Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Nahas et al. investigated the roles of herpes simplex virus 1 (HSV-1) structural proteins using correlative cryo-light microscopy and soft X-ray tomography. The authors generated nine viral variants with deletions or mutations in genes encoding structural proteins. They employed a chemical fixation-free approach to study native-like events during viral assembly, enabling observation of a wider field of view compared to cryo-ET. The study effectively combined virology, cell biology, and structural biology to investigate the roles of viral proteins in virus assembly and budding.

Strengths:

(1) The study presented a novel approach to studying viral assembly in cellulo.

(2) The authors generated nine mutant viruses to investigate the roles of essential proteins in nuclear egress and cytoplasmic envelopment.

(3) The use of correlative imaging with cryoSIM and cryoSXT allowed for the study of viral assembly in a near-native state and in 3D.

(4) The study identified the roles of VP16, pUL16, pUL21, pUL34, and pUS3 in nuclear egress.

(5) The authors demonstrated that deletion of VP16, pUL11, gE, pUL51, or gK inhibits cytoplasmic envelopment.

(6) The manuscript is well-written, clearly describing findings, methods, and experimental design.

(7) The figures and data presentation are of good quality.

(8) The study effectively correlated light microscopy and X-ray tomography to follow virus assembly, providing a valuable approach for studying other viruses and cellular events.

(9) The research is a valuable starting point for investigating viral assembly using more sophisticated methods like cryo-ET with FIB-milling.

(10) The study proposes a detailed assembly mechanism and tracks the contributions of studied proteins to the assembly process.

(11) The study includes all necessary controls and tests for the influence of fluorescent proteins.

Weaknesses:

Overall, the manuscript does not have any major weaknesses, just a few minor comments:

(1) The gel quality in Figure 1 is inconsistent for different samples, with some bands not well resolved (e.g., for pUL11, GAPDH, or pUL20).

We thank the reviewer for their suggestion. We tried to resolve the bands several times, but unfortunately this was the best outcome we could achieve.

(2) The manuscript would benefit from a summary figure or table to concisely present the findings for each protein. It is a large body of manuscript, and a summary figure showing the discovered function would be great.

We thank the reviewer for their suggestion. We have created a summary table (Table 2).

(3) Figure 2 lacks clarity on the type of error bars used (range, standard error, or standard deviation). It says, however, range, and just checking if this is what the authors meant.

We thank the reviewer for double-checking, but it is meant to be range, as reported in the legend. We used range because there are only two data points for each time point, which are insufficient to calculate standard deviation or standard error.

(4) The manuscript could be improved by including details on how the plasma membrane boundary was estimated from the saturated gM-mCherry signal. An additional supplementary figure with the data showing the saturation used for the boundary definition would be helpful.

We appreciate the suggestion and have included an example of how saturated gM-mCherry signal was used to delineate the cytoplasm in Supp. Fig. 4A.

(5) Additional information or supplementary figures on the mask used to filter the YFP signal for Figure 4 would be helpful.

Thanks, we have adapted the text in the results section to clarify: “eYFP-VP26 signal was manually inspected to determine threshold values that filtered out background and included pixels containing individual or clustered puncta that represent capsids.”

(6) The figure legends could include information about which samples are used for comparison for significance calculations. As the colour of the brackets is different from the compared values (dUL34), it would be great to have this information in the figure legend.

Thanks, we have adapted Fig. 4B to make the colour of the brackets match the colour used for the ΔUL34 mutant, and we have included labels next to the brackets for clarity. We have applied similar adjustments to Fig. 5D & E and Supp. Fig. 4C.

(7) In Figure 5B, the association between YFP and mCherry signals is difficult to assess due to the abundance of mCherry signal; single-channel and combined images might improve visualization.

Thanks, we have provided split and combined channel views in Supp. Fig. 4B to improve visualization.

(8) In Figure 6D, staining for tubulin could help identify the cytoskeleton structures involved in the observed virus arrays.

We thank the reviewer for their suggestion, which we think would be interesting future work to build on the current study. Given the competitive nature of access to the cryoSIM and cryoSXT, CLXT, including staining for tubulin was outside the scope of additional experiments we were able to conduct at this time.

(9) It is unclear in Figure 6D if the microtubule-associated capsids are with the gM envelope or not, as the signal from mCherry is quite weak. It could be made clearer with the split signals to assess the presence of both viral components.

We have provided split channels to the figure to aid with visualization.

(10) The representation of voxel intensity in Figure 8 is somewhat confusing. Reversion of the voxel intensity representation to align brighter values with higher absorption, which would simplify interpretation.

We thank the reviewer for this suggestion. In contrast to fluorescence microscopy where high intensities reflect signal, low intensities represent signal (absorbance of X-rays) in cryoSXT. We respectfully decided not to reverse the values, as we believe that could cause more confusion. We have instead added a black-to-white gradient bar to illustrate that low voxel intensities correspond to dark signal in Fig 8.

(11) The visualization in panel I of Figure 8 might benefit from a more divergent colormap to better show the variation in X-ray absorbance.

We thank the reviewer for their suggestion. We experimented with a few different colour schemes but concluded that the current one produced the clearest results and was most accessible for color-blind viewers.

(12) Figure 9 would be enhanced by images showing the different virus sizes measured for the comparative study, which would help assess the size differences between different assembly stages.

We thank the reviewer for their suggestion and have included images to accompany the graph.

Overall, this is an excellent manuscript and an enjoyable read. It would be interesting to see this approach applied to the study of other viruses, providing valuable insights before progressing to high-resolution methods.

Reviewer #2 (Public review):

Summary:

For centuries, humans have been developing methods to see ever smaller objects, such as cells and their contents. This has included studies of viruses and their interactions with host cells during processes extending from virion structure to the complex interactions between viruses and their host cells: virion entry, virus replication and virion assembly, and release of newly constructed virions. Recent developments have enabled simultaneous application of fluorescence-based detection and intracellular localization of molecules of interest in the context of sub-micron resolution imaging of cellular structures by electron microscopy.

The submission by Nahas et al., extends the state-of-the-art for visualization of important aspects of herpesvirus (HSV-1 in this instance) virion morphogenesis, a complex process that involves virus genome replication, and capsid assembly and filling in the nucleus, transport of the nascent nucleocapsid and some associated tegument proteins through the inner and outer nuclear membranes to the cytoplasm, orderly association of several thousand mostly viral proteins with the capsid to form the virion's tegument, envelopment of the tegumented capsid at a virus-tweaked secretory vesicle or at the plasma membrane, and release of mature virions at the plasma membrane.

In this groundbreaking study, cells infected with HSV-1 mutants that express fluorescently tagged versions of capsid (eYFP-VP26) and tegument (gM-mCherry) proteins were visualized with 3D correlative structured illumination microscopy and X-ray tomography. The maturation and egress pathways thus illuminated were studied further in infections with fluorescently tagged viruses lacking one of nine viral proteins.

Strengths:

This outstanding paper meets the journal's definitions of Landmark, Fundamental, Important, Valuable, and Useful. The work is also Exceptional, Compelling, Convincing, and Solid. The work is a tour de force of classical and state-of-the-art molecular and cellular virology. Beautiful images accompanied by appropriate statistical analyses and excellent figures. The numerous complex issues addressed are explained in a clear and coordinated manner; the sum of what was learned is greater than the sum of the parts. Impacts go well beyond cytomegalovirus and the rest of the herpesviruses, to other viruses and cell biology in general.

Reviewer #3 (Public review):

Summary:

Kamal L. Nahas et al. demonstrated that pUL16, pUL21, pUL34, VP16, and pUS3 are involved in the egress of the capsids from the nucleous, since mutant viruses ΔpUL16, ΔpUL21, ΔUL34, ΔVP16, and ΔUS3 HSV-1 show nuclear egress attenuation determined by measuring the nuclear:cytoplasmic ratio of the capsids, the dfParental, or the mutants. Then, they showed that gM-mCherry+ endomembrane association and capsid clustering were different in pUL11, pUL51, gE, gK, and VP16 mutants. Furthermore, the 3D view of cytoplasmic budding events suggests an envelopment mechanism where capsid budding into spherical/ellipsoidal vesicles drives the envelopment.

Strengths:

The authors employed both structured illumination microscopy and cellular ultrastructure analysis to examine the same infected cells, using cryo-soft-X-ray tomography to capture images. This combination, set here for the first time, enabled the authors to obtain holistic data regarding a biological process, as a viral assembly. Using this approach, the researchers studied various stages of HSV-1 assembly. For this, they constructed a dual-fluorescently labelled recombinant virus, consisting of eYFP-tagged capsids and mCherry-tagged envelopes, allowing for the independent identification of both unenveloped and enveloped particles. They then constructed nine mutants, each targeting a single viral protein known to be involved in nuclear egress and envelopment in the cytoplasm, using this dual-fluorescent as the parental one. The experimental setting, both the microscopic and the virological, is robust and well-controlled. The manuscript is well-written, and the data generated is robust and consistent with previous observations made in the field.

Weaknesses:

It would be helpful to find out what role the targeted proteins play in nuclear egress or envelopment acquisition in a different orthoherpesvirus, like HSV-2. This would confirm the suitability of the technical approach set and would also act as a way to validate their mechanism at least in one additional herpesvirus beyond HSV-1. So, using the current manuscript as a starting point and for future studies, it would be advisable to focus on the protein functions of other viruses and compare them.

We appreciate the suggestion and agree that this would be a great starting point for future studies. At present, we do not have a panel of mutant viruses in HSV-2 or another orthoherpesvirus, and it would be significant work to generate them, so we consider this outside the scope of the current study.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) There are enough uncommon abbreviations in the text to justify the inclusion of an abbreviation list.

We thank the reviewer for the suggestion, but we define all uncommon abbreviations at first mention and an abbreviations list is not part of eLife’s house style.

(2) The complex paragraph on p. 7 would be much easier to digest if broken into smaller chunks. Consider similar treatment for other lengthy landmark-free blocks of text, e.g., the one that begins on p. 14. Subheadings would help.

We thank the reviewer for this suggestion. We have divided large paragraphs into more easily digestible chunks throughout the manuscript, for example in the discussion where the previous monolithic 3rd paragraph has been divided into five shorter, focussed paragraphs.

(3) Table 1 needs units.

We thank the reviewer for noticing our omission and apologise for the oversight - the table has been updated accordingly.

Reviewer #3 (Recommendations for the authors):

(1) Toward the end of the manuscript, I missed some lines attempting to speculate on the origin/nature of the spherical/ellipsoidal vesicles providing the envelopment. Would it be possible to incorporate this in the Discussion section?

Thank you for noticing that omission. We have now included a few lines speculating that they may represent recycling endosomes, trans-Golgi network vesicles, or a hybrid compartment.

(2) I congratulate the authors. The work is robust, and I personally highlight the way they managed to include others' results merged with their own, providing a complete view of the story.

We thank the reviewer for their kind words.

Note to editors

In addition to these responses to the reviewer’s comments, we have also now included in the methods section details of the Tracking of Indels by Decomposition (TIDE) analysis we performed (data in Supplementary Figure 3) that was omitted by mistake from the original submission.

A não fruição das férias no período correto gera o dever de pagar o dobro da remuneração.

Obs.: Estava vigente a Súmula nº 450/TST, que previa o pagamento em dobro no caso de inobservância do prazo para pagamento das verbas relativas às férias, para além da hipótese legal do pagamento dobrado para fruição de férias fora do período adequado. Porém, foi julgada inconstitucional pela ADPF 501.

Ementa: ARGUIÇÃO DE DESCUMPRIMENTO DE PRECEITO FUNDAMENTAL. CONSTITUCIONAL E TRABALHISTA. SÚMULA 450 DO TRIBUNAL SUPERIOR DO TRABALHO. PAGAMENTO DA REMUNERAÇÃO DE FÉRIAS EM DOBRO QUANDO ULTRAPASSADO O PRAZO DO ART. 145 DA CLT. IMPOSSIBILIDADE DE O PODER JUDICIÁRIO ATUAR COMO LEGISLADOR POSITIVO. AUSÊNCIA DE LACUNA. INTERPRETAÇÃO RESTRITIVA DE NORMA SANCIONADORA. OFENSA À SEPARAÇÃO DE PODERES E AO PRINCÍPIO DA LEGALIDADE. PROCEDÊNCIA. - 1. Os poderes de Estado devem atuar de maneira harmônica, privilegiando a cooperação e a lealdade institucional e afastando as práticas de guerrilhas institucionais, que acabam minando a coesão governamental e a confiança popular na condução dos negócios públicos pelos agentes públicos. Precedentes. - 2. Impossibilidade de atuação do Poder Judiciário como legislador positivo, de modo a ampliar o âmbito de incidência de sanção prevista no art. 137 da CLT para alcançar situação diversa, já sancionada por outra norma. - 3. Ausência de lacuna justificadora da construção jurisprudencial analógica. Necessidade de interpretação restritiva de normas sancionadoras. Proibição da criação de obrigações não previstas em lei por súmulas e outros enunciados jurisprudenciais editados pelo Tribunal Superior do Trabalho e pelos Tribunais Regionais do Trabalho (CLT, art. 8º, § 2º). - 4. Arguição julgada procedente.

(ADPF 501, Relator(a): ALEXANDRE DE MORAES, Tribunal Pleno, julgado em 08-08-2022, PROCESSO ELETRÔNICO DJe-163 DIVULG 17-08-2022 PUBLIC 18-08-2022)

Pode segmentar as férias em até 3 períodos: - 14 - 5 - 5

Reviewer #3 (Public review):

Summary:

The authors seek to determine the underlying traits that support the exceptional capacity of Aspergillus oryzae to secrete enzymes and heterologous proteins. To do so, they leverage the availability of multiple domesticated isolates of A. oryzae along with other Aspergillus species to perform comparative imaging and genomic analysis.

Strengths:

The strength of this study lies in the use of multifaceted approaches to identify significant differences in hyphal morphology that correlate with enzyme secretion, which is then followed by the use of genomics to identify candidate functions that underlie these differences.

Weaknesses:

The authors addressed all suggestions satisfactorily.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Recommendations for the authors): 

The authors addressed all suggestions satisfactorily. 

Reviewer #2 (Recommendations for the authors):

The authors have adequately dealt with the comments. 

Reviewer #3 (Recommendations for the authors):

(1) Line 157. Although the authors have added a statement acknowledging that addition of YE increased hyphal width and secretion in A. nidulans without increasing nuclear number, they have not indicated how this result might impact their model. It might just boil down to variation between the different Aspergilli, but it merits attention. 

(2) Line 341. To extend the argument, you might consider adding this citation (https://elifesciences.org/articles/76075), which provides evidence that nuclear size might scale with osmotic pressure based on the density of macromolecules in the nucleus vs. cytoplasm.

Thanks for the suggestion.

L341 This is likely related to the phenomenon in which a decrease in cell size is accompanied by a reduction in nuclear size (66).

(3) Line 343. Neurospora crass hyphal cells can exceed 100 nuclei... 

Changed.

eLife Assessment

This study presents a valuable finding regarding the role of Arp2/3 and the actin nucleators N-WASP and WAVE complexes in myoblast fusion. The data presented is convincing, and the work will be of interest to biologists studying skeletal muscle stem cell biology in the context of skeletal muscle regeneration.

Reviewer #2 (Public review):

To fuse, differentiated muscle cells must rearrange their cytoskeleton and assemble actin-enriched cytoskeletal structures. These actin foci are proposed to generate mechanical forces necessary to drive close membrane apposition and the fusion pore formation. While the study of these actin-rich structures has been conducted mainly in drosophila and in vertebrate embryonic development, the present manuscript present clear evidence this mechanism is necessary for fusion of adult muscle stem cells in vivo, in mice. The data presented here clearly demonstrate that ARP2/3 and SCAR/WAVE complexes are required for differentiating satellite cells fusion into multinucleated myotubes, during skeletal muscle regeneration.

Reviewer #3 (Public review):

The authors have satisfactorily addressed my inquiries. However, I had to look quite hard to find where they responded to my final comment regarding the potential role of Arpc2 post-fusion during myofiber growth and/or maintenance, which I eventually located on page 7. I would appreciate it if the authors could state this point more explicitly, perhaps by adding a sentence such as "However, we cannot rule out the possibility that Arpc2 may also play a role in....." to improve clarity of communication.

While I understood from the original version that this issue falls beyond the immediate scope of the study, I believe it is important to adopt a more cautious and rigorous interpretative framework, especially given the widespread use of this experimental approach. In particular, when a gene could potentially have additional roles in myofibers, it may be helpful to explicitly acknowledge that possibility. Even if Arpc2 may not necessarily be one of them, such roles cannot be fully excluded without direct testing.

1. f.read([size])：一次性读出整个文件内容（返回字符串）。
2. f.readline()：每次读取 一行 内容（包括行末的 \n）。
3. f.readlines()：一次性把文件中所有行读到一个 列表 里。

这里x的生成写在训练批次的循环里面，循环三次，每次随机生成3张随机图片

B is supposed to be redefined as \(\mathbb{R}^3\) here, instead of \(\mathbb{R}^2\)

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1. I anticipate 4 years. 2.I/m not really sure how many I will need. 3.Turning in all of my assignments. 4.Yes I am confident.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

Summary:

This computational modeling study builds on multiple previous lines of experimental and theoretical research to investigate how a single neuron can solve a nonlinear pattern classification task. The authors construct a detailed biophysical and morphological model of a single striatal medium spiny neuron, and endow excitatory and inhibitory synapses with dynamic synaptic plasticity mechanisms that are sensitive to (1) the presence or absence of a dopamine reward signal, and (2) spatiotemporal coincidence of synaptic activity in single dendritic branches. The latter coincidence is detected by voltage-dependent NMDA-type glutamate receptors, which can generate a type of dendritic spike referred to as a "plateau potential." In the absence of inhibitory plasticity, the proposed mechanisms result in good performance on a nonlinear classification task when specific input features are segregated and clustered onto individual branches, but reduced performance when input features are randomly distributed across branches. Interestingly, adding inhibitory plasticity improves classification performance even when input features are randomly distributed.

Strengths:

The integrative aspect of this study is its major strength. It is challenging to relate low-level details such as electrical spine compartmentalization, extrasynaptic neurotransmitter concentrations, dendritic nonlinearities, spatial clustering of correlated inputs, and plasticity of excitatory and inhibitory synapses to high-level computations such as nonlinear feature classification. Due to high simulation costs, it is rare to see highly biophysical and morphological models used for learning studies that require repeated stimulus presentations over the course of a training procedure. The study aspires to prove the principle that experimentally-supported biological mechanisms can explain complex learning.

Weaknesses:

The high level of complexity of each component of the model makes it difficult to gain an intuition for which aspects of the model are essential for its performance, or responsible for its poor performance under certain conditions. Stripping down some of the biophysical detail and comparing it to a simpler model may help better understand each component in isolation.

We greatly appreciate your recognition of the study’s integrative scope and the challenges of linking detailed biophysics to high-level computation. We acknowledge that the model’s complexity can obscure the contribution of individual components. However, as stated in the introduction the principles already have been shown in simplified theoretical models for instance  in Tran-Van-Minh et al. 2015. Our aim here was to extend those ideas into a more biologically detailed setting to test whether the same principles still hold under realistic constraints. While simplification can aid intuition, we believe that demonstrating these effects in a biophysically grounded model strengthens the overall conclusion. We agree that further comparisons with reduced models would be valuable for isolating the contribution of specific components and plan to explore that in future work.  

Reviewer #2 (Public review):

Summary:

The study explores how single striatal projection neurons (SPNs) utilize dendritic nonlinearities to solve complex integration tasks. It introduces a calcium-based synaptic learning rule that incorporates local calcium dynamics and dopaminergic signals, along with metaplasticity to ensure stability for synaptic weights. Results show SPNs can solve the nonlinear feature binding problem and enhance computational efficiency through inhibitory plasticity in dendrites, emphasizing the significant computational potential of individual neurons. In summary, the study provides a more biologically plausible solution to single-neuron learning and gives further mechanical insights into complex computations at the single-neuron level.

Strengths:

The paper introduces a novel learning rule for training a single multicompartmental neuron model to perform nonlinear feature binding tasks (NFBP), highlighting two main strengths: the learning rule is local, calcium-based, and requires only sparse reward signals, making it highly biologically plausible, and it applies to detailed neuron models that effectively preserve dendritic nonlinearities, contrasting with many previous studies that use simplified models.

Thank you for highlighting the biological plausibility of our calcium- and dopamine-dependent learning rule and its ability to exploit dendritic nonlinearities. Your positive assessment reinforces our commitment to refining the rule and exploring its implications in larger, more diverse settings.

Reviewer #1 (Recommendations for the authors):

Major recommendations:

P9: When introducing the excitatory learning rule, the reader is referred to the Methods. I suggest moving Figure 7A-D, "Excitatory plasticity" to be more prominently presented in the main body of the paper where the reader needs to understand it. There are errors in the current Figure 7, and wrong/confusing acronyms. The abbreviations "LTP-K" and "MP-K" are not intuitive. In A, I would spell out "LTP kernel" and "Theta_LTP adaptation".  In B, I would spell out "LTD kernel" and "Theta_LTD adaptation".

We have clarified the terminology in Figure 7 by replacing “LTP-K” with “LTP kernel” and “MP-K” with “metaplasticity kernel”.  While we kept Figure 7 in the Methods section to maintain the flow of the main text, we agree that an earlier introduction of the learning rule improves clarity. To that end, we added a simplified schematic to Figure 3 in the Results section, which provides readers with an accessible overview of the excitatory plasticity mechanism at the point where it is first introduced.

In C, for simplicity and clarity, I would only show the initial and updated LTP kernel and Calcium and remove the Theta_LTP adaptation curve, it's too busy and not necessary. Similarly in D, I would show only the initial and updated LTD kernel and Calcium and remove the Theta_LTD adaptation curve. In the current version of the Figure, panel B, right incorrectly labels "Theta_LTD" as "Theta_LTP". Panel D incorrectly labels "LTD kernel" as "LTP/MP-K" in the subheading and "MP/LTP-K" in the graph.

To avoid confusion and better illustrate the interactions between calcium signals, kernels, and thresholds, we have added a movie showing how these components evolve during learning. The figure panels remain as originally designed, since the LTP kernel governs both potentiation and depression through metaplastic threshold adaptation, while the LTD kernel remains fixed.

P17: Again, instead of pointing the reader to the Methods, I would move Figure 7E, "Inhibitory plasticity" to the main body of the paper where the reader needs to understand it. For clarity, I would label "C_TL" and "Theta_Inh,low" and "C_TH" as "Theta_Inh,high". The right panel could be better labeled "Inhibitory plasticity kernel". The left panel could be better labeled "Theta_Inh adaptation", with again replacing the acronyms "C_TL" and "C_TH". The same applies to Fig. 5D on P19.

We have updated the labeling in Figures 5D and 7E for clarity, including replacing "C_TL" and "C_TH" with "Theta_Inh,low" and "Theta_Inh,high". In addition, we added a simplified schematic of the inhibitory plasticity rule to Figure 5 to assist the reader’s understanding when presenting the results. Figure 7E remains in the Methods section to preserve the flow of the main text.

P12: I would suggest simplifying Fig. 3 panels and acronyms as well. Remove "MP-K" from C and D. Relabel "LTP-K" as "LTP kernel". The same applies to Fig. 5E on P19 and Fig. 3 - supplement 1 on P46 and Fig 6 - supplement 1 on P49.

We have simplified the labeling across all relevant figures by replacing “MP-K” with “metaplasticity kernel” and “LTP-K” with “LTP kernel.” To maintain clarity, we retained these terms in only one panel as a reference.

Minor recommendations:

P4: "Although not discussed much in more theoretical work, our study demonstrates the necessity of metaplasticity for achieving stable and physiologically realistic synaptic weights." This sentence is jarring. BCM and metaplasticity has been discussed in hundreds of theory papers! Cite some. This sentence would more accurately read, "Our study corroborates prior theory work (citations) demonstrating that metaplasticity helps to achieve stable and physiologically realistic synaptic weights."

We have followed the reviewers suggestion and updated the sentence to: Previous theoretical studies (Bienenstock et al., 1982; Fusi et al., 2005; Clopath et al., 2010; Benna & Fusi, 2016; Zenke & Gerstner, 2017) demonstrate the essential role of metaplasticity in maintaining stability in synaptic weight distributions. (page 2 line 49-51, page 3 line 1)

P9: Grammar. "The neuron model was during training activated..." should read "During training, the neuron model was activated..."

Corrected

P17: Lovett-Barron et al., 2012 is appropriately cited here. Milstein et al., Neuron, 2015 also showed dendritic inhibition regulates plateau potentials in CA1 pyramidal cells in vitro, and Grienberger et al., Nat. Neurosci., 2017 showed it in vivo.

P19 vs P16 vs P21. Fig. 4B, Fig. 5B, and Fig. 6B choose different strategies to show variance across seeds. Please choose one strategy and apply to all comparable plots.

We thank the reviewer for these helpful points.

We have added the suggested citations (Milstein et al., 2015; Grienberger et al., 2017) alongside Lovett-Barron et al., 2012. 

Variance across seeds is now displayed uniformly (mean is solid line STD is shaded area) in Figures 4B, 5B, and 6B.

Reviewer #2 (Recommendations for the authors):

Major Points:

(1)  Quality of Scientific Writing:

i. Mathematical and Implementation Details:

I appreciate the authors' efforts in clarifying the mathematical details and providing pseudocode for the learning rule, significantly improving readability and reproducibility. The reference to existing models via GitHub and ModelDB repositories is acceptable. However, I suggest enhancing the presentation quality of equations within the Methods section-currently, they are low-resolution images. Please consider rewriting these equations using LaTeX or replacing them with high-resolution images to further improve clarity.

We appreciate the reviewer’s comment regarding clarity and reproducibility. In response, we have rewritten all equations in LaTeX to improve their readability and presentation quality in the Methods section.

ii. Figure quality.

I acknowledge the authors' effort to improve figure clarity and consistency throughout the manuscript. However, I notice that the x-axis label "[Ca]_v (μm)" in Fig. 7E still appears compressed and unclear. Additionally, given the complexity and abundance of hyperparameters or artificial settings involved in your experimental design and learning rule (such as kernel parameters, metaplasticity kernels, and unspecific features), the current arrangement of subfigures (particularly Fig. 3C, D and Fig. 5D, E) still poses readability challenges. I recommend reordering subfigures to present primary results (e.g., performance outcomes) prominently upfront, while relegating visualizations of detailed hyperparameter manipulations or feature weight variations to later sections or the discussion, thus enhancing clarity for readers.

We thank the reviewer for pointing out the readability issue. We have corrected the x-axis label in Figure 7D. We hope this new layout with a simplified rule in Fig 3 and Fig 5   presents the key findings while retaining full mechanistic detail to make it easier to understand the model behavior.  

iii. Writing clarity.

The authors have streamlined the "Metaplasticity" section and reduced references to dopamine, which is a positive step. However, the broader issue remains: the manuscript still appears overly detailed and more like a technical report of a novel learning rule, rather than a clearly structured scientific paper. I strongly recommend that the authors further distill the manuscript by clearly focusing on one or two central scientific questions or hypotheses-for instance, emphasizing core insights such as "inhibitory inputs facilitate nonlinear dendritic computations" or "distal dendritic inputs significantly contribute to nonlinear integration." Clarifying and highlighting these primary scientific questions early and consistently throughout the manuscript would substantially enhance readability and impact.

We appreciate the reviewer’s guidance on improving the manuscript’s clarity and focus.In response, we now highlight two central questions at the end of the Introduction and have retitled the main Results subsections to follow this thread, thereby sharpening the manuscript’s focus while retaining necessary technical detail (page3 line 20-28).We have also removed redundant passages and simplified technical details to improve overall readability .

Minor:

(1) The [Ca]NMDA in Figure 2A and 2C can have large values even when very few synapses are activated. Why is that? Is this setting biologically realistic?

The authors acknowledge that their simulated [Ca²⁺] levels exceed typical biological measurements but claim that the learning rule remains robust across variations in calcium concentrations. However, robustness to calcium variations was not explicitly demonstrated in the main figures. To convincingly address this concern, I recommend the authors explicitly test and present whether adopting biologically realistic calcium concentrations (~1 μM) impacts the learning outcomes or synaptic weight dynamics. Clarifying this point with a supplemental analysis or an additional figure panel would significantly strengthen their argument regarding the model's biological plausibility and robustness.

We thank the reviewer for the comment. The elevated [Ca^²⁺]_NMDA values reflect localized transients in spine heads with narrow necks and high NMDA conductance. These values are not problematic for our model, as the plasticity rule depends on relative calcium differences rather than absolute levels as the metaplasticity kernel will adjust. In future versions of our detailed neuron model, we will likely decrease the spine axial resistance of the spine neck.

If you leave out the 3*F it becomes more general. Trees per acre is just the sum of tree expansion factors. Then it can also be used for unequal probability designs in which expansion factors might vary with tree size

Reviewer #2 (Public review):

Summary:

In this study, Mondal and co-authors present the development of a computational model of homeostatic plasticity incorporating activity-dependent regulation of gating properties (activation, inactivation) of ion channels. The authors show that, similar to what has been observed for activity-dependent regulation of ion channel conductances, implementing activity-dependent regulation of voltage sensitivity participates in the achievement of a target phenotype (bursting or spiking). The results however suggest that activity-dependent regulation of voltage sensitivity is not sufficient to allow this and needs to be associated with the regulation of ion channel conductances in order to reliably reach target phenotype. Although the implementation of this biologically relevant phenomenon is undeniably relevant, a few important questions are left unanswered.

Strengths:

(1) Implementing activity-dependent regulation of gating properties of ion channels is biologically relevant.

(2) The modeling work appears to be well performed and provides results that are consistent with previous work performed by the same group.

Weaknesses:

(1) The main question not addressed in the paper is the relative efficiency and/or participation of voltage-dependence regulation compared to channel conductance in achieving the expected pattern of activity. Is voltage-dependence participating to 50% or 10%. Although this is a difficult question to answer (and it might even be difficult to provide a number), it is important to determine whether channel conductance regulation remains the main parameter allowing the achievement of a precise pattern of activity (or its recovery after perturbation).

(2) Another related question is whether the speed of recovery is significantly modified by implementing voltage-dependence regulation (it seems to be the case looking at Figure 3). More generally, I believe it would be important to give insights into the overall benefit of implementing voltage-dependence regulation, beyond its rather obvious biological relevance.

(3) Along the same line, the conclusion about how voltage-dependence regulation and channel conductance regulation interact to provide the neuron with the expected activity pattern (summarized and illustrated in Figure 6) is rather qualitative. Consistent with my previous comments, one would expect some quantitative answers to this question, rather than an illustration that approximately places a solution in parameter space.

Reviewer #3 (Public review):

Mondal et al. use computational modeling to investigate how activity-dependent shifts in voltage-dependent (in)activation curves can complement changes in ion channel conductance to support homeostatic plasticity. While it is well established that the voltage-dependent properties of ion channels influence neuronal excitability, their potential role in homeostatic regulation, alongside conductance changes, has remained largely unexplored. The results presented here demonstrate that activity-dependent regulation of voltage dependence can interact with conductance plasticity to enable neurons to attain and maintain target activity patterns, in this case, intrinsic bursting. Notably, the timescale of these voltage-dependent shifts influences the final steady-state configuration of the model, shaping both channel parameters and activity features such as burst period and duration. A major conclusion of the study is that altering this timescale can seamlessly modulate a neuron's intrinsic properties, which the authors suggest may be a mechanism for adaptation to perturbations.

While this conclusion is largely well-supported, additional analyses could help clarify its scope. For instance, the effects of timescale alterations are clearly demonstrated when the model transitions from an initial state that does not meet the target activity pattern to a new stable state. However, Fig. 6 and the accompanying discussion appear to suggest that changing the timescale alone is sufficient to shift neuronal activity more generally. It would be helpful to clarify that this effect primarily applies during periods of adaptation, such as neurodevelopment or in response to perturbations, and not necessarily once the system has reached a stable, steady state. As currently presented, the simulations do not test whether modifying the timescale can influence activity after the model has stabilized. In such conditions, changes in timescale are unlikely to affect network dynamics unless they somehow alter the stability of the solution, which is not shown here. That said, it seems plausible that real neurons experience ongoing small perturbations which, in conjunction with changes in timescale, could allow gradual shifts toward new solutions. This possibility is not discussed but could be a fruitful direction for future work.

Editor's note: The authors have adequately addressed the concerns raised in the public reviews above, as well as the previous recommendations, and revised the manuscript where necessary.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

I still have a bone to pick with the claim that "activity-dependent changes in channel voltage-dependence alone are insufficient to attain bursting". As I mentioned in my previous comment, this is also the case for the gmax values (channel density). If you choose the gmax's to be in a reasonable range, then the statement above is simply cannot be true. And if, in contrast, you choose the activation/inactivation parameters to be unreasonable, then no set of gmax's can produce proper activity. So I remain baffled what exactly is the point that the authors are trying to make.

We thank the reviewer for this clarification. We did not intend to imply that voltage-dependence modulation is universally incapable of supporting bursting or that conductance changes alone are universally sufficient. To avoid any overstatement, we now write:

“…activity-dependent changes in channel voltage-dependence alone did not assemble bursting from these low-conductance initial states (cf. Figure 1B)”.

Reviewer #2 (Public review):

(1) The main question not addressed in the paper is the relative efficiency and/or participation of voltage-dependence regulation compared to channel conductance in achieving the expected pattern of activity. Is voltage-dependence participating to 50% or 10%. Although this is a difficult question to answer (and it might even be difficult to provide a number), it is important to determine whether channel conductance regulation remains the main parameter allowing the achievement of a precise pattern of activity (or its recovery after perturbation).

We appreciate the reviewer’s interest in a quantitative partitioning of the contributions from voltage-dependence regulation versus conductance regulation. We agree that this would be an important analysis in principle. In practice, obtaining this would be difficult.

Our goal here was to establish the principle: that half-(in)activation shifts can meaningfully influence recovery. This is not an obvious result, given that these two processes can act on vastly different timescales.

That said, our current dataset does provide partial quantitative insight. Eight of the twenty models required some form of voltage-dependence modulation to recover; among these, two only recovered under fast modulation and two only under slow modulation. This demonstrates that voltage-dependence regulation is essential for recovery in some neurons, and its timescale critically shapes the outcome.

(2) Another related question is whether the speed of recovery is significantly modified by implemeting voltage-dependence regulation (it seems to be the case looking at Figure 3). More generally, I believe it would be important to give insights into the overall benefit of implementing voltage-dependence regulation, beyond its rather obvious biological relevance.

Our current results suggest that voltage-dependence regulation can indeed accelerate recovery, as illustrated in Figure 3 and supported by additional simulations (not shown). However, a fully quantitative comparison (e.g., time-to-recovery distributions or survival analysis) would require a much larger ensemble of degenerate models to achieve sufficient statistical power across all four conditions. Generating and simulating this expanded model set is computationally intensive, requiring stochastic searches in a high-dimensional parameter space, full time-course simulations, and a subsequent selection process that may succeed or fail.

The principal aim of the present study is conceptual: to demonstrate that this multi-timescale homeostatic model—built here for the first time—can capture interactions between conductance regulation and voltage-dependence modulation during assembly (“neurodevelopment”) and perturbation. Establishing the conceptual framework and exploring its qualitative behavior were the necessary first steps before pursuing a large-scale quantitative study.

(3) Along the same line, the conclusion about how voltage-dependence regulation and channel conductance regulation interact to provide the neuron with the expected activity pattern (summarized and illustrated in Figure 6) is rather qualitative. Consistent with my previous comments, one would expect some quantitative answers to this question, rather than an illustration that approximately places a solution in parameter space.

We appreciate the reviewer’s interest in a more quantitative characterization of the interaction between voltage-dependence and conductance regulation (Fig. 6). As noted in our responses to Comments 1 and 2, some of the facets of this interaction—such as the ability to recover from perturbations and the speed of assembly—can be measured.

However, fully quantifying the landscape sketched in Figure 6 would require systematically mapping the regions of high-dimensional parameter space where stable solutions exist. In our model, this space spans 18 dimensions (maximal conductances and half‑(in)activations). Even a coarse grid with three samples per dimension would entail over 100 million simulations, which is computationally prohibitive and would still collapse to a schematic representation for visualization.

For this reason, we chose to present Figure 6 as a conceptual summary, illustrating the qualitative organization of solutions and the role of multi-timescale regulation, rather than attempting an exhaustive mapping. We view this figure as a necessary first step toward guiding future, more quantitative analyses.

Reviewer #3 (Public review):

Mondal et al. use computational modeling to investigate how activity-dependent shifts in voltage-dependent (in)activation curves can complement changes in ion channel conductance to support homeostatic plasticity. While it is well established that the voltage-dependent properties of ion channels influence neuronal excitability, their potential role in homeostatic regulation, alongside conductance changes, has remained largely unexplored. The results presented here demonstrate that activity-dependent regulation of voltage dependence can interact with conductance plasticity to enable neurons to attain and maintain target activity patterns, in this case, intrinsic bursting. Notably, the timescale of these voltage-dependent shifts influences the final steady-state configuration of the model, shaping both channel parameters and activity features such as burst period and duration. A major conclusion of the study is that altering this timescale can seamlessly modulate a neuron's intrinsic properties, which the authors suggest may be a mechanism for adaptation to perturbations.

While this conclusion is largely well-supported, additional analyses could help clarify its scope. For instance, the effects of timescale alterations are clearly demonstrated when the model transitions from an initial state that does not meet the target activity pattern to a new stable state. However, Fig. 6 and the accompanying discussion appear to suggest that changing the timescale alone is sufficient to shift neuronal activity more generally. It would be helpful to clarify that this effect primarily applies during periods of adaptation, such as neurodevelopment or in response to perturbations, and not necessarily once the system has reached a stable, steady state. As currently presented, the simulations do not test whether modifying the timescale can influence activity after the model has stabilized. In such conditions, changes in timescale are unlikely to affect network dynamics unless they somehow alter the stability of the solution, which is not shown here. That said, it seems plausible that real neurons experience ongoing small perturbations which, in conjunction with changes in timescale, could allow gradual shifts toward new solutions. This possibility is not discussed but could be a fruitful direction for future work.

We thank the reviewer for this thoughtful comment and for highlighting an important point about the scope of our conclusions regarding timescale effects. The reviewer is correct that our simulations demonstrate the influence of voltage-dependence timescale primarily during periods of adaptation—when the neuron is moving from an initial, target-mismatched state toward a final target-satisfying state. Once the system has reached a stable solution, simply changing the timescale of voltage-dependent modulation does not by itself shift the neuron’s activity, unless a new perturbation occurs that re-engages the homeostatic mechanism. We have clarified this point in the revised Discussion.

The confusion likely arose from imprecise phrasing in the original text describing Figure 6. Previously, we wrote:

“When channel gating properties are altered quickly in response to deviations from the target activity, the resulting electrical patterns are shown in Figure 6 as the orange bubble labeled 𝝉_{𝒉𝒂𝒍𝒇} = 6 s”. 

We have revised this sentence to emphasize that the orange bubble represents the eventual stable state, rather than implying that timescale changes alone drive activity shifts:

”When channel gating properties are altered quickly in response to deviations from the target activity, the neuron ultimately settles into a stable activity pattern. The resulting electrical patterns are shown in Figure 6 as the orange bubble labeled 𝝉_{𝒉𝒂𝒍𝒇} = 6 s”.

Reviewer #1 (Recommendations for the authors):

Unless I am missing something, Figure 2 should be a supplement to Figure 1. I would prefer to see panel B in Figure 1 to indicate that the findings of that figure are general. Panel A really is not showing anything useful to the reader.

We appreciate the suggestion to combine Figure 2 with Figure 1, but we believe keeping Figure 2 separate better preserves the manuscript’s flow. Figure 1 illustrates the mechanism in a single model, while Figure 2 presents the population-level summary that generalizes the phenomenon across all models.

Also, I find Figure 6 unnecessary and its description in the Discussion more detracting than useful. Even with the descriptions, I find nothing in the figure itself that clarifies the concept.

