronal populations during development. These findings validate our previous results (PMID: 31509576) and are consistent with the results of our current study. Therefore, we have chosen to keep these panels. However, in line with the suggestion from the reviewer, we have removed panels I-L from Fig. 6.

Figure 7:

SNCA expression in panels A and G is not specific nor is the Otx2 staining in panel B making the data in panels C and I uninterpretable and these panels need to be replaced. The Meis2 data however is much better and I agree this data shows that the dorsal RL-derived cells are deleted in Atoh1-/- while the SNCA+ cells remain. This is strong data supporting the dual origins of NTZ.

Thank you for the points, Panel A and G have been replaced with high-resolution images. In addition, panels A-C have been carefully cropped to enhance focus on the NTZ area, to improve the quality and visibility of panels.  To enhance clarity, we have included a summary fig. 9 for clarification.

Figure 8:

The diI experiments are a key addition to this paper and clearly show the direct movement of some cells from the mesencephalon into the developing cerebellum, but data presentation must be considerably strengthened.

(1) What is the inset in panel A? Low mag of embryo? Perhaps conversion of image to PDF degraded resolution - add a description in the legend. Arrowhead and arrow identities are reversed in the legend. The arrow points to the isthmus.

Thank you for the comment, for clarification we have included information in the Fig. legend (highlighted in yellow). In addition, the issues with the arrows have been addressed and corrected.

(2) Panels B and C are also shown in Supplementary Figure 2 with arrows indicating rostral and caudal movement - these arrows need to be added here. There is no need to replicate these same panels in the supplement.

Thanks, arrows have been added in panels B, C of Fig. 8.

(3) The text states that "almost all DiI cells migrated caudally into the cerebellum" and refers to Figure 8E and Suppementl 3 but there is no evidence/support shown for this, just a few + cells in 8E and some very difficult-to-see positive cells in sections in Supplement E-F. Given the importance of this data, I am surprised that the authors chose bright field/phase microscopy to show this. This section's data is not convincing data at all. I find it very difficult to see specific staining. These panels must be improved. This is key data for paper conclusions.

These are valid points, and we acknowledge that this experiment alone may not provide conclusive evidence regarding the subset of CN originating from mesencephalon. At this stage of the study, we do not claim definitively that the SNCA/OTX2/MEIS2 positive cells originate from the mesencephalon. As stated in our manuscript, "In conclusion, our study indicates that the SNCA+/ OTX2+/ MEIS2+/ p75NTR+/ LMX1A- rostroventral subset of CN neurons do not originate from the well-known distinct germinative zones of the cerebellar primordium. Instead, our findings suggest the existence of a previously unidentified extrinsic germinal zone, potentially the mesencephalon."  We have also discussed embryonic culture approaches in the manuscript, which could involve the use of other agents such as plasmid/viral vectors, hinting at the possibility of origin from the mesencephalon. While tracing the origin from the mesencephalon in vivo and in vitro is promising and on our to-do list, the data will not be available for this manuscript. To prevent confusion, we have eliminated redundant panels of Fig. 8 with Supplementary Fig. 2 and 3. However, if the reviewer deems it necessary to remove these panels, we are prepared to do so.

Reviewer #2 (Public Review):

Summary:

Complexin (Cplx) is expressed at nearly all chemical synapses. Mammalian Cplx comes in four different paralogs which are differentially expressed in different neurons or secretory cell types, either selectively or in combination with one or two other Cplx isoforms. Cplx binds with high affinity to assembled SNARE complexes and promotes evoked synchronous release. Cplx is assumed to preclude premature SV fusion by preventing full SNARE assembly, thereby arresting subsequent SNARE-driven fusion ("fusion-clamp" theory). The protein has multiple domains, the functions of which are controversially discussed. Cplx's function has been studied in a variety of model organisms including mouse, fly, worm, and fish with seemingly conflicting results which led to partly contradicting conclusions.<br /> Makee et al. study the function of mammalian Cplx2 in chromaffin cells by making use of Cplx2 ko mice to overexpress and functionally characterize mutant Cplx2 forms in cultured chromaffin cells. The main conclusion of the present study are:

The hydrophobic character of the amphipathic helix in Cplx's C-terminal domain is essential for inhibiting premature vesicle fusion at a [Ca2+]i of several hundreds of nM (pre-flash [Ca2+]i). The Cplx-mediated inhibition of fusion under these conditions does not rely on expression of either Syt1 or Syt7.

Slow-down of exocytosis by N-terminally truncated Cplx mutants in response to a [Ca2+]i of several µM (peak flash [Ca2+]i) occurs regardless of the presence or absence of Syt7 demonstrating that Cplx2 does not act as a switch favoring preferential assembly of the release machinery with Syt1,2 rather than the "slow" sensor Syt7.

Cplx's N-terminal domain is required for the Cplx2-mediated increase in the speed of exocytosis and faster onset of exocytosis which likely reflect an increased apparent Ca2+ sensitivity and faster Ca2+ binding of the release machinery.

Strengths:

The authors perform systematic truncation/mutational analyses of Cplx2. They analyze the impact of single and combined deficiencies for Cplx2 and Syt1 to establish interactions of both proteins.<br /> State-of-the-art methods are employed: Vesicle exocytosis is assayed directly and with high resolution using capacitance measurements. Intracellular [Ca2+] is controlled by loading via the patch-pipette and by UV-light induced flash-photolysis of caged [Ca2+]. The achieved [Ca2+ ] is measured with Ca2+ -sensitive dyes.<br /> The data is of high quality and the results are compelling.

Weaknesses:

With the exception of mammalian retinal ribbon synapses (and some earlier RNAi knock down studies which had off-target effects), there is little experimental evidence for a "fusion-clamp"-like function of Cplxs at mammalian synapses. At conventional mammalian synapses, genetic loss of Cplx (i.e. KO) consistently decreases AP-evoked release, and generally either also decreases spontaneous release rates or does not affect spontaneous release, which is inconsistent with a "fusion-clamp" theory. This is in stark contrast to invertebrate (D. m. and C. e.) synapses where genetic Cplx loss is generally associated with a strong upregulation of spontaneous release.

There are alternative scenarios explaining how Cplx may phenomenological "clamp" vesicle fusion rates without mechanistically assigning a "clamping" function to Cplx (Neher 2010, Neuron). In fact, changes in asynchronous release kinetics following conditioning AP trains observed at Cplx1 ko calyx of Held synapses do not favor a "fusion clamp" model (Chang et al., 2015, J.Neurosci.), while an alternative model, assigning Cplx the role of a "checkpoint" protein in SNARE assembly, quantitatively reproduces all experimental observations (Lopez et al., 2024, PNAS). It might be helpful for a reader to mention such alternative scenarios.

eLife assessment

This important work shows compelling data that significantly advances our understanding of the regulation of neurotransmitter and hormone secretion by exploring the mechanisms of how the protein complexin 2 (Cplx2) interacts with the calcium sensor synaptotagmin. The function of mammalian Cplx2 is studied using chromaffin cells derived from Cplx2 knock out mice as a system to overexpress and functionally characterize mutant Cplx2 forms and the interaction between Cplx2 and synaptotagmin. The authors identify structural requirements within the protein for Cplx's dual role in preventing premature vesicle exocytosis and enhancing evoked exocytosis. The findings are of broad interest to neuroscientists and cell biologists.

Reviewer #1 (Public Review):

Summary:

Using chromaffin cells as a powerful model system for studying secretion, the authors study the regulatory role of complexin in secretion. Complexin is still enigmatic in its regulatory role, as it both provides inhibitory and facilitatory functions in release. The authors perform an extensive structure-function analysis of both the C- and N-terminal regions of complexin. There are several interesting findings that significantly advances our understanding of cpx/SNARe interactions in regulating release. C-terminal amphipathic helix interferes with SNARE complex assembly and thus clamps fusion. There are acidic residues in the C-term that may be seen as putative interaction partners for Synaptotagmin. The N-terminus of Complexin promoting role may be associated with an interaction with Syt1. In particular the putative interaction with Syt1 is of high interest and supported by quite strong functional and biochemical evidence. The experimental approaches are state of the art, and the results are of the highest quality and convincing throughout. They are adequate and intelligently discussed in the rich context of the standing literature. Whilst there are some concerns about whether the facilitatory actions of complexion have to be tightly linked to Syt1 interactions, the proposed model will significantly advance the field by providing new directions in future research.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

The revised manuscript addressed my minor concerns adequately, and the manuscript is now further improved. I have no remaining criticisms.

Reviewer #2 (Recommendations For The Authors):

Abstract:

line 45 The abbreviation "SytI" should perhaps be introduced above.

done

Results:

line 139 "RRP kinetics" should perhaps read "RRP depletion kinetics" or "secretion kinetics".

We replaced “RRP kinetics” with “RRP secretion kinetics”

line 325ff and Figure 8

As far as I understand, SytI 875 R233Q ki cells shown in violet express wt CplxII. Perhaps this should be explicitly stated?

To accommodate this suggestion: We now state on page 13 line 302: “Overexpression of the CpxII DN mutant in SytI R233Q ki cells, which is expected to outcompete the function of endogenous CpxII in these cells (Dhara et al., 2014), further slowed down the rate of synchronized release and restored the EB size to the wt level (Figure 7C, D)”

line 332ff and Figure 8

What is plotted in Figure 8B bottom and in Figure 8D is not a "rate" but rather a "unitary rate", more commonly referred to as a "rate constant".

The y-axis label of Figures 8B and 8D should therefore better be changed to "rate constant". See also line 528 of the Discussion.

Figure (y-axis label) and text were changed accordingly

eLife assessment

The ExA-SPIM methodology developed will be important to the field of light sheet microscopy as the new technology provides an impressive field of view making it possible to image the entire expanded mouse brain at cellular and subcellular resolution. The authors provide solid evidence that mostly supports the conclusions.

Reviewer #1 (Public Review):

Summary:

Glaser et al present ExA-SPIM, a light-sheet microscope platform with large volumetric coverage (Field of view 85mm^2, working distance 35mm ), designed to image expanded mouse brains in their entirety. The authors also present an expansion method optimized for whole mouse brains, and an acquisition software suite. The microscope is employed in imaging an expanded mouse brain, the macaque motor cortex and human brain slices of white matter.<br /> This is impressive work, and represents a leap over existing light-sheet microscopes. As an example, it offers a ~ fivefold higher resolution than mesoSPIM (https://mesospim.org/), a popular platform for imaging large cleared samples. Thus while this work is rooted in optical engineering, it manifests a huge step forward and has the potential to become an important tool in the neurosciences.

Strengths:

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

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

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

Weaknesses:

-There is a general question about the scaling laws of lenses, and expansion microscopy, which in my opinion remained unanswered: In the context of whole brain imaging, a larger expansion factor requires a microscope system with larger volumetric coverage, which in turn will have lower resolution (Figure 1B). So what is optimal? Could one alternatively image a cleared (non-expanded) brain with a high resolution ASLM system (Chakraborty, Tonmoy, Nature Methods 2019, potentially upgraded with custom objectives) and get similar effective resolution as the authors get with expansion? This is not meant to diminish the achievement, but it was unclear if the gains in resolution from the expansion factor are traded off by the scaling laws of current optical systems.

-It was unclear if 300 nm lateral and 800 nm axial resolution is enough for many questions in neuroscience. Segmenting spines, distinguishing pre- and postsynaptic densities, or tracing densely labeled neurons might be challenging. A discussion about the necessary resolution levels in neuroscience would be appreciated.

-Would it be possible to characterize the aberrations that might be still present after whole brain expansion? One approach could be to image small fluorescent nanospheres behind the expanded brain, and recover the pupil function via phase retrieval. But even full width half maximum (FWHM) measurements of the nanospheres' images would give some idea of the magnitude of the aberrations.

Review of the revised manuscript:

The authors have carefully addressed my concerns and suggestions.

I appreciate the extended discussion on tissue clearing compared to expansion. I would recommend substantiating some of the statements though with references, or in other instances expanding a little further. I would encourage the authors to consider the points below. But there is also another path to actually reduce that specific discussion, if the conclusion is that it opened more questions than answers.

Specifically, here are some points in the paragraph that discusses tissue clearing and expansion that could be improved:<br /> -The statement "Spherical aberration increases with NA" reads nonspecific to me. I think a more precise formulation would be "The effect of spherical aberration (e.g. loss of Strehl ratio) increases with NA. The stated third power law would also benefit from a reference.<br /> -The statement "the index of refraction gradients in tissue decreases with the third power of the expansion factor..." reads a bit odd. "Gradients in refractive index" would be more consistent with the usage of r.i. throughout the manuscript.<br /> For the third power law, it might be important to know what drives the remaining refractive index variation in expansion microscopy. If it is the labels and their linkers, then indeed, they get increasingly diluted as their amount remains constant. However, if the aberrations are caused by the polymer gel, I would assume you would need more monomer material for higher expansion factors? Thus, I was not fully sure about the scaling law in this case. If there is a reference where this was explored in detail, that would resolve this issue.

-The statement that aberrations scale with gradients in refractive index also needs either a reference, or an explanation for the reader. I think figure S4 was supposed to illustrate this, but was not referenced in the discussion (and could be clarified, see comment below).

To me, the discussion focused strongly on tissue clearing vs expansion. What was left out in the discussion was if larger expansion factors would be favorable (i.e. whole brain imaging with 10-20X expansion instead of 4-5X). Some arguments implicitly seemed to stipulate that a larger expansion factor would optically be favorable. But Figure S7 highlights another tradeoff with the decay in sensitivity and Figure 1b provides the technological constraints on lens design. So as a reader, I was not fully sure if the next frontier should be 10-20X expansion brain imaging, or if 4-5X is currently a sweet spot.

Further comments:

Please explain the variables in Figure S4, such as F, WD and d. It was unclear to me what the RI profile should mean in the bottom row. Naively, the figure of merit would be the optical path length that is integrated along the different rays, as this leads to a variation in the wavefront.

Figure S5: I would caution to say the SNR was quantified, but rather say it was estimated (in the shot noise limit). Was the background subtracted for the SNR measurements?<br /> Squaring the SNR estimates, it looks like the photon counts went down ~10-fold from z=2mm to z=25mm. That is a larger reduction in signal than I had expected. If it was based solely on aberrations, a 10-fold drop in Strehl ratio seems significant (potentially smaller if we assume the light-sheet also underwent aberrations). Are there other factors that could explain the signal reduction (maybe from the labeling side)?<br /> Further on Figure S5: Fourier transforms (power spectrum) and single line profiles are in my opinion not the best way to quantify resolution. Could the authors perform image decorrelation analysis on the region of interest (Descloux, A., Kristin Stefanie Grußmayer, and Aleksandra Radenovic. "Parameter-free image resolution estimation based on decorrelation analysis." Nature methods 2019) or Fourier ring correlation? This would give in some sense an average resolving power in that depth, and would remove the bias from picking a line profile.

Reviewer #2 (Public Review):

Summary:

In this revised manuscript, Glaser et al. have responded to the reviewer comments by removing some of the overstated claims from the prior manuscript and editing portions of the manuscript text to enhance the clarity. Although the manuscript would be stronger if the authors had been able to provide data that justified the original high-impact claims from the initial publication (e.g. that the images could be used for robust and automated neuronal tracing across large volumes), the amended manuscript text now more closely matches the supporting data. As with the initial submission, I believe that the microscope design and characterization is a useful contribution to the field and the data are quite stunning. However, I still feel like there are some overstated claims in this revision that should be addressed so as not to mislead readers.

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

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

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

Strengths: 

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

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

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

Weaknesses: 

- There is a general question about the scaling laws of lenses, and expansion microscopy, which in my opinion remained unanswered: In the context of whole brain imaging, a larger expansion factor requires a microscope system with larger volumetric coverage, which in turn will have lower resolution (Figure 1B). So what is optimal? Could one alternatively image a cleared (non-expanded) brain with a high-resolution ASLM system (Chakraborty, Tonmoy, Nature Methods 2019, potentially upgraded with custom objectives) and get a similar effective resolution as the authors get with expansion? This is not meant to diminish the achievement, but it was unclear if the gains in resolution from the expansion factor are traded off by the scaling laws of current optical systems. 

Paraphrasing the reviewer: Expanding the tissue requires imaging larger volumes and allows lower optical resolution. What has been gained?

The answer to the reviewer’s question is nuanced and contains four parts. 

First, optical engineering requirements are more forgiving for lenses with lower resolution. Lower resolution lenses can have much larger fields of view (in real terms: the number of resolvable elements, proportional to ‘etendue’) and much longer working distances. In other words, it is currently more feasible to engineer lower resolution lenses with larger volumetric coverage, even when accounting for the expansion factor. 

Second, these lenses are also much better corrected compared to higher resolution (NA) lenses. They have a flat field of view, negligible pincushion distortions, and constant resolution across the field of view. We are not aware of comparable performance for high NA objectives, even when correcting for expansion.

Third, although clearing and expansion render tissues ‘transparent’, there still exist refractive index inhomogeneities which deteriorate image quality, especially at larger imaging depths. These effects are more severe for higher optical resolutions (NA), because the rays entering the objective at higher angles have longer paths in the tissue and will see more aberrations. For lower NA systems, such as ExaSPIM, the differences in paths between the extreme and axial rays are relatively small and image formation is less sensitive to aberrations. 

Fourth, aberrations are proportional to the index of refraction inhomogeneities (dn/dx). Since the index of refraction is roughly proportional to density, scattering and aberration of light decreases as M^3, where M is the expansion factor. In contrast, the imaging path length through the tissue only increases as M. This produces a huge win for imaging larger samples with lower resolutions. 

To our knowledge there are no convincing demonstrations in the literature of diffraction-limited ASLM imaging at a depth of 1 cm in cleared mouse brain tissue, which would be equivalent to the ExA-SPIM imaging results presented in this manuscript.  

In the discussion of the revised manuscript we discuss these factors in more depth. 

- It was unclear if 300 nm lateral and 800 nm axial resolution is enough for many questions in neuroscience. Segmenting spines, distinguishing pre- and postsynaptic densities, or tracing densely labeled neurons might be challenging. A discussion about the necessary resolution levels in neuroscience would be appreciated. 

We have previously shown good results in tracing the thinnest (100 nm thick) axons over cm scales with 1.5 um axial resolution. It is the contrast (SNR) that matters, and the ExaSPIM contrast exceeds the block-face 2-photon contrast, not to mention imaging speed (> 10x).  

Indeed, for some questions, like distinguishing fluorescence in pre- and postsynaptic structures, higher resolutions will be required (0.2 um isotropic; Rah et al Frontiers Neurosci, 2013). This could be achieved with higher expansion factors.

This is not within the intended scope of the current manuscript. As mentioned in the discussion section, we are working towards ExA-SPIM-based concepts to achieve better resolution through the design and fabrication of a customized imaging lens that maintains a high volumetric coverage with increased numerical aperture.  

- Would it be possible to characterize the aberrations that might be still present after whole brain expansion? One approach could be to image small fluorescent nanospheres behind the expanded brain and recover the pupil function via phase retrieval. But even full width half maximum (FWHM) measurements of the nanospheres' images would give some idea of the magnitude of the aberrations. 

We now included a supplementary figure highlighting images of small axon segments within distal regions of the brain.  

Reviewer #2 (Public Review): 

Summary: 

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

Strengths: 

I commend the authors for making all of the documentation, models, and acquisition software openly accessible and believe that this will help assist others who would like to replicate the instrument. I anticipate that the protocols for imaging large expanded tissues (such as an entire mouse brain) will also be useful to the community. 

Weaknesses: 

The characterization of the instrument needs to be improved to validate the claims. If the manuscript claims that the instrument allows for robust automated neuronal tracing, then this should be included in the data. 

The reviewer raises a valid concern. Our assertion that the resolution and contrast is sufficient for robust automated neuronal tracing is overstated based on the data in the paper. We are hard at work on automated tracing of datasets from the ExA-SPIM microscope. We have demonstrated full reconstruction of axonal arbors encompassing >20 cm of axonal length.  But including these methods and results is out of the scope of the current manuscript. 

The claims of robust automated neuronal tracing have been appropriately modified.  

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Smaller questions to the authors: 

- Would a multi-directional illumination and detection architecture help? Was there a particular reason the authors did not go that route?

Despite the clarity of the expanded tissue, and the lower numerical aperture of the ExA-SPIM microscope, image quality still degrades slightly towards the distal regions of the brain relative to both the excitation and detection objective. Therefore, multi-directional illumination and detection would be advantageous. Since the initial submission of the manuscript, we have undertaken re-designing the optics and mechanics of the system. This includes provisions for multi-directional illumination and detection. However, this new design is beyond the scope of this manuscript. We now mention this in L254-255 of the Discussion section.

- Why did the authors not use the same objective for illumination and detection, which would allow isotropic resolution in ASLM? 

The current implementation of ASLM requires an infinity corrected objective (i.e. conjugating the axial sweeping mechanism to the back focal plane). This is not possible due to the finite conjugate design of the ExA-SPIM detection lens.

More fundamentally, pushing the excitation NA higher would result in a shorter light sheet Rayleigh length, which would require a smaller detection slit (shorter exposure time, lower signal to noise ratio). For our purposes an excitation NA of 0.1 is an excellent compromise between axial resolution, signal to noise ratio, and imaging speed. 

For other potentially brighter biological structures, it may be possible to design a custom infinity corrected objective that enables ASLM with NA > 0.1.

- Have the authors made any attempt to characterize distortions of the brain tissue that can occur due to expansion? 

We have not systematically characterized the distortions of the brain tissue pre and post expansion. Imaged mouse brain volumes are registered to the Allen CCF regardless of whether or not the tissue was expanded. It is beyond the scope of this manuscript to include these results and processing methods, but we have confirmed that the ExA-SPIM mouse brain volumes contain only modest deformation that is easily accounted for during registration to the Allen CCF. 

- The authors state that a custom lens with NA 0.5-0.6 lens can be designed, featuring similar specifications. Is there a practical design? Wouldn't such a lens be more prone to Field curvature? 

This custom lens has already been designed and is currently being fabricated. The lens maintains a similar space bandwidth product as the current lens (increased numerical aperture but over a proportionally smaller field of view). Over the designed field of view, field curvature is <1 µm. However, including additional discussion or results of this customized lens is beyond the scope of this manuscript.

Reviewer #2 (Recommendations For The Authors): 

• System characterization: 

- Please state what wavelength was used for the resolution measurements in Figure 2.

An excitation wavelength of 561 nm was used. This has been added to the manuscript text.

- The manuscript highlights that a key advance for the microscope is the ability to image over a very large 13 mm diameter field of view. Can the authors clarify why they chose to characterize resolution over an 8diameter mm field rather than the full area? 

The 13 mm diameter field of view refers to the diagonal of the 10.6 x 8.0 mm field of view. The results presented in Figure 1c are with respect to the horizontal x direction and vertical y direction. A note indicating that the 13 mm is with respect to the diagonal of the rectangular imaging field has been added to the manuscript text. The results were presented in this way to present the axial and lateral resolution as a function of y (the axial sweeping direction).

- The resolution estimates seem lower than I would expect for a 0.30 NA lens (which should be closer to ~850 nm for 515 nm emission). Could the authors clarify the discrepancy? Is this predicted by the Zemax model and due to using the lens in immersion media, related to sampling size on the camera, or something else? It would be helpful if the authors could overlay the expected diffraction-limited performance together with the plots in Figure 2C. 

As mentioned previously, the resolution measurements were performed with 561 nm excitation and an emission bandpass of ~573 – 616 nm (595 nm average). Based on this we would expect the full width half maximum resolution to be ~975 nm. The resolution is in fact limited by sampling on the camera. The 3.76 µm pixel size, combined with the 5.0X magnification results in a sampling of 752 nm. Based on the Nyquist the resolution is limited to ~1.5 µm. We have added clarifying statements to the text.

- I'm confused about the characterization of light sheet thickness and how it relates to the measured detection field curvature. The authors state that they "deliver a light sheet with NA = 0.10 which has a width of 12.5 mm (FWHM)." If we estimate that light fills the 0.10 NA, it should have a beam waist (2wo) of ~3 microns (assuming Gaussian beam approximations). Although field curvature is described as "minimal" in the text, it is still ~10-15 microns at the edge of the field for the emission bands for GFP and RFP proteins. Given that this is 5X larger than the light sheet thickness, how do the authors deal with this? 

The generated light sheet is flat, with a thickness of ~ 3 µm. This flat light sheet will be captured in focus over the depth of focus of the detection objective. The stated field curvature is within 2.5X the depth of focus of the detection lens, which is equivalent to the “Plan” specification of standard microscope objectives.

- In Figure 2E, it would be helpful if the authors could list the exposure times as well as the total voxels/second for the two-camera comparison. It's also worth noting that the Sony chip used in the VP151MX camera was released last year whereas the Orca Flash V3 chosen for comparison is over a decade old now. I'm confused as to why the authors chose this camera for comparison when they appear to have a more recent Orca BT-Fusion that they show in a picture in the supplement (indicated as Figure S2 in the text, but I believe this is a typo and should be Figure S3). 

This is a useful addition, and we have added exposure times to the plot. We have also added a note that the Orca Flash V3 is an older generation sCMOS camera and that newer variants exist. Including the Orca BT-Fusion. The BT-Fusion has a read noise of 1.0 e- rms versus 1.6 e- rms, and a peak quantum efficiency of ~95% vs. 85%. Based on the discussion in Supplementary Note S1, we do not expect that these differences in specifications would dramatically change the data presented in the plot. In addition, the typo in Figure S2 has been corrected to Figure S3.

- In Table S1, the authors note that they only compare their work to prior modalities that are capable of providing <= 1 micron resolution. I'm a bit confused by this choice given that Figure 2 seems to show the resolution of ExA-SPIM as ~1.5 microns at 4 mm off center (1/2 their stated radial field of view). It also excludes a comparison with the mesoSPIM project which at least to me seems to be the most relevant prior to this manuscript. This system is designed for imaging large cleared tissues like the ones shown here. While the original publication in 2019 had a substantially lower lateral resolution, a newer variant, Nikita et al bioRxiv (which is cited in general terms in this manuscript, but not explicitly discussed) also provides 1.5-micron lateral resolution over a comparable field of view. 

We have updated the table to include the benchtop mesoSPIM from Nikita et al., Nature Communications, 2024. Based on this published version of the manuscript, the lateral resolution is 1.5 µm and axial resolution is 3.3 µm. Assuming the Iris 15 camera sensor, with the stated 2.5 fps, the volumetric rate (megavoxels/sec) is 37.41.

- The authors state that, "We systematically evaluated dehydration agents, including methanol, ethanol, and tetrahydrofuran (THF), followed by delipidation with commonly used protocols on 1 mm thick brain slices. Slices were expanded and examined for clarity under a macroscope." It would be useful to include some data from this evaluation in the manuscript to make it clear how the authors arrived at their final protocol. 

Additional details on the expansion protocol may be included in another manuscript.

General comments: 

• There is a tendency in the manuscript to use negative qualitative terms when describing prior work and positive qualitative terms when describing the work here. Examples include: 

- "Throughput is limited in part by cumbersome and error-prone microscopy methods". While I agree that performing single neuron reconstructions at a large scale is a difficult challenge, the terms cumbersome and error-prone are qualitative and lacking objective metrics.

We have revised this statement to be more precise, stating that throughput is limited in part by the speed and image quality of existing microscopy methods.

- The resolution of the system is described in several places as "near-isotropic" whereas prior methods were described as "highly anisotropic". I agree that the ~1:3 lateral to axial ratio here is more isotropic than the 1:6 ratio of the other cited publications. However, I'm not sure I'd consider 3-fold worse axial resolution than lateral to be considered "near" isotropic.

We agree that the term near-isotropic is ambiguous. We have modified the text accordingly, removing the term near-isotropic and where appropriate stating that the resolution is more isotropic than that of other cited publications.

- exposures (which in the caption is described as "modest"). I'd suggest removing these qualitative terms and just stating the values.

We agree and have changed the text accordingly.

• The results section for Figure 5 is titled "Tracing axons in human neocortex and white matter". Although this section states "larger axons (>1 um) are well separated... allowing for robust automated and manual tracing" there is no data for any tracing in the manuscript. Although I agree that the images are visually impressive, I'm not sure that this claim is backed by data.

We have now removed the text in this section referring to automated and manual tracing.

eLife assessment

The paper investigates a potential cause of a type of severe epilepsy that develops in early life because of a defect in a gene called KCNQ2. The significance is fundamental because it substantially advances our understanding of a major research question. The strength of the evidence is convincing because appropriate methods are used that are in line with the state-of-the art.

Reviewer #1 (Public Review):

Abreo et al., performed a detailed multidisciplinary analysis of a pathogenic variant of the KCNQ2 ion channel subunit identified in a child with neonatal-onset epilepsy and neurodevelopmental disorders. These analyses revealed multiple molecular and cellular mechanisms associated with this variant, and providing important insights into what distinguishes distinct pathogenic variants of KCNQ2 associated with self-limited familial neonatal epilepsy versus those leading to developmental and epileptic encephalopathy, and how they may mechanistically differ, to result in different extents of developmental impairment. The authors first provide a detailed clinical description of the patient heterozygous for a novel pathogenic variant encoding KCNQ2 G256W. They then model the structure of the G256W variant based on recent cryo-EM structures of KCNQ2 and other ion channel subunits and find that while the affected position is quite distinct from the channel pore, it participates in a novel, evolutionarily conserved set of amino acids that form a network of hydrogen bonds that stabilize the structure of the pore domain. They then undertake a series of rigorous and quantitative laboratory experiments in which the KCNQ2 G256W variant is coexpressed exogenously with WT KCNQ2 and KCNQ3 subunits in heterologous cells, and endogenously in novel gene edited mice generated for this study. This includes detailed electrophysiological analyses in the transfected heterologous cells revealing the dominant-negative phenotype of KCNQ2 G256W. They find altered firing properties in hippocampal CA1 neurons in brain slices from the heterozygous KCNQ2 G256W mice. They next show that the expression and localization of KCNQ channels is altered in brain neurons from heterozygous KCNQ2 G256W mice, suggesting that this variant impacts KCNQ2 trafficking and stability. Together, these laboratory studies reveal that the molecular and cellular mechanisms shaping KCNQ channel expression, localization and function are impacted at multiple levels by the variant encoding KCNQ2 G256W, likely contributing to the clinical features of the child heterozygous for this variant relative to patients harboring distinct KCNQ2 pathogenic variants.

Reviewer #3 (Public Review):

Summary:

This manuscript describes the symptoms of patients harboring KCNQ2 mutation G256W, functional changes of the mutant channel in exogenous expression, and phenotypes of G256W/+ mice. The patients presented seizures, the mutation reduced currents of the channel, and the G256W/+ mice show seizures, increased firing frequency in neurons, and reduced KCNQ2 expression and altered subcellular distribution.

Strengths:

This is a large amount of work and all results corroborated the pathogenicity of the mutation in KCNQ2, providing an interesting example of KCNQ2-associated neurological disorder's impact on functions at all levels including molecular, cellular, tissue, animal model and patients.

Author response:

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

eLife assessment

The paper investigates a potential cause of a type of severe epilepsy that develops in early life because of a defect in a gene called KCNQ2. The significance is fundamental because it substantially advances our understanding of a major research question. The strength of the evidence is convincing because appropriate methods are used that are in line with the state-of-the art, although there are some revisions/corrections that would strengthen the evidence further.

Thank you for the expert, thorough, and helpful review.  We believe that addressing the reviewers’ points has improved our paper greatly.   

Public Reviews:

Reviewer #1 (Public Review):

Abreo et al. performed a detailed multidisciplinary analysis of a pathogenic variant of the KCNQ2 ion channel subunit identified in a child with neonatal-onset epilepsy and neurodevelopmental disorders. These analyses revealed multiple molecular and cellular mechanisms associated with this variant and provided important insights into what distinguishes distinct pathogenic variants of KCNQ2 associated with self-limited familial neonatal epilepsy versus those leading to developmental and epileptic encephalopathy, and how they may mechanistically differ, to result in different extents of developmental impairment.

The authors first provide a detailed clinical description of the patient heterozygous for a novel pathogenic variant encoding KCNQ2 G256W. They then model the structure of the G256W variant based on recent cryo-EM structures of KCNQ2 and other ion channel subunits and find that while the affected position is quite distinct from the channel pore, it participates in a novel, evolutionarily conserved set of amino acids that form a network of hydrogen bonds that stabilize the structure of the pore domain.

They then undertake a series of rigorous and quantitative laboratory experiments in which the KCNQ2 G256W variant is coexpressed exogenously with WT KCNQ2 and KCNQ3 subunits in heterologous cells, and endogenously in novel gene-edited mice generated for this study. This includes detailed electrophysiological analyses in the transfected heterologous cells revealing the dominant-negative phenotype of KCNQ2 G256W. They found altered firing properties in hippocampal CA1 neurons in brain slices from the heterozygous KCNQ2 G256W mice.

They next showed that the expression and localization of KCNQ channels are altered in brain neurons from heterozygous KCNQ2 G256W mice, suggesting that this variant impacts KCNQ2 trafficking and stability.

Together, these laboratory studies reveal that the molecular and cellular mechanisms shaping KCNQ channel expression, localization, and function are impacted at multiple levels by the variant encoding KCNQ2 G256W, likely contributing to the clinical features of the child heterozygous for this variant relative to patients harboring distinct KCNQ2 pathogenic variants.

Thank you for the thorough summary and estimation of the initial submission, we are very glad that our approach, analytical methods, and conclusions were convincing.   

Reviewer #2 (Public Review):

Summary:

The paper entitled "Plural molecular and cellular mechanisms of pore domain KCNQ2 encephalopathy" by Abreo et al. is a complex and integrated paper that is well-written with a focus on a single gene variant that causes a severe developmental

encephalopathy. The paper collates clinical outcomes from 4 individuals and investigates a variant causing KCNQ2-DEE using a wide range of experimental techniques including structural biology, in vitro electrophysiology, generation of genetically modified animal models, immunofluorescence, and brain slice recordings. The overall results provide a plausible explanation of the pathophysiology of the G265W variant and provide important findings to the KCNQ2-DEE field as well as beginning to separate the understanding between seizures and encephalopathies.

Strengths:

(1) The authors describe in detail how the structural biology of the channel with a mutation changes the movement of the protein and adds insights into how one variant can change the function of the M-current. The proposed model linking this change to pathogenic consequences should help pave the way for additional studies to further support this type of approach.

(2) The multiple co-expression ratio experiments drill down to the complex nature of the assembly of channels in over-expression systems and help to move toward an understanding of heterozygosity. It might have been interesting if TEA was tested as a blocker to better understand the assembly of the transfected subunits or possibly use vectors to force desired configurations.

(3) The immunofluorescent approach to understanding re-distribution is another component of understanding the function of this critical current. The demonstration that Q2 and Q3 are diminished at the AIS is an important finding and a strength to the totality of the data presented in the paper.

(4) Brain slice work is an important component of studying genetically modified animals as it brings in the systems approach, and helps to explain seizure generation and EEG recordings. The finding that G265W/+ neurons were more sensitive to current injections is a critical component of the paper.

(5) The strength of this body of work is how the authors integrated different scientific approaches to knitting together a compelling set of experiments to better explain how a single variant, and likely extrapolation to other variants, can cause a severe neonatal developmental encephalopathy with a poor clinical outcome.

Thank you for the thorough and encouraging reading of our work and its strengths, we are very glad that, excepting the issues mentioned which we have addressed, our approach and conclusions were convincing.

Weaknesses:

(1) Minor comment: Under the clinical history it is unclear whether the mother was on Leviracetam for suspected in-utero seizures or if Leviracetam was given to individual 1.

The latter seems more likely, and if so this should be reworded.

We revised the results text to clarify that the drug was begun postnatally, after epilepsy was diagnosed in the child.   

(2) As described in the clinical history of patient 1, treatment with ezogabine was encouraging with rapid onset by a parental global impression with difficulty in weaning off the drug. When studying the genetically modified mice, it would have been beneficial to the paper to talk about any ezogabine effects on the genetically modified mice.

We agree this is of great interest, but sampling and metrics are challenging due to the very low frequency of seizures and delayed mortality in the heterozygous G256 mice.  Accordingly, we have not performed ezogabine treatment experiments in the mice described in this study, which model a human variant associated with a brief neonatal window of frequent seizures.  We hope to return this issue using other transgenic mice with higher seizure frequency, but such results are outside the current scope.

(3) It is a bit surprising that CA1 pyramidal neurons from the heterozygous G256W mice have no difference in resting membrane potential. The discussion section might explore this in a bit more detail.

Thank you for raising this issue. This combination of outcomes has been seen previously and is interpreted as an outcome of low somatodendritic surface expression of the channels.  Relatively higher expression within the AIS membrane, with its the relatively small surface area and electrical isolation from the soma, allow the KCNQ2/3 channels to influence AIS excitability with little or (in this instance) undetectable influence on the RMP (see e.g., Otto et al. 2006, PMID: 16481438; Singh et al. 2008, PMID 16481438  for KCNQ2 mutant mice.  See Hu and Bean, 2018, figure 2; PMID: 29526554 for explicit testing via focal AIS vs. somatic blocker perfusion).  Additionally, in previous work, we did not find any changes to the RMP of CA1 pyramidal neurons in either Kcnq2 knockout mice (PMID: 24719109) or mice expressing a Kcnq2 GOF variant (PMID: 37607817).  We modified the discussion including adding references to prior studies combining experimental and multicompartmental computational models.

(4) It was mentioned in the paper about a direct comparison between SLFNE and G256W.

However, in the slice recordings, there was no comparison. Having these data comparing

SLFNE to G256W would have been a more fulsome story and would have added to the concept around susceptibility to action potential firing.

Thank you for this point. We agree that such side-by-side recordings would be interesting.  However, slice recordings were not performed on the SLFNE mice. The study design was based on the fact that extensive prior studies of both haploinsufficient and missense human SLFNE variant mice have been published (Otto et al. 2006 J Neuroscience, PMID: 16481438; Singh et al. 2008, PMID 16481438; Kim et al 2020 PMID: 31283873) and show good agreement, but DEE missense variants have not been previously studied. We revised the discussion, to place the current DEE model results in the context of the prior SNFLE model slice work. We contrast the similarity of the CA1 cellular hyperexcitability phenotype ex vivo (at least in CA1 pyramidal cells) across models to the differences in electrographic and behavioral seizures (i.e., network level physiology).  

Reviewer #3 (Public Review):

Summary:

This manuscript describes the symptoms of patients harboring KCNQ2 mutation G256W, functional changes of the mutant channel in exogenous expression, and phenotypes of G256W/+ mice. The patients presented seizures, the mutation reduced currents of the channel, and the G256W/+ mice showed seizures, increased firing frequency in neurons, reduced KCNQ2 expression, and altered subcellular distribution.

Strengths:

This is a large amount of work and all results corroborated the pathogenicity of the mutation in KCNQ2, providing an interesting example of KCNQ2-associated neurological disorder's impact on functions at all levels including molecular, cellular, tissue, animal model, and patients.

Weaknesses:

The manuscript described observations of changes in association with the mutation at molecular cellular functions and animal phenotype, but the results in some aspects are not as strong as in others. Nevertheless, the manuscript made overarching conclusions even when the evidence was not sufficiently strong.

Thank you for your review.  In our revision (as listed in the recommendations to authors section) we have attempted to better justify the conclusions you mention there.

Recommendations for the authors: 

Reviewer #1 (Recommendations For The Authors):

Suggestions for improved or additional experiments, data, or analyses.

Page 7: the authors' statement that G256 could be intolerant to substitution would be strengthened by a straightforward analysis of available genome- and exome-wide sequencing data to determine the level of genic intolerance at this position in the human population, as has been used previously to highlight critical residues including those impacted by pathogenic variants in many other proteins including ion channels (e.g., Genome Biology 17:9, 2016; Am J Hum Genet 99:1261, 2016; Biochim Biophys Acta Biomemb 1862:183058, 2020).

Thank you for this suggestion, we have revised the opening of this section to point out the low ratio of benign to pathogenic variants in the region surrounding G256 shown by prior work. We have added citations to the papers describing the MTR and gnomAD tools that highlight these data and calculations.   

The overall interpretation of the CHO cell results would be enhanced by the authors including in their discussion an explicit statement that they did not attempt to evaluate the overall and plasma membrane expression levels of the exogenously expressed WT and mutant KCNQ2 subunits, nor that of KCNQ3, in the transfected CHO cells. They could also highlight that this is an important future experiment to determine whether the dominant negative effects are due to impaired expression/trafficking or impaired function of plasma membrane channels, as this may be an important consideration for designing therapeutic strategies.

We agree.  We revised the discussion to explicitly mention this additional direction.  We agree this topic has therapeutic implications, especially given our in vivo protein localization results.  We added a mention that combinations of molecules enhancing surface localization with channel openers could be a therapeutic strategy, analogous to approved therapies for cystic fibrosis.  

The authors conclude that the impact of ezogabine treatment is reduced in the cells expressing G256+/W versus those expressing WT KCNQ2. However, the delta pA/pF graph in panel 3G expresses the effects of ezogabine as absolute increases in current density. Determining the relative increase (i.e., fold change) in current density in ezogabine-treated versus control conditions is a more valid way to analyze these data. This provides a better reflection of the impact of ezogabine as the control currents already have a much larger amplitude than the G256+/W currents. By eye the impact of ezogabine looks comparable or even larger for the G256+/W condition than for WT, fundamentally changing the interpretation of these results.

Thank you for this helpful comment.  The reviewer calls attention to the fact that although G256W/+ mean whole cell currents from are less than WT, before and after application of ezogabine, it appeared from Fig. 3G that ezogabine enhanced currents to a “proportionally equivalent extent” in G256W/+ and WT cells.  We revised panel 3G to try to make this more clear.  It now shows WT currents +/- ezogabine currents normalized to (WT, no ezogabine at +40 mV), along with G256W/+ cells +/- ezogabine currents, normalized to (G256W/+, no ezogabine at +40 mV).  This normalization shows that the mixed population of channels expressed by G256W/+ cells are equally augmented (with a trend toward greater augmentation), compared to controls.  This is a striking result given that channels lacking WT KCNQ2 subunits do not respond to ezogabine (i.e., the “homozygous heteromer” condition, Fig. 3F) do not respond to ezogabine.  Although the underlying data are unchanged, we agree with the reviewers’ conclusion about emphasizing the effect “per channel”.  This reframing is mechanistically and clinically important.  We have made changes to the results text and discussion to highlight related issues.   

Figure 7: it is not clear from the information presented whether the qPCR would only measure WT KCNQ2 mRNA levels or detect levels of both WT and E254fs transcripts. The authors assume nonsense-mediated decay, but they did [not] determine experimentally that this occurred. The sequencing in the supplemental figure shows the presence of E254fs transcripts but does not allow for insights into their abundance. It should be straightforward to develop primer sets that could then be used to selectively amplify WT and E254fs transcripts for quantitation. 

Thank you for this helpful suggestion.  The assay used in the initial submission measures total Kcnq2 mRNA. We developed and performed a new assay where the probe binding site is the WT sequence, centered on the mutations. New Figure 7-Figure supplement 1, panel A is a cartoon showing the differences between the assays.  Using the WT alleleselective RT-qPCR assay, both  G256W/+ and E254fs/+ samples showed a 50% loss of WT Kcnq2.   We now can conclude that NMD is absent for G256W and incomplete for E254fs mRNA. Neither mutant heterozygous line shows a compensatory increase in WT Kcnq2 expression.  These conclusions are much more specific than previously, and documenting incomplete NMD of KCNQ2 is novel and of potential clinical significance.  The KCNQ2 protein (western blot) and WT mRNA (qPCR) results now agree, both showing ~50% loss.   

For reporting transparency, the authors should provide the sequences of each of the primers used. Perhaps this is in the "key reagents" section, but this was missing from the manuscript. I note the authors use NMD in this section without defining it. and added a reference to a review where “incomplete NMD” is discussed.

We have added the assay catalogue numbers to the key reagents table.  We eliminated the use of the NMD abbreviation. We added citations to the “incomplete NMD” literature including an excellent recent review and a directly relevant primary paper.  These show how NMD efficiency may differ: between genes, transcripts, cells, tissues and, remarkably, between human individuals (see doi: 10.1093/hmg/ddz028, cited in the review—caffeine inhibits NMD!).  The revised discussion mentions this, and relevance to future studies of novel KCNQ2 variant pathogenicity and severity prediction.  

Recommendations for improving the writing and presentation.

I found the presentation of the IHC images deficient in terms of accessibility and transparency. While the movies provided are also useful, it is important the authors also provide conventional static merged images of each of their multiplex labeling images in the body of the paper. This allows a reader to see the labeling with the different antibodies in the context of each other (one of the major advantages of multiplex labeling), instead of trying to remember the pattern each label gave in prior sections of the movie.

[We queried the reviewer via the eLife editorial staff]: To clarify my suggestion to improve Figure 8, the authors should generate from their movies static images that are basically what they already did in Fig8S3 for the G256W Het panel of the Fig8 movie. This involves revising Fig8S3 to include WT panels, and adding two new supplemental figures that show WT/Het panels with the separate antibodies and then a merged image from Fig8S1 and Fig8S2, just like they did in Fig8S3 for the mutant part of the Fig8 movie.

Thank you for this comment. As suggested by the reviewer, for each IHC movie (Fig. 8, Fig. 8-figure supplement 1 and Fig. 8-figure supplement 2), we added a new supplementary  figure showing WT and mutant animal static images corresponding to the movies.  For main Figure 8 (CA1, G256W/+ comparison), the new static images enable evaluating the patterns of colocalization by providing selected portions of the images at the highest useful magnification.  These show  each individual antibody in greyscale (best for comparing) and 4 different green-red merged images to show overlap (yellow) vs non-overlap.  The merged images demonstrate colocalization of KCNQ2 and KCNQ3 at the distal portions of AnkG-labelled CA1 pyramidal cell AISs, in agreement with prior publications.  In G256W/+ but not E254fs/+ images, KCNQ2 and KCNQ3 show reduced relative labeling of AISs and increased relative labeling of somata in the pyramidal cell layer.   For CA3, the merged views show the redistributed relative labeling of KCNQ2 and KCNQ3 between stratum lucidum and stratum pyramidale.  

We also revised Fig. 8 supplement 3 (CA1) to include WT panels, On reexamination, all WT interneurons  in the small sample lacked somatic KCNQ2 and KCNQ3 labeling.  Some s. oriens and radiatum AISs of both WT and G256W/+ sections showed KCNQ2 and KCNQ3 labeling, as shown in the revised figure.  Counting statistics are included in the supporting data.  Importantly, our belief that the images shown are representative is supported by the blinded analysis of a much larger sample (Figure 9, unchanged in revision).  

Dragging the movie viewer “slider” allows the viewer to move  back and forth between color channels.  It works well in eLife if used in that way.   This is a way of seeing the “representativeness” of the merges shown in the CA1 conventional static images, which necessarily include a smaller x-y area and include only a few AISs.   We also added a KCNQ2/KCNQ3 merge to the movies. 

Western blot results in Figure 9 - Supplement 1: for transparency, the authors need to show the entire blot, as they did in Figure 4 - Supplement 2. This is required in many journals, and in the case of KCNQ2 it provides crucial information as to the different forms of KCNQ2 present on SDS gels in these samples that contain different KCNQ2 isoforms. Given the surprising decrease in levels of KCNQ2 monomer in the G256+/W mice, it is important to present and analyze the levels of the monomer, dimer, and higher oligomeric forms of KCNQ in these samples, to determine whether protein "missing" in the monomeric form is not present in the dimeric or higher oligomeric form. This is especially important as the G256W mutant could lead to misfolding and aggregation leading to a higher proportion of both WT and G256W subunits being present in a higher-order oligomeric form. I note that it is odd that the figure legend states "Images of entire filter used for western blot of lysates, probed for KCNQ2 and KCNQ3.", even though only selected portions are shown.

Thank you for this suggestion. We agree that the wording of the legend needed improvement.  

In revision, the western blots are renumbered as Figure 10, and Figure 10-Figure supplement 1. In the main figure, monomer bands and densitometry are shown, as previously.  In the new Figure 10-Figure supplement 1,  we show (1) the ECL image of the entire filter probed with rabbit anti-KCNQ2, (2) the same blot, stripped, and reprobed with guinea pig KCNQ3, (3) the lower portion, probed with mouse anti-tubulin. The revised Fig. 10-fig supplement 1 shows 3 genotypes x 3 individual (male) p21 mice, with all steps performed in parallel from homogenization to ECL detection.  As suggested, we performed new analysis of the immunoreactive bands corresponding to (apparent) monomer, dimer, and higher oligomeric forms of KCNQ2. Analysis of the sum of those bands showed loss of KCNQ2 protein in both mutant lines.  

The methods are sufficiently detailed with the exception that there is inconsistent inclusion of catalog numbers and RRIDs. Having these would improve transparency as to specific reagents used and would allow for enhanced reproducibility of the lab research performed here.

The revised submission includes the key resources table, which we understood was not requested from eLife at initial submission. 

Minor corrections to the text and figures.

Typos/mistakes as to antibodies used in the IHC methods section "anti-AnkG36 N106/36 " should be "anti-AnkG N106/36", and "mouse anti-PanNav IgG1 supernatant" should be mouse anti-PanNav IgG1 purified antibody". 

Thank you, corrections made.

It would facilitate a reader's interpretation of the IHC results if the authors explicitly stated in the IHC results section that the KCNQ2 antibody used is against the N-terminus and therefore should recognize both mutant isoforms as the mutations are downstream of this.

We added this point to the results section in relation to Figure 4-figure supplement 2 (western), and in IHC methods.

PV is not defined when used in the discussion, nor is why knowing that somatic KCNQ2 immunolabeling is present in both PV and non- PV interneurons of WT mice of value to the reader.

We revised these sentences for clarity.

The IHC methods state that "mice were transcardially perfused with....ice cold 2% paraformaldehyde in PBS, freshly prepared from a 20% stock (Electron Microscopy Sciences).". The authors presumably mean "formaldehyde" as paraformaldehyde is the inert polymeric storage form of active depolymerized monomeric formaldehyde that is a fixative.

The reviewer is correct regarding the chemistry; the manufacturer’s product name is “Paraformaldehyde 20% aqueous solution”.  We revised accordingly.

Reviewer #3 (Recommendations For The Authors):

Some comments regarding the presentation are as follows.

(1) The section "G256W lies atop a dome-shaped hydrogen bond network linking helix S5 to the turret and selectivity filter" is entirely based on structural observations without functional validation. This may be more appropriate in Discussion. The emphasis on the "turret arch" bonding should be tuned down due to the lack of functional support.

We understand and agree with this concern about the distinction between structural analysis and implied function.  However, we believe that the structural model reinterpretation and phylogenetic sequence analysis in our submission are results.  Structures as complex as those of KCNQ channels necessarily cannot be fully shown or analyzed in an initial publication. To our knowledge, the word “turret” has not appeared in a KCNQ channel cryoEM paper to date.  Bringing clinical motivation to prioritize study of an overlooked spot on the channel is creditworthy. The comprehensive heterologous patch clamp results in our study (including absence of effects on voltage-dependence, evidence of partial functional activity of channels containing one mutant subunit per channel shown for KCNQ2 homomers, KCNQ2/3 heteromers, and via acute ezogabine rescue experiments in the biologically most relevant heteromers) are functional evidence consistent with G256W acting through disruption of the SF.  

However, we agree that more support is needed. The words “dome” and “arch”, though accurate for describing shape, tend to imply a mechanical “load bearing and distributing” function --our study does not prove this. Accordingly, we have toned down the emphasis by removing the words “keystone”, “turret dome bonding”, and  “as a structural novelty” from the abstract.   The revised discussion section replaces arch with “arch-shaped”, calls the idea that the turret functions as a stabilizing arch a “novel hypothesis”, and proposes next experiments (with relevant citations).

Section title "Heterozygous G256W mice have neonatal seizures" does not seem to match the results since there was only one mouse that showed neonatal seizures.

Thank you, we have revised the section title.  The text is transparent regarding sample size. The discussion highlights that these seizures are rare (indeed, not previously shown for any heterozygous missense model, to our knowledge).

(2) It will be nice for the non-expert readers if the observations of "discrete seizures", "clusters", "diffuse bilateral onset", "unilateral onset" etc. are marked in Figure 1.

Thank you for making this point. Figure 1 shows key excerpts of one bilateral onset seizure; a unilateral onset example isn’t shown since previous KCNQ2 DEE papers we cite have emphasized and illustrated focal onset seizures (Weckhuysen et al., 2013; Numis et al., 2014).    We revised the results section (p. 4) and Figure 1 and supplement captions to improve clarity for all readers including non-specialists.  

(3) Figure 5 and page 10 first paragraph. Please specify the number of cells and the number of mice that were studied.

Thank you, this information has been added to legend.

eLife assessment

This study attempts to solve long-standing puzzles about inversion polymorphisms in Drosophila melanogaster by invoking sexually antagonism and negative frequency dependent selection. While the idea developed here is a valuable contribution to the field, the description of the empirical work and the simulations remain incomplete, as they do not provide a full picture of what exactly has been done.

Reviewer #1 (Public Review):

The hypothesis is based on the idea that inversions capture genetic variants that have antagonistic effects on male sexual success (via some display traits) and survival of females (or both sexes) until reproduction. Furthermore, a sufficiently skewed distribution of male sexual success will tend to generate synergistic epistasis for male fitness even if the individual loci contribute to sexually selected traits in an additive way. This should favor inversions that keep these male-beneficial alleles at different loci together at a cis-LD. A series of simulations are presented and show that the scenario works at least under some conditions. While a polymorphism at a single locus with large antagonistic effects can be maintained for a certain range of parameters, a second such variant with somewhat smaller effects tends to be lost unless closely linked. It becomes much more likely for genomically distant variants that add to the antagonism to spread if they get trapped in an inversion; the model predicts this should drive accumulation of sexually antagonistic variants on the inversion versus standard haplotype, leading to the evolution of haplotypes with very strong cumulative antagonistic pleiotropic effects. This idea has some analogies with one of predominant hypotheses for the evolution of sex chromosomes, and the authors discuss these similarities. The model is quite specific, but the basic idea is intuitive and thus should be robust to the details of the model assumption. It makes perfect sense in the context of the geographic pattern of inversion frequencies.

To provide empirical support for this idea, the authors study the dynamics of inversions in population cages over one generation, tracking their frequencies through amplicon sequencing at three time points: (young adults), embryos and very old adult offspring of either sex (>2 months from adult emergence). Out of four inversions included in the experiment, two show patterns consistent with antagonistic effects on male sexual success (competitive paternity) and the survival of offspring, especially females, until an old age, which the authors interpret as consistent with their theory.

There are several reasons why the support from these data for the proposed theory is not waterproof.

(1) As I have already pointed out in my previous review, survival until 2 months (in fact, it is 10 weeks and so 2.3 months) of age is of little direct relevance to fitness, whether under natural conditions or under typical lab conditions.

The authors argue this objection away with two arguments<br /> First, citing Pool (2015) they claim that the average generation time (i.e. the average age at which flies reproduce) in nature is 24 days. That paper made an estimate of 14.7 generations per year under the North Carolina climate. As also stated in Pool (2015), the conditions in that locality for Drosophila reproduction and development are not suitable during three months of the year. This yields an average generation length of about 19.5 days during the 9 months during which the flies can reproduce. On the highly nutritional food used in the lab and at the optimal temperature of 25 C, Drosophila need about 11-12 days to develop from egg to adult. Even assuming these perfect conditions, the average age (counted from adult eclosion) would be about 8 days. In practice, larval development in nature is likely longer for nutritional and temperature reasons, and thus the genomic data analyzed by Pool imply that the average adult age of reproducing flies in nature would be about 5 days, and not 24 days, and even less 10 weeks. This corresponds neatly to the 2-6 days median life expectancy of Drosophila adults in the field based on capture-recapture (e.g., Rosewell and Shorrocks 1987).<br /> Second, the authors also claim that survival over a period of 2 month is highly relevant because flies have to survive long periods where reproduction is not possible. However, to survive the winter flies enter a reproductive diapause, which involves profound physiological changes that indeed allow them to survive for months, remaining mostly inactive, stress resistant and hidden from predators. Flies in the authors' experiment were not diapausing, given that they were given plentiful food and kept warm. It is still possible that survival to the ripe old age of 10 weeks under these conditions still correlates well with surviving diapause under harsh conditions, but if so, the authors should cite relevant data. Even then, I do not think this allows the authors to conclude that longevity is "the main selective pressure" on Drosophila (l. 936).

(2) It appears that the "parental" (in fact, paternal) inversion frequency was estimated by sequencing sires that survived until the end of the two-week mating period. No information is provided on male mortality during the mating period, but substantial mortality is likely given constant courtship and mating opportunities. If so, the difference between the parental and embryo inversion frequency could reflect the differential survival of males until the point of sampling rather than / in addition to sexual selection.

(3) Finally, irrespective of the above caveats, the experimental data only address one of the elements of the theoretical hypothesis, namely antagonistic effects of inversions on reproduction and survival, notably that of females. It does not test for two other key elements of the proposed theory: the assumption of frequency-dependence of selection on male sexual success, and the prediction of synergistic epistasis for male fitness among genetic variants in the inversion. To be fair, particularly testing the latter prediction would be exceedingly difficult. Nonetheless, these limitations of the experiment mean that the paper is much stronger theoretical than empirical contribution.

Reviewer #2 (Public Review):

Summary:<br /> In their manuscript the authors address the question of whether the inversion polymorphism in D. melanogaster can be explained by sexually antagonistic selection. They designed a new simulation tool to perform computer simulations, which confirmed their hypothesis. They also show a tradeoff between male reproduction and survival. Furthermore, some inversions display sex-specific survival.

Strengths:<br /> It is an interesting idea on how chromosomal inversions may be maintained

Weaknesses:<br /> General points:<br /> The manuscript lacks clarity of writing. It is impossible to fully grasp what the authors did in this study and how they reached their conclusions. Therefore, I cannot guarantee that I spotted all the problems in the study and in my review I will only highlight some cases that I found problematic.<br /> Although this is an interesting idea, but it clearly cannot explain the apparent influence of seasonal and clinal variation on inversion frequencies.

Comments on the latest version:

I would like to give an example of the confusing terminology of the authors:

"Additionally, fitness conveyed by an allele favoring display quality is also frequency-dependent: since mating success depends on the display qualities of other males, the relative advantage of a display trait will be diminished as more males carry it..."

I do not understand the difference to an advantageous allele, as it increases in frequency the frequency increase of this allele decreases, but this has nothing to do with frequency dependent selection. In my opinion, the authors re-define frequency dependent selection, as for frequency dependent selection needs to change with frequency, but from their verbal description this is not clear.

One example of how challenging the style of the manuscript is comes from their description of the DNA extraction procedure. In principle a straightforward method, but even here the authors provide a convoluted uninformative description of the procedure.

It is not apparent to the reviewer why the authors have not invested more effort to make their manuscript digestible.

Reviewer #3 (Public Review):

Summary:<br /> In this study, McAllester and Pool develop a new simulation model to explain the maintenance of balanced inversion polymorphism, based on (sexually) antagonistic alleles and a trade-off between male reproduction and survival (in females or both sexes). In support of the plausibility of this model, the authors use laboratory experiments on four naturally occurring inversion polymorphisms in Drosophila melanogaster, finding evidence for the existence of the above-mentioned trade-off in two out of the four cases.

Strengths:<br /> (1) The study develops and analyzes a new (Drosophila melanogaster-inspired) model for the maintenance of balanced inversion polymorphism, combining elements of (sexually) antagonistically (pleiotropic) alleles, negative frequency-dependent selection and synergistic epistasis. To this end, the authors develop and use a new simulator.

(2) The above-mentioned model assumes, as a specific example, a trade-off between male reproductive display and survival; in the second part of their study, the authors perform laboratory experiments on four common D. melanogaster inversions to study whether these polymorphisms may be subject to such a trade-off. The authors find that two of the four inversions show suggestive evidence that is consistent with a trade-off between male reproduction and survival. The new amplicon sequencing approach to track inversion frequencies used by the authors seems promising in terms of studying fitness effects / trade-offs associated with polymorphic inversions and how such effects play out dynamically.

Weaknesses:<br /> A gap in the current modeling is that, while a diploid situation is being studied, the model does not investigate the effects of varying degrees of dominance. It would be important and interesting to fill this gap in future work.

Comments on the latest version:

Most of the comments which I have made in my public review have been adequately addressed.

Some of the writing still seems somewhat verbose and perhaps not yet maximally succinct; some additional line-by-line polishing might still be helpful at this stage in terms of further improving clarity and flow (for the authors to consider and decide).

Author response:

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

Reviewer #1 (Public Review):

[…]

(1) The authors claim that the negative frequency dependence that maintains polymorphism in their model results from a non-linear relationship between the display trait and sexual success [...] Maybe I missed something, but the authors do not provide support for their claim about the negative frequency-dependence of sexual selection in their simulations. To do so they could (1) extract the relationship between the relative mating success of the two male types from the simulations and (2) demonstrate that polymorphism is not maintained if the relationship between male display trait and mating success is linear.

We believe that there is a confusion of terminology here. We agree that for the two alleles at a locus impacting male display in our model, the allele conferring inferior display quality will have a fitness that increases as its frequency increases, so this allele displays positive frequency dependent fitness. And, the alternate, display-favoring allele at the locus does display negative frequency dependence. Our use of the terminology ‘negative frequency dependence’ was meant to refer to the negative dependence of the fitness of the display-favoring allele with respect to its own frequency. However, a significant body of literature instead discusses models in which both an allele and its alternate(s) are beneficial when at low frequency and deleterious when at high frequency under the same selective challenge, entailing negative frequency dependence of fitness for all alleles involved. This benefit-when-rare model of a single trait is often described simply as negative frequency dependence, and generates balancing selection at the locus, but is not the model we are presenting here, and does not encompass all models involving negative frequency dependent fitness. This lexical expectation may make the interpretation of our work more difficult, and we have amended the manuscript to make our model clearer (lines 227-231). In this model, we have a negative frequency dependence for the fitness of the display-favoring allele in mate competition, but the net selective disadvantage of this allele at high frequency is due to a cost in another, pleiotropic, fitness challenge: the constant survival effect. So, the alleles are under balancing selection where alternate alleles are favored by selection when rare, but not due solely to selection during mate competition. Instead, our model relies on pleiotropy for an emergent form of frequency-dependent balancing selection (in the sense that each allele is predicted to be beneficial on balance when rare).

In the reviewer’s model of the success of two alleles at one locus, the ratio of success is vaguely linear with allele frequency for n=3, though it starts quite convex and has an inflection point between convex and concave segments (for the disfavored allele) at p≈0.532. This is visualized easily by plotting the function and its derivatives in Wolfram-Alpha. For n>=4, the fitness function with respect to the display-favoring/disfavoring allele becomes increasingly concave/convex respectively, and this specific nonlinearity is needed to act along with the antagonistic pleiotropy to maintain balancing selection, rather than being maintained by a model that favors any rare allele on the basis of its rarity in some manner. In an attempt to make the importance of the encounter number parameter clearer, we’ve generated new panels for Figure S1 which simulate encounter numbers 2, 3, and 4, and we have updated corresponding text and figure references in lines 335-338.

For (1-2), it is not clear how to modify the simulation such that the relationship between the trait value and mating success can be perfectly linear - either linear with respect to allele frequency in a one locus model or linear with respect to trait value at a specific population composition, without removing the simulation of mate competition altogether. While it may be of interest to explore a more comprehensive range of biological trade-offs in future studies, we are not able to meaningfully do so within the context of the present manuscript.

(2) The authors only explore versions of the model where the survival costs are paid by females or by both sexes. We do not know if polymorphism would be maintained or not if the survival cost only affected males, and thus if sexual antagonism is crucial.

We now present simulations with male costs only as added panels to Figure S1 and mention these results in the main text (lines 334-335). Maintenance of the polymorphism is significantly reduced or completely absent in such simulations.

(3) The authors assume no cost to aneuploidy, with no justification. Biologically, investment in aneuploid eggs would not be recoverable by Drosophila females and thus would potentially act against inversions when they are rare.

We did offer some discussion and justification of our decision to model no inherent fitness of the inversion mutation itself, specifically aneuploidy, in lines 36-39 and 78-80 of the original reviewed preprint. Previous research suggests that D. melanogaster females may not actually invest in aneuploid eggs generated from crossover within paracentric inversions. While surprising, and potentially limited to a subset of clades, many ‘r-selected’ taxa or those in which maternal investment is spread out over time may have some degree of reproductive compensation for non-viable offspring, which can reduce the costs of generating aneuploids significantly (for example, t-haplotypes in mice). We have added this example and citation to lines 34ff in the current draft.

(4) The authors appear to define balanced polymorphism as a situation in which the average allele frequency from multiple simulation runs is intermediate between zero and one (e.g., Figure 3). However, a situation where 50% of simulation runs end up with the fixation of allele A and the rest with the fixation of allele B (average frequency of 0.5) is not a balanced polymorphism. The conditions for balanced polymorphism require that selection favors either variant when it is rare.

We originally chose mean final frequency for presenting the single locus simulations based on the ease of generating a visual plot that included information on fixation vs loss and equilibrium frequency. Figure 3 and related supplemental images have been changed to now also represent the proportion of simulations retaining polymorphism at the locus in the final generation.

(5) Possibly the most striking result of the experiment is the fact that for 14 out of 16 combinations of inversion x maternal background, the changes in allele frequencies between embryo and adult appear greater in magnitude in females than in males irrespective of the direction of change, being the same in the remaining two combinations. The authors interpret this as consistent with sexually antagonistic pleiotropy in the case of In(3L)Ok and In(3R)K. The frequencies of adult inversion frequencies were, however, measured at the age of 2 months, at which point 80% of flies had died. For all we know, this may have been 90% of females and 70% of males that died at this point. If so, it might well be that the effects of inversion on longevity do not systematically differ between the ages and the difference in Figure 9B results from the fact that the sample includes 30% longest-lived males and 10% longest-lived females.

This critique deserves some consideration. The aging adults were separated by sex during aging, but while we recorded the number of survivors, we did not record the numbers of eclosed adults and their sexes initially collected out of an interest in maintaining high throughput collection. We therefore cannot directly calculate the associated survival proportions, but we can estimate them. We collected 1960 females and 3156 males, and we can very roughly estimate survival if we assume that equal numbers of each sex eclosed, and that the survivors represent 20% of the original population. That gives 12790 individuals per sex, or 84.7% female mortality and 75.3% male mortality.

So, we have added a qualification discussing the possibility of stronger selection on females and its influence on observed sex-specific frequency changes, on lines 602-605.

(6) Irrespective of the above problem, survival until the age of 2 months is arguably irrelevant from the viewpoint of fitness consequences and thus maintenance of inversion polymorphism in nature. It would seem that trade-offs in egg-to-adult survival (as assumed in the model), female fecundity, and possibly traits such as females resistance to male harm would be much more relevant to the maintenance of inversion polymorphisms.

Adult Drosophila will continue to reproduce in good conditions until mortality, and the estimated age of a mean reproductive event for a Drosophila melanogaster individual is 24 days (Pool 2015), and likewise for D. simulans (Turelli and Hoffman 1995). Given that reproduction is centered around 24 days, we expect sampling at 2 months of age to still be relevant to fitness. In seasonally varying climates, either temperate or with long dry season, survival through challenging conditions is expected to require several months. In many such cases, females are in reproductive diapause, and so longevity is the main selective pressure. See lines 931-936 in the revised manuscript.

As we agreed above, it would of interest to investigate a wider range of trade-offs in future studies. We focused here on the balanced between survival and male reproductive success because the latter trait generates negative frequency dependence for display-favoring alleles and a disproportionate skew towards higher quality competitors, whereas many other fitness-relevant traits lack that property.

(7) The experiment is rather minimalistic in size, with four cages in total; given that each cage contains a different female strain, it essentially means N=1. The lack of replication makes statements like " In(2L)t and In(2R)NS each showed elevated survival with all maternal strains except ZI418N" (l. 493) unsubstantiated because the claimed special effect of ZI418N is based on a single cage subject to genetic drift and sampling error. The same applies to statements on inversion x female background interac7on (e.g., l. 550), as this is inseparable from residual variation. It is fortunate that the most interesting effects appear largely consistent across the cages/female backgrounds. Still, I am wondering why more replicates had not been included.

Our experimental approach might be described as “diversity replication”. Essentially, the four maternal genetic backgrounds are serving dual purposes – both to assess experimental consistency and to ensure that our conclusions are not solely driven by a single non-representative genotype (which in so many published studies, can not be ruled out). It would indeed be interesting if we could have quadrupled the size of our experiment by having four replicates per maternal background. However, we suspect the reviewer may not recognize the substantial effort involved in our four existing experiments. Each of these involved collecting 500+ virgin females, hand-picking thousands of embryos during the duration of egg-laying, and repeatedly transferring offspring to maintain conditions during aging, such that cages had to be staggered by more than a month. These four cages took a year of benchwork just to collect frozen samples, before any preparation and quality control of the associated amplicon libraries for sequencing. Adding a further multiplier would take it well beyond the scope of a single PhD thesis.  Fortunately, we were able to obtain the key results of interest without that additional effort, even if clearer insights into the role of maternal background would also be of strong interest.

We do agree that no firm conclusions about maternal background can be reached without further replication, and so we have qualified or removed relevant statements accordingly (lines 568ff, 620-622).

Reviewer #1 (Recommendations For The Authors):

The description of the model is confusing and incomplete, e.g., the values of several parameters used to obtain the numerical results are not given. It is first stated (l. 223) that the model is haploid, but text elsewhere talks about homozygotes and heterozygotes. If the model is diploid (this in itself is not clear), what is assumed about dominance?

We are not presenting results for a mathematical model estimated numerically. We have now clarified our transition from a conceptual depiction of our model, in which we use haploid representations for simplified presentation, to our forward population genetic simulations, which are entirely diploid. More broadly, we have improved our communication of the assumptions and parameters used in our simulations. The scenarios we investigate involve purely additive trait effects within and between loci (except that survival probabilities are multiplicative to avoid negative values). We think that considering other dominance scenarios would be a worthy subject for a follow-up study, whereas the present manuscript is already covering a great deal of ground.   

Similarly, it is hard to understand the design (l.442ff). I was confused as to whether a population was set up for each inversion or for all of them and what the unit or replication was. I found the description in Methods (l. 763-771) much clearer and only slightly longer; I suggest the authors transfer it to the Results. Also, Figure 8 should contain the entire crossing scheme; the current version is misleading in that it implies males with only two genotypes.

All four tested inversions were segregating within the same karyotypically diverse population of males, and were assayed from the same experiments. We have attempted to improve the relevant description. For Figure 8, we had trouble conceiving a graphic update that contained a more complete cross scheme without seeming much more confused and cluttered. We have tried to clarify in the relevant text and the figure caption instead.

There are a number of small issues that should be addressed:

- No epistasis for viability assumed - what would be the consequence?

We explored a model in which we intentionally included no terms for epistatic effects on phenotype. All epistasis with regard to fitness is emergent from competition between individuals with phenotypes composed of non-epistatic, non-dominant genetic effects. So, the simplest model of antagonism would have no epistasis for viability whatsoever. One could explore a model that has emergent viability epistasis in a similar way, by implementing stabilizing selection on a quantitative trait with a gaussian or similar non-linear phenotype-to-fitness map, but that might be better served as a topic for a future study. We have, however, tried to make this intent clearer in the text.

l. 750 implies that aneuploidy generated by the inversion has no cost (aneuploid games are resampled)

Yes, as addressed in public review item (3). Alternately see lines 34ff, 293, 369, 392 for in-text edits.

l. 24-25: unclear; is this to mean that there is haplotype x sex interaction for survival?

l. 25: success in what? (I assume this will be explained in the paper, but the abstract should stand on its own).

l. 193-4: "producing among most competitive males": something missing or a word too much?? Figure 1B,C: a tiny detail, but the plots would be more intuitive if the blue (average) bars were ager (i.e., to the right) of the male and female ones, given that the average is derived from the two sex-specific values.

Each of the above have been edited or implemented as suggested

l. 205. It is convex function, but I do not understand what the authors mean by "convex distribution".

Hopefully the updated text is clearer: “yielding a distribution of male reproductive output that follows a relatively convex trend”.

l. 223ff: some references to Fig 1 panels in this paragraph seem off by one letter (i.e., A should be B, etc.).

l. 231 "fitness...are equally fit": rephrase 

l. 260: maybe "thrown out" is not the most fortunate term, maybe "eliminated" would be better?

Each of the above have been edited or implemented as suggested

Figure 3: I do not understand the meaning of "additive" and "multiplicative" in the case of a single locus haploid model

All presented simulations are diploid, and these refer to the interactions between the two alleles at the locus. Hopefully the language is overall clearer in this draft.

l. 274: "Mutation of new nucleotide" meaning what? Or is it mutation _to_ a new nucleotide?

Hopefully the revised text is clearer.

Figure 5. The right panel of figure 5A implies that, with the inversion, the population evolves to an extreme display trait that is so costly that it fills 95% of all individuals (or of all females?

What is assumed about this here?). Apart from the biological realism of this result, what does it say about the accumulation of polymorphism and maintenance of the inversion? The graphs in fig 5B do plot a divergence between haplotypes, but it is not clear how they relate to those in panel A - the parameter values used to generate these plots are again not listed. Furthermore, from the viewpoint of the polymorphism, it would be good to report the frequencies at the steady-state.

We have now clarified the figure description, including the parameter values used. The distribution of frequencies at the end of the simulation is represented in figure 6. Given that we set up the simulation with assumptions that are otherwise common to population models, what biological process would prevent this extreme? Why isn’t this extreme observed in natural populations? One possible explanation is that they become sex chromosomes, with increasing likelihood as the cost increases. Or other compensatory changes may occur that we don’t simulate, like regulatory evolution giving a complementary phenotype. Maybe genetic constraints in natural populations prevent the mutation of the kind of pleiotropic mutations that drive this dynamic. The populations still survive, though they are parameterized by relative fitness. What would an absolute fitness population function be? Would it go extinct or not? It would be of interest to explore a wider range of models, but it is the purpose of this paper to establish that this is a viable model for the maintenance of sexually antagonistic polymorphism and association with inversions. We have added a paragraph motivated by this comment to the Discussion starting on line 765.

l. 401-2: Z-like, W-like : please specify you are talking about patterns resembling sex chromosomes. 

l. 738: "population calculates"?

l. 743-4 and 746-7: is this the same thing said twice, or are there two components of noise?  l. 357: there is no figure 5C.

Each of the above have been addressed with text edits.

L. 473-5: Yes, the offspring did not contain inversion homozygotes, but the sire pool did, didn't it? So homozygous inversions may have affected male reproductive success. Anyway, most of this paragraph (from line 473) seems to belong in Discussion rather than Results.

We have revised this sentence to focus on offspring survival. 

We can understand the reviewer’s suggestion about Results vs. Discussion text. While this can often be a challenging balance, we find that papers are often clearer if some initial interpretation is offered within the Results text. However, we moved the portion of this paragraph relating our findings to the published literature to the Discussion.

l. 516: " In(3L)Ok favored male survival": this is misleading/confusing given the data, " In(3L)Ok reduced female survival more strongly than male survival..."

Hopefully the phrasing is clearer now.

l. 663ff: I did not have an impression that this section added anything new and could safely be cut.

We have done some editing to make this more concise and emphasize what we think is essential, but we believe that the model of an autosomal, sexually antagonistic inversion differentiating before contributing to the origin of a sex chromosome is novel and interesting. And, that this additional emphasis is worthwhile to encourage thought and consideration of this idea in future research and among interested researchers.

l. 751: "flat probability per locus": do the authors mean a constant probability?

Edited.

Reviewer #2 (Public Review):

The manuscript lacks clarity of writing. It is impossible to fully grasp what the authors did in this study and how they reached their conclusions. Therefore, I will highlight some cases that I found problematic.

Hopefully the revised manuscript improves writing clarity. 

Although this is an interesting idea, it clearly cannot explain the apparent influence of seasonal and clinal variation on inversion frequencies.

We do not believe that our model predicts a non-existence of temporal and spatial dependence of the fitness of inverted haplotypes, nor do we seek to identify the manner in which seasonal and clinal differences affect fitness of inverted haplotypes. Rather, we argued that the influence of seasonal and clinal selection on inversions does not on its own predict the observed maintenance of inversions at low to intermediate frequencies across such a diverse geographic range, along with the higher frequencies of many derived inversions in more ancestral environments. 

We might imagine that trade-offs between life history traits such as mate competition and survival should be universal across the range of an organism. But in practice, the fitness benefits and costs of a pleiotropic variant (or haplotype) may be heavily dependent on the environment. A harsh environment such as a temperate winter may both reduce the number of females that a male encounters (decreasing the benefit of display-enhancing variants) and also increase the likelihood that survival-costly variants lead to mortality (thus increasing their survival penalty). In light of such dynamics, our model would predict that equilibrium inversion frequencies should be spatially and temporally variable, in agreement with a number of empirical observations regarding D. melanogaster inversions.

We have edited the introduction to emphasize that inversion frequencies vary temporally as well as seasonally, on lines 144ff. We also note relevant discussion of the potential interplay between the environment and trade-offs such as those we investigate, on lines 153-155.

The simulations are highly specific and make very strong assumptions, which are not well-justified.

We respond to all specific concerns expressed in the Recommendations For The Authors section below. We also note that we have made further clarifications throughout the text regarding the assumptions made in our analysis and their justification.  

Reviewer #2 (Recommendations For The Authors):

I think that the manuscript would greatly benefit from a major rewrite and probably also a reanalysis of the empirical data.

In particular, a genome-wide analysis of differences in SNP frequencies between sexes and developmental stages would help the reader to appreciate that inversions are special.

[moved up within this section for clarity] We are lacking a genomic null model-how often do the authors see similar allele frequency differences when looking at the entire genome? This could be easily done with whole genome Pool-Seq and would tell us whether inversions are really different from the genomic background. I think that this information would be essential given the many uncertainties about the statistical tests performed. 

We expect that autosome-wide SNP frequencies will be heavily influenced by the frequencies of inversions, which occur on all four major autosomal chromosome arms. These inversions often show moderate disequilibrium with distant variants (e.g. Corbett-Detig & Hartl 2012).