We appreciate the reviewer’s feedback on Figure 6. The purpose of this figure is to conceptually illustrate that multiple degenerate solutions can satisfy the calcium target and that the timescale of voltage‑dependence modulation can influence which region of this solution space is accessed during the acquisition of the activity target. Reviewer 3 noted some confusion about this point. We made a small clarifying edit.

At the risk of being really picky, I also don't see the purpose of Figure 7. And I find it strange to plot -Vm just because that's the argument of findpeaks.

We appreciate the reviewer’s comment on Figure 7. The purpose of this figure is to illustrate exactly what the findpeaks function is detecting, as indicated by the red arrows on the traces. For readers unfamiliar with findpeaks, it may not be obvious how the algorithm interprets the waveform. Showing the peaks directly ensures that the measurements used in our analysis align with what one would intuitively expect.

Reviewer #2 (Recommendations for the authors):

The writing of the article has been much improved since the last version. It is much clearer, and the discussion has been improved and better addresses the biological foundations and relevance of the study. However, conclusions are rather qualitative, while one would expect some quantitative answers to be provided by the modeling approach.

We appreciate the reviewer’s concern regarding quantification and share this perspective. As noted above, our study is primarily conceptual. Many aspects of the model, such as calcium handling and channel regulation, are parameterized based on incomplete biological data. These uncertainties make robust quantitative predictions difficult, so we focus on qualitative outcomes that are likely to hold independently of specific parameter choices.

Reviewer #1 (Public review):

In this work, Ligneul and coauthors implemented diffusion-weighted MRS in young rats to follow longitudinally and in vivo the microstructural changes occurring during brain development. Diffusion-weighted MRS is here instrumental in assessing microstructure in a cell-specific manner, as opposed to the claimed gold-standard (manganese-enhanced MRI) that can only probe changes in brain volume. Differential microstructure and complexification of the cerebellum and the thalamus during rat brain development were observed non-invasively. In particular, lower metabolite ADC with increasing age were measured in both brain regions, reflecting increasing cellular restriction with brain maturation. Higher sphere (representing cell bodies) fraction for neuronal metabolites (total NAA, glutamate) and total creatine and taurine in the cerebellum compared to the thalamus were estimated, reflecting the unique structure of the cerebellar granular layer with a high density of cell bodies. Decreasing sphere fraction with age was observed in the cerebellum, reflecting the development of the dendritic tree of Purkinje cells and Bergmann glia. From morphometric analyses, the authors could probe non-monotonic branching evolution in the cerebellum, matching 3D representations of Purkinje cells expansion and complexification with age. Finally, the authors highlighted taurine as a potential new marker of cerebellar development.

From a technical standpoint, this work clearly demonstrates the potential of diffusion-weighted MRS at probing microstructure changes of the developing brain non-invasively, paving the way for its application in pathological cases. Ligneul and coauthors also show that diffusion-weighted MRS acquisitions in neonates are feasible, despite the known technical challenges of such measurements, even in adult rats. They also provide all necessary resources to reproduce and build upon their work, which is highly valuable for the community.

From a biological standpoint, claims are well supported by the microstructure parameters derived from advanced biophysical modelling of the diffusion MRS data.

Specific strengths:

(1) The interpretation of dMRS data in terms of cell-specific microstructure through advanced biophysical modelling (e.g. the sphere fraction, modelling the fraction of cell bodies versus neuronal or astrocytic processes) is a strong asset of the study, going beyond the more commonly used signal representation metrics such as the apparent diffusion coefficient, which lacks specificity to biological phenomena.

(2) The fairly good data quality despite the complexity of the experimental framework should be praised: diffusion-weighted MRS was acquired in two brain regions (although not in the same animals) and longitudinally, in neonates, including data at high b-values and multiple diffusion times, which altogether constitutes a large-scale dataset of high value for the diffusion-weighted MRS community.

(3) The authors have shared publicly data and codes used for processing and fitting, which will allow one to reproduce or extend the scope of this work to disease populations, and which goes in line with the current effort of the MR(S) community for data sharing.

Specific weaknesses:

Ligneul and coauthors have convincingly addressed and included my comments from the first and second round in their revised manuscript.

I believe the following conceptual concerns, which are inherent to the nature of the study and do not require further adjustments of the manuscript, remain:

(1) Metabolite compartmentation in one cell type or the other has often been challenged and is currently impossible to validate in vivo. Here, Ligneul and coauthors did not use this assumption a priori and supported their claims also with non-MR literature (eg. for Taurine), but the interpretation of results in that direction should be made with care.

(2) Longitudinal MR studies of the developing brain make it difficult to extract parameters with an "absolute" meaning. Indirect assumptions used to derive such parameters may change with age and become confounding factors (brain structure, cell distribution, concentrations normalizing metabolites (here macromolecules), relaxation times...). While findings of the manuscript are convincing and supported with literature, the true underlying nature of such changes might be difficult to access.

(3) Diffusion MRI in addition to diffusion MRS would have been complementary and beneficial to validate some of the signal contributions, but was unfeasible in the time constraints of experiments on young animals.

Reviewer #3 (Public review):

To summarize: The authors' overfilling hypothesis depends crucially on the premise that the very-quickly reverting paired-pulse depression seen after unusually short rest intervals of << 50 ms is caused by depletion of release sites whereas Dobrunz and Stevens (1997) concluded that the cause was some other mechanism that does not involve depletion. The authors now include experiments where switching extracellular Ca2+ from 1.2 to 2.5 mM increases synaptic strength on average, but not by as much as at other synapse types. They contend that the result supports the depletion hypothesis. I didn't agree because the model used to generate the hypothesis had no room for any increase at all, and because a more granular analysis revealed a mixed population with a subset where: (a) synaptic strength increased by as much as at standard synapses; and yet (b) the quickly reverting depression for the subset was the same as the overall population.

The authors raise the possibility of additional experiments, and I do think this could clarify things if they pre-treat with EGTA as I recommended initially. They've already shown they can do this routinely, and it would allow them to elegantly distinguish between pv and pocc explanations for both the increases in synaptic strength and the decreases in the paired pulse ratio upon switching Ca2+ to 2.5 mM. Plus/minus EGTA pre-treatment trials could be interleaved and done blind with minimal additional effort.

Showing reversibility would be a great addition too, because, in our experience, this does not always happen in whole-cell recordings in ex-vivo tissue even when electrical properties do not change. If the goal is to show that L2/3 synapses are less sensitive to changes in Ca2+ compared to other synapse types - which is interesting but a bit off point - then I would additionally include a positive control, done by the same person with the same equipment, at one of those other synapse types using the same kind of presynaptic stimulation (i.e. ChRs).

Specific points (quotations are from the Authors' rebuttal)

(1) Regarding the Author response image 1, I was instead suggesting a plot of PPR in 1.2 mM Ca2+ versus the relative increase in synaptic strength in 2.5 versus in 1.2 mM. This continues to seem relevant.

(2) "Could you explain in detail why two-fold increase implies pv < 0.2?"

a. start with power((2.5/(1 + (2.5/K1) + 1/2.97)),4) = 2*power((1.3/(1 + (1.3/K1) + 1/2.97)),4);

b. solve for K1 (this turns out to be 0.48);

c. then implement the premise that pv -> 1.0 when Ca2+ is high by calculating Max = power((C/(1 + (C/K1) + 1/2.97)),4) where C is [Ca] -> infinity.

d. pv when [Ca] = 1.3. mM must then be power((1.3/(1 + (1.3/K1) + 1/2.97)),4)/Max, which is <0.2.

Note that modern updates of Dodge and Rahamimoff typically include a parameter that prevents pv from approaching 1.0; this is the gamma parameter in the versions from Neher group.

(3) "If so, we can not understand why depletion-dependent PPD should lead to PPF."

When PPD is caused by depletion and pv < 0.2, the number of occupied release sites should not be decreased by more than one-fifth at the second stimulus so, without facilitation, PPR should be > 0.8. The EGTA results then indicate there should be strong facilitation, driving PPR to something like 1.2 with conservative assumptions. And yet, a value of < 0.4 is measured, which is a large miss.

(4) Despite the authors' suggestion to the contrary, I continue to think there is a substantial chance that Ca2+-channel inactivation is the mechanism underlying the very quickly reverting paired-pulse depression. However, this is only one example of a non-depletion mechanism among many, with the main point being that any non-depletion mechanism would undercut the reasoning for overfilling. And, this is what Dobrunz and Stevens claimed to show; that the mechanism - whatever it is - does not involve depletion. The most effective way to address this would be affirmative experiments showing that the quickly reverting depression is caused by depletion after all. Attempting to prove that Ca2+-channel inactivation does not occur does not seem like a worthwhile strategy because it would not address the many other possibilities.

(5) True that Kusick et al. observed morphological re-docking, but then vesicles would have to re-prime and Mahfooz et al. (2016) showed that re-priming would have to be slower than 110 ms (at least during heavy use at calyx of Held).

1 de 6 et suivants, 2 de 6, 3 de 6, 4 de 6. 5 de 6, 6 de 6, 7 de 6

should look like. We believe in diversity.

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Main benefits

• Exchange and commerce
• Cross-organization dispute resolution
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• Member hosting and benefits across organizations
• Values alignment / adherence to standards

DAOs vouched

Despite a decade of chants about "trustless systems", Web3 is constantly working on trust... how do we avoid rugs, thugs, drugs and mugs

Yes, stick it to the Web 3 croud 80% of which is fatally misdirected. Invert the drive for autonomy to build blocks of chains for global enslavement

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DOI: 10.1101/2025.09.03.674035

Resource: RRID:Addgene_67639

Curator: @dhovakimyan1

SciCrunch record: RRID:Addgene_67639

What is this?

DOI: 10.1038/s41557-025-01928-3

Resource: None

Curator: @scibot

SciCrunch record: RRID:SCR_023307

What is this?

DOI: 10.1016/j.celrep.2025.116217

Resource: (MBL International Cat# D351-3, RRID:AB_2815002)

Curator: @scibot

SciCrunch record: RRID:AB_2815002

What is this?

Reviewer #1 (Public review):

Summary:

The authors present a nanobody-based pulse-labeling system to track yeast NPCs. Transient expression of a nanobody targeting Nup84 (fused to NeonGreen or an affinity tag) permits selective visualization and biochemical capture of NPCs. Short induction effectively labels NPCs, and the resulting purifications match those from conventional Nup84 tagging. Crucially, when induction is repressed, dilution of the labeled pool through successive cell cycles allows the visualization of "old" NPCs (and potentially individual NPCs), providing a powerful view of NPC lifespan and turnover without permanently modifying a core scaffold protein.

Strengths:

(1) A brief expression pulse labels NPCs, and subsequent repression allows dilution-based tracking of older (and possibly single) NPCs over multiple cell cycles.

(2) The affinity-purified complexes closely match known Nup84-associated proteins, indicating specificity and supporting utility for proteomics.

Weaknesses:

(1) Reliance on GAL induction introduces metabolic shifts (raffinose → galactose → glucose) that could subtly alter cell physiology or the kinetics of NPC assembly. Alternative induction systems (e.g., β-estradiol-responsive GAL4-ER-VP16) could be discussed as a way to avoid carbon-source changes.

(2) While proteomics is solid, a comprehensive supplementary table listing all identified proteins (with enrichment and statistics) would enhance transparency.

(3) Importantly, the authors note that the method is particularly useful "in conditions where direct tagging of Nup84 interferes with its function, while sub-stoichiometric nanobody binding does not." After this sentence, it would be valuable to add concrete examples, such as experiments examining NPC integrity in aging or stress conditions where epitope tags can exacerbate phenotypes. These examples will help readers identify situations in which this approach offers clear advantages.

Reviewer #3 (Public review):

Summary:

Submitted to the Tools and Resources series, this study reports on the use of a single-domain antibody targeting the nucleoporin Nup84 to probe and track NPCs in budding yeast. The authors demonstrate their ability to rapidly label or pull down NPCs by inducing the expression of a tagged version of the nanobody (Figure 1).

Strengths:

This tool's main strength is its versatility as an inexpensive, easy-to-set-up alternative to metabolic labelling or optical switching. This same rationale could, in principle, be applied to the study of other multiprotein complexes using similar strategies, provided that single-chain antibodies are available.

Weaknesses:

This approach has no inherent weaknesses, but it would be useful for the authors to verify that their pulse labelling strategy can also be used to detect assembly intermediates, structural variants, or damaged NPCs.

Overall, the data clearly show that Nup84 nanobodies are a valuable tool for imaging NPC dynamics and investigating their interactomes through affinity purification.

Reviewer #3 (Public review):

Summary:

In "Alternative Splicing Across the Tree of Life: A Comparative Study," the authors use rich annotation features from nearly 1,500 high-quality NCBI genome assemblies to develop a novel genome-scale metric, the Alternative Splicing Ratio, that quantifies the extent to which coding sequences generate multiple mRNA transcripts via alternative splicing (AS). This standardized metric enables cross-species comparisons and reveals clear phylogenetic patterns: minimal AS in prokaryotes and unicellular eukaryotes, moderate AS in plants, and high AS in mammals and birds. The study finds a strong negative correlation between AS and coding content, with genomes containing approximately 50% intergenic DNA exhibiting the highest AS activity. By integrating diverse lines of prior evidence, the study offers a cohesive evolutionary framework for understanding how alternative splicing varies and evolves across the tree of life.

Strengths:

By studying alternative splicing patterns across the tree of life, the authors systematically address an important yet historically understudied driver of functional diversity, complexity, and evolutionary innovation. This manuscript makes a valuable contribution by leveraging standardized, publicly available genome annotations to perform a global survey of transcriptional diversity, revealing lineage-specific patterns and evolutionary correlates. The authors have done an admirable job in this revised version, thoroughly addressing prior reviewer comments. The updated manuscript includes more rigorous statistical analyses, careful consideration of potential methodological biases, expanded discussion of regulatory mechanisms, and acknowledgment of non-adaptive alternatives. Overall, the work presents an intriguing view of how alternative splicing may serve as a flexible evolutionary strategy, particularly in lineages with limited capacity for coding expansion (e.g., via gene duplication). Notably, the identification of genome size and genic coding fraction thresholds (~20 Mb and ~50%, respectively) as tipping points for increased splicing activity adds conceptual depth and potential generalizability.

Weaknesses:

While the manuscript offers a broad comparative view of alternative splicing, its central message becomes diffuse in the revised version. The focus of the study is unclear, and the manuscript comes across as largely descriptive without a well-articulated hypothesis or explanatory evolutionary model. Although the discussion gestures toward adaptive and non-adaptive mechanisms, these interpretations are not developed early or prominently enough to anchor the reader. The negative correlation between alternative splicing and coding content is compelling, but the biological significance of this pattern remains ambiguous: it is unclear whether it reflects functional constraint, genome organization, or annotation bias. This uncertainty weakens the manuscript's broader evolutionary inferences.

Sections of the Introduction, particularly lines 72-90, lack cohesion and logical flow, shifting abruptly between topics without a clear structure. A more effective approach may involve separating discussions of coding and non-coding sequence evolution to clarify their distinct contributions to splicing complexity. Furthermore, some interpretive claims lack nuance. For example, the assertion that splicing in plants "evolved independently" seems overstated given the available evidence, and the citation regarding slower evolution of highly expressed genes overlooks counterexamples from the immunity and reproductive gene literature.

Presentation of the results is occasionally vague. For instance, stating "we conducted comparisons of mean values" (line 146) without specifying the metric undercuts interpretability. The authors should clarify whether these comparisons refer to the Alternative Splicing Ratio or another measure. Additionally, the lack of correlation between splicing and coding region fraction in prokaryotes may reflect a statistical power issue, particularly given their limited number of annotated isoforms, rather than a biological absence of pattern.

Finally, the assessment of annotation-related bias warrants greater methodological clarity. The authors note that annotations with stronger experimental support yield higher splicing estimates, yet the normalization strategy for variation in transcriptomic sampling (e.g., tissue breadth vs sequencing depth) is insufficiently described. As these factors can significantly influence splicing estimates, a more rigorous treatment is essential. While the authors rightly acknowledge that splicing represents only one layer of regulatory complexity, the manuscript would benefit from a more integrated consideration of additional dimensions, such as 3D genome architecture, e.g., the potential role of topologically associating domains in constraining splicing variation.

Reviewer #4 (Public review):

The manuscript reports on a large-scale study correlating genomic architecture with splicing complexity over almost 1,500 species. We still know relatively little about alternative splicing functional consequences and evolution, and thus, the study is relevant and timely. The methodology relies on annotations from NCBI for high-quality genomes and a main metric proposed by the authors and named Alternative Splicing Ratio (ASR). It quantifies the level of redundancy of each coding nucleotide in the annotated isoforms.

According to the authors' response to the first reviewers' comments, the present version of the manuscript seems to be a profoundly revised version compared to the original submission. I did not have access to the reviewers' comments.

Although the study addresses an important question and the authors have visibly made an important effort to make their claims more statistically robust, I have a number of major concerns regarding the methodology and its presentation.

(1) A large part of the manuscript is speculative and vague. For instance, the Discussion is very long (almost longer than the Results section) and the items discussed are sometimes not in direct connection with the present work. I would suggest merging the last 2 paragraphs, for instance, since the before last paragraph is essentially a review of the literature without direct connection to the present work.

(2) The Methods section lacks clarity and precision. A large part is devoted to explaining the biases in the data without any reference or quantification. The definition of ASR is very confusing. It is first defined in equation 2, with a different name, and then again in the next subsection from a different perspective on lines 512-518. Why build matrices of co-occurrences if these are, in practice, never used? It seems the authors exploit only the trace. A major revision, if I understood correctly, was the correction/normalisation of the ASR metric. This normalisation is not explained. The authors argue that they will write another paper about it, I do not think this is acceptable for the publication of the present manuscript. Furthermore, there is no information about the technical details of the implementation: which packages did the authors use?

(3) Could the authors motivate why they do not directly focus on the MC permutation test? They motivate the use of permutations because the data contains extreme outliers and are non normal in most cases. Hence, it seems the Welch's ANOVA is not adapted. "To further validate our findings, we also conducted<br /> 148 a Monte Carlo permutation test, which supported the conclusions (see Methods)." Where is the comparison shown? I did not see any report of the results for the non-permuted version of the Welch's ANOVA.

(4) What are the assumptions for the Phylogenetic Generalized Least Squares? Which evolution model was chosen and why? What is the impact of changing the model? Could the authors define more precisely (e.g. with equations) what is lambda? Is it estimated or fixed?

(5) I think the authors could improve their account of recent literature on the topic. For instance, the paper https://doi.org/10.7554/eLife.93629.3, published in the same journal last year, should be discussed. It perfectly fits in the scope of the subsection "Evidence for the adaptive role of alternative splicing". Methods and findings reported in https://doi.org/10.1186/s13059-021-02441-9 and https://www.genome.org/cgi/doi/10.1101/gr.274696.120 directly concern the assessment of AS evolutionary conservation across long evolutionary times and/or across many species. These aspects are mentioned in the introduction on p.3. but without pointing to such works. Can we really qualify a work published in 2011 as "recent" (line 348-350)?

The generated data and codes are available on Zenodo, which is a good point for reproducibility and knowledge sharing with the community.

Reviewer #3 (Public review):

Summary:

Su et al. sought to understand how the opportunistic pathogen Staphylococcus aureus responds to multiple selection pressures during infection. Specifically, the authors were interested in how the host environment and antibiotic exposure impact the evolution of both virulence and antibiotic resistance in S. aureus. To accomplish this, the authors performed an evolution experiment where S. aureus was fed to Caenorhabditis elegans as a model system to study the host environment and then either subjected to the antibiotic oxacillin or not. Additionally, the authors investigated the difference in evolution between an antibiotic-resistant strain, MRSA, and an isogenic susceptible strain, MSSA. They found that MRSA strains evolved in both antibiotic and host conditions became more virulent, and that strains evolved outside these conditions lost virulence. Looking at the strains evolved in just antibiotic conditions, the authors found that S. aureus maintained its ability to lyse blood cells. Mutations in codY, gdpP, and pbpA were found to be associated with increased virulence. Additionally, these mutations identified in these experiments were found in S. aureus strains isolated from human infections.

Strengths:

The data are well-presented, thorough, and are an important addition to the understanding of how certain pathogens might adapt to different selective pressures in complex environments.

Weaknesses:

There are a few clarifications that could be made to better understand and contextualize the results. Primarily, when comparing the number of mutations and selection across conditions in an evolution experiment, information about population sizes is important to be able to calculate the mutation supply and number of generations throughout the experiment. These calculations can be difficult in vivo, but since several steps in the methodology require plating and regrowth, those population sizes could be determined. There was also no mention of how the authors controlled the inoculation density of bacteria introduced to each host. This would need to be known to calculate the generation time within the host. These caveats should be addressed in the manuscript.

Another concern is the number of generations the populations of S. aureus spent either with relaxed selection in rich media or under antibiotic pressure in between the host exposure periods. It is probable then that the majority of mutations were selected for in these intervening periods between host infection. Again, a more detailed understanding of population sizes would contribute to the understanding of which phase of the experiment contributed to the mutation profile observed.

Reviewer #1 (Public review):

Summary:

This manuscript presents an extensive body of work and an outstanding contribution to our understanding of the IFN type I and III system in chickens. The research started with the innovative approach of generating KO chickens that lack the receptor for IFNα/β (IFNAR1) or IFN-λ (IFNLR1). The successful deletion and functional loss of these receptors was clearly and comprehensively demonstrated in comparison to the WT. Moreover, the homozygous KO lines (IFNAR1-/- or IFNLR1-/- ) were found to have similar body weights, and normal egg production and fertility compared to their WT counterparts. These lines are a major contribution to the toolbox for the study of avian/chicken immunology.

The significance of this contribution is further demonstrated by the use of these lines by the authors to gain insight into the roles of IFN type I and IFN-type III in chickens, by conducting in ovo and in vivo studies examining basic aspects of immune system development and function, as well as the responses to viral challenges conducted in ovo and in vivo.

Based on solid, state-of the-art methods and convincing evidence from studies comparing various immune system related functions in the IFNAR1-/- or IFNLR1-/- lines to the WT, revealed that the deletion of IFNAR1 and/or IFNLR1 resulted in:<br /> (1) impaired IFN signaling and induction of anti-viral state;<br /> (2) modulation of immune cell profiles in the peripheral blood circulation and spleen;<br /> (3) modulation of the cecum microbiome;<br /> (4) reduced concentrations of IgM and IgY in the blood plasma before and following immunization with model antigen KLH, whereby also line differences in the time-course of the antibody production were observed;<br /> (5) decrease in MHCII+ macrophages and B cells in the spleen of IFNAR1 KO chickens, although the MHCII-expression per cell was not affected in this line; and<br /> (6) reduction in the response of αβ1 TCR+ T cells of IFNAR1 KO chickens as suggested by clonal repertoire analyses.

These studies were then followed by examination of the role of type I and type III IFN in virus infection, using different avian influenza A virus strains as well as an avian gamma corona virus (IBV) in in ovo challenge experiments. These studies revealed: viral titers that reflect virus-species and strain-specific IFN responses; no differences in the secretion of IFN-α/β in both KO compared to the WT lines; a predominant role of type I IFN in inducing the interferon-stimulated gene (ISG) Mx; and that an excessive and unbalanced type I IFN response can harm host fitness (survival rate, length of survival) and contribute to immunopathology.

Based on guidance from the in ovo studies, comprehensive in vivo studies were conducted on host-pathogen interactions in hens from the three lines (WT, IFNAR1 KO, or IFNLR1 KO). These studies revealed the early appearance of symptoms and poor survival of hens from the IFNR1 KO line challenged with H3N1 avian influenza A virus; efficient H#N1 virus replication in IFNAR1 KO hens, increased plasma concentrations of IFNα/β and mRNA expression of IFN-λ in spleens of the IFNAR1 KO hens; a pro-inflammatory role of IFN-λ in the oviduct of hens infected with H3N1 virus; increased proinflammatory cytokine expression in spleens of IFNAR1 KO hens, and Impairment of negative feedback mechanisms regulating IFN-α/β secretion in IFNAR1-KO hens and a significant decrease in this group's antiviral state; additionally it was demonstrated that IFN-α/β can compensate IFN-λ to induce an adequate antiviral state in the spleen during H3N1 infection, but IFN-λ cannot compensate for IFN-α/β signaling in the spleen.

Strengths:

(1) Both the methods and results from the comprehensive, well-designed, and well-executed experiments are considered excellent. The results are well and correctly described in the result narrative and well presented in both the manuscript and supplement Tables and Figures. Excellent discussion/interpretation of results.

(2) The successful generation of the type I and type III IFN KO lines offers unprecedented insight and opens multiple new venues for exploring the IFN system in chickens. The new knowledge reported here is direct evidence of the high impact of this model system on effectively addressing a critical knowledge gap in avian immunology.

(3) The thoughtful selection of highly relevant viruses to poultry and human health for the in ovo and in vivo challenge studies to examine and assess host-pathogen interactions in the IFNR KO and WT lines.

(4) Making use of the unique opportunities in the chicken model to examine and evaluate the host's IFN system responses to various viral challenges in ovo, before conducting challenge studies in hens.

(5) The new knowledge gained from the IFNAR1 and IFNLR1 KO lines will find much-needed application in developing more effective strategies to prevent health challenges like avian influenza and its devastating effects on poultry, humans, and other mammals.

(6) The excellent cooperation and contributions of the co-authors and institutions.

Weaknesses:

No weaknesses were identified by this reviewer.

Reviewer #2 (Public review):

Summary:

This study attempts to dissect the contributions of type I and type III IFNs to the antiviral response in chickens. The first part of the study characterises the generation of IFNAR and IFNLR KO chicken strains and describes basic differences. Four different viruses are then tested in chicken embryos, while the subsequent analysis of the antiviral response in vivo is performed with one influenza H3N1 strain.

Strengths:

Having these two KO chicken strains as a tool is a great achievement. The initial analysis is solid. Clear effect of IFNAR deficiency in in vivo infection, less so for IFNLR deficiency.

Weaknesses:

(1) The antibody induction by KLH immunisation: No data indicated whether or not this vaccination induces IFN responses in wt mice, so the effects observed may be due to steady-state differences or to differential effects of IFN induced during the vaccination phase. No pre-immune results are shown. The differences are relatively small and often found at only one plasma dilution - the whole of Figure 4 could be condensed into one or two panels by proper calculation of Ab titers - would these titres be significantly different? This, as all of the other in vivo experiments, has not been repeated, if I understand the methods section correctly.

(2) The basic conundrum here and in later figures is never addressed by the authors: Situations where IFN type 1 and 3 signalling deficiency each have an independent effect (i.e., Figure 4d) suggest that they act by separate, unrelated mechanisms. However, all the literature about these IFN families suggests that they show almost identical signalling and gene induction downstream of their respective receptors. How can the same signalling, clearly active here downstream of the receptors for IFN type 1 or type 3, be non-redundant, i.e., why does the unaffected IFN family not stand in? This is a major difference from the mouse studies, which showed a rather subtle phenotype when only one of the two IFN systems was missing, but a massive reduction in virus control in double KO mice (the correct primary paper should be quoted here, not only the review by McNab). Reasons could be a direct effect of IFNab on B cells and an indirect effect of IFNL through non-B cells, timing issues, and many other scenarios can be envisaged. The authors do not address this question, which limits the depth of analysis.

(3) In the one in vivo experiment performed with chickens, only one virus was tested; more influenza strains should be included, as well as non-influenza viruses.

(4) The basic conundrum of point 2 applies equally to Figure 6a; both KOs have a phenotype. Again in 6d, both IFNs appear to be separately required for Mx induction. An explanation is needed.

(5) Line 308, where are the viral titers you refer to in the text? The statement that the results demonstrate that excessive IFNab has a negative impact is overstretched, as no IFN measurements of the infected embryos are shown here.

(6) The in vivo infection is the most interesting experiment, and the key outcome here is that IFN type 1 is crucial for anti-H3N1 protection in chickens, while type 3 is less impactful. However, this experiment suffers from the different time points when chickens were culled, so many parameters are impossible to compare (e.g., weight loss, histopathology, IFN measurements, and more). Many of these phenomena are highly dynamic in acute virus infections, so disparate time points do not allow a meaningful comparison between different genotypes. What are the stats in 7b? Is the median rather than the mean indicated by the line? Otherwise, the lines appear in surprising places. SD must be shown, and I find it difficult to believe that there is a significant difference in weight, for e.g., IFNAR KO, unless maybe with a paired t test. What is the statistical test?

(7) Figures 7e,f: these comparisons are very difficult to interpret as the virus loads at these time points already differ significantly, so any difference could be secondary to virus load differences.

Reviewer #2 (Public review):

While the importance of asparagine in the differentiation and activation of CD8 T cells has been previously reported, its role in CD4 T cells remained unclear. Using culture media containing specific amino acids, the authors demonstrated that extracellular asparagine promotes CD4 T cell proliferation. Consistent with this, depletion of extracellular asparagine using PEG-AsnASE suppressed CD4 T cell activation. Proteomic analysis focusing on asparagine content revealed that, during the early phase of T cell activation, most asparagine incorporated into proteins is derived from extracellular sources. The authors further confirmed the importance of extracellular asparagine in vivo, demonstrating improved EAE pathology.

While the data are well organized and convincing, the mechanism by which asparagine deficiency leads to altered T cell differentiation remains unclear. It is also necessary to investigate the transporters involved in asparagine uptake. In particular, elucidating whether different T cell subsets utilize the same or distinct transport mechanisms would provide important insight into the immunoregulatory role of asparagine.

(1) The finding that asparagine supplementation promotes T cell proliferation under various amino acid conditions is highly significant. However, the concentration at which this effect occurs remains unclear. A titration analysis would be necessary to determine the dose-dependency of asparagine.

(2) The effects of asparagine deficiency occur during the early phase of T cell activation. Thus, it is likely that the transporters responsible for asparagine uptake are either rapidly induced upon activation or already expressed in the resting state. Since this is central to the focus of the manuscript, it is interesting to identify the transporter responsible for asparagine uptake during early T cell activation. A recent paper (DOI: 10.1126/sciadv.ads350) reported that macrophages utilize Slc6a14 to use extracellular asparagine. Is this also true for CD4+ T cells?

(3) Given that depletion of extracellular asparagine impairs differentiation of Th1 and Th17 cells, it is possible that TCR signaling is compromised under these conditions. This point should be investigated by targeting downstream signaling molecules such as Lck, ZAP70, or mTOR. Also, does it affect the protein stability of master transcription factors such as T-bet and RORgt?

(4) Is extracellular asparagine also important for the differentiation of helper T cell subsets other than Th1 and Th17, such as Th2, Th9, and iTreg?

(5) Asparagine taken up from outside the cell has been shown to be used for de novo protein synthesis (Figure 3E), but are there any proteins that are particularly susceptible to asparagine deficiency? This can be verified by performing proteome analysis, and the effects on Th1/17 subset differentiation mentioned above should also be examined.

(6) While the importance of extracellular asparagine is emphasized, Asns expression is markedly induced during early T cell activation. Nevertheless, the majority of asparagine incorporated into proteins appears to be derived from extracellular sources. Does genetic deletion of Asns have any impact on early CD4+ T cell activation? The authors indicated that newly synthesized Asns have little impact on CD8+ T cells in the Discussion section, but is this also true for CD4+ T cells? This could be verified through experiments using CRISPR-mediated Asns gene targeting or pharmacological inhibition.

Reviewer #3 (Public review):

Summary:

This study aimed to investigate pseudouridylation across various RNA species in multiple bacterial strains using an optimized BID-seq approach. It examined both conserved and divergent modification patterns, the potential functional roles of pseudouridylation, and its dynamic regulation across different growth conditions.

Strengths:

The authors optimized the BID-seq method and applied this important technique to bacterial systems, identifying multiple pseudouridylation sites across different species. They investigated the distribution of these modifications, associated sequence motifs, their dynamics across growth phases, and potential functional roles. These data are of great interest to researchers focused on understanding the significance of RNA modifications, particularly mRNA modifications, in bacteria.

Weaknesses:

(1) The reliability of BID-seq data is questionable due to a lack of experimental validations.

(2) The manuscript is not well-written, and the presented work shows a major lack of scientific rigor, as several key pieces of information are missing.

(3) The manuscript's organization requires significant improvement, and numerous instances of missing or inconsistent information make it difficult to understand the key objectives and conclusions of the study.

(4) The rationale for selecting specific bacterial species is not clearly explained, and the manuscript lacks a systematic comparison of pseudouridylation among these species.

Reviewer #2 (Public review):

Summary:

In this manuscript, Thompson et al. investigate the impact of prior ATP exposure on later macrophage functions as a mechanism of immune training. They describe that ATP training enhances bactericidal functions, which they connect to the P2x7 ATP receptor, Nlrp3 inflammasome activation, and TWIK2 K+ movement at the cell surface and subsequently at phagosomes during bacterial engulfment. With stronger methodology, these findings could provide useful insight into how ATP can modulate macrophage immune responses, though they are generally an incremental addition to existing literature. The evidence supporting their conclusions is currently inadequate. Gaps in explaining methodology are substantial enough to undermine trust in much of the data presented. Some assays may not be designed rigorously enough for interpretation.

Strengths:

The authors demonstrate two novel findings that have sufficient rigor to assess:

(1) prolonged persistence of TWIK2 at the macrophage plasma membrane following ATP, and can translocate to the phagosome during particle engulfment, which builds upon their prior report of ATP-driven 'training' of macrophages.

(2) administering mice intra-nasal ATP to 'train' lungs to protect mice from otherwise fatal bacterial infection.

Weaknesses:

(1) Missing details from methods/reported data: Substantial sections of key methods have not been disclosed (including anything about animal infection models, RNA-sequencing, and western blotting), and the statistical methods, as written, only address two-way comparisons, which would mean analysis was improperly performed. In addition, there is a general lack of transparency - the methods state that only representative data is included in the manuscript, and individual data points are not shown for assays.

(2) Poor experimental design including missing controls: Particularly problematic are the Seahorse assay data (requires normalization to cell numbers to interpret this bulk assay - differences in cell growth/loss between conditions would confound data interpretation) and bacterial killing assays (as written, this method would be heavily biased by bacterial initial binding/phagocytosis which would confound assessment of killing). Controls need to be included for subcellular fractionating to confirm pure fractions and for dye microscopy to show a negative background. Conclusions from these assays may be incorrect, and in some cases, the whole experiment may be uninterpretable.

(3) The conclusions overstate what was tested in the experiments: Conceptually, there are multiple places where the authors draw conclusions or frame arguments in ways that do not match the experiments used. Particularly:<br /> a) The authors discuss their findings in the context of importance for AM biology during respiratory infection but in vitro work uses cells that are well-established to be poor mimics of resident AMs (BMDM, RAW), particularly in terms of glycolytic metabolism.<br /> b) In vivo work does not address whether immune cell recruitment is triggered during training.<br /> c) Figure 3 is used to draw conclusions about K+ in response to bacterial engulfment, but actually assesses fungal zymosan particles.<br /> d) Figure 5 is framed in bacterial susceptibility post-viral infection, but the model used is bacterial post-bacterial.<br /> e) In their discussion, the authors propose to have shown TWIK2-mediated inflammasome activation. They link these separately to ATP, but their studies do not test if loss of TWIK2 prevents inflammasome activation in response to ATP (Figure 4E does not use TWIK2 KO).

In summary, this work contains some useful data showing how ATP can 'train' macrophages. However, it largely lacks the expected level of rigor. For this work to be valuable to the field, it is likely to need substantial improvement in methods reporting, inclusion of missing assay controls, may require repeating key experiments that were run with insufficient methodology (or providing details and supplemental data to prove that methodology was sufficient), and should either add additional experiments that properly test their experimental question or rewrite their conclusions.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

Summary

This paper summarises responses from a survey completed by around 5,000 academics on their manuscript submission behaviours. The authors find several interesting stylised facts, including (but not limited to):

Women are less likely to submit their papers to highly influential journals (e.g., Nature, Science and PNAS).

Women are more likely to cite the demands of co-authors as a reason why they didn't submit to highly influential journals.

Women are also more likely to say that they were advised not to submit to highly influential journals.

The paper highlights an important point, namely that the submission behaviours of men and women scientists may not be the same (either due to preferences that vary by gender, selection effects that arise earlier in scientists' careers or social factors that affect men and women differently and also influence submission patterns). As a result, simply observing gender differences in acceptance rates - or a lack thereof - should not be automatically interpreted as as evidence for or against discrimination (broadly defined) in the peer review process.

Major comments

What do you mean by bias?

In the second paragraph of the introduction, it is claimed that "if no biases were present in the case of peer review, then we should expect the rate with which members of less powerful social groups enjoy successful peer review outcomes to be proportionate to their representation in submission rates." There are a couple of issues with this statement.

First, the authors are implicitly making a normative assumption that manuscript submission and acceptance rates *should* be equalised across groups. This may very well be the case, but there can also be valid reasons - even when women are not intrinsically better at research than men - why a greater fraction of female-authored submissions are accepted relative to male-authored submissions (or vice versa). For example, if men are more likely to submit their less ground-breaking work, then one might reasonably expect that they experience higher rejection rates compared to women, conditional on submission.

We do assume that normative statement: unless we believe that men’s papers are intrinsically better than women’s papers, the acceptance rate should be the same. But the referee is right: we have no way of controlling for the intrinsic quality of the work of men and women. That said, our manuscript does not show that there is a different acceptance rate for men and women; it shows that women are less likely to submit papers to a subset of journals that are of a lower Journal Impact Factor, controlling for their most cited paper, in an attempt to control for intrinsic quality of the manuscripts.

Second, I assume by "bias", the authors are taking a broad definition, i.e., they are not only including factors that specifically relate to gender but also factors that are themselves independent of gender but nevertheless disproportionately are associated with one gender or another (e.g., perhaps women are more likely to write on certain topics and those topics are rated more poorly by (more prevalent) male referees; alternatively, referees may be more likely to accept articles by authors they've met before, most referees are men and men are more likely to have met a given author if he's male instead of female). If that is the case, I would define more clearly what you mean by bias. (And if that isn't the case, then I would encourage the authors to consider a broader definition of "bias"!)

Yes, the referee is right that we are taking a broad definition of bias. We provide a definition of bias on page 3, line 92. This definition is focused on differential evaluation which leads to differential outcomes. We also hedge our conversation (e.g., page 3, line 104) to acknowledge that observations of disparities may only be an indicator of potential bias, as many other things could explain the disparity. In short, disparities are a necessary but insufficient indicator of bias. We add a line in the introduction to reinforce this. The only other reference to the term bias comes on page 10, line 276. We add a reference to Lee here to contextualize.

Identifying policy interventions is not a major contribution of this paper

I would take out the final sentence in the abstract. In my opinion, your survey evidence isn't really strong enough to support definitive policy interventions to address the issue and, indeed, providing policy advice is not a major - or even minor - contribution of your paper. (Basically, I would hope that someone interested in policy interventions would consult another paper that much more thoughtfully and comprehensively discusses the costs and benefits of various interventions!) While it's fine to briefly discuss them at the end of your paper - as you currently do - I wouldn't highlight that in the abstract as being an important contribution of your paper.

We thank the referee for this comment. While we agree that our results do not lead to definitive policy interventions, we believe that our findings point to a phenomenon that should be addressed through policy interventions. Given that some interventions are proposed in our conclusion, we feel like stating this in the abstract is coherent.

Minor comments

What is the rationale for conditioning on academic rank and does this have explanatory power on its own - i.e., does it at least superficially potentially explain part of the gender gap in intention to submit?

Thank you for this thoughtful question. We conditioned on academic rank in all regression analyses to account for structural differences in career stage that may potentially influence submission behaviors. Academic rank (e.g., assistant, associate, full professor) is a key determinant of publishing capacity and strategic considerations, such as perceived likelihood of success at elite journals, tolerance for risk, and institutional expectations for publication venues.

Importantly, academic rank is also correlated with gender due to cumulative career disadvantages that contribute to underrepresentation of women at more senior levels. Failing to adjust for rank would conflate gender effects with differences attributable to career stage. By including rank as a covariate, we aim to isolate gender-associated patterns in submission behavior within comparable career stages, thereby producing a more precise estimate of the gender effect.

Regarding explanatory power, academic rank does indeed contribute significantly to model fit across our analyses, indicating that it captures meaningful variation in submission behavior. However, even after adjusting for rank, we continue to observe significant gender differences in submission patterns in several disciplines. This suggests that while academic rank explains part of the variation, it does not fully account for the gender gap—highlighting the importance of examining other structural and behavioral factors that shape the publication trajectory.

Reviewer #2 (Public review):

Basson et al. present compelling evidence supporting a gender disparity in article submission to "elite" journals. Most notably, they found that women were more likely to avoid submitting to one of these journals based on advice from a colleague/mentor. Overall, this work is an important addition to the study of gender disparities in the publishing process.

I thank the authors for addressing my concerns.

Reviewer #4 (Public review):

Main strengths

The topic of the MS is very relevant given that across the sciences/academia, genders are unevenly represented, which has a range of potential negative consequences. To change this, we need to have the evidence on what mechanisms cause this pattern. Given that promotion and merit in academia are still largely based on the number of publications and the impact factor, one part of the gap likely originates from differences in publication rates of women compared to men.

Women are underrepresented compared to men in journals with a high impact factor. While previous work has detected this gap and identified some potential mechanisms, the current MS provides strong evidence that this gap might be due to a lower submission rate of women compared to men, rather than the rejection rates. These results are based on a survey of close to 5000 authors. The survey seems to be conducted well (though I am not an expert in surveys), and data analysis is appropriate to address the main research aims. It was impossible to check the original data because of the privacy concerns.

Interestingly, the results show no gender bias in rejection rates (desk rejection or overall) in three high-impact journals (Science, Nature, PNAS). However, submission rates are lower for women compared to men, indicating that gender biases might act through this pathway. The survey also showed that women are more likely to rate their work as not groundbreaking and are advised not to submit to prestigious journals, indicating that both intrinsic and extrinsic factors shape women's submission behaviour.

With these results, the MS has the potential to inform actions to reduce gender bias in publishing, but also to inform assessment reform at a larger scale.

I do not find any major weaknesses in the revised manuscript.

Reviewer #4 (Recommendations for the authors):

(1) Colour schemes of the Figures are not adjusted for colour-blindness (red-green is a big NO), some suggestions can be found here https://www.nceas.ucsb.edu/sites/default/files/2022-06/Colorblind%20Safe%20Color%20Schemes.pdf

We appreciate the suggestion. We’ve adjusted the colors in the manuscript to be color-blind friendly using one of the colorblind safe palettes suggested by the reviewer.

(2) I do not think that the authors have fully addressed the comment about APCs and the decision to submit, given that PNAS has publication charges that amount to double of someone's monthly salary. I would add a sentence or two to explain that publication charges should not be a factor for Nature and Science, but might be for PNAS.

While APCs are definitely a factor affecting researchers’ submission behavior, it is mostly does so for lower prestige journals rather than for the three elite journals analyzed here. As mentioned in the previous round of revisions, Nature and Science have subscription options. And PNAS authors without funding have access to waivers: https://www.pnas.org/author-center/publication-charges

(3) Line 268, the first suggestion here is not something that would likely work. Thus, I would not put it as the first suggestion.

We made the suggested change.

(4) Data availability - remove AND in 'Aggregated and de-identified data' because it sounds like both are shared. Suggest writing: 'Aggregated, de-identified data..'. I still suggest sharing data/code in a trusted repository (e.g. Dryad, ZENODO...) rather than on GitHub, as per the current recommendation on the best practices for data sharing.

Thank you for your comment regarding data availability. Due to IRB restrictions and the conditions of our ethics approval, we are not permitted to share the survey data used in this study. However, to support transparency and reproducibility, we have made all analysis code available on Zenodo at https://doi.org/10.5281/zenodo.16327580. In addition, we have included a synthetic dataset with the same structure as the original survey data but containing randomly generated values. This allows others to understand the data structure and replicate our analysis pipeline without compromising participant confidentiality.

Reviewer #1 (Public review):

Summary:

Chao et al. produced an updated version of the SpliceAI package using modern deep learning frameworks. This includes data preprocessing, model training, direct prediction, and variant effect prediction scripts. They also added functionality for model fine-tuning and model calibration. They convincingly evaluate their newly trained models against those from the original SpliceAI package and investigate how to extend SpliceAI to make predictions in new species. Their comparisons to the original SpliceAI models are convincing on the grounds of model performance and their evaluation of how well the new models match the original's understanding of non-local mutation effects. However, their evaluation of the new calibration functionality would benefit from a more nuanced discussion of the limitations of calibration.

Strengths

(1) They provide convincing evidence that their new implementation of SpliceAI matches the performance and mutation effect estimation capabilities of the original model on a similar dataset while benefiting from improved computational efficiencies. This will enable faster prediction and retraining of splicing models for new species as well as easier integration with other modern deep learning tools.

(2) They produce models with strong performance on non-human model species and a simple well well-documented pipeline for producing models tuned for any species of interest. This will be a boon for researchers working on splicing in these species and make it easy for researchers working on new species to generate their own models.

(3) Their documentation is clear and abundant. This will greatly aid the ability of others to work with their code base.

Weaknesses

(1) Their discussion of their package's calibration functionality does not adequately acknowledge the limitations of model calibration. This is problematic as this is a package intended for general use and users who are not experienced in modeling broadly and the subfield of model calibration specifically may not already understand these limitations. This could lead to serious errors and misunderstandings down the road. A model is not calibrated or uncalibrated in and of itself, only with respect to a specific dataset. In this case they calibrated with respect to the training dataset, a set of canonical transcript annotations. This is a perfectly valid and reasonable dataset to calibrate against. However, this is unlikely to be the dataset the model is applied to in any downstream use case, and this calibration is not guaranteed or expected to hold for any shift in the dataset distribution. For example, in the next section they use ISM based approaches to evaluate which sequence elements the model is sensitive to and their calibration would not be expected to hold for this set of predictions. This issue is particularly worrying in the case of their model because annotation of canonical transcript splice sites is a task that it is unlikely their model will be applied to after training. Much more likely tasks will be things such as predicting the effects of mutations, identification of splice sites that may be used across isoforms beyond just the canonical one, identification of regulatory sequences through ISM, or evaluation of human created sequences for design or evaluation purposes (such as in the context of an MPSA or designing a gene to splice a particular way), we would not expect their calibration to hold in any of these contexts. To resolve this issue, the authors should clarify and discuss this limitation in their paper (and in the relevant sections of the package documentation) to avoid confusing downstream users.

(2) The clarity of their analysis of mutation effects could be improved with some minor adjustments. While they report median ISM importance correlation it would be helpful to see a histogram of the correlations they observed. Instead of displaying (and calculating correlations using) importance scores of only the reference sequence, showing the importance scores for each nucleotide at each position provides a more informative representation. This would also likely make the plots in 6B clearer.

Author response:

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

Reviewer #1 (Public review):

Summary:

Chao et al. produced an updated version of the SpliceAI package using modern deep learning frameworks. This includes data preprocessing, model training, direct prediction, and variant effect prediction scripts. They also added functionality for model fine-tuning and model calibration. They convincingly evaluate their newly trained models against those from the original SpliceAI package and investigate how to extend SpliceAI to make predictions in new species. While their comparisons to the original SpliceAI models are convincing on the grounds of model performance, their evaluation of how well the new models match the original's understanding of non-local mutation effects is incomplete. Further, their evaluation of the new calibration functionality would benefit from a more nuanced discussion of what set of splice sites their calibration is expected to hold for, and tests in a context for which calibration is needed.

Strengths:

(1) They provide convincing evidence that their new implementation of SpliceAI matches the performance of the original model on a similar dataset while benefiting from improved computational efficiencies. This will enable faster prediction and retraining of splicing models for new species as well as easier integration with other modern deep learning tools.

(2) They produce models with strong performance on non-human model species and a simple, well-documented pipeline for producing models tuned for any species of interest. This will be a boon for researchers working on splicing in these species and make it easy for researchers working on new species to generate their own models.

(3) Their documentation is clear and abundant. This will greatly aid the ability of others to work with their code base.

We thank the reviewer for these positive comments.  

Weaknesses:

(1) The authors' assessment of how much their model retains SpliceAI's understanding of "nonlocal effects of genomic mutations on splice site location and strength" (Figure 6) is not sufficiently supported. Demonstrating this would require showing that for a large number of (non-local) mutations, their model shows the same change in predictions as SpliceAI or that attribution maps for their model and SpliceAI are concordant even at distances from the splice site. Figure 6A comes close to demonstrating this, but only provides anecdotal evidence as it is limited to 2 loci. This could be overcome by summarizing the concordance between ISM maps for the two models and then comparing across many loci. Figure 6B also comes close, but falls short because instead of comparing splicing prediction differences between the models as a function of variants, it compares the average prediction difference as a function of the distance from the splice site. This limits it to only detecting differences in the model's understanding of the local splice site motif sequences. This could be overcome by looking at comparisons between differences in predictions with mutants directly and considering non-local mutants that cause differences in splicing predictions.

We agree that two loci are insufficient to demonstrate preservation of non-local effects. To address this, we have extended our analysis to a larger set of sites: we randomly sampled 100 donor and 100 acceptor sites, applied our ISM procedure over a 5,001 nt window centered at each site for both models, and computed the ISM map as before. We then calculated the Pearson correlation between the collection of OSAI_MANE and SpliceAI ISM importance scores. We also created 10 additional ISM maps similar to those in Figure 6A, which are now provided in Figure S23.

Follow is the revised paragraph in the manuscript’s Results section:

First, we recreated the experiment from Jaganathan et al. in which they mutated every base in a window around exon 9 of the U2SURP gene and calculated its impact on the predicted probability of the acceptor site. We repeated this experiment on exon 2 of the DST gene, again using both SpliceAI and OSAI_MANE . In both cases, we found a strong similarity between the resultant patterns between SpliceAI and OSAI_MANE, as shown in Figure 6A. To evaluate concordance more broadly, we randomly selected 100 donor and 100 acceptor sites and performed the same ISM experiment on each site. The Pearson correlation between SpliceAI and OSAI_MANE yielded an overall median correlation of 0.857 (see Methods; additional DNA logos in Figure S23). 

To characterize the local sequence features that both models focus on, we computed the average decrease in predicted splice-site probability resulting from each of the three possible singlenucleotide substitutions at every position within 80bp for 100 donor and 100 acceptor sites randomly sampled from the test set (Chromosomes 1, 3, 5, 7, and 9). Figure 6B shows the average decrease in splice site strength for each mutation in the format of a DNA logo, for both tools.

We added the following text to the Methods section:

Concordance evaluation of ISM importance scores between OSAI_MANE and SpliceAI

To assess agreement between OSAI_MANE  and SpliceAI across a broad set of splice sites, we applied our ISM procedure to 100 randomly chosen donor sites and 100 randomly chosen acceptor sites. For each site, we extracted a 5,001 nt window centered on the annotated splice junction and, at every coordinate within that window, substituted the reference base with each of the three alternative nucleotides. We recorded the change in predicted splice-site probability for each mutation and then averaged these Δ-scores at each position to produce a 5,001-score ISM importance profile per site.

Next, for each splice site we computed the Pearson correlation coefficient between the paired importance profiles from ensembled OSAI_MANE and ensembled SpliceAI. The median correlation was 0.857 for all splice sites. Ten additional zoom-in representative splice site DNA logo comparisons are provided in Supplementary Figure S23.

(2) The utility of the calibration method described is unclear. When thinking about a calibrated model for splicing, the expectation would be that the models' predicted splicing probabilities would match the true probabilities that positions with that level of prediction confidence are splice sites. However, the actual calibration that they perform only considers positions as splice sites if they are splice sites in the longest isoform of the gene included in the MANE annotation. In other words, they calibrate the model such that the model's predicted splicing probabilities match the probability that a position with that level of confidence is a splice site in one particular isoform for each gene, not the probability that it is a splice site more broadly. Their level of calibration on this set of splice sites may very well not hold to broader sets of splice sites, such as sites from all annotated isoforms, sites that are commonly used in cryptic splicing, or poised sites that can be activated by a variant. This is a particularly important point as much of the utility of SpliceAI comes from its ability to issue variant effect predictions, and they have not demonstrated that this calibration holds in the context of variants. This section could be improved by expanding and clarifying the discussion of what set of splice sites they have demonstrated calibration on, what it means to calibrate against this set of splice sites, and how this calibration is expected to hold or not for other interesting sets of splice sites. Alternatively, or in addition, they could demonstrate how well their calibration holds on different sets of splice sites or show the effect of calibrating their models against different potentially interesting sets of splice sites and discuss how the results do or do not differ.

We thank the reviewer for highlighting the need to clarify our calibration procedure. Both SpliceAI and OpenSpliceAI are trained on a single “canonical” transcript per gene: SpliceAI on the hg 19 Ensembl/Gencode canonical set and OpenSpliceAI on the MANE transcript set. To calibrate each model, we applied post-hoc temperature scaling, i.e. a single learnable parameter that rescales the logits before the softmax. This adjustment does not alter the model’s ranking or discrimination (AUC/precision–recall) but simply aligns the predicted probabilities for donor, acceptor, and non-splice classes with their observed frequencies. As shown in our reliability diagrams (Fig. S16-S22), temperature scaling yields negligible changes in performance, confirming that both SpliceAI and OpenSpliceAI were already well-calibrated. However, we acknowledge that we didn’t measure how calibration might affect predictions on non-canonical splice sites or on cryptic splicing. It is possible that calibration might have a detrimental effect on those, but because this is not a key claim of our paper, we decided not to do further experiments. We have updated the manuscript to acknowledge this potential shortcoming; please see the revised paragraph in our next response.

(3) It is difficult to assess how well their calibration method works in general because their original models are already well calibrated, so their calibration method finds temperatures very close to 1 and only produces very small and hard to assess changes in calibration metrics. This makes it very hard to distinguish if the calibration method works, as it doesn't really produce any changes. It would be helpful to demonstrate the calibration method on a model that requires calibration or on a dataset for which the current model is not well calibrated, so that the impact of the calibration method could be observed.

It’s true that the models we calibrated didn’t need many changes. It is possible that the calibration methods we used (which were not ours, but which were described in earlier publications) can’t improve the models much. We toned down our comments about this procedure, as follows.

Original:

“Collectively, these results demonstrate that OSAIs were already well-calibrated, and this consistency across species underscores the robustness of OpenSpliceAI’s training approach in diverse genomic contexts.”

Revised:

“We observed very small changes after calibration across phylogenetically diverse species, suggesting that OpenSpliceAI’s training regimen yielded well‐calibrated models, although it is possible that a different calibration algorithm might produce further improvements in performance.”

Reviewer #2 (Public review):

Summary:

The paper by Chao et al offers a reimplementation of the SpliceAI algorithm in PyTorch so that the model can more easily/efficiently be retrained. They apply their new implementation of the SpliceAI algorithm, which they call OpenSpliceAI, to several species and compare it against the original model, showing that the results are very similar and that in some small species, pretraining on other species helps improve performance.

Strengths:

On the upside, the code runs fine, and it is well documented.

Weaknesses:

The paper itself does not offer much beyond reimplementing SpliceAI. There is no new algorithm, new analysis, new data, or new insights into RNA splicing. There is no comparison to many of the alternative methods that have since been published to surpass SpliceAI. Given that some of the authors are well-known with a long history of important contributions, our expectations were admittedly different. Still, we hope some readers will find the new implementation useful.

We thank the reviewer for the feedback. We have clarified that OpenSpliceAI is an open-source PyTorch reimplementation optimized for efficient retraining and transfer learning, designed to analyze cross-species performance gains, and supported by a thorough benchmark and the release of several pretrained models to clearly position our contribution.

Reviewer #3 (Public review):

Summary:

The authors present OpenSpliceAI, a PyTorch-based reimplementation of the well-known SpliceAI deep learning model for splicing prediction. The core architecture remains unchanged, but the reimplementation demonstrates convincing improvements in usability, runtime performance, and potential for cross-species application.

Strengths:

The improvements are well-supported by comparative benchmarks, and the work is valuable given its strong potential to broaden the adoption of splicing prediction tools across computational and experimental biology communities.

Major comments:

Can fine-tuning also be used to improve prediction for human splicing? Specifically, are models trained on other species and then fine-tuned with human data able to perform better on human splicing prediction? This would enhance the model's utility for more users, and ideally, such fine-tuned models should be made available.

We evaluated transfer learning by fine-tuning models pretrained on mouse (OSAI_Mouse), honeybee (OSAI_Honeybee), Arabidopsis (OSAI_Arabidopsis), and zebrafish (OSAI_Zebrafish) on human data. While transfer learning accelerated convergence compared to training from scratch, the final human splicing prediction accuracy was comparable between fine-tuned and scratch-trained models, suggesting that performance on our current human dataset is nearing saturation under this architecture.

We added the following paragraph to the Discussion section:

We also evaluated pretraining on mouse (OSAI_Mouse), honeybee (OSAI_Honeybee), zebrafish (OSAI_Zebrafish), and Arabidopsis (OSAI_Arabidopsis) followed by fine-tuning on the human MANE dataset. While cross-species pretraining substantially accelerated convergence during fine-tuning, the final human splicing-prediction accuracy was comparable to that of a model trained from scratch on human data. This result indicates that our architecture seems to capture all relevant splicing features from human training data alone, and thus gains little or no benefit from crossspecies transfer learning in this context (see Figure S24).

Reviewer #1 (Recommendations for the authors):

We thank the editor for summarizing the points raised by each reviewer. Below is our point-bypoint response to each comment:

(1) In Figure 3 (and generally in the other figures) OpenSpliceAI should be replaced with OSAI_{Training dataset} because otherwise it is hard to tell which precise model is being compared. And in Figure 3 it is especially important to emphasize that you are comparing a SpliceAI model trained on Human data to an OSAI model trained and evaluated on a different species.

We have updated the labels in Figures 3, replacing “OpenSpliceAI” with “OSAI_{training dataset}” to more clearly specify which model is being compared.

(2) Are genes paralogous to training set genes removed from the validation set as well as the test set? If you are worried about data leakage in the test set, it makes sense to also consider validation set leakage.

Thank you for this helpful suggestion. We fully agree, and to avoid any data leakage we implemented the identical filtering pipeline for both validation and test sets: we excluded all sequences paralogous or homologous to sequences in the training set, and further removed any sequence sharing > 80 % length overlap and > 80 % sequence identity with training sequences. The effect of this filtering on the validation set is summarized in Supplementary Figure S7C.

Reviewer #3 (Recommendations for the authors):

(1) The legend in Figure 3 is somewhat confusing. The labels like "SpliceAI-Keras (species name)" may imply that the model was retrained using data from that species, but that's not the case, correct?

Yes, “SpliceAI-Keras (species name)” was not retrained; it refers to the released SpliceAI model evaluated on the specified species dataset. We have revised the Figure 3 legends, changing “SpliceAI-Keras (species name)” to “SpliceAI-Keras” to clarify this.

(2) Please address the minor issues with the code, including ensuring the conda install works across various systems.

We have addressed the issues you mentioned. OpenSpliceAI is now available on Conda and can be installed with:  conda install openspliceai. 

The conda package homepage is at: https://anaconda.org/khchao/openspliceai We’ve also corrected all broken links in the documentation.

(3) Utility:

I followed all the steps in the Quick Start Guide, and aside from the issues mentioned below, everything worked as expected.

I attempted installation using conda as described in the instructions, but it was unsuccessful. I assume this method is not yet supported.

In Quick Start Guide: predict, the link labeled "GitHub (models/spliceai-mane/10000nt/)" appears to be incorrect. The correct path is likely "GitHub (models/openspliceaimane/10000nt/)".

In Quick Start Guide: variant (https://ccb.jhu.edu/openspliceai/content/quick_start_guide/quickstart_variant.html#quick-startvariant), some of the download links for input files were broken. While I was able to find some files in the GitHub repository, I think the -A option should point to data/grch37.txt, not examples/data/input.vcf, and the -I option should be examples/data/input.vcf, not data/vcf/input.vcf.

Thank you for catching these issues. We’ve now addressed all issues concerning Conda installation and file links. We thank the editor for thoroughly testing our code and reviewing the documentation.

A definition that is key. A mean is about balance. Median is making it mini.

Paying close attention and realizing the mode would oftentimes be seen.

I'm really interested in King's distinction between militancy and violence. I’m not sure where he draws the line between the two. I think he’s getting at a wholehearted dedication to the cause, and a critical mass of dedicated people coming together to organize action. Here are the first definitions that pop up on Google: Militant means “combative and aggressive in support of a political or social cause, and typically favoring extreme, violent, or confrontational methods.” Violent means “using or involving physical force intended to hurt, damage, or kill someone or something.” I guess militancy doesn’t necessitate use of force, but under these definitions requires a direct confrontation and refusal of the status quo. Looking at the definitions (which vary widely between sources) reminded me of the politics of how these labels are applied, to the point that they’re almost meaningless without further explanation.

This is quite optimistic, because although many people are not ready to be violent themselves, most of the white population would allow or even advocate for violence from others (ex. police, lynch mobs, those in power). They are bystanders, they see violence and they do nothing to stop it.

Love a user friendly info source.

Archives are such great sources of knowledge on a variety of topics.

Audience and speaker are the two fundamental requirements for communication.

Great book I've read it

This is typically the "make or break" point of a novel.

Code switching

This happens often with AAVE. People see it as improper, even though it's a perfectly acceptable English dialect.

Respecting alternate human communication methods is basic human decency.

I've never heard this term before. Its an interesting way to define your personal speaking and writing method.

United Nations Educational, Scientific and Cultural Organization

relating to a person's awareness of the position and movement of the parts of the body by means of sensory organs (proprioceptors) in the muscles and joints.-Oxford Dictionary

very well said.

This is a really creative idea and could be great for people who love to write or create for fun

The important part of most childrens' stories is that they make the readers feel empowered

I think stories are so important for everyone, because for kids it's fun for them to hear and imagine it, and for adults, it keeps them young and the imaginative qualities of kids. Also when stories are told through generations, it becomes a piece of family history and it could be the story that can pick up their mood or make them feel better after a long day

interesting concept to me- everyone has their own voice that they developed through culture, their family and environment they grew up in

In principle I understand but I don't understand how the equation explains the message it's trying to convey @rebelford

i.e., scholars are divided by discipline, if they get to claim X is a discipline, so can IS

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Reply to the reviewers

Response to reviewers

We thank the reviewers for their constructive feedback, which has greatly improved the clarity and rigor of our manuscript. We have carefully addressed each comment below, indicating changes made to the text, figures, or supplementary material where appropriate. References to line numbers correspond to the revised version of the manuscript.

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

* In this paper, the authors focus on the role of Reticulon-1C in concert with Spastin in response to axonal injury. In data mining, they find axonal mRNAs encoding for ER-associated proteins including Rtn-1. They establish a knockdown targeting both Rtn-1 isoforms Rtn-1A and Rtn-1C. They observe decreased beta-3-Tubulin levels in the soma while axonal protein levels are unchanged. In microfluidic devices, they characterise the effect of a compartment-specific Rtn-1 KD on axonal outgrowth in the axonal compartment. The authors quantify axonal outgrowth, seeing increased outgrowth in an axonal compartment-specific Rtn-1 KD, while the effect seems to be reversed when applying the KD construct in the somatic compartment. When focussing on the axonal growth cone, they find the Rtn-1 KD shows differences in several morphological features of the growth cone. They find an increase in Tubulin levels in an axonal compartment-specific, but a decrease in a somatic compartment-specific Rtn-1 KD. Colocalisation of Rtn-1C and Spastin is shown to be monolaterally increased following axotomy. Combining axotomy with the Rtn-1 KD shows increases in dynamic microtubule growth rates and track lengths. In another model system, neuron balls, they show Rtn1-C, but not Rtn1-A to be present in the axon. In a puro-PLA assay they also show it can be synthesised in the axonal compartment. To investigate the mechanism enabling the cooperation between Spastin and Rtn-1C, they move to a cell line model in which they see a correlating distribution between Spastin and Rtn-1C but not Rtn-1A. Finally, they use in silico modelling to speculate on binding between Spastin domains and Rtn-1 isoforms.*

Major comment:

The rationale behind the work is convincing, however some interpretations are presented as more robust than some data allow. Most notably, while the interaction between Rtn-1 and Spastin has been shown prior to this study, it is only presented here through in silico analysis. In figure 5, an increase in the growth rate of dynamic microtubules is observed in either a Rtn-1C KD or by using a Spastin-inhibitor. Due to a described increase in colocalisation between Rtn-1C and Spastin (5A), the increase in growth rate is displayed as caused by Rtn-1 promoting Spastin's severing ability. This result might however be correlative. Further in the injured samples, Spastin-levels seemingly increase (in the representative images) and it is thus not surprising that the level of Rtn-1C colocalising with Spastin increases as well. This might not be indicative of a cooperation and further experimental evidence are required.

R: We thank the reviewer for this thoughtful comment. We agree that our interpretation should be more cautious, and we have revised the Title, Results and Discussion sections accordingly. In particular:

1. Following yours and other reviewer comments, we have analyzed a new set of experiments regarding the STED images of non-injured and injured axons. To eliminate the risk of artifactual descriptions, we have avoided deconvolution and worked directly with raw STED images (Figure 5A). Under these conditions, the distribution of Spastin and its intensity in distal axons are not modified by injury, nor those of Rtn-1C and Spastin (Supplementary figure 4). We emphasize in the revised text that the in silico modeling we present is supportive, but not definitive, of a direct interaction. To address this concern, we clarify that our study builds on prior evidence of biochemical interaction between Rtn-1C and Spastin (Mannan et al., 2006), and that our own data demonstrate: i) compatible subcellular distribution in axons by super-resolution (STED microscopy, Figure 5A);ii) a potential functional interplay in axons (rescue of β3-tubulin levels by Spastin inhibition, Figure 5B), and iii) isoform-specific co-distribution with Spastin in heterologous cells that is associated with changes on microtubule integrity (see improved Figure 7). Together, these results go beyond correlative localization, but we acknowledge that they do not directly demonstrate a molecular complex in axons. Thus, we now indicate that "Although we did not directly test their molecular association, these results are consistent with Rtn-1C and Spastin sharing a similar subcellular localization, potentially enabling their functional interaction in distal axons" (lines 285-287)

We would like to clarify a possible misunderstanding: in our experiments, the increase in microtubule growth rate was observed after axonal Rtn-1 KD. Spastazoline (SPTZ) only prevented the reduction in β3-tubulin levels induced by Rtn-1 KD, while leaving the KD-driven increase in growth rate and track length unaffected (Figures 5B-E). Thus, our interpretation is that axonal Rtn-1 KD correlates with increased Spastin function. (lines 307-309)

Other comments:

• Generally, graphs would benefit from individual values plotted as well as the summary. Font sizes and types (but rarely) are sometimes inconsistent. Proteins should be consistently written (capitalised or not).

__R: __ We agree with the reviewer and thank for taking the time for noticing these inconsistencies as it significantly affects the quality of the work. We have improved several figures and added graphs plotting individual values (Figures: 2 C, 2E; 4 (A-E); 5E; 6D). We have reviewed the Font size and types more carefully and capitalized the proteins accordingly.

• *Table 1 and figure 1 present data collected from a vast amount of resources. It should be highlighted that datasets from which data was obtained includes many different models, different DIVs and neuronal cell types. Figure 1B may benefit from a different colour scheme. "Ex-vivo" should be "Ex vivo". For "ER mRNAs are a relevant category" it is not described what "relevant" would mean in this context. The title might remove this small part or describe it in the text. It should be described how it is decided that mRNAs are "common". *

• *

__R: __We have now highlighted in the result section the diverse origins of the analyzed samples; We removed the indicated part from the text and explained that common mRNAs were chosen based on the Benjamini-Hochberg (Ben) analysis. (Page 33, lines 1299-1304).

* - Figure 2: add description to y-axis to describe what fold change is displayed, applies to multiple figures. Will improve readability of the figures. In 2C, the ROI showing neuronal somata should be increased to show part of the axon and not cut off the soma.*

• *

__R: __We thank the reviewer for taking the time to highlight this. We have included this modification in figure 2 and throughout the article. We have also enlarged the indicated ROIs in figure 2C as requested. (Page 34)

• *Figure 3: Three out of four axonal compartments seem to be comprised of dying or damaged axons. Especially the axonal KD scrambled image. It should be ensured that neuronal cultures are healthy. *

• *

__R: __We completely agree with the reviewer that the selected images were not describing the general good health of axons which has been accredited by the lack of fragmentation and functional responsiveness shown in (Figure 4 and 5 B, C, E). Thus, we have now replaced the previous axonal fields by more representative ones (Figure 3). (page 36)

• *

Typo in "intersections". The schematic of 3B is a great addition to explain the graphs above. Perhaps it could be a bit refined as it is currently hard to see whether this is a neuron or a growth cone without context. Maybe show where the axon connects to the depicted growth cones and change the third icon which looks like it was crossed out. Small formatting issues: remove additional space bar before "Figure 3." And add after "Bar"

__R: __Many thanks for these great suggestions. We have now improved the figures as suggested and changed the indicated formatting issues. (page 36)

- Figure 4: If not misunderstanding what is depicted, in 4A and B, different lookup tables are used to depict the same signal. Only one of each images is necessary. Do the axons have more tiny branches in the Rtn-1 KD condition in 4A? Unclear why Rtn-1 levels are increased in the Rtn-1 KD (4C), please clarify.

• *

__R: __We thank the reviewer for these observations. The reviewer is correct that different lookup tables were initially applied to the same image. Our intention was to highlight the fine distribution of axonal Rtn-1, but since this aspect is already clearly shown in previous figures, we now retain only a single lookup table. The appearance of tiny branches in the Rtn-1 KD condition represents an isolated observation and does not reflect a consistent or robust phenotype associated with Rtn-1 KD.

As the reviewer points out, the increase of Rtn-1 in the cell bodies of injured neurons following axonal KD was initially surprising to us. However, this was a consistent phenomenon, as shown in the improved Figure 4. Of note, previous studies have reported that total Rtn-1C (but not Rtn-1A) levels increase in response to injury in cortical neurons(Fan et al., 2018). In our case, we interpret this as a compensatory somatic response triggered by the local reduction of Rtn-1 in injured axons. This interpretation is also consistent with the apparent lack of effect of siRNA on distal axonal Rtn-1 levels when applied locally after injury (while somatic application of the same siRNA does reduce axonal Rtn-1). Thus, after 24 hours of KD, the somatic upregulation of Rtn-1 may partially compensate for its expected local synthesis decrease. We have clarified this assumption in the revised text. (lines 247-251)

- Figure 5: It may be easier to understand what "axotomy" samples are if just referred to as "injured" as later in the same figure. The procedure could also very briefly be explained in the results. 5C should depict AUC in µm2 not µm. 5D Spastin is barely visible, brightness and contrast should be adjusted to enhance visibility.

• *

__R: __We thank the reviewer for these helpful suggestions and have implemented the requested changes in Figure 5. Specifically:

We now consistently refer to "axotomy" samples as "injured" throughout the figure and article. In addition, a brief explanation of the axotomy procedure has been added before Figure 2 and before figure 5, also the description has been clarified in Materials and methods. (lines 191-192) and (lines 289-290) and (lines 779-787)

To improve the reproducibility of our outgrowth measurements, we revised this analysis approach. Based on previous work from a co-autor (McCurdy et al., 2019), instead of reporting the "relative number of intersections," we now present the total counts obtained from Sholl analysis of binarized axons (see Methods). To this end, we took advantage of the NeuroAnatomy plugin of FIJI, which more precisely tracks axon trajectories and makes the measurement more independent of axon width. Also, this new approach avoids the conflict we had with what we considered the "first line" after the groove ends, which was a bit of arbitrary. Accordingly, the correct term is now "summation of intersections (sum.)" at different distance bins, as reflected in Figure 5D. (page 40)

For the former Figure 5D (now Figure 5B), we have improved the acquisition of representative images and applied a different set of lookup tables to enhance visibility. (page 40)

- Figure 6: It should be made clear why it is necessary to switch to another model system just for 6A, please indicate this in the text. PCR bands seem very pixelated, check the quality. It is unclear why soma genes/proteins were only tested with either PCR or WB others with both. Rtn-1C and Rtn1-A should be presented in the same order in the PCR and WB panel. Correct "Rtn1-1A" typo. In 6D, 1.5 dots per soma seems like a low number. When normalized to the area the soma vs the axon occupies, the compartmentalization does not work? Maybe it makes sense to refine analysis or apply puromycin in the somatic compartment and analyze the axonal compartment as comparison?

__R: __Many thanks for these observations. We have now included the following clarification in the text: "We sought to characterize the isoform expression of Rtn-1 mRNA and protein in both axons and cell bodies. Because microfluidic chambers yield only limited cellular material, we adopted an alternative culture approach using 'neuronballs.' This method enables the segregation of an axon-enriched fraction by mechanically separating axons from somato-dendritic structures" (lines 375-376).

The resolution of PCR bands has been improved in the revised figure. Note that because the amount of cellular material is relatively scarce, we did not obtain too strong bands.

The difference in the genes/proteins used for characterizing RNA and protein samples reflects our intention to treat both approaches as complementary. The PCR markers were primarily included to confirm sample purity, which also applies to the WB samples since they derive from the same preparation. In both assays, we used MAP2 as a dendritic marker to demonstrate axonal purity. While we acknowledge that the same genes could have been tested by both methods, we believe the results as presented adequately demonstrate the effective isolation of axons.

We have switched the order of Rtn-1C/1A for consistency across PCR and WB panels and corrected the indicated typo in Figure 6A.

We agree with the reviewer that an average of 1.5 puncta per soma initially appeared low. We have identified at least three reasons for this:

First, the signal derives from only a 15-minute puromycin pulse, which is a very short labeling window. Second, our puro-PLA assay is particularly stringent, as ligation relies directly on puromycin- and Rtn-1C-labeled primary antibodies, without the additional spacing normally introduced by secondary antibodies. In standard PLA, the critical distance for amplification is ~30-40 nm, whereas in our assay this distance is even more restrictive. Third, in our initial analysis we applied an overly cautious threshold to define "true" amplification. We have now refined this threshold using a baseline defined by the absence of puromycin stimulation. With this improved criterion, we now quantify an average of ~5 puncta per soma and ~10 puncta per 1000 µm² of axonal area (Figure 6D and Supplementary Figure 3D). Assuming a neuronal soma diameter of 15 µm (area ≈ 176.71 µm²), this yields ~0.028 puncta per µm² in soma. In comparison, axons display ~0.01 puncta per µm², approximately one-third of the soma value, which is compatible with the idea thar cell bodies dominate neuronal protein synthesis.

Following the reviewer's valuable suggestion, we performed additional quantifications in which puromycin was applied exclusively to the somatic compartment. Under these conditions, we still observed amplification in axons (~5 puncta per 1000 µm²), although this value was significantly lower than when puromycin was applied directly to axons. This analysis provided a novel appreciation of the puro-PLA technique in neurons: at least half of the signal originates in the axonal compartment, while a portion may reflect proteins synthesized in soma and transported anterogradely to the axon through yet-unknown mechanisms (potentially involving rapid anterograde transport) (Figure 6D). (page 42)

• Figure 7: 7A shows two images depicting the same information that may not be needed. Can probably be removed. In 7B there is no negative (or any) correlation between Spastin levels and Tubulin, however later it is mentioned that Rtn-1C transports Spastin thus causing a decrease in Tubulin at certain locations? It is nclear if Spastin levels vary intensely between different samples. Mean intensity of the somatic area may be beneficial to rule this out. 7B Tubulin on the right top panel seems to have a decrease in Tubulin levels which is not visible due to the Y axis of Tubulin being set to a different range than the middle and lower panel. The average of line scans from multiple cells may be helpful to determine whether there is indeed no colocalization between Rtn-1A and Spastin. The provided representative images seem to show similar degrees of colocalization between Spastin and Rtn-1A/C.

• *

__R: __We thank the reviewer for these valuable observations and acknowledge that Figure 7 may have caused confusion. We have eliminated the fluorescence line-scan traces, as they can be biased depending on the region of the cell analyzed. Although this may not have been sufficiently emphasized in the text, we had already performed a quantitative colocalization analysis across multiple cells and independent experiments, using Mander's coefficients (Figure 7B). These analyses showed higher colocalization between Rtn-1C and Spastin compared to Rtn-1A. Regarding the concerns about variability in Spastin levels or possible bias from Y-axis scaling, we have eliminated those traces by the risk of bias. Also, we had already quantified the total tubulin fluorescence intensity across all the z-stacks and from multiple cells from independent experiments as shown in Figure 7C. To further rule out artifacts caused by variable transfection efficiency, we quantified total fluorescence intensity in both RFP and GFP channels across conditions. As shown in Supplementary Figure 6, no significant differences were observed, suggesting that the changes in tubulin reflect specific effects of Spastin/Rtn-1C co-expression rather than variability in expression levels.

Results: - It would be helpful to reiterate the hypothesis at the start to ease the reading flow.

__ R: __Many thanks, we have introduced a line reiterating the hypothesis as suggested (lines 117-118)

- There seems to be minor redundancy in lines 132-138.

• *

__R: __Indeed, we have now removed the indicated phrase.

• There are several spellings, proof-reading is recommended. For example, in line 136 should be "promotes". 160 "localla", 192 should be "the actin cytoskeleton".,194 should be "we first examined", 195 should be "Different", 223 "using", 259 "axons".

__R: __We apologize for the spellings; we have now performed a careful proof-reading and introduced these corrections.

- 154-155: Unclear, why the lower MW Rtn-1C was seen as more important.

__R: __We apologize for not being clear enough. It is not necessarily more important, but we just took the Rtn-1C molecular weight as reference for the analysis considering that this isoform is the predominant in axons. In any case we have found a significant effect for both isoforms at least on siRNA 2 (data not shown), which is now expressed in the text (line 165-169) : "We also examined the 180 kDa band and found that siRNA 1 reduced expression to a mean of 0.41 relative to Scr, showing a strong trend that did not reach statistical significance (p = 0.05; N = 3; Wilcoxon test compared to 1, data not shown). In contrast, siRNA 2 further reduced expression to a mean of 0.29, which was statistically significant (p = 0.04; N = 3; Wilcoxon test compared to 1, data not shown)."

- 167 results of 2E not stated before interpreting them.

• *

__R: __We have corrected this mistake.

- 181 would suggest "outline" instead of "perimeter".

• *

__R: __We have considered this suggestion and included "outline", nevertheless the morphometric parameter is defined as perimeter, so we retained the term, but with the suggested clarification.

• *

- 183-184 "longest shortest path" is a confusing term.

__R: __We agree that it is a confusing term, thus have now introduced multiple clarifications for the term in the leyend of figure 3 (page 36), and with more detail in a new section of Materials and methods (lines 697-699).

• figure 4B should be referenced earlier in the sentence.

__R: __We have corrected the sentence in the text.

- 243-244 may be correlation. Rtn-1 and Spastin do not necessarily interact so that this result is achieved.

• *

__R: __Thanks for the clarification, we are aware that so far in the manuscript the conclusion is not correct, thus now we have stated at the end of the paragraph: "Together, these observations suggest that axonal Rtn-1 KD correlates with higher Spastin microtubule severing" (lines 307-309)

- 246: In figure 1 the KD seemed to influence both Rtn-1 isoforms, why not here anymore? 259 "axons". 284 "counteract" instead of "suppress"?

• *

__R: __We acknowledge the confusion at this point of the article because of measuring a specific isoform. We now indicate that we will focus on Rtn-1C because of previous evidence of the literature pointing to an interaction of Rtn-1C with Spastin (line 264-267). Later we show that Rtn-1C is the predominant isoform in axons (Figure 6). We have corrected all the suggestions in the manuscripts.

- 485: rephrase as the interaction between Rtn-1C with Spastin has not been shown directly in these experiments.