Furthermore, the limited number of haplotypes present, given that the paternal population was founded from 10 inbred lines, would further enhance associations between inversions and distant variants. Therefore, we do not expect that whole-genome Pool-Seq data would provide an appropriate empirical null distribution for frequency changes. Instead, we have generated appropriate null predictions by accounting for both sampling effects and experimental variance, and we have aimed to make this methodology clearer in the current draft. 

Some basic questions:

why start at a frequency of 50% (line 287)?

Isn't it obvious that in this scenario strong alleles with sexually antagonistic effects can survive?

The initial goal of the associated Figure 4 was not to show that a strongly antagonistic variant could persist. Instead, we wanted to test the linkage conditions in which a second, relatively weaker antagonistic variant survived – which did not occur in the absence of strong linkage. 

We have now added simulations with relatively lower initial frequencies, in which the weaker variant and the inversion both start at 0.05 frequency, while the stronger variant is still initialized at 0.5 to reflect the initial presence of one balanced locus with a strongly antagonistic variant. Here, the weaker antagonistic variant is still usually maintained when it is close to the stronger variant, and while the inversion-mediated maintenance of the weaker variant at greater distance from the stronger variant because less frequent than the original investigated case, it still happens often enough to hypothetically allow for such outcomes over evolutionary time-scales.

Still, we should also emphasize that the goals of this proof-of-concept analysis are to establish and convey some basic elements of our model. Subsequently, analyses such as those presented in Figures 5 and 6 provide clearer evidence that the hypothesized dynamics of inversions facilitating the accumulation of sexual antagonism actually occur in our simulations.

The experiments seem to be conducted in replicate (which is of course essential), but I could not find a clear statement of how many replicates were done for each maternal line cross.

How did the authors arrive at 16 binomial trials (line 473)? 4 inversions, 4 maternal genotypes?

How were replicates dealt with?

In Figure 9, it would be important to visualize the variation among replicates.

Unfortunately, we did not have the bandwidth to perform replicates of each maternal line. Instead, we use four maternal backgrounds to simultaneously establish consistency across independent experiments and genetic backgrounds (see our response to Reviewer 1, point 7). We’ve edited the draft to make this clearer and more clearly delineate what is supported and not supported by our data. Replicate variation for the control replicates of the extraction and sequencing process, and the exact read counts of the experiment, are available in Supplemental Tables S5, S6, and S7.

The statistical analysis of trade-off is not clear: which null model was tested? No frequency change? In my opinion, two significances are needed: a significant difference between parental and embryo and then embryo and adult offspring. The issue with this is, however, that the embryo data are used twice and an error in estimating the frequency of the embryos could be easily mistaken as antagonistic selection.

Hopefully the description of our null model is clearer in the text, now starting around line 967 in the Methods. We are aware of the positive dependence when performing tests comparing the paternal to embryo and then embryo to offspring frequencies, and this is accounted for by our analysis strategy - see lines 1009-1012.

It was not clear how the authors adjusted their chi-squared test expectations. Were they reinventing the wheel? There is an improved version of the chi-squared test, which accounts for sampling variation.

We did not actually perform chi-square tests. Instead, we used the chi statistic from the chi-squared test as a quantitative summary of the differences in read counts between samples. We compared an observed value of chi to values for this statistic obtained from simulated replicates of the experiment. Sampling from this simulation generated our ‘expected’ distribution of read counts, sampled to match sources of variance introduced in the experimental procedure, but without any effect of natural selection, per lines 825ff in the original submission. Hence, we are approximating the likelihood of observing an empirical chi statistic by generating random draws from a model of the experiment and comparing values calculated from each draw to the experimental value: a Monte Carlo method of approximating a p-value for our data. We have attempted to make the structure of these simulations and their use as a null-model clearer in this draft.

It is not sufficiently motivated why the authors model differences in the extraction procedure with a binomial distribution.

Adding a source of variance here seemed necessary as running control sequencing replicates revealed that there was residual variance not fully recapitulated by sample-size-dependent resampling. Given that we were still sampling a number of draws from a binomial outcome (the read being from the inverted or standard arrangement), a binomial distribution seemed a reasonable model, and we fit the level of this additional noise source to an experiment-wide constant, read-count or genome-count independent parameter that best fit the variance observed in the controls (lines 830ff in the original draft). Clarification is made in this manuscript draft, lines 979-989.

How many reads were obtained from each amplicon? It looks like the authors tried to mimic differences between technical replicates by a binomial distribution, which matches the noise for a given sample size, but this depends on the sequence coverage of the technical replicates.

We provide read counts in Supplemental Tables S6 and S7. The relevant paragraph in the methods has been edited for clarity, lines 972ff. Accounting for sampling differences between replicates used a hypergeometric distribution for paternal samples to account for paternal mortality before collection, and the rest were resampled with a binomial distribution. There were two additional binomial samplings, to account for resampling the read counts and to capture further residual variance in the library prep that did not seem to depend on either allele or read counts.

It would be good to see an estimate for the strength of selection: 10% difference in a single generation appears rather high to me.

Estimates of selection strength based on solving for a Wright-Fisher selection coefficient for each tested comparison can now be found in Table S8, mentioned in text on lines 589-590. The mean magnitude of selection coefficients for all paternal to embryo comparisons was 0.322, and for embryo to all adult offspring it was 0.648. For In(3L)Ok the mean selection coefficients were 0.479 and -0.53, and for In(3R)K they were -0.189 and 1.28, respectively. Some are of quite large magnitude, but we emphasize that the coefficients for embryo to adult are based on survival to old age, rather than developmental viability. That factor, in addition to the laboratory environment, makes these estimates distinct from selection coefficients that might be experienced in natural populations.

Reviewer #3 (Public Review):

Strengths:

(1) …the authors developed and used a new simulator (although it was not 100% clear as to why SLiM could not have been used as SLiM has been used to study inversions).

Before SLiM 3.7 or so (and including when we did the bulk of our simulation work), we do not think it would have been feasible to use SLiM to model the mutation of inversions with random breakpoints and recombination between without altering the SLiM internals. Separately, needing to script custom selection, mutation, and recombination functions in Eidos would have slowed SLiM down significantly. Given our greater familiarity with python and numpy, and the ability to implement a similar efficiency simulator more quickly than through learning C++ and Eidos, we chose to write our own.

It should be a fair bit easier to implement comparable simulations in SLiM now, but it will still require scripting custom mutation, selection, and recombination functions and would still result in a similarly slow runtime. The current script recipe recommended by SLiM for simulating inversions uses constants to specify the breakpoints of a single inversion, without the ability to draw multiple inversions from a mutational distribution, or model recombination between more complicated karyotypes. Hence, our simulator still seems to be a more versatile and functional option for the purposes of this study.

Weaknesses:

[Comments 1 through 4 on Weaknesses included numerous citation suggestions, and some discussion recommendations as well. In our revised manuscript, we have substantially implemented these suggestions. In particular, we have deepened our introduction of mechanisms of balancing selection and prior work on inversion polymorphism, integrating many

suggested references. While especially helpful, these suggestions are too extensive to completely quote and respond to in this already-copious document. Therefore, we focus our response on two select topics from these comments, and then proceed to comment 5 thereafter.]

(2) The general reduction principle and inversion polymorphism. In Section 1.2., the authors state that "there has not been a proposed mechanism whereby alleles at multiple linked loci would directly benefit from linkage and thereby maintain an associated inversion polymorphism under indirect selection." Perhaps I am misunderstanding something, but in my reading, this statement is factually incorrect. In fact, the simplest version of Dobzhansky's epistatic coadaptation model

(see Charlesworth 1974; also see Charlesworth and Charlesworth 1973 and discussion in Charlesworth & Flatt 2021; Berdan et al. 2023) seems to be an example of exactly what the authors seem to have in mind here: two loci experiencing overdominance, with the double heterozygote possessing the highest fitness (i.,e., 2 loci under epistatic selection, inducing some degree of LD between these loci), with subsequent capture by an inversion; in such a situation, a new inversion might capture a haplotype that is present in excess of random expectation (and which is thus filer than average)…

We agree that the quoted statement could be misleading and have rewritten it. We intended to point out that we are presenting a model in which all loci contribute additively (with respect to display) or multiplicatively (with respect to survival probability), without any dominance relationships or genetic interaction terms. And yet, the model generates epistatic balancing selection in a panmictic population under a constant environment. This represents a novel mechanism by which (the life-history characteristics of) a population would generate epistatic balancing selection as an emergent property, instead of assuming a priori that there is some balancing mechanism and representing frequency dependence, dominance effects, or epistatic interactions directly using model parameters. We have therefore refined the scope of the statement in question (lines 155-158). 

(4) Hearn et al. 2022 on Littorina saxatilis snails. 

A good reference. There is considerable work on ecotype-associated inversions in L. saxatalis, but we previously cut some discussion of this and of other populations with high gene flow but identifiable spatial structure for inversion-associated phenotypes (e.g. butterfly mimicry polymorphisms, Mimulus, etc.). Due to the spatially discrete environmental preferences and sampled ranges of the inversions in these populations, we considered these examples to be somewhat distinct from explaining inversion polymorphism in a potentially homogenous and panmictic environment. 

(4) cont. A very interesting paper that may be worth discussing is Connallon & Chenoweth (2019) about dominance reversals of antagonistically selected alleles (even though C&C do not discuss inversions): AP alleles (with dominance reversals) affecting two or more life-history traits provide one example of such antagonistically selected alleles (also see Rose 1982, 1985; Curtsinger et al. 1994) and sexually antagonistically selected alleles provide another. The two are of course not necessarily mutually exclusive, thus making a conceptual connection to what the authors model here.

We had removed a previously drafted discussion of dominance reversal for brevity’s sake, but this topic is once again represented in the updated draft of the manuscript with a short reference in the introduction, lines 76-80. We also mention ‘segregation lift’ (Wittmann et al. 2017) involving a similar reversal of dominance for fitness between temporally fluctuating conditions, as opposed to between sexes or life history stages. 

(5) The model. In general, the description of the model and of the simulation results was somewhat hard to follow and vague. There are several aspects that could be improved:  [5](1) it would help the reader if the terminology and distinction of inverted vs. standard arrangements and of the three karyotypes would be used throughout, wherever appropriate.

We have attempted to do so, using the suggested heterokaryotypic/homokaryotypic terminology.

[5](2) The mention of haploid populations/situations and haploid loci (e.g., legend to Figure 1) is somewhat confusing: the mechanism modelled here, of course, requires suppressed recombination in the inversion/standard heterokaryotype; and thus, while it may make sense to speak of haplotypes, we're dealing with an inherently diploid situation. 

While eukaryotes with haploid-dominant life history may still experience similar dynamics, we do expect that most male display competition is in diploid animals, and we are only simulating diploid fitnesses and experimenting with diploid Drosophila. We have tried to minimize the discussion of haploids in this draft.

[5](3) The authors have a situation in mind where the 2 karyotypes (INV vs. STD) in the heterokaryotype carry distinct sets of loci in LD with each other, with one karyotype/haplotype carrying antagonistic variants favoring high male display success and with the other karyotype/haplotype carrying non-antagonistic alternative alleles at these loci and which favor survival. Thus, at each of the linked loci, we have antagonistic alleles and non-antagonistic alleles - however, the authors don't mention or discuss the degree of dominance of these alleles. The degree of dominance of the alleles could be an important consideration, and I found it curious that this was not mentioned (or, for that matter, examined). 

In this study, our goal was to show that the investigated model could produce balanced and increasing antagonism without the need to invoke dominance. We think there would be a strong case for a follow-up study that more investigates how dominance and other variables impact the parameter space of balanced antagonism, but this goal is beyond our capacity to pursue in this initial study. We’ve added several lines clarifying the absence of dominance from our investigated models, and pointing out that dominance could modulate the predictions of these models (lines 211-213, 278-282).  

[5](4) In many cases, the authors do not provide sufficient detail (in the main text and the main figures) about which parameter values they used for simulations; the same is true for the Materials & Methods section that describes the simulations. Conversely, when the text does mention specific values (e.g., 20N generations, 0.22-0.25M, etc.), little or no clear context or justification is being provided. 

We have sought to clarify in this draft that 20N was chosen as an ample time frame to establish equilibrium levels and frequencies of genetic variation under neutrality. We present a time sequence in Figure 5, and these results indicate that that antagonism has stabilized in models without inversions or with higher recombination rates, whereas its rate of increase has slowed in a model with inversions and lower levels of crossing over. 

The inversion breakpoints and the position of the locus with stronger antagonistic effects in Figure 4 were chosen arbitrarily for this simple proof of concept demonstration, with the intent that this locus was close to one breakpoint. Hopefully these and other parameters are clearer in the revised manuscript.

[5](5) The authors sometimes refer to "inversion mutation(s)" - the meaning of this terminology is rather ambiguous.

Edited, hopefully the wording is clearer now. The quoted phrase had uniformly referred to the origin of new inversions by a mutagenic process. 

(6) Throughout the manuscript, especially in the description and the discussion of the model and simulations, a clearer conceptual distinction between initial "capture" and subsequent accumulation / "gain" of variants by an inversion should be made. This distinction is important in terms of understanding the initial establishment of an inversion polymorphism and its subsequent short- as well as long-term fate. For example, it is clear from the model/simulations that an inversion accumulates (sexually) antagonistic variants over time - but barely anything is said about the initial capture of such loci by a new inversion.

We do not have a good method of assessing a transition between these two phases for the simulations in which both antagonistic alleles and inversions arise stochastically by a mutagenic process. However, we have tried to be clearer on the distinction in this draft: we have included simulations in Figure 4 with variants starting at lower frequencies, and we have tried to better contextualize the temporal trajectories in Figure 5 as (in part) modeling the accumulation of variants after such an origin.

Reviewer #3 (Recommendations For The Authors):

- In general: the whole paper is quite long, and I felt that many parts could be written more clearly and succinctly - the whole manuscript would benefit from shortening, polishing, and making the wording maximally precise. Especially the Introduction (> 8 pages) and Discussion (7.5 pages) sections are quite long, and the description of the model and model results was quite hard to follow.

We have attempted to condense some portions of the manuscript, but inevitably added to others based on important reviewer suggestions. Regarding the length Introduction and Discussion, we are covering a lot of intellectual territory in this study, and we aim to make it accessible to readers with less prior familiarity. At this point, we have well over 100 citations – far more than a typical primary research paper – in part thanks to the relevant sources provided by this reviewer. We are therefore optimistic that our text will provide a valuable reference point for future studies. We have also made significant efforts to clarify the Results and Methods text in this draft without notably expanding these sections.

- In general: the conceptual parts of the paper (introduction, discussion) could be better connected to previous work - this concerns e.g. the theoretical mechanisms of balancing selection that might be involved in maintaining inversions; the general, theoretical role of antagonistic pleiotropy (AP) and trade-offs in maintaining polymorphisms; previously made empirical connections between inversions and AP/trade-offs; previously made empirical connections between inversions and sexual antagonism.

In the revised manuscript, we have improved the connection of these topics to prior work.

- L3: "accumulate". A clearer distinction could be made, throughout, between initial capture of alleles/haplotypes by an inversion vs. subsequent gain.

Please see point 6 in the response to the Public Review, above.

- L29: I basically agree about the enigma, however, there are quite many empirical examples in D. melanogaster / D. pseudoobscura and other species where we do know something about the nature of selection involved, e.g., cases of NFDS, spatially and temporally varying selection, fitness trade-offs, etc.

At least for our focal species, we have emphasized that geographic (and now temporal) associations have been found for some inversions. For the sake of length and focus, we probably should not go down the road of documenting each phenotypic association that has been reported for these inversions, or say too much about specific inversions found in other species. As indicated in our response to reviewer 2, some previously documented inversion-associated trade-offs may be compatible with the model presented here. However, we did locate and add to our Discussion one report of frequency-dependent selection on a D. melanogaster inversion (Nassar et al. 1973).

- L43: it is actually rather unlikely, though not impossible, that new inversions are ever completely neutral (see the review by Berdan et al. 2023).

This line was intended to convey that, in line with Said et al. 2018’s results, the structural alterations involved in common segregating inversions are not expected to contribute significantly to the phenotype and fitness (as indicated by lack of strong regulatory effects), and that their phenotypic consequences are instead due to linked variation. We have rewritten this passage to better communicate this point, now lines 44-52. Interpreting Section 2 and Figure 1 of Berdan et al. 2023, the linked variation may be what is in mind when saying that inversions are almost never neutral. We have also added a line referencing the expected linked variation of a new inversion (lines 49-52).

- L51-73: I felt this overview should be more comprehensive. The model by Kirkpatrick & Barton (2016 ) is in many ways less generic than the one of Charlesworth (1974) which essentially represents one way of modeling Dobzhansky's epistatic coadaptation. Also, the AOD mechanism is perhaps given too much weight here as this mechanism is very unlikely to be able to explain the establishment of a balanced inversion polymorphism (see Charlesworth 2023 preprint on bioRxiv). NFDS, spatially varying selection and temporally varying selection (for all of which there is quite good empirical evidence) should all be mentioned here, including the classical study of Wright and Dobzhansky (1946) which found evidence for NFDS (also see Chevin et al. 2021 in Evol. Lett.)

On reflection, we agree that we put too much emphasis on AOD and have edited the section to be more representative.

- L57. Two earlier Dobzhansky references, about epistatic coadaptation, would be: Dobzhansky, T. (1949). Observations and experiments on natural selection in Drosophila. Hereditas, 35(S1), 210-224. hlps://doi.org/10.1111/j.1601-5223.1949.tb033 34.xM; Dobzhansky, T. (1950). Genetics of natural populations. XIX. Origin of heterosis through natural selection in populations of Drosophila pseudoobscura. Genetics, 35, 288-302.hlps://doi.org/10.1093/gene7cs/35.3.288 - In general, in the introduction, the classical chapter by Lemeunier and Aulard (1992) should be cited as the primary reference and most comprehensive review of D. melanogaster inversion polymorphisms.

- L101: this is of course true, though there are some exceptions, such as In(3R)Mo.

- L110: the papers by Knibb, the chapter by Lemeunier and Aulard (1992), and the meta-analysis of INV frequencies by Kapun & Flatt (2019) could be cited here as well.

Citation suggestions integrated.

- L123 and elsewhere: the common D. melanogaster inversions are old but perhaps not THAT old - if we take the Corbett-Detig & Hartl (2012) es7mates, then most of them do not really exceed an age of Ne generations, or at least not by much. I mean: yes, they are somewhat old but not super-old (cf. discussion in Andolfatto et al. 2001).

Edited to curb any hyperbole. We agree that there are much more ancient polymorphisms in populations.

- L133-135. This needs to be rewritten: this claim is incorrect, to my mind (Charlesworth 1974; also see Charlesworth and Charlesworth 1973; discussion in Charlesworth & Flatt 2021).

Edited. See public review response (2).

- L154: the example of inversion polymorphism is actually explicitly discussed in Altenberg's and Feldman's (1987) paper on the reduction principle.

Edited to mention this. Inversions are also mentioned in Feldman et al. 1980, Feldman and Balkau 1973, Feldman 1972, and have been in discussion since the origins of the idea.

- L162ff: see Connallon & Chenoweth (2019).

Citation suggestion integrated, along with Cox & Calsbeek 2009 which seems more directly applicable, now line 185ff.

- L169: why? There is much evidence for other important trade-offs in this system.

Reworded.

- L178-179: other studies have found that trade-offs/AP contribute to the maintenance of inversion polymorphisms, e.g. Mérot et al. 2020 and Betrán et al. 1998, etc.

Added Betrán et al. 1998 - a good reference. Moved up mention of Mérot et al. 2020 from later in the text and directed readers to the Discussion, lines 202-205.

- L198. "alternate inversion karyotypes" - you mean INV vs. STD? It would be good to adopt a maximally clear, uniform terminology throughout.

Edited to communicate this better.

- L215-217: this is a theoretically well-known result due to Hazel (1943); Dickerson (1955); Robertson (1955); e.g., see the discussion in the quantative genetics book by Roff (1997) or in the review of Flatt (2020).

Citations integrated, now lines 232ff.

- L223 and L245: "haploid" - somewhat confusing (see public review). 

- L259-260: This may need some explanation. 

- L261-262: simply state that there is no recombination in D. melanogaster males.

Edited for increased clarity.

- L274 (and elsewhere): the meaning of "mutation...of new..inversion polymorphisms" is ambiguous - do you mean a polymorphic inversion and hence a new inversion polymorphism or do you mean polymorphisms/variants accumulating in an inversion?

- L275: maybe better heterokaryotypic instead of heterozygous? (note that INV homokaryotypes or STD homokaryotypes can be homo- or heterozygous, so when referring to chromosomal heterozygotes instead of heterozygous chromosomes it may be best to refer to heterokaryotypes).

Per [5](1) and [5](5) in the public review, we have edited our terminology.

- L276: referral to M&M - I found the description of the model/simulation details there to be somewhat vague, e.g. in terms of parameter settings, etc.

Further described.

- L281-282: would SLiM not have worked?

See public review response.

- L286-287: why these parameters?

Further described.

- L296ff: it is not immediately clear that the loci under consideration are polymorphic for antagonistic alleles vs. non-antagonistic alternative alleles - maybe this could be made clear very explicitly.

Edited to be explicit as suggested.

- L341, 343: "inversion mutation" - meaning ambiguous.

- L348, 352: "specified rate" - vague.

- L354-357: initial capture and/or accumulation/gain? 

- L401, 402, 404: Z-, W- and Y- are brought up here without sufficient context/explanation.

The above have been addressed by edits in the text.

- L523, 557, 639, 646, and elsewhere: not the first evidence - see the paper by Mérot et al. (2020) (and e.g. also by Yifan Pei et al. (2023)). 

Citations integrated in the introduction and discussion. Mérot et al. (2020) was cited (L486 in original) but discussion was curtailed in the previous draft. 

- L558-559. I agree but it is clear that there are many mechanisms of balancing selection that can achieve this, at least in principle; for some of them (NFDS, etc.) we have pretty good evidence. 

- L576-577. This is correct but for In(3R)C that study did find a differential hot vs. cold selection response.

Addressed with text edit. 

- L584-L586: cf. Betrán et al. (1998), Mérot et al. (2020), Pei et al. (2023), etc.

- L591. "other forms of balancing selection": yes! This should be stressed throughout. Multiple forms of balancing selection exist and they are not mutually exclusive. 

- L593: consider adding Dobzhansky (1943), Machado et al. (2021) 

- L596-597: this is rather unlikely, at least in terms of inversion establishment (see Charlesworth 2023; hlps://www.biorxiv.org/content/10.1101/2023.10.16.562579v1).

- L608: consider adding Kapun & Flal (2019). 

- L611-612: see studies by Mukai & Yamaguchi, 1974; and Watanabe et al., 1976. 

- L639, 646: AP - see general literature on AP as a factor in maintaining polymorphism (Rose

1982, 1985; Curtsinger et al. 1994; Charlesworth & Hughes 2000 chapter in Lewontin Festschrift; Conallon & Chenoweth 2019 - this latter paper is par7cularly relevant in terms of AP effects in the context of sexual antagonism) 

Citation suggestions integrated.

- L657: inversion polymorphism is explicitly discussed in Altenberg's and Feldman's (1987) paper on the reduction principle.

Hopefully this is better communicated.

- L724-755: I felt that this section generally lacks sufficient details, especially in terms of parameter choices and settings for the simula7ons. 

- L732L: why not state these rates?

Parameter values are now given a fuller description in figure legends and in the methods.  

- L746: but we know that mutational effect sizes are not uniformly distributed (?).

We made this choice for simplicity and to avoid invoking seemingly arbitrary distribution, but one could instead simulate trait effects with some gamma distribution. Display values would still have variable fitness effects that fluctuate with population composition, but we agree that distribution shifted toward small effects would be more realistic.

- L765: In(3R)P is not mentioned elsewhere - is this really correct?

That was incorrect, fixed.

eLife assessment

This important study reveals that the malaria parasite protein PfHO, though lacking typical heme oxygenase activity, is vital for the survival of Plasmodium falciparum. Structural and localization analyses showed that PfHO is essential for apicoplast maintenance, particularly in gene expression and biogenesis, indicating a novel adaptive role for this protein in parasite biology. While the results supporting the claims of the authors are convincing, the lack of data defining a molecular understanding or mechanism of action of the protein in question limits the impact of the study.

Reviewer #1 (Public Review):

Malaria parasites detoxify free heme molecules released from digested host hemoglobins by biomineralizing them into inert hemozoin. Thus, why malaria parasites retain PfHO, a dead enzyme that loses the capacity of catabolizing heme, is an outstanding question that has puzzled researchers for more than a decade. In the current manuscript, the authors addressed this question by first solving the crystal structure of PfHO and aligning it with structures of other heme oxygenase (HO) proteins. They found that the N-terminal 95 residues of PfHO, which failed to crystalize due to their disordered nature, may serve as signal and transit peptides for PfHO subcellular localization. This was confirmed by subsequent microscopic analysis with episomally expressed PfHO-GFP and a GFP reporter fused to the first 83 residues of PfHO (PfHO N-term-GFP). To investigate the functional importance of PfHO, the authors generated an anhydrotetracycline (aTC) controlled PfHO knockdown strain. Strikingly, the parasites lacking PfHO failed to grow and lost their apicoplast. Finally, by chromatin immunoprecipitation (ChIP), quantitative PCR/RT-PCR, and growth assays, the authors showed that both the cognate N-terminus and HO-like domain were required for PfHO function as an apicoplast DNA interacting protein.

The authors systemically performed multidisciplinary approaches to address this difficult question: what is the function of this enzymatically dead PfHO? I enjoyed reading this manuscript and its thoughtful discussion. This study is not of clinical importance for antimalarial treatments but also deepens our understanding of protein function evolution. While I understand these experiments are challenging to conduct in malaria parasites, the data quality of some of the experiments could be improved. For example, most of the Western blots and Southern blots are not of high quality.

Reviewer #2 (Public Review):

Summary:

Blackwell et al. investigated the structure, localization, and physiological function of Plasmodium falciparum (Pf) heme oxygenase (HO). Pf and other malaria parasites scavenge and digest large amounts of hemoglobin from red cells for sustenance. To counter the potentially cytotoxic effects of heme, it is biomineralized into hemozoin and stored in the food vacuole. Another mechanism to counteract heme toxicity is through its enzymatic degradation via heme oxygenases. However, it was previously found by the authors that PfHO lacks the ability to catalyze heme degradation, raising the intriguing question of what the physiological function of PfHO is. In the current contribution, the authors determine that PfHO localizes to the apicoplast, determine its targeting sequence, establish the essentiality of PfHO for parasite viability, and determine that PfHO is required for proper maintenance of apicoplasts and apicoplast gene expression. In sum, the authors establish an essential physiological function for PfHO, thereby providing new insights into the role of PfHO in plasmodium metabolism.

Strengths:

The studies are rigorously conducted and the results of the experiments unambiguously support a role for PfHO as being an apicoplast-targeted protein required for parasite viability and maintenance of apicoplasts.

Weaknesses:

While the studies conducted are rigorous and support the primary conclusions, the lack of experiments probing the molecular function of PfHO limits the impact of the work. Nevertheless, the knowledge that PfHO is required for parasite viability and plays a role in the maintenance of apicoplasts is still an important advance.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Malaria parasites detoxify free heme molecules released from digested host hemoglobins by biomineralizing them into inert hemozoin. Thus, why malaria parasites retain PfHO, a dead enzyme that loses the capacity of catabolizing heme, is an outstanding question that has puzzled researchers for more than a decade. In the current manuscript, the authors addressed this question by first solving the crystal structure of PfHO and aligning it with structures of other heme oxygenase (HO) proteins. They found that the N-terminal 95 residues of PfHO, which failed to crystalize due to their disordered nature, may serve as signal and transit peptides for PfHO subcellular localization. This was confirmed by subsequent microscopic analysis with episomally expressed PfHO-GFP and a GFP reporter fused to the first 83 residues of PfHO (PfHO N-term-GFP). To investigate the functional importance of PfHO, the authors generated an anhydrotetracycline (aTC) controlled PfHO knockdown strain. Strikingly, the parasites lacking PfHO failed to grow and lost their apicoplast. Finally, by chromatin immunoprecipitation (ChIP), quantitative PCR/RT-PCR, and growth assays, the authors showed that both the cognate N-terminus and HO-like domain were required for PfHO function as an apicoplast DNA interacting protein.

The authors systemically performed multidisciplinary approaches to address this difficult question: what is the function of this enzymatically dead PfHO? I enjoyed reading this manuscript and its thoughtful discussion. This study is not of clinical importance for antimalarial treatments but also deepens our understanding of protein function evolution. While I understand these experiments are challenging to conduct in malaria parasites, the data quality of some of the experiments could be improved. For example, most of the Western blots and Southern blots are not of high quality.

We thank the reviewer for the positive comments but are a bit puzzled by the final statement about western and Southern blot quality. We agree that the two anti-PfHO western blots probed with custom antibody (Fig. 3- source data 2 and 8) have substantial background signal in the higher molecular mass region >75 kDa. However, we note that the critical region <50 kDa is clear in both cases and readily enables target band visualization. All other western blots probing GFP or HA epitopes are of high quality with minimal off-target background. We present two Southern blot images. We agree that the signal is somewhat faint for the Southern blot demonstrating on-target integration of the aptamer/TetR-DOZI plasmid (Fig. 3- fig. supplement 4), although we note that the correct band pattern for integration is visible. We also note that the accompanying genomic PCR data is unambiguous. The Southern blot for GFP-DHFRDD incorporation into the PfHO locus (Fig. 3- fig. supplement 1) has clear signal and strongly supports on-target integration. The minor background signal in the lower left region of the image does not extend into nor impact interpretation of correct clonal integration.

Reviewer #2 (Public Review):

Summary:

Blackwell et al. investigated the structure, localization, and physiological function of Plasmodium falciparum (Pf) heme oxygenase (HO). Pf and other malaria parasites scavenge and digest large amounts of hemoglobin from red cells for sustenance. To counter the potentially cytotoxic effects of heme, it is biomineralized into hemozoin and stored in the food vacuole. Another mechanism to counteract heme toxicity is through its enzymatic degradation via heme oxygenases. However, it was previously found by the authors that PfHO lacks the ability to catalyze heme degradation, raising the intriguing question of what the physiological function of PfHO is. In the current contribution, the authors determine that PfHO localizes to the apicoplast, determine its targeting sequence, establish the essentiality of PfHO for parasite viability, and determine that PfHO is required for proper maintenance of apicoplasts and apicoplast gene expression. In sum, the authors establish an essential physiological function for PfHO, thereby providing new insights into the role of PfHO in plasmodium metabolism.

Strengths:

The studies are rigorously conducted and the results of the experiments unambiguously support a role for PfHO as being an apicoplast-targeted protein required for parasite viability and maintenance of apicoplasts.

Weaknesses:

While the studies conducted are rigorous and support the primary conclusions, the lack of experiments probing the molecular function of PfHO limits the impact of the work. Nevertheless, the knowledge that PfHO is required for parasite viability and plays a role in the maintenance of apicoplasts is still an important advance.

We appreciate the positive assessment. We agree that further mechanistic understanding of PfHO function remains a key future challenge. Indeed, we made extensive efforts to unravel PfHO interactions that underpin its critical function. We elucidated key interactions with the apicoplast genome, reliance on the electropositive N-terminus, association with DNA-binding proteins, and a specific defect in apicoplast mRNA levels. The major limitation we faced in further defining PfHO function is the general lack of understanding of apicoplast transcription and broader gene expression. That limitation and the challenges to overcome it go well beyond our study and will require concerted efforts across several manuscripts (likely by multiple groups) to define the mechanistic features of apicoplast gene expression. We look forward to contributing further molecular understanding of PfHO function as broader understanding of apicoplast transcription emerges.

eLife assessment

This study investigates the conditions under which abstract knowledge transfers to new learning. It presents evidence across a number of behavioral experiments that when explicit awareness of learned statistical structure is present, knowledge can transfer immediately, but that otherwise similar transfer requires sleep-dependent consolidation. The valuable results provide new constraints on theories of transfer learning and consolidation, though limitations in the statistical approach and interpretation make the current evidence incomplete.

Reviewer #1 (Public Review):

Summary:

This paper investigates the effects of the explicit recognition of statistical structure and sleep consolidation on the transfer of learned structure to novel stimuli. The results show a striking dissociation in transfer ability between explicit and implicit learning of structure, finding that only explicit learners transfer structure immediately. Implicit learners, on the other hand, show an intriguing immediate structural interference effect (better learning of novel structure) followed by successful transfer only after a period of sleep.

Strengths:

This paper is very well written and motivated, and the data are presented clearly with a logical flow. There are several replications and control experiments and analyses that make the pattern of results very compelling. The results are novel and intriguing, providing important constraints on theories of consolidation. The discussion of relevant literature is thorough. In summary, this work makes an exciting and important contribution to the literature.

Weaknesses:

There have been several recent papers that have identified issues with alternative forced choice (AFC) tests as a method of assessing statistical learning (e.g. Isbilen et al. 2020, Cognitive Science). A key argument is that while statistical learning is typically implicit, AFC involves explicit deliberation and therefore does not match the learning process well. The use of AFC in this study thus leaves open the question of whether the AFC measure benefits the explicit learners in particular, given the congruence between knowledge and testing format, and whether, more generally, the results would have been different had the method of assessing generalization been implicit. Prior work has shown that explicit and implicit measures of statistical learning do not always produce the same results (eg. Kiai & Melloni, 2021, bioRxiv; Liu et al. 2023, Cognition).

Given that the explicit/implicit classification was based on an exit survey, it is unclear when participants who are labeled "explicit" gained that explicit knowledge. This might have occurred during or after either of the sessions, which could impact the interpretation of the effects.

Reviewer #2 (Public Review):

Summary:

Sleep has not only been shown to support the strengthening of memory traces but also their transformation. A special form of such transformation is the abstraction of general rules from the presentation of individual exemplars. The current work used large online experiments with hundreds of participants to shed further light on this question. In the training phase, participants saw composite items (scenes) that were made up of pairs of spatially coupled (i.e., they were next to each other) abstract shapes. In the initial training, they saw scenes made up of six horizontally structured pairs, and in the second training phase, which took place after a retention phase (2 min awake, 12 h incl. sleep, 12 h only wake, 24 h incl. sleep), they saw pairs that were horizontally or vertically coupled. After the second training phase, a two-alternatives-forced-choice (2-AFC) paradigm, where participants had to identify true pairs versus randomly assembled foils, was used to measure the performance of all pairs. Finally, participants were asked five questions to identify, if they had insight into the pair structure, and post-hoc groups were assigned based on this. Mainly the authors find that participants in the 2-minute retention experiment without explicit knowledge of the task structure were at chance level performance for the same structure in the second training phase, but had above chance performance for the vertical structure. The opposite was true for both sleep conditions. In the 12 h wake condition these participants showed no ability to discriminate the pairs from the second training phase at all.

Strengths:

All in all, the study was performed to a high standard and the sample size in the implicit condition was large enough to draw robust conclusions. The authors make several important statistical comparisons and also report an interesting resampling approach. There is also a lot of supplemental data regarding robustness.

Weaknesses:

My main concern regards the small sample size in the explicit group and the lack of experimental control.

Reviewer #3 (Public Review):

In this project, Garber and Fiser examined how the structure of incidentally learned regularities influences subsequent learning of regularities, that either have the same structure or a different one. Over a series of six online experiments, it was found that the structure (spatial arrangement) of the first set of regularities affected the learning of the second set, indicating that it has indeed been abstracted away from the specific items that have been learned. The effect was found to depend on the explicitness of the original learning: Participants who noticed regularities in the stimuli were better at learning subsequent regularities of the same structure than of a different one. On the other hand, participants whose learning was only implicit had an opposite pattern: they were better in learning regularities of a novel structure than of the same one. This opposite effect was reversed and came to match the pattern of the explicit group when an overnight sleep separated the first and second learning phases, suggesting that the abstraction and transfer in the implicit case were aided by memory consolidation.

These results are interesting and can bridge several open gaps between different areas of study in learning and memory. However, I feel that a few issues in the manuscript need addressing for the results to be completely convincing:

(1) The reported studies have a wonderful and complex design. The complexity is warranted, as it aims to address several questions at once, and the data is robust enough to support such an endeavor. However, this work would benefit from more statistical rigor. First, the authors base their results on multiple t-tests conducted on different variables in the data. Analysis of a complex design should begin with a large model incorporating all variables of interest. Only then, significant findings would warrant further follow-up investigation into simple effects (e.g., first find an interaction effect between group and novelty, and only then dive into what drives that interaction). Furthermore, regardless of the statistical strategy used, a correction for multiple comparisons is needed here. Otherwise, it is hard to be convinced that none of these effects are spurious. Last, there is considerable variation in sample size between experiments. As the authors have conducted a power analysis, it would be good to report that information per each experiment, so readers know what power to expect in each.

(2) Some methodological details in this manuscript I found murky, which makes it hard to interpret results. For example, the secondary results section of Exp1 (under Methods) states that phase 2 foils for one structure were made of items of the other structure. This is an important detail, as it may make testing in phase 2 easier, and tie learning of one structure to the other. As a result, the authors infer a "consistency effect", and only 8 test trials are said to be used in all subsequent analyses of all experiments. I found the details, interpretation, and decision in this paragraph to lack sufficient detail, justification, and visibility. I could not find either of these important design and analysis decisions reflected in the main text of the manuscript or in the design figure. I would also expect to see a report of results when using all the data as originally planned. Similarly, the matched sample analysis is a great addition, but details are missing. Most importantly, it was not clear to me why the same matching method should be used for all experiments instead of choosing the best matching subgroup (regardless of how it was arrived at), and why the nearest-neighbor method with replacement was chosen, as it is not evident from the numbers in Supplementary Table 1 that it was indeed the best-performing method overall. Such omissions hinder interpreting the work.

(3) To me, the most surprising result in this work relates to the performance of implicit participants when phase 2 followed phase 1 almost immediately (Experiment 1 and Supplementary Experiment 1). These participants had a deficit in learning the same structure but a benefit in learning the novel one. The first part is easier to reconcile, as primacy effects have been reported in statistical learning literature, and so new learning in this second phase could be expected to be worse. However, a simultaneous benefit in learning pairs of a new structure ("structural novelty effect") is harder to explain, and I could not find a satisfactory explanation in the manuscript. After possible design and statistical confounds (my previous comments) are ruled out, a deeper treatment of this finding would be warranted, both empirically (e.g., do explicit participants collapse across Experiments 1 and Supplementary Experiment 1 show the same effect?) and theoretically (e.g., why would this phenomenon be unique only to implicit learning, and why would it dissipate after a long awake break?).

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This paper investigates the effects of the explicit recognition of statistical structure and sleep consolidation on the transfer of learned structure to novel stimuli. The results show a striking dissociation in transfer ability between explicit and implicit learning of structure, finding that only explicit learners transfer structure immediately. Implicit learners, on the other hand, show an intriguing immediate structural interference effect (better learning of novel structure) followed by successful transfer only after a period of sleep.

Strengths:

This paper is very well written and motivated, and the data are presented clearly with a logical flow. There are several replications and control experiments and analyses that make the pattern of results very compelling. The results are novel and intriguing, providing important constraints on theories of consolidation. The discussion of relevant literature is thorough. In summary, this work makes an exciting and important contribution to the literature.

Weaknesses:

There have been several recent papers that have identified issues with alternative forced choice (AFC) tests as a method of assessing statistical learning (e.g. Isbilen et al. 2020, Cognitive Science). A key argument is that while statistical learning is typically implicit, AFC involves explicit deliberation and therefore does not match the learning process well. The use of AFC in this study thus leaves open the question of whether the AFC measure benefits the explicit learners in particular, given the congruence between knowledge and testing format, and whether, more generally, the results would have been different had the method of assessing generalization been implicit. Prior work has shown that explicit and implicit measures of statistical learning do not always produce the same results (eg. Kiai & Melloni, 2021, bioRxiv; Liu et al. 2023, Cognition).

We agree that numerous papers in the Statistical Learning literature discuss how different test measures can lead to different results and, in principle, using a different measure could have led to varying results in our study. In addition, we believe there are numerous additional factors relevant to this issue including the dichotomous vs. continuous nature of implicit vs. explicit learning and the complexity of the interactions between the (degree of) explicitness of the participants' knowledge and the applied test method that transcend a simple labeling of tests as implicit or explicit and that strongly constrains the type of variations the results of  different test would produce. Therefore, running the same experiments with different learning measures in future studies could provide additional interesting data with potentially different results.

However, the most important aspect of our reply concerning the reviewer's comment is that although quantitative differences between the learning rate of explicit and implicit learners are reported in our study, they are not of central importance to our interpretations. What is central are the different qualitative patterns of performance shown by the explicit and the implicit learners, i.e., the opposite directions of learning differences for “novel” and “same” structure pairs, which are seen in comparisons within the explicit group vs. within the implicit group and in the reported interaction. Following the reviewer's concern, any advantage an explicit participant might have in responding to 2AFC trials using “novel” structure pairs should also be present in the replies of 2AFC trials using the “same” structure pairs and this effect, at best, could modulate the overall magnitude of the across groups (Expl/Impl.) effect but not the relative magnitudes within one group. Therefore, we see no parsimonious reason to believe that any additional interaction between the explicitness level of participants and the chosen test type would impede our results and their interpretation. We will make a note of this argument in the revised manuscript.

Given that the explicit/implicit classification was based on an exit survey, it is unclear when participants who are labeled "explicit" gained that explicit knowledge. This might have occurred during or after either of the sessions, which could impact the interpretation of the effects.

We agree that this is a shortcoming of the current design, and obtaining the information about participants’ learning immediately after Phase 1 would have been preferred. However, we made this choice deliberately as the disadvantage of assessing the level of learning at the end of the experiment is far less damaging than the alternative of exposing the participants to the exit survey question earlier and thereby letting them achieve explicitness or influence their mindset otherwise through contemplating the survey questions before Phase 2. Our Experiment 5 shows how realistic this danger of unwanted influence is: with a single sentence alluding to pairs in the instructions of Exp 5, we  could completely change participants' quantitative performance and qualitative response pattern. Unfortunately, there is no implicit assessment of explicitness we could use in our experimental setup. We also note that given the cumulative nature of statistical learning, we expect that the effect of using an exit survey for this assessment only shifts absolute magnitudes (i.e. the fraction of people who would fall into the explicit vs. implicit groups) but not aspects of the results that would influence our conclusions.

Reviewer #2 (Public Review):

Summary:

Sleep has not only been shown to support the strengthening of memory traces but also their transformation. A special form of such transformation is the abstraction of general rules from the presentation of individual exemplars. The current work used large online experiments with hundreds of participants to shed further light on this question. In the training phase, participants saw composite items (scenes) that were made up of pairs of spatially coupled (i.e., they were next to each other) abstract shapes. In the initial training, they saw scenes made up of six horizontally structured pairs, and in the second training phase, which took place after a retention phase (2 min awake, 12 h incl. sleep, 12 h only wake, 24 h incl.

sleep), they saw pairs that were horizontally or vertically coupled. After the second training phase, a two-alternatives-forced-choice (2-AFC) paradigm, where participants had to identify true pairs versus randomly assembled foils, was used to measure the performance of all pairs. Finally, participants were asked five questions to identify, if they had insight into the pair structure, and post-hoc groups were assigned based on this. Mainly the authors find that participants in the 2-minute retention experiment without explicit knowledge of the task structure were at chance level performance for the same structure in the second training phase, but had above chance performance for the vertical structure. The opposite was true for both sleep conditions. In the 12 h wake condition these participants showed no ability to discriminate the pairs from the second training phase at all.

Strengths:

All in all, the study was performed to a high standard and the sample size in the implicit condition was large enough to draw robust conclusions. The authors make several important statistical comparisons and also report an interesting resampling approach. There is also a lot of supplemental data regarding robustness.

Weaknesses:

My main concern regards the small sample size in the explicit group and the lack of experimental control.  

The sample sizes of the explicit participants in our experiments are, indeed, much smaller than those of the implicit participants due to the process of how we obtain the members of the two groups. However, these sample sizes of the explicit groups are not small at all compared to typical experiments reported in Visual Statistical Learning studies, rather they tend to be average to large sizes. It is the sizes of the implicit subgroups that are unusually high due to the aforementioned data collecting process. Moreover, the explicit subgroups have significantly larger effect sizes than the implicit subgroup, bolstering the achieved power that is also confirmed by the reported Bayes Factors that support the “effect” or the “no effect” conclusions in the various tests ranging in value from substantial to very strong.  Based on these statistical measures,  we think the sample sizes of the explicit participants in our studies are adequate.

However, we do agree that the unbalanced nature of the sample and effect sizes can be problematic for the between-group comparisons. We aim to replace the student’s t-tests that directly compares explicit and implicit participants with Welch’s t-tests that are better suited for unequal sample sizes and variances.

As for the lack of experimental control, indeed, we could not fully randomize consolidation condition assignment. Instead, the assignment was a product of when the study was made available on the online platform Prolific. This method could, in theory, lead to an unobserved covariate, such as morningness, being unbalanced between conditions. We do not have any reasons to believe that such a condition would critically alter the effects reported in our study, but as it follows from the nature of unobserved variables, we obviously cannot state this with certainty. Therefore, we will explicitly discuss these potential pitfalls in the revised version of the manuscript.  

Reviewer #3 (Public Review):

In this project, Garber and Fiser examined how the structure of incidentally learned regularities influences subsequent learning of regularities, that either have the same structure or a different one. Over a series of six online experiments, it was found that the structure (spatial arrangement) of the first set of regularities affected the learning of the second set, indicating that it has indeed been abstracted away from the specific items that have been learned. The effect was found to depend on the explicitness of the original learning: Participants who noticed regularities in the stimuli were better at learning subsequent regularities of the same structure than of a different one. On the other hand, participants whose learning was only implicit had an opposite pattern: they were better in learning regularities of a novel structure than of the same one. This opposite effect was reversed and came to match the pattern of the explicit group when an overnight sleep separated the first and second learning phases, suggesting that the abstraction and transfer in the implicit case were aided by memory consolidation.

These results are interesting and can bridge several open gaps between different areas of study in learning and memory. However, I feel that a few issues in the manuscript need addressing for the results to be completely convincing:

(1) The reported studies have a wonderful and complex design. The complexity is warranted, as it aims to address several questions at once, and the data is robust enough to support such an endeavor. However, this work would benefit from more statistical rigor. First, the authors base their results on multiple t-tests conducted on different variables in the data. Analysis of a complex design should begin with a large model incorporating all variables of interest. Only then, significant findings would warrant further follow-up investigation into simple effects (e.g., first find an interaction effect between group and novelty, and only then dive into what drives that interaction). Furthermore, regardless of the statistical strategy used, a correction for multiple comparisons is needed here. Otherwise, it is hard to be convinced that none of these effects are spurious. Last, there is considerable variation in sample size between experiments. As the authors have conducted a power analysis, it would be good to report that information per each experiment, so readers know what power to expect in each.

Answering the questions we were interested in required us to investigate two related but separate types of effects within our data: general above-chance performance in learning, and within- and across-group differences.

Above-chance performance: As typical in SL studies, we needed to assess whether learning happened at all and which types of items were learned. For this, a comparison to the chance level is crucial and, therefore, one-sample t-test is the statistical test of choice. Note that all our t-tests were subject to experiment-wise correction for multiple comparisons using the Holm-Bonferroni procedure, as reported in the Supplementary Materials.

Within- and across-group differences: To obtain our results regarding group and partype differences and their interactions, we used mixed ANOVAs and appropriate post-hoc tests as the reviewer suggested. These results are reported in the method section.

Concerning power analysis, we will add the requested information on achieved power by experiment to the revised version of the manuscript.  

(2) Some methodological details in this manuscript I found murky, which makes it hard to interpret results. For example, the secondary results section of Exp1 (under Methods) states that phase 2 foils for one structure were made of items of the other structure. This is an important detail, as it may make testing in phase 2 easier, and tie learning of one structure to the other. As a result, the authors infer a "consistency effect", and only 8 test trials are said to be used in all subsequent analyses of all experiments. I found the details, interpretation, and decision in this paragraph to lack sufficient detail, justification, and visibility. I could not find either of these important design and analysis decisions reflected in the main text of the manuscript or in the design figure. I would also expect to see a report of results when using all the data as originally planned.  

We thank the reviewer for pointing out these critical open questions our manuscript that need further clarification. The inferred “consistency effect” is based on patterns found in the data, which show an increase in negative correlation between test types during the test phase. As this is apparently an effect of the design of the test phase and not an effect of the training phase, which we were interested in, we decided to minimize this effect as far as possible by focusing on the early test trials. For the revised version of the manuscript, we will revamp and expand how this issue was handled and also add a short comment in the main text, mentioning the use of only a subset of test trials and pointing the interested reader to the details.

Similarly, the matched sample analysis is a great addition, but details are missing. Most importantly, it was not clear to me why the same matching method should be used for all experiments instead of choosing the best matching subgroup (regardless of how it was arrived at), and why the nearest-neighbor method with replacement was chosen, as it is not evident from the numbers in Supplementary Table 1 that it was indeed the best-performing method overall. Such omissions hinder interpreting the work.

Since our approach provided four different balanced metrics (see Supp. Tables 1-4) for each matching method, it is not completely straightforward to make a principled decision across the methods. In addition, selecting the best method for each experiment separately carries the suspicion of cherry-picking the most suitable results for our purposes. For the revised version, we will expand on our description of the matching and decision process and add additional descriptive plots showing what our data looks like under each matching method for each experiment. These plots highlight that the matching techniques produce qualitatively roughly identical results and picking one of them over the other does not alter the conclusions of the test.  The plots will give the interested reader all the necessary information to assess the extent our design decisions influence our results.

(3) To me, the most surprising result in this work relates to the performance of implicit participants when phase 2 followed phase 1 almost immediately (Experiment 1 and Supplementary Experiment 1). These participants had a deficit in learning the same structure but a benefit in learning the novel one. The first part is easier to reconcile, as primacy effects have been reported in statistical learning literature, and so new learning in this second phase could be expected to be worse. However, a simultaneous benefit in learning pairs of a new structure ("structural novelty effect") is harder to explain, and I could not find a satisfactory explanation in the manuscript.  

Although we might not have worded it clearly, we do not claim that our "structural novelty effect" comes from a “benefit” in learning pairs of the novel structure. Rather, we used the term “interference” and lack of this interference. In other words, we believe that one possible explanation is that there is no actual benefit for learning pairs of the novel structure but simply unhindered learning for pairs of the novel structure and simultaneous inference for learning pairs of the same structure. Stronger interference for the same compared to the novel structure items seems as a reasonable interpretation as similarity-based interference is well established in the general (not SL-specific) literature under the label of proactive interference. We will clarify these ideas in the revised manuscript.

After possible design and statistical confounds (my previous comments) are ruled out, a deeper treatment of this finding would be warranted, both empirically (e.g., do explicit participants collapse across Experiments 1 and Supplementary Experiment 1 show the same effect?) and theoretically (e.g., why would this phenomenon be unique only to implicit learning, and why would it dissipate after a long awake break?).

Across all experiments, the explicit participants showed the same pattern of results but no significant difference between pair types, probably due to insufficiency of the available  sample sizes. We already included in the main text the collapsed explicit results across Experiments 1-4 and Supplementary Experiment 1 (p. 16).  This analysis confirmed that, indeed, there was a significant generalization for explicit participants across the two learning phases. We could re-run the same analysis for only Experiment 1 and

Supplementary Experiment 1, but due to the small sample of  N=12 in Suppl. Exp. 1, this test will be likely completely underpowered. Obtaining the sufficient sample size for this one test would require an excessive number (several hundreds) of new participants.  

In terms of theoretical treatment, we already presented our interpretation of our results in the discussion section, which we can expand on in the revised manuscript.

eLife assessment

This study presents valuable findings on the role of a well-studied signal transduction pathway, the Slit/Robo system, in the context of the assembly of the hematopoietic niche in the Drosophila embryo. The evidence supporting the claims of the authors is solid. However, one aspect that needs attention is whether the cells are migrating and not being pushed to a more dorsal position through dorsal closure and/or other similar large-scale embryo movement. This does not detract from the very interesting analysis of PSC morphogenesis and will interest developmental biologists working on molecular mechanisms of tissue morphogenesis.

Reviewer #1 (Public Review):

Summary:

The study by Nelson et al. is focused on the formation of the Drosophila Posterior Signaling Center (PSC) which ultimately acts as a niche to support hematopoietic stem cells of the lymph gland (LG). Using a combination of genetics and live imaging, the authors show that PSC cells migrate as a tight collective and associate with multiple tissues during a trajectory that positions them at the posterior of the LG.<br /> This is an important study that identifies Slit-Robo signaling as a regulator of PSC morphogenesis, and highlights the complex relationship of interacting cell types - PSC, visceral mesoderm (VM), and cardioblasts (CBs) - in the coordinated development of these three tissues during organ development. However, one point requiring clarification is the idea that PSC cells exhibit a collective cell migration; it is not clear that the cells are migrating rather than being pushed to a more dorsal position through dorsal closure and/or other similar large-scale embryo movement. This does not detract from the very interesting analysis of PSC morphogenesis as presented.

Strengths:

(1) Using the expression of Hid or Grim to ablate associated tissues, they find evidence that the VM and CB of the dorsal vessel affect PSC migration/morphology whereas the alary muscles do not. Slit is expressed by both VM and CBs, and therefore Slit-Robo signaling was investigated as PSCs express Robo.

(2) Using a combination of approaches, the authors convincingly demonstrate that Slit expression in the CBs and VM acts to support PSC positioning. A strength is the ability to knockdown slit levels in particular tissue types using the Gal4 system and RNAi.

(3) Although in the analysis of robo mutants, the PSC positioning phenotype is weaker in the individual mutants (robo1 and robo2) with only the double mutant (robo1,robo2) exhibiting a phenotype comparable to the slit RNAi. The authors make a reasonable argument that Slit-Robo signaling has an intrinsic effect, likely acting within PSCs because PSCs show a phenotype even when CBs do not (Figure 4G).

(4) New insight into dorsal vessel formation by VM is presented in Figure 4A, B, as loss of the VM can affect dorsal vessel morphogenesis. This result additionally points to the VM as important.

Weaknesses:

(1) The authors are cautioned to temper the result that Slit-Robo signaling is intrinsic to PSC since the loss of robo may affect other cell types (besides CBs and PSCs) to indirectly affect PSC migration/morphogenesis. In fact, in the robo2, robo1 mutant, the VM appears to be incorrectly positioned (Figure 4G).

(2) If possible, the authors should use RNAi to knockdown Robo1 and Robo2 levels specifically in the PSCs if a Gal4 is available; might Antp.Gal4 (Fig 1K) be useful? Even if knockdown is achieved in PSCs+CBs, this would be a better/complementary experiment to support the approach outlined in Figure 4D.

(3) Movies are hard to interpret, as it seems unclear that the PSCs actively migrate rather than being pushed/moved indirectly due to association with VM and CBs/dorsal vessel.

Reviewer #2 (Public Review):

The paper by Nelson KA, et al. explored the collective migration, coalescence, and positioning of the posterior signaling center (PSC) cells in Drosophila embryo. With live imaging, the authors observed the dynamic progress of PSC migration. Throughout this process, visceral mesoderm (VM), alary muscles (Ams), and cardioblasts (CBs) are in proximity to PSC. Genetic ablation of these tissues reveals the requirement for VM and CBs, but not AMs in this process. Genetic manipulations further demonstrated that Slit-Robo signaling was critical during PSC migration and positioning. While the genetic mechanisms of positioning the PSC were explored in much detail, including using live imaging, the functional consequence of mispositioning or (partial) absence of PSC cells has not been addressed, but would much increase the relevance of their findings. A few additional issues need to be addressed as well in this otherwise well-done study.

Major points:

(1) The only readout in their experiments is the relative correctness of PSC positioning. Importantly, what is the functional consequence if PSC is not properly positioned? This would be particularly important with robo-sli manipulations, where the PSC is present but some cells are misplaced. What is the consequence? Are the LGs affected, like the specification of their cell types, structure, and function? To address this for at least the robo-slit requirement in the PSC, it may be important to manipulate them directly in the PSC with a split Gal4 system, using Antp and Odd promoters.

(2) The densely, parallel aligned fibers in the part of Figure 1J seemed to be visceral mesoderm, but further up (dorsally) that may be epidermis. It is possible that the PSC migrate together with the epidermis? This should be addressed.

(3) Although the authors described the standards of assessing PSC positioning as "normal" or "abnormal", it is rather subtle at times and variable in the mutant or KD/OE examples. The criteria should be more clearly delineated and analyzed double-blind, also since this is the only readout. Further examples of abnormal positioning in supplementary figures would also help.

(4) The Discussion is very lengthy and should shortened.

Reviewer #3 (Public Review):

Summary:

This work is a detailed and thorough analysis of the morphogenesis of the posterior signaling center (PSC), a hematopoietic niche in the Drosophila larva. Live imaging is performed from the stage of PSC determination until the appearance of a compact lymph gland and PSC in the stage 16 embryo. This analysis is combined with genetic studies that clarify the involvement of adjacent tissue, including the visceral mesoderm, alary muscle, and cardioblasts/dorsal vessels. Lastly, the Slit/Robo signaling system is clearly implicated in the normal formation of the PSC.

Strengths:

The data are clearly presented, well documented, and fully support the conclusions drawn from the different experiments. The manuscript differs in character from the mainstay of "big data" papers (for example, no sets of single-cell RNAseq data of, for instance, PSC cells with more or less Slit input, are offered), but what it lacks in this regard, it makes up in carefully planned and executed visualizations and genetic manipulations.

Weaknesses:

A few suggestions concerning improvement of the way the story is told and contextualized.

(1) The minute cluster of PSC progenitors (5 or so cells per side) is embedded (as known before and shown nicely in this study) in other "migrating" cell pools, like the cardioblasts, pericardial cells, lymph gland progenitors, alary muscle progenitors. These all appear to move more or less synchronously. What should also be mentioned is another tissue, the dorsal epidermis, which also "moves" (better: stretches?) towards the dorsal midline during dorsal closure. Would it be reasonable to speculate (based on previously published data) that without the force of dorsal closure, operating in the epidermis, at least the lateral>medial component of the "migration" of the PSC (and neighboring tissues) would be missing? If dorsal closure is blocked, do essential components of PSC and lymph gland morphogenesis (except for the coming-together of the left and right halves) still occur? Are there any published data on this?

(2) Along similar lines: the process of PSC formation is characterized as "migration". To be fair: the authors bring up the possibility that some of the phenotypes they observe could be "passive"/secondary: "Thus, it became important to test whether all PSC phenotypes might be 'passive', explained by PSC attachment to a malforming dorsal vessel. Alternatively, the PSC defects could reflect a requirement for Robo activation directly in PSC cells." And the issue is resolved satisfactorily. But more generally, "cell migration" implies active displacement (by cytoskeletal forces) of cells relative to a substrate or to their neighbors (like for example migration of hemocytes). This to me doesn't seem really clearly to happen here for the dorsal mesodermal structures. Couldn't one rather characterize the assembly of PSC, lymph gland, pericardial cells, and dorsal vessel in terms of differential adhesion, on top of a more general adhesion of cells to each other and the epidermis, and then dorsal closure as a driving force for cell displacement? The authors should bring in the published literature to provide a background that does (or does not) justify the term "migration".

(3) That brings up the mechanistic centerpiece of this story, the Slit/Robo system. First: I suggest adding more detailed data from the study by Morin-Poulard et al 2016, in the Introduction, since these authors had already implicated Slit-Robo in PSC function and offered a concrete molecular mechanism: "vascular cells produce Slit that activates Robo receptors in the PSC. Robo activation controls proliferation and clustering of PSC cells by regulating Myc, and small GTPase and DE-cadherin activity, respectively". As stated in the Discussion: the mechanism of Slit/Robo action on the PSC in the embryo is likely different, since DE-cadherin is not expressed in the embryonic PSC; however, it maybe not be THAT different: it could also act on adhesion between PSC cells themselves and their neighbors. What are other adhesion proteins that appear in the late lateral mesodermal structures? Could DN-cadherin or Fasciclins be involved?

Author response:

eLife assessment

This study presents valuable findings on the role of a well-studied signal transduction pathway, the Slit/Robo system, in the context of the assembly of the hematopoietic niche in the Drosophila embryo. The evidence supporting the claims of the authors is solid. However, one aspect that needs attention is whether the cells are migrating and not being pushed to a more dorsal position through dorsal closure and/or other similar large-scale embryo movement. This does not detract from the very interesting analysis of PSC morphogenesis and will interest developmental biologists working on molecular mechanisms of tissue morphogenesis.

We appreciate the thoughtful and quite useful comments provided by each of the referees. Our responses are noted below each referee’s comment.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The study by Nelson et al. is focused on the formation of the Drosophila Posterior Signaling Center (PSC) which ultimately acts as a niche to support hematopoietic stem cells of the lymph gland (LG). Using a combination of genetics and live imaging, the authors show that PSC cells migrate as a tight collective and associate with multiple tissues during a trajectory that positions them at the posterior of the LG.

This is an important study that identifies Slit-Robo signaling as a regulator of PSC morphogenesis, and highlights the complex relationship of interacting cell types - PSC, visceral mesoderm (VM), and cardioblasts (CBs) - in the coordinated development of these three tissues during organ development. However, one point requiring clarification is the idea that PSC cells exhibit a collective cell migration; it is not clear that the cells are migrating rather than being pushed to a more dorsal position through dorsal closure and/or other similar large-scale embryo movement. This does not detract from the very interesting analysis of PSC morphogenesis as presented.

Since each referee asked for clarification concerning collective cell migration, we present a combined response further below, placed after the comments from Reviewer #3.

Strengths:

(1) Using the expression of Hid or Grim to ablate associated tissues, they find evidence that the VM and CB of the dorsal vessel affect PSC migration/morphology whereas the alary muscles do not. Slit is expressed by both VM and CBs, and therefore Slit-Robo signaling was investigated as PSCs express Robo.

(2) Using a combination of approaches, the authors convincingly demonstrate that Slit expression in the CBs and VM acts to support PSC positioning. A strength is the ability to knockdown slit levels in particular tissue types using the Gal4 system and RNAi.

(3) Although in the analysis of robo mutants, the PSC positioning phenotype is weaker in the individual mutants (robo1 and robo2) with only the double mutant (robo1,robo2) exhibiting a phenotype comparable to the slit RNAi. The authors make a reasonable argument that Slit-Robo signaling has an intrinsic effect, likely acting within PSCs because PSCs show a phenotype even when CBs do not (Figure 4G).

(4) New insight into dorsal vessel formation by VM is presented in Figure 4A, B, as loss of the VM can affect dorsal vessel morphogenesis. This result additionally points to the VM as important.

Weaknesses:

(1) The authors are cautioned to temper the result that Slit-Robo signaling is intrinsic to PSC since the loss of robo may affect other cell types (besides CBs and PSCs) to indirectly affect PSC migration/morphogenesis. In fact, in the robo2, robo1 mutant, the VM appears to be incorrectly positioned (Figure 4G).

We have reexamined our wording in the relevant Results section and, given that this referee agrees that we, “make a reasonable argument that Slit-Robo signaling has an intrinsic effect, likely acting within PSCs because PSCs show a phenotype even when CBs do not (Figure 4G)”, it was not clear how we might temper our conclusions more. Given that PSC cells express Robo1 and Robo2, and that the Vm does not contact the PSC, our ‘reasonable argument’ appears fair and parsimonious. Since we agree with the referee that a reader should be made as aware as possible of alternatives, we will add a comment to the Discussion, reminding the reader of the possibility of a secondary defect.

(2) If possible, the authors should use RNAi to knockdown Robo1 and Robo2 levels specifically in the PSCs if a Gal4 is available; might Antp.Gal4 (Fig 1K) be useful? Even if knockdown is achieved in PSCs+CBs, this would be a better/complementary experiment to support the approach outlined in Figure 4D.

While we agree that PSC-specific knockdown of Robo1 and Robo2 simultaneously would be ideal, this is not possible. First, the most-effective UAS-RNAi transgenes (that is, those in a Valium 20 backbone) are both integrated at the same chromosomal position; these cannot be simultaneously crossed with a GAL4 transgenic line to attempt double knock down. Additionally, as with all RNAi approaches that must rely on efficient knockdown over the rapid embryonic period, even having facile access to the above does not ensure the RNAi approach will cause as effective depletion as the genetic null condition that we use. Second, as the referee concedes, there is no embryonic PSC-specific GAL4. The proposed use of Antp-GAL4 would cause knockdown in many tissues (PSC, CB, Vm, epidermis and amnioserosa). This would lead to a reservation similar to that caused by our use of the straight genetic double mutant, as regards potential indirect requirement for Robo function.

(3) Movies are hard to interpret, as it seems unclear that the PSCs actively migrate rather than being pushed/moved indirectly due to association with VM and CBs/dorsal vessel.

First, the Vm does not directly contact the PSC, so it cannot be pushing the PSC dorsally. We will re-examine our text to be certain to make this clear. Second, in our analysis of bin mutants, which lack Vm, LGs and PSCs are able to reach the dorsal midline region in the absence of Vm. Finally, please see our response to Reviewer #3, point 2, for why we maintain that PSC cells are “migrating” even though some PSC cells are attached to CBs.

Reviewer #2 (Public Review):

The paper by Nelson KA, et al. explored the collective migration, coalescence, and positioning of the posterior signaling center (PSC) cells in Drosophila embryo. With live imaging, the authors observed the dynamic progress of PSC migration. Throughout this process, visceral mesoderm (VM), alary muscles (Ams), and cardioblasts (CBs) are in proximity to PSC. Genetic ablation of these tissues reveals the requirement for VM and CBs, but not AMs in this process. Genetic manipulations further demonstrated that Slit-Robo signaling was critical during PSC migration and positioning. While the genetic mechanisms of positioning the PSC were explored in much detail, including using live imaging, the functional consequence of mispositioning or (partial) absence of PSC cells has not been addressed, but would much increase the relevance of their findings. A few additional issues need to be addressed as well in this otherwise well-done study.

Major points:

(1) The only readout in their experiments is the relative correctness of PSC positioning. Importantly, what is the functional consequence if PSC is not properly positioned? This would be particularly important with robo-sli manipulations, where the PSC is present but some cells are misplaced. What is the consequence? Are the LGs affected, like the specification of their cell types, structure, and function? To address this for at least the robo-slit requirement in the PSC, it may be important to manipulate them directly in the PSC with a split Gal4 system, using Antp and Odd promoters.

We agree that the functional consequence of PSC mis-positioning is important and a relevant question to eventually address. However, virtually all markers and reagents used to assess the effect of the PSC on progenitor cells and their differentiated descendants are restricted to analyses carried out on the third larval instar - some three days after the experiments reported here. Most of the manipulated conditions in our work are no longer viable at this phase and, thus, addressing the functional consequences of a malformed PSC will require the field to develop new tools. 

As we noted in the Introduction, the consistency with which the wildtype PSC forms as a coalesced collective at the posterior of the LG strongly suggests importance of its specific positioning and shape, as has now been found for other niches (citations in manuscript). Additionally, in the Discussion we mention the existence of a gap junction-dependent calcium signaling network in the PSC that is important for progenitor maintenance. Without continuity of this network amongst all PSC cells (under conditions of PSC mis-positioning), we strongly anticipate that the balance of progenitors to differentiated hemocytes will be mis-managed, either constitutively, and / or under immune challenge conditions. 

Finally, to our knowledge, the tools do not exist to build a “split Gal4 system using Antp and Odd promoters”. The expression pattern observed using the genomic Antp-GAL4 line must be driven by endogenous enhancers–none of which have been defined by the field, and thus cannot be used in constructing second order drivers. Similarly, for odd skipped, in the embryo the extant Odd-GAL4 driver expresses only in the epidermis, with no expression in the embryonic LG. Thus, the cis regulatory element controlling Odd expression in the embryonic LG is unknown. In the future, the discovery of an embryonic PSC-specific driver will aid in addressing the specific functional consequences of PSC mis-positioning.

(2) The densely, parallel aligned fibers in the part of Figure 1J seemed to be visceral mesoderm, but further up (dorsally) that may be epidermis. It is possible that the PSC migrate together with the epidermis? This should be addressed.

See response to Reviewer #3.

(3) Although the authors described the standards of assessing PSC positioning as "normal" or "abnormal", it is rather subtle at times and variable in the mutant or KD/OE examples. The criteria should be more clearly delineated and analyzed double-blind, also since this is the only readout. Further examples of abnormal positioning in supplementary figures would also help.

We appreciate the Reviewer’s concern and acknowledge that the phenotypes we observed were indeed variable, and, at times subtle. As we show and discuss in the paper, our results revealed that the signaling requirements for proper PSC positioning are complex; this was favorably commented upon by Reviewer #1 (“...highlights the complex relationship of interacting cell types - PSC, visceral mesoderm (VM), and cardioblasts (CBs) - in the coordinated development of these three tissues during organ development.…”). We suspect the phenotypic variability is attributable to any number of biological differences such as heterogeneity of PSC cells and an accompanying difference in the timing of their competence to receive and respond to Slit-Robo signaling, the timing of release of Slit from CBs and Vm, number of cells in a given PSC, which PSC cells in the cluster respond to too little or too much signaling, and/or typical variability between organisms. Furthermore, PSC positioning analyses were conducted by two of the authors, who independently came to the same conclusions. For many of the manipulations double blinding was not possible since the genotype of the embryo was discernible due to the obvious phenotype of the manipulated tissue.

(4) The Discussion is very lengthy and should [be] shortened.

We will re-examine the prose and emphasize more conciseness, while maintaining clarity for the reader.

Reviewer #3 (Public Review):

Summary:

This work is a detailed and thorough analysis of the morphogenesis of the posterior signaling center (PSC), a hematopoietic niche in the Drosophila larva. Live imaging is performed from the stage of PSC determination until the appearance of a compact lymph gland and PSC in the stage 16 embryo. This analysis is combined with genetic studies that clarify the involvement of adjacent tissue, including the visceral mesoderm, alary muscle, and cardioblasts/dorsal vessels. Lastly, the Slit/Robo signaling system is clearly implicated in the normal formation of the PSC.

Strengths:

The data are clearly presented, well documented, and fully support the conclusions drawn from the different experiments. The manuscript differs in character from the mainstay of "big data" papers (for example, no sets of single-cell RNAseq data of, for instance, PSC cells with more or less Slit input, are offered), but what it lacks in this regard, it makes up in carefully planned and executed visualizations and genetic manipulations.

Weaknesses:

A few suggestions concerning improvement of the way the story is told and contextualized.

(1) The minute cluster of PSC progenitors (5 or so cells per side) is embedded (as known before and shown nicely in this study) in other "migrating" cell pools, like the cardioblasts, pericardial cells, lymph gland progenitors, alary muscle progenitors. These all appear to move more or less synchronously. What should also be mentioned is another tissue, the dorsal epidermis, which also "moves" (better: stretches?) towards the dorsal midline during dorsal closure. Would it be reasonable to speculate (based on previously published data) that without the force of dorsal closure, operating in the epidermis, at least the lateral>medial component of the "migration" of the PSC (and neighboring tissues) would be missing? If dorsal closure is blocked, do essential components of PSC and lymph gland morphogenesis (except for the coming-together of the left and right halves) still occur? Are there any published data on this?

Each of the Reviewers is interested in our response to this very relevant question, and, thus, we will address the issue en bloc here. First, we will add a Supplementary Figure showing that LG and CBs are still able to progress medially towards the dorsal midline when dorsal closure stalls.  This rules out any major effect for the most prominent “large-scale embryo cell sheet movement” in positioning the PSC. Second, published work by Haack et. al. and Balaghi et. al. shows that CBs and leading edge epidermal cells are independently migratory, and we will add this context to the manuscript for the reader.

(2) Along similar lines: the process of PSC formation is characterized as "migration". To be fair: the authors bring up the possibility that some of the phenotypes they observe could be "passive"/secondary: "Thus, it became important to test whether all PSC phenotypes might be 'passive', explained by PSC attachment to a malforming dorsal vessel. Alternatively, the PSC defects could reflect a requirement for Robo activation directly in PSC cells." And the issue is resolved satisfactorily. But more generally, "cell migration" implies active displacement (by cytoskeletal forces) of cells relative to a substrate or to their neighbors (like for example migration of hemocytes). This to me doesn't seem really clearly to happen here for the dorsal mesodermal structures. Couldn't one rather characterize the assembly of PSC, lymph gland, pericardial cells, and dorsal vessel in terms of differential adhesion, on top of a more general adhesion of cells to each other and the epidermis, and then dorsal closure as a driving force for cell displacement? The authors should bring in the published literature to provide a background that does (or does not) justify the term "migration".

Before addressing this specifically, we remind readers of our response above that states the rationale ruling out large, embryo-scale movements, such as epidermal dorsal closure, in driving PSC positioning. So, how are PSC cells arriving at their reproducible position? This manuscript reports the first live-imaging of the PSC as it comes to be positioned in the embryo. We interpret these movies to suggest strongly that these cells are a ‘collective’ that migrates. Neither the data, nor we, are asserting that each PSC cell is ‘individually’ migrating to its final position. Rather, our data suggest that the PSC migrates as a collective. The most paradigmatic example of directed, collective cell migration, is of Drosophila ovarian border cells. That cell cluster is surrounded at all times by other cells (nurse cells, in that case), and for the collective to traverse through the tissue, the process requires constant remodeling of associations amongst the migrating cells in the collective (the border cells), as well as between cells in the collective and those outside of it (the nurse cells). In fact, the nurse cells are considered the substrate upon which border cells migrate. Note also that in collective border cell migration cells within the collective can switch neighbors, suggesting dynamic changes to cell associations and adhesions. 

In our analysis, the PSC cells exhibit qualities reminiscent of the border cells, and thus we infer that the PSC constitutes a migratory cell collective.  We also show in Figure 1H that PSC cells exhibit cellular extensions, and thus have a very active, intrinsic actin-based cytoskeleton. In fact, in Figure 1I, we point out that PSC cells shift position within the collective, which is not only a direct feature of migration, but also occurs within the border cell collective as that collective migrates. Additionally, the fact that the lateral-most PSC cells shift position in the collective while remaining a part of the collective–and they do this while executing net directional movement–makes a strong argument that the PSC is migratory, as no cell types other than PSCs are contacting the surfaces of those shifting PSC cells. Lastly, the Reviewer’s supposition that, rather than migration, dorsal mesoderm structures form via “differential adhesion, on top of a more general adhesion of cells to each other” is, actually, precisely an inherent aspect of collective cell migration as summarized above for the ovarian border collective.

In our resubmission we will adjust text citing the existing literature to better put into context the reasoning for why PSC formation based on our data is an example of collective cell migration.

(3) That brings up the mechanistic centerpiece of this story, the Slit/Robo system. First: I suggest adding more detailed data from the study by Morin-Poulard et al 2016, in the Introduction, since these authors had already implicated Slit-Robo in PSC function and offered a concrete molecular mechanism: "vascular cells produce Slit that activates Robo receptors in the PSC. Robo activation controls proliferation and clustering of PSC cells by regulating Myc, and small GTPase and DE-cadherin activity, respectively". As stated in the Discussion: the mechanism of Slit/Robo action on the PSC in the embryo is likely different, since DE-cadherin is not expressed in the embryonic PSC; however, it maybe not be THAT different: it could also act on adhesion between PSC cells themselves and their neighbors. What are other adhesion proteins that appear in the late lateral mesodermal structures? Could DN-cadherin or Fasciclins be involved?

We agree with the Reviewer that Slit-Robo signaling likely acts in part on the PSC by affecting PSC cell adhesion to each other and/or to CBs (lines 428-435). As stated in the Discussion, we do not observe Fasciclin III expression in the PSC until late stages when the PSC has already been positioned, suggesting that Fasciclin III is not an active player in PSC formation. Assessing whether the PSC expresses any other of the suite of potential cell adhesion molecules such as DN-Cadherin or other Fasciclins, and then study their potential involvement in the Slit-Robo pathway in PSC cells, would be part of a follow-up study.

eLife assessment

To elucidate the precise function of variants in the UTRs, the authors established and conducted a massively parallel poly(ribo)some profiling method to compare ribosome associations and effects of genetic variants. The approach and results are valuable, as this is a new approach to studying UTRs. However, the experimental and analytic validation seems to be incomplete, as the results are less robust than expected.

Reviewer #1 (Public Review):

The authors describe a massively parallel reporter assays (MPRA) screen focused on identifying polymorphisms in 5' and 3' UTRs that affect translation efficiency and thus might have a functional impact on cells. The topic is of timely interest, and indeed, several related efforts have recently been published and preprinted (e.g., https://pubmed.ncbi.nlm.nih.gov/37516102/ and https://www.ncbi.nlm.nih.gov/pmc/articles/PMC10635273/). This study has several major issues with the results and their presentation.

Major comments:

(1) The main issue is that it appears that the screen has largely failed, yet the reasons for that are unclear, which makes it difficult to interpret. The authors start with a library that includes approximately 6,000 variants, which makes it a medium-sized MPRA. But then, only 483 pairs of WT/mutated UTRs yield high-confidence information, which is already a small number for any downstream statistical analysis, particularly since most don't actually affect translation in the reporter screen setting (which is not unexpected). It is unclear why >90% of the library did not give high-confidence information. The profiles presented as base-case examples in Figure 2B don't look very informative or convincing. All the subsequent analysis is done on a very small set of UTRs that have an effect, and it is unclear to this reviewer how these can yield statistically significant and/or biologically relevant associations.

(2) From the variants that had an effect, the authors go on to carry out some protein-level validations and see some changes, but it is not clear if those changes are in the same direction as observed in the screen.

(3) The authors follow up on specific motifs and specific RBPs predicted to bind them, but it is unclear how many of the hits in the screen actually have these motifs, or how significant motifs can arise from such a small sample size.

(4) It is particularly puzzling how the authors can build a machine learning predictor with >3,000 features when the dataset they use for training the model has just a few dozens of translation-shifting variants.

(5) The lack of meaningful validation experiments altering the SNPs in the endogenous loci by genome editing limits the impact of the results.