__R: __Many thanks for the relevant clarification. Now, we have corrected:" Here, we have described an emerging mechanism relating Rtn-1C with the activity of Spastin, which is the most frequently mutated isoform in HSP (Hazan et al., 1999; Mannan et al., 2006)." (line 632-634). * Methods: 535 "in PBS". 543 citation error. 689-699 is it necessary to add a gaussian blur?*

• *

__R: __We have corrected the words and removed the wrong reference. Regarding the use of Gaussian blur, it is a very important point. We used this approach because, in our experimental conditions, it was critical to highlight moving particles that otherwise would go unnoticed by the noise. This was particularly manifest for the seemingly more "unorganized" movements of axonal microtubules after injury.

References: Mannan, A U et al. appears twice in the citation list (36 and 44).

* *R: Many thanks for the observation. Now we have corrected it.

Reviewer #1 (Significance (Required)):

Overall, this manuscript describes novel fundings which will be interesting to the neuronal cell biology community and scientists working on the field of neuronal injury and regeneration. It is well structured, and the data are mostly well presented but sometimes conclusions are over-interpreted. However, several points need to be addressed in a more convincing way.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Axonal mRNA localization and localized translation support many neuronal functions and is an important determinant of the regenerative potential of axons after injury. How this works mechanistically remains unclear. The authors present a well performed and technically challenging study in which they identify RTN-1 as a regulator of axonal outgrowth after injury. They provide evidence using experiments in microfluidic chambers that RTN1 is locally synthesized in axons. Interestingly, they identify a (local) interplay between RTN1 and Spastin which affects microtubules and thereby regulates the outgrowth of cortical axons after injury. This study provides an interesting new link between a locally synthesized protein (RTN1) and a microtubule-regulating protein Spastin that is changed upon axon injury. This provides an advance in our understanding in axon regeneration after injury and provides the basis for new studies that can further investigate this interplay. Although interesting, I have several concerns that should be clarified and are needed to substantiate the findings and model presented in this study.

Major concerns:

2. In figure 1, the authors provide an analysis of overlapping axonal mRNAs. There are more axonal transcriptome studies and a recent study by von Kugelgen and Chekulaeva (2020; doi: 10.1002/wrna.1590) already performed such an analysis, which included more studies. It would be good to mention this. It can be perceived that studies were now chosen to get the outcome that Rtn-1 is present in all studies. For example, von Kugelgen finds mRNA coding for RTN3, another ER structural protein, as present in 16 out of 20 studies analyzed. That said, the authors present more reasons to look at Rtn-1, so the selection to continue with this protein remains valid but can be written up differently so not to present it as the 'sole' ER-shaping protein consistently present in axonal transcriptomes. __R: __We appreciate this important observation to enrich the article; we are aware that the transcriptome data can be even further expanded to more recent studies. Thus, we have now included this reference in the main text and highlighted the relevant finding of RTN3. However, Kugelgen and Chekulaeva used data from dendrites/axons (neurites). Thus, we indicate that "...On a similar approach, but combining data from dendrites and axons, it was found that Reticulon-3 *mRNA is present in 16 out of 20 studies, further suggesting a wider presence of other mRNAs coding for ER structural proteins in axons " (line 128-131)

3. The description of methods is currently insufficient and incomplete and does not allow for reproducibility of this study. For example, different Rtn-1 antibodies seem to be used in this study. Is the same antibody used for staining and WB? There is no listing of any of the antibodies used in the study and which one is used for which technique/experiment. This should be clarified and should be easy to do so in the methods section (antibody name, origin/company, dilution used) to enhance reproducibility of this study. This is not limited to primary antibodies and any information on secondary antibodies, including what was used for STED is completely missing.*

4. *

__R: __Thanks for these critical comments. First, we apologize for the former method version which was mistakenly not as accurate as it should. We have now revisited it and improved several points throughout this section. Regarding the use of primary and secondary antibodies, plasmids, siRNAs, and general reagents, they are all indicated in the Supplementary material, including company and dilution ("Reagent tables").

• The timeline of KD experiments in Figures 2 and 3 are unclear. For the Western blot KD is performed at DIV7 and collected 48 hours later. However, this is not specified for the stainings done in Figure 2C-E. Is this also at DIV7 and then for 48 hours? In figure 3 the siRNA is added at DIV8 (together with axotomy) and outgrowth is measured 24 hours later. Is 24 hours sufficient to achieve knockdown? Is this also what was done for stainings? Later on in Figure 5B, 48 hours of KD is again used. It is unclear what the rationale of these differing timepoints is. Why was this chosen? Is the timeline also the reason for the difference in segment lengths chosen? In Figure 3, there is a significant effect on outgrowth in the KD in the 'mid-range' which is not present in Figure 5.*

__R: __We regret the confusion, now all this information is explicitly clarified in the main text (lines 297-299) and the corresponding figure legends. We have strong reasons to have used these different time points. Figure 2 A-B is aimed at validating the siRNA against Rtn-1 thus we treated 7 DIV cultures for 48 hours to be sure of revealing a global effect by WB. In figure 2 C-D, we used the same 7 DIV cultures, but only for 24 hours. The reason for this is that, once the RNAi was validated, we explored its control on local synthesis in a shorter period based in previous literature supporting that axonal KD for 24 hours is sufficient for regulating axonal transcripts (Batista et al., 2017; Gracias et al., 2014; Lucci et al., 2020). We are also confident of using this time point based in the new supplementary figure 3D that shows a significant decrease on puro-PLA signal (indicative of Rtn-1C synthesis) 24 hours after axonal KD.

In figure 3, we performed axotomy thus we had to wait a longer period for axons to grow (8 DIV) before fully cut them out, in this case we performed axonal KD from 8 to 9 DIVs. This is the same period used for the staining and quantifications shown in figure 4. All this is properly clarified in the main text and figures.

In Figure 5 we performed a more challenging experiment that required to transfect cells with an EB3-GFP plasmid, then perform axotomy along with axonal KD as well as pharmacological treatment selectively in axonal compartment. First, we tried to measure microtubule dynamics under the same temporal frame of figure 3. Nevertheless, expression levels of EB3-GFP were not adequate for axonal measurements by live-cell imaging. Therefore, compared to figure 3, we increased the time frame after axotomy 24 hours (from 9 to 10 DIV) by this technical reason, but also to explore whether the changes on tubulin intensity might be revealed more clearly (which was the case, figure 5B). These considerations are now included in the main text

Regarding the significant effect on outgrowth in the KD in the 'mid-range' which is not present in Figure 5. Given that in figure 5D axons are left growing for two days instead of one, the number of intersections and the differences between conditions is modified compared to figure 3, while retaining the overall trends. Note that to improve the reproducibility of our outgrowth measurements, we revised this analysis approach. Based on previous work of a co-autor (McCurdy et al., 2019), instead of reporting the "relative number of intersections," we now present the total counts obtained from the Sholl analysis of binarized axons (see Materials and methods). To this end, we took advantage of the NeuroAnatomy plugin of FIJI, which precisely tracks axon trajectories and makes the measurements more independent of axon width segmentation. Also, this new approach avoids the conflict we had with what we considered the "first line" after the groove ends, which was a bit of arbitrary. Accordingly, the correct term is now "summation of intersections (sum.)" at different distance bins, as reflected in the new Figure 5D.

Could the authors provide a rescue condition for their siRNA (using a siRNA-resistant construct) to show that their siRNA is specific for RTN1. They nicely show the efficiency of the siRNA but not its specificity. This is crucial because if not specific, this will affect a large part of their study. They already have RTN1A and RTN1C constructs available. Such a rescue experiment should ideally also be performed for one or more of their phenotypic experiments, such as the one presented in Figure 3A or 5 to show that the phenotype is really RTN1 dependent. If done by re-expressing either RTN1A or RTN1C, this could provide insightful information on the relevant isoforms.

__R: __We agree with the reviewer that this is a critical point. A major challenge in demonstrating the functional role of axonally synthesized proteins using a KD approach is that the rescue may also need to occur locally. Since axonal Rtn-1 appears to play a distinct role compared to its somato-dendritic counterpart (Figure 3), a siRNA-resistant construct would ideally require an axon-targeting sequence to restore local synthesis. As this is technically demanding, we have not yet been able to perform such an experiment, but we are actively working on identifying the optimal sequence to direct Rtn-1C to axons. Importantly, studies performing axonal KD typically rely on at least two independent siRNA sequences, thereby minimizing the likelihood that a phenotype arises from off-target effects. Thus, we have now validated a third siRNA (siRNA 3), which selectively downregulates Rtn-1C. Then, following the same experimental frame of figure 3, we performed axonal Rtn-1 KD after injury and observed that siRNA 3 also significantly increases the outgrowth of injured axons (Supplementary figure 2). This suggests that, at least this phenotype, is not product of an off-target effect. Complementarily, pharmacological rescue with the Spastin inhibitor SPTZ mitigated both the reduction in distal axonal β3-tubulin and the increase on axon outgrowth, supporting that the observed phenotypes are unlikely to arise from off-target effects. If these effects were due to random interference with unrelated mRNA targets, inhibition of an ostensibly independent target such as Spastin would not be expected to yield such a consistent rescue. Accordingly, SPTZ treatment alone did not increase β3-tubulin, indicating that its action is specifically contingent upon Rtn-1 KD. Taken together, the pharmacological rescue in axons (Figure 5B) and the Rtn-1C/Spastin co-distribution in heterologous cells, which correlates with preserved microtubules (improved Figure 7), provide converging evidence to suggest that Rtn-1C-Spastin interplay may underly the observed phenotypes in axons.

• I find the data presented in Figure 4A/B confusing. Axonal RTN-1 KD does not reduce axonal RTN1 levels, but somatic KD does. I understand that this implies most protein comes from the soma, and the authors indeed present an explanation that increased somatic RTN1 occurs after axonal KD as a compensation mechanism. However, this can also be interpreted that there is no axonal synthesis of RTN1 after injury and axonal KD has indirect or even aspecific effects. Their model depends on this difference. Their data in Figure 6 could provide supporting evidence if it shows RTN1 puro-PLA after injury. Along these same lines, in Figure 6, they nicely include a compartment control for puro-PLA. It therefore seems doable to include a somatic puromycin control for their axonal puro-PLA, to exclude and diffusion/transport of the newly synthesized peptides. This is especially considering two recent papers reporting on this possible phenomenon, although these studies were not performed in neurons.*

__R: __We consider the possibility that after injury there is no axonal Rtn-1 synthesis as a plausible and relevant appreciation. Unfortunately, we could not perform a puro-PLA experiment after injury, which would have provided a more definite answer. However, now we are more confident of regulating Rtn-1 synthesis before injury as supported by a new supplementary figure 3D that shows a significant decrease on puro-PLA signal (indicative of Rtn-1C synthesis) 24 hours after axonal KD. Thus, based on the similar phenotypes observed before and after injury, we consider our results are still compatible with Rtn-1 axonal synthesis being downregulated, but not absent after injury. First, axonal Rtn-1 KD decreased β3-tubulin levels before and after injury according to figure 5B and the improved statistical analysis performed on figure 2E. Similarly, axonal Rtn-1KD significantly increases microtubule growth rate before and after injury according to the current statistical comparisons (Figure 5E). Second, if β3-tubulin decrease was a merely unspecific siRNA targeting, it is unlikely that SPTZ treatment should increase and restore β3-tubulin levels only in the context of axonal Rtn-1 KD (Figure 5B). We have now included these considerations in the discussion (lines 537-543). Although on a different track, the mechanistic relationship between Rtn-1C and Spastin suggested in Figure 7 could make more plausible that a similar phenomenon regarding the control of tubulin levels may occur locally in axons.

Following the reviewer's valuable suggestion, we performed additional quantifications in which puromycin was applied exclusively to the somatic compartment. Under these conditions, we still observed amplification in axons (~4 puncta per 1000 µm²), although this value was significantly lower than when puromycin was applied directly to axons (~10 puncta per 1000 µm²). This analysis provided a novel appreciation of the puro-PLA technique in neurons: at least half of the signal originates in the axonal compartment, while a portion may reflect proteins synthesized in soma and transported anterogradely to the axon through yet-unknown mechanisms (potentially involving rapid anterograde transport). Note that we revised the criteria for detecting true amplification spots based in staining without puromycin, which increased true amplification numbers. Still, these seemingly low values are compatible with reflecting a limited amount of time (only 15´ of puromycin pulse) and the stringent conditions of this experiment in which secondary antibodies were avoided by directly labeling primary ones. This approach makes the classical 30-40nm distance for PLA even narrower, thus reducing signal. In any case, assuming a neuronal soma diameter of 15 µm (area ≈ 176.71 µm²), this yields ~0.028 puncta per µm² in somata. In comparison, axons display ~0.01 puncta per µm², approximately one-third of the soma value, which makes sense for the expected difference in ribosome density.

• In Figure 5A the authors find an increased co-localization (RTN1/Spastin) after axotomy. From their images, it seems that the amount of Spastin is hugely increased, which would by default increase the chance of (random) colocalization of RTN1 on Spastin. Could the authors comment on this?*

__R: __Thanks for this relevant and constructive critique. We formerly based our colocalization analysis on deconvolved images. However, after performing several quantifications through different deconvolution parameters, we were not convinced about the robustness of this finding and the performed staining. Thus, we performed a new set of experiments and found that non-deconvolved images from the STED microscope were more informative about the expected tubular morphology of the axonal ER. Thus, we improved figure 5A, and now the main conclusion is just that both proteins are closely distributed in distal axons before and after injury.

• In figure 5E and 5F, the condition of scr + SPTZ is omitted. What is the reason for this? The explanation of results in these figures is confusing. The authors report a 'clear trend' in increase in comet track length and lifetime upon addition of SPTZ to axonal RTN-1 KD. This is however not significant. The comparisons that are made afterwards are confusing (e.g. increase in comet lifetime of SPTZ in non-injured axons with RTN1 KD compared to Scr+DMSO and KD + DMSO in injured axons). Their conclusion is axonal RTN-1 synthesis in injured axons (see my concern in the points above on this) governs microtubules growth rate beyond Spastin activity yet blocking Spastin activity still completely blocks the effect of KD on outgrowth.*

* *__R: __We thank this observation and fully agree that the general description provided in figure 5 E wasn't satisfactory. We have re-organized the descriptions of these results and performed more relevant statistical comparisons (lines 338-359). Based on the reviewer observation, we now conclude: "Together, these results suggest that axonal Rtn-1 synthesis controls microtubule dynamics in both non-injured and injured axons, mostly independently of Spastin-mediated microtubule severing." (lines 357-359).

Other/minor concerns:

- The gene ontology analysis in Figure 1A contains the category 'Endoplasmic reticulum'. In this category are mainly ribosomal proteins. Although in a gene ontology analysis these proteins will be included in this category, it is misleading in this respect since they are just as likely to be coming from cytoplasmic ribosomes. Although it cannot be excluded that these are ER-bound ribosomes, not in the last place because a recent study (Koppers et al., 2024, doi: 10.1016/j.devcel.2024.05.005) found ribosomes attached to the ER in axons, I believe the category should be adapted or at the least clarified in the text.

• *

__R: __Many thanks for the suggestion, which is now included in the text. "Note that several of the identified transcripts in the category 'endoplasmic reticulum' code for cytoplasmic ribosomal components, which indeed can be attached to the axonal ER (Koppers et al., 2024) and be locally synthesized in axons (Shigeoka et al., 2019)." (lines 125-128)

- Is RTN-1C isoform still an ER-shaping protein or rather an ER protein with alternative functions? The final sentence in the abstract makes a statement that a locally synthesized ER-shaping protein lessens microtubule dynamics. Could the authors provide a clearer description and discussion of the evidence in literature for this? RTN1C has been suggested to perform alternative functions in which case the statement that the local synthesis of an ER-shaping protein is important for axonal outgrowth should be adapted.

R: We agree with the reviewer and are aware that some non-canonical roles of Rtn-1C may partially explain the observed phenotypes. Thus, we have rephrased the last statement of the abstract: "These findings uncover a mechanism by which axonal protein synthesis provides fine control over the microtubule cytoskeleton in response to injury.". Also, we have modified the discussion section introducing new references accordingly..." Some studies have pointed to a non-canonical role for Rtn-1C in the nucleus, including DNA binding and histone deacetylase inhibition (Nepravishta et al., 2010, 2012). It is tempting to speculate that these still emerging roles may also contribute to the observed phenotypes. Of note, different axonally synthesized proteins exert transcriptional control in response to injury or local cues (Twiss et al., 2016)." (lines 576-580).

• Is there a difference in RTN1 distribution or levels pre- and post-axotomy?

R: Thanks for the suggestion, with the new analysis we have only found slight reorganization of Rtn-1C and Spastin in distal axons (Figure 5A). We have also included now quantification of their levels and found no significant differences for both proteins (Supplementary figure 4)

- Line 100/101 states 'the interactome of the axonal ER provides...'. To my knowledge there has been no study looking at the interactome of the axonal ER specifically. Surely axonal ER proteins are known but there is a difference.

• *

__R: __We agree with the reviewer that the phrase was misleading, so we rephrased it in the introduction "...Different lines of evidence support that the protein components of the axonal ER may interact with proteins that regulate microtubule dynamics"

* - Typo line 160 'localla'*

• *

__R: __Thanks for taking the time, we have now corrected it.

- In Figure S1 B, please add the DIVs to make it clearer what each graph corresponds to. The legend of S1B states different distances from the cell body but the graph shows distances from the tip.

• *

__R: __We have now corrected the legend accordingly.

- Figure 2C, why does B3 tubulin decrease in soma, aspecific effect of siRNA?

• *

__R: __This was indeed an unexpected finding. However, we do not observe unspecific or global changes in β3-tubulin levels (see Figure 2A and Supplementary Figure 2). Considering our other results linking Rtn-1 to the regulation of the microtubule cytoskeleton, we interpret this decrease as an indirect effect of Rtn-1 depletion rather than an off-target action of the siRNA. Moreover, if the effect were unspecific, both proteins would likely be reduced in the cell body, given that the siRNA was specifically designed to target Rtn-1 as its primary sequence-specific target.

- What is the rationale on the opposite effect found in outgrowth in Figure 3?

• *

__R: __The apparent opposite outcomes observed in Figure 3 - where axonal versus somatic Rtn-1 knockdown leads to divergent effects on axonal outgrowth - can be explained by compartment-specific environments and isoform distribution. The siRNA targets the conserved RHD region, reducing both Rtn-1A and Rtn-1C. Axons are enriched in Rtn-1C. Thus, axonal KD preferentially reduces Rtn-1C. In contrast, somatic KD reduces both isoforms. Rtn-1A, predominant in cell bodies, may probably engage other signaling pathways (Kaya et al., 2013). Interestingly, it was reported by Nozumi et al. (2009b) that global Rtn-1 depletion reduces axonal outgrowth in developing cortical neurons. This aligns with the notion that somatic KD mimics a more global loss of function, whereas axonal KD reveals a compartmentalized, pro-regenerative effect due to local Rtn-1C regulation. (All the references indicated here are in the main manuscript). These considerations are now included in the discussion ( lines 581-593).

* - Missing word 'we' on line 194*

• *

__R: __ We have corrected it.

- Typo line 629 'witmn h', please proofread the entire manuscript carefully.

• *

__R: __ We apologize for the spellings, now we have carefully revised the manuscript.

- Could the authors comment on why, in Figure 7B/C, GFP only is colocalizing with Spastin-RFP? In general, GFP should be diffusive and not display punctate colocalization with Spastin.

• *

We appreciate the reviewer's comment. Under normal conditions, GFP displays a diffuse cytoplasmic distribution. However, in our experimental setup, we observed punctate GFP signals only in the context of co-expression with Spastin-RFP. This is consistent with prior reports showing that soluble GFP can occasionally be sequestered into late endosomal structures (Sahu et al., 2011), which are also known to harbor the M87 Spastin isoform (Allison et al., 2013; Allison et al., 2019). To rigorously exclude the possibility of unspecific fluorescence crosstalk, we independently acquired each fluorophore channel and confirmed that GFP puncta were genuine and not due to bleed-through (Supplementary Figure 5). Further, cells expressing only GFP or only Spastin-RFP did not show overlapping puncta, and co-expression of GFP with Rtn-1A-RFP did not produce any apparent overlap, indicating that the punctate GFP pattern is specifically associated with Spastin co-expression. Thus, the observed GFP colocalization with Spastin reflects a biological phenomenon potentially linked to the endosomal localization of M87 Spastin, and not an artifact of imaging or fluorophore bleed-through.

Reviewer #2 (Significance (Required)):

* Axonal mRNA localization and localized translation support many neuronal functions and is an important determinant of the regenerative potential of axons after injury. How this works mechanistically remains unclear. The authors present a well performed and technically challenging study in which they identify RTN-1 as a regulator of axonal outgrowth after injury. They provide evidence using experiments in microfluidic chambers that RTN1 is locally synthesized in axons. Interestingly, they identify a (local) interplay between RTN1 and Spastin which affects microtubules and thereby regulates the outgrowth of cortical axons after injury. This study provides an interesting new link between a locally synthesized protein (RTN1) and a microtubule-regulating protein Spastin that is changed upon axon injury. This provides an advance in our understanding in axon regeneration after injury and provides the basis for new studies that can further investigate this interplay. Although interesting, I have several concerns that should be clarified and are needed to substantiate the findings and model presented in this study.*

*

The audience for this study will be mainly basic research in the fields of both axonal protein synthesis and axon regeneration. My expertise is in the field of mRNA localization and local protein synthesis.*

Batista, A. F. R., Martínez, J. C., & Hengst, U. (2017). Intra-axonal synthesis of SNAP25 is required for the formation of presynaptic terminals. Cell Reports, 20(13), 3085. https://doi.org/10.1016/J.CELREP.2017.08.097

Fan, X. xuan, Hao, Y. ying, Guo, S. wen, Zhao, X. ping, Xiang, Y., Feng, F. xue, Liang, G. ting, & Dong, Y. wei. (2018). Knockdown of RTN1-C attenuates traumatic neuronal injury through regulating intracellular Ca2+ homeostasis. Neurochemistry International, 121, 19-25. https://doi.org/10.1016/J.NEUINT.2018.10.018

Gracias, N. G., Shirkey-Son, N. J., & Hengst, U. (2014). Local translation of TC10 is required for membrane expansion during axon outgrowth. Nature Communications 2014 5:1, 5(1), 1-13. https://doi.org/10.1038/ncomms4506

Lucci, C., Mesquita-Ribeiro, R., Rathbone, A., & Dajas-Bailador, F. (2020). Spatiotemporal regulation of GSK3β levels by miRNA-26a controls axon development in cortical neurons. Development (Cambridge), 147(3). https://doi.org/10.1242/DEV.180232,

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

This manuscript investigates the relationship between the endoplasmic reticulum morphogen reticulon-1 (Rtn-1) and the microtubule severing protein spastin in axons after injury. The main message and conclusion of the paper is that local axonal synthesis of Rtn-1 plays a role in regulating the microtubule severing activity of spastin by interacting with spastin and inhibiting its activity. This mechanism would be important after injury by regulating axonal growth.

* The conclusions of the paper are based on the following claims:*

* 1) Rtn-1 is synthesized locally in axons.*

* 2) Specific downregulation in Rtn-1 in axons using microfluidic chambers affects microtubules abundance (measured by beta-3 tubulin) and promotes axon growth after injury.*

* 3) Inhibition of spastin MT-severing activity with a specific drug rescues the growth effect induced by axonal downregulation of Rtn-1.*

* 4) Rtn-1c interacts with spastin-M87 to limit its MT-severing activity in a cellular system upon overexpression.*

*

*

Major comments:

1) Evidence that Rtn-1 is synthesized in axons comes from two experiments. Initially, the authors show that Rtn-1 siRNA transfection in the axonal compartment of microfluidic chambers reduces Rtn-1 levels in axons, suggesting that there is some local synthesis. Although this method is very attractive, I am concerned about the statistical analysis. The graphs show bars rather than individual data points from the average of many neurons (about 300). The plots also show the SEM instead of the SD, thus covering all the variability that is inherent in this type of experiment. The statistics are probably not performed on the 3 biological replicates, but consider the individual neurons as N. This is obviously not correct, since neurons in an experiment may all be affected by the same technical problem and are not independent replicates. For this reason, I am a bit skeptical about this quantification. Another problem is that the quantification of the fluorescence intensity of the sample does not take the nuclei into account. Are the nuclei removed for analysis? Are the images single planes? Addressing the quantification issues is crucial also for data in Figure 4, where the authors show a different effect of Rtn-1 axonal KD after injury.

* The second experiment is the Puro-PLA in Figure 6D. This experiment shows an average of 1.5 dots of signal per soma, which is a very low level of translation for this compartment where most of the synthesis should be taking place. In the axons, it is not clear how they calculate the axonal area. Again, the number of dots detected is very low and the physiological significance is questionable. A control with a known mRNA translated in axons would be important.*

* Finally, as an important control, the authors should show the presence of Rtn-1 mRNA by FISH in their experimental system.*

__R: __We appreciate the critical points addressed here as they moved us to improve the quality of the findings. We analyzed cells/axons as statistical units to increase statistical power given the subtle nature of these local changes. We agree with the reviewer that this approach may increase the risk of finding false positives. To address this point, i) we plotted the individual data points and colored them according with the different experimental dates (all the dates showed a similar trend) ii) We indicated SD instead of SEM iii) We analyzed our data using linear mixed-effects models, with experimental date included as a random effect. This approach allows to preserve the granularity and statistical power, while avoiding pseudoreplication. To exclude artifactual changes, we now analyzed the intensity fold change of total fluorescence normalized to Scr. Our former quantifications were based on the corrected fluorescence intensity used to construct the plot profiles, which could be adding some distortion to the measurements. These changes were applied throughout figures 2 and 4 (pages 34 and 38, respectively). After these new analyses the formerly presented results remain valid.

We thank the reviewer for raising concerns about the quantification of fluorescence intensity in cell bodies. We now specify in Materials and methods that fluorescence intensity analysis of distal axons (always isolated by the microfluidic chambers) and of cell bodies was performed using the wide-field configuration of the microscope. In all the cases, a single (epifluorescent) plane was analyzed to reflect the total fluorescence of a cell or axon. We did not exclude the nuclear region from the quantifications, as this would also remove cytoplasmic signal located above or below the nucleus.

We also understand the concerns about puro-PLA experiments. We agree with the reviewer that an average of 1.5 puncta per soma initially appeared low. We have identified at least three reasons for this. First, the signal derives from only a 15-minute puromycin pulse, which is a short labeling window. Second, our puro-PLA assay is particularly stringent, as ligation relied directly on puromycin- and Rtn-1C-labeled primary antibodies, without the additional spacing normally introduced by secondary antibodies. In standard PLA, the critical distance for amplification is ~30-40 nm, whereas in our assay this distance is even more restrictive. Third, in our initial analysis we applied an overly cautious threshold to define "true" amplification. We have now refined this threshold using a baseline defined by the absence of puromycin stimulation. With this improved criterion, we now quantify an average of ~5 puncta per soma and ~10 puncta per 1000 µm² of axonal area (Supplementary Figure 3D). As it is now included in methods, we calculated the axonal area by binarizing β3-tubulin staining and only counted the true amplification spots inside this region. Assuming a neuronal soma diameter of 15 µm (area ≈ 176.71 µm²), this yields ~0.028 puncta per µm² in somata. In comparison, axons display ~0.01 puncta per µm², approximately one-third of the soma value which seems more reasonable. This is also compatible with most of Rtn-1C synthesis comes from the cell body.

Unfortunately, we could not be able to perform puro-PLA of other axonally synthesized proteins. Nevertheless, to further validate our puro-PLA signal, we tested the specificity of the Rtn-1C antibody we used for this assay by WB, IF, and Rtn-1 KD (Supplementary figure 3 A-C). In addition, we performed axonal Rtn-1 KD in microfluidic chambers for twenty-four hours, which elicited a significant decrease in puro PLA signal compared to Scr (Supplementary figure 3D). Together, these results strongly indicate that the quantified signal reflects Rtn-1C synthesis. To prove that Rtn-1 mRNA is present in these conditions, we now included a RT-PCR performed on RNA isolated from the somato-dendritic and pure axonal fractions of 8 DIV microfluidic chambers (Supplementary figure 3D). Note that the presence of this mRNA in axons has been supported by several studies, one of them using cortical neurons of similar DIV and cultured in microfluidic chambers (Table I and figure 1).

2) The effects on tubulin following Rtn-1 downregulation in axons is potentially very interesting, but the authors should be careful because it could also mean that the axons are suffering. Can they also stain for other cytoskeletal markers?

R: Regarding this concern, we are aware that in the former Figure 3 we mistakenly selected axonal fields that did not display healthy axons, which was not the dominant trend. This is accredited by the lack of fragmentation and by the functional responsiveness (microtubule dynamics) shown in Figures 4 and 5B, C, E. We have now replaced the previous axonal fields in Figure 3 with more representative axons (healthy), devoid of varicosities and fragmentation (page 37)

3) The results using SPTZ are very interesting and implicate spastin microtubule severing activity in the observed phenotype. In my opinion these experiments however do not prove that "axonal Rtn-1 is indeed promoting the severing of microtubules by spastin", but simply that the blocking spastin activity prevents the appearance of the microtubular phenotype (which appears still with a mysterious mechanism). What happens if they try to stabilize the cytoskeleton by another mean (with taxol for example?). The authors should rephrase this conclusion.

__R: __We completely agree with the reviewer's appreciation. We now explicitly indicate in the main text that this is (so far in the manuscript) a still correlative phenomenon that suggests an interplay with Spastin activity "..Together, these results suggest that locally synthesized Rtn-1 normally acts to suppress the outgrowth of injured axons, a process that could involve the microtubule-severing activity of Spastin." (lines 321-323). Later in the article, with the improved Figure 7, we further propose that these findings may reflect a causal relationship, although this mechanism has not yet been directly demonstrated in axons.

4) The last experiment (Figure 7) that aims to connect Rtn-1 and spastin function is very artificial, since it is based on overexpression. Why should spastin M87 interact with an ER morphogen? Endogenously it is conceivable that spastin M1 which localizes to the ER would interact with Rtn-1. Moreover, this experiment needs further controls and quantifications. First, it is quite obvious from panel 7C that there is crossover of signal in the two fluorescence channels (see GFP and spastin). Controls need to be shown, where only one of the two fluorescent proteins is expressed, and the specificity of the laser is tested. This experiment is based on only 1 cell shown where co-localisation is detected based on a line that is placed in a specific area of the cell. The effects on the microtubular network needs quantification.

__R: __We have now improved Figure 7 and added the requested controls to rule out crosstalk as indicated in Supplementary Figure 5 and in the main text. We agree that under normal conditions GFP should display a diffuse cytoplasmic distribution. However, in our experimental setup, we observed punctate GFP signals only in the context of co-expression with Spastin-RFP. This is consistent with prior reports showing that soluble GFP can occasionally be sequestered into late endosomal structures (Sahu et al., 2011), which are also known to harbor the M87 Spastin isoform (Allison et al., 2013; Allison et al., 2019). To exclude the possibility of unspecific fluorescence crosstalk, we independently acquired each fluorophore channel and confirmed that GFP puncta were genuine and not due to bleed-through (Supplementary Figure 5). Further, cells expressing only GFP or only Spastin-RFP did not show overlapping puncta (arrowheads), and the co-expression of GFP with Rtn-1A-RFP did not produce any apparent overlap, indicating that the punctate pattern of GFP is specifically associated with Spastin co-expression. Thus, we consider that the observed GFP colocalization with Spastin potentially reflects a true phenomenon and not an artifact of imaging or fluorophore bleed-through.

We thank for these observations and apologize for the confusion in the outline of the former figure 7 and the lack of a better description. As the reviewer indicates, one interesting aspect of the M87 isoform is that lacks the ER morphogen domain (so is soluble or cytoplasmic in principle). However, it also harbors endosome and microtubule binding domains which according to previous literature (now included in the main text) may render it a punctate rather than a homogeneous pattern. Also, M87 is the most abundant isoform in the nervous system, particularly at early development. This is the reason why we selected this isoform to test our model. To clarify this point, we based our colocalization analysis in different cells and experimental dates and analyzed all the z-stacks for each cell (see new figure 7B and methods), the intensity plots (now removed) were only for graphical purposes. Similarly, we had already quantified the total tubulin intensity in COS cells based on many cells from different dates and included the sum projections of all the z-stacks from these cells (see new figure 7C). Thus, we removed the intensity profiles as they were clearly misleading (see new figure 7).

We agree that over-expressing constructs may force interactions or co-distribution of proteins. However, in this case, if the observed results were mainly due to over-expression, we should see a similar trend with isoform A as both constructs are under the control of the same strong promoter (CMV) and harbor the same ER morphogen domain (RHD). Nevertheless, the distribution of M87 tightly mirrors Rtn-1C, which is not the case for Rtn-1A. Only as a theoretical prediction, our molecular modeling suggests that Rtn-1C may be associated with Spastin through its microtubule binding domain (Figure 7E). This would suppose that Spastin "decorates" ER-tubules rather than being in the same ER membranous structure. This discrete pattern of Spastin is more coherent with the distribution of both proteins that is now more clearly observed in distal axons by STED super-resolution (new figure 5A). So, despite a bit unexpected, these results suggest a novel interaction mechanism between these two proteins that deserves further validation.

5) What is exactly the model proposed? The title implies that axonal synthesis of Rtn-1 is important during injury, but the data in the paper rather suggest that upon injury the majority of Rtn-1 is not locally synthesized. If the levels of Rtn-1 do not change, why the effect on the microtubules should be specific? Why would a siRNA against Rtn-1 in axons not affect the levels of Rtn-1, but those of tubulin? The authors should be careful, and test other control siRNAs, and Rtn-1 siRNAs, since it is well known even in more simple cellular systems that the toxicity of individual siRNAs can vary greatly.

We consider the possibility that after injury there is no axonal Rtn-1 synthesis as a plausible and relevant appreciation. Unfortunately, we could not perform a puro-PLA experiment after injury, which would have provided a more definite answer. However, now we are more confident of regulating Rtn-1 synthesis before injury as supported by a Supplementary figure 3D that shows a significant decrease on puro-PLA signal (indicative of Rtn-1C synthesis) 24 hours after axonal KD. Thus, based on some similar phenotypes before and after injury, we consider our results are still compatible with Rtn-1 axonal synthesis being downregulated, but not fully absent (the mRNA is still detected, as described by Taylor 2009). As such, axonal Rtn-1 KD decreased β3-tubulin levels before and after injury according to figure 5B and the improved statistical analysis performed on figure 2E. Similarly, axonal Rtn-1KD significantly increases microtubule growth rate before and after injury according to the current statistical comparisons (Figure 5E). in complement, if β3-tubulin decrease was merely due to unspecific siRNA targeting, it is unlikely that SPTZ treatment should restore β3-tubulin only in the context of axonal Rtn-1 KD (Figure 5B). Although on a different track, the mechanistic relationship between Rtn-1C and Spastin suggested in Figure 7 could make more plausible that a similar phenomenon regarding the control of tubulin levels could be occurring locally in axons. We have now included these considerations in the discussion (lines 535-543).

To discard off-targets effects, we have now validated a third siRNA sequence (siRNA 3) specifically designed against Rtn-1 and showed that it selectively downregulates Rtn-1C but not β3-tubulin in cultured cortical neurons. Then, following the same experimental frame of figure 3, we performed axonal Rtn-1 KD after injury and observed that siRNA 3 also significantly increases the outgrowth of injured axons (Supplementary figure 2). This suggests that, at least this phenotype, is not product of an off-target effect. Thus, the pharmacological rescue of β3-tubulin levels by SPTZ (Figure 5B) and the Rtn-1C/Spastin co-distribution in heterologous cells, which correlates with preserved microtubules (improved Figure 7), provide converging evidence to suggest that Rtn-1C-Spastin interplay may underly the observed phenotypes in axons.

Minor comments:

In Figure 5A, it would be helpful to indicate the border of the axon. The figure is not really convincing.

Following yours and other reviewer comments, we have analyzed a new set of experiments regarding the STED images of non-injured and injured axons. To eliminate the risk of artifactual descriptions, we have avoided deconvolution and worked directly with raw STED images (Figure 5A). Under these conditions, distribution of Spastin and its intensity in distal axons are not modified by injury, nor those of Rtn-1C and Spastin (Supplementary figure 4). Despite these results, data still supports that both proteins are restricted to similar domains subcellular domains before and after injury.

Reviewer #3 (Significance (Required)):

The manuscript uses complex methods to address an interesting cell biological question of relevance to understand axonal growth regulation upon injury. A limitation of the study is the statistical analysis, which triggers some doubts about the reproducibility of the data. Further experiments and the addition of controls would be important to support the claims of the authors.

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Referee #3

Evidence, reproducibility and clarity

This manuscript investigates the relationship between the endoplasmic reticulum morphogen reticulon-1 (Rtn-1) and the microtubule severing protein spastin in axons after injury. The main message and conclusion of the paper is that local axonal synthesis of Rtn-1 plays a role in regulating the microtubule severing activity of spastin by interacting with spastin and inhibiting its activity. This mechanism would be important after injury by regulating axonal growth.

The conclusions of the paper are based on the following claims:

1. Rtn-1 is synthesized locally in axons.
2. Specific downregulation in Rtn-1 in axons using microfluidic chambers affects microtubules abundance (measured by beta-3 tubulin) and promotes axon growth after injury.
3. Inhibition of spastin MT-severing activity with a specific drug rescues the growth effect induced by axonal downregulation of Rtn-1.
4. Rtn-1c interacts with spastin-M87 to limit its MT-severing activity in a cellular system upon overexpression.

Major comments:

1. Evidence that Rtn-1 is synthesized in axons comes from two experiments. Initially, the authors show that Rtn-1 siRNA transfection in the axonal compartment of microfluidic chambers reduces Rtn-1 levels in axons, suggesting that there is some local synthesis. Although this method is very attractive, I am concerned about the statistical analysis. The graphs show bars rather than individual data points from the average of a large number of neurons (about 300). The plots also show the SEM instead of the SD, thus covering all the variability that is inherent in this type of experiment. The statistics are probably not performed on the 3 biological replicates, but consider the individual neurons as N. This is obviously not correct, since neurons in an experiment may all be affected by the same technical problem and are not independent replicates. For this reason, I am a bit skeptical about this quantification. Another problem is that the quantification of the fluorescence intensity of the sample does not take the nuclei into account. Are the nuclei removed for analysis? Are the images single planes? Addressing the quantification issues is crucial also for data in Figure 4, where the authors show a different effect of Rtn-1 axonal KD after injury. The second experiment is the Puro-PLA in Figure 6D. This experiment shows an average of 1.5 dots of signal per soma, which is a very low level of translation for this compartment where most of the synthesis should be taking place. In the axons, it is not clear how they calculate the axonal area. Again, the number of dots detected is very low and the physiological significance is questionable. A control with a known mRNA translated in axons would be important. Finally, as an important control, the authors should show the presence of Rtn-1 mRNA by FISH in their experimental system.
2. The effects on tubulin following Rtn-1 downregulation in axons is potentially very interesting, but the authors should be careful because it could also mean that the axons are suffering. Can they also stain for other cytoskeletal markers?
3. The results using SPTZ are very interesting and implicate spastin microtubule severing activity in the observed phenotype. In my opinion these experiments however do not prove that "axonal Rtn-1 is indeed promoting the severing of microtubules by spastin", but simply that the blocking spastin activity prevents the appearance of the microtubular phenotype (which appears still with a mysterious mechanism). What happens if they try to stabilize the cytoskeleton by another mean (with taxol for example?). The authors should rephrase this conclusion.
4. The last experiment (Figure 7) that aims to connect Rtn-1 and spastin function is very artificial, since it is based on overexpression. Why should spastin M87 interact with an ER morphogen? Endogenously it is conceivable that spastin M1 which localizes to the ER would interact with Rtn-1. Moreover, this experiment needs further controls and quantifications. First, it is quite obvious from panel 7C that there is crossover of signal in the two fluorescence channels (see GFP and spastin). Controls need to be shown, where only one of the two fluorescent proteins is expressed and the specificity of the laser is tested. This experiment is based on only 1 cell shown where co-localisation is detected based on a line that is placed in a specific area of the cell. The effects on the microtubular network needs quantification.
5. What is exactly the model proposed? The title implies that axonal synthesis of Rtn-1 is important during injury, but the data in the paper rather suggest that upon injury the majority of Rtn-1 is not locally synthesized. If the levels of Rtn-1 do not change, why the effect on the microtubules should be specific? Why would a siRNA against Rtn-1 in axons not affect the levels of Rtn-1, but those of tubulin? The authors should be careful, and test other control siRNAs, and Rtn-1 siRNAs, since it is well known even in more simple cellular systems that the toxicity of individual siRNAs can vary greatly.