Reviewer #2 (Public Review):

Summary:

In their paper "Massively Parallel Polyribosome Profiling Reveals Translation Defects of Human Disease‐Relevant UTR Mutations" the authors use massively parallel polysome profiling to determine the effects of 5' and 3' UTR SNPs (from dbSNP/ClinVar) on translational output. They show that some UTR SNPs cause a change in the polysome profile with respect to the wild-type and that pathogenic SNPs are enriched in the polysome-shifting group. They validate that some changes in polysome profiles are predictive of differences in translational output using transiently expressed luciferase reporters. Additionally, they identify sequence motifs enriched in the polysome-shifting group. They show that 2 enriched 5' UTR motifs increase the translation of a luciferase reporter in a protein-dependent manner, highlighting the use of their method to identify translational control elements.

Strengths:

This is a useful method and approach, as UTR variants have been more difficult to study than coding variants. Additionally, their evidence that pathogenic mutations are more likely to cause changes in polysome association is well supported.

Weaknesses:

The authors acknowledge that they "did not intend to immediately translate the altered polysome profile into an increase or decrease in translation efficiency, as the direction of the shift was not readily evident. Additionally, sedimentation in the sucrose gradient may have been partially affected by heavy particles other than ribosomes." However, shifted polysome distribution is used as a category for many downstream analyses. Without further clarity or subdivision, it is very difficult to interpret the results (for example in Figure 5A, is it surprising that the polysome shifting mutants decrease structure? Are the polysome "shifts" towards the untranslated or heavy fractions?)

Author response:

Public Reviews:

Reviewer #1 (Public Review):

The authors describe a massively parallel reporter assays (MPRA) screen focused on identifying polymorphisms in 5' and 3' UTRs that affect translation efficiency and thus might have a functional impact on cells. The topic is of timely interest, and indeed, several related efforts have recently been published and preprinted (e.g., https://pubmed.ncbi.nlm.nih.gov/37516102/ and https://www.ncbi.nlm.nih.gov/pmc/articles/PMC10635273/). This study has several major issues with the results and their presentation.

Major comments:

(1) The main issue is that it appears that the screen has largely failed, yet the reasons for that are unclear, which makes it difficult to interpret. The authors start with a library that includes approximately 6,000 variants, which makes it a medium-sized MPRA. But then, only 483 pairs of WT/mutated UTRs yield high-confidence information, which is already a small number for any downstream statistical analysis, particularly since most don't actually affect translation in the reporter screen setting (which is not unexpected). It is unclear why >90% of the library did not give highconfidence information. The profiles presented as base-case examples in Figure 2B don't look very informative or convincing. All the subsequent analysis is done on a very small set of UTRs that have an effect, and it is unclear to this reviewer how these can yield statistically significant and/or biologically relevant associations.

To make sure our final results are technically and statistically sound, we applied stringent selection criteria and cutoffs in our analytics workflow. First, from our RNA-seq dataset, we filtered the UTRs with at least 20 reads in a polysome profile across all three repeated experiments. Secondly, in the following main analysis using a negative binomial generalized linear model (GLM), we further excluded the UTRs that displayed batch effect, i.e. their batch-related main effect and interaction are significant. We believe our measure has safeguarded the filtered observations (UTRs) from the (potential) high variation of our massively parallel translation assays and thus gives high confidence to our results.

Regarding the interpretation of Figure 2B, since we aimed to identify the UTRs whose interaction term of genotype and fractions is significant in our generalized linear model, it is statistically conventional to double-check the interaction of the two variables using such a graph. For instance, in the top left panel of Figure 2B (5'UTR of ANK2:c.-39G>T), we can see that read counts of WT samples congruously decreased from Mono to Light, whereas the read counts of mutant samples were roughly the same in the two fractions – the trend is different between WT and mutant. Ergo, the distinct distribution patterns of two genotypes across three fractions in Figure 2B offer the readers a convincing visual supplement to our statistics from GLM.

In contrast to Figure 2B, the graphs of nonsignificant UTRs (shown below) reveal that the trends between the two genotypes are similar across the 'Mono and Light' and 'Light and Heavy' polysome fractions. Importantly, our analysis remains unaffected by differential expression levels between WT and mutant, as it specifically distinguishes polysome profiles with different distributions. This consistent trend further supports the lack of interaction between genotype and polysome fractions for these UTRs.

Author response image 1.

Figure: Examples of non-significant UTR pairs in massively parallel polysome profiling assays.

(2) From the variants that had an effect, the authors go on to carry out some protein-level validations and see some changes, but it is not clear if those changes are in the same direction as observed in the screen.

To infer the directionality of translation efficiency from polysome profiles, a common approach involves pooling polysome fractions and comparing them with free or monosome fractions to identify 'translating' fractions. However, this method has two major potential pitfalls: (i) it sacrifices resolution and does not account for potential bias toward light or heavy polysomes, and (ii) it fails to account for discrepancies between polysome load and actual protein output (as discussed in https://doi.org/10.1016/j.celrep.2024.114098 and https://doi.org/10.1038/s41598-019-47424-w). Therefore, our analysis focused on the changes within polysome profiles themselves. 'Significant' candidates were identified based on a significant interaction between genotype and polysome distribution using a negative binomial generalized linear model, without presupposing the direction of change on protein output. 

(3) The authors follow up on specific motifs and specific RBPs predicted to bind them, but it is unclear how many of the hits in the screen actually have these motifs, or how significant motifs can arise from such a small sample size.

We calculated the Δmotif enrichment in significant UTRs versus nonsignificant UTRs using Fisher’s exact test. For example, the enrichment of the Δ‘AGGG’ motif in 3’ UTRs is shown below:

Author response table 1.

This test yields a P-value of 0.004167 by Fisher’s exact test. The P-values and Odds ratios of Δmotifs in relation to polysome shifting are included in Supplementary Table S4, and we will update the detailed motif information in the revised Supplementary Table S4.

(4) It is particularly puzzling how the authors can build a machine learning predictor with >3,000 features when the dataset they use for training the model has just a few dozens of translation-shifting variants.

We understand the concern regarding the relatively small number of translation-shifting variants compared to the large number of features. To address this, we employed LASSO regression, which, according to The Elements of Statistical Learning by Hastie, Tibshirani, and Friedman, is particularly suitable for datasets where the number of features 𝑝𝑝 is much larger than the number of samples 𝑁𝑁. LASSO effectively performs feature selection by shrinking less important coefficients to zero, allowing us to build a robust and generalizable model despite the limited number of variants.

(5) The lack of meaningful validation experiments altering the SNPs in the endogenous loci by genome editing limits the impact of the results.

We plan to assess the endogenous effect by generating CRISPR knock-in clones carrying the UTR variant.

Reviewer #2 (Public Review):

Summary:

In their paper "Massively Parallel Polyribosome Profiling Reveals Translation Defects of Human Disease‐Relevant UTR Mutations" the authors use massively parallel polysome profiling to determine the effects of 5' and 3' UTR SNPs (from dbSNP/ClinVar) on translational output. They show that some UTR SNPs cause a change in the polysome profile with respect to the wild-type and that pathogenic SNPs are enriched in the polysome-shifting group. They validate that some changes in polysome profiles are predictive of differences in translational output using transiently expressed luciferase reporters. Additionally, they identify sequence motifs enriched in the polysome-shifting group. They show that 2 enriched 5' UTR motifs increase the translation of a luciferase reporter in a proteindependent manner, highlighting the use of their method to identify translational control elements.

Strengths:

This is a useful method and approach, as UTR variants have been more difficult to study than coding variants. Additionally, their evidence that pathogenic mutations are more likely to cause changes in polysome association is well supported.

Weaknesses:

The authors acknowledge that they "did not intend to immediately translate the altered polysome profile into an increase or decrease in translation efficiency, as the direction of the shift was not readily evident. Additionally, sedimentation in the sucrose gradient may have been partially affected by heavy particles other than ribosomes." However, shifted polysome distribution is used as a category for many downstream analyses. Without further clarity or subdivision, it is very difficult to interpret the results (for example in Figure 5A, is it surprising that the polysome shifting mutants decrease structure? Are the polysome "shifts" towards the untranslated or heavy fractions?)

Our approach, combining polysome fractionation of the UTR library with negative binomial generalized linear model (GLM) analysis of RNA-seq data, systematically identifies variants that affect translational efficiency. The GLM model is specifically designed to detect UTR pairs with significant interactions between genotype and polysome fractions, relying solely on changes in polysome profiles to identify variants that disrupt translation. Consequently, our analytical method does not determine the direction of translation alteration.

Following the massively parallel polysome profiling, we sought to understand how these polysomeshifting variants influence the translation process. To do this, we examined their effects on RNA characteristics related to translation, such as RBP binding and RNA structure. In Figure 5A, we observed a notable trend in significant hits within 5’ UTRs—they tend to increase ΔG (weaker folding energy) in response to changes in polysome profiles, regardless of whether protein production increases or decreases (Fig. 3).

eLife assessment

This important study further validates DNAH12 as a causative gene for asthenoteratozoospermia and male infertility in humans and mice. The data supporting the notion that DNAH12 is required for proper axonemal development are generally convincing, although more experiments would solidify the conclusions. This work will interest reproductive biologists working on spermatogenesis and sperm biology, as well as andrologists working on male fertility.

Reviewer #1 (Public Review):

Summary:

Even though this is not the first report that the mutation in the DNAH12 gene causes asthenoteratozoospermia, the current study explores the sperm phenotype in-depth. The authors show experimentally that the said mutation disrupts the proper axonemal arrangement and recruitment of DNALI1 and DNAH1 - proteins of inner dynein arms. Based on these results, the authors propose a functional model of DNAH12 in proper axonemal development. Lastly, the authors demonstrate that the male infertility caused by the studies mutation can be rescued by ICSI treatment at least in the mouse. This study furthers our understanding of male infertility caused by a mutation of axonemal protein DNAH12, and how this type of infertility can be overcome using assisted reproductive therapy.

Strengths:<br /> This is an in-depth functional study, employing multiple, complementary methodologies to support the proposed working model.

Weaknesses:

The study strength could be increased by including more controls such as peptide blocking of the inhouse raised mouse and rat DNAH12 antibodies, and mass spectrometry of control IP with beads/IgG only to exclude non-specific binding. Objective quantifications of immunofluorescence images and WB seem to be missing. At least three technical replicates of western blotting of sperm and testis extracts could have been performed to demonstrate that the decrease of the signal intensity between WT and mutant was not caused by a methodological artifact.

Reviewer #2 (Public Review):

Summary:

The authors first conducted whole exome sequencing for infertile male patients and families where they co-segregated the biallelic mutations in the Dynein Axonemal Heavy Chain 12 (DNAH12) gene.<br /> Sperm from patients with biallelic DNAH12 mutations exhibited a wide range of morphological abnormalities in both tails and heads, reminiscing a prevalent cause of male infertility, asthenoteratozoospermia. To deepen the mechanistic understanding of DNAH12 in axonemal assembly, the authors generated two distinct DNAH12 knockout mouse lines via CRISPR/Cas9, both of which showed more severe phenotypes than observed in patients. Ultrastructural observations and biochemical studies revealed the requirement of DNAH12 in recruiting other axonemal proteins and that the lack of DNAH12 leads to the aberrant stretching in the manchette structure as early as stage XI-XII. At last, the authors proposed intracytoplasmic sperm injection as a potential measure to rescue patients with DNAH12 mutations, where the knockout sperm culminated in the blastocyst formation with a comparable ratio to that in WT.

Strengths:

The authors convincingly showed the importance of DNAH12 in assembling cilia and flagella in both human and mouse sperm. This study is not a mere enumeration of the phenotypes, but a strong substantiation of DNAH12's essentiality in spermiogenesis, especially in axonemal assembly.

The analyses conducted include basic sperm characterizations (concentration, motility), detailed morphological observations in both testes and sperm (electron microscopy, immunostaining, histology), and biochemical studies (co-immunoprecipitation, mass-spec, computational prediction). Molecular characterizations employing knockout animals and recombinant proteins beautifully proved the interactions with other axonemal proteins.

Many proteins participate in properly organizing flagella, but the exact understanding of the coordination is still far from conclusive. The present study gives the starting point to untangle the direct relationships and order of manifestation of those players underpinning spermatogenesis. Furthermore, comparing flagella and trachea provides a unique perspective that attracts evolutional perspectives.

Weaknesses:

Seemingly minor, but the discrepancies found in patients and genetically modified animals were not fully explained. For example, both knockout mice vastly reduced the count of sperm in the epididymis and the motility, while phenotypes in patients were rather milder. Addressing the differences in the roles that the orthologs play in spermatogenesis would deepen the comprehensive understanding of axonemal assembly.

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors reveal a new role for SDG7 in the regulation of H3K36me2 and me3. SDG7 appear to be functionally redundant to SDG8 as the double mutant presents lower levels of H3K36me and stronger phenotypes than either single mutant, however, their mechanisms of action might differ as the proteins displayed different localization on their target genes, with SDG7 localizing preferentially to TSS and TES while SDG8 covers the gene body. SDG7 binds preferentially to PREs, which recruit PRC2 for H3K27me3 deposition. The authors therefore present an interesting model where SDG7 evicts PRC2 from silenced genes, leading to a loss of H3K27me3. This would allow the transcriptional activation of the genes and the deposition of H3K36me3.

Strengths:

Overall, the manuscript is well-written and organized, although some paragraphs need clarifications. The figures are clear and well designed and the proposed model is compelling. While the manuscript is already interesting as it is, I think addressing the following questions would elevate it even more and refine the proposed model:

Weaknesses/potential aspects to address:

(1) It is still unclear whether SDG7 directly catalyzes H3K36me or if it promotes its deposition simply by eviction of PRC2. The AlphaFold and structure analyses show a significant similarity between the catalytic domains which would support the first possibility, but some more experiments would be required to prove this more definitively.

(2) Does SDG7 directly recognize the PRE (as suggested by the model in Figure 5F) or is it recruited by some transcription factors? Is SDG7 known to interact with any of the PRC2 recruiters?

(3) Line154/Figure 2A: The metagene plot for H3K36me3 shows a lower level on the gene body but a higher peak in sdg7sdg8 double mutants compared to the Wild-type, which is a bit surprising, especially considering that the immunostaining in reference 19 showed a near complete loss of H3K36me3 signal in the same double mutant. Can this higher peak be an artifact from the normalization strategy, or due to the existence of different subpopulations of genes?

Indeed, on the genome tracks presented by the authors, the hypomethylated genes show a loss of signal on the entire gene body, and not a higher peak near the TSS. It might be interesting to generate metagene plots for H3K36me3 hypo and hyper-methylated genes, to see if the higher peak at the TSS is solely due to the hyper-methylated genes.

(4) Figure 2C: More than 40% of differentially methylated genes are actually hypermethylated, but the authors do not discuss this at all. What are those genes, are they targeted by SDG7 or 8? Could they be responsible for the higher peak at the TSS observed in the double mutant? (see previous comment).

(5) Figure 2C and D: The method section states that the ChIP-seq was performed on 5-day-old seedlings, while the legend of this figure mentions root and shoot samples but this does not appear in the figure itself. There is also mention of shoot and root samples in Supplementary Tables 1 and 2. The authors should clarify which tissue was used for the data presented in Figure 2 and correct the legends or the methods accordingly.

(6) Line 270/Fig 4K and L: The text mentions looking at the 838 genes "downregulated in clf sdg7 sdg8 relative to sdg7 sdg8" and in the overlap, the authors identified FLC. However, in Figure 5D, FLC is upregulated in clf sdg7-sdg8 compared to sdg7-sdg8, not downregulated as mentioned in line 270. The Venn diagram in Figure 4L mentions "sdg vs clf sdg up", which would fit the pattern seen in Figure 5D, but the number of genes (838) matches the number of downregulated genes in the sdg7sdg8 vs clf s dg7sdg8 volcano plot.

I would actually expect the phenotype rescue to be caused by genes that are up in Wt vs clf, down in Wt vs sdg7-sdg8, and back up in sdg7-sdg8 vs clf-sdg7-sdg8, not "up/down/down" as mentioned in the text: genes would be downregulated in sdg7-sdg8 because of a loss of H3K36me and therefore hypermethylation of H3K27, but in the absence of CLF, this hypermethylation is reversed and the genes are upregulated in the triple mutant compared to the sdg7-sdg8 mutant. This is also what the authors see and describe in their cluster analysis in Figure 4M and line 280, mentioning an upregulation in clf-sdg7-sdg8 vs sdg7-sdg8. Could the authors please clarify these discrepancies between the different subplots and within the text itself? Was there maybe some error plotting the volcano plot and/or Venn diagram?

In general, as this part is quite complicated, maybe it would benefit from a clearer explanation from the authors as to why they look at those particular overlaps, so that the reader can more easily follow their train of thought.

(7) Figure 4N/Line 286: How were these 828 genes identified? Is it stemming from a clf-sdg7-sdg8 vs sdg7-sdg8 comparison? The legend says "genes shown by white color in Fig. 4M", do the authors mean the two clusters previously described?

(8) Line 300: "suggesting that SDG8 primarily mediates target gene expression in conjunction with PAF1C". This statement is based on overlapping genes that are downregulated in sdg7-sdg8 double mutant and paf1c mutants but concludes only on the role of SDG8. I feel that to state that SDG8 regulates expression in conjunction with PAF1C, the authors should rather examine the genes downregulated in the sdg8 mutant, especially considering the reduced overlap between genes downregulated in sdg8 and sdg7-sdg8 (according to Figure 2C, only 30% of the genes downregulated in sdg8 are also downregulated in the double mutant), or this statement should be corrected to also include SDG7.

Maybe it would be easier to read the figure if the authors created a master list of genes downregulated in at least one of the paf1c mutants they examined (as they anyway do not examine in detail the contribution of each individual paf1c mutant), and overlap it with the genes downregulated in sdg7, sdg8 or sdg7-sdg8.

(9) Line 326: "We also discovered that SDG7 and SDG8 overcome PRC2-mediated silencing, leading to a switch from H3K27 methylation to H3K36 methylation during growth and development." While part of this statement is supported by the ChIP data presented in Figure 4E, I think a ChIP for H3K36me2 and/or me3 is necessary to prove the existence of a K27me to K36me switch.

(10) Line 347: The authors state that SDG8 is located at the TSS and 3' end of genes, but on line 187 they state that it occupies the gene body (which is supported by the plot in Figure 3A).

(11) Line 351: The authors suggest a role of RNApolII in the deposition of K36me, but their data are not sufficient to support this hypothesis. The transcriptome data show that both SDGs and PAF1C regulate a similar set of genes, but they do not show data demonstrating that RNApolII is necessary for the deposition of K36me. It might be interesting to examine H3K36me levels in a paf1c mutant to further consolidate their hypothesis.

Reviewer #2 (Public Review):

Summary:

In this manuscript, the authors combined imaging approaches with molecular and genetic experiments to

(i) for the first time establish a chromatin regulatory role for SDG7;<br /> (ii) examine its role in H3K36 methylation, along with its homolog SDG8;<br /> (iii) examine its potential role in mediating antagonism to PRC2, thereby mediating transcriptional activation.

Strengths:

The manuscript explores interesting and relevant mechanistic hypotheses about chromatin-mediated gene regulation by combining a range of experimental tools and a genome-wide perspective. The writing is very clear. The study makes good connections to existing data and generates datasets that complement existing datasets, providing a valuable resource to the community.

Weaknesses:

Some of the claims appear to need further supporting evidence to establish their robustness.

Review of the main conclusions and supporting evidence:

(1) SDG7 contributes to H3K36 methylation at several loci along with SDG8:<br /> This conclusion is supported by the genome-wide differences (measured by ChIP-seq) in H3K36me3 and me2 levels observed between WT, the sdg7 and sdg8 single mutants, and the double mutant. The reduction in H3K36 methylation levels observed at a large number of genes in the sdg7 mutant, and the further reduction in H3K36 methylation levels in the double mutant compared to sdg8 (observed at multiple genes) indicates that SDG7 promotes this transcription-associated modification. The significantly larger number of H3K36 hypomethylated genes in the double mutant (3380) compared to either of the single mutants (523 and 605) indicates lower overall H3K36me3 levels in the double mutant.<br /> While direct evidence of SDG7 methyltransferase activity on H3K36 is lacking, the study reports structural comparisons using AlphaFold predictions that suggest the possibility of such a role.

(2) SDG7 influences gene expression together with SDG8:<br /> This conclusion is supported by a range of phenotypic differences observed between sdg8 and the double mutant sdg7 sdg8. The reported genome-wide differential gene expression between the WT and the double mutant as well as expression differences in specific genes detected by imaging are also consistent with SDG7 and SDG8 together influencing gene expression. However, a role specifically for SDG7 could be further supported by a direct differential expression analysis between the single mutant sdg8 and the double mutant sdg7 sdg8. A role for SDG7 in gene expression is also consistent with its observed effect on H3K36 methylation, which is generally associated with productive transcription.

(3) SDG8 is exclusively nuclear, but SDG7 localises to the cytosol and the nucleus in meristematic cells:<br /> This conclusion is supported by imaging of fluorescent-tagged SDG8 and SDG7 in the root tip, which shows nuclear localisation of SDG8-GFP, consistent with previous reports, and a combination of nuclear and cytosolic localisation for SDG7-VENUS. However, the study presents only one replicate - more replicates are needed to establish the robustness of this conclusion.

(4) Distinct binding patterns of SDG7 and SDG8 on chromatin:<br /> This conclusion is supported by the analysis of genome-wide binding patterns of these proteins measured by ChIP-seq (using fluorescent tagged versions). This data indicates that while SDG7 tends to localise to TSS and TES regions of genes, SDG8 tends to be more uniformly spread across gene loci. These patterns suggest that SDG7 and SDG8 may influence H3K36 methylation through distinct mechanisms, but do not indicate what these mechanisms may be.

(5) SDG7/SDG8 antagonism with PRC2:<br /> a. SDG7 overlaps with PRC2 and its recruiters on chromatin and can bind to PREs<br /> This conclusion is supported by statistically significant overlaps genome-wide between cis-elements at SDG7 binding peaks and those previously reported to be Polycomb associated. This is further supported by the observation of SDG7 binding peaks close to PRC2 subunit binding peaks at known PRC2 targets.<br /> b. SDG7/SDG8 antagonism with PRC2<br /> This conclusion is supported by the observation that the sdg7 sdg8 double mutant phenotypes are partially rescued by disrupting CLF, one of the PRC2 methyltransferases. However, this does not necessarily suggest a direct antagonism with PRC2, but could be part of a more general antagonism between productive transcription (in which H3K36 methylation plays an active role), and PRC2-mediated silencing.<br /> c. SDG7 can evict PRC2 from PREs to overcome H3K27me3-mediated silencing<br /> This conclusion - that SDG7 directly antagonises PRC2 interaction with cis-elements that mediate its targeting - is partly supported by the observation that inducing overexpression of SDG7 (through dexamethasone induction) can cause changes in CLF occupancy and H3K27me3 levels at certain designated PREs. To establish the robustness of these conclusions, it will be necessary to examine designated regions to be used as a negative control and include a non-transgenic control for the SDG-7-HA ChIP. A suitable negative control may be a non-PRE region known to have a CLF peak and high H3K27me3 levels, where the levels would not be expected to change in this experiment.<br /> It remains to be established whether this apparent antagonism of PRC2 by SDG7 is only part of a more general antagonism of PRC2 by productive transcriptional activity, or whether SDG7 can evict PRC2 from PREs independent of transcripts and therefore is a precursor to switching to an active transcriptional state.<br /> Another aspect that would be interesting to examine in the light of recent findings is the single-cell-level behaviour at these genes targeted by SDG7-to examine whether SDG7 induction is causing individual copies of these genes to stochastically switch to an active transcriptional state so that the observed changes in H3K27me3 result from a fraction of copies completely losing silencing rather than all copies losing some H3K27me3.

(6) H3K36me3 levels are co-regulated by SDG8 and Paf1c, SDG8 associates with Pol II to deliver transcription-coupled H3K36 methylation<br /> This conclusion is supported by analysis of a subset of loci previously reported to be regulated by Paf1c, which also exhibit changes in the sdg7 sdg8 double mutant as well as a clf mutant. This analysis is based on a qualitative examination of ChIP-seq signal at a small number of loci, and therefore provides indirect support for this conclusion. It is, therefore, difficult to draw mechanistic insights from this analysis that go beyond correlation.

eLife assessment

The authors developed a method to allow a hypothermic agent, neurotensin, to cross the blood-brain barrier so it could potentially protect the brain from seizures and the adverse effects of seizures. The work is important because it is known that cooling the brain can protect it but developing a therapeutic approach based on that knowledge has not been done. The paper is well presented and the data are convincing. Revisions to clarify some of the methods and results, and to address effects on chronic seizures and tolerability would improve the paper.

Reviewer #1 (Public Review):

In this manuscript, Ferhat and colleagues describe their study aimed at developing a blood-brain barrier (BBB) penetrant agent that could induce hypothermia and provide neuroprotection from the sequelae of status epilepticus (SE) in mice. Hypothermia is used clinically in an attempt to reduce neurological sequelae of injury and disease. Hypothermia can be effective, but physical means used to reduce core body temperature are associated with untoward effects. Pharmacological means to induce hypothermia could be as effective with fewer untoward complications. Intracerebroventricularly applied neurotensin can cause hypothermia; however, neurotensin applied peripherally is degraded and does not cross the BBB. Here the authors develop and characterize a neurotensin conjugate that can reach the brain, induce hypothermia, and reduce seizures, cognitive changes, and inflammatory changes associated with status epilepticus.

Strengths:

(1) In general, the study is well-reasoned, well-designed, and seemingly well-executed.

(2) Strong dose-response assessment of multiple neurotensin conjugates in mice.

(3) Solid assessment of binding affinity, in vitro stability in blood, and brain uptake of the conjugate.

(4) Appropriate inclusion of controls for SE and for drug injections. However, perhaps a vehicle control could have been employed.

(5) Multifaceted assessment of neurodegeneration, inflammation, and mossy fiber sprouting in the different groups.

(6) Inclusion of behavioral assessments.

(7) Evaluates NSTR1 receptor distribution in multiple ways; however, does not evaluate changes in receptor distribution or ping wo/w SE and/or various drugs.

(8) Demonstrates that this conjugate can induce hypothermia and have positive effects on the sequelae of SE. Could have a great impact on the application of pharmacologically-induced hypothermia as a neuroprotective measure in patients.

Weaknesses:

(1) The authors make the claim, repeatedly, that the hypothermia caused by the neurotensin conjugate is responsible for the effects they see; however, what they really show is that the conjugate causes hypothermia AND has favorable effects on the sequelae of SE. They need to discuss that they did not administer the conjugate without allowing the pharmacological hypothermia (e.g., by warming the animal, etc.).

(2) In the status epilepticus studies, it is unclear how or whether they monitored animals for the development of spontaneous seizures. Can the authors please describe this?

(3) They do not evaluate changes in receptor distribution or ping wo/w SE and/or various drugs.

(4) It is not clear why several different mouse strains were employed.

Reviewer #2 (Public Review):

Summary:

The authors generated analogs consisting of modified neurotensin (NT) peptides capable of binding to low-density lipoprotein (LDL) and NT receptors. Their lead analog was further evaluated for additional validation as a novel therapeutic. The putative mechanism of action for NT in its antiseizure activity is hypothermia, and as therapeutic hypothermia has been demonstrated in epilepsy, NT analogs may confer antiseizure activity and avoid the negative effects of induced hypothermia.

Strengths:

The authors demonstrate an innovative approach, i.e. using LDLR as a means of transport into the brain, that may extend to other compounds. They systematically validate their approach and its potential through binding, brain penetration, in vivo antiseizure efficacy, and neuroprotection studies.

Weaknesses:

Tolerability studies are warranted, given the mechanism of action and the potential narrow therapeutic index. In vivo studies were used to assess the efficacy of the peptide conjugate analogs in the mouse KA model. However, it would be beneficial to have shown tolerability in naïve animals to better understand the therapeutic potential of this approach.

Mice may be particularly sensitive to hypothermia. It would be beneficial to show similar effects in a rat model.

eLife assessment

The authors develop a self-returning self-avoiding polymer model of chromosome organization and show that their framework can recapitulate at the same time local density and large-scale contact structural properties observed experimentally by various technologies. The presented theoretical framework and the results are valuable for the community of modelers working on 3D genomics. The work provides solid evidence that such a framework can be used, is reliable in describing chromatin organization at multiple scales, and could represent an interesting alternative to standard molecular dynamics simulations of chromatin polymer models.

Reviewer #1 (Public Review):

Carignano et al propose an extension of the self-returning random walk (SRRW) model for chromatin to include excluded volume aspects and use it to investigate generic local and global properties of the chromosome 3D organization inside eukaryotic nuclei. In particular, they focus on chromatin volumic density, contact probability and domain size and suggest that their framework can recapitulate several experimental observations and predict the effect of some perturbations.

Strengths:<br /> • The developed methodology is convincing and may offer an alternative - less computationally demanding - framework to investigate the single-cell and population structural properties of 3D genome organization at multiple scales.<br /> • Compared to the previous SRRW model, it allows for investigation of the role of excluded volume locally.<br /> • They perform some experiments to compare with model predictions and show consistency between the two.

Weaknesses:<br /> • The model currently cannot fully account for specific mechanisms that may shape the heterogeneous, complex organization of chromosomes (TAD at specific positions, A/B compartmentalization, promoter-enhancer loops, etc.).<br /> • By construction of their framework, excluded volume only impacts locally the polymer organization and larger-scale properties for which excluded volume could be a main actor (formation of chromosome territories [Rosa & Everaers, PLoS CB 2009], bottle-brush effects due to loop extrusion [Polovnikov et al, PRX 2023], etc.) cannot be captured.<br /> • Comparisons with experiments are solid but are not clearly quantified.

Impact:<br /> Building on the presented framework in the future to incorporate TAD and compartments may offer an interesting model to study the single-cell heterogeneity of chromatin organization. But currently, in this reviewer's opinion, standard polymer modeling frameworks may offer more possibilities.

Author response:

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

eLife assessment

The authors develop a self-returning self-avoiding polymer model of chromosome organization and show that their framework can recapitulate at the same time local density and large-scale contact structural properties observed experimentally by various technologies. The presented theoretical framework and the results are valuable for the community of modelers working on 3D genomics. The work provides solid evidence that such a framework can be used, is reliable in describing chromatin organization at multiple scales, and could represent an interesting alternative to standard molecular dynamics simulations of chromatin polymer models.

We appreciate the editor for an accurate description of the scope of the paper.

Public Reviews:

Reviewer #1 (Public Review):

Carignano et al propose an extension of the self-returning random walk (SRRW) model for chromatin to include excluded volume aspects and use it to investigate generic local and global properties of the chromosome 3D organization inside eukaryotic nuclei. In particular, they focus on chromatin volumic density, contact probability, and domain size and suggest that their framework can recapitulate several experimental observations and predict the effect of some perturbations.

We thanks the reviewer for the attention paid to the manuscript and all the relevant comments.

Strengths:

- The developed methodology is convincing and may offer an alternative - less computationally demanding - framework to investigate the single-cell and population structural properties of 3D genome organization at multiple scales.

- Compared to the previous SRRW model, it allows for investigation of the role of excluded volume locally.

Excluded volume is accounted for everywhere, not locally. We emphasized this on page 3, line 182:

“The method that we employ to remove overlaps is a low-temperature-controlled molecular dynamics simulation using a soft repulsive interaction potential between initially overlapping beads, that is terminated as soon as all overlaps have been resolved, as described in the Appendix 3.”


- They perform some experiments to compare with model predictions and show consistency between the two.

Weaknesses:

- The model is a homopolymer model and currently cannot fully account for specific mechanisms that may shape the heterogeneous, complex organization of chromosomes (TAD at specific positions, A/B compartmentalization, promoter-enhancer loops, etc.).

The SR-EV model is definitely not a homo-polymer, as it is not a regular concatenation of a single monomeric unit.

The model includes loops, which may happen in two ways: 1) As in the SRRW, branching structures emerging from the configuration backbone can be interpreted as nested loops and 2) A relatively long forward step followed by a return is a single loop. The model induces the formation of packing domains, which are not TADs, and are quantitatively in agreement with ChromSTEM experiments.

We consider convenient to add a new figure that will further clarify the structures obtained with the SR-EV model. The following paragraph and figure has been added in page 5:

“The density heterogeneity displayed by the SR-EV configurations can be analyzed in terms of the accessibility. One way to reveal this accessibility is by calculating the coordinations number (CN) for each nucleosome, using a coordination radius of 11.5 nm, along the SR-EV configuration. CN values range from 0 for an isolated nucleosome to 12 for a nucleosome immersed in a packing domain. In Figure 3 we show the SR-EV configuration showed in Figure 2, but colored according to CN. CN can be also considered as a measure to discriminate heterochromatin (red) and euchromatin (blue). Figure 3-A shows how the density inhomogeneity is coupled to different CN, with high CN represented in red and low CN represented in blue. Figure 3-B show a 50 nm thick slab obtained from the same configuration that clearly show the nucleosomes at the center of each packing domains are almost completely inaccesible, while those outside are open and accessible. It is also clear that the surface of the packing domains are characterized by nearly white nucleosomes, i.e. coordinated towards the center of the domain and open in the opposite direction.”

- By construction of their framework, the effect of excluded volume is only local and larger-scale properties for which excluded volume could be a main actor (formation of chromosome territories [Rosa & Everaers, PLoS CB 2009], bottle-brush effects due to loop extrusion [Polovnikov et al, PRX 2023], etc.) cannot be captured.

Excluded volume is considered for all nucleosomes, including overlapping beads distant along the polymer chain. Chromosome territories can be treated, but it is not in this case because we look at a single model chromosome.

- Apart from being a computationally interesting approach to generating realistic 3D chromosome organization, the method offers fewer possibilities than standard polymer models (eg, MD simulations) of chromatin (no dynamics, no specific mechanisms, etc.) with likely the same predictive power under the same hypotheses. In particular, authors often claim the superiority of their approach to describing the local chromatin compaction compared to previous polymer models without showing it or citing any relevant references that would show it.

We apologize if the text transmit an idea of superiority over other methods that was not intended. SR-EV is an alternative tool that may give a different, even complementary point of view, to standard polymer models.

- Comparisons with experiments are solid but are not quantified.

The comparisons that we have presented are quantitative. We do not have so far a way to characterize alpha or phi, a priori, for a particular system.

Impact:

Building on the presented framework in the future to incorporate TAD and compartments may offer an interesting model to study the single-cell heterogeneity of chromatin organization. But currently, in this reviewer's opinion, standard polymer modeling frameworks may offer more possibilities.

We thank the reviewer for the positive opinion on the potential of the presented method. The incorporation of TADs and compartments is left for a future evolution of the model as its complexity will make this work extremely long.

Reviewer #2 (Public Review):

Summary:

The authors introduce a simple Self Returning Excluded Volume (SR-EV) model to investigate the 3D organization of chromatin. This is a random walk with a probability to self-return accounting for the excluded volume effects. The authors use this method to study the statistical properties of chromatin organization in 3D. They compute contact probabilities, 3D distances, and packing properties of chromatin and compare them with a set of experimental data.

We thank the reviewer for the attention paid to our manuscript.

Strengths:

(1) Typically, to generate a polymer with excluded volume interactions, one needs to run long simulations with computationally expensive repulsive potentials like the WeeksChanlder-Anderson potential. However, here, instead of performing long simulations, the authors have devised a method where they can grow polymer, enabling quick generation of configurations.

(2) Authors show that the chromatin configurations generated from their models do satisfy many of the experimentally known statistical properties of chromatin. Contact probability scalings and packing properties are comparable with Chromatin Scanning Transmission Electron Microscopy (ChromSTEM)  experimental data from some of the cell types.

Weaknesses:

This can only generate broad statistical distributions. This method cannot generate sequence-dependent effects, specific TAD structures, or compartments without a prior model for the folding parameter alpha. It cannot generate a 3D distance between specific sets of genes. This is an interesting soft-matter physics study. However, the output is only as good as the alpha value one provides as input.

We proposed a model to create realistic chromatin configuration that we have contrasted with specific single cell experiments, and also reproducing ensemble average properties. 3D distances between genes can be calculated after mapping the genome to the SR-EV configuration. The future incorporation of the genome sequence will also allow us to describe TADs and A/B compartments. See added paragraph in the Discussion section:

“The incorporation of genomic character to the SR-EV model will allow us to study all individual single chromosomes properties, and also topological associated domains and A/B compartmentalization from ensemble of configurations as in HiC experiments. “

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major:

- In the introduction and along the text, the authors are often making strong criticisms of previous works (mostly polymer simulation-based) to emphasize the need for an alternative approach or to emphasize the outcomes of their model. Most of these statements (see below) are incomplete if not wrong. I would suggest tuning down or completely removing them unless they are explicitly demonstrated (eg, by explicit quantitative comparisons). There is no need to claim any - fake - superiority over other approaches to demonstrate the usefulness of an approach. Complementarity or redundance in the approaches could also be beneficial.

We regret if we unintentionally transmitted a claim of superiority. We have made several small edits to change that.

- Line 42-43: at least there exist many works towards that direction (including polymer modeling, but also statistical modeling). For eg, see the recent review of Franck Alber.

Line removed. Citation to Franck Alber included below in the text.

- Line 54-57: Point 1 is correct but is it a fair limitation? These models can predict TADs & compartments while SR-EV no. Point 2 is wrong, it depends on the resolution of the model and computer capacity but it is not an intrinsic limitation. Point 3 is wrong, such models can predict very well single-cell properties, and again it is not an intrinsic limitation of the model. Point 4 is incorrect. The space-filling/fractal organization was an (unfortunate) picture to emphasize the typical organization of chromosomes in the early times (2009), but crumpled polymers which are a more realistic description are not space-filling (see Halverson et al, 2013).

Text involving points 1 to 4 removed. It was unnecessary and does not change the line of the paper.

- L400-402 + 409-411: in such a model, the biphasic structure may emerge from loop extrusion but also naturally from the crumpled polymer organization. Simple crumpled polymer without loop extrusion and phase separation would also produce biphasic structures.

Yes, we agree. Also SR-EV leads to biphasic structures.

- L 448-449: any data to show that existing polymer modeling would predict a strong dependency of C_p(n) on the volumic fraction (in the range studied here)?

No, I don’t know a work predicting that.

- Fig. 4:

- Large-scale structural properties (R^2(n) and C_p(n)) are not dependent on phi. Is it surprising that by construction, SR-EV only relaxes the system locally after SRRW application?

Excluded volume is considered at all length scales. However, as the decreasing C_p curves observed in theories and experiments imply, the fraction of overlap (or contacts) is more important at small separations (local) than at large separations. Yet, it was a surprise for us to observed negligible effect on phi.

- Why not make a quantitative comparison between predicted and measured C_p(n)? Or at least plotting them on the same panel.

Panels B and C are in the same scale and show a good agreement between SR-EV and experiments. However, it is not perfectly quantitative agreement. SR-EV represents the generic structure of chromatin and perfect agreement should not be expected.

- Comparison with an average C_p(n) over all the chromosomes would be better.

Possibly, but we don’t think it adds anything to the paper.

- In Figure 5,6,7 (and related text): authors often describe some parameter values that are 'closest to experiment findings'. Can the authors quantify/justify this? The various 'closest' parameters are different. Can the authors comment?

The folding parameter and average volume fraction are chose so that the agreement is best with the displayed experimental system, different cell for each case.