Minor comments:

In Figure 5A, it would be helpful to indicate the border of the axon. The figure is not really convincing.

Significance

The manuscript uses complex methods to address an interesting cell biological question of relevance to understand axonal growth regulation upon injury. A limitation of the study is the statistical analysis, which triggers some doubts about the reproducibility of the data. Further experiments and the addition of controls would be important to support the claims of the authors.

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Referee #2

Evidence, reproducibility and clarity

Axonal mRNA localization and localized translation supports many neuronal functions and is an important determinant of the regenerative potential of axons after injury. How this works mechanistically remains unclear. The authors present a well performed and technically challenging study in which they identify RTN-1 as a regulator of axonal outgrowth after injury. They provide evidence using experiments in microfluidic chambers that RTN1 is locally synthesized in axons. Interestingly, they identify a (local) interplay between RTN1 and Spastin which affects microtubules and thereby regulates the outgrowth of cortical axons after injury. This study provides an interesting new link between a locally synthesized protein (RTN1) and a microtubule-regulating protein Spastin that is changed upon axon injury. This provides an advance in our understanding in axon regeneration after injury and provides the basis for new studies that can further investigate this interplay. Although interesting, I have several concerns that should be clarified and are needed to substantiate the findings and model presented in this study.

Major concerns:

1. In figure 1, the authors provide an analysis of overlapping axonal mRNAs. There are more axonal transcriptome studies and a recent study by von Kugelgen and Chekulaeva (2020; doi: 10.1002/wrna.1590) already performed such an analysis, which included more studies. It would be good to mention this. It can be perceived that studies were now chosen to get the outcome that Rtn-1 is present in all studies. For example, von Kugelgen finds mRNA coding for RTN3, another ER structural protein, as present in 16 out of 20 studies analyzed. That said, the authors present more reasons to look at Rtn-1, so the selection to continue with this protein remains valid but can be written up differently so not to present it as the 'sole' ER-shaping protein consistently present in axonal transcriptomes.
2. The description of methods is currently insufficient and incomplete and does not allow for reproducibility of this study. For example, different Rtn-1 antibodies seem to be used in this study. Is the same antibody used for staining and WB? There is no listing of any of the antibodies used in the study and which one is used for which technique/experiment. This should be clarified and should be easy to do so in the methods section (antibody name, origin/company, dilution used) to enhance reproducibility of this study. This is not limited to primary antibodies and any information on secondary antibodies, including what was used for STED is completely missing.
3. The timeline of KD experiments in Figure 2 and 3 are unclear. For the Western blot KD is performed at DIV7 and collected 48 hours later. However, this is not specified for the stainings done in Figure 2C-E. Is this also at DIV7 and then for 48 hours? In figure 3 the siRNA is added at DIV8 (together with axotomy) and outgrowth is measured 24 hours later. Is 24 hours sufficient to achieve knockdown? Is this also what was done for stainings? Later on in Figure 5B, 48 hours of KD is again used. It is unclear what the rationale of these differing timepoints is. Why was this chosen? Is the timeline also the reason for the difference in segment lengths chosen? In Figure 3, there is a significant effect on outgrowth in the KD in the 'mid-range' which is not present in Figure 5.
4. Could the authors provide a rescue condition for their siRNA (using a siRNA-resistant construct) to show that their siRNA is specific for RTN1. They nicely show the efficiency of the siRNA but not its specificity. This is crucial because if not specific, this will affect a large part of their study. They already have RTN1A and RTN1C constructs available. Such a rescue experiment should ideally also be performed for one or more of their phenotypic experiments, such as the one presented in Figure 3A or 5 to show that the phenotype is really RTN1 dependent. If done by re-expressing either RTN1A or RTN1C, this could provide insightful information on the relevant isoforms.
5. I find the data presented in Figure 4A/B confusing. Axonal RTN-1 KD does not reduce axonal RTN1 levels but somatic KD does. I understand that this implies most protein comes from the soma and the authors indeed present an explanation that increased somatic RTN1 occurs after axonal KD as a compensation mechanism. However, this can also be interpreted that there is no axonal synthesis of RTN1 after injury and axonal KD has indirect or even aspecific effects. Their model depends on this difference. Their data in Figure 6 could provide supporting evidence if it shows RTN1 puro-PLA after injury. Along these same lines, in Figure 6, they nicely include a compartment control for puro-PLA. It therefore seems doable to include a somatic puromycin control for their axonal puro-PLA, to exclude and diffusion/transport of the newly synthesized peptides. This is especially in light of two recent papers reporting on this possible phenomenon, although these studies were not performed in neurons.
6. In Figure 5A the authors find an increased co-localization (RTN1/Spastin) after axotomy. From their images, it seems that the amount of Spastin is hugely increased, which would by default increase the chance of (random) colocalization of RTN1 on Spastin. Could the authors comment on this?
7. In figure 5E and 5F, the condition of scr + SPTZ is omitted. What is the reason for this? The explanation of results in these figures is confusing. The authors report a 'clear trend' in increase in comet track length and lifetime upon addition of SPTZ to axonal RTN-1 KD. This is however not significant. The comparisons that are made afterwards are confusing (e.g. increase in comet lifetime of SPTZ in non-injured axons with RTN1 KD compared to Scr+DMSO and KD + DMSO in injured axons). Their conclusion is axonal RTN-1 synthesis in injured axons (see my concern in the points above on this) governs microtubules growth rate beyond Spastin activity yet blocking Spastin activity still completely blocks the effect of KD on outgrowth.

Other/minor concerns:

• The gene ontology analysis in Figure 1A contains the category 'Endoplasmic reticulum'. In this category are mainly ribosomal proteins. Although in a gene ontology analysis these proteins will be included in this category, it is misleading in this respect since they are just as likely to be coming from cytoplasmic ribosomes. Although it cannot be excluded that these are ER-bound ribosomes, not in the last place because a recent study (Koppers et al., 2024, doi: 10.1016/j.devcel.2024.05.005) found ribosomes attached to the ER in axons, I believe the category should be adapted or at the least clarified in the text.
• Is RTN-1C isoform still an ER-shaping protein or rather an ER protein with alternative functions? The final sentence in the abstract makes a statement that a locally synthesized ER-shaping protein lessens microtubule dynamics. Could the authors provide a clearer description and discussion of the evidence in literature for this? RTN1C has been suggested to perform alternative functions in which case the statement that the local synthesis of an ER-shaping protein is important for axonal outgrowth should be adapted.
• Is there a difference in RTN1 distribution or levels pre- and post-axotomy?
• Line 100/101 states 'the interactome of the axonal ER provides...'. To my knowledge there has been no study looking at the interactome of the axonal ER specifically. Surely axonal ER proteins are known but there is a difference.
• Typo line 160 'localla'
• In Figure S1 B, please add the DIVs to make it more clear what each graph corresponds to. The legend of S1B states different distances from the cell body but the graph shows distances from the tip.
• Figure 2C, why does B3 tubulin decrease in soma, aspecific effect of siRNA?
• What is the rationale on the opposite effect found in outgrowth in Figure 3?
• Missing word 'we' on line 194
• Typo line 629 'witmn h', please proofread the entire manuscript carefully.
• Could the authors comment on why, in Figure 7B/C, GFP only is colocalizing with Spastin-RFP? In general, GFP should be diffusive and not display punctate colocalization with Spastin.

Significance

Axonal mRNA localization and localized translation supports many neuronal functions and is an important determinant of the regenerative potential of axons after injury. How this works mechanistically remains unclear. The authors present a well performed and technically challenging study in which they identify RTN-1 as a regulator of axonal outgrowth after injury. They provide evidence using experiments in microfluidic chambers that RTN1 is locally synthesized in axons. Interestingly, they identify a (local) interplay between RTN1 and Spastin which affects microtubules and thereby regulates the outgrowth of cortical axons after injury. This study provides an interesting new link between a locally synthesized protein (RTN1) and a microtubule-regulating protein Spastin that is changed upon axon injury. This provides an advance in our understanding in axon regeneration after injury and provides the basis for new studies that can further investigate this interplay. Although interesting, I have several concerns that should be clarified and are needed to substantiate the findings and model presented in this study.

The audience for this study will be mainly basic research in the fields of both axonal protein synthesis and axon regeneration. My expertise is in the field of mRNA localization and local protein synthesis.

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Referee #1

Evidence, reproducibility and clarity

In this paper, the authors focus on the role of Reticulon-1C in concert with Spastin in response to axonal injury. In data mining, they find axonal mRNAs encoding for ER-associated proteins including Rtn-1. They establish a knockdown targeting both Rtn-1 isoforms Rtn-1A and Rtn-1C. They observe decreased beta-3-Tubulin levels in the soma while axonal protein levels are unchanged. In microfluidic devices, they characterise the effect of a compartment-specific Rtn-1 KD on axonal outgrowth in the axonal compartment. The authors quantify axonal outgrowth, seeing increased outgrowth in an axonal compartment-specific Rtn-1 KD, while the effect seems to be reversed when applying the KD construct in the somatic compartment. When focussing on the axonal growth cone, they find the Rtn-1 KD shows differences in several morphological features of the growth cone. They find an increase in Tubulin levels in an axonal compartment-specific, but a decrease in a somatic compartment-specific Rtn-1 KD. Colocalisation of Rtn-1C and Spastin is shown to be monolaterally increased following axotomy. Combining axotomy with the Rtn-1 KD shows increases in dynamic microtubule growth rates and track lengths. In another model system, neuron balls, they show Rtn1-C, but not Rtn1-A to be present in the axon. In a puro-PL assay they also show it can be synthesised in the axonal compartment. To investigate the mechanism enabling the cooperation between Spastin and Rtn-1C, they move to a cell line model in which they see a correlating distribution between Spastin and Rtn-1C but not Rtn-1A. Finally, they use in silico modelling to speculate on binding between Spastin domains and Rtn-1 isoforms.

Major comment:

The rationale behind the work is convincing, however some interpretations are presented as more robust than some data allow. Most notably, while the interaction between Rtn-1 and Spastin has been shown prior to this study, it is only presented here through in silico analysis. In figure 5, an increase in the growth rate of dynamic microtubules is observed in either a Rtn-1C KD or by using a Spastin-inhibitor. Due to a described increase in colocalisation between Rtn-1C and Spastin (5A), the increase in growth rate is displayed as caused by Rtn-1 promoting Spastin's severing ability. This result might however be correlative. Further in the injured samples, Spastin-levels seemingly increase (in the representative images) and it is thus not surprising that the level of Rtn-1C colocalising with Spastin increases as well. This might not be indicative of a cooperation and further experimental evidence are required.

Other comments:

• Generally, graphs would benefit from individual values plotted as well as the summary. Font sizes and types (but rarely) are sometimes inconsistent. Proteins should be consistently written (capitalised or not).
• Table 1 and figure 1 present data collected from a vast amount of resources. It should be highlighted that datasets from which data was obtained includes many different models, different DIVs and neuronal cell types. Figure 1B may benefit from a different colour scheme. "Ex-vivo" should be "Ex vivo". For "ER mRNAs are a relevant category" it is not described what "relevant" would mean in this context. The title might remove this small part or describe it in the text. It should be described how it is decided that mRNAs are "common".
• Figure 2: add description to y-axis to describe what fold change is displayed, applies to multiple figures. Will improve readability of the figures. In 2C, the ROI showing neuronal somata should be increased to show part of the axon and not cut off the soma.
• Figure 3: Three out of four axonal compartments seem to be comprised of dying or damaged axons. Especially the axonal KD scrambled image. It should be ensured that neuronal cultures are healthy. Typo in "intersections". The schematic of 3B is a great addition to explain the graphs above. Perhaps it could be a bit refined as it is currently hard to see whether this is a neuron or a growth cone without context. Maybe show where the axon connects to the depicted growth cones and change the third icon which looks like it was crossed out. Small formatting issues: remove additional space bar before "Figure 3." And add after "Bar"
• Figure 4: If not misunderstanding what is depicted, in 4A and B, different lookup tables are used to depict the same signal. Only one of each images is necessary. Do the axons have more tiny branches in the Rtn-1 KD condition in 4A? Unclear why Rtn-1 levels are increased in the Rtn-1 KD (4C), please clarify.
• Figure 5: It may be easier to understand what "axotomy" samples are if just referred to as "injured" as later in the same figure. The procedure could also very briefly be explained in the results. 5C should depict AUC in µm2 not µm. 5D Spastin is barely visible, brightness and contrast should be adjusted to enhance visibility.
• Figure 6: It should be made clear why it is necessary to switch to another model system just for 6A, please indicate this in the text. PCR bands seem very pixelated, check the quality. It is unclear why soma genes/proteins were only tested with either PCR or WB others with both. Rtn-1C and Rtn1-A should be presented in the same order in the PCR and WB panel. Correct "Rtn1-1A" typo. In 6D, 1.5 dots per soma seems like a low number. When normalised to the area the soma vs the axon occupies, the compartmentalisation does not work? May be it make sense to refine analysis or apply puromycin in the somatic compartment and analyse the axonal compartment as comparison?
• Figure 7: 7A shows two images depicting the same information that may not be needed. Can probably be removed. In 7B there is no negative (or any) correlation between Spastin levels and Tubulin, however later it is mentioned that Rtn-1C transports Spastin thus causing a decrease in Tubulin at certain locations? It is nclear if Spastin levels vary intensely between different samples. Mean intensity of the somatic area may be beneficial to rule this out. 7B Tubulin on the right top panel seems to have a decrease in Tubulin levels which is not visible due to the Y axis of Tubulin being set to a different range than the middle and lower panel. The average of line scans from multiple cells may be helpful to determine whether there is indeed no colocalization between Rtn-1A and Spastin. The provided representative images seem to show similar degrees of colocalization between Spastin and Rtn-1A/C.

Results:

• It would be helpful to reiterate the hypothesis at the start to ease the reading flow.
• There seems to be minor redundancy in lines 132-138.
• There are several spellings, proof-reading is recommended. For example, in line 136 should be "promotes". 160 "localla", 192 should be "the actin cytoskeleton".,194 should be "we first examined", 195 should be "Different", 223 "using", 259 "axons". ...
• 154-155: Unclear, why the lower MW Rtn-1C was seen as more important.
• 167 results of 2E not stated before interpreting them.
• 181 would suggest "outline" instead of "perimeter".
• 183-184 "longest shortest path" is a confusing term.
• figure 4B should be referenced earlier in the sentence.
• 243-244 may be correlation. Rtn-1 and Spastin do not necessarily interact so that this result is achieved.
• 246: In figure 1 the KD seemed to have an effect on both Rtn-1 isoforms, why not here anymore? 259 "axons". 284 "counteract" instead of "suppress"?
• 485: rephrase as the interaction between Rtn-1C with Spastin has not been shown directly in these experiments.

Methods: 535 "in PBS". 543 citation error. 689-699 is it necessary to add a gaussian blur?

References: Mannan, A U et al. appears twice in the citation list (36 and 44).

Significance

Overall, this manuscript describes novel fundings which will be interesting to the neuronal cell biology community and scientists working on the field of neuronal injury and regeneration. It is well structured, and the data are mostly well presented but sometimes conclusions are over-interpreted. However, several points need to be addressed in a more convincing way.

??

Three Main Points: 1. Our goal and Gods goal is so that we may become like him. This is why we have spiritual gifts and talents, all things that will allow us to gain and learn spiritual qualities that help us become more like Him. 2. The more we become like God, the more able we are to serve God and others. 3. By understanding our divinity and eternal potential, we will have more motivation and direction in how to achieve ours and Gods goal.

Reviewer #2 (Public review):

Chalamalasetty et al. investigate the regulatory circuit of signaling molecules and transcription factors that drive the fate of neuromesodermal competent progenitors (NMCs). NMCs contribute to Sox2-positive spinal cord and Tbxt/Bra-expressing somitic mesoderm, and this choice is governed by the interplay between Wnt3a and Fgf signaling. The authors discovered that the transcription factors SP5 and SP8 participate in this process. Mouse genetics, in vivo development, and transcription factors profiling point to a model where SP5 and SP8 directly regulate Wnt3a expression to foster Tbxt-marked mesoderm formation at the expense of Sox2-marked neural ectoderm. Mechanistically, SP5/8 bind to an enhancer which the authors characterize: its activity depends on the presence of SP5, CDX2, TCF7, and TBXT binding sites, and it is activated only in primitive streak cells at E7.5, in NMP, and in caudal and somitic mesoderm, underscoring the tissue and stage-specific nature of this Wnt3a enhancer.

Moreover, the authors find that SP5/8 likely regulate the TCF7 association with the chromatin and compete for its binding to the TLE repressor.

The study is extensive, compelling, and well written. The combination of in vivo evidence with single-cell transcriptomics, transcription factors profiling, and in vitro regulatory element characterization is notable and builds a convincing picture of the action of SP5/SP8.

Here, I provide a series of comments and questions that, if addressed and clarified, could, in my opinion, improve the study.

(1) While Sp5 and Sp8 are both present in NMCs, their expression does not fully overlap. Sp5 is also detected in caudal and presomitic mesoderm, notochord and gut, while Sp8 overlaps with Sox2 in neural progenitors of the spinal cord and brain (Fig. 1D). Accordingly, Sp8 expression is also activated by the neural-promoting RA+Fgf. It is not easy for me to reconcile this non-fully overlapping expression pattern - and in particular the overlap of Sp8 and Sox2 - with the presumed redundancy (or similarity of function) described later. Sp5/8 dko NMCs show reduced Tbxt and expanded Sox2, indicating that SP8 also represses Sox2 or neural fate, an observation confirmed by Sp8 overexpression (Figure 4c). What is the explanation for this, and is the function of SP8 in Sox2-positive neural progenitors different from its Wnt3a-sustaining role in NMCs? Or what am I missing?

(2) I suggest that the authors show relevant ChIP-seq peaks in Figure 3 to lend credibility to the complicated overlapping Venn diagrams. I consider visual inspection of peak tracks as primary quality control of this type of experiment. A good choice could be the cis-regulatory elements at Sp5, Sp8, Tbxt, Cdx1, 2, 4 bound by TBXT and either CDX2, SP5, or SP8 (now referring to the Venn diagrams and the annotated peak table). On ChIP-seq visualization, in reference to Figures 5 and 7, I also suggest that the authors show the tracks of a negative control (IgG, non-related antibody, or better anti-flag in Sp5/8 dko). While I do not doubt the validity of these experiments, there are peaks in these figures bound by all factors tested that could be suspicious (even though, admittedly, they look like genuinely good TF peaks). A negative track would clearly show beyond any doubt that these are not suspect regions of positive unspecific signal caused by open chromatin, excessive cross-linking, or antibody cross-reaction.

(3) SP5 here is found as a direct inducer of Wnt3a expression, and accordingly positive regulator of Tbxt and mesoderm, caudal development. I find this in partial contradiction with a finding by the Willert group (PMID: 29044119). They show that "genes with an associated SP5 peak, such as SP5 itself, AXIN2, AMOTL2, GPR37, GSC, MIXL1, NODAL, and T, show significant upregulation in expression upon Wnt3a treatment in SP5 mutant cells". There, essentially, SP5 inhibits Wnt target genes. While the authors are aware of this and cite Huggins et al., I find that this deserves a better discussion addressing how opposite functions could be sustained in different contexts, if these really are different cellular contexts in the first place, or if this could result from different methodologies.

(4) The gastruloid experiment is nice, but I wonder whether there is any marker that the authors can use to show that other features of the gastruloids respond accordingly. For example, is the Sox2 expression domain expanded? And is there any unaffected marker to emphasize the specificity of the decreased Tbxt and Cdx2?

(5) SP5/8 seems to enhance the TCF7 occupancy at WRE. And then, SP5/8 appears to counteract the presence of TLE repressor associated with TCF7. While these two mechanisms are interesting, they are not necessarily interconnected. According to the still-established view, TCF7 should be associated with WRE even in the absence of the Wnt signal, when TLEs are also present on the locus. One could expect that SP5 competes with TLE, to decrease its presence on TCF7-bound loci, leaving the abundance of TCF7 binding unchanged. Yet, the authors also observe that the TCF7 association changes. What is the mechanism implied? Do they perhaps consider a TCF7L1 > TCF7 switch, and if so, what evidence exists for this?

(6) Along the same line as above, I wonder whether beta-catenin binding is also enhanced at these sites? Any TCF/LEF would require beta-catenin for gene upregulation.

(7) The authors write that "Small Tle peaks were identified at these WREs in WT cells, demonstrating that both repressive Tle and activating Tcf7 could be detected at active genes". However, ChIP-seq is a population assay, and it is possible - more plausible, in fact - that cells displaying TLE binding are not expressing the target genes.

Reviewer #3 (Public review):

Summary:

This is a well-done study. It shows, in a comprehensive manner, that Sp5 and Sp8 play essential roles in maintaining the complicated positive feedback circuitry needed for specification of neuromesodermal competent progenitors (NMCs) in caudal mesodermal development in murine embryos.

Strengths:

The developmental genetics, transcriptomic, and genomic survey of TF binding are all satisfactory and make a compelling story. The CRISPR deletion of the Wnt3a downstream enhancer clearly demonstrates that it plays an important role in the positive feedback circuit.

Weaknesses:

My only concerns are some of the language surrounding the mechanistic interpretation of the Wnt3a downstream enhancer and the relationship between TCF and TLE binding.

However, SoA approaches do not work in many critical applications

Figure B-2 should be the heat figure, and this should be B-3. But maybe you did not have the latest version where the callout is?

So I know that some species of shark or other life can survive for hundreds of years. This may be a little off topic but how can they do this and would this not affect the curve of this drastically for the animals that do survive for possible centuries

torch.rand 会生成在 [0,1) 区间的随机浮点数。

x = torch.rand(1, 3, 224, 224) # 随机生成一张假图片

I read with interest the article by Bascur, Costas, and Verberne, which examines the use of diverse data sources to influence topic emergence in science maps.

At the outset, I note that I am affiliated with Digital Science, the owner and operator of both Altmetric and Dimensions—two of the data sources analysed in the study.

The article focuses on the mapping of articles onto science maps characterised by clusters of topical areas. These are typically visualised in two dimensions, where the relative positions of topics are determined by a selected distance metric. This area of study has seen considerable development in recent years, and science maps continue to serve as a compelling tool in various analytical and strategic contexts.

While the paper’s focus on mapping research outputs onto science maps is timely and relevant, I was disappointed to see that key foundational works in this field were not cited. In particular, I believe the following references are highly relevant, especially the last, which explores the use of Wikipedia in a manner closely related to the current paper:

• Börner, K., Chen, C., & Boyack, K. W. (2005). Visualizing knowledge domains. Annual Review of Information Science and Technology, 37(1), 179. https://doi.org/10.1002/aris.1440370106

• Boyack, K., Klavans, R., & Börner, K. (2005). Mapping the backbone of science. Scientometrics, 64, 351–374. https://doi.org/10.1007/s11192-005-0255-6

• Holloway, T., Bozicevic, M., & Börner, K. (2007). Analyzing and visualizing the semantic coverage of Wikipedia and its authors. Complexity, 12, 3–85. https://doi.org/10.1002/cplx.20164

The paper is framed as an exploration of how networks emerge, which is an important and intriguing subject. Visual representations play a crucial role in knowledge communication and decision-making, and I consider this work both significant and valuable.

That said, I initially interpreted the paper as an exploration of science map construction via bibliometric coupling informed by different data sources. However, the paper does not appear to explore alternative embedding metrics, topological variations, or the graphs that might result from different coupling strategies. Instead, it primarily assesses how faithfully papers can be mapped onto an existing topic structure using alternative data sources. I use the term "faithful" here in its group-theoretic sense—capturing both purity and effectiveness—as it conveys the intended meaning more precisely, in my opinion.

This focus differs somewhat from the broader ambitions implied in the title and abstract. I recommend the authors reassess whether the current framing accurately reflects the content, or alternatively, provide a more explicit explanation of the embedding method used and how it relates to the structural similarity being evaluated. Even if the scope is narrower than anticipated, the findings remain rigorous, well-articulated, and represent a valuable contribution.

If the paper is best understood as a study of the faithfulness of mapping unclassified papers to an existing clustering structure using different linking mechanisms (e.g., social data vs. textual or citation-based), then its key result appears to be that BERT-based methods offer a more faithful reproduction of the existing map than bibliometric approaches using the alternative data sources.

Given the clustering methodology behind the target map, this result is sensible. The use of social media data, as discussed in the paper, is more likely to yield alternative representations rather than a faithful reproduction. By contrast, BERT embeddings naturally align more closely with textual structures already reflected in the map. This outcome is consistent with the analytic approach adopted.

As an aside, the paper does not appear to reference the work of Evans and Lambiotte (https://doi.org/10.1103/PhysRevE.80.016105), which investigates the use of bipartite graphs and their duals for community detection. Their work is directly relevant to the paper’s discussion of faithfulness, particularly in terms of minimising overlap in cluster assignments.

Finally, I believe the paper would benefit from a stronger articulation of the contexts in which science mapping is applied. I have previously explored this in (https://doi.org/10.1162/qss_a_00244), and I believe the current work holds particular promise in evaluative settings. Preserving classification consistency over time is often vital for longitudinal comparisons, and the paper’s approach could be valuable in assessing alternative coupling strategies against a stable reference framework.

In summary, this paper presents a thoughtful and well-executed study. I find the technical development in the methodology around the refinement of purity to be helpful and something that those in the field will want to explore further. I recommend the authors consider refining the framing and expanding the contextualisation to strengthen the contribution and clarify its position within the existing literature.

The article “Use of diverse data sources to control which topics emerge in a science map” aims to analyze the effects of different data sources on topic clustering bias in science maps. For this purpose, the clustering effectiveness of different topic categories is analyzed based on different traditional and non-traditional data sources.

(1) contribution to existing literature

The present research is well embedded in the existing body of literature and builds on the study “Which topics are best represented by science maps? An analysis of clustering effectiveness for citation and text similarity networks” by Bascur, Verberne, van Eck, and Waltman (2024). That study explored the extent to which science maps can successfully cluster documents that address the same topic - a concept referred to as clustering effectiveness. This metric serves as an indicator of the thematic precision of clustering approaches. Bascur et al. (2024) found that clustering effectiveness varies depending on the topic domain: documents related to certain topics, such as diseases, were more accurately clustered than those related to others, such as geography. Building on these findings, the present study investigates whether the clustering effectiveness for documents on the same topic is influenced by the choice of data source, and whether this effectiveness can be systematically adjusted or optimized through the selection of that source.

(2) major strengths and weaknesses

The article’s ideas and arguments are presented with clarity and precision. Its structure follows a classic and well-established format - introduction, background, methods, results, discussion, and conclusion - which makes it easy to follow. As a reader, I never lost the thread; the narrative remains coherent and accessible throughout. The current state of research is conveyed in a thorough, well-reasoned, and nuanced manner. Particularly noteworthy is the detailed introduction to the topics of science maps based on diverse sources and comparing clustering solutions of different networks. This contextualization is both comprehensive and essential for understanding the research that follows.

The document selection is highly extensive (4,142,511 documents) and well-justified. The rationale for which documents are included in the study is clearly and convincingly presented. All selection criteria are explained in detail in Section 3.1.

The introduction clearly explains the rationale for using non-traditional data sources alongside traditional data sources, and the justification is both logical and easy to follow. The external data sources are introduced and described in Section 3.2. The procedures for building the different networks (Sections 3.3 and 3.4), as well as the clustering approaches (Section 3.5), are also thoroughly explained. The topics and topic categories analyzed in the study are presented and justified in detail in Section 3.6. To evaluate how well different topics are represented within the clustering networks, the study employs the concept of clustering effectiveness. The relevant calculations are described in Section 3.7.

The article presents its complex results in a well-structured and sensible tabular format. Figure 2 provides an example to illustrate how the results are displayed. Table 3 reports all detailed results, while Table 4 offers a summary, and Table 5 draws conclusions on which network performed best for each topic. The tables and their captions are extensive and may seem overwhelming at first glance. However, the article makes it clear that this level of detail is both intentional and necessary. The thorough descriptions guide the reader through the results and enhance comprehension. Rather than being a weakness, the comprehensive presentation reflects the authors’ careful and rigorous approach.

Regarding additional strengths of the article, I would like to highlight and support those identified by the authors themselves. This study represents a clear advancement over the 2024 publication. By focusing on a single metric—purity, rather than also including inverse cluster number—the evaluation and interpretation of results have been significantly simplified, and comparability has improved. Whereas the earlier study only allowed comparisons between cluster solutions based on identical document sets and similar cluster sizes, the current study enables comparisons across different networks, even when they involve varying documents and cluster structures. A notable innovation in this article is the introduction of purity profiles, which effectively illustrate how clearly topic clusters would be perceived by users navigating the science map.

In addition to highlighting the strengths of their work, the authors also acknowledge three key limitations. These include the absence of a specified minimum cluster size, the combination of bipartite and non-bipartite networks, and the potential inaccessibility of certain data sources for other researchers (e.g., due to paywalls such as those associated with the Twitter API). Each of these limitations is clearly presented and discussed in the article. The authors provide thoughtful reasoning on the impact of these constraints and explain how they have addressed them within the scope of their study.

(3)    suggestions for improvements

I have no suggestions for improving the article.

(4)    data and code availability/ research ethics/ MetaROR policies

The research data is available on Zenodo in accordance with the principle as open as possible, as closed as necessary. Due to legal restrictions, the raw data used in the experiments cannot be shared. However, the code used to conduct the experiments and generate the results is provided, along with a summary of the data utilized.<br /> This ensures transparency and allows others to understand the methodology and replicate the results, even in the absence of the original raw data.

In this article, the authors present a study using different networks from various data sources to measure differences in gathering scholarly document topics and to show which networks provide the best information to represent the scientific topics considered appropriately. The work is built on a previous contribution and analyses networks obtained from six sources: scholarly document authors, Facebook users, Twitter users and conversations, patents, and policy documents. These networks are also accompanied by other networks, i.e. the text similarity network and the citation network, that are mainly used for comparison purposes.

The work particularly interests the scholarly community, aiming to work with science map generation. However, some passages need further explanation to be clear to the reader.

1. In the abstract, there is a mention of traditional and non-traditional data sources. While in the text of the article there are, indeed, some clarifications, it would be ideal to briefly explain in the abstract what the authors refer to these terms, since it is not immediately clear what is a traditional data source in the context of topic identification.

2. In the introduction, the authors anticipate the outcomes of a previous work they have conducted on a similar topic. They claim that some topics are well-represented in maps based on citation links and text similarity, while others are not. However, it is not clear which sources they have used to get to this claim, and it is also not evident what the main difference is that characterises the current work compared to the previous one.

3. In section 3, the authors introduce all the methods and materials used for their analysis. Despite the fact that some of the material cannot be shared since it is behind a paywall (e.g. the Web of Science data), by reading the section, it is not clear that all the code developed and the data obtained from the analysis have been published on Zenodo. While it is okay to address this aspect in the appropriate section at the end of the article, I would suggest to anticipate this information at the beginning of section 3, citing the Zenodo record appropriately and clarifying which of material is not included in that record, thus explaining that the full reproducibility of the experiment cannot be conducted.

4. Considering all the external sources of networks, it is not clear what the datetime window of each source is - are all these sources containing information from the year of publication of the oldest article in the document set considered to 2024?

5. As far as I understood from the formula in section 3.7.1, the Purity is always calculated against a particular topic M. Thus, why not refer to such "M" in the formula definition, defining it in a function-like way Purity(N, M)? In addition, still in this section, it is not clear how the N clusters considered are selected. A running example of Purity calculation would probably help the reader here.

6. In section 3.7.2, the denominator of the formula is set to 5. However, it is unclear why such a number is sensitive for the calculation presented. Why not 6 or 7? Why not 3? I think the authors should clearly justify the choice of such a denominator by bringing in explicit evidence.

7. In section 3.7.3, it is not entirely clear what the difference is between topics and topic categories.

8. In the discussions, it would be good to extend a bit on the work's limitation and envision possible paths for future works in the area. A few points that I would love to see discussed in detail:

   • The analysis has been done by using sources that may have changed drastically in the past months/years - e.g. Twitter that, after becoming X, has seen a series of abandons from the academics towards more open (in a broad sense) platforms and networks (e.g. Mastodon and, more recently, BlueSky). Would it be possible to gather the necessary data from these platforms to run the study again? If yes, would it be possible to download them? If not, should we consider these sources unreliable for scientific purposes and, if so, what preconditions should be in place for their reliability? Considering the present situation, what is the relevance of the results obtained with the data gathered from Twitter (now X)?

   • The authors transparently claim that some of the data used (e.g. Web of Science data) are not freely available to the reader, thus preventing the full replication of the study. Is it possible to substitute these closed sources with others offering open research information? For instance, OpenCitations for gathering the citation network (full disclosure: I'm director of OpenCitations), PubMed and PubMed Central for gathering titles and abstracts of the article considered, etc.?

   • The core set of scholarly documents considered are primarily from the biomedical domain since the authors considered only those with a PubMed identifier specified. While the results shown are sensitive for this domain, how much does the approach the authors presented scale also in other scholarly areas, e.g. Social Science and Humanities? Is it possible to speculate that the approach presented is discipline-agnostic? Is there any evidence for such a claim?

Some final remarks:

A. The figures should be closer (i.e. maximum on the next page) to the place they are mentioned the very first time.

B. The research question introduced in the article is introduced in section 1, and then it is not explicitly mentioned anymore in the text. It would be ideal to add an explicit reference to that question when the authors present appropriate evidence to answer it (e.g. in section 4) and to recall the answer to that question in the conclusion of the paper.

Note: This response was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

This manuscript described the translational responses to single and combined BCAA shortages in mouse cell lines. Using Ribo-seq and RNA-seq analysis, the authors found selective ribosome pausing at codons that encode the depleted amino acids, where the pausing at valine codons was prominent at both a single and triple starvations whereas isoleucine codons showed pausing only under a single depletion. They analyzed the mechanisms of the unexpected selective pausing and proposed that the positional codon usage bias could shape the ribosome stalling and tRNA charging patterns across different amino acids. They also examined the stress responses and the changes in the protein expression levels under BCAA starvation.

The manuscript was well-written, and the findings are interesting, especially their model that positional codon usage bias could be a regulator of ribosome pausing and tRNA charging levels. Although different translational responses to distinct amino acid starvation have been widely documented, the positional codon usage bias is an interesting aspect. The manuscript's central message could have been made clearer. The authors may consider emphasizing this point more explicitly in the abstract. The rich multi-omics dataset in this work provides valuable resources for the translation field.

We thank the reviewer for the thoughtful and positive evaluation of our work.

Major comments

1. The abstract may need to be revised since it is hard to immediately catch the authors' main point. If the authors regard this work as a resource paper, the current version is fine. But it could be better to point out the positional codon usages the authors found, which is a strong point of the current manuscript.

Response: We thank the reviewer for highlighting the importance of positional codon usage, which indeed represents a key finding of our study. We revised the abstract, and we now emphasize this aspect more clearly. However, in response to review #2, we have framed the observed positional effects and the idea of an elongation bottleneck as one possible contributing mechanism among others and relate it specifically to the attenuation of isoleucine-specific stalling under triple starvation.

1. Page 18 "Beyond these tRNA dynamics, our data also highlight the importance of the codon positional context within mRNAs, indicating that where a codon is located within the CDS can influence both the extent of ribosomal stalling and overall translation efficiency during nutrient stress." This idea is interesting. To what extent the authors think this could be generalized? The authors may discuss whether they think their proposed model is specific to the different ribosome stalling patterns between valine and isoleucine codons or generalized to other codon combinations. For example, the positional codon usage bias will be different among different organisms, and are there any previous reports on ribosome behaviors that align with their model?

Response: We thank the reviewer for raising these important points. While our study primarily focuses on the differential stalling patterns of valine and isoleucine codons, we believe the underlying principle, that the position of codons within the CDS can modulate the extent of ribosome stalling, may under very specific circumstances extend beyond this amino acid pair. We expect this positional effect to be potentially relevant for combinations in which one amino acid has considerable enrichment near the 5′ end of coding sequences, coupled with starvation-sensitive tRNA isoacceptors, while the other does not. In our case, valine meets these criteria (see Fig. S11A and Fig. 6). In contrast, isoleucine and leucine codons, although also relatively frequent, show more variable positional distributions and are both decoded by isoacceptors that appear more resistant to starvation, as illustrated in Fig. 6 and reported for mammals and bacteria in Saikia et al. 2016; Darnell, Subramaniam, and O’Shea 2018; Elf et al. 2003; Dittmar et al. 2005. To explore the generalizability of this model, we have now included a transcriptome-wide analysis of codon position biases in mouse for all codons in the revised manuscript (Supplementary Figures 10 and 11). This analysis may serve as a basis to identify additional candidate codons for future studies. Furthermore, we now mention in the Discussion that amino acids with similar properties to valine regarding their positional distribution and tRNA isoacceptors, such as phenylalanine, and glutamine, whose tRNA isoacceptors are predicted to be fully deacylated under their respective starvation in bacteria (Elf et al. 2003), could be promising candidates for testing this model, in combination with amino acids, whose tRNAs are expected to remain partially charged under starvation or to be depleted at the start of the CDS such as i.e. His (Supplementary Fig.11C).

Even if the authors think this model can be applied to BCAA starvation, would it be possible to explain the different isoleucine codon responses between single and double starvation? The authors may discuss why the ribosome stalling at isoleucine AUU and AUC codons was slightly attenuated under double starvation. And how about the different leucine codon responses among single, double, and triple starvations, although the pausing is not as strong as isoleucine and valine codons?

Response: Regarding the attenuated isoleucine stalling under double starvation, we believe this is primarily due to stronger inhibition of the mTORC1 pathway when leucine is co-depleted (i.e., in the double starvation condition; Fig. 2D–F). This results in a more substantial suppression of global translation, reducing overall tRNA demand and thereby mitigating stalling (Darnell, 2018). A similar effect may explain the only mild leucine codon stalling observed under single leucine starvation, which also triggers strong mTORC1 inhibition and reduced initiation. In contrast, triple starvation does not suppress mTORC1 to the same extent, and thus reduced initiation alone cannot explain the absence of leucine codon stalling. Instead, we propose that additional features, such as the relative sensitivity of tRNA isoacceptors to starvation and their aminoacylation dynamics, must be considered. Valine tRNAs, for example, are known to be highly sensitive and become strongly deacylated under starvation in bacteria (Elf et al. 2003), a pattern that we also find in our own data (Fig. 6). Leucine tRNAs, by contrast, appear more resistant, possibly due to better amino acid recycling or isoacceptor-specific differences in charging kinetics, though further validation would be needed. However, combined with the strong stalling at 5′-enriched valine codons, this could reduce downstream ribosome traffic and limit exposure of leucine codons, thus preventing stalling. However, our new analysis of the positional relationship between valine and leucine codons within individual transcripts (now shown in Supplementary Figure 11B) did not reveal as strong a pattern as we observed for valine and isoleucine codons. We now discuss these points and their implications in the revised Discussion.

Experimental validation using artificial reporters carrying biased sequences may also be considered.

Response: We appreciate the reviewer’s suggestion. In fact, we explored this experimentally using a dual-fluorescent reporter system (GFP–RFP) (Juszkiewicz and Hegde 2017) containing consecutive Val or Ile codons. However, the constructs yielded variable and non-reproducible results under starvation conditions. In addition, testing the role of codon position would require placing the same codons at multiple defined positions within a single transcript and performing ribosome profiling directly on the reporter. This type of targeted experimental validation is technically challenging and falls beyond the scope of the current study. We now mention this explicitly in the revised Discussion as an interesting direction for future work.