- Figure 5: why not show the experimental distribution from Ou et al?

- Figure 6 & 7: experimental results. Can the authors show images from their own experiments? Can they show that cohesion/RAD21 is really depleted after auxin treatment?

It is currently under review in a different journal.

- In the Discussion, a fair discussion on the limitations of the methods (dynamics, etc) is missing.

Minor

- Line 34-36: the logical relationship between this sentence and the ones before and after is very unclear.

- Along the text, authors use the term 'connectivity' to describe 3D (Hi-C) contacts between different regions of the same chromosome/polymer. This is misleading as connectivity in polymer physics describes the connection along the polymer and not in the 3D space.

No. I don’t think we used connectivity in that sense. We agree with your statement on the use of connectivity in polymer physics, and is what we always had in mind for this model.

- Line 92: typo.

- On the SR-EV method: does the relaxation process create local knots in the structure?

We have not checked for knots.

- Table 1: the good correspondence with linker length is remarkable but likely 'fortunate', other chosen resolutions would have led to other results. Moreover, the model cannot account for the fine structure of chromatin fiber. Can the authors comment on that?

Fortunate to the extent that we sample the model parameter to overall catch the structure of chromatin.

- Line 211: 'without the need of imposing any parameter': alpha is a parameter, no?

Correct. Phrase deleted.

- L267-269 & 450-451: actually in Liu & Dekker, they do observe an effect on Hi-C map (C_p(n)), weak but significant and not negligible.

Our statements read ‘minimal’ and ‘relatively insensitive’. It is observed, but very small.

- L283-286: This is a perspective statement that should be in the discussion.

Moved to the Discussion, as suggested.

- L239-241: The authors seem to emphasize some contradictions with recent results on phase separation. This is unclear and should be relocated to discussion.

We just pointed out recent experiments, as stated. No intention to generate a discussion with any of them.

- L311-313: Unclear statement.

- L316-325: This is not results but discussion/speculation.

Moved to Discussion

- Along the text: 'promotor'-> 'promoter'. 

- Corrected.

- L364: explain more in detail PWS microscopy.

Reviewer #2 (Recommendations For The Authors):

Even though there are claims about nucleosome-resolution chromatin polymer, it is not clear that this work can generate structures with known nucleosome-resolution features. Nucleosome-level structure is much beyond a random walk with excluded volume and is driven by specific interactions. The authors should clarify this.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Yang, Hu et al. examined the molecular mechanisms underlying astrocyte activation and its implications for multiple sclerosis. This study shows that the glycolytic enzyme PKM2 relocates to astrocyte nuclei upon activation in EAE mice. Inhibiting PKM2's nuclear import reduces astrocyte activation, as evidenced by decreased proliferation, glycolysis, and inflammatory cytokine release. Crucially, the study identifies TRIM21 as pivotal in regulating PKM2 nuclear import via ubiquitination. TRIM21 interacts with PKM2, promoting its nuclear translocation and enhancing its activity, affecting multiple signaling pathways. Confirmatory analyses using single-cell RNA sequencing and immunofluorescence demonstrate TRIM21 upregulation in EAE astrocytes. Modulating TRIM21 expression in primary astrocytes impacts PKM2-dependent glycolysis and proliferation. In vivo experiments targeting this mechanism effectively mitigate disease severity, CNS inflammation, and demyelination in EAE.

The authors supported their claims with various experimental approaches, however, some results should be supported with higher-quality images clearly depicting the conclusions and additional quantitative analyses of Western blots.

Thanks for the reviewer’s comments. We agree with the reviewer and have added higher magnification images, for example Fig.2A to better visualize the localization of PKM2 in DASA-treated conditions, and Fig. 3A and Fig.3B to better visualize the pSTAT3 and pp65. Moreover, we have added quantitative analyses of Western blots for some key experiments, for example quantitative results for Fig.2D is added in Fig.S3 to show the change of PKM2 and p-c-myc in DASA-58-treated conditions and quantitative results for Fig. 3D are added in Fig.S4B and S4C to show the change of nuclear and cytoplasmic PKM2, STAT3 and NF-κB in different conditions.

Strength:

This study presents a comprehensive investigation into the function and molecular mechanism of metabolic reprogramming in the activation of astrocytes, a critical aspect of various neurological diseases, especially multiple sclerosis. The study uses the EAE mouse model, which closely resembles MS. This makes the results relevant and potentially translational. The research clarifies how TRIM21 regulates the nuclear import of PKM2 through ubiquitination by integrating advanced techniques. Targeting this axis may have therapeutic benefits since lentiviral vector-mediated knockdown of TRIM21 in vivo significantly reduces disease severity, CNS inflammation, and demyelination in EAE animals.

We thank the reviewer for their positive and constructive comments on the manuscript.

Weaknesses:

The authors reported that PKM2 levels are elevated in the nucleus of astrocytes at different EAE phases compared to cytoplasmic localization. However, Figure 1 also shows elevated cytoplasmic expression of PKM2. The authors should clarify the nuclear localization of PKM2 by providing zoomed-in images. An explanation for the increased cytoplasmic PKM2 expression should provided. Similarly, while PKM2 translocation is inhibited by DASA-58, in addition to its nuclear localization, a decrease in the cytoplasmic localization of PKM2 is also observed. This situation brings to mind the possibility of a degradation mechanism being involved when its nuclear translocation of PKM2 is inhibited.

According to the results of immunofluorescence staining of PKM2 in spinal cord of EAE mice and in cultured primary astrocytes, in addition to the observation of PKM2 nuclear translocation in EAE conditions, we showed an elevated expression of PKM2 in astrocytes, including the cytoplasmic and nuclear expression. In neurological diseases, various studies showed consistent results, for example, following spinal cord injury (SCI), not only the upregulated expressing of PKM2 but also nuclear translocation was observed in astrocytes (Zhang et al., 2015). In EAE conditions, CNS inflammation is elevated and several proinflammatory cytokines and chemokines might contribute to the upregulated expression of PKM2 in astrocytes. We have tested TNFα and IL-1β, which are recognized to play important roles in EAE and MS (Lin and Edelson, 2017, Wheeler et al., 2020), and results from western blots showed the increased expression of PKM2 upon stimulation with TNFα and IL-1β (Author response image 1). Moreover, according to the reviewer’s suggestions, we have added zoomed-in images for figure 2A.

Additionally, the reviewer has noted the decrease in the cytoplasmic PKM2 level, degradation-related mechanism and other mechanisms might be involved in this process.

Author response image 1.

Upregulated expression of PKM2 in astrocytes following stimulation with TNF-α and IL-1β. Primary astrocytes were stimulated with TNF-α and IL-1β (50 ng/mL) for 48 h and western blotting analysis were performed.

In Figure 3D, the authors claim that PKM2 expression causes nuclear retention of STAT3, p65, and p50, and inhibiting PKM2 localization with DASA-58 suppresses this retention. The western blot results for the MOG-stimulated group show high levels of STAT3, p50, and p65 in nuclear localization. However, in the MOG and DASA-58 treated group, one would expect high levels of p50, p65, and STAT3 proteins in the cytoplasm, while their levels decrease in the nucleus. These western blot results could be expanded. Additionally, intensity quantification for these results would be beneficial to see the statistical difference in their expressions, especially to observe the nuclear localization of PKM2.

We agree with the reviewer’s comments and we have incorporated the quantification of STAT3，p50 and p65 for Fig.3D and Fig.S4B and Fig.S4C. Nevertheless, given that DASA-58 did not trigger a notable increase in the cytoplasmic level of PKM2, we did not detect an upregulation of STAT3, p50, or p65 in the cytoplasm of the MOG and DASA-58-treated groups. With the quantification results, it is more obvious to see the changes of these proteins in different conditions.

The discrepancy between Figure 7A and its explaining text is confusing. The expectation from the knocking down of TRIM21 is the amelioration of activated astrocytes, leading to a decrease in inflammation and the disease state. The presented results support these expectations, while the images showing demyelination in EAE animals are not highly supportive. Clearly labeling demyelinated areas would enhance readers' understanding of the important impact of TRIM21 knockdown on reducing the disease severity.

Thank you for pointing this out. We sincerely apologize for our carelessness. Based on your comments, we have made the corrections in the manuscript. As there is indeed a statistical difference in the mean clinical scores between shTRIM21-treated group and shVec group, we have accordingly revised the sentence for Figure 7A to state, “At the end time point at day 22 p.i., shTRIM21-treated group showed reduced disease scores compared to control groups (Fig. 7A).” .

Additionally, we have added the whole image of the spinal cord for MBP in Author Response image 2. Moreover, we have labelled the demyelinated areas to facilitate readers’ understanding.

Author response image 2.

MBP staining of the whole spinal cord in EAE mice from shVec and shTRIM21 group. Scale bar: 100 μm. Demyelinated areas are marked with dashed lines.

Reviewer #2 (Public Review):

This study significantly advances our understanding of the metabolic reprogramming underlying astrocyte activation in neurological diseases such as multiple sclerosis. By employing an experimental autoimmune encephalomyelitis (EAE) mouse model, the authors discovered a notable nuclear translocation of PKM2, a key enzyme in glycolysis, within astrocytes.

Preventing this nuclear import via DASA 58 substantially attenuated primary astrocyte activation, characterized by reduced proliferation, glycolysis, and inflammatory cytokine secretion.<br /> Moreover, the authors uncovered a novel regulatory mechanism involving the ubiquitin ligase TRIM21, which mediates PKM2 nuclear import. TRIM21 interaction with PKM2 facilitated its nuclear translocation, enhancing its activity in phosphorylating STAT3, NFκB, and c-myc. Single-cell RNA sequencing and immunofluorescence staining further supported the upregulation of TRIM21 expression in astrocytes during EAE.

Manipulating this pathway, either through TRIM21 overexpression in primary astrocytes or knockdown of TRIM21 in vivo, had profound effects on disease severity, CNS inflammation, and demyelination in EAE mice. This comprehensive study provides invaluable insights into the pathological role of nuclear PKM2 and the ubiquitination-mediated regulatory mechanism driving astrocyte activation.

The author's use of diverse techniques, including single-cell RNA sequencing, immunofluorescence staining, and lentiviral vector knockdown, underscores the robustness of their findings and interpretations. Ultimately, targeting this PKM2-TRIM21 axis emerges as a promising therapeutic strategy for neurological diseases involving astrocyte dysfunction.

While the strengths of this piece of work are undeniable, some concerns could be addressed to refine its impact and clarity further; as outlined in the recommendations for the authors.

Thanks for the reviewer’s comment and positive evaluation of our present work. We have further answered each question in recommendations section.

Reviewer #3 (Public Review):

Summary:

Pyruvate kinase M2 (PKM2) is a rate-limiting enzyme in glycolysis and its translocation to the nucleus in astrocytes in various nervous system pathologies has been associated with a metabolic switch to glycolysis which is a sign of reactive astrogliosis. The authors investigated whether this occurs in experimental autoimmune encephalomyelitis (EAA), an animal model of multiple sclerosis (MS). They show that in EAA, PKM2 is ubiquitinated by TRIM21 and transferred to the nucleus in astrocytes. Inhibition of TRIM21-PKM2 axis efficiently blocks reactive gliosis and partially alleviates symptoms of EAA. Authors conclude that this axis can be a potential new therapeutic target in the treatment of MS.

Strengths:

The study is well-designed, controls are appropriate and a comprehensive battery of experiments has been successfully performed. Results of in vitro assays, single-cell RNA sequencing, immunoprecipitation, RNA interference, molecular docking, and in vivo modeling etc. complement and support each other.

Weaknesses:

Though EAA is a valid model of MS, a proposed new therapeutic strategy based on this study needs to have support from human studies.

We agree that although we have clarified the therapeutic potential of targeting TRIM21 or PKM2 in the treatment of EAE, a mouse model of MS, the application in human studies warrants further studies. While considering the use of TRIM21 as a target for treating multiple sclerosis in clinical trials, several issues need to be addressed to ensure the safety, efficacy and feasibility. One such aspect is the development of drug that specifically target TRIM21 in brain, capable of crossing the blood-brain barrier and have minimal off-target effects. The translation of preclinical finding into clinical trials poses a significant challenge. To provide evidence for the similarities between the EAE model and multiple sclerosis, we have screened GEO databases (Author response image 3). In GSE214334 which analyzed transcriptional profiles of normal-appearing white matter from non-MS and different subtypes of disease (RRMS, SPMS and PPMS). Although no statistical difference was observed among different groups, the TRIM21 expression has tendency to increase in SPMS (secondary progressive MS) and PPMS (primary progressive MS) patients. In GSE83670, astrocytes from 3 control white matter and 4 multiple sclerosis normal appearing white matter (NAWM) were analyzed. TRIM21 mRNA expression is higher in MS group (78.73 ± 10.44) compared to control group (46.67 ± 24.15). Although these two GEO databases did not yield statistically significant differences, TRIM21 expression appears to be elevated in the white matter of MS patients compared to controls.

To address this limitation, we have incorporated the following statement in the discussion section: “However, whether TRIM21-PKM2 could potentially serve as therapeutic targets in multiple sclerosis warrants further studies.”

Author response image 3.

TRIM21 expression in control and MS patients based on published GEO database. (A) The expression of TRIM21 in normal-appearing white matter in non-MS (Ctl) and different clinical subtypes of MS (RRMS, SPMS, PPMS) based on GSE214334 (one-way ANOVA). (B) The expression of TRIM21 from multiple sclerosis normal appearing white matter (NAWM) and control WM based on GSE83670. RRMS, relapsing--remitting MS; SPMS, secondary progressive MS; PPMS, primary progressive MS (unpaired Student's t test). Data are represented as the means ± SEM.

Reviewer #4 (Public Review):

Summary:

The authors report the role of the Pyruvate Kinase M2 (PKM2) enzyme nuclear translocation as fundamental in the activation of astrocytes in a model of autoimmune encephalitis (EAE). They show that astrocytes, activated through culturing in EAE splenocytes medium, increase their nuclear PKM2 with consequent activation of NFkB and STAT3 pathways. Prevention of PKM2 nuclear translocation decreases astrocyte counteracts this activation. The authors found that the E3 ubiquitin ligase TRIM21 interacts with PKM2 and promotes its nuclear translocation. In vivo, either silencing of TRIM21 or inhibition of PKM2 nuclear translocation ameliorates the severity of the disease in the EAE model.

Strengths:

This work contributes to the knowledge of the complex action of the PKM2 enzyme in the context of an autoimmune-neurological disease, highlighting its nuclear role and a novel partner, TRIM21, and thus adding a novel rationale for therapeutic targeting.

Weaknesses:

Despite the relevance of the work and its goals, some of the conclusions drawn would require more thorough proof:

I believe that the major weakness is the fact that TRIM21 is known to have per se many roles in autoimmune and immune pathways and some of the effects observed might be due to a PKM2-independent action. Some of the experiments to link the two proteins, besides their interaction, do not completely clarify the issue. On top of that, the in vivo experiments address the role of TRIM21 and the nuclear localisation of PKM2 independently, thus leaving the matter unsolved.

We agree that TRIM21 has multifunctional roles and only some of their effects are due to PKM2-independent action. It is obvious that TRIM21 functions as ubiquitin ligases and its substrate are various. Here we identify PKM2 as one of its interacting proteins and our focus is the relationship between TRIM21 and the nuclear translocation PKM2, we have used diverse experiments to clarify their relationships, for example immunoprecipitation, western blotting, immunofluorescence, cyto-nuclear protein extraction. These aforementioned experiments are key points of our studies. From the results of in vitro experiments, targeting either TRIM21 or PKM2 might be potential targets for EAE treatment. Expectedly, from in vivo experiments, either targeting TRIM21 or PKM2 nuclear transport ameliorated EAE. In order to test the relationship of TRIM21 and PKM2 nuclear transport in vivo, we have stained PKM2 in shVec and shTRIM21-treated mice. Expectedly, knocking down TRIM21 led to a decrease in the nuclear staining of PKM2 in spinal cord astrocytes in EAE models (Figure S7A). This observation underscores that the therapeutic potential of inhibiting TRIM21 in astrocytes in vivo might be partially due to its role in triggering the reduced nuclear translocation of PKM2.

Some experimental settings are not described to a level that is necessary to fully understand the data, especially for a non-expert audience: e.g. the EAE model and MOG treatment; action and reference of the different nuclear import inhibitors; use of splenocyte culture medium and the possible effect of non-EAE splenocytes.

According to the reviewer’s suggestions, we have added more detailed descriptions in the materials and methods section, for example, the use of splenocytes culture medium, mass spectrometry, HE and LFB staining have been added. More details are incorporated in the part for “EAE induction and isolation and culture of primary astrocytes”. Moreover, the reference of DASA-58 in vitro and TEPP-46 in vivo as inhibitors of PKM2 nuclear transport were added.

The statement that PKM2 is a substrate of TRIM21 ubiquitin ligase activity is an overinterpretation. There is no evidence that this interaction results in ubiquitin modification of PKM2; the ubiquitination experiment is minimal and is not performed in conditions that would allow us to see ubiquitination of PKM2 (e.g. denaturing conditions, reciprocal pull-down, catalytically inactive TRIM21, etc.).

To prevent the misunderstanding, we have revised certain statements in the manuscript. In the updated version, the description is as follows: Hereby, we recognized PKM2 as an interacting protein of TRIM21, and further studies are required to determine if it is a substrate of E3 ligase TRIM21.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

General recommendations:

- The whole manuscript needs language editing.

We appreciate the comments of the reviewers. We have improved the writing of the manuscript. All modifications are underlined.

- Details of many experiments are not given in the materials and methods.

According to the reviewer’s suggestions, we have added more details for experiments in the materials and methods. For example, “Splenocyte isolation and supernatant of MOG35-55-stimulated-splenocytes”, “mass spectrometry”, “Hematoxylin-Eosin (HE) and Luxol Fast Blue (LFB) staining” were added in the section of Materials and Methods. More detailed information is given for EAE induction and isolation and culture of primary astrocytes.

- Line properties in graphics should be corrected, some lines in box plots and error bars are very weak and hardly visible. Statistical tests should be included in figure legends as well. Statistical differences should be mentioned for control vs DASA-58 (alone) in all related figures.

We have revised the figures to enhance their visibility by thickening the lines and error bars. In accordance with the reviewer’s suggestions, we have incorporated statistical tests in figure legends. Moreover, statistical analysis has been made among all groups, if there is no asterisk indicated in the figure legend and figure panels, it means there is no statistical difference between the control vs DASA-58 groups. For most of the experiments conducted in our studies, including lactate production, glucose consumption, the EdU analysis and CCK8 analysis, the change of STAT3 and NF-κB pathways, no statistical difference was observed between the control and DASA-58 group. The reason might be due to that in unstimulated astrocytes, the expression of PKM2 is low and nuclear translocation of PKM2 are few, which may explain why DASA-58 did not exert the anticipated effect. Thus, in our experiments, we have used MOGsup to stimulate astrocytes, enabling us to observe the impact of DASA-58 on the astrocyte proliferation and glycolysis in this condition.

- Scale bars, arrows, and labeling in the images are not visible.

We have improved the images according to the reviewer’s suggestions. The scale bars, arrows are made thicker and labeling are larger. The updated figures are visible.

- Quantitative analysis of all western blot results and their statistics could be provided in every image and for every protein.

For western blotting results which are further processed with quantitative analysis, for example, Fig.2D, fig. 5G, Fig. 6A and 6B, Fig. S4, we have added their statistics in the raw data sections. The other western blot results, for example, IP analysis, which are used to analyze protein-protein binding are not further processed with quantitative analysis.

- Proteins that are used for normalizations in western blots should be stated in the text.

We have added description of proteins that are used for normalization in western blots in figure legends. Moreover, in figure panels, proteins used for normalization are indicated. Globally, whole protein level is normalized to protein level of β-actin. For nuclear and cytoplasmic proteins, nuclear protein is normalized to the expression of lamin, cytoplasmic protein is normalized to the expression of tubulin. 

- The manuscript investigates the role of TRIM21 in the nuclear localization of PKM2 in astrocytes in EAE mice, however almost no information is given about TRIM21 in the introduction. Extra information is given for PKM2, yet can be concisely explained.

We have added a paragraph that describes the information of TRIM21 in the introduction section. The description is as follows: “TRIM21 belongs to the TRIM protein family which possess the E3 ubiquitin ligase activity. In addition to its well-recognized function in antiviral responses, emerging evidences have documented the multifaceted role of TRIM21 in cell cycle regulation, inflammation and metabolism (Chen et al., 2022). Nevertheless, the precise mechanisms underlying the involvement of TRIM21 in CNS diseases remain largely unexplored.”

- "As such, deciphering glycolysis-dominant metabolic switch in astrocytes is the basis for understanding astrogliosis and the development of neurological diseases such as multiple sclerosis." The sentence could be supported by references.

To support this sentence, we have added the following references:

(1) Xiong XY, Tang Y, Yang QW. Metabolic changes favor the activity and heterogeneity of reactive astrocytes. Trends in endocrinology and metabolism: TEM 2022;33(6):390-400.

(2) das Neves SP, Sousa JC, Magalhães R, Gao F, Coppola G, Mériaux S, et al. Astrocytes Undergo Metabolic Reprogramming in the Multiple Sclerosis Animal Model. Cells 2023;12(20):2484.

Figure 1/Result 1:

- Figure 1A-B: Quality of the images should be improved.

According to the reviewer’s suggestion, we have improved the quality of the image, images with higher resolution were added in figure 1A and figure 1B.

- Control images of Figure 1B are not satisfying. GFAP staining is very dim. Images from control cells should be renewed.

As mentioned by the reviewer’s, we have renewed the control images and added the DAPI staining figures for all groups. Compared with MOGsup stimulated astrocytes, the control cells are not in activated state and GFAP are relatively low.

- Labelings on the images are not sufficient, arrows and scale bars are not visible.

We have improved the images including labels, arrows and scale bars in all figures.

- How splenocytes were obtained from MOG induced mice were not given in the material and methods section. Thus, it should be clearly stated how splenocyte supernatant is generated (treatment details).

We have added the detailed information relating to splenocyte isolation and splenocyte supernatant entitled “Splenocyte isolation and supernatant of MOG35-55-stimulated-splenocytes” in the section of Materials and methods. “Splenocytes were isolated from EAE mice 15 d (disease onset) after MOG35-55 immunization. Briefly, spleen cells were suspended in RPMI-1640 medium containing 10% FBS. Splenocytes were plated in 12-well plates at 1x106 cells/well containing 50 μg/mL MOG35-55 and cultured at 37°C in 5% CO2. After stimulation for 60 h, cell suspension was centrifuged at 3000 rpm for 5 min and supernatants were collected. For the culture of MOGsup-stimulated astrocytes, astrocytes were grown in medium containing 70% DMEM supplemented with 10% FBS and 30% supernatant from MOG35-55-stimulated-splenocytes.”

- For general astrocyte morphology: authors showed the cells are GFAP+ astrocytes. It is surprising that these cells do not bear classical astrocyte morphology in cell culture. How long do you culture astrocytes before treatment? How do you explain their morphological difference?

Astrocytes were cultured for 2 to 3 weeks which correspond to 2-3 passages before treatment. There are several possible reasons for the morphological differences observed between GFAP+ astrocytes and their classical morphology. Firstly, the cell density. In low-density culture just as shown in Figure 1B, we have observed that astrocytes adopt a more flattened morphology. In high-density cultures, they adopt a stellate shape. Moreover, variations in culture conditions, such as the use of different fetal bovine serum, can also influence the morphology of astrocytes. In addition, the mechanical injury induced by the isolation procedures for astrocytes might contribute to variations in their morphology during in vitro cultivation. In summary, the morphological differences observed in GFAP+ astrocytes in cell culture likely result from a combination of culture conditions, cell density, and mechanical injury occured during astrocyte isolation etc.

- Additional verification of reactive astrocytes could be performed by different reactive astrocyte markers, such as GLAST, Sox9, S100ß. Thus, quantitative analysis of activated astrocytes can be done by counting DAPI vs GLAST, Sox9 or S100ß positive cells.

We really agree with the reviewer that there are other markers of reactive astrocytes such as GLAST, sox9 and S100β. However, numerous evidences support that GFAP is the most commonly used reactive astrocyte markers. Most of the cases, reactive astrocytes undergo GFAP overexpression. GFAP is one the most consistently induced gene in transcriptomic datasets of reactive astrocytes, confirming its usefulness as a reactive marker (Escartin et al., 2019). Thus, we have used GFAP as the marker of astrocyte activation in our study.

- How you performed quantifications for Figures 1C and 1D should be clearly explained, details are not given.

Quantification for Figure 1C and 1D were added in the figure legend. In general, Mean fluorescence intensity of PKM2 in different groups of (B) was calculated by ImageJ. The number of nuclear PKM2 was quantified by Image-Pro Plus software manually (eg. nuclear or cytoplasmic based on DAPI blue staining). The proportion of nuclear P KM2 is determined by normalizing the count of nuclear PKM2 to the count of nuclear DAPI, which represents the number of cell nuclei.

- "Together, these data demonstrated the nuclear translocation of PKM2 in astrocytes from EAE mice." Here the usage of "suggests" instead of "demonstrated".

Based on the reviewer's suggestion, we have revised the use of "demonstrated" to "suggest" in this sentence.

Result 2 and 3:

- In the literature, DASA-58 is shown to be the activator of PKM2 (https://www.nature.com/articles/nchembio.1060, https://doi.org/10.1016/j.cmet.2019.10.015).

- Providing references for the inhibitory use of DASA-58 for PKM2 would be appreciated.

DASA-58 is referred to as “PKM2 activator” due to its ability to enforce the tetramerization of PKM2, enhancing the enzymatic ability of PKM2 to catalyze PEP to pyruvate conversion. However, the enforced conversion of tetramerization of PKM2 inhibited the dimer form of PKM2, thereby inhibiting its nuclear translocation. For this reason, DASA-58 is also used as the inhibitor of nuclear translocation of PKM2. In primary BMDMs, LPS induced nuclear PKM2. However, driving PKM2 into tetramers using DASA-58 and TEPP-46 inhibited LPS-induced PKM2 nuclear translocation (Palsson-McDermott et al., 2015). Consistently, FSTL1 induced PKM2 nuclear translocation was inhibited by DASA-58 in BMDMs (Rao et al., 2022). Accordingly, we have added these references in the manuscript.

- Western blot results and statistics for PKM2 should be quantitatively given for all groups.

According to the reviewer’s suggestions, we have added the quantification of PKM2 for western blots in figure 2 and figure 3. Quantification of PKM2 in figure 2D is added in Fig S3. Quantification of PKM2 in figure 3D is added in Fig.S4B and Fig. S4C.

- Figure 3A-B: staining method/details are not mentioned in materials and methods.

Staining methods is in the paragraph entitled “Immunofluorescence” in the section of materials and methods. The descriptions are as follows:

For cell immunochemistry, cells cultured on glass coverslips were fixed with 4% PFA for 10 min at RT, followed by permeabilization with 0.3% Triton X-100. Non-specific binding was blocked with buffer containing 3% BSA for 30 min at RT. Briefly, samples were then incubated with primary antibodies and secondary antibodies. DAPI was used to stain the nuclei. Tissues and cells were observed and images were acquired using an EVOS FL Auto 2 Cell image system (Invitrogen). The fluorescence intensity was measured by ImageJ.

- In Figure 3A, in only DASA-58 treated cells, it looks like GFAP staining is decreased. It would be better to include MFI analysis for GFAP in the supplementary information.

We have added the MFI analysis for GFAP in Figure 3A in Fig.S4A. GFAP expression is decreased after DASA-58 treatment (in both control and MOGsup condition), the reason might be due to the effect of DASA-58 on inhibition of PKM2 nuclear transport, which subsequently suppress the activation of astrocytes, leading to the decreased expression of GFAP.

Result 4

- Detailed explanation of the mass spectrometry and IP experiments should be given in materials and methods. What are the conditions of the cells? Which groups were analyzed? Are they only MOG stimulated, MOG-DASA-58 treated, or only primary astrocytes without any treatment? The results should be interpreted according to the experimental group that has been analyzed.

We have added the detailed information relating to mass spectrometry and immunoprecipitation in the materials and methods. In general, two groups of cells were subjected to mass spectrometry analysis, primary astrocytes without any treatment and MOGsup-stimulated primary astrocytes. These two groups were immunoprecipitated with anti-PKM2 antibody. Moreover, in the manuscript, we have revised the sentence concerning the description of mass spectrometry. The description is as follows: “To illustrate underlying mechanism accounting for nuclear translocation of PKM2 in astrocytes, we sought to identify PKM2-interacting proteins. Here, unstimulated and MOGsup-stimulated primary astrocytes were subjected to PKM2 immunoprecipitation, followed by mass spectrometry”. Furthermore, the description of these two groups of cells were added in the figure legend of Fig.4.

Result 5:

- For the reader, it would be better to start this part by explaining the role of TRIM21 in cells by referring to the literature.

We agreed with the reviewer that beginning this part by explaining the role of TRIM21 would be better. Accordingly, we have added the following descriptions at the beginning of this part: “TRIM21 is a multifunctional E3 ubiquitin ligase that plays a crucial role in orchestrating diverse biological processes, including cell proliferation, antiviral responses, cell metabolism and inflammatory processes (Chen X. et al., 2022).” The relevant literature has been included: Chen X, Cao M, Wang P, Chu S, Li M, Hou P, et al. The emerging roles of TRIM21 in coordinating cancer metabolism, immunity and cancer treatment. Front Immunol 2022;13:968755.

- The source and the state of the cells (control vs MOG induced) should be stated (Figure 5A).

In figure 5A to 5D, single-cell RNA-seq were performed from CNS tissues of naive and different phases of EAE mice (peak and chronic). We have added this detailed information in the figure legend of Figure 5.

- Figure 5D can be placed after 5A. Data in Figure 5A is probably from naive animals, if so, it should be stated in the legend where A is explained. The group details of the data shown in Figure 5 should be clearly stated.

According to the reviewer’s suggestions, we have placed 5D after 5A. Single-cell RNA seq analysis were performed from CNS tissues of naïve mice and EAE mice. This information is stated in the legend of Figure 5A-D. “Single-cell RNA-seq profiles from naive and EAE mice (peak and chronic phase) CNS tissues. Naive (n=2); peak (dpi 14–24, n=3); chronic (dpi 21–26, n=2).”

- Immunofluorescence images should be replaced with better quality images, in control images, stainings are not visible.

We have replaced with better quality images in figure 5H and in control images, the staining is now visible.

Result 6:

- Experimental procedures should be given in detail in materials and methods.

We have revised the section of materials and methods, and more details are added. Detailed information was added for astrocyte isolation, immunoprecipitation. Moreover, mass spectrometry, Hematoxylin-Eosin (HE) and Luxol Fast Blue (LFB) staining, Splenocyte isolation and supernatant of MOG35-55-stimulated-splenocytes were added in materials and methods.

Result 7:

- In Figure 7A, the mean clinical score seems significantly reduced in the shTRIM21-treated group, although it is explained in the result text that it is not significant. Explain to us the difference between Figure 7A and the explaining text?

Thank you for pointing this out. We sincerely apologize for our carelessness. Based on your comments, we have made the corrections in the manuscript. As there is indeed a statistical difference in the mean clinical scores between shTRIM21-treated group and shVec group, we have accordingly revised the sentence for Figure 7A to state, “At the end time point at day 22 p.i., shTRIM21-treated group showed reduced disease scores compared to control groups (Fig. 7A).” .

- The staining methods for luxury fast blue and HE are not given in materials and methods.

According to the reviewer’s comments, we have added the staining methods for HE and LFB in materials and methods.

- In Figure 7E, authors claim that MBP staining is low in an image, however the image covers approximately 500 um area. One would like to see the demyelinated areas in dashed lines, and also the whole area of the spinal cord sections.

In Author response image 2, we have added the images for MBP staining of the whole area of spinal cord sections. Demyelinated areas are marked with dashed lines.

- "TEPP-46 is an allosteric activator that blocks the nuclear translocation of PKM2 by promoting its tetramerization." should be supported by references.

We have added two references for this sentence. Anastasiou D et al. showed that TEPP-46 acts as an activator by stabilizing subunit interactions and promoting tetramer formation of PKM2. Angiari S et al. showed that TEPP-46 prevented the nuclear transport of PKM2 by promoting its tetramerization in T cells.

These two references are added:

Angiari S, Runtsch MC, Sutton CE, Palsson-McDermott EM, Kelly B, Rana N, et al. Pharmacological Activation of Pyruvate Kinase M2 Inhibits CD4(+) T Cell Pathogenicity and Suppresses Autoimmunity. Cell metabolism 2020;31(2):391-405.e8.

Anastasiou D, Yu Y, Israelsen WJ, Jiang JK, Boxer MB, Hong BS, et al. Pyruvate kinase M2 activators promote tetramer formation and suppress tumorigenesis. Nature chemical biology 2012;8(10):839-47.

- Could you explain what the prevention stage is?

The term “prevention stage” was used to describe the administration of TEPP-46 before disease onset. To be more accurate, we have revised the phrase from “prevention stage” to “preventive treatment” as described in other references. For example, Ferrara et al. (Ferrara et al., 2020) used “preventive” and “preventive treatment” to mean administration before disease onset.

The revised sentences are as follows: “To test the effect of TEPP-46 on the development of EAE, the “preventive treatment” (i.e, administration before disease onset) was administered. Intraperitoneal treatment with TEPP-46 at a dosage of 50 mg/kg every other day from day 0 to day 8 post-immunization with MOG35-55 resulted in decreased disease severity (Fig. S8A).”

- In in vitro experiments, authors used DASA-58, and in vivo they used TEPP-46. What might be the reason that DASA-58 is not applied in vivo?

The effects of DASA-58 and TEPP-46 in promoting PKM2 tetramerization have been tested in vitro and has been documented. Based on in vitro absorption, distribution, metabolism and excretion profiling studies, Anastasiou et al. predicted that TEPP-46 had better in vivo drug exposure compared to DASA-58. Moreover, TEPP-46, but not DASA-58, is pharmacokinetically validated in vivo (Anastasiou et al., 2012). Thus, we used TEPP-46 for in vivo studies.

- Authors claim that TEPP-46 activates PKM2 and leads it its nuclear translocation, however, they did not verify PKM2 expression in the nucleus.

To support that TEPP-46 exerts effects in inhibiting PKM2 nuclear translocation both in vivo and in vitro, we have performed western blotting analysis and immunofluorescence staining. In vitro, TEPP-46 administration inhibited the MOGsup-induced PKM2 nuclear translocation, which exerts similar effects as DASA-58 (Author response image 4). The in vivo effects of TEPP-46 was analyzed by co-immunostaining of PKM2 and GFAP. The results showed reduced nuclear staining of PKM2 in spinal cord astrocytes in TEPP-46-treated EAE mice compared with control EAE mice (Figure S7B).

Author response image 4.

TEPP-46 inhibited the nuclear transport of PKM2 in primary astrocytes. Nuclear-cytoplasmic protein extraction analysis showed the nuclear and cytoplasmic changes of PKM2 in TEPP-46 treated astrocytes and MOGsup-stimulated astrocytes. Primary astrocytes were pretreated with 50 μM TEPP-46 for 30 min and stimulated with MOGsup for 24 h.

Supplementary Figure 3:

- In Figure 3D, merge should be stated on top of the merged images, it is confusing to the reader.

According to the reviewer’s comments, we have added merge on top of the merged images.

Discussion:

All results should be discussed in detail by interpreting them according to the literature.

We have further discussed the results in the discussion n section. Firstly, we added a paragraph describing the role of nuclear translocation of PKM2 in diverse CNS diseases. Moreover, a paragraph discussing the nuclear function of PKM2 as a protein kinase or transcriptional co-activator was added. Now the discussion section is more comprehensive, which nearly discuss all the results by interpreting them according to the literature in detail.

Reviewer #2 (Recommendations For The Authors):

The authors could address the following points:

(1) In Figure 1A, the authors present immunofluorescence staining of PKM2 in both control mice and MOG35-725 55-induced EAE mice across different stages of disease progression: onset, peak, and chronic stages. Observing the representative images suggests a notable increase in PKM2 levels, particularly within the nucleus of MOG35-725 55-induced EAE mice. However, to provide a more comprehensive analysis, it would be beneficial for the authors to include statistical data, such as average intensities {plus minus} standard deviation (SD), along with the nuclear PKM2 ratio, akin to the presentation for cultured primary astrocytes in vitro in panels B-D. Additionally, the authors should clearly specify the number of technical repeats and the total number of animals utilized for these data sets to ensure transparency and reproducibility of the findings.

Thanks for the reviewer’s suggestion. Accordingly, for figure 1A, we have added the nuclear PKM2 ratio in astrocytes in control and different stages of EAE mice in Supplementary figure S1A. Moreover, the quantification of mean fluorescence intensity (MFI) for PKM2 was added in figure S1B. Moreover, we have added the number of animals used in each group in figure legend.

(2) The blue hue observed in the merged images of Figure 1B (lower panel) presents a challenge for interpretation. The source of this coloration remains unclear from the provided information. Did the authors also include a co-stain for the nucleus in their imaging? To enhance clarity, especially for individuals with color vision deficiency, the authors might consider utilizing different color combinations, such as presenting PKM2 in green and GFAP in magenta, which would aid in distinguishing the two components. Furthermore, for in vitro cell analysis, incorporating a nuclear stain could provide valuable insights into estimating the cytosolic-to-nuclear ratio of PKM2.

For the question relating to the merged images in figure 1B, PKM2 was presented in green, GFAP was presented in red and blue represents the nuclear staining by DAPI. “Merge” represents the merged images of these three colors. To enhance the clarity, we have added the images for the nuclear staining of DAPI.

(3) To substantiate the conclusion of the authors regarding the enhancement of aerobic glycolysis due to PKM2 expression and nuclear translocation in MOGsup-stimulated astrocytes, employing supplementary methodologies such as high-resolution respirometry and metabolomics could offer valuable insights. These techniques would provide a more comprehensive understanding of metabolic alterations and further validate the observed changes in glycolytic activity.

While we recognize the merits of techniques such as high-resolution respirometry and metabolomics, we believe that the conclusions regarding the enhancement of aerobic glycolysis due to PKM2 expression and nuclear translocation in MOGsup-stimulated astrocytes are sufficiently supported by the current experimental evidence. Our study has relied on a robust set of experiments, including lactate production, glucose consumption, cyto-nuclear localization analysis and western blotting analysis of key enzymes in glycolysis. These results, in conjunction with the literature on the role of PKM2 in various cancer cells, keratinocytes and immune cells, provide a strong foundation for our conclusions. Although metabolomics could offer a global view of the changes in metabolic states in astrocytes, as the end product of aerobic glycolysis is lactate, our study, which analyze the change of lactate levels in different experimental conditions might be more direct. However, we fully acknowledge that future studies employing these advanced methodologies could provide further insights into the precise mechanisms underlying PKM2's effects on aerobic glycolysis.

(4) Minor: Why is the style of the columns different in Gig 2 panel D compared to those shown in panels B, C, and G of Figure 2.

To maintain consistency in the column style across figure 2, we have updated the column in figure 2D. Now, we use same style of columns in Fig 2B, C, D and G.