1. Page 13 "Moreover, we noticed that DT changes extend beyond the ribosomal A-site, including the P-site, E-site, and even further positions (Supplementary Fig. 2A), consistent with other studies on single amino acid starvation 39 (Supplementary Fig. 2B-C)." Could the widespread DT changes be due to Ribo-DT pipeline they used or difficulties in offset determination? Indeed the authors showed that this feature was found in other datasets, but it seems that the datasets were processed and analyzed in the same way as their data. The original Ribo-DT paper (Gobet and Naef, 2022, Methods) also showed some widespread DT changes even from RNA-seq. Another analysis method like the codon subsequence abundant shift as a part of diricore analysis (Loayza-Puch et al., 2016, Nature) did not show that broad changed regions. The authors are encouraged to re-analyze the data sets using different methods.

Response: We agree with the reviewer that the fact that DT changes beyond the ribosomal A-site is puzzling, but this has already been seen in other papers using other approaches (Darnell, Subramaniam, and O’Shea 2018). To validate that this shift is not due to our A-site assignment, enrichment analysis, or DT method, we applied the Diricore pipeline to our Ribo-Seq data. The output of the pipeline provides either 5’-end ribosome density or “subsequence” analysis using an A-site offset for each read size based on the metagene profile at the start codon. Both analyses show the same enriched codons across the different conditions as in our analyses, and the broad shift is similar, with the maximum signal at E, -1 position (Fig. R1).

1. Page 13 "Intriguingly, only two of the three isoleucine codons (AUU and AUC) showed increased DTs upon Ile starvation (p < 0.01), while just one leucine codon (CUU) exhibited a modest but significant DT increase (p < 0.01) under Leu starvation (Figure 1A-B, Supplementary Figure 2A)." How can the authors explain the different strengths of ribosome pausing at Ile codons under Ile and double starvation? The AUA codon did not show any pausing under either of the starvation conditions. Throughout the manuscript, the authors mainly describe the difference between amino acids but it is desirable to discuss the codon-level difference as well.

Response: Thank you for raising this point. The observed differences in stalling between the isoleucine codons can likely be explained by differences in tRNA isoacceptor charging and positional bias within transcripts. The AUA codon is decoded by a distinct tRNAIle isoacceptor (tRNAIleUAU), which, according to our tRNA charging data (Fig. 6), remains largely charged during Ile starvation. This observation aligns with previous reports suggesting that this isoacceptor is more resistant to starvation-induced deacylation in mammalian cells and bacteria (Saikia et al. 2016; Elf et al. 2003). In contrast, the AUU and AUC codons are primarily decoded by the tRNAIleAAU isoacceptor, which we find to be strongly deacylated under Ile starvation, likely contributing to the observed codon-specific ribosome pausing. Additionally, we found that the AUA codons are relatively rare in general and particularly underrepresented near the 5′ ends of coding sequences. Our new spatial analysis (now included in Supplementary Figure 11B) confirms that AUA codons tend to occur downstream of AUU and AUC codons within transcripts. This potentially further reduces stalling on these codons and further diminishes their apparent DT increase under starvation. In order to better explain these important points, we have now expanded the codon-level discussion of these differences in the revised manuscript.

1. Page 13 "We examined the effects of single amino acid starvations (-Leu, -Ile and -Val), as well as combinations, including a double starvation of leucine and isoleucine (hereafter referred to as "double") and a starvation of leucine, isoleucine, and valine ("triple"), allowing us to identify potential non-additive effects." The different double starvations, isoleucine and valine, and leucine and valine, will further support their hypothesis on the effects of the positional codon usage bias on ribosome pausing and tRNA charging patterns. Although this could be beyond the scope of the current manuscript, the authors are encouraged to provide a rationale for the chosen combination.

Response: Our experimental design evolved stepwise: we initially focused on leucine and isoleucine depletion as we found that despite their structure similarity these had respectively short and long dwell times in our previous work in the mouse liver (Gobet et al. 2020). Valine was included at a later stage to cover all the BCAAs. At the time, we did not anticipate valine to yield particularly striking effects in cells, and therefore we did not include systematic pairwise depletions involving valine. However, the strong and unexpected stalling observed at valine codons, especially under triple starvation, became a central aspect of the study. Thus, we agree that additional combinations, such as Leu/Val or Val/Ile, could be informative and now mention this in the Discussion as a potential direction for future studies.

Minor comments

Page 16 "these results imply that BCAA deprivation lowers protein output through multiple pathways: a combination of reduced initiation, direct elongation blocks (stalling), and possibly an increased proteolysis" This conclusion is totally right but may be too general. Could the authors summarize BCAA-specific features of the events including reduced initiation, stalling, and proteolysis that all contribute to protein outputs? This is not well discussed in the latter sections including Discussion.

Response: We thank the reviewer for this helpful suggestion. We agree that the original statement was too general and have revised the relevant section to more clearly delineate the distinct responses observed under each BCAA starvation condition. Specifically, we now summarize that valine starvation is characterized by strong, positionally biased ribosome stalling; leucine starvation primarily impacts translation initiation, likely via mTORC1 repression; and isoleucine starvation shows a mixed phenotype, with features of both impaired initiation and codon-specific elongation delays. We also clarify that while protein stability or degradation may contribute to the observed changes in protein output, our current data do not allow for quantitative assessment of proteolytic effects (e.g., changes in protein half-life). Therefore, we refrain from making direct quantitative conclusions about the differential modulations of proteolysis and instead focus our discussion on the translational mechanisms supported by our data.

Reviewer #1 (Significance):

The manuscript was well-written, and the findings are interesting, especially their model that positional codon usage bias could be a regulator of ribosome pausing and tRNA charging levels. Although different translational responses to distinct amino acid starvation have been widely documented, the positional codon usage bias is an interesting aspect. The manuscript's central message could have been made clearer. The authors may consider emphasizing this point more explicitly in the abstract. The rich multi-omics dataset in this work provides valuable resources for the translation field.

We thank the reviewer for the encouraging comments and share the view that positional codon-usage bias is an important result; accordingly, we now underscore this point explicitly in the revised Abstract. We also emphasise that our other observations are, to our knowledge, novel: only a handful of multi-omics studies have combined ribosome-pausing profiles with direct tRNA-aminoacylation measurements, and none has systematically examined multiple amino-acid-deprivation conditions as presented here.

Reviewer #2 (Evidence, reproducibility and clarity):

This study examines the consequences of starvation for the BRCAAs, either singly, for Leu & Ile, or for all three simultaneously in HeLa cells on overall translation rates, decoding rates at each codon, and on ribosome density, protein expression, and distribution of ribosome stalling events across the CDS for each expressed gene. The single amino acid starvation regimes specifically reduce the cognate intracellular amino acid pool and lead to deacylation of at least a subset of the cognate tRNAs in a manner dependent on continuing protein synthesis. They also induce the ISR equally and decrease bulk protein synthesis equally in a manner that appears to occur largely at the initiation level for -Leu and -Val, judging by the decreased polysome:monsome ratio, but at both the initiation and elongation levels for -Ile-a distinction that remains unexplained. Only -Leu appears to down-regulate mTORC1 and TOP mRNA translation.There is a significant down-regulation of protein levels for 50-200 genes, which tend to be unstable in nutrient-replete cells, only a fraction of which are associated with reduced ribosome occupancies (RPFs measured by Ribo-Seq) on the corresponding mRNAs in the manner expected for reduced initiation, suggesting that delayed elongation is responsible for reduced protein levels for the remaining fraction of genes. All three single starvations lead to increased decoding times for a subset of the cognate "hungry" codons: CUU for -Leu, AUU and AUC for -Ile, and all of the Val codons, in a manner that is said to correspond largely to the particular tRNA isoacceptors that become deacylated, although this correspondence was not explained explicitly and might not be as simple as claimed. All three single starvations also evoke skewing of RPFs towards the 5' ends of many CDSs in a manner correlated with an enrichment within the early regions of the CDSs for one or more of the cognate codons that showed increased decoding times for -Ile (AUC codon) and -Val (GUU, GUC, and GUG), but not for -Leu-of which the latter was not accounted for. These last findings suggest that, at least for -Val and -Ile, delays in decoding N-terminal cognate codons cause elongating ribosomes to build-up early in the CDS. They go on to employ a peak calling algorithm to identify stalling sites in an unbiased way within the CDS, which are greatest in number for -Val, and find that Val codons are enriched in the A-sites (slightly) and adjacent 5' nucleotides (to a greater extent) for -Val starvation; and similarly for Ile codons in -Ile conditions, but not for -Leu starvation-again for unknown reasons. It's unclear why their called stalling sites have various other non-hungry codons present in the A sites with the cognate hungry codons being enriched further upstream, given that stalling should occur with the "hungry" cognate codon in the A site. The proteins showing down-regulation are enriched for stalling sites only in the case of the -Val starvation in the manner expected if stalling is contributing to reduced translation of the corresponding mRNA. It's unclear why this enrichment apparently does not extend to -Ile starvation which shows comparable skewing of RPFs towards the 5'ends, and this fact diminishes the claim that pausing generally contributes to reduced translation for genes with abundant hungry codons. All of the same analyses were carried out for the Double -Ile/-Leu and Triple starvations and yield unexpected results, particularly for the triple starvation wherein decoding times are increased only at Val codons, skewing of RPFs towards the 5' ends of CDSs is correlated only with an enrichment for Val codons within the early regions of the CDSs, and stall sites are enriched only for Val codons at nearly upstream sites, all consistent with the finding that only Val tRNAs become deacylated in the Triple regime. To explain why only Val tRNA charging is reduced despite the observed effective starvation for all three amino acids, they note first that stalling at Val codons is skewed towards the 5'ends of CDS for both -Val and triple starvations more so than observed for Ile or -Leu starvation, which they attribute to a greater frequency of Val codons vs Ile codons in the 5' ends of CDSs. As such, charged Val tRNAs are said to be consumed in translating the 5'ends of CDSs and the resulting stalling prevents ribosomes from reaching downstream Ile and Leu codons at the same frequencies and thus prevents deacylation of the cognate Ile and Leu tRNAs. It's unclear whether this explanation is adequate to explain the complete lack of Ile or Leu tRNA deacylation observed even when amino acid recycling by the proteasome is inhibited-a treatment shown to exacerbate deacylation of cognate tRNAs in the single amino acid starvations and of Val tRNA in the triple starvation. As such, the statement in the Abstract "Notably, we could show that isoleucine starvation-specific stalling largely diminished under triple starvation, likely due to early elongation bottlenecks at valine codons" might be too strong and the word "possibly" would be preferred over "likely". It's also unclear why the proteins that are down-regulated in the triple starvation are not significantly enriched for stalling sites (Fig. 5B) given that the degree of skewing is comparable or greater than for -Val. This last point seems to undermine their conclusion in the Abstract that "that many proteins downregulated under BCAA deprivation harbor stalling sites, suggesting that compromised elongation contributes to decreased protein output." In the case of the double -Ile/-Leu starvation, a related phenomenon occurs wherein decoding rates are decreased for only the AUU Ile codon and only the AAU Ile tRNA becomes deacylated; although in this case increased RPFs in the 5' ends are not correlated with enrichment for Ile or Leu codons and, although not presented, apparently stall sites are not associated with the Ile codon in the double starvation. In addition, stalling sites are not enriched in the proteins down-regulated by the double starvation. Moreover, because Ile codons are not enriched in the 5'ends of CDS, it doesn't seem possible to explain the selective deacylation of the single Ile tRNA observed in the double starvation by the same "bottleneck" mechanism proposed to explain selective deacylation of only Val tRNAs during the triple starvation. This is another reason for questioning their "bottleneck" mechanism.

We thank the reviewer for their deep assessment, exhaustive reading, and constructive feedback, which have greatly contributed to improving the clarity and contextualization of our manuscript. We would first like to clarify that all experiments in this study were conducted in NIH3T3 mouse fibroblasts, not HeLa cells; we assume this was a misunderstanding and have verified that the correct cell line is consistently indicated throughout the manuscript. We also clarify that our data show that -Leu, double starvation, and to a lesser extent -Ile, downregulate mTORC1 signaling and TOP mRNA translation, whereas valine -Val and triple starvation had minimal effects on these pathways. We agree that some of our conclusions and observed phenomena were not explained in sufficient detail in the original version. To address this, we have significantly reworked the discussion, added complementary figures and clarified key points throughout the text, to better convey the underlying rationale and biological interpretation of our findings. We address each of the reviewer’s points in detail in the point-by-point responses below.

Specific comments (some of which were mentioned above):

-The authors have treated cells with CHX in the Ribo-Seq experiments, which has been shown to cause artifacts in determining the locations of ribosome stalling in vivo owing to continued elongation in the presence of CHX (https://doi.org/10.1371/journal.pgen.1005732 ). The authors should comment on whether this artifact could be influencing some of their findings, particular the results in Fig. 5C where the hungry codons are often present upstream of the A sites of called stalling sites in the manner expected if elongation continued slowly following stalling in the presence of CHX.

Response: We thank the reviewer for raising this important concern. We would like to clarify that our ribosome profiling protocol did not include CHX pretreatment of live cells. CHX was added only during the brief PBS washes immediately before lysis and in the lysis buffer itself. This approach aligns with best practices aimed at minimizing post-lysis ribosome run-off, and is intended to prevent the downstream ribosome displacement artifacts described by Hussmann et al. 2015, which result from pre-incubation of live cells with CHX for several minutes before harvesting. Furthermore, recent studies have demonstrated that CHX-induced biases are species-specific. For instance, Sharma et al. 2021 found that human (and mice) ribosomes are not susceptible to conformational restrictions by CHX, nor does CHX distort gene-level measurements of ribosome occupancy. This suggests that the use of CHX in the lysis buffer, as performed in our protocol, is unlikely to introduce significant artifacts in our ribosome profiling data. To further support this, we reanalyzed data from Darnell, Subramaniam, and O’Shea 2018, where the ribosome profiling samples were prepared without any CHX pretreatment or CHX in the wash buffer, and still observed similar upstream enrichments in their stalling profiles (see Supplementary Figure 2B-C in our manuscript). Additionally, in our previous work (Gobet et al. 2020), we compared ribosome dwell times with and without CHX in the lysis buffer and found no significant differences, reinforcing the notion that CHX use during lysis does not substantially affect the measurement of ribosome stalling. Given these considerations, we believe that CHX-related artifacts, such as downstream ribosome movement, are unlikely to explain the enrichment of hungry codons upstream of identified stalling sites in our data. We have now adjusted the Methods section to clarify this point.

-p. 12: "These starvation-specific DT and ribosome density modulations were also evident at the individual transcript level, as exemplified by Col1a1, Col1a2, Aars, and Mki67 which showed persistent Val-codon-specific ribosome density increases but lost Ile-codon-specific increases under triple starvation (Supplementary Figure 3A-D). " This conclusion is hard to visualize for any but Val codons. It would help to annotate the relevant peaks of interest for -Ile starvation with arrows.

Response: We agree and thank the reviewer for this observation. We have now annotated exemplary peaks in Supplementary Figure 3A–D to highlight ribosome pileups over Ile codons. However, we agree that it is still hard to visualize in the given Figure. Therefore, we added scatter plots for each of the transcripts that show the RPM of each position in the Ctrl vs starvation to allow for a better illustration of the milder effects upon Ile starvation (Supplementary Figure 4).

-To better make the point that codon-specific stalling under BCAA starvation appears to be not driven by codon usage, rather than the analysis in Fig. 1H, wouldn't it be better to examine the correlation between increases in DT under the single amino acid starvation conditions and the codon frequencies across all codons?

Response: We appreciate the suggestion. We have now added an additional analysis correlating the change in DT with codon usage frequency for each starvation condition. This is included in Supplementary Figure 5A-D and supports our interpretation that codon frequency alone does not explain the observed stalling behavior.

-p. 13, entire paragraph beginning with "Our RNA-seq and Ribo-seq revealed a general activation of stress response pathways across all starvations..." It is difficult to glean any important conclusions from this lengthy analysis, and the results do not appear to be connected to the overall topic of the study. If there are important conclusions here that relate to the major findings then these connections should be made or noted later in the Discussion. If not, perhaps the analysis should be largely relegated to the Supplemental material.

Response: We thank the reviewer for this comment. The paragraph in question is intended to provide a global overview of transcriptional and translational responses across the starvation conditions. It serves both as a quality control (e.g., PCA clustering and global shifts in RPF/RNA-seq profiles), and to confirm that expected starvation-induced responses are among the strongest detectable signals separating the starved samples from the control. Indeed, these observations establish that the perturbations are effective and that hallmark nutrient stress responses are globally engaged across conditions. Importantly, very few studies to date have examined transcriptional and translational responses under single or combined branched-chain amino acid (BCAA) starvation conditions. It therefore remains unclear to what extent BCAA depletion broadly remodels gene expression and translation. Our analysis contributes to addressing this gap, revealing that while certain stress pathways are commonly induced, others show condition-specific patterns such as we observed for -Ile starvation. To maintain focus, we have kept the detailed pathway analyses and transcript-level enrichments in the Supplement and rewritten the corresponding text in a more compact manner, reducing it by more than one third.

-p. 15: "Together, these findings highlight that BCAA starvation triggers a combination of effects on initiation and elongation, with varying dynamics by amino acid starvation." I take issue with this statement as it appears that translation is reduced primarily at the initiation step for all conditions except -Ile. As noted above, these data are never menitioned in the DISCUSSION as to why only -Ile would show a marked elongation component to the inhibition whereas -Val gives the greatest amount of ribosome stalling.

Response: We acknowledge the reviewer’s point. While the polysome profiles (Figure 3F-H) directly indicate that most conditions repress initiation, codon- and condition-specific elongation defects can still contribute to reduced protein output, even if they are not always detectable as global polysome shifts. Polysome profiles reflect the combined outcome of reduced initiation (which decreases polysome numbers) and ribosome stalling (which can, but does not always have to, increase ribosome density on individual transcripts, potentially counteracting the effects of reduced initiation). For valine starvation strong stalling occurs very early in the CDS (Figure 5F). This bottleneck restricts overall ribosome movement to downstream regions. Thus, while elongation is profoundly impaired, the total number of ribosomes per transcript (which polysome signals largely reflect) may appear low due to reduced overall ribosome traffic. In contrast, isoleucine codon stalling tends to occur also further downstream on the transcript (Figure 5F), allowing ribosomes to accumulate in larger numbers on the mRNA, leading to a clearer "elongation signature" in polysome profiles (Figure 3F, H). Additionally, we observed slightly higher inter-replicate variance for isoleucine starvation (Supplementary Figure 6B), which may have reduced the number of statistically significant stalling sites extracted compared to valine. We have revised the main text and discussion to clarify these points.

-I cannot decipher Fig. 4D and more detail is required to indicate the identity of each column of data.

Response: We thank the reviewer for pointing this out. Figure 4D (now Figure 4E) presents an UpSet plot, which is a scalable alternative to Venn diagrams commonly used to visualize intersections across multiple sets. Briefly, each bar in the upper plot represents the number of transcripts with increased 5′ ribosome coverage (Δpi < -0.15; p < 0.05) shared across the conditions indicated in the dot matrix below. Each column in the dot matrix highlights the specific combination of conditions contributing to a given intersection (e.g., dots under “Val” and “Triple” show the overlap between these two). To improve clarity, we have expanded the figure legend accordingly and now refer to the UpSetR methodology in the main text.

-In Fig. 4E, one cannot determine what the P values actually are, which should be provided in the legend to confirm statistical significance.

Response: Thank you for pointing that out. The legend in Figure 4E (now Figure 4F) for the p-values was accidentally removed during figure editing. We have added the legend back, so that the statistical significance is clear.

-It's difficult to understand how the -Leu condition and the Double starvation can produce polarized RPFs (Fig. 4A) without evidence of stalling at the cognate hungry codons (Fig. 4E), despite showing later in Fig. 5A that the numbers of stall sites are comparable in those cases to that found for -Ile.

Response: We appreciate this comment, which points to an important property of RPF profiles under nutrient stress. As shown in Figure 4A, all starvation conditions induce a degree of 5′ ribosome footprint polarization, a pattern that can be observed under various stress conditions and perturbations (Allen et al. 2021; Hwang and Buskirk 2017; Li et al. 2023). This general 5′ bias likely reflects a combination of slowed elongation and altered ribosome dynamics and is not necessarily linked to codon-specific stalling. However, Val and Triple starvation show a much stronger and more asymmetric polarization, characterized by pronounced 5′ accumulation and 3′ depletion of ribosome density. To better illustrate this, we have updated the visualization of polarity scores and added a new bar chart summarizing the number of transcripts showing strong 5′ polarization under each condition. This quantification highlights that the effect is markedly more prevalent under Val and Triple conditions than under Leu or Double starvation. In addition, Figure 4F demonstrates that this polarity is codon-specific under Val and Triple starvation. We clarify that this analysis tests for enrichment of specific codons near the start codon among the polarized transcripts and does not directly assess stalling. The observed enrichment of Val codons in the 5′ regions of polarized transcripts supports the interpretation that early elongation delays contribute to the RPF shift. In contrast, no such enrichment is observed for Leu starvation, reinforcing that Leu-induced polarity is not driven by stalling at Leu codons. While Figure 5 shows a similar number of peak-called stalling sites in -Leu, -Ile, and Double starvation, we note that Ribo-seq signal variability under Ile starvation was higher, which may have limited statistical power for detecting stalling sites, even though clear dwell time increases were observed at specific codons. Additionally, we have improved the metagene plots depicting total ribosome footprint density in Figure 4A. The previous version incorrectly showed sharp drops at CDS boundaries due to binning artifacts. The updated version more accurately reflects the density distribution and further highlights the stronger polarization in Val and Triple conditions. Together, these clarifications and improvements within the main text now more clearly distinguish between general polarity effects and codon-specific stalling.

-Fig. 5B: the P values should be given for all five columns, and it should be explained here or in the Discussion why the authors conclude that stalling is an important determinant for reduced translation when a significant correlation seems to exist only for the -Val condition and not even for the Triple condition.

Response: We thank the reviewer for this important observation. In response, we have revised both the text and the figures to provide a clearer and biologically more meaningful representation of the relationship between ribosome stalling and reduced protein output. Specifically, we have replaced the previous Figure 5B with a new analysis that stratifies transcripts based on the number of identified stalling sites. This updated analysis, now shown in Figure 5B, reveals that under Val and Triple starvation conditions, proteins that are downregulated tend to originate from transcripts with multiple stalling sites. Importantly, the corresponding p-values for all five conditions are now explicitly shown in the figure (as red lines). As the reviewer correctly notes, only the Val condition shows a statistically significant enrichment when considering overall overlap. Triple starvation shows a similarly high proportion of overlap (72.3%) but does not reach statistical significance, likely due to the more complex background composition under combined starvation, which increases the expected overlap and reduces statistical power. By stratifying transcripts by the number of stalling sites, we uncover that transcripts with ≥2 stalling sites are enriched among downregulated proteins specifically under Val and Triple conditions, providing a more robust indication of the link between stalling and translation repression under Valine deprivations. We believe this refined approach, prompted by the reviewer’s comment, offers a clearer and biologically more relevant perspective on the role of ribosome stalling. The original analysis previously shown in Figure 5B is now provided as Supplemental Figure 10C for transparency and comparison. We have clarified this in the revised text and now interpret the relationship more cautiously.

-p. 17: "Of note, in cases where valine or isoleucine codons were present just upstream (rather than at) the stalling position, we noted a strong bias for GAG (E), GAA (E), GAU (D), GAC (D), AAG (K), CAG (Q), GUG (V) and GGA (G) (Val starvation) and AAC (N), GAC (D), CUG (L), GAG (E), GCC (A), CAG (Q), GAA (E) and AAG (K) (Ile starvation) at the stalling site (Supplementary Figure 7B)." The authors fail to explain why these codons would be present in the A sites at stalling sites rather than the hungry codons themselves, especially since it is the decoding times of the hungry codons that are increased according to Fig. 1A-E. As suggested above, is this a CHX artifact?

Response: We agree that the observation that the listed codons are enriched at identified stalling positions (now Supplementary Figure 10C), while the depleted amino acid codon is located upstream, is a finding that needs more detailed explanation. Importantly, this phenomenon is not attributable to CHX artifacts, as our Ribo-seq protocol employs CHX solely during brief washes and lysis to prevent post-lysis ribosome run-off, rather than live-cell pre-treatment. Instead, we propose two hypotheses to explain this pattern: Firstly, many of these enriched codons are already inherently slow-decoded with longer DTs even under control conditions (Supplementary Figure 5H, newly added). Together with the upstream hungry codons they might form a challenging consecutive decoding environment, which results in an attenuated ribosome slowdown downstream after the hungry codon. Second, ribosome queuing may further explain this pattern. When a ribosome encounters a critically hungry codon and stalls, subsequent ribosomes can form a queue. The codon within the A-site of the queued ribosome would be (more or less) independent of the identity of the hungry codon itself that caused the initial stall. Since the listed codons have a high frequency within the transcriptome (Supp. Fig 5B), they therefore have an increased likelihood of appearing at this “stalling site”. Importantly, both of these phenomena are not necessarily represented by a general increase of DT on all of the listed codons and would therefore only be captured by the direct extraction of stalling sites but might be averaged out in the global dwell time analysis. We mention this phenomenon now in the Discussion.

-Fig. 5D: P values for the significance, or lack thereof, of the different overlaps should be provided.

Response: Thanks for pointing out this omission. We have now computed hypergeometric p-values for comparisons shown in Figure 5D and Figure 5E, and report them directly in the main text. As described, the overlap in stalling sites between Val and triple starvation is highly significant (2522 positions, p < 2.2×10⁻¹⁶), while overlaps involving Ile-specific stalling positions are smaller but still statistically robust (e.g., 149 positions for Ile – Triple, p = 1.77×10⁻⁵²). Notably, we also calculated p-values at the transcript level and found that a large fraction of transcripts with Ile-specific stalling under single starvation also stall under triple starvation, though often at different positions (1806 transcripts, p = 1.78×10⁻⁵⁸). These values are now included in the revised results section to support the interpretation of these overlaps.

-p. 17: "Nonetheless, when we examined entire transcripts rather than single positions, many transcripts that exhibited isoleucine-related stalling under Ile starvation also stalled under triple starvation, but at different sites along the CDS (Figure 5E). This finding is particularly intriguing, as it suggests that while Ile-starvation-specific stalling sites may shift under triple starvation, the overall tendency of these transcripts to stall remains." The authors never come back to account for this unexpected result.

Response: Thank you for highlighting this point. We've incorporated this finding as part of the proposed "bottleneck" scenario. While the isoleucine-specific stalling sites identified under Ile starvation do shift or disappear under triple starvation, we've observed that the same transcripts still tend to exhibit stalling. However, this now primarily occurs at upstream valine codons. We interpret this as a consequence of early elongation stalling caused by strong pausing at Val codons. This restriction on ribosome progression effectively prevents ribosomes from reaching the original Ile stalling sites. Therefore, the stalling sites identified under triple starvation are largely explained by the Val codons, reflecting a redistribution of stalling rather than its loss. To further clarify this crucial point, we've now explicitly mentioned Figure 5D-E again in the subsequent paragraph, which introduces the bottleneck theory.

-It seems very difficult to reconcile the results in Fig. 5F with those in Fig. 4A, where similar polarities in RPFs are observed for -Ile and -Val in Fig, 4A but dramatically different distributions of stalling sites in Fig. 5F. More discussion of these discrepancies is required.

Response: Thank you for pointing this out. The apparent discrepancy between the RPF profiles shown in Figure 4A and the stalling site distributions in Figure 5F likely reflects the fact that RPF polarization includes both general (unspecific) and codon-specific components. Figure 4A displays total ribosome footprint density, capturing both broad stress-induced effects and codon-specific contributions, whereas Figure 5F focuses specifically on peak-called stalling sites, representing localized and statistically significant pauses. Importantly, we would like to emphasise that Fig 4 shows that -Val and -Ile starvation exhibit different responses and not the same patterns. To make these differences even clearer, we have now updated the visualizations in Figure 4, including improved polarity plots and a new bar chart summarizing the number of transcripts with strong 5′ polarization. These additions highlight that the RPF profiles under -Val starvation are more pronounced and asymmetric, particularly due to 3′ depletion, while the polarity under -Ile is milder and a distinct, much smaller subset of transcripts appears to show polarity score shifts. We believe the updated figures and accompanying explanations now make these distinctions clearer.

• p. 18: " These isoacceptor-specific patterns correlate largely with the particular subsets of leucine and isoleucine codons that stalled (Figure 1A)." This correlation needs to be addressed for each codon-anticodon pair for all of the codons showing stalling in Fig. 1A.

Response: We thank the reviewer for this important comment. In the revised manuscript, we have expanded the relevant sections to address codon–anticodon relationships more thoroughly. We now explicitly match codons that exhibited increased dwell times under starvation to the corresponding tRNA isoacceptors whose charging was affected, and we provide a clearer discussion of the caveats involved. As noted by the reviewer, this correlation is not straightforward, as it is complicated by wobble base pairing, anticodon modifications, and the fact that multiple codons can be decoded by more than one isoacceptor, and vice versa. Moreover, in our qPCR-based tRNA charging assay, certain isoacceptors cannot be distinguished due to highly similar sequences (e.g., LeuAAG and LeuUAG, and LeuCAA and LeuCAG), which limits resolution for exact pairing. In addition, we did not assess absolute tRNA abundance, which may further influence decoding capacity. Nevertheless, where resolution is possible, the patterns align well: All tRNAVal isoacceptors became uncharged under Val and triple starvation, matching the consistent dwell time increases across all Val codons. Only tRNAIleAAU (decoding AUU and AUC) was deacylated, matching to these codons showing increased dwell times, while AUA (decoded by still-charged tRNAIleUAU) did not. Only CUU (decoded by uncharged tRNALeuGAA) showed increased dwell time. A mild deacylation of the other Leu isoacceptors was observed, but isoacceptor-level resolution is limited by assay constraints. However, these rather minimal tRNA and DT changes were consistent with more dominant initiation repression rather than elongation stalls. To support this analysis, we included an illustrative figure (now in Supplementary Figure 12F) summarizing the codon–anticodon matches.

-p. 19: "For instance, in our double starvation condition, unchanged tRNA charging levels (Figure 6E) may result from a pronounced downregulation of global translation initiation, likely driven by the activation of stress responses (Figure 2), subsequently lowering the demand for charged tRNAs as it has been observed previously for Leu starvation 39.” This seems at odds with the comparable down-regulation of protein synthesis for the Double starvation and -Leu and -Ile single starvations shown in Fig. 3C. Also, in the current study, Leu starvation does lower charging of certain Leu tRNAs.

Response: We thank the reviewer for raising this important point. In the revised manuscript, we have clarified this section and now offer a more refined interpretation of the tRNA charging patterns observed under double starvation. While Figure 3C shows a comparable reduction in global protein synthesis across the -Leu, -Ile, and double starvation conditions, it needs to be considered that the OPP assay has limited sensitivity. It operates in a relatively low fluorescence intensity range and is subject to background signal, which may obscure subtle differences between conditions. Moreover, other factors such as changes in protein stability or turnover could also contribute to the observed differences. Therefore, inter-condition differences in translation repression should be interpreted with caution. However, based on our stress response analysis (Figure 2), mTORC1 inactivation appears strongest under double starvation, likely leading to more profound suppression of translation initiation. This would reduce the overall demand for charged tRNAs and could explain why no detectable tRNA deacylation was observed under double starvation, even though mild uncharging of Leu isoacceptors occurred under -Leu, which exhibited a milder stress response. This distinction is consistent with the observed mild dwell time increases for one Leu codon under -Leu, but not in the double condition. Similarly, the absence of Ile codon stalling and tRNA deacylation under double starvation may be attributed to stress-driven reductions in elongation demand, preventing the tRNA depletion and codon-specific delays observed under single Ile starvation. A more direct clarification is now included in the revised manuscript.

Reviewer #2 (Significance):

The results here are significant in showing that starvation for a single amino acid does not lead to deacylation of all isoacceptors for that amino acid and in revealing that starvation for one amino acid can prevent deacylation of tRNAs for other amino acids, as shown most dramatically for the selective deacylation of only Val tRNAs in the triple BRCAA starvation condition. For the various reasons indicated above, however, I'm not convinced that their "bottleneck" mechanism is adequate to explain this phenomenon, especially in the case of the selective deacylation of Ile vs Leu tRNA in the Double starvation regime. It's also significant that deacylation leads to ribosome build-up near the 5'ends of CDS, which seems to be associated with an enrichment for the hungry codons in the case of Val and Ile starvation, but inexplicably, not for Leu or the Double starvations. This last discrepancy makes it hard to understand how the -Leu and Double starvations produce RPF buildups near the 5 ends of CDSs. In addition, the claim in the Discussion that "our data also highlight the importance of the codon positional context within mRNAs, indicating that where a codon is located within the CDS can influence both the extent of ribosomal stalling and overall translation efficiency during nutrient stress" overstates the strength of evidence that the stalling events lead to substantial decreases in translational efficiencies for the affected mRNAs, as the stalling frequency and decreased protein output are significantly correlated only for the -Val starvation, and the data in Fig. 3 D-H suggest that the reductions in protein synthesis generally occur at the level of initiation, even for -Val starvation, with a contribution from slow elongation only for -Ile-which is in itself difficult to understand considering that stalling frequencies are highest in -Val. Thus, while many of the results are very intriguing and will be of considerable interest to the translation field, it is my opinion that a number of results have been overinterpreted and that important inconsistencies and complexities have been overlooked in concluding that a significant component of the translational inhibition arises from the increased decoding times at hungry codons during elongation and that the selective deacylation of Val tRNAs in the Triple starvation can be explained by the "bottleneck" mechanism. The complexities and limitations of the data and their intepretations should be discussed much more thoroughly in the Discussion, which currently is devoted mostly to other phenomena often of tangential importance to the current findings. A suitably revised manuscript would clearly state the limitations and caveats of the proposed mechanisms and consider other possible explanations as well.

Again, we thank the reviewer for the valuable insights and constructive critiques. We believe that the concerns regarding potential overinterpretation and inconsistencies have now been addressed through clearer explanations and more cautious interpretation throughout the revised manuscript. We also agree that the original Discussion included aspects that, while interesting, were of secondary importance. In light of the reviewer’s suggestions, we have restructured and rebalanced the Discussion to focus more directly on the key findings and their implications. Importantly, we wish to clarify that we do not propose the elongation bottleneck model as a general mechanism across all conditions. In particular, for double (Leu/Ile) starvation, we attribute the observed effects primarily to stress response–mediated translational repression, and not to codon-specific stalling or tRNA depletion. We believe that this distinction is now more clearly conveyed in the revised manuscript.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary

Worpenberg and colleagues investigated the translational consequences of branched-chain amino acid (BCAA) starvation in mouse cells. Limitation of individual BCAAs has been reported to cause codon-specific and global translational repression. In this paper, the authors use RNA-seq, ribosome profiling (Ribo-seq), proteomics, and tRNA charging assays to characterize the impacts of individual and combined depletion of leucine, isoleucine, and valine on translation. They find that BCAA starvation increases codon-specific ribosome dwell times, activates global translational stress responses and reduces global protein synthesis. They infer that this effect is due to decreased translation initiation and codon-specific translational stalling. They find that the effects of simultaneous depletion are non-additive. In valine and triple (valine, leucine, and isoleucine) depletion, they show that affected transcripts have a high density of valine codons early in their coding sequences, creating an "elongation bottleneck" that obscures the impact of starvation of other amino acids. Finally, they identify isoacceptor-specific differences in tRNA charging that help explain the codon-specific effects that they observe.

We find the major findings convincing and clear. We find that some results are incompletely explained. We suggest an additional experiment and also have some minor comments that we hope will improve clarity and rigor.

We thank the reviewer for the thorough and constructive feedback. We appreciate the recognition of our main findings and the helpful suggestions for improving the manuscript. Below we address each point in detail.

Major comments

Figure 3O: In this figure and the associated text, the authors try to determine whether differences in protein degradation can explain why some proteins have higher ribosome density but lower proteomic expression. However, since this analysis relies on published protein half-lives from non-starvation conditions and on the assumption that protein synthesis has entirely stopped, we are not convinced it is informative for this experimental context. It does not distinguish between a model in which protein synthesis has been reduced by stalling and a model in which both protein synthesis and degradation rate have increased, which are both consistent with their Ribo-seq and proteomic data. To address this issue, the authors should either perform protein half-life measurements under their starvation conditions, or more clearly explain these two models in the text and acknowledge that they cannot distinguish between them.

Response: We agree with the reviewer that our current analysis, which is based on protein half-lives obtained under non-starvation conditions, can not definitively separate the effects of reduced translation from those of increased protein degradation. We have revised the relevant section in the manuscript to more clearly state that this analysis is correlative in nature and serves only to explore one possible explanation for the observed disconnect between ribosome density and protein levels. We now also explicitly acknowledge that our dataset does not allow us to distinguish between a model in which protein output is reduced due to stalling and one in which both translation and degradation rates are altered. However, the observed log2FC in the proteomics data are often milder than expected based on complete-medium condition half-life alone, which would be difficult to reconcile with a dominant contribution from global protein destabilization. That said, we also acknowledge that protein degradation is highly context- and protein-specific, and that proteolytic regulation might still play a role. Performing a direct protein half-life measurement under our starvation conditions would indeed be required to rigorously test this, but such an experiment is outside the scope of this study. We now highlight this as a limitation and a valuable direction for future work, and we have softened any interpretations in the main text to reflect the uncertainty regarding the contribution of protein stability changes.

Minor comments

Figure 1G: Why does intracellular valine seem to be less depleted under starvation conditions than intracellular leucine or isoleucine? Are the limits of detections different for different amino acids? The authors should acknowledge this discrepancy and comment on whether it has any implications for interpretation of their results.

Response: We thank the reviewer for this important point. While valine appears slightly less depleted than leucine or isoleucine in Figure 1G, the fold changes and absolute reductions are strong for all three BCAAs, including valine. To further illustrate this, we have added a supplementary bar chart showing the measured intracellular concentrations in µmol/L, including mean and variance across five biological replicates (Supplementary Figure 5A). We believe that the variation may reflect technical factors, such as differences in detection sensitivity or ionization efficiency between amino acids in the targeted metabolomics assay and, therefore, that the observed difference does not have a meaningful impact on the interpretation of our results. We now directly acknowledge these differences in the main text.

Figure 1H: These data do not appear to meet the assumptions for linear regression. We suggest either reporting a Spearman R correlation (as the data appears linear in rank but not absolute value), or remove it entirely - we think the plot without statistics is sufficient.

Response: We thank the reviewer for the suggestion. In the revised manuscript, we removed the statistical annotation and retained only the trend line to illustrate the general pattern. We agree that this visualization alone is sufficient to support the qualitative point we aimed to convey.

Figure 2B: The in-text description of this figure states that "most" ISR genes show a "robust induction," but only three genes are shown in the figure, two of which are upregulated. The authors should instead specify that 2 out of the 3 genes profiled were robustly induced.

Response: We have rephrased the sentence to say “two of the three genes profiled…” for precision and consistency with the data shown.

Figure 2D: Please include the full, uncropped blots in the supplementary materials.

Response: We have now added the full, uncropped western blots to the supplementary material (Supplementary Figure 8).

Figure 2E: Swap the positions of the RPS6 and 4E-BP1 plots so they line up with their respective blots to make these figures easier to interpret. Authors should consider doing a one-way ANOVA and post-hoc analysis, if we correctly understand that they are making a conclusion about the difference between multiple groups in aggregate.

Response: We thank the reviewer for the suggestion. The alignment of the RPS6 and 4E-BP1 plots with their respective blots has been corrected. As this panel focuses on comparisons to the control condition only, we have retained the original presentation.

Figure 4B: Panel A in this figure is very convincing, and these plots don't add additional information. The authors could consider removing them. If this panel stays in, we suggest removing the "mid index" plot, since it is never referenced in the text and doesn't seem relevant to the message of the figure.