(5) The effect of stimulating astrocytes with MOGsup on cell proliferation, as shown in Figure 2E, is very moderate. Does DASA-58 reduce the proliferation of control cells in this assay?

In response to the reviewer’s questions, we conducted a CCK8 analysis in astrocytes subjected to DASA-58 treatment. As depicted in Author response image 5, administration of DASA-58 did not reduce the proliferation of control cells. This result aligns with our other findings in the glycolysis assays and EdU analysis, where there is no statistical difference between control group and DASA-58-treated group. One plausible explanation for this is that in their steady state, astrocytes in the control group are not in a hyperproliferative state. Under such conditions, inhibiting the translocation of PKM2 via DASA-58 or other inhibitors did not significantly affect the proliferation of astrocytes.

Author response image 5.

CCK8 analysis of astrocyte proliferation. Primary astrocytes were pretreated with 50 μM DASA-58 for 30 min before stimulation with MOGsup. Data are represented as mean ± SEM. ***P<0.001. SEM, standard error of the mean.

(6) The tables and lists in Figure 4, panels A-D, are notably small, hindering readability and comprehension. Consider relocating these components to the supplementary materials as larger versions.

We have updated the tables and lists, the lines are made thicker. As suggested by the reviewer, we relocate theses components in Supplementary Figure S5.

Reviewer #3 (Recommendations For The Authors):

Higher magnification images that more clearly show nuclear translocation of PKM2 and pp65 and pSTAT3 immunoreactivity should be added to the figures panels, for example as inlets.

Thank you for pointing out this issue in the manuscript. According to the reviewer’s comments we have included higher magnification images as inlets for Figure 3A, Figure 3B and Figure 2A. These enlarged images now provide a clearer visualization of the nuclear translocation state of PKM2, pp65, and pSTAT3.

There are seldom wording errors like features => feathers at line 364.

We are very sorry for our incorrect writing. We have corrected this spelling mistake in the manuscript.

Reviewer #4 (Recommendations For The Authors):

Here below are major and minor concerns on the data presented:

(1) It is not clear from the Methods section what are the culture conditions defined as 'control' in Figure 1B-D. I believe the control should be culturing with the conditioned medium of normal (non-EAE) mice splenocytes to be sure the effect is not from cytokines naturally secreted by these cells.

Thanks for the reviewer’s comments and we totally understand the reviewer's concern. The control means non-treated primary astrocytes cultured with traditional DMEM medium supplemented with 10% FBS. In fact, we have performed experiments to exclude the possibility that the observed effect of MOGsup on the activation of astrocytes is from cytokines secreted by splenocytes. Splenocytes from normal (non-EAE) mice were isolated, cultured in RPMI-1640 medium containing 10% FBS for 60 hours, and supernatant was collected. Immunofluorescence staining of PKM2 and GFAP were performed in non-treated primary astrocytes and astrocytes stimulated with supernatant from control splenocytes. As shown in Figure S1C, in both groups, no difference was observed in PKM2 expression and localization, PKM2 was located mainly in the cytoplasm in theses conditions. These results indicate that observed effect of PKM2 in MOGsup-stimulated condition is not due to the cytokines secreted from splenocytes. Thus, we used non-treated primary astrocytes as controls in our study. To clarify the control group, we have revised the description in the figure legend, The revised expression is as follows: “Immunofluorescence staining of PKM2 (green) with GFAP (red) in non-treated primary astrocytes (control) or primary astrocytes cultured with splenocytes supernatants of MOG35–55-induced EAE mice (MOGsup) for different time points (6 h, 12 h and 24 h). ”

(2) Figure 3D: the presence of PMK2 in the nuclear fraction upon MOGSUP together with the DASA-58 (last lane of Figure 3D) is not supporting the hypothesis proposed and further may indicate that the reduction of pSTAT3, pp65, etc. observed is independent of PMK2 nuclear translocation/astrocyte activation being observed even in absence of MOGSUP.

Thank you for pointing out this problem in manuscript. The representing image of nuclear level of PKM2 in Figure 3D is not obvious, as shown by figure 3D, which has raised doubts among the reviewers. To strengthen our conclusion that the reduction of STAT3 and p65 pathway is related to the inhibited nuclear level of PKM2 induced by DASA-58, nuclear PKM2 level was quantified and added in Figure S4B. From the quantification results, it is evident that DASA-58 administration decreased the nuclear level of PKM2 in MOGsup-stimulated astrocytes. To address this concern, we have updated the immunoblot image for PKM2 in figure 3D and incorporated quantification results in supplementary Figure S4.

(3) Molecular docking indication and deletion co-immunoprecipitation reported in Figure 4 data are not concordant on TRIM21: N-terminal Phe23 and Thr87 (Figure 4E) predicted by MD to bind PMK2 are not in the PRY-SPRY domain suggested by the co-IP experiment (Figure 4I).

The discrepancy between the molecular docking prediction and the co-immunoprecipitation can be explained as follows:

Firstly, molecular docking is computational methods that predicts protein-protein interaction based on 3-D structures of the proteins. However, the accuracy of this predication can be influenced by the different models of 3D structures of TRIM21 and PKM2, as well as by factors such as post-translational modifications and flexibility of the proteins. Proteins in vivo are subject to post-translational modifications that can affect their interactions. These modifications are not fully captured in molecular docking analysis. For example, in our analysis, the predicted N-terminal Phe23 and Thr87 in TRIM21 hold the potential to interact with PKM2 by hydrogen bonds. However, such binding can be influenced by diverse biological environments, such as different cells and pathological conditions. Molecular docking predication may suggest the specific residues and binding pocked within the protein complex, however, the accuracy should be verified by experimental techniques such as immunoprecipitation. To address the predication results of molecular docking, the description has been revised as follows: “TRIM21 is predicted to bound to PKM2 via hydrogen bonds between the amino acids of the two molecules.”

Co-immunoprecipitation that involves the use of truncated domains of TRIM21 and PKM2, is an experimental technique relies on the specific interaction between antibody and targeted proteins. This technique can provide insights into the precise binding domains between TRIM21 and PKM2. As demonstrated in our study, PRY-SPRY domain of TRIM21 is involved in this binding. In summary, while molecular docking and Co-IP are valuable tools for studying protein-protein interactions, their differing focus and limitations may result in discrepancies between the predicted interaction sites and the experimentally identified interaction domains.

(4) The Authors state that PMK2 is a substrate of TRIM21 E3 ligase activity, however, this is not proved: i) interaction does not imply a ligase-substrate relationship; ii) the ubiquitination shown in Figure 6C is not performed in denaturing conditions thus the K63-Ub antibody can detect also interacting FLAG-IPed proteins (besides, only a single strong band is seen, not a chain; molecular weights in immunoblot should be indicated); iii) use of a catalytically inactive TRIM21 would be required as well.

We appreciate the reviewer’s comments regarding the limitations of the immunoprecipitation and K63-antibody test, which could not lead to the conclusion that PKM2 is a substrate of TRIM21. To avoid any misunderstandings, we have revised the relevant sentence from “Hereby, we recognized PKM2 as a substrate of TRIM21” to “Hereby, we recognized PKM2 as an interacting protein of TRIM21, and further studies are required to determine if it is a substrate of E3 ligase TRIM21”. Moreover, we have revised the title of the relevant part in the results section, the previous title, “TRIM21 ubiquitylates and promotes the nuclear translocation of PKM2” has been replaced with “TRIM21 promotes ubiquitylation and the nuclear translocation of PKM2”. Moreover, molecular weights for all proteins in western blotting were indicated.

(5) As above, molecular weights should always be indicated in immunoblot.

Thanks for pointing out this problem in the figures. Accordingly, we have added the molecular weights for every protein tested in immunoblot.

(6) The authors should describe the EAE mouse model in the text and in the material and methods as it may not be so well known to the entire reader audience, and the basic principle of MOG35-55 stimulation, in order to understand the experimental plan meaning.

We appreciate the reviewer’s comments highlighting the importance of clarifying EAE model for a broader understanding of the reader audience. In response, we have described the EAE model both in the text and in the materials and methods section. In the text, the description of EAE model was added at the beginning of the first paragraph in the Results section. The description is as follows: “EAE is widely used as a mouse model of multiple sclerosis, which is typically induced by active immunization with different myelin-derived antigens along with adjuvants such as pertussis toxin (PTX). One widely used antigen is the myelin oligodendrocyte glycoprotein (MOG) 35-55 peptide (Nitsch et al., 2021), which was adopted in our current studies.”

We have also added the detailed experimental procedures for EAE induction in the materials and methods section.

(7) The authors should better explain and give the rationale for the use of splenocytes and why directly activated astrocytes (isolated from the EAE model) cannot be employed to confirm/prove some of the presented data.

Firstly, splenocytes offer a heterogenous cell population, encompassing T cells and antigen presenting cells (APC), which may better mimic the microenvironment and complex immune responses observed in vivo.

Myelin oligodendrocyte glycoprotein (MOG) 35-55 peptide is one widely used antigen for EAE induction. MOG35-55 elicits strong T responses and is highly encephalitogenic. Moreover, MOG35-55 induces T cell-mediated phenotype of multiple sclerosis in animal models. Thus, by isolating splenocytes from the onset stage of EAE mice, which contains APC and effector T cells, followed by stimulation with antigen MOG35-55 in vitro for 60 hours, the T-cell response in the acute stage of EAE diseases could be mimicked in vitro. The supernatant from MOG35-55 stimulated splenocytes has high levels of IFN-γ and IL-17A, which in part mimic the pathological process and environment in EAE, and this technique has been documented in the references (Chen et al., 2009, Kozela et al., 2015).

Correspondingly, we have revised sentence for the use of MOG35-55 stimulates splenocytes in EAE mice and add the relevant references: “Supernatant of MOG35-55-stimulated splenocytes isolated from EAE mice were previously shown to elicit a T-cell response in the acute stage of EAE and are frequently used as an in vitro autoimmune model to investigate MS and EAE pathophysiology (Chen et al., 2009, Du et al., 2019, Kozela et al., 2015).”

Secondly, activated astrocytes (isolated from the EAE model) can not be employed for in vitro culture for the following reasons:

(1) Low cell viability. Compared to embryonic or neonatal mice, adult mice yield a limited number of viable cells. The is mainly because that adult tissues possess less proliferative capacity.

(2) Disease changes. Astrocytes in EAE mice are exposed to microenvironment including inflammatory cytokines, antigens and other pathological factors. Without this environment, the function and morphology of astrocytes undergo changes, which make it difficult to interpret the results in vitro.

For these reasons, the in vitro cultured primary astrocytes used the neonatal mice.

(8) The authors should indicate the phosphorylation sites they are referring to when analysing p-c-myc, pSTAT3, pp65, etc...

According to the reviewer’s suggestions, we have added the phosphorylation sites for pSTAT3 (Y705), pp65 (S536), p-c-myc (S62) and pIKK (S176+S180) in the figure panels.

(9) Reference of DASA-58 and TEPP-46 inhibitors and their specificity should be given.

According to the reviewer’s comments, we have added the relevant references for the use of DASA-58 and TEPP-46 as inhibitors of PKM2 nuclear transport. In primary BMDMs, LPS induced nuclear PKM2. However, driving PKM2 into tetramers using DASA-58 and TEPP-46 inhibited LPS-induced PKM2 nuclear translocation (Palsson-McDermott et al., 2015). Consistently, FSTL1 induced PKM2 nuclear translocation was inhibited by DASA-58 in BMDMs (Rao et al., 2022). Accordingly, we have added these references in the manuscript.

To address the selectivity of TEPP-46 and add the references, the relevant sentence has been revised from “TEPP-46 is an allosteric activator that blocks the nuclear translocation of PKM2 by promoting its tetramerization” to “TEPP-46 is a selective allosteric activator for PKM2, showing little or no effect on other pyruvate isoforms. It promotes the tetramerization of PKM2, thereby diminishing its nuclear translocation (Anastasiou et al., 2012, Angiari et al., 2020).”

Reviewing Editor (Recommendations For The Authors):

The reviewing editor would appreciate it if the original blots from the western blot analysis, which were used to generate the final figures, could be provided.

Thanks for the reviewing editor’s comment, accordingly, we will add the original blots for the western blots analysis.

References

Anastasiou D, Yu Y, Israelsen WJ, Jiang JK, Boxer MB, Hong BS, et al. Pyruvate kinase M2 activators promote tetramer formation and suppress tumorigenesis. Nature chemical biology 2012;8(10):839-47.

Escartin C, Guillemaud O, Carrillo-de Sauvage M-A. Questions and (some) answers on reactive astrocytes. Glia 2019;67(12):2221-47.

Ferrara G, Benzi A, Sturla L, Marubbi D, Frumento D, Spinelli S, et al. Sirt6 inhibition delays the onset of experimental autoimmune encephalomyelitis by reducing dendritic cell migration. Journal of neuroinflammation 2020;17(1):228.

Lin CC, Edelson BT. New Insights into the Role of IL-1β in Experimental Autoimmune Encephalomyelitis and Multiple Sclerosis. Journal of immunology (Baltimore, Md : 1950) 2017;198(12):4553-60.

Palsson-McDermott Eva M, Curtis Anne M, Goel G, Lauterbach Mario AR, Sheedy Frederick J, Gleeson Laura E, et al. Pyruvate Kinase M2 Regulates Hif-1α Activity and IL-1β Induction and Is a Critical Determinant of the Warburg Effect in LPS-Activated Macrophages. Cell metabolism 2015;21(1):65-80.Rao J, Wang H, Ni M, Wang Z, Wang Z, Wei S, et al. FSTL1 promotes liver fibrosis by reprogramming macrophage function through modulating the intracellular function of PKM2. Gut 2022;71(12):2539-50.

Wheeler MA, Clark IC, Tjon EC, Li Z, Zandee SEJ, Couturier CP, et al. MAFG-driven astrocytes promote CNS inflammation. Nature 2020;578(7796):593-9.

Zhang J, Feng G, Bao G, Xu G, Sun Y, Li W, et al. Nuclear translocation of PKM2 modulates astrocyte proliferation via p27 and -catenin pathway after spinal cord injury. Cell Cycle 2015;14(16):2609-18.

Reviewer #3 (Public Review):

Summary:

Pyruvate kinase M2 (PKM2) is a rate limiting enzyme in glycolysis and its translocation to nucleus in astrocytes in various nervous system pathologies has been associated with a metabolic switch to glycolysis which is a sign of reactive astrogliosis. Authors investigated whether this occurs in experimental autoimmune encephalomyelitis (EAA), an animal model of multiple sclerosis (MS). They show that in EAA, PKM2 is ubiquitinated by TRIM21 and transferred to the nucleus in astrocytes. Inhibition of TRIM21-PKM2 axis efficiently blocks reactive gliosis and partially alleviates symptoms of EAA. Authors conclude that this axis can be a potential new therapeutic target in the treatment of MS.

Strengths:

The study is well-designed, controls are appropriate and a comprehensive battery of experiments has been successfully performed. Results of in vitro assays, single cell RNA sequencing, immunoprecipitation, RNA interference, molecular docking and in vivo modeling etc. complement and support each other.

Weaknesses:

Though EAA is a valid model of MS, a proposed new therapeutic strategy based on this study needs to have support from human studies.

The comments above are still valid for this revised version of the manuscript.

eLife assessment

This important work describes the activation of astrocytes via the nuclear translocation of PKM2 in an animal model of multiple sclerosis. This study provides convincing evidence of the interaction between TRIM21 and PKM2 as the crucial molecular event leading to the translocation of PKM2 and a metabolic shift towards glycolysis dominance, fostering proliferation in stimulated astrocytes. This finding is significant as it underscores the potential of targeting glycolytic metabolism to mitigate neurological diseases mediated by astrocytes, offering a strong rationale for potential therapeutic interventions.

Reviewer #1 (Public Review):

Summary:

Yang. Hu et al. investigated the molecular mechanism that cause astrocyte activation and its implications for multiple sclerosis. This study focuses on the enzyme PKM2, known for its role in glycolysis, and its nuclear translocation in reactive astrocytes in a mouse model of multiple sclerosis (EAE). Preventing the nuclear translocation of PKM2 reduces astrocyte activation, proliferation, glycolysis, and inflammatory cytokine secretion. Importantly, the study reveals that TRIM21 controls PKM2's nuclear translocation through ubiquitination, promoting its nuclear import and enhancing its activity. Single-cell RNA sequencing and immunofluorescence confirm TRIM21 upregulation in EAE astrocytes, and alteration of TRIM21 levels affect PKM2-dependent glycolysis and proliferation. Their findings suggest that targeting the TRIM21-PKM2 axis could be a therapeutic strategy for treating neurological diseases involving astrocyte activation.

Strength:

This work provides a comprehensive exploration of PKM2's nuclear role and its interaction with TRIM21 in EAE, offering new insights for therapeutic strategies targeting metabolic reprogramming in astrocyte activation. The strength of the study is the use of advanced techniques such as single cell RNA sequencing, in vitro and in vivo knockdown techniques to support the data. With the addition of new data and explanations in the manuscript, the authors have rendered their claimed ideas more supportive.

Weakness:

The revisions and implementation of suggestions have greatly improved the overall quality of the manuscript. I would like to thank the authors for carefully evaluating all the suggestions and for providing extra explanations and response figures. However, there are still some points that need to be corrected and clarified.

Reviewer #2 (Public Review):

This study significantly advances our understanding of the metabolic reprogramming underlying astrocyte activation in neurological diseases such as multiple sclerosis. By employing an experimental autoimmune encephalomyelitis (EAE) mouse model, the authors discovered a notable nuclear translocation of PKM2, a key enzyme in glycolysis, within astrocytes. Preventing this nuclear import via DASA 58 substantially attenuated primary astrocyte activation, characterized by reduced proliferation, glycolysis, and inflammatory cytokine secretion.

Moreover, the authors uncovered a novel regulatory mechanism involving the ubiquitin ligase TRIM21, which mediates PKM2 nuclear import. TRIM21 interaction with PKM2 facilitated its nuclear translocation, enhancing its activity in phosphorylating STAT3, NFκB, and c-myc. Single-cell RNA sequencing and immunofluorescence staining further supported the upregulation of TRIM21 expression in astrocytes during EAE.

Manipulating this pathway, either through TRIM21 overexpression in primary astrocytes or knockdown of TRIM21 in vivo, had profound effects on disease severity, CNS inflammation, and demyelination in EAE mice. This comprehensive study provides invaluable insights into the pathological role of nuclear PKM2 and the ubiquitination-mediated regulatory mechanism driving astrocyte activation.

The author's use of diverse techniques, including single-cell RNA sequencing, immunofluorescence staining, and lentiviral vector knockdown, underscores the robustness of their findings and interpretations. Ultimately, targeting this PKM2-TRIM21 axis emerges as a promising therapeutic strategy for neurological diseases involving astrocyte dysfunction.

While the strengths of this piece of work are undeniable, some concerns could be addressed to refine its impact and clarity further.

Reviewer #4 (Public Review):

The authors report the role of the Piruvate Kinase M2 (PKM2) enzyme nuclear translocation as fundamental in the activation of astrocytes in a model of autoimmune encephalitis (EAE). They show that astrocytes, activated through culturing in EAE splenocytes medium, increase their nuclear PKM2 with a consequent activation of NFkB and STAT3 pathways. Prevention of PKM2 nuclear translocation decreases astrocyte counteracts this activation. The authors found that the E3 ubiquitin ligase TRIM21 interacts with PKM2 and promotes its nuclear translocation. In vivo, either silencing of TRIM21 or inhibition of PKM2 nuclear translocation ameliorates the severity of the disease in the EAE model.

Strengths

This work contributes to the knowledge of the complex action of the PKM2 enzyme in the context of an autoimmune-neurological disease, highlighting its nuclear role and a novel partner, TRIM21, promoting its nuclear translocation. In vivo amelioration of the pathological signs through inhibition of either of the two, PKM2 and TRIM21, provides a novel rationale for therapeutic targeting.

Weaknesses

I believe that the major weakness is the fact that TRIM21 is known to have per se many roles in autoimmune and immune pathways and some of the effects observed might be due to a PKM2-independent action. Some of the experiments to link the two proteins, besides their interaction, are not completely clarifying the issue. On top of that, the in vivo experiments address the role of TRIM21 and the nuclear localisation of PKM2 independently, thus leaving the matter unsolved.

In general, the conclusions of the manuscript are supported by the reported results. The points to be addressed in future are the assessment of PKM2 as substrate of TRIM21 ubiquitin ligase activity and the proof of the epistatic relationship of TRIM21 and PKM2 in astrocyte activation. However, the data surely open novel directions to follow for the understanding of multiple sclerosis and related pathologies.

eLife assessment

This valuable study presents a computational model that simulates walking motions in Drosophila and suggests that, if sensorimotor delays in the neural circuitry were any longer, the system would be easily destabilized by external perturbations. The hierarchical control model is sensible and the evidence supporting the conclusions is solid. However, because the modular model has many interacting components with varying degrees of biological realism, it is difficult to judge the degree to which the observed differences between simulation and empirical data are meaningful, and the precise source of the discrepancies.

Reviewer #1 (Public Review):

Summary:

In this work, the authors present a novel, multi-layer computational model of motor control to produce realistic walking behaviour of a Drosophila model in the presence of external perturbations and under sensory and motor delays. The novelty of their model of motor control is that it is modular, with divisions inspired by the fly nervous system, with one component based on deep learning while the rest are based on control theory. They show that their model can produce realistic walking trajectories. Given the mostly reasonable assumptions of their model, they convincingly show that the sensory and motor delays present in the fly nervous system are the maximum allowable for robustness to unexpected perturbations.

Their fly model outputs torque at each joint in the leg, and their dynamics model translates these into movements, resulting in time-series trajectories of joint angles. Inspired by the anatomy of the fly nervous system, their fly model is a modular architecture that separates motor control at three levels of abstraction:<br /> (1) oscillator-based model of coupling of phase angles between legs,<br /> (2) generation of future joint-angle trajectories based on the current state and inputs for each leg (the trajectory generator), and<br /> (3) closed-loop control of the joint-angles using torques applied at every joint in the model (control and dynamics).

These three levels of abstraction ensure coordination between the legs, future predictions of desired joint angles, and corrections to deviations from desired joint-angle trajectories. The parameters of the model are tuned in the absence of external perturbations using experimental data of joint angles of a tethered fly. A notable disconnect from reality is that the dynamics model used does not model the movement of the body and ground contacts as is the case in natural walking, nor the movement of a ball for a tethered fly, but instead something like legs moving in the air for a tethered fly.

In order to validate the realism of the generated simulated walking trajectories, the authors compare various attributes of simulated to real tethered fly trajectories and show qualitative and quantitative similarities, including using a novel metric coined as Kinematic Similarity (KS). The KS score of a trajectory is a measure of the likelihood that the trajectory belongs to the distribution of real trajectories estimated from the experimental data. While such a metric is a useful tool to validate the quality of simulated data, there is some room for improvement in the actual computation of this score. For instance, the KS score is computed for any given time-window of walking simulation using a fraction of information from the joint-angle trajectories. It is unclear if the remaining information in joint-angle trajectories that are not used in the computation of the KS score can be ignored in the context of validating the realism of simulated walking trajectories.

The authors validate simulated walking trajectories generated by the trained model under a range of sensorimotor delays and external perturbations. The trained model is shown to generate realistic joint-angle trajectories in the presence of external perturbations as long as the sensorimotor delays are constrained within a certain range. This range of sensorimotor delays is shown to be comparable to experimental measurements of sensorimotor delays, leading to the conclusion that the fly nervous system is just fast enough to be robust to perturbations.

Strengths:

This work presents a novel framework to simulate Drosophila walking in the presence of external perturbations and sensorimotor delay. Although the model makes some simplifying assumptions, it has sufficient complexity to generate new, testable hypotheses regarding motor control in Drosophila. The authors provide evidence for realistic simulated walking trajectories by comparing simulated trajectories generated by their trained model with experimental data using a novel metric proposed by the authors. The model proposes a crucial role in future predictions to ensure robust walking trajectories against external perturbations and motor delay. Realistic simulations under a range of prediction intervals, perturbations, and motor delays generating realistic walking trajectories support this claim. The modular architecture of the framework provides opportunities to make testable predictions regarding motor control in Drosophila. The work can be of interest to the Drosophila community interested in digitally simulating realistic models of Drosophila locomotion behaviors, as well as to experimentalists in generating testable hypotheses for novel discoveries regarding neural control of locomotion in Drosophila. Moreover, the work can be of broad interest to neuroethologists, serving as a benchmark in modelling animal locomotion in general.

Weaknesses:

As the authors acknowledge in their work, the control and dynamics model makes some simplifying assumptions about Drosophila physics/physiology in the context of walking. For instance, the model does not incorporate ground contact forces and inertial effects of the fly's body. It is not clear how these simplifying assumptions would affect some of the quantitative results derived by the authors. The range of tolerable values of sensorimotor delays that generate realistic walking trajectories is shown to be comparable with sensorimotor delays inferred from physiological measurements. It is unclear if this comparison is meaningful in the context of the model's simplifying assumptions. The authors propose a novel metric coined as Kinematic Similarity (KS) to distinguish realistic walking trajectories from unrealistic walking trajectories. Defining such an objective metric to evaluate the model's predictions is a useful exercise, and could potentially be applied to benchmark other computational animal models that are proposed in the future. However, the KS score proposed in this work is calculated using only the first two PCA modes that cumulatively account for less than 50% of the variance in the joint angles. It is not obvious that the information in the remaining PCA modes may not change the log-likelihood that occurs in the real walking data.

Reviewer #2 (Public Review):

Summary:

In this study, Karashchuk et al. develop a hierarchical control system to control the legs of a dynamic model of the fly. They intend to demonstrate that temporal delays in sensorimotor processing can destabilize walking and that the fly's nervous system may be operating with as long of delays as could possibly be corrected for.

Strengths:

Overall, the approach the authors take is impressive. Their model is trained using a huge dataset of animal data, which is a strength. Their model was not trained to reproduce animal responses to perturbations, but it successfully rejects small perturbations and continues to operate stably. Their results are consistent with the literature, that sensorimotor delays destabilize movements.

Weaknesses:

The model is sophisticated and interesting, but the reviewer has great concerns regarding this manuscript's contributions, as laid out in the abstract:

(1) Much simpler models can be used to show that delays in sensorimotor systems destabilize behavior (e.g., Bingham, Choi, and Ting 2011; Ashtiani, Sarvestani, and Badri-Sproewitz 2021), so why create this extremely complex system to test this idea? The complexity of the system obscures the results and leaves the reviewer wondering if the instability is due to the many, many moving parts within the model. The reviewer understands (and appreciates) that the authors tested the impact of the delay in a controlled way, which supports their conclusion. However, the reviewer thinks the authors did not use the most parsimonious model possible, and as such, leave many possible sources for other causes of instability.

(2) In a related way, the reviewer is not sure that the elements the authors introduced reflect the structure or function of the fly's nervous system. For example, optimal control is an active field of research and is behind the success of many-legged robots, but the reviewer is not sure what evidence exists that suggests the fly ventral nerve cord functions as an optimal controller. If this were bolstered with additional references, the reviewer would be less concerned.

(3) "The model generates realistic simulated walking that matches real fly walking kinematics...". The reviewer appreciates the difficulty in conducting this type of work, but the reviewer cannot conclude that the kinematics "match real fly walking kinematics". The range of motion of several joints is 30% too small compared to the animal (Figure 2B) and the reviewer finds the video comparisons unpersuasive. The reviewer would understand if there were additional constraints, e.g., the authors had designed a robot that physically could not complete the prescribed motions. However the reviewer cannot think of a reason why this simulation could not replicate the animal kinematics with arbitrary precision, if that is the goal.

Author response:

We thank the editor and reviewers for their supportive comments about our modeling approach and conclusions, and for raising several valid concerns; we address them briefly below.

Concerns about model’s biological realism and impact on interpretations

The goal of this paper was to use an interpretable and modular model to investigate the impact of varying sensorimotor delays. Aspects of the model (e.g. layered architecture, modularity) are inspired by biology; at the same time, necessary abstractions and simplifications (e.g. using an optimal controller) are made for interpretability and generalizability, and they reflect common approaches from past work. The hypothesized effects of certain simplifying assumptions are discussed in detail in Section 3.5. Furthermore, the modularity of our model allows us to readily incorporate additional biological realism (e.g. biomechanics, connectomics, and neural dynamics) in future work. In the revision, we will add citations and edits to the text to clarify these points.

Concerns that the model is overly complex

To investigate the impact of sensorimotor delays on locomotion, we built a closed-loop model that recapitulates the complex joint trajectories of fly walking. We agree that locomotion models face a tradeoff between simplicity/interpretability and realism — therefore, we developed a model that was as simple and interpretable as possible, while still reasonably recapitulating joint trajectories and generalizing to novel simulation scenarios. Along these lines, we also did not select a model that primarily recreates empirical data, as this would hinder generalizability and add unnecessary complexity to the model. We do not think these design choices are significant weaknesses of this model; in fact, few comparable models account for all joints involved in locomotion, and fewer explicitly compare model kinematics with kinematics from data. We will add citations and edits to the text to clarify these points in the revision.

Concerns about the validity of the Kinematic Similarity (KS) metric to evaluate walking

We chose to incorporate only the first two PCA modes dimensions in the KS metric because the kernel density estimator performs poorly for high dimensional data. Our primary use of this metric was to indicate whether the simulated fly continues walking in the presence of perturbations. For technical reasons, it is not feasible to perform equivalent experiments on real walking flies, which is one of the reasons we explore this phenomenon with the model. We note the dramatic shift from walking to non-walking as delay increases (Figure 5). To be thorough, in the revision, we will investigate the effect of incorporating additional PCA modes, and whether this affects the interpretation of our results. We will additionally edit the discussion and presentation of the KS metric to clarify its purpose in this study. We agree with the reviewers that the KS metric is too coarse to reflect fine details of joint kinematics; indeed, in the unperturbed case, we evaluate our model’s performance using other metrics based on comparisons with empirical data (Figures 2, 7, 8).

eLife assessment

This study presents a useful finding for the prevention of diarrhea with loperamide in patients with early HER2-positive breast cancer treated with nab-paclitaxel in combination with pyrotinib. The evidence supporting the claims of the authors is somewhat incomplete. The enrollment of patients as a control group who have not received prophylactic treatment for diarrhea would have strengthened the study, and the addition of double-blinding for the assessment of treatment may be necessary. The work will be of interest to scientists working in the field of clinical breast cancer treatment.

Reviewer #1 (Public Review):

Summary:

This manuscript described a clinical trial to understand the different treatment durations of loperamide in preventing pyrotinib-induced diarrhea. The authors concluded that no significant differences were observed between 21-day and 42-day loperamide durations in preventing grade {greater than or equal to} grade 3 diarrhea. The authors suggested that considering the economic cost and patient compliance, 21-day loperamide prophylaxis might represent a more pragmatic and appropriate approach for clinical application.

Strengths:

It is essential to understand if loperamide for primary prevention of diarrhea helps or not for postoperative treatment with nab-paclitaxel and pyrotinib in HER2-positive patients. This clinical trial would answer this question eventually.

Weaknesses:

(1) There are no patients who have not received prophylactic treatment for diarrhea to serve as a control group. This limited the finding that if the loperamide for primary prevention of diarrhea benefits or not for postoperative treatment with nab-paclitaxel and pyrotinib in HER2-positive patients. This would not help much for the guidance of clinical use of the loperamide for primary prevention of diarrhea.

(2) The clinical trial needs double-blinding for evaluation of treatment. In this manuscript, the blinding was not employed.

Reviewer #2 (Public Review):

Summary:

Pyrotinib, a pan-HER tyrosine kinase inhibitor, has shown significant survival benefits in patients with HER2-positive breast cancer. However, diarrhea is a frequent and important adverse event during pyrotinib treatment. Severe diarrhea may require interruption of pyrotinib treatment, thus affecting its anti-tumor effect and becoming a clinical safety issue. This study evaluated the incidence of diarrhea in patients with early-stage HER2-positive breast cancer treated with nab-paclitaxel and pyrotinib using 42- and 21-day loperamide primary prevention strategies. No significant differences were observed between the 21- and 42-day loperamide durations in the prevention of grade 3 and above diarrhea. Considering the economic cost and patient compliance, 21-day loperamide prophylaxis might represent a more pragmatic and appropriate approach for clinical application.

Strengths:

This study has a reasonable design, a clear hypothesis and methodology, and clear results, making the conclusion reliable. Most importantly, the findings have practical implications for the clinical management of pyrotinib-induced diarrhea.

Weaknesses:

Although the paper does have strengths in the practical implications for the clinical management of pyrotinib-induced diarrhea, there are still many data presentations that are not clear:

(1) The baseline characteristics mention that at the cut-off date on September 27, 2023, two patients withdrew from the 21-day group due to intolerable diarrhea and received other anti-tumor therapies for liposarcoma on the face. In the 42-day group, one patient was lost to follow-up and two withdrew from the study due to intolerable diarrhea and bone metastases. So, in the study, how many cases are in each group? The numbers of cases indicated in Figures 1 and 2 are inconsistent.

(2 ) Why does Figure 3a only compare 3 months of data, while Figure 3b compares 12 months of data?

(3) It is mentioned in lines 222-229 that a combination treatment of nab-paclitaxel plus pyrotinib is 1-3 months, whereas those of pyrotinib alone is 3-12 months. So, what is the exact duration of the combination treatment and pyrotinib alone treatment?

(4) This study found that no significant differences were observed between 21-day and 42-day loperamide durations in preventing grade 3 and above diarrhea. However, nab-paclitaxel can also cause diarrhea, and the conclusions would be more reliable if a control group that was not given loperamide were added. It is suggested that the authors add relevant data to further confirm the conclusion.

eLife assessment

This valuable study uses in vitro and in vivo methods to identify HpARI proteins from H. polygyrus as modulators of the host immune system. Based on comprehensive approaches for investigating differential roles of HpARI proteins, the data are solid, but there are some concerns whether the claims are fully validate. This paper is relevant to those who investigate host-pathogen interactions at the systems and molecular levels.

Reviewer #1 (Public Review):

Summary:

Colomb et al have further explored the mechanisms of action of a family of three immunodulatory proteins produced by the murine gastrointestinal nematode parasite Heligmosomoides polygyrus bakeri. The family of HpARI proteins binds to the alarmin interleukin 33 and depending on family members, exhibits differential activities, either suppressive or enhancing. The present work extends previous studies by this group showing the binding of DNA by members of this family through a complement control protein (CCP1) domain. Moreover, they identify two members of the family that bind via this domain in a non-specific manner to the extracellular matrix molecule heparan sulphate through a basic charged patch in CCP1. The authors thus propose that binding to DNA or heparan sulphate extends the suppressive action of these two parasite molecules, whereas the third family member does not bind and consequently has a shorter half-life and may function via diffusion.

Strengths:

A strength of the work is the multifaceted approach to examining and testing their hypotheses, using a well-established and well-defined family of immunomodulatory molecules using multiple approaches including an in vivo setting.

Weaknesses:

There are a few weaknesses of the approach. Perhaps some discussion and speculation as to how these three family members might operate in concert during Heligmosomoides polygyrus bakeri infection would help place the biology of these molecules in context for the reader, e.g. when and where they are produced.

Reviewer #2 (Public Review):

Summary:

Colomb et al. investigated here the heparin-binding activity of the HpARI family proteins from H. polygyrus. HpARIs bind to IL-33, a pleiotropic cytokine, and modulate its activities. HpARI1/2 has suppressive functions, while HpARI3 can enhance the interaction between IL-33 and its receptor. This study builds upon their previous observation that HpARI2 binds DNA via its CCP1 domain. Here, the authors tested the CCP1 domain of HpARIs in binding heparan sulfate, an important component of the extracellular matrix, and found that 1/2 bind heparan, but 3 cannot, which is related to their half-lives in vivo.

Strengths:

The authors use a comprehensive multidisciplinary approach to assess the binding and their effects in vivo, coupled with molecular modeling.

Weaknesses:

(1) Figure 1C should include Western.

(2) Figure 1E: Why does HpARI1 stop binding DNA at 50%?

(3) ITC binding experiment with HpARI1?Also, the ITC results from HpARI2 do not seem to saturate, thus it is difficult to really determine the affinity.

(4) It would be helpful to add docking results from HpARI1.

(5) Some conclusions are speculative and need to remain in the Discussion. e.g.:<br /> a) That HpARI3 may be able to diffuse farther<br /> b) That DNA/HS may trap HpARI1/2 at the infection site.

Reviewer #2 (Public Review):

The paper by Willems aimed to uncover the neural implementations of threat omissions and showed that the VTA/SN activity was stronger following the omissions of more probable and intense shock stimulation, mimicking a reward PE signal.

My main concern remains regarding the interpretation of the task as a learning paradigm (extinction) or simply an expectation violation task (difference between instructed and experienced probability), though I appreciate some of the extra analyses in the responses to the reviewers. Looking at both the behavioral and neural data, a clear difference emerges among different US intensities and non-0% vs. 0% contrasts, however, the difference across probabilities was not clear in the figures, potentially partly due to the false instructions subjects received about the shock probabilities.

The lack of probability related PE demonstration, both in behavior and to a less extent in imaging data, does not fully support the PE axioms (0% and 100% are by themselves interesting categories since the instruction and experience matched well and therefore might need to be interpreted differently from other probabilities).

As the other reviewers pointed out, the application of instruction together with extinction paradigm complicates the interpretation of results. Also, the trial-by-trial analysis suggestion was responded by the probability x run interaction analysis, which still averaged over trials within each run to estimate a beta coefficient. So my evaluation remains that this is a valuable study to test PE axioms in the human reward and salience systems but authors need to be extremely careful with their wordings as to why this task is not a particularly learning paradigm (or the learning component did not affect their results, which was in conflict with the probability related SCR, pleasantness ratings as well as BOLD signals).

eLife assessment

Unlocking the potential of molecular genetic tools (optogenetics, chemogenetics, sensors, etc.) for the study of systems neuroscience in nonhuman primates requires the development of effective regulatory elements for cell-type specific expression to facilitate circuit dissection. This study provides a valuable building block, by carefully characterizing the laminar expression profile of two optogenetic enhancers, one designed for general GABA+ergic neurons (h56D) and the second (S5E2) for parvalbumin+ cell-type selective expression in the marmoset primary visual cortex. This study contributes solid evidence to our understanding of these tools but is limited by the understandably small number of animals used.

Reviewer #1 (Public Review):

Summary:

Federer et al. tested AAVs designed to target GABAergic cells and parvalbumin-expressing cells in marmoset V1. Several new results were obtained. First, AAV-h56D targeted GABAergic cells with high specificity but in ways that varied across serotype and layer. Second, AAV-PHP.eB.S5E2 targeted parvalbumin-expressing neurons with similarly high specificity. Third, immunohistochemical GABA and PV signals were attenuated near viral injection sites.

A strength of this study is the analysis of marker gene expression at AAV injection sites. Some endogenous genes are difficult to detect following AAV injections, which is an important observation. A second contribution is the demonstration that AAV-S5E2 drives transgene expression selectively in parvalbumin-expressing neurons when vectors are delivered intraparenchymally (the study introducing AAV-S5E2 used intravenous injections).

A weakness of this study is that the data set is small. Which of the results would hold up had a larger number of injections been made into a larger number of marmosets remains unclear.