Response: We appreciate the feedback. While we considered removing panel B as suggested, we decided to retain it because it provides a useful summary of panel A. To improve clarity and visual interpretation, we replaced the original boxplot with a bar plot displaying mean values and SEM error bars. We believe the bar plot now nicely illustrates that Val and Triple starvation lead to stronger effects, especially in the reduction of the 3′ index. The “mid index” plot, which was not referenced in the text and did not contribute to the central message, has been removed as suggested.

Figure 4E: Why is there a reduction in frequency of a Leu and a Val codon under Ile starvation?

Response: Thank you for highlighting this observation. The reduction in the frequency of a specific Leu and Val codon under Ile starvation in Figure 4F (former Figure 4E) is indeed intriguing. This figure reflects codon usage in the first 20% of the CDSs among the subset of transcripts that exhibit a footprint polarization under each starvation condition. As such, the observed depletion likely arises from the specific transcript composition of the polarized subset under -Ile, which differs from that under -Val or other conditions. Importantly, this pattern is not consistently observed when analyzing the full transcripts (another Leu codon is affected), indicating that it is not a systematic depletion of these codons. One possibility is that an increased frequency of Ile codons (AUC) within the constrained region may lead to a relative underrepresentation of other codons, such as Leu and Val. Alternatively, this may reflect non-random codon co-occurrence patterns within specific transcripts. While our current data do not allow us to investigate this further, we acknowledge these as speculative explanations and now mention this point in the Discussion as a potential avenue for future study.

Figure 5G: There appears to be one Val codon early in the Hint1 transcript without much stalling under triple or valine starvation conditions. The authors should acknowledge this and comment on why this may be.

Response: We thank the reviewer for pointing this out. While the Hint1 transcript indeed contains a valine codon early in its CDS, no clear stalling peak was observed at that position under valine or triple starvation. Several factors may contribute to this: local sequence context can influence ribosome pausing, and not all cognate codons necessarily lead to detectable stalling even under amino acid starvation. Additionally, coverage at the 5′ end of Hint1 is relatively sparse in our dataset, and potential mappability limitations, such as regions with low complexity or repetitive elements, may further reduce resolution at specific sites. We now briefly mention this in the manuscript to clarify the possible causes.

Figure 5B: In the text referencing this figure, the authors state that "a high number of downregulated proteins with associated ribosome stalling sites did not show an overall decreased mean RPF count...as it would be expected from translation initiation defects, linking these stalling sites directly to proteomic changes." However, RPF is affected both by stalling (increases RPF) and initiation defects (decreases RPF). A gene with both stalling and decreased initiation may appear to have no RPF change. The data does suggest a contribution from stalling, but the authors should also acknowledge that reduced initiation may also be playing a role.

Response: We agree with the reviewer comment. Our cited statement should indeed be more nuanced. The reviewer correctly points out that RPFs are influenced by both increased ribosome density due to stalling and decreased ribosome density due to reduced initiation. Therefore, a gene experiencing both stalling and reduced initiation might appear to have no net change in RPF, or even a slight increase if stalling is dominant. Thus, while the presence of stalling sites strongly suggests a contribution from compromised elongation to reduced protein output, we cannot definitively rule out a concurrent role for reduced initiation, even in cases where RPF counts are not globally decreased. We revised this section in the manuscript to acknowledge this interplay.

Figure 5E: the black text on dark brown in the center of the Venn diagram is difficult to read. The diagram should either have a different color scheme, or the text in the center should be white instead of black for higher contrast.

Response: We have adjusted the text color for better contrast and improved readability.

Supplementary Figure 1C: The ribosome dwell time data in this study is described as "highly correlated" with another published dwell time dataset, but the P and E site data do not seem strongly correlated. The authors should remove the word "highly."

Response: We have removed the word “highly” to have a more cautious interpretation in the text.

Supplementary Figure 3E: Not all of the highlighted codons in this figure are ones with prolonged dwell times. To clarify the point that dwell time change is not related to codon frequency, this figure should only highlight codons that have a significantly prolonged dwell time in at least one starvation condition.

Response: We thank the reviewer for pointing this out. To improve clarity, we have revised the figure and now specifically highlight codons with significantly prolonged dwell times with stars.

Supplementary Figure 5C: The gene Chop is mentioned in the main text when referencing this figure, but is absent from the heatmap.

Response: We thank the reviewer for noting this. The gene Chop is annotated under its alternative name Ddit3 in the current version of the heatmap and is indeed present. To avoid confusion, we have now updated the label in the figure to display Chop (Ddit3) directly.

Supplementary Figure 7A: The authors could clarify this figure by adding additional language to either the figure panel or the figure legend specifying that the RPM metric being used comes from Ribo-seq.

Response: We have updated the legend to explicitly state that the RPM values shown are derived from Ribo-seq data.

Supplementary Figure 7D: The metric used to describe the spatial relationship between the first valine and isoleucine codons in transcripts in this figure seems to be describing something conceptually similar to the stalling sites in Figure 5G, but uses a different metric. These figures would be easier to interpret if these spatial relationships were presented in a consistent way throughout the manuscript.

Response: We thank the reviewer for this helpful observation. Supplementary Figure 7D (now Supplementary Figure 11B) originally used a gene-length-normalized metric to describe codon spacing, whereas Figure 5G depicted absolute nucleotide distances to stalling sites. To ensure consistency across the manuscript, we have now updated Supplementary Figure 11B to also use absolute distances. We believe this adjustment improves clarity and allows for a more direct comparison between spatial codon patterns and stalling events.

Discussion:

Reader understanding would be improved if the relevance of paragraphs were established in the first sentence. For instance, in the paragraphs about adaptive misacylation and posttranscriptional modifications, it is unclear until the end of the paragraph how these topics are relevant. Introducing the relevant aspects of the study (the fact that some starvation conditions have less severe effects and the observation about m6A-related mRNAs) at the beginning of these paragraphs would improve clarity.

Response: We thank the reviewer for this helpful comment. We agree that the flow and clarity of the Discussion can be improved by making the relevance of each paragraph clearer from the outset. In the revised manuscript, we have restructured these sections to better highlight the connection between each topic and our main findings. These changes also align with suggestions from Reviewer 2, and we believe they help to focus the Discussion more tightly around the core insights of our study.

The authors should provide more information and speculation about possible physiological relevance of their findings, particularly about the way that the effects of triple starvation are highly valine-dependent. Are there physiological conditions under which starvation of all three BCAAs is more likely than starvation of one or two of them? If so, are there any reasons why a valine-based bottleneck might be advantageous?

Response: We appreciate the reviewer's insightful question regarding the physiological relevance of our findings, particularly the valine-dependent bottleneck observed under triple BCAA starvation. This prompts a crucial discussion on the broader biological context of our work.

While complete starvation of all three BCAAs might be less frequent than individual deficiencies, such conditions are physiologically relevant in several contexts. In prolonged fasting, starvation, or severe cachectic states associated with chronic diseases (e.g., advanced cancer, critical illness), systemic amino acid pools, including BCAAs, can become significantly depleted due to increased catabolism and insufficient intake (Yu et al. 2021). Moreover, certain specialized diets or therapeutic strategies aim to modulate BCAA levels. For instance, in some Maple Syrup Urine Disease (MSUD) management protocols, BCAA intake is severely restricted to prevent the accumulation of toxic BCAA metabolites (Mann et al. 2021). Similarly, emerging cancer therapies sometimes explore nutrient deprivation strategies to selectively target tumor cells, which could involve broad BCAA reduction (e.g. Sheen et al. 2011; Xiao et al. 2016).

In these contexts, a valine-based bottleneck, as we describe, could indeed represent an adaptive strategy. If valine-tRNAs are particularly susceptible to deacylation and valine codons are strategically enriched at the 5' end of transcripts, stalling at these early positions could serve as a rapid "gatekeeper" for global translation. This early-stage inhibition would conserve cellular energy and available amino acids by quickly reducing the overall demand for charged tRNAs. Such a mechanism could potentially prioritize the translation of a subset of proteins that might have different codon usage biases or are translated via alternative, less valine-dependent mechanisms. This aligns with the concept of a multi-layered translational control where global initiation repression (as reflected in mTORC1 inhibition and polysome profiles) is complemented by specific elongation checkpoints, allowing for a more nuanced and adaptive response to severe nutrient stress.

Reviewer #3 (Significance):

Nature and significance of the advance

The main contribution of this work is to demonstrate that depletion of multiple amino acids simultaneously impacts translation elongation in ways that are not necessarily additive. These impacts can depend on the distribution of codons in a transcript. It adds to a growing body of work showing that essential amino acid starvation can cause codon-specific ribosome stalling. The authors suggest that the position-dependent stalling they observe could be a novel regulatory mechanism to alleviate the effects of multi-amino acid starvation. However, it is not fully clear from the paper what the significance of a valine-based regulatory adaptation to BCAA starvation is, or whether simultaneous starvation of all three BCAAs is of particular physiological relevance. The paper's primary contribution is mainly focused on the similarity between valine and triple BCAA starvation, and it provides limited insight into the effects of combined depletion of two BCAAs.

Context of existing literature

Although ribosome profiling does not distinguish between actively-elongating and stalled ribosomes, sites with higher read coverage, and thereby higher inferred dwell time, can be used to infer ribosome stalling (Ingolia 2011). Various downstream effects of essential amino acid depletion have been documented, such as leucine deficiency being sensed by mTORC1 via leucyl-tRNA synthetase (Dittmar 2005, Han 2012), and shared transcriptional responses among many amino acid depletion conditions (Tang 2015). These authors have previously measured the translational effects of nutrient stress using ribosome profiling (e.g., Gobet 2020), as have others (Darnell 2018, Kochavi et al. 2024). The present work represents the first study (to our knowledge) combining BCAA depletions, representing an incremental and useful contribution to our understanding of translational responses to stress conditions.

Audience

This work is of interest to investigators studying the response of human cells in stress conditions, such as in human disease, as well as investigators studying the basic biology of eukaryotic translational control.

Reviewer expertise: mRNA decay and translation regulation in bacteria.

We hope the authors have found our comments thoughtful and useful. We welcome further discussion or clarification via email: Juliana Stanley (julianst@mit.edu) and Hannah LeBlanc (leblanch@mit.edu).

We sincerely thank the reviewers for their thoughtful and constructive feedback, as well as for their careful and thorough reading of our manuscript. We also gratefully acknowledge the invitation for further discussion and would be happy to engage in future correspondence.

References

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Darnell, Alicia M., Arvind R. Subramaniam, and Erin K. O’Shea. 2018. “Translational Control through Differential Ribosome Pausing during Amino Acid Limitation in Mammalian Cells.” Molecular Cell 71 (2): 229-243.e11. https://doi.org/10.1016/j.molcel.2018.06.041.

Dittmar, Kimberly A., Michael A. Sørensen, Johan Elf, Måns Ehrenberg, and Tao Pan. 2005. “Selective Charging of tRNA Isoacceptors Induced by Amino-Acid Starvation.” EMBO Reports 6 (2): 151–57. https://doi.org/10.1038/sj.embor.7400341.

Elf, Johan, Daniel Nilsson, Tanel Tenson, and Mans Ehrenberg. 2003. “Selective Charging of tRNA Isoacceptors Explains Patterns of Codon Usage.” Science (New York, N.Y.) 300 (5626): 1718–22. https://doi.org/10.1126/science.1083811.

Gobet, Cédric, Benjamin Dieter Weger, Julien Marquis, Eva Martin, Nagammal Neelagandan, Frédéric Gachon, and Felix Naef. 2020. “Robust Landscapes of Ribosome Dwell Times and Aminoacyl-tRNAs in Response to Nutrient Stress in Liver.” Proceedings of the National Academy of Sciences of the United States of America 117 (17): 9630–41. https://doi.org/10.1073/pnas.1918145117.

Hussmann, Jeffrey A., Stephanie Patchett, Arlen Johnson, Sara Sawyer, and William H. Press. 2015. “Understanding Biases in Ribosome Profiling Experiments Reveals Signatures of Translation Dynamics in Yeast.” Edited by Michael Snyder. PLOS Genetics 11 (12): e1005732. https://doi.org/10.1371/journal.pgen.1005732.

Hwang, Jae-Yeon, and Allen R. Buskirk. 2017. “A Ribosome Profiling Study of mRNA Cleavage by the Endonuclease RelE.” Nucleic Acids Research 45 (1): 327–36. https://doi.org/10.1093/nar/gkw944.

Juszkiewicz, Szymon, and Ramanujan S. Hegde. 2017. “Initiation of Quality Control during Poly(A) Translation Requires Site-Specific Ribosome Ubiquitination.” Molecular Cell 65 (4): 743-750.e4. https://doi.org/10.1016/j.molcel.2016.11.039.

Li, Fajin, Jianhuo Fang, Yifan Yu, Sijia Hao, Qin Zou, Qinglin Zeng, and Xuerui Yang. 2023. “Reanalysis of Ribosome Profiling Datasets Reveals a Function of Rocaglamide A in Perturbing the Dynamics of Translation Elongation via eIF4A.” Nature Communications 14 (1): 553. https://doi.org/10.1038/s41467-023-36290-w.

Mann, Gagandeep, Stephen Mora, Glory Madu, and Olasunkanmi A. J. Adegoke. 2021. “Branched-Chain Amino Acids: Catabolism in Skeletal Muscle and Implications for Muscle and Whole-Body Metabolism.” Frontiers in Physiology 12 (July):702826. https://doi.org/10.3389/fphys.2021.702826.

Saikia, Mridusmita, Xiaoyun Wang, Yuanhui Mao, Ji Wan, Tao Pan, and Shu-Bing Qian. 2016. “Codon Optimality Controls Differential mRNA Translation during Amino Acid Starvation.” RNA (New York, N.Y.) 22 (11): 1719–27. https://doi.org/10.1261/rna.058180.116.

Sharma, Puneet, Jie Wu, Benedikt S. Nilges, and Sebastian A. Leidel. 2021. “Humans and Other Commonly Used Model Organisms Are Resistant to Cycloheximide-Mediated Biases in Ribosome Profiling Experiments.” Nature Communications 12 (1): 5094. https://doi.org/10.1038/s41467-021-25411-y.

Sheen, Joon-Ho, Roberto Zoncu, Dohoon Kim, and David M. Sabatini. 2011. “Defective Regulation of Autophagy upon Leucine Deprivation Reveals a Targetable Liability of Human Melanoma Cells In Vitro and In Vivo.” Cancer Cell 19 (5): 613–28. https://doi.org/10.1016/j.ccr.2011.03.012.

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Yu, Deyang, Nicole E. Richardson, Cara L. Green, Alexandra B. Spicer, Michaela E. Murphy, Victoria Flores, Cholsoon Jang, et al. 2021. “The Adverse Metabolic Effects of Branched-Chain Amino Acids Are Mediated by Isoleucine and Valine.” Cell Metabolism 33 (5): 905-922.e6. https://doi.org/10.1016/j.cmet.2021.03.025.

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Referee #3

Evidence, reproducibility and clarity

Summary

Worpenberg and colleagues investigated the translational consequences of branched-chain amino acid (BCAA) starvation in mouse cells. Limitation of individual BCAAs has been reported to cause codon-specific and global translational repression. In this paper, the authors use RNA-seq, ribosome profiling (Ribo-seq), proteomics, and tRNA charging assays to characterize the impacts of individual and combined depletion of leucine, isoleucine, and valine on translation. They find that BCAA starvation increases codon-specific ribosome dwell times, activates global translational stress responses and reduces global protein synthesis. They infer that this effect is due to decreased translation initiation and codon-specific translational stalling. They find that the effects of simultaneous depletion are non-additive. In valine and triple (valine, leucine, and isoleucine) depletion, they show that affected transcripts have a high density of valine codons early in their coding sequences, creating an "elongation bottleneck" that obscures the impact of starvation of other amino acids. Finally, they identify isoacceptor-specific differences in tRNA charging that help explain the codon-specific effects that they observe.

We find the major findings convincing and clear. We find that some results are incompletely explained. We suggest an additional experiment and also have some minor comments that we hope will improve clarity and rigor.

Major comments

Figure 3O: In this figure and the associated text, the authors try to determine whether differences in protein degradation can explain why some proteins have higher ribosome density but lower proteomic expression. However, since this analysis relies on published protein half-lives from non-starvation conditions and on the assumption that protein synthesis has entirely stopped, we are not convinced it is informative for this experimental context. It does not distinguish between a model in which protein synthesis has been reduced by stalling and a model in which both protein synthesis and degradation rate have increased, which are both consistent with their Ribo-seq and proteomic data. To address this issue, the authors should either perform protein half-life measurements under their starvation conditions, or more clearly explain these two models in the text and acknowledge that they cannot distinguish between them.

Minor comments

Figure 1G: Why does intracellular valine seem to be less depleted under starvation conditions than intracellular leucine or isoleucine? Are the limits of detections different for different amino acids? The authors should acknowledge this discrepancy and comment on whether it has any implications for interpretation of their results.

Figure 1H: These data do not appear to meet the assumptions for linear regression. We suggest either reporting a Spearman R correlation (as the data appears linear in rank but not absolute value), or remove it entirely - we think the plot without statistics is sufficient.

Figure 2B: The in-text description of this figure states that "most" ISR genes show a "robust induction," but only three genes are shown in the figure, two of which are upregulated. The authors should instead specify that 2 out of the 3 genes profiled were robustly induced.

Figure 2D: Please include the full, uncropped blots in the supplementary materials.

Figure 2E: Swap the positions of the RPS6 and 4E-BP1 plots so they line up with their respective blots to make these figures easier to interpret. Authors should consider doing a one-way ANOVA and post-hoc analysis, if we correctly understand that they are making a conclusion about the difference between multiple groups in aggregate.

Figure 4B: Panel A in this figure is very convincing, and these plots don't add additional information. The authors could consider removing them. If this panel stays in, we suggest removing the "mid index" plot, since it is never referenced in the text and doesn't seem relevant to the message of the figure.

Figure 4E: Why is there a reduction in frequency of a Leu and a Val codon under Ile starvation?

Figure 5G: There appears to be one Val codon early in the Hint1 transcript without much stalling under triple or valine starvation conditions. The authors should acknowledge this and comment on why this may be.

Figure 5B: In the text referencing this figure, the authors state that "a high number of downregulated proteins with associated ribosome stalling sites did not show an overall decreased mean RPF count...as it would be expected from translation initiation defects, linking these stalling sites directly to proteomic changes." However, RPF is affected both by stalling (increases RPF) and initiation defects (decreases RPF). A gene with both stalling and decreased initiation may appear to have no RPF change. The data does suggest a contribution from stalling, but the authors should also acknowledge that reduced initiation may also be playing a role.

Figure 5E: the black text on dark brown in the center of the Venn diagram is difficult to read. The diagram should either have a different color scheme, or the text in the center should be white instead of black for higher contrast.

Supplementary Figure 1C: The ribosome dwell time data in this study is described as "highly correlated" with another published dwell time dataset, but the P and E site data do not seem strongly correlated. The authors should remove the word "highly."

Supplementary Figure 3E: Not all of the highlighted codons in this figure are ones with prolonged dwell times. To clarify the point that dwell time change is not related to codon frequency, this figure should only highlight codons that have a significantly prolonged dwell time in at least one starvation condition.

Supplementary Figure 5C: The gene Chop is mentioned in the main text when referencing this figure, but is absent from the heatmap.

Supplementary Figure 7A: The authors could clarify this figure by adding additional language to either the figure panel or the figure legend specifying that the RPM metric being used comes from Ribo-seq.

Supplementary Figure 7D: The metric used to describe the spatial relationship between the first valine and isoleucine codons in transcripts in this figure seems to be describing something conceptually similar to the stalling sites in Figure 5G, but uses a different metric. These figures would be easier to interpret if these spatial relationships were presented in a consistent way throughout the manuscript.

Discussion:

Reader understanding would be improved if the relevance of paragraphs were established in the first sentence. For instance, in the paragraphs about adaptive misacylation and posttranscriptional modifications, it is unclear until the end of the paragraph how these topics are relevant. Introducing the relevant aspects of the study (the fact that some starvation conditions have less severe effects and the observation about m6A-related mRNAs) at the beginning of these paragraphs would improve clarity.<br /> The authors should provide more information and speculation about possible physiological relevance of their findings, particularly about the way that the effects of triple starvation are highly valine-dependent. Are there physiological conditions under which starvation of all three BCAAs is more likely than starvation of one or two of them? If so, are there any reasons why a valine-based bottleneck might be advantageous?

We hope the authors have found our comments thoughtful and useful. We welcome further discussion or clarification via email: Juliana Stanley (julianst@mit.edu) and Hannah LeBlanc (leblanch@mit.edu).

Significance

Nature and significance of the advance

The main contribution of this work is to demonstrate that depletion of multiple amino acids simultaneously impacts translation elongation in ways that are not necessarily additive. These impacts can depend on the distribution of codons in a transcript. It adds to a growing body of work showing that essential amino acid starvation can cause codon-specific ribosome stalling. The authors suggest that the position-dependent stalling they observe could be a novel regulatory mechanism to alleviate the effects of multi-amino acid starvation. However, it is not fully clear from the paper what the significance of a valine-based regulatory adaptation to BCAA starvation is, or whether simultaneous starvation of all three BCAAs is of particular physiological relevance. The paper's primary contribution is mainly focused on the similarity between valine and triple BCAA starvation, and it provides limited insight into the effects of combined depletion of two BCAAs.

Context of existing literature

Although ribosome profiling does not distinguish between actively-elongating and stalled ribosomes, sites with higher read coverage, and thereby higher inferred dwell time, can be used to infer ribosome stalling (Ingolia 2011). Various downstream effects of essential amino acid depletion have been documented, such as leucine deficiency being sensed by mTORC1 via leucyl-tRNA synthetase (Dittmar 2005, Han 2012), and shared transcriptional responses among many amino acid depletion conditions (Tang 2015). These authors have previously measured the translational effects of nutrient stress using ribosome profiling (e.g., Gobet 2020), as have others (Darnell 2018, Kochavi et al. 2024). The present work represents the first study (to our knowledge) combining BCAA depletions, representing an incremental and useful contribution to our understanding of translational responses to stress conditions.

Audience

This work is of interest to investigators studying the response of human cells in stress conditions, such as in human disease, as well as investigators studying the basic biology of eukaryotic translational control.

Reviewer expertise: mRNA decay and translation regulation in bacteria.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #2

Evidence, reproducibility and clarity

Summary and General Critique:

This study examines the consequences of starvation for the BRCAAs, either singly, for Leu & Ile, or for all three simultaneously in HeLa cells on overall translation rates, decoding rates at each codon, and on ribosome density, protein expression, and distribution of ribosome stalling events across the CDS for each expressed gene. The single amino acid starvation regimes specifically reduce the cognate intracellular amino acid pool and lead to deacylation of at least a subset of the cognate tRNAs in a manner dependent on continuing protein synthesis. They also induce the ISR equally and decrease bulk protein synthesis equally in a manner that appears to occur largely at the initiation level for -Leu and -Val, judging by the decreased polysome:monsome ratio, but at both the initiation and elongation levels for -Ile-a distinction that remains unexplained. Only -Leu appears to down-regulate mTORC1 and TOP mRNA translation. There is a significant down-regulation of protein levels for 50-200 genes, which tend to be unstable in nutrient-replete cells, only a fraction of which are associated with reduced ribosome occupancies (RPFs measured by Ribo-Seq) on the corresponding mRNAs in the manner expected for reduced initiation, suggesting that delayed elongation is responsible for reduced protein levels for the remaining fraction of genes. All three single starvations lead to increased decoding times for a subset of the cognate "hungry" codons: CUU for -Leu, AUU and AUC for -Ile, and all of the Val codons, in a manner that is said to correspond largely to the particular tRNA isoacceptors that become deacylated, although this correspondence was not explained explicitly and might not be as simple as claimed. All three single starvations also evoke skewing of RPFs towards the 5' ends of many CDSs in a manner correlated with an enrichment within the early regions of the CDSs for one or more of the cognate codons that showed increased decoding times for -Ile (AUC codon) and -Val (GUU, GUC, and GUG), but not for -Leu-of which the latter was not accounted for. These last findings suggest that, at least for -Val and -Ile, delays in decoding N-terminal cognate codons cause elongating ribosomes to build-up early in the CDS. They go on to employ a peak calling algorithm to identify stalling sites in an unbiased way within the CDS, which are greatest in number for -Val, and find that Val codons are enriched in the A-sites (slightly) and adjacent 5' nucleotides (to a greater extent) for -Val starvation; and similarly for Ile codons in -Ile conditions, but not for -Leu starvation-again for unknown reasons. It's unclear why their called stalling sites have various other non-hungry codons present in the A sites with the cognate hungry codons being enriched further upstream, given that stalling should occur with the "hungry" cognate codon in the A site. The proteins showing down-regulation are enriched for stalling sites only in the case of the -Val starvation in the manner expected if stalling is contributing to reduced translation of the corresponding mRNA. It's unclear why this enrichment apparently does not extend to -Ile starvation which shows comparable skewing of RPFs towards the 5'ends, and this fact diminishes the claim that pausing generally contributes to reduced translation for genes with abundant hungry codons.<br /> All of the same analyses were carried out for the Double -Ile/-Leu and Triple starvations and yield unexpected results, particularly for the triple starvation wherein decoding times are increased only at Val codons, skewing of RPFs towards the 5' ends of CDSs is correlated only with an enrichment for Val codons within the early regions of the CDSs, and stall sites are enriched only for Val codons at nearly upstream sites, all consistent with the finding that only Val tRNAs become deacylated in the Triple regime. To explain why only Val tRNA charging is reduced despite the observed effective starvation for all three amino acids, they note first that stalling at Val codons is skewed towards the 5'ends of CDS for both -Val and triple starvations more so than observed for Ile or -Leu starvation, which they attribute to a greater frequency of Val codons vs Ile codons in the 5' ends of CDSs. As such, charged Val tRNAs are said to be consumed in translating the 5'ends of CDSs and the resulting stalling prevents ribosomes from reaching downstream Ile and Leu codons at the same frequencies and thus prevents deacylation of the cognate Ile and Leu tRNAs. It's unclear whether this explanation is adequate to explain the complete lack of Ile or Leu tRNA deacylation observed even when amino acid recycling by the proteasome is inhibited-a treatment shown to exacerbate deacylation of cognate tRNAs in the single amino acid starvations and of Val tRNA in the triple starvation. As such, the statement in the Abstract "Notably, we could show that isoleucine starvation-specific stalling largely diminished under triple starvation, likely due to early elongation bottlenecks at valine codons" might be too strong and the word "possibly" would be preferred over "likely". It's also unclear why the proteins that are down-regulated in the triple starvation are not significantly enriched for stalling sites (Fig. 5B) given that the degree of skewing is comparable or greater than for -Val. This last point seems to undermine their conclusion in the Abstract that "that many proteins downregulated under BCAA deprivation harbor stalling sites, suggesting that compromised elongation contributes to decreased protein output."<br /> In the case of the double -Ile/-Leu starvation, a related phenomenon occurs wherein decoding rates are decreased for only the AUU Ile codon and only the AAU Ile tRNA becomes deacylated; although in this case increased RPFs in the 5' ends are not correlated with enrichment for Ile or Leu codons and, although not presented, apparently stall sites are not associated with the Ile codon in the double starvation. In addition, stalling sites are not enriched in the proteins down-regulated by the double starvation. Moreover, because Ile codons are not enriched in the 5'ends of CDS, it doesn't seem possible to explain the selective deacylation of the single Ile tRNA observed in the double starvation by the same "bottleneck" mechanism proposed to explain selective deacylation of only Val tRNAs during the triple starvation. This is another reason for questioning their "bottleneck" mechanism.

Specific comments (some of which were mentioned above):

• The authors have treated cells with CHX in the Ribo-Seq experiments, which has been shown to cause artifacts in determining the locations of ribosome stalling in vivo owing to continued elongation in the presence of CHX (https://doi.org/10.1371/journal.pgen.1005732 ). The authors should comment on whether this artifact could be influencing some of their findings, particular the results in Fig. 5C where the hungry codons are often present upstream of the A sites of called stalling sites in the manner expected if elongation continued slowly following stalling in the presence of CHX.
• p. 12: "These starvation-specific DT and ribosome density modulations were also evident at the individual transcript level, as exemplified by Col1a1, Col1a2, Aars, and Mki67 which showed persistent Val-codon-specific ribosome density increases but lost Ile-codon-specific increases under triple starvation (Supplementary Figure 3A-D). " This conclusion is hard to visualize for any but Val codons. It would help to annotate the relevant peaks of interest for -Ile starvation with arrows.
• To better make the point that codon-specific stalling under BCAA starvation appears to be not driven by codon usage, rather than the analysis in Fig. 1H, wouldn't it be better to examine the correlation between increases in DT under the single amino acid starvation conditions and the codon frequencies across all codons?
• p. 13, entire paragraph beginning with "Our RNA-seq and Ribo-seq revealed a general activation of stress response pathways across all starvations..." It is difficult to glean any important conclusions from this lengthy analysis, and the results do not appear to be connected to the overall topic of the study. If there are important conclusions here that relate to the major findings then these connections should be made or noted later in the Discussion. If not, perhaps the analysis should be largely relegated to the Supplemental material.
• p. 15: "Together, these findings highlight that BCAA starvation triggers a combination of effects on initiation and elongation, with varying dynamics by amino acid starvation." I take issue with this statement as it appears that translation is reduced primarily at the initiation step for all conditions except -Ile. As noted above, these data are never menitioned in the DISCUSSION as to why only -Ile would show a marked elongation component to the inhibition whereas -Val gives the greatest amount of ribosome stalling.
• I cannot decipher Fig. 4D and more detail is required to indicate the identify of each column of data.
• In Fig. 4E, one cannot determine what the P values actually are, which should be provided in the legend to confirm statistical significance.
• It's difficult to understand how the -Leu condition and the Double starvation can produce polarized RPFs (Fig. 4A) without evidence of stalling at the cognate hungry codons (Fig. 4E), despite showing later in Fig. 5A that the numbers of stall sites are comparable in those cases to that found for -Ile.
• Fig. 5B: the P values should be given for all five columns, and it should be explained here or in the Discussion why the authors conclude that stalling is an important determinant for reduced translation when a significant correlation seems to exist only for the -Val condition and not even for the Triple condition.
• p. 17: "Of note, in cases where valine or isoleucine codons were present just upstream (rather than at) the stalling position, we noted a strong bias for GAG (E), GAA (E), GAU (D), GAC (D), AAG (K), CAG (Q), GUG (V) and GGA (G) (Val starvation) and AAC (N), GAC (D), CUG (L), GAG (E), GCC (A), CAG (Q), GAA (E) and AAG (K) (Ile starvation) at the stalling site (Supplementary Figure 7B)." The authors fail to explain why these codons would be present in the A sites at stalling sites rather than the hungry codons themselves, especially since it is the decoding times of the hungry codons that are increased according to Fig. 1A-E. As suggested above, is this a CHX artifact?
• Fig. 5D: P values for the significance, or lack thereof, of the different overlaps should be provided.
• p. 17: "Nonetheless, when we examined entire transcripts rather than single positions, many transcripts that exhibited isoleucine-related stalling under Ile starvation also stalled under triple starvation, but at different sites along the CDS (Figure 5E). This finding is particularly intriguing, as it suggests that while Ile-starvation-specific stalling sites may shift under triple starvation, the overall tendency of these transcripts to stall remains." The authors never come back to account for this unexpected result.
• It seems very difficult to reconcile the results in Fig. 5F with those in Fig. 4A, where similar polarities in RPFs are observed for -Ile and -Val in Fig, 4A but dramatically different distributions of stalling sites in Fig. 5F. More discussion of these discrepancies is required.
• p. 18: " These isoacceptor-specific patterns correlate largely with the particular subsets of leucine and isoleucine codons that stalled (Figure 1A)." This correlation needs to be addressed for each codon-anticodon pair for all of the codons showing stalling in Fig. 1A.
• p. 19: "For instance, in our double starvation condition, unchanged tRNA charging levels (Figure 6E) may result from a pronounced downregulation of global translation initiation, likely driven by the activation of stress responses (Figure 2), subsequently lowering the demand for charged tRNAs as it has been observed previously for Leu starvation 39. This seems at odds with the comparable down-regulation of protein synthesis for the Double starvation and -Leu and -Ile single starvations shown in Fig. 3C. Also, in the current study, Leu starvation does lower charging of certain Leu tRNAs.

Significance

The results here are significant in showing that starvation for a single amino acid does not lead to deacylation of all isoacceptors for that amino acid and in revealing that starvation for one amino acid can prevent deacylation of tRNAs for other amino acids, as shown most dramatically for the selective deacylation of only Val tRNAs in the triple BRCAA starvation condition. For the various reasons indicated above, however, I'm not convinced that their "bottleneck" mechanism is adequate to explain this phenomenon, especially in the case of the selective deacylation of Ile vs Leu tRNA in the Double starvation regime. It's also significant that deacylation leads to ribosome build-up near the 5'ends of CDS, which seems to be associated with an enrichment for the hungry codons in the case of Val and Ile starvation, but inexplicably, not for Leu or the Double starvations. This last discrepancy makes it hard to understand how the -Leu and Double starvations produce RPF buildups near the 5 ends of CDSs. In addition, the claim in the Discussion that "our data also highlight the importance of the codon positional context within mRNAs, indicating that where a codon is located within the CDS can influence both the extent of ribosomal stalling and overall translation efficiency during nutrient stress" overstates the strength of evidence that the stalling events lead to substantial decreases in translational efficiencies for the affected mRNAs, as the stalling frequency and decreased protein output are significantly correlated only for the -Val starvation, and the data in Fig. 3 D-H suggest that the reductions in protein synthesis generally occur at the level of initiation, even for -Val starvation, with a contribution from slow elongation only for -Ile-which is in itself difficult to understand considering that stalling frequencies are highest in -Val. Thus, while many of the results are very intriguing and will be of considerable interest to the translation field, it is my opinion that a number of results have been overinterpreted and that important inconsistencies and complexities have been overlooked in concluding that a significant component of the translational inhibition arises from the increased decoding times at hungry codons during elongation and that the selective deacylation of Val tRNAs in the Triple starvation can be explained by the "bottleneck" mechanism. The complexities and limitations of the data and their intepretations should be discussed much more thoroughly in the Discussion, which currently is devoted mostly to other phenomena often of tangential importance to the current findings. A suitably revised manuscript would clearly state the limitations and caveats of the proposed mechanisms and consider other possible explanations as well.

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Referee #1

Evidence, reproducibility and clarity

This manuscript described the translational responses to single and combined BCAA shortages in mouse cell lines. Using Ribo-seq and RNA-seq analysis, the authors found selective ribosome pausing at codons that encode the depleted amino acids, where the pausing at valine codons was prominent at both a single and triple starvations whereas isoleucine codons showed pausing only under a single depletion. They analyzed the mechanisms of the unexpected selective pausing and proposed that the positional codon usage bias could shape the ribosome stalling and tRNA charging patterns across different amino acids. They also examined the stress responses and the changes in the protein expression levels under BCAA starvation.

The manuscript was well-written, and the findings are interesting, especially their model that positional codon usage bias could be a regulator of ribosome pausing and tRNA charging levels. Although different translational responses to distinct amino acid starvation have been widely documented, the positional codon usage bias is an interesting aspect. The manuscript's central message could have been made clearer. The authors may consider emphasizing this point more explicitly in the abstract. The rich multi-omics dataset in this work provides valuable resources for the translation field.

Major comments

1. The abstract may need to be revised since it is hard to immediately catch the authors' main point. If the authors regard this work as a resource paper, the current version is fine. But it could be better to point out the positional codon usages the authors found, which is a strong point of the current manuscript.
2. Page 18 "Beyond these tRNA dynamics, our data also highlight the importance of the codon positional context within mRNAs, indicating that where a codon is located within the CDS can influence both the extent of ribosomal stalling and overall translation efficiency during nutrient stress."<br /> This idea is interesting. To what extent the authors think this could be generalized? The authors may discuss whether they think their proposed model is specific to the different ribosome stalling patterns between valine and isoleucine codons or generalized to other codon combinations. For example, the positional codon usage bias will be different among different organisms, and are there any previous reports on ribosome behaviors that align with their model? Even if the authors think this model can be applied to BCAA starvation, would it be possible to explain the different isoleucine codon responses between single and double starvation? The authors may discuss why the ribosome stalling at isoleucine AUU and AUC codons was slightly attenuated under double starvation. And how about the different leucine codon responses among single, double, and triple starvations, although the pausing is not as strong as isoleucine and valine codons? Experimental validation using artificial reporters carrying biased sequences may also be considered.
3. Page 13 "Moreover, we noticed that DT changes extend beyond the ribosomal A-site, including the P-site, E-site, and even further positions (Supplementary Fig. 2A), consistent with other studies on single amino acid starvation 39 (Supplementary Fig. 2B-C)." Could the widespread DT changes be due to Ribo-DT pipeline they used or difficulties in offset determination? Indeed the authors showed that this feature was found in other datasets, but it seems that the datasets were processed and analyzed in the same way as their data. The original Ribo-DT paper (Gobet and Naef, 2022, Methods) also showed some widespread DT changes even from RNA-seq. Another analysis method like the codon subsequence abundant shift as a part of diricore analysis (Loayza-Puch et al., 2016, Nature) did not show that broad changed regions. The authors are encouraged to re-analyze the data sets using different methods.
4. Page 13 "Intriguingly, only two of the three isoleucine codons (AUU and AUC) showed increased DTs upon Ile starvation (p < 0.01), while just one leucine codon (CUU) exhibited a modest but significant DT increase (p < 0.01) under Leu starvation (Figure 1A-B, Supplementary Figure 2A)." How can the authors explain the different strengths of ribosome pausing at Ile codons under Ile and double starvation? The AUA codon did not show any pausing under either of the starvation conditions. Throughout the manuscript, the authors mainly describe the difference between amino acids but it is desirable to discuss the codon-level difference as well.
5. Page 13 "We examined the effects of single amino acid starvations (-Leu, -Ile and -Val), as well as combinations, including a double starvation of leucine and isoleucine (hereafter referred to as "double") and a starvation of leucine, isoleucine, and valine ("triple"), allowing us to identify potential non-additive effects." The different double starvations, isoleucine and valine, and leucine and valiene, will further support their hypothesis on the effects of the positional codon usage bias on ribosome pausing and tRNA charging patterns. Although this could be beyond the scope of the current manuscript, the authors are encouraged to provide a rationale for the chosen combination.

Minor comments

Page 16 "these results imply that BCAA deprivation lowers protein output through multiple pathways: a combination of reduced initiation, direct elongation blocks (stalling), and possibly an increased proteolysis" This conclusion is totally right but may be too general. Could the authors summarize BCAA-specific features of the events including reduced initiation, stalling, and proteolysis that all contribute to protein outputs? This is not well discussed in the latter sections including Discussion.

Significance

The manuscript was well-written, and the findings are interesting, especially their model that positional codon usage bias could be a regulator of ribosome pausing and tRNA charging levels. Although different translational responses to distinct amino acid starvation have been widely documented, the positional codon usage bias is an interesting aspect. The manuscript's central message could have been made clearer. The authors may consider emphasizing this point more explicitly in the abstract. The rich multi-omics dataset in this work provides valuable resources for the translation field.

1. 卷积操作: 卷积核上的每一个元素都是可学习的权重参数,网络训练的过程，就是不断更新这些权重，使它们能够提取出有用的特征。

2. 卷积求特征值: 使用卷积核上的权重参数与原始图上的像素值对应位置作计算求和得到特征值

3. 卷积核元素更新: 卷积核中的权重值也是通过计算损失,反向传播进行更新的.

np.multiply 是 逐元素相乘,不会做矩阵乘法（dot product）,只是对应位置相乘.得到的结果类似: np.multiply(input_patch, w_array): [[ 0, 0, 0], [ 0, 2, 3], [-1, 0, 2]],所以后面需要value.sum()+b_array

矩阵乘法是@或np.dot 矩阵乘法会执行“行 × 列”的规则，自动把相乘结果加和 numpy中dot既可以点积又可以矩阵相乘,但是在torch中,dot只能作点积,矩阵相乘用matmul,然后无论是numpy还是torch都推荐用@作矩阵相乘.

range(rows)生成一个 从 0 到 rows-1 的整数序列。 例:range(6) -> 0,1,2,3,4,5,6 list(range(rows))把 range 对象转成真正的 列表。 list(range(6)) → [0, 1, 2, 3, 4, 5]

Reviewer #2 (Public review):

In this study, Xiong et al. investigate whether rhythmic sampling - a process typically observed in the attended processing of visual stimuli - extends to task-irrelevant distractors. By using EEG with frequency tagging and multivariate pattern analysis (MVPA), they aimed to characterize the temporal dynamics of both target and distractor processing and examine whether these processes oscillate in time. The central hypothesis is that target and distractor processing occur rhythmically, and the phase relationship between these rhythms correlates with behavioral performance.

Major Strengths<br /> (1) The extension of rhythmic attentional sampling to include distractors is a novel and interesting question.<br /> (2) The decoding of emotional distractor content using MVPA from SSVEP signals is an elegant solution to the problem of assessing distractor engagement in the absence of direct behavioral measures.<br /> (3) The finding that relative phase (between 1 Hz target and distractor processes) predicts behavioral performance is compelling.

Major Weaknesses and Limitations<br /> (1) The central claim of 1 Hz rhythmic sampling is insufficiently validated. The windowing procedure (0.5s windows with 0.25s step) inherently restricts frequency resolution, potentially biasing toward low-frequency components like 1 Hz. Testing different window durations or providing controls would significantly strengthen this claim.<br /> (2) The study lacks a baseline or control condition without distractors. This makes it difficult to determine whether the distractor-related decoding signals or the 1 Hz effect reflect genuine distractor processing or more general task dynamics.<br /> (3) The pairwise decoding accuracies for distractor categories hover close to chance (~55%), raising concerns about robustness. While statistically above chance, the small effect sizes need careful interpretation, particularly when linked to behavior.<br /> (4) Neither target nor distractor signal strength (SSVEP amplitude) correlates with behavioral accuracy. The study instead relies heavily on relative phase, which-while interesting-may benefit from additional converging evidence.<br /> (5) Phase analysis is performed between different types of signals hindering their interpretability (time-resolved SSVEP amplitude and time-resolved decoding accuracy).

The authors largely achieved their stated goal of assessing rhythmic sampling of distractors. However, the conclusions drawn - particularly regarding the presence of 1 Hz rhythmicity - rest on analytical choices that should be scrutinized further. While the observed phase-performance relationship is interesting and potentially impactful, the lack of stronger and convergent evidence on the frequency component itself reduces confidence in the broader conclusions.

If validated, the findings will advance our understanding of attentional dynamics and competition in complex visual environments. Demonstrating that ignored distractors can be rhythmically sampled at similar frequencies to targets has implications for models of attention and cognitive control. However, the methodological limitations currently constrain the paper's impact.

Additional Considerations<br /> • The use of EEG-fMRI is mentioned but not leveraged. If BOLD data were collected, even exploratory fMRI analyses (e.g., distractor modulation in visual cortex) could provide valuable converging evidence.<br /> • In turn, removal of fMRI artifacts might introduce biases or alter the data. For instance, the authors might consider investigating potential fMRI artifact harmonics around 1 Hz to address concerns regarding induced spectral components.

Comments on revisions:

The authors have addressed my previous points, and the manuscript is substantially improved. The key methodological clarifications have been incorporated, and the interpretation of findings has been appropriately moderated. I have no further major concerns.

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Reply to the reviewers

Prior to the point-by-point response to the reviewer, we would like to sincerely thank all the peer reviewers for their overwhelmingly positive comments and helpful suggestions. The recommendations have undoubtedly improved our initial submission, and we have done our best to incorporate as many of the suggestions as possible.

Reviewer #1* (Evidence, reproducibility and clarity (Required)): *

*Jones et al. have submitted a manuscript detailing the role of Coenzyme A in the regulation of macrophage polarization. Overall, the manuscript is well designed, and the conclusions are well supported by the data. I find no major or minor deficiencies that need to be corrected. *

* Reviewer #1 (Significance (Required)): *

For decades the immunology community has boldly stated that mitochondrial metabolism not only provides the bioenergetics for cell expansion but also dictates cell fate. This has been especially true for fatty acid beta oxidation. Macrophage, T-cell and B-cell polarization have all been shown to require FAO for their polarization, but all based on one inhibitor. NONE of these observations hold up with more rigorous experimentation. The Divakaruni group has previously suggested that intracellular CoA homeostasis was the driver of macrophage differentiation as they could reverse the inhibitory effects by providing heroic levels of CoA extracellularly. Here, they have clarified the role of CoA. Intracellular CoA does not affect macrophage polarization/differentiation. This was done with cleaver manipulation of the CoA pools. Rather, extracellular CoA can act as a weak TLR4 ligand. This work nicely clarifies their previous work and further demonstrates a role for this metabolite as an endogenous activator of type 1 macrophages.

We are thrilled by the positive comments about our work, and we are grateful the reviewer found our submission to be clarifying for the field and significant in the larger context of immunometabolism research.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

*This is a fairly straightforward manuscript that indicated CoA acts as a "weak" TLR4 agonist and primes macrophages for alternative activation. Overall, the experiments are well done and clear enough. There are two major issues that need to be addressed: *

We thank the reviewer for their positive comments regarding the quality and clarity of our work.

1. *Previous work has shown the following pathway: LPS>IL10>STAT3>IL4Ra>>>increased responsiveness to IL4/IL13 and increased expression of M2 associated markers (please note, this pathway does not apply to Arg1, often erroneously associated with M2 macrophages - LPS induces Arg1 far more than IL4 and this is independent of the STAT6 pathway - Dichtl et al., Science Advances and El Kasmi et al. Nature Immunology, and others). This pathway was first described in Lang et al. 2002 J. Immunol. Subsequently, other groups showed IL6 (Jens Brüning) and OSM (Carl Richards) do the same thing, which is not surprising given that they are STAT3 activators. Thus, Il4ra is a STAT3 target gene; this also makes sense in the kinetic evolution of macrophages from inflammatory to tissue reparative (if they survive). In my view, the authors have most likely found the same pathway. In Jones, expression of the IL4Ra was not quantified. Thus, the pathway described above needs to be accounted for. It may not apply here but seems the easiest explanation of the data. *

This is an excellent and important experiment suggested by the reviewer, and we address this in our revised Supplemental Figure 5. To determine whether the effect of CoA can be explained simply by a STAT3-mediated effect on the IL-4 receptor, we treated cells with the well-characterized STAT3 inhibitor Napabucasin and measured whether CoA could enhance the macrophage IL-4 response. Two results are clear from the data:

• Treatment with Napabucasin reduced the expression of IL-4-linked cell surface markers and the IL-4 target gene Ccl8. This serves as an important control consistent with the Il4ra gene being a STAT3 target that increases IL-4 responsiveness.
• Despite STAT3 inhibition and a reduced IL-4 response, CoA provision still augmented the IL-4-induced expression of Ccl8 and the percentage of CD206+/CD301+ cells, indicating a STAT3-independent mechanism. The result aligns with our ATAC-Seq data in Figure 6 that shows broad changes in chromatin accessibility that cannot be completely explained by expression-level changes in the IL-4 receptor.

*Can the authors come up with a meaningful in vivo experiment to corroborate their data. Pantothenate-deficient mice have many phenotypes (not fully explored at all - PMID 31918006, for example) and pantothenate metabolism can be manipulated in different ways. Obviously, a complex in vivo experiment is not feasible here. But this should be discussed. What happens in human macrophages, where "polarization" is a completely different beast? *

We thank the reviewer for these thoughtful comments, and address the questions regarding in vivo proof-of-concept and polarization of human macrophages separately:

• Regarding the question of whether CoA can enhance the phenotype of IL-4-activated human macrophages, this is an excellent suggestion and we have added the data as Figure 1h. Indeed, Coenzyme A dramatically amplifies expression of the human IL-4 responsive genes CCL17, TGM2, and PDCD1LG2 (similarly to mouse macrophages). The result substantially expands the significance of our work by showing the phenotype is reproducible in both mouse and human macrophages – unlike many immunometabolic phenotypes – and we thank the reviewer again for suggesting this experiment.
• With respect to an in vivo experiment to corroborate our data, we entirely agree with the reviewer regarding both the importance, but also the difficulty in interpretation, of an experiment genetically manipulating CoA synthesis in vivo. As they have suggested, we raise these issues in the discussion on Lines 370-377 of the revised manuscript. Here, we note the following points:
• Wherever possible/appropriate (e.g. Figures 1g, 3f&g, 5g&h), we have sought to corroborate our in vitro findings with in vivo/ex vivo proofs-of-concept.
• Studying immune phenotypes in pantothenate-deficient mice would be an exciting experiment in principle, but difficult to interpret if conducted. As noted by the reviewer in the work from Drs. Rock and Jackowski, knockout of one of four isoforms of pantothenate kinase (PANK) shows mild phenotypes consistent with compensation across isoforms for CoA provision. Global double knockout of PANK1 and PANK2, however, is postnatally lethal. Regardless, a tissue-specific double knockout in myeloid cells is unlikely to show a phenotype given our results showing that manipulating intracellular CoA levels in BMDMs does not alter the IL-4 response (Figs. 2h-j).
• Given the established role of CoA in postnatal development, it would be difficult to attribute any immunologic phenotypes in genetically modified mice to direct effects of CoA as a metabolic DAMP as opposed to indirect effects from a chronically altered immune system.

Reviewer #2 (Significance (Required)): *This is a fairly straightforward manuscript that indicated CoA acts as a "weak" TLR4 agonist and primes macrophages for alternative activation. Overall, the experiments are well done and clear enough.

*

We reiterate our gratitude for the comments on the quality and clarity of our work.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

Summary: In this manuscript on enhancement of mIL-4 polarization by exogenous CoA, the authors follow up on their previous studies that had shown a correlation between Etomoxir-driven block in mIL-4 and a reduction of intracellular CoA levels. The results obtained (lack of enhancement of IL-4-induced changes in oxidative phosphorylation and glycolysis; lack of impact of pharmacological decrease/increase of intracellular CoA levels) led them to discard their initial hypothesis. Instead, the presence of a proinflammatory gene signature in macrophages treated with IL-4+CoA triggered experiments testing the involvement of TLR-Myd88 signaling and the identification of CoA as a weak agonist for TLR4 (which is consistent with a preprint manuscript posted in 2022 by others and showing induction of proinflammatory gene express in a TLR2/4-dependent manner).

• Significance: Overall, these results are novel and interesting, although the use of yeast-derived CoA preparations raises a question about the contribution of contaminants that is only partially controlled by data obtained with a synthetic CoA. Regarding a biological role for CoA in macrophage biology in vivo, the authors propose that CoA may act as a DAMP upon release from dying/dead cells and thereby modify transcriptional polarization of m(IL-4). I have several comments related to specific experimental conditions and interpretation that should be addressed. Most importantly, the key findings of the manuscript should be demonstrated using synthetic CoA as described in comment #5. *

We are heartened that the reviewer found our initial submission to be novel and interesting, and are grateful for their suggestions to reinforce our existing data with more studies comparing yeast-derived and synthetically-derived Coenzyme A. We have done our best to address each of the individual questions below:

Major comments:

1. *Increasing/decreasing intracellular CoA levels does not alter IL-4-induced CD206 expression (Fig. 2i/j. However, the impact of CoA addition to mIL-4 is stronger for Ccl8 and Mgl2 mRNA (Fig. 1a) than for the CD206+ cell fraction (Fig. 1d). Therefore, it would be better (higher sensitivity) to include expression of these genes as readout after CPCA/PZ-2891 treatment. *

This is a helpful suggestion, and we have now conducted gene expression studies to complement our flow cytometry and mass spectrometry studies while manipulating the intracellular CoA pool. In line with our previous work, neither CPCA (which decreases intracellular free CoA) or PZ-2891 (which increases intracellular free CoA) meaningfully alter expression of IL-4-linked genes including Ccl8 or Mgl2. In fact, the only (statistically insignificant) trend refutes the hypothesis, as gene expression with CPCA leads to marginally increased gene expression. These results are now included in Supplemental Figure S2f. We thank the reviewer for this helpful suggestion, as it has strengthened our conclusion that intracellular CoA levels do not adjust the macrophage IL-4 response.

• The CoA-induced proinflammatory gene expression in Fig. 3c is relatively weak (e.g. compared to LPS). The authors use CoA throughout the manuscript at a concentration of 1 mM, and we do not know how much of it is required to cause an effect at all. Therefore, dose-response curves for the stimulation of macrophages with titrated amounts of CoA should be provided. In addition, *

We thank the reviewer for bringing up this point so we could clarify and add to our existing data. We should note that Supplemental Figures 1b&c of our previous submission (and resubmitted manuscript) detail a concentration-response curve showing that at little as 62.5 mM CoA – the lowest concentration tested – was sufficient to enhance IL-4 cell surface marker expression.

However, it is an excellent suggestion as the reviewer notes, to conduct a similar concentration-response to determine if this lines up with CoA inducing a pro-inflammatory response. The full data set is presented in the answer to reviewer question 4 (comparing CoA purchased from Sigma vs. Avanti Polar Lipids), though we now show in Supplemental Figure S3 that 62.5 mM CoA is sufficient to elicit a pro-inflammatory response. Though it is indeed a weak effect as noted by the reviewer, our data suggest that the relatively mild stimulus is crucial for the effect. Given the results with the TLR3 agonist Poly I:C (Figure 5), which engages a Type 1 interferon response, strong TLR4 agonists that engage the TRIF/Type I interferon arm of the TLR4 response are likely to blunt or block the IL-4 response.

• Related question: we are informed that the concentration of CoA in the mitochondrial matrix is 5mM, whereas cytosol contains 100µM. For CoA to act as DAMP, I would like to know the concentration of it in supernatants of cell cultures (live vs. dying/dead cells) and from tissues. *

This is an important point brought up by the reviewer, and we agree that the implicit issue raised (i.e. “do the concentrations of CoA required to see an effect reconcile with a physiological role as a DAMP?”) should be more thoroughly addressed in the manuscript. Tissue concentrations of free CoA (in ng/mg tissue) are well established for mice and range from >100 nmol/g tissue (liver, heart, brown adipose tissue) to Nonetheless, the reviewer’s larger point is very well reasoned, and we address it in the following ways in the discussion on __Lines 378-391. __

• In light of the reviewer’s comment, we now mention specific instances in the discussion where CoA acting as a DAMP may reasonably play a physiological role (e.g. acetaminophen-induced acute liver injury or other forms of sterile liver injury given that DAMPs are known to be important factors and liver tissue contains relatively high concentrations of CoA).
• Although cytoplasmic concentrations of CoA may only be 50-100 mM, our work establishes a framework for how ubiquitous metabolic co-factors can activate pattern recognition receptors. Put another way, although CoA itself may not be a physiologically relevant DAMP, discovering this pathway could inform how other nucleotide or nucleoside analogs (e.g. adenine- or adenosine-containing molecules present at millimolar concentrations) exert their effects on innate immunity.
• Our newly obtained data with HMDMs (Figure 1h) shows that the CoA response in human macrophages – boosting IL-4-linked gene expression by 10-100X – may be much stronger than the 1.5-5X effect observed in mouse BMDMs. As such, it is exciting to speculate that CoA may have a more potent effect on the IL-4 response in humans relative to mice. We trust the reviewer understands the limitations of obtaining human macrophages that preclude conducting a thorough concentration-response analysis given the restrictions of a manuscript revision.

• It is very good that the authors validate the findings obtained using the yeast-derived CoA with the synthetic molecule. It is very conceivable that the 15% contaminating substances in the yeast CoA could be causing the observed changes in m(IL-4). The fact that synthetic CoA has higher activity in proinflammatory gene expression by BMM (Suppl. Fig. S3) is reassuring, however, it raises the question why this is the case. One possibility is that the concentrations of the different CoA preps cannot directly be compared. Therefore, dose response curves should also be provided for synthetic CoA. *

This is an astute observation by the reviewer and we thank them for reading our manuscript with such detailed attention to pick this up. We are reassured that the reviewer shares our interpretation that the effect of CoA is not due to a contaminating TLR4 agonist in the yeast-derived preparation (from Sigma-Aldrich; ~85% pure) given a negative Limulus Test (Supplemental Figure S4b). Moreover, the synthetically-derived preparation (from Avanti Polar Lipids; ~99% pure) yields a stronger TLR4 response.

An exploration of the follow-on question regarding why the effect is greater than 15% is presented below. These experiments have been added to Supplemental Figure S4c&d. The summary of our data suggests the individual concentrations indeed cannot be compared – matched concentrations of synthetic Avanti CoA have greater than a 15% effect than yeast-derived Sigma CoA. There are likely multiple factors that could explain this, some of which are listed below.

• The physiological effect of a TLR agonist need not be linear with its concentration, as demonstrated by the sigmoidal calibration curves for the TLR-expressing HEK-blue cells (Figures 4b, S4a). This likely does not explain the dramatic difference between the two CoA preparations but is worth noting.
• While we have determined that the 15% contaminating substances in the yeast-derived CoA are not causing the observed changes in the IL-4 response, it is formally possible that there are contaminating substances blunting the pro-inflammatory response and therefore limiting the effect of CoA purchased from Sigma-Aldrich relative to that from Avanti Polar Lipids. Importantly, however, our data in response to Reviewer Question #5 show there is no difference in amplifying the IL-4 response between the yeast- and synthetically-derived CoA.

• The difference in activity of yeast and synth. CoA could also be caused by the additional biologically active molecules in the yeast CoA. Therefore, it is important to show that the key findings in the paper (enhancement of m(IL-4) associated gene expression and CD206+ upregulation in vitro and in vivo) are also induced by synth. CoA. This is even more important in the context of the Myd88-independence of CD206+ upregulation in BMM treated with CoA (Suppl. Fig. S4). The experiment should be repeated with synth. CoA. If the enhancement of CD206+ cells induced by CoA is indeed unchanged in Myd88 KO BMM, then the title of the manuscript "CoA enhances alternative macrophage activation via Myd88" would not be supported by the data and needed to be changed. Activation of the TLR4 reporter cell line should also be tested using the synth. CoA molecule.*

We are grateful for this suggestion by the reviewer to further cement the idea that our observation of CoA enhancing the macrophage IL-4 response was not due to a contaminant in the Sigma-Aldrich CoA preparation. The reviewer makes a few points in this question which we address individually here.

• The suggestion to confirm that the CoA-induced enhancement of M(IL-4) is not due to a contaminating substance in the Sigma-Aldrich CoA is excellent and necessary. Here we show that synthetically derived CoA (99% pure, purchased from Avanti Polar Lipids) quantitatively reproduces the effect from yeast-derived CoA from Sigma-Aldrich in Supplemental Figure S4e. The response is noteworthy because synthetic CoA has profoundly stronger pro-inflammatory response than yeast-derived CoA, yet both have a similar effect on augmenting M(IL-4). This suggests that any appropriate pro-inflammatory response – irrespective of the relative strength or weakness – is sufficient to maximize the effect. This can also be observed with the range of MyD88-linked TLR agonists used in Figures 5 and S6a.
• Similarly, we also conducted experiments to show that the effect of synthetic CoA on M(IL-4) is independent of MyD88 similarly to yeast-derived CoA. These data are present in Supplemental Figure S6b&c. Here again, we should note that the effect of synthetic CoA is quantitatively similar to the effect of yeast CoA and Imiquimod (Supplemental Figure S6a).
• Activation of the TLR4 reporter cell line is available in Supplemental Figure S4c.
• Regarding the title of the manuscript, we acknowledge that we struggled a bit with how to frame our findings. Importantly, our findings support a model where (i) CoA provision enhances the IL-4 response not via metabolic changes but rather by acting as a mild pro-inflammatory stimulus, and (ii) MyD88 signaling augments the IL-4 response. We should also note that our findings simply show that CoA does not exclusively enhance the IL-4 response via MyD88 signaling, and there may be other redundant pathways (similarly to MyD88 agonist imiquimod but unlike the MyD88 agonists Pam3-CSK4 and low concentrations of LPS). We are open to working journal editors to strike the right balance of scientific accuracy and representation of the work when deciding on a final title.

• The results from the tumor model in Fig. 5 are presented to show a stronger tumor-promoting effect of m(IL-4) stimulated with Pam3. However, the variability of the data is high and 2 out of 6 mice in the +Pam3 group appear to actually have a lower tumor weight than the control mice. Therefore, these data are quite superficial and preliminary, and would benefit from a replicate experiment. Furthermore, for the evaluation of CoA as a biologically relevant DAMP, it would be important to know whether CoA-treated m(IL-4) show the same tumor-promoting effect in vivo as Pam3. *

We thank the reviewer for their comment, and agree that our in vivo work is indeed preliminary. Our goal with this report was to focus on the initial discovery of this molecular pathway and its first, broad characterization using a range of techniques (e.g. in vivo outcomes, ATAC-Seq, etc.), many of which can spur more detailed follow-up studies for future papers. As detailed in the manuscript discussion (Lines 415-419), future work beyond our initial discovery is warranted to thoroughly explore the physiological outcomes of CoA as a metabolic DAMP in relevant model systems such as acute liver injury. As an initial proof-of-concept to show that MyD88 signaling can enhance alternative activation, however, we believe our two discrete experiments (sterile inflammation and tumor formation) are sufficient to indicate the phenotype is likely relevant in animal models. In vivo syngeneic tumor models display natural variability in tumor size due to differences in implantation efficiency, host immune responses, and tumor-intrinsic growth kinetics. Nonetheless, our statistical analysis demonstrates that, with high confidence, that the observed differences are reproducible and not attributable to random variation.

Minor comments:

1. • Fig. 1b: where the gates for CD206/CD301 set based on isotype control stainings? *

We thank the reviewer for pointing out this oversight in our methods. The gates were indeed set on isotype control stains, and this is now mentioned in Lines 519-521 of the revised manuscript.

The formatting not cohesive m(IL-4) vs. M(IL-4)

Again, this is an embarrassing oversight on our part and we have done our very best to copy edit the piece and remove any inconsistencies and errors.

*Methods: primer sequences are not shown. They should be provided. *

We thank the reviewer for pointing this out, and now include all primer sequences used in Supplemental Table 1 of the revised manuscript.

Description of flowcytometry (L/D staining after surface? No washing steps after addition of L/D staining)

We thank the reviewer for pointing out another oversight in our methods, and have provided a more detailed description of the flow cytometric analysis in Lines 509-521 of the revised manuscript.

Statistics: the methods section states that variability is indicated by SD, but the Figure legends always mention SEM. Please correct.

We are grateful for the reviewer’s helpful attention to detail, and have corrected the methods to line up with the figure legends.

*A multitude of typos and editorial inconsistencies (e.g. spelling of m(IL-4), punctation and capitalization) should be corrected/streamlined. *

We are grateful for the reviewer’s helpful attention to detail, and have done our best to copy edit the manuscript prior to resubmission.

Reviewer #3 (Significance (Required)):

strengths: I like that the authors follow up their previous work on Etomoxir and CoA, now finding again an unexpected twist in how the effect on m(IL-4) is brought about. This makes the story more complicated, but is important to get to a more precise and realistic understanding of metabolic and transcriptomic regulation and how they are interconnected (or not). In addition, the use of a relatively broad set of methods including ATACseq and mass spectrometry is a strength.

weakness: the use of the not very pure yeast derived CoA prep, which is controlled for induction of proinflammatory cytokines by one experiment with synth. CoA. This validation needs to be expanded (see comments above) to substantiate the main message of the manuscript.

The scope of the manuscript is quite focussed on the mechanism of CoA enhanced m(IL-4). The finding that CoA appears not to act by changing intracellular macrophage metabolism but instead after its release by activation TLR4 widens the scope and suggests a new function for CoA as DAMP. This aspect would need to be further substantiated to be convincing.

Audience: scientists working at the intersection between metabolism and innate immunity will be interested in the results.

We thank the reviewer for their kind comments regarding the precision, credibility, and breadth of our manuscript. We hope they find our revised manuscript an improvement over our previous submission regarding both the new experiments and modified text. The comments have undoubtedly improved our manuscript and we are grateful to the reviewer for the considerable effort they put into reading our submission.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #3

Evidence, reproducibility and clarity

Summary:

In this manuscript on enhancement of mIL-4 polarization by exogenous CoA, the authors follow up on their previous studies that had shown a correlation between Etomoxir-driven block in mIL-4 and a reduction of intracellular CoA levels. The results obtained (lack of enhancement of IL-4-induced changes in oxidative phosphorylation and glycolysis; lack of impact of pharmacological decrease/increase of intracellular CoA levels) led them to discard their initial hypothesis. Instead, the presence of a proinflammatory gene signature in macrophages treated with IL-4+CoA triggered experiments testing the involvement of TLR-Myd88 signaling and the identification of CoA as a weak agonist for TLR4 (which is consistent with a preprint manuscript posted in 2022 by others and showing induction of proinflammatory gene express in a TLR2/4-dependent manner).

Significance:

Overall, these results are novel and interesting, although the use of yeast-derived CoA preparations raises a question about the contribution of contaminants that is only partially controlled by data obtained with a synthetic CoA. Regarding a biological role for CoA in macrophage biology in vivo, the authors propose that CoA may act as a DAMP upon release from dying/dead cells and thereby modify transcriptional polarization of m(IL-4). I have several comments related to specific experimental conditions and interpretation that should be addressed. Most importantly, the key findings of the manuscript should be demonstrated using synthetic CoA as described in comment #5.

Major comments:

1. Increasing/decreasing intracellular CoA levels does not alter IL-4-induced CD206 expression (Fig. 2i/j. However, the impact of CoA addition to mIL-4 is stronger for Ccl8 and Mgl2 mRNA (Fig. 1a) than for the CD206+ cell fraction (Fig. 1d). Therefore, it would be better (higher sensitivity) to include expression of these genes as readout after CPCA/PZ-2891 treatment.
2. The CoA-induced proinflammatory gene expression in Fig. 3c is relatively weak (e.g. compared to LPS). The authors use CoA throughout the manuscript at a concentration of 1 mM, and we do not know how much of it is required to cause an effect at all. Therefore, dose-response curves for the stimulation of macrophages with titrated amounts of CoA should be provided. In addition,
3. Related question: we are informed that the concentration of CoA in the mitochondrial matrix is 5mM, whereas cytosol contains 100µM. For CoA to act as DAMP, I would like to know the concentration of it in supernatants of cell cultures (live vs. dying/dead cells) and from tissues.
4. It is very good that the authors validate the findings obtained using the yeast-derived CoA with the synthetic molecule. It is very conceivable that the 15% contaminating substances in the yeast CoA could be causing the observed changes in m(IL-4). The fact that synthetic CoA has higher activity in proinflammatory gene expression by BMM (Suppl. Fig. S3) is reassuring, however, it raises the question why this is the case. One possibility is that the concentrations of the different CoA preps cannot directly be compared. Therefore, dose response curves should also be provided for synthetic CoA.
5. The difference in activity of yeast and synth. CoA could also be caused by the additional biologically active molecules in the yeast CoA. Therefore, it is important to show that the key findings in the paper (enhancement of m(IL-4) associated gene expression and CD206+ upregulation in vitro and in vivo) are also induced by synth. CoA. This is even more important in the context of the Myd88-independence of CD206+ upregulation in BMM treated with CoA (Suppl. Fig. S4). The experiment should be repeated with synth. CoA. If the enhancement of CD206+ cells induced by CoA is indeed unchanged in Myd88 KO BMM, then the title of the manuscript "CoA enhances alternative macrophage activation via Myd88" would not be supported by the data and needed to be changed. Activation of the TLR4 reporter cell line should also be tested using the synth. CoA molecule.
6. The results from the tumor model in Fig. 5 are presented to show a stronger tumor-promoting effect of m(IL-4) stimulated with Pam3. However, the variability of the data is high and 2 out of 6 mice in the +Pam3 group appear to actually have a lower tumor weight than the control mice. Therefore, these data are quite superficial and preliminary, and would benefit from a replicate experiment. Furthermore, for the evaluation of CoA as a biologically relevant DAMP, it would be important to know whether CoA-treated m(IL-4) show the same tumor-promoting effect in vivo as Pam3.

Minor comments:

1. Fig. 1b: where the gates for CD206/CD301 set based on isotype control stainings?
2. The formatting not cohesive m(IL-4) vs. M(IL-4)
3. Methods: primer sequences are not shown. They should be provided.
4. Description of flowcytometry (L/D staining after surface? No washing steps after addition of L/D staining)
5. Statistics: the methods section states that variability is indicated by SD, but the Figure legends always mention SEM. Please correct.
6. A multitude of typos and editorial inconsistencies (e.g. spelling of m(IL-4), punctation and capitalization) should be corrected/streamlined.

Significance

Strengths: I like that the authors follow up their previous work on Etomoxir and CoA, now finding again an unexpected twist in how the effect on m(IL-4) is brought about. This makes the story more complicated, but is important to get to a more precise and realistic understanding of metabolic and transcriptomic regulation and how they are interconnected (or not). In addition, the use of a relatively broad set of methods including ATACseq and mass spectrometry is a strength.

Weakness: the use of the not very pure yeast derived CoA prep, which is controlled for induction of proinflammatory cytokines by one experiment with synth. CoA. This validation needs to be expanded (see comments above) to substantiate the main message of the manuscript.

The scope of the manuscript is quite focussed on the mechanism of CoA enhanced m(IL-4). The finding that CoA appears not to act by changing intracellular macrophage metabolism but instead after its release by activation TLR4 widens the scope and suggests a new function for CoA as DAMP. This aspect would need to be further substantiated to be convincing.

Audience: scientists working at the intersection between metabolism and innate immunity will be interested in the results.

Reviewer #3 (Public review):

Summary:

It has been a long time since I enjoyed reviewing a paper as much as this one. In it, the authors generate an unprecedented view of the aboral organ of a 5-day-old ctenophore. They proceed to derive numerous insights by reconstructing the populations and connections of cell types, with up to 150 connections from the main Q1-4 neuron.

Strengths:

The strengths of the analysis are the sophisticated imaging methods used, the labor-intensive reconstruction of individual neurons and organelles, and especially the mapping of synapses. The synaptic connections to and from the main coordinating neurons allow the authors to create a polarized network diagram for these components of the aboral organ. These connections give insight into the potential functions of the major neurons. This also gives some unexpected results, particularly the lack of connections from the balancer system to the coordinating system.

Weaknesses:

There were no significant weaknesses in the paper - only a slate of interesting unanswered questions to motivate future studies.

Reviewer #1 (Public review):

Summary:

The manuscript "Realistic coupling enables flexible macroscopic traveling waves in the mouse cortex" by Sun, Forger, and colleagues presents a novel computational framework for studying macroscopic traveling waves in the mouse cortex by integrating realistic brain connectivity data with large-scale neural simulations.

The key contributions include:<br /> (1) developing an algorithm that combines spatial transcriptomic data (providing detailed neuron positions and molecular properties) with voxelized connectivity data from the Allen Brain Atlas to construct neuron-to-neuron connections across ~300,000 cortical neurons;<br /> (2) building a GPU-accelerated simulation platform capable of modeling this large-scale network with both excitatory and inhibitory Hodgkin-Huxley neurons;<br /> (3) extending phase-based analysis methods from 2D to 3D to quantify traveling wave activity in the realistic brain geometry; and<br /> (4) demonstrating that realistic Allen connectivity generates significantly higher levels of macroscopic traveling waves compared to simplified local or uniform connectivity patterns.

The study reveals that wave activity depends non-monotonically on coupling strength and that slow oscillations (0.5-4 Hz) are particularly conducive to large-scale wave propagation, providing new insights into how anatomical connectivity enables flexible spatiotemporal dynamics across the cortex.

Strengths:

The authors leverage two existing dense datasets of spatial transcriptomic data and connection strength between pairwise voxels in the mouse cortex in a novel way, allowing for the computational model to capture molecular and functional properties of neurons as determined by their neurotransmitter profiles, rather than making arbitrary assignments of excitatory/inhibitory roles. Additionally, the author's expansion of 2D phase dynamics to 3D phase gradient analysis methods is important and can be widely applied to calcium imaging, LFP recordings, and likely other electrophysiological recordings.

Weaknesses:

Despite these important computational advancements, a few aspects of this model, particularly the inability to validate the model with experimental neural data, diminish my enthusiasm for this paper:

(1) The model's Allen connectivity approach overlooks critical aspects of real cortical dynamics. Most importantly, it excludes subcortical structures, especially the thalamus, which drives cortical traveling waves through thalamocortical interactions. The authors' method of electrically stimulating all layer 4 neurons simultaneously to initiate waves is artificially crude and bears little resemblance to natural wave generation mechanisms.

(2) The model handles voxel-to-voxel connections crudely when neurons have mixed excitatory/inhibitory properties and varying synaptic strengths. Real connectivity differs dramatically between neuron types (pyramidal cells vs. interneurons, across cortical layers), but the model only distinguishes excitatory and inhibitory neurons. Additionally, uniform synaptic weights ignore natural variations in connection strength based on neuron type, distance, and functional role. Integrating the updated thalamocortical dataset mentioned by the authors, even at regional resolution, would substantially improve the model.

(3) While the authors bridge microscopic (single neuron) and mesoscopic (regional connectivity) data to study macroscopic (whole-cortex) waves, they don't integrate the distinct mechanisms operating at each scale. The framework demonstrates that realistic connectivity enables macroscopic waves but fails to connect how wave dynamics emerge and interact across spatial scales systematically.

(4) Claims that Allen connectivity produces higher phase gradient directionality (PGD) than local connectivity appear limited to delta oscillations at very specific coupling strengths and applied currents. Few parameter combinations show significantly higher PGD for Allen connectivity, and these are generally low PGD values overall.

(5) Broadly, it's unclear how this computational framework can study memory, learning, sleep, sensory processing, or disease states, given the disconnect between simulated intracellular voltages and the local field potentials or other electrophysiological measurements typically used to study cortical traveling waves. While computationally impressive, the practical research applications remain vague.

(6) The paper needs a clearer explanation for why medium coupling (100%) eliminates waves in Allen connectivity (Figure 6) while stronger coupling (150%) restores them.

(7) Does using a single connectivity parameter (ρ = 300) across all regions miss important regional differences in cortical connectivity density?

Reviewer #2 (Public review):

Summary:

This work presents a spiking network model of traveling waves at the whole-brain scale in the mouse neocortex. The authors use data from the Allen Institute to reconstruct connectivity between different neocortical sites. They then quantify macroscopic traveling waves following stimulation of all layer 4 neurons in the neocortex.

Strengths:

Overall, the results are interesting and shed new light on the dynamic organization of activity across the neocortex of the mouse. The paper uses realistic neuron models specifically fit to intracellular recordings, demonstrating that traveling waves occur in the mouse neocortex with both realistic connectivity and realistic single-neuron dynamics. The paper is also well-written in general. For these reasons, the authors have generally achieved their aims in this work.

Weaknesses:

(1) Description of Algorithm 1:<br /> While the Methods section clearly explains the density parameter \rho, the statement on line 358 concerning the "ideal" average number of connections is a little unclear. The authors should explicitly clarify that \rho is a free parameter that can be adjusted to balance computational feasibility (for a given set of computational resources) and biological fidelity.

(2) Lines 102-103:<br /> The \rho parameter used here results in approximately 300 connections per neuron on average. The authors should state clearly that the number of connections per cell is the key determinant of computational feasibility (cf. Morrison et al., Neural Computation, 2005). The authors should also review neuronal density and synaptic connectivity in the mouse neocortex and clearly reference density and connectivity in their model to the biological scales found in the mouse.

(3) Line 131:<br /> From the plots in Figure 2, it is not clear that the stimulus response is necessarily a rhythmic oscillation, in the sense of a single narrowband frequency.

(4) Line 217:<br /> The authors should clarify how these findings relate to the results from Mohajerani et al. (Nature Neuroscience, 2013) or differ from them.

(5) Line 230:<br /> Because higher temporal frequency activity also tends to be more spatially localized, a correlation between PGD and temporal frequency could be an inherent consequence of this relationship, rather than a meaningful result.

(6) Line 247-248:<br /> It is not clear that the algorithm for generating connections between neurons presented here really relates to those for community detection. For example, in the case of the Allen Institute data, the communities are essentially in the data already.

(7) Line 284-285:<br /> The relationship between conduction delay is more direct than this sentence suggests. Conduction delay is fundamentally determined by the time required for action potentials to propagate along axons, making it intrinsically linked to anatomical distance.

(8) Line 287-288:<br /> The authors suggest at this point that they do not have enough information to estimate time delays due to axonal conduction along white matter fibers. However, experimental data from white matter connections typically includes information about fiber length, which does enable estimating conduction delays. These estimations have been previously implemented for Allen Institute connectome data in the mouse (Choi and Mihalas, PLoS Comput Biology, 2019) and human connectome data (Budzinski et al., Physical Review Research, 2023).

(9) Lines 294-295:<br /> Several methods do exist for detecting and characterizing wave dynamics in three-dimensional data (Budzinski et al., Physical Review Research, 2023).

Reviewer #1 (Public review):

Summary: This study investigated how visuospatial attention influences the way people build simplified mental representations to support planning and decision-making. Using computational modeling and virtual maze navigation, the authors examined whether spatial proximity and the spatial arrangement of obstacles determine which elements are included in participants' internal models of a task. The study developed and tested an extension of the value-guided construal (VGC) model that incorporates features of spatial attention for selecting simpler task mental representation.

Strengths:

(1) Original Perspective: The study introduces an explicit attentional component to established models of planning, offering an approach that bridges perception, attention, and decision-making.

(2) Methodological Approach: The combination of computational modeling, behavioral data, and eye-tracking provides converging measures to assess the relationship between attention and planning representations.

(3) Cross-validated data: The study relies on the analysis of three separate datasets, two already published and an additional novel one. This allows for cross-validation of the findings and enhances the robustness of the evidence.

(4) Focus on Individual Differences: Reports of how individual variability in attentional "spillover" correlates with the sparsity of task representations and spatial proximity add depth to the analysis.

Weaknesses:

(1) Clarity of the VGC model and behavioral task: The exposition of the VGC model lacks sufficient detail for non-expert readers. It is not clear how this model infers which maze obstacles are relevant or irrelevant for planning, nor how the maze tasks specifically operationalize "planning" versus other cognitive processes.

The method for classifying obstacles as relevant or irrelevant to the task and connecting metacognitive awareness (i.e., participants' reports of noticing obstacles) to attentional capture is not well justified. The rationale for why awareness serves as a valid attention proxy, as opposed to behavioral or neurophysiological markers, should be clearer.

(2) Attention framework: The account of attention is largely limited to the "spotlight" model. When solving a maze, participants trace the correct trail, following it mentally with their overt or covert attention. In this perspective, relevant concepts are also rooted in attention literature pertaining to object-based attention using tasks like curve tracing (e.g., Pooresmaeili & Roelfsema, 2014) and to mental maze solving (e.g., Wong & Scholl, 2024), which may be highly relevant and add nuance to the current work. This view of attention may be more pertinent to the task than models of simultaneously tracking multiple objects cited here. Prior work (notably from the Roelfsema group) indicates that attentional engagement in curve-tracing tasks may be a continuous, bottom-up process that progressively spreads along a trajectory, in time and space, rather than a "spotlight" that simply travels along the path. The spread of attention depends on the spatial proximity to distractors - a point that could also be pertinent to the findings here.

Moreover, the tracing of a "solution" trail in a maze may be spontaneous and not only a top-down voluntary operation (Wong & Scholl, 2024), a finding that requires a more careful framing of the link to conscious perception discussed in the manuscript.

Conceptualizing attention as a spatial spotlight may therefore oversimplify its role in navigation and planning. Perhaps the observed attentional modulation reflects a perceptual stage of building the trail in the maze rather