A major goal of this study was to quantify the specificity and coverage of AAV-h56D and AAV-S5E2 vectors in marmoset cortex. This goal was achieved. This report provides a valuable guide for other investigators using these tools. It also provides a rigorous survey of the laminar distributions of GABA+ and PV+ neurons in marmoset V1 which has value independent of the viral injections.

Reviewer #3 (Public Review):<br /> Summary:

Federer et al. describe the laminar profiles of GABA+ and of PV+ neurons in marmoset V1. They also report on the selectivity and efficiency of expression of a PV-selective enhancer (S5E2) across laminae. Three further viruses were tested, with a view to characterizing the expression profiles of a GABA-selective enhancer (h56d), but these results are preliminary.

Strengths:

The derivation of cell-type specific enhancers is key for translating the types of circuit analyses that can be performed in mice - which rely on germline modifications for access to cell-type specific manipulation - in higher-order mammals. Federer et al. further validate the utility of S5E2 as a PV-selective enhancer in NHPs.

Additionally, the authors characterize the laminar distribution pattern of GABA+ and PV+ cells in V1. This survey may prove valuable to researchers seeking to understand and manipulate the microcircuitry mediating the excitation-inhibition balance in this region of the marmoset brain.

Weaknesses:

Enhancer/promoter specificity and efficiency cannot be directly compared, because they were packaged in different serotypes of AAV.

The three different serotypes of AAV expressing reporter under the h56D promoter were only tested once each, and all in the same animal. There are many variables that can contribute to the success (or failure) of a viral injection, so observations with an n=1 cannot be considered reliable.

Added after revision:

The revisions satisfy my concerns. In particular, the new language to qualify the strength of evidence relating to the interpretation of the data relating to the 3 different serotypes of virus used to test h56D is appropriate.

Author response:

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

Public Reviews

Reviewer #1 (Public Review):

Summary:

Federer et al. tested AAVs designed to target GABAergic cells and parvalbumin-expressing cells in marmoset V1. Several new results were obtained. First, AAV-h56D targeted GABAergic cells with >90% specificity, and this varied with serotype and layer. Second, AAV-PHP.eB.S5E2 targeted parvalbumin-expressing neurons with up to 98% specificity. Third, the immunohistochemical detection of GABA and PV was attenuated near viral injection sites.

Strengths:

Vormstein-Schneider et al. (2020) tested their AAV-S5E2 vector in marmosets by intravenous injection. The data presented in this manuscript are valuable in part because they show the transduction pattern produced by intraparenchymal injections, which are more conventional and efficient.

Our manuscript additionally provides detailed information on the laminar specificity and coverage of these viral vectors, which was not investigated in the original studies.

Weaknesses:

The conclusions regarding the effects of serotype are based on data from single injection tracks in a single animal. I understand that ethical and financial constraints preclude high throughput testing, but these limitations do not change what can be inferred from the measurements. The text asserts that "...serotype 9 is a better choice when high specificity and coverage across all layers are required". The data presented are consistent with this idea but do not make a strong case for it.

We are aware of the limitations of our results on the AAV-h56D. We agree with the Reviewer that a single injection per serotype does not allow us to make strong statements about differences between the 3 serotypes. Therefore, in the revised version of the manuscript we have tempered our claims about such differences and use more caution in the interpretation of these data (Results p. 6 and Discussion p.10). Despite this weakness, we feel that these data still demonstrate high efficiency and specificity across cortical layers of transgene expression in GABA cells using the h56D promoter, at least with two of the 3 AAV serotypes we tested. We feel that in itself this is sufficiently useful information for the primate community, worthy of being reported. Due to cost, time and ethical considerations related to the use of primates, we chose not to perform additional experiments to determine precise differences among serotypes. Thus, for example, while it is possible that had we replicated these experiments, serotype 7 could have proven equally efficient and specific as the other two serotypes, we felt answering this question did not warrant additional experiments in this precious species.

A related criticism extends to the analysis of Injection volume on viral specificity. Some replication was performed here, but reliability across injections was not reported. My understanding is that individual ROIs were treated as independent observations. These are not biological replicates (arguably, neither are multiple injection tracks in a single animal, but they are certainly closer). Idiosyncrasies between animals or injections (e.g., if one injection happened to hit one layer more than another) could have substantial impacts on the measurements. It remains unclear which results regarding injection volume or serotype would hold up had a large number of injections been made into a large number of marmosets.

For the AAV-S5E2, we made a total of 7 injections (at least 2 at each volume), all of which, irrespective of volume, resulted in high specificity and efficiency for PV interneurons. Our conclusion is that larger volumes are slightly less specific, but the differences are minimal and do not warrant additional injections. Additionally, we kept all the other parameters across animals constant (see new Supplementary Table 1), all of our injections involved all cortical layers, and the ROIs we selected for counts encompassed reporter protein expression across all layers. To provide a better sense of the reliability of the results across injections, in the revised version of the manuscript we now provide results for each of the AAV-S5E2 injection case separately in a new Supplementary Table 2. The results in this table indicate the results are indeed rather consistent across cases with slightly greater specificity for injection volumes in the range of 105-180 nl.

Reviewer #2 (Public Review):

This is a straightforward manuscript assessing the specificity and efficiency of transgene expression in marmoset primary visual cortex (V1), for 4 different AAV vectors known to target transgene expression to either inhibitory cortical neurons (3 serotypes of AAV-h56D-tdTomato) or parvalbumin (PV)+ inhibitory cortical neurons in mice. Vectors are injected into the marmoset cortex and then postmortem tissue is analyzed following antibody labeling against GABA and PV. It is reported that: "in marmoset V1 AAV-h56D induces transgene expression in GABAergic cells with up to 91-94% specificity and 80% efficiency, depending on viral serotype and cortical layer. AAV-PHP.eB-S5E2 induces transgene expression in PV cells across all cortical layers with up to 98% specificity and 86-90% efficiency."

These claims are largely supported but slightly exaggerated relative to the actual values in the results presented. In particular, the overall efficiency for the best h56D vectors described in the results is: "Overall, across all layers, AAV9 and AAV1 showed significantly higher coverage (66.1{plus minus}3.9 and 64.9%{plus minus}3.7)". The highest coverage observed is just in middle layers and is also less than 80%: "(AAV9: 78.5%{plus minus}9.1; AAV1: 76.9%{plus minus}7.4)".

In the abstract, we indeed summarize the overall data and round up the decimals, and state that these percentages are upper bound but that they vary by serotype and layer while in the Results we report the detailed counts with decimals. To clarify this, in the revised version of the Abstract we have changed 80% to 79% and emphasize even more clearly the dependence on serotype and layer. We have amended this sentence of the Abstract as follows: “We show that in marmoset V1 AAV-h56D induces transgene expression in GABAergic cells with up to 91-94% specificity and 79% efficiency, but this depends on viral serotype and cortical layer.”

For the AAV-PHP.eB-S5E2 the efficiency reported in the abstract (“86-90%) is also slightly exaggerated relative to the results: “Overall, across all layers coverage ranged from 78%{plus minus}1.9 for injection volumes >300nl to 81.6%{plus minus}1.8 for injection volumes of 100nl.”

Indeed, the numbers in the Abstract are upper bounds, for example efficiency in L4A/B with S5E2 reaches 90%. To further clarify this important point, in the revised abstract we now state ”AAV-PHP.eB-S5E2 induces transgene expression in PV cells across all cortical layers with up to 98% specificity and 86-90% efficiency, depending on layer”.

These data will be useful to others who might be interested in targeting transgene expression in these cell types in monkeys. Suggestions for improvement are to include more details about the vectors injected and to delete some comments about results that are not documented based on vectors that are not described (see below).

Major comments:

Details provided about the AAV vectors used with the h56D enhancer are not sufficient to allow assessment of their potential utility relative to the results presented. All that is provided is: "The fourth animal received 3 injections, each of a different AAV serotype (1, 7, and 9) of the AAV-h56D-tdTomato (Mehta et al., 2019), obtained from the Zemelman laboratory (UT Austin)." At a minimum, it is necessary to provide the titers of each of the vectors. It would also be helpful to provide more information about viral preparation for both these vectors and the AAVPHP.eB-S5E2.tdTomato. Notably, what purification methods were used, and what specific methods were used to measure the titers?

We thank the Reviewer for this comment. In the revised version of the manuscript, we now provide a new Supplementary Table 1 with titers and other information for each viral vector injection. We also provide information regarding viral preparation in a new sections in the Methods entitled “ Viral Preparation”  (p12).

The first paragraph of the results includes brief anecdotal claims without any data to support them and without any details about the relevant vectors that would allow any data that might have been collected to be critically assessed. These statements should be deleted. Specifically, delete: “as well as 3 different kinds of PV-specific AAVs, specifically a mixture of AAV1-PaqR4-Flp and AAV1-h56D-mCherry-FRT (Mehta et al., 2019), an AAV1-PV1-ChR2-eYFP (donated by G. Horwitz, University of Washington),” and delete “Here we report results only from those vectors that were deemed to be most promising for use in primate cortex, based on infectivity and specificity. These were the 3 serotypes of the GABA-specific pAAV-h56D-tdTomato, and the PV-specific AAVPHP.eB-S5E2.tdTomato.” These tools might in fact be just as useful or even better than what is actually tested and reported here, but maybe the viral titer was too low to expect any expression.

These data are indeed anecdotal, but we felt this could be useful information, potentially preventing other primate labs from wasting resources, animals and time, particularly, as some of these vectors have been reported to be selective and efficient in primate cortex, which we have not been able to confirm. We made several injections in several animals of those vectors that failed either to infect a sufficient number of cells or turned out to be poorly specific. Therefore, the negative results have been consistent in our hands. But we agree with the Reviewer that our negative results could have depended on factors such as titer. In the revised version of the manuscript, following the reviewer’s suggestion, we have deleted this information.

Based on the description in the Methods it seems that no antibody labeling against TdTomato was used to amplify the detection of the transgenes expressed from the AAV vectors. It should be verified that this is the case - a statement could be added to the Methods.

That is indeed the case. We used no immunohistochemistry to enhance the reporter proteins as this was unnecessary. The native/ non-amplified tdT signal was strong. This is now stated in the methods (p.12).

Reviewer #3 (Public Review):

Summary:

Federer et al. describe the laminar profiles of GABA+ and of PV+ neurons in marmoset V1. They also report on the selectivity and efficiency of expression of a PV-selective enhancer (S5E2). Three further viruses were tested, with a view to characterizing the expression profiles of a GABA-selective enhancer (h56d), but these results are preliminary.

Strengths:

The derivation of cell-type specific enhancers is key for translating the types of circuit analyses that can be performed in mice - which rely on germline modifications for access to cell-type specific manipulation - in higher-order mammals. Federer et al. further validate the utility of S5E2 as a PV-selective enhancer in NHPs.

Additionally, the authors characterize the laminar distribution pattern of GABA+ and PV+ cells in V1. This survey may prove valuable to researchers seeking to understand and manipulate the microcircuitry mediating the excitation-inhibition balance in this region of the marmoset brain.

Weaknesses:

Enhancer/promoter specificity and efficiency cannot be directly compared, because they were packaged in different serotypes of AAV.

The three different serotypes of AAV expressing reporter under the h56D promoter were only tested once each, and all in the same animal. There are many variables that can contribute to the success (or failure) of a viral injection, so observations with an n=1 cannot be considered reliable.

This is an important point that was also brough up by Reviewer 1, which we have addressed in our reply-to-Reviewer 1. For clarity and convenience, below we copy our response to Reviewer 1.

“We are aware of the limitations of our results on the AAV-h56D. We agree with the Reviewer that a single injection per serotype does not allow us to make strong statements about differences between the 3 serotypes. Therefore, in the revised version of the manuscript we will temper our claims about such differences and use more caution in the interpretation of these data. Despite this weakness, we feel that these data still demonstrate high efficiency and specificity across cortical layers of transgene expression in GABA cells using the h56D promoter, at least with two of the 3 AAV serotypes we tested. We feel that in itself this is sufficiently useful information for the primate community, worthy of being reported. Due to cost, time and ethical considerations related to the use of primates, we chose not to perform additional experiments to determine precise differences among serotypes. Thus, for example, while it is possible that had we replicated these experiments, serotype 7 would have proven equally efficient and specific as the other two serotypes, we felt answering this question did not warrant additional experiments in this precious species.”

The language used throughout conflates the cell-type specificity conferred by the regulatory elements with that conferred by the serotype of the virus.

Authors’ reply. In the revised version of the manuscript, we have corrected ambiguous language throughout.

Recommendations for the authors

Reviewer #1 (Recommendations For The Authors):

My Public Review comments can be addressed by dialing down the interpretation of the data or providing appropriate caveats in the presentation of the relevant results and their discussion.

We have done so. See text additions on p. 6 of the Results and p.10 of the Discussion.

Minor comments:

92% of PV+ neurons in the marmoset cortex were GABAergic. Can the authors speculate on the identity of the 8% PV+/GABA- neurons (e.g., on the basis of morphology)? Are they likely excitatory? Are they more likely to represent failures of GABA staining?

We do not know what the other 8% of PV+/GABA- neurons are because we did not perform any other kind of IHC staining. Our best guess is that at least to some extent these represent failures of GABA staining, which is always challenging to perform in primate cortex. However, in mouse PV expression has been demonstrated in a minority of excitatory neurons.

"Coverage of the PV-AAV was high, did not depend on injection volume.." The fact that the coverage did not depend on injection volume presumably depends, at least in part, on how ROIs were selected. Surely different volumes of injection transduce different numbers of neurons at different distances from the injection track. This should be clarified.

The ROIs were selected at the center of the injected site/expression core from sections in which the expression region encompassed all cortical layers. Of course, larger volumes of injection resulted in larger transduced regions and therefore overall larger number of transduced neurons, but we counted cells only withing 100 µm wide ROIs at the center of the injection and the percent of transduced PV cells in this core region did not vary significantly across volumes. We have clarified the methods of ROI selection (see Methods pp. 13).

Figure 2. What is meant by “absolute” in the legend for Figure 2? (How does “mean absolute density” differ from “mean density?”)

We meant not relative, but this is obvious from the units, so we have removed the word “absolute” in the legend.

Some non-significant p-values are indicated by "p>0.05" whereas others are given precisely (e.g., p = 1). Please provide precise p-values throughout. Also, the p-value from a surprisingly large number of comparisons in the first section of the results is "1". Is this due to rounding? Is it possible to get significance in a Bonferroni-corrected Kruskal-Wallis test with only 6 observations per condition?

We now report exact p values throughout the manuscript (with a couple of exceptions where, in order to avoid reporting a large number of p values which interrupts the flow of the manuscript) we provide the upper bound value and state all those comparisons were below that value). The minimum sample size for Kruskall Wallis is 5, for each group being compared, and we our sample is 6 per group.

Figure 3: The density of tdTomato-expressing cells appears to be greater at the AAV9 injection site than at the AAV1 injection site in the example sections shown. Might some of the differences between serotypes be due to this difference? I would imagine that resolving individual cells with certainty becomes more difficult as the amount of tdTomato expression increases.

There was an error in the scale bar of Fig. 3C, so that the AAV1 injection site was shown at higher magnification than indicated by the wrong scale bar. Hence the density of tdTomato appeared lower than it is. Moreover, the tdT expression region shown in Fig. 3A is a merge of two sections, while it is only from a single section in panels B and C, leading to the impression of higher density of infected cells in panel A. The pipette used for the injection in panel A was not inserted perfectly vertical to the cortical surface, resulting in an injection site that did not span all layers in a single section; thus, to demonstrate that the injection indeed encompassed all layers (and that the virus infected cells in all layers), we collapsed label from two sections. We have now corrected the magnification of panel C so that it matches the scale bar in panel A, and specify in the figure legend that panel A label is from two sections.

Text regarding Figure 3: The term “injection sizes” is confusing. I think it is intended to mean “the area over which tdTomato-expressing cells were found” but this should be clarified.

Throughout the manuscript, we have changed the term injection site to “viral-expression region”.

Figure 3: What were the titers of the three AAV-h56D vectors?

Titers are now reported in the new Supplementary Table 1.

Figure 3: The yellow box in Figure 3C is slightly larger than the yellow boxes in 3A and 3B. Is this an error or should the inset of Figure 3 have a scale bar that differs from the 50 µm scale bar in 3A?

There were indeed errors in scale bars in this figure, which we have now corrected. Now all boxes have the same scale bar.

Was MM423 one of the animals that received the AAV-h56D injections or one of the three that received AAV-S5E2 injection?

This is an animal that received a 315nl injection of AAV-PHP.eB-S5E2.tdTomato. This is now specified in the Methods (see p. 12) and in the new Supplementary Table 1.

Please provide raw cell counts and post-injection survival times for each animal.

We now provide this information in Supplementary Tables 1 and 2.

How were the different injection volumes of the AAV-S5E2 virus arranged by animal? Which volume of the AAV-S5E2 virus was injected into the two animals who received single injections?

We now provide this information in Supplementary Table 1.

Figure 6A: the point is made in the text that "[the distribution of tdT+ and PV+ neurons] did not differ significantly... peaking in L2/3 and 4C " Is the fact that the number of tdT+ and PV+ peak in layers 2/3 and 4C a consequence of these layers being thicker than the others? If so, this statement seems trivial.

No, and this is the reason why we measured density in addition to percent of cells across layers in Figure 2. Figure 2B shows that even when measuring density, therefore normalizing by area, GABA+ and PV+ cell density still peaks in L2/3 and 4. Thus, these peaks do not simply reflect the greater thickness of these layers.

Do the authors have permission to use data from Xu et al. 2010?

Yes, we do.

Reviewer #2 (Recommendations For The Authors):

Minor comments:

"Viral strategies to restrict gene expression to PV neurons have also been recently developed (Mehta et al., 2019; Vormstein-Schneider et al., 2020)." Mich et al. should also be cited here. Cell Rep. 2021;34(13):108754.

We thank the reviewer for pointing out this missing references. This is now cited.

“GABA density in L4C did not differ from any other layers, but the percent of GABA+ cells in L4C was significantly higher than in L1 (p=0.009) and 4A/B (p=<0.0001).” This and other similar observations depend on calculating the percentage of cells relative to the total number of DAPI-labeled cells in each layer. Since it is apparent that there must be considerable variability between layers, it would be helpful to add a histogram showing the densities of all DAPI-labeled cells for each layer.

This is not how we calculated density. Density, as now clarified in the Results on p. 4, was defined as the number of cells per unit area. Counts in each layer were divided by each layers’ counting area. This corrects for differences in number of total labeled cells per layer. Therefore, reporting DAPI density is not necessary (we did not count DAPI cell density per layer).

"Identical injection volumes of each serotype, delivered at 3 different cortical depths (see Methods), resulted in different injection sizes, suggesting the different serotypes have different capacity of infecting cortical neurons. AAV7 produced the smallest injection site, which additionally was biased to the superficial and deep layers, with only few cells expressing tdT in the middle layers (Fig. 3B). AAV9 (Fig. 3A) and AAV1 (Fig. 3C) resulted in larger injection sites and infected all cortical layers." Differences noted here might reflect either differences related to the AAV serotype or to differences in titers. Please add details about titers for each vector and add comments as appropriate. Another interpretation would be that there are differences in viral spread within the tissue.

We have now added Supplementary Table 1 which reports titers in addition to other information about injections. The titers and volumes used for AAV9 and AAV7 were identical, while the titer for AAV1 was higher. Therefore, the differences in infectivity, particularly the much smaller expression region obtained with AAV7 cannot be attributed to titer. Likely this is due to differences in tropism and/or viral spread among serotypes. This is now discussed (see Results p. 5bottom and 6 top).

“Recently, several viral vectors have been identified that selectively and efficiently restrict gene expression to GABAergic neurons and their subtypes across several species, but a thorough validation and characterization of these vectors in primate cortex has lacked.” Is this really a fair statement, or is the characterization presented here also lacking? Methods used by others for quantifying specificity and efficiency are essentially the same as used here. See for example Mich et al. (which is not cited).

The original validation in primates of the vectors examined in our study was based on small tissue samples and did not examine the laminar expression profile of transgene expression induced by these enhancer-AAVs. For example, the validation of the h56D-AAV in marmoset cortex in the original paper by Mehta et al (2019) was performed on a tissue biopsy with no knowledge of which cortical layers were included in the tissue sample. The only study that shows laminar expression in primate cortex (Mich et al., which is now cited), only shows qualitative images of viral expression across layers, reporting total specificity and coverage pooled across samples; moreover, the study by Mich et al.  deals with different PV-specific enhancers than the ones characterized in our study. Unlike any of the previous studies, here we have quantified specificity and coverage across layers.

"Specifically, we have shown that the GABA-specific AAV9-h56D (Mehta et al., 2019) induces transgene expression in GABAergic cells with up to 91-94% specificity and 80% coverage, and the PV-specific AAV-PHP.eB-S5E2 (Vormstein-Schneider et al., 2020) induces transgene expression in PV cells with up to 98% specificity and 86-90% coverage." These statements in the discussion repeat the somewhat exaggerated coverage numbers noted above for the Abstract.

The averages across all layers are reported in the Results. The Discussion, abstract and discussion report upper limits, and this is made clear by stating “up to”, and now we have also added “depending on layer”.

Reviewer #3 (Recommendations For The Authors):

Abstract:

• Ln 2: Can you be more specific about what you mean by the 'various functions of inhibition'? e.g. do you mean 'the various inhibitory influences on the local microcircuit' or similar?

These are listed in the introduction to the paper but there is no space in the abstract to do so. Now the sentence reads: “various computational functions of…”.

• Ln 5: 'has' to 'is'/'has been'.

The grammar here is correct “has derived”.

• Ln 6: humans are primates! Maybe change this to 'nonhuman primates'?

We have added “non-human”

• Ln n-1: 'viral vectors represent' -> 'viral vectors are'.

We have changed it to “are”

Intro:

• Many readers may expect 'VIP' to be listed as the third major sub-class of interneurons. Could you note that the 5HT3a receptor-expressing group includes VIP cells?

Done (p.3).

• "Understanding cortical inhibitory neuron function in the primate is critical for understanding cortical function and dysfunction in the model system closest to humans" - this seems close to being circular logic (not quite, but close). Could you modify this sentence to reflect why understanding cortical function and dysfunction in NHP may be of interest?

This sentence now reads (p.3):” Understanding cortical inhibitory neuron function in the primate is critical for understanding cortical function and dysfunction in the model system closest to humans, where cortical inhibitory neuron dysfunction has been implicated in many neurological and psychiatric disorders, such as epilepsy, schizophrenia and Alzheimer’s disease (Cheah et al., 2012; Verret et al., 2012; Mukherjee et al., 2019)”. We also note that this was already stated in the previous version of the paper but in the Discussion section which read (and still reads on p. 9 2nd paragraph): “It is important to study inhibitory neuron function in the primate, because it is unclear whether findings in mice apply to higher species, and inhibitory neuron dysfunction in humans has been implicated in several neurological and psychiatric disorders (Marin, 2012; Goldberg and Coulter, 2013; Lewis, 2014).”.

• "In particular, two recent studies have developed recombinant adeno-associated viral vectors (AAV) that restrict gene expression to GABAergic neurons". This sentence places the emphasis on the wrong component of the technology. The fact that AAV was used is irrelevant; these constructs could equally have been packaged in a lenti, CAV, HSV, rabies, etc. The emphasis should be on the recently developed regulatory elements (the enhancers/promoters).

Same problem with the following excerpts; this text implies that the serotype/vector confers cell-type selectivity, but the results presented do not support this assertion (the promoter/enhancer is what confers the selectivity).

• "specifically, three serotypes of an AAV that restricts gene expression to GABAergic neurons".

• "one serotype of an AAV that restricts gene expression to PV cells".

• "GABA- and PV-specific AAVs".

• "GABA-specific AAV" (in results).

• "PV-specific AAVs".

• "In this study, we have characterized several AAV vectors designed to restrict expression to GABAergic cells" (in discussion).

• "GABA-virus". GABA is a NT, not a virus.

We have modified the language in all these sections and throughout the manuscript.

Results:

• Enhancer specificity and efficiency cannot be directly compared, because they were packaged in different serotypes of AAV.

We agree, and in fact we are not making comparisons between different enhancers (i.e., S5E2 and h56D).

The three different serotypes of AAV expressing reporter under the h56D promoter were only tested once each, and all in the same animal. There are many variables that can contribute to the success (or failure) of a viral injection, so observations with an n=1 cannot be considered reliable.

The authors need to either: (1) replicate the h56D virus injections in (at least) a second animal, or (2) rewrite the paper to focus on the AAV.PhP mDlx virus alone - for which they have adequate data - and mention the h56D data as an anecdotal result, with clear warnings about the preliminary nature of the observations due to lack of replication.

We agree about the lack of sufficient data to make strong statements about the differences between serotypes for the h56D-AAV. In the revised version of the manuscript, following the Reviewers’ suggestion, we have chosen to temper our claims about differences between serotypes for the h56D enhancer and use more caution in the interpretation of these data. We feel that these data still demonstrate sufficiently high efficiency and specificity across cortical layers of transgene expression in GABA cells using the h56D promoter, at least with two of the 3 AAV serotypes we tested, to warrant their use in primates. Due to cost, time and ethical considerations related to the use of primates, we chose not to perform additional experiments to determine precise differences among serotypes. Thus, for example, while it is possible that had we replicated these experiments, serotype 7 could have proven equally efficient and specific as the other two serotypes, we felt answering this question did not warrant additional experiments in this precious species. Our edits in regard to this point can be found in the Results on p. 6 and Discussion on p. 10.

• Did the authors compare h56D vs mDlx? This would be a useful and interesting comparison.

We did not.

• 3 tissue sections were used for analysis. How were these selected? Did the authors use a stereological approach?

For the analysis in Fig. 2, the 3 sections were randomly selected and for the positioning of the ROIs we selected a region in dorsal V1 anterior to the posterior pole  (to avoid laminar distortions due to the curvature of the brain). This is now specified (see p. 4).

• "both GABA+ and PV+ cells peak in layers" revise for clarity (e.g., the counts peak).

In now reads “GABA+ and PV+ cell percent and density” (see p.4).

• "we refer to this virus as GABA-AAV" these are 3 different viruses!

The idea here was to use an abbreviation instead of using the full viral name every single time. Clearly the reviewer does not like this, so we have removed this convention throughout the paper and now specify the entire viral name each time.

• "Identical injection volumes of each serotype, delivered at 3 different cortical depths (see Methods), resulted in different injection sizes". Do you mean 'resulted in different volumes of expression'?

Yes. We have now rephrased this as follows: “…resulted in viral expression regions that differed in both size as well as laminar distribution” (p.5).

• “suggesting the different serotypes have different capacity of infecting cortical neurons”. You can’t draw any firm conclusions from a single injection. The rest of this section of the results, along with the whole of Figure 4, and Figure 7a-d, is in danger of being misleading. Please remove. The best you can do here is to say ‘we injected 3 different viruses that express reporter under the h56D promoter. The results are shown in Figure 3, but these are anecdotal, as only a single injection of each virus was performed’. You could then note in the discussion to what extent these results are consistent with the existing literature (e.g., AAV9 often produces good coverage in NHP – anterograde and retrograde, AAV1 also works well in the CNS, although generally doesn’t infect as aggressively as AAV9. I’m not familiar with any attempts to use AAV7).

With respect to Fig. 4, our approach in the revised version is detailed above. For convenience we copy it below here. With respect to Fig 7A-D, we feel the results are more robust as the data from the 3 serotypes here were pooled together, as the 3 serotype similarly downregulated GABA and PV expression at the injection site, and we do not make any statement about differences among serotypes for the data shown in Fig. 7A-D.

“In the revised version of the manuscript, following the Reviewer ’s suggestion, we have chosen to temper our claims about differences between serotypes for the h56D enhancer and use more caution in the interpretation of these data (see revised text in the Results on p. 6 and in the Discussion on p. 10). We feel that these data still demonstrate sufficiently high efficiency and specificity across cortical layers of transgene expression in GABA cells using the h56D promoter, at least with two of the 3 AAV serotypes we tested, to warrant their use in primates. Due to cost, time and ethical considerations related to the use of primates, we chose not to perform additional experiments to determine precise differences among serotypes. Thus, for example, while it is possible that had we replicated these experiments, serotype 7 could have proven equally efficient and specific as the other two serotypes, we felt answering this question did not warrant additional experiments in this precious species.”

• Figure 3: why the large variation in tissue quality? Are the 3 upper images taken at the same magnification? If not, they need different scale bars. The cells in A (upper row) look much smaller than those in B and C, and the size of the 'inset' box varies.

We thank the reviewer for noticing this. We discovered an error in the scale bar of Fig. 3C, so that the AAV1 injection site was shown at higher magnification than indicated by the wrong scale bar. We have now corrected the error in scale bars. We have also fixed the different box sizes.

• "Overall, across all layers coverage ranged from 78%{plus minus}1.9 for injection volumes >300nl to 81.6%{plus minus}1.8 for injection volumes of 100nl." Coverage didn't differ between layers, so revise this to: "Overall, across all layers coverage ranged from 78% to 81.6%." or give an overall mean (~80%).

We have corrected the sentence as suggested by the Reviewer (see p. 8 first paragraph).

• "extending farther from the borders" -> "extending beyond the borders".

We have corrected the sentence as suggested by the Reviewer (see p. 8).

• "The reduced GABA and PV immunoreactivity caused by the viruses implies that the specificity of the viruses we have validated in this study is likely higher than estimated". Yes, but for balance you should also note that they may harm the physiology of the cell.

We have added a sentence acknowledging this to the Discussion. Specifically, on p. 10, we now state: “However, this reduced immunoreactivity raises concerns about the virus or high levels of reporter protein possibly harming the cell physiology.”

Discussion:

• "but a thorough validation and characterization of these vectors in primate cortex has lacked" better to say "has been limited", because Dimidschstein 2016 (marmoset V1) and Vormstein-schneider 2020 (macaque S1 and PFC) both reported expression in NHP.

We have added the following sentence to this paragraph of the Discussion. “In particular, previous studies have not characterized the specificity and coverage of these vectors across cortical layers.”(see p. 8).

• "whether finding in mice" -> 'whether findings in mice'.

Corrected, thanks.

• The discussion re: species differences is missing reference to Kreinen 2020 (10.1038/s41586-020-2781-z).

This reference has been added. Thanks.

• “Injections of about 200nl volume resulted in higher specificity (95% across layers) and coverage” – this is misleading. The coverage was not statistically different among injection volumes.

We have added the following sentence: ”although coverage did not differ significantly across volumes.” (see p. 10).

• "it is possible that subtle alteration of the cortical circuit upon parenchymal injection of viruses (including AAVs) leads to alteration of activity-dependent expression of PV and GABA." Or (and I would argue, more likely) the expression of large quantities of your big reporter protein compromised the function of the cell, leading to reduced expression of native proteins. You don't mention any IHC to amplify the RFP signal, so I'm assuming that your images are of direct expression. If so, you are expressing A LOT of reporter protein.

We have added a sentence acknowledging this to the Discussion. Specifically, on p. 10, we now state: “However, this reduced immunoreactivity raises concerns about the virus or high levels of reporter protein possibly harming the cell physiology.”

Methods:

• It's difficult to piece together which viruses were injected in which monkeys, at what volumes, and at what titer. Please compile this info into a table for ease of reference (including any other relevant parameters).

We now provide a Supplementary Table 1.

eLife assessment

This important study describes the discovery and further engineering of a red light-activated, chloride-conducting Channelrhodopsin (ACR) that could be used to inhibit neuronal activity. The evidence for the spectral confirmation and biophysical characterization of MsACR and raACR, and ion selectivity are solid; however, the evidence supporting the use of the tools in vivo is incomplete and missing proper controls. In addition, benchmarking against other inhibitory tools is somewhat missing. With the in vivo part strengthened, this paper would interest neuroscientists seeking more efficient ways to inhibit neuronal activity.

Reviewer #1 (Public Review):

Summary:

The authors of this manuscript characterize new anion conducting that is more red-shifted in its spectrum than prior variants called MsACR1. An additional mutant variant of MsACR1 that is renamed raACR has a 20 nm red-shifted spectral response with faster kinetics. Due to the spectral shift of these variants, the authors proposed that it is possible to inhibit expression of MsACR1 and raACR with lights at 635 nm in vivo and in vitro. The authors were able to demonstrate inhibition in vitro and in vivo with 635 nm light. Overall the new variants with unique properties should be able to suppress neuronal activities with red-shifted light stimulation.

Strengths:

The authors were able to identify a new class of anion conducting channelrhodopsin and have variants that respond strongly to lights with wavelength >550 nm. The authors were able to demonstrate this variant, MsACR1, can alter behavior in vivo with 635 nm light.

The second major strength of the study is the development of a red-shifted mutant of MsACR1 that has faster kinetics and 20 nm red-shifted from a single mutation.

Weaknesses:

There are many claims not supported by the evidence provided in the submitted version of the manuscript and would require further experiments to support such claims.

(1) From the data shown, the red-shifted raACR work much less efficiently than MsACR1 even with 635 nm light illumination both in vivo (Figure 4D) and in vitro (Figure 3E) despite the 20 nm red-shift. This is inconsistent with the benefits and effects of red-shifting the spectrum in raACR. The authors claimed that this is due to the faster kinetics of raACR which is plausible from the data shown in Fig 3E but this could be experimentally shown if more examples of continuous illumination and pulsed illumination (such as the one shown in Fig 3D) can be shown in supplemental figures. If this is truly due to the off-kinetics, the spikes would appear after the termination of the pulses but there is little difference in the cases of continuous illumination or during illumination. The fact that 635nm is equally effective as raACR suggests that there is an overall stronger effect of MsACR1 that compensates for the red-shift of raACR.

(2) There are limited comparisons to existing variants of ACRs under the same conditions in the manuscript overall. There should be more parallel comparison with gtACR1, ZipACR and RubyACR in identical conditions in cultured cell line, cultured neurons and in vivo. In terms of overall performance, efficiency, expression in identical conditions. Without this information, it is unclear whether the effects at 635 nm is due to the expression level which can compensate for the spectral shift (which may be the case for MsACR1). The authors stated they are saving this data for another manuscript, this is important data for the current manuscript which should be presented in the existing manuscript.

(3) Despite being able to activate the channelrhodopsin with 635 nm light, the main utility of the variant would be transcranial stimulation which were not demonstrated here.

(4) For the in vivo characterization, there is no mention of animal number and results from Fig 4 and 5 appear to come from multiple samples from a single animal. This is not sufficient scientific evidence to support the claims. Fig 4 and 5 should have statistical analysis from multiple animals and not multiple measurements from single animals in each of the conditions.

(5) As reviewer 2 also pointed out, there is a lack of proper controls (in addition to the low number of animals). The authors point out the current absence of technicians in the laboratory, this should not be a reason to not attempt or do the experiments.

Reviewer #2 (Public Review):

Summary:

The authors identified a new chloride-conducting Channelrhodopsin (MsACR1) that can be activated at low light intensities and within the red part of the visible spectrum. Additional engineering of MsACR1 yielded a variant (raACR1) with increased current amplitudes, accelerated kinetics, and a 20nm red-shifted peak excitation wavelength. Stimulation of MsACR1 and raACR1 expressing neurons with 635nm in mice's primary motor cortices inhibited the animals' locomotion.

Strengths:

The in vitro characterization of the newly identified ACRs is very detailed and confirms the biophysical properties as described by the authors. Notably, the ACRs are very light sensitive and allow for efficient in vitro inhibition of neurons in the nano Watt/mm^2 range. These new ACRs give neuroscientists and cell biologists a new tool to control chloride flux over biological membranes with high temporal and spatial precision. The red-shifted excitation peaks of these ACRs could allow for multiplexed application with blue-light excited optogenetic tools such as cation-conducting channelrhodopsins or green-fluorescent calcium indicators such as GCaMP.

Weaknesses:

(1) The in-vivo characterization of MsACR1 and raACR1 lacks critical control experiments and is, therefore, too preliminary. The experimental conditions differ fundamentally between in vitro and in vivo characterizations. For example, chloride gradients differ within neurons which can weaken inhibition or even cause excitation at synapses, as pointed out by the authors. Notably, the patch pipettes for the in vitro characterization in neurons contained low chloride concentrations that might not reflect possible conditions found in vivo preparations, i.e., increasing chloride gradients from dendrites to synapses.<br /> 2nd review: The authors have addressed this comment in their rebuttal.

(2) Interestingly, the authors used soma-targeted (st) MsACR1 and raACR1 for some of their in vitro characterization yielding more efficient inhibition and reduction of co-incidental "on-set" spiking. Still, the authors do not seem to have utilized st-variants in vivo.<br /> 2nd review: The authors offered an explanation in their rebuttal and aim to add these experiments later.

(3) Most importantly, critical in vivo control experiments, such as negative controls like GFP or positive controls like NpHR, are missing. These controls would exclude potential behavioral effects due to experimental artifacts. Moreover, in vivo electrophysiology could have confirmed whether targeted neurons were inhibited under optogenetic stimulations.<br /> Some of these concerns stem from the fact that the pulsed raACR stimulation at 635 nm at 10Hz (Fig. 3E) was far less efficient compared to MsACR1, yet the in vivo comparison yielded very similar results (Fig. 4D).<br /> Also, the cortex is highly heterogeneous and comprises excitatory and inhibitory neurons. Using the synapsin promoter, the viral expression paradigm could target both types and cause differential effects, which has not been investigated further, for example, by immunohistochemistry. An alternative expression system, for example, under VGLUT1 control, could have mitigated some of these concerns.<br /> 2nd review: The authors have not added control experiments in Fig 4 yet but plan to conduct them later. They added a new set of experiments in Fig.5 in which PV neurons were exclusively targeted. However, the authors show in vivo electrophysiology demonstrating the expected inhibition of firing neurons (presumably PV neurons expressing raACR) under 635 nm light and disinhibition (presumably excitatory neurons).

(4) Furthermore, the authors applied different light intensities, wavelengths, and stimulation frequencies during the in vitro characterization, causing varying spike inhibition efficiencies. The in vivo characterization is notably lacking this type of control. Thus, it is unclear why the 635nm, 2s at 20Hz every 5s stimulation protocol, which has no equivalent in the in vitro characterization, was chosen.<br /> 2nd review: The authors offered a satisfactory explanation.

In summary, the in vivo experiments did not confirm whether the observed inhibition of mouse locomotion occurred due to the inhibition of neurons or experimental artifacts.<br /> 2nd review: New experiments were added which demonstrate the expected inhibition of raACR expressing PV neurons in vivo.

In addition, the author's main claim of more efficient neuronal inhibition would require to threshold MsACR1 and raACR1 against alternative methods such as the red-shifted NpHR variant Jaws or other ACRs to give readers meaningful guidance when choosing an inhibitory tool.<br /> The light sensitivity of MsACR1 and raACR1 are impressive and well characterized in vitro. However, the authors only reported the overall light output at the fiber tip for the in vivo experiments: 0.5 mW. Without context, it is difficult to evaluate this value. Calculating the light power density at certain distances from the light fiber or thresholding against alternative tools such as NpHR, Jaws, or other ACRs would allow for a more meaningful evaluation.<br /> 2nd review: The authors added Supl Fig. 8 in which light power density and propagation of photons at 550 nm and 635nm through brain tissue was calculated when emitted from light fibers of varying diameter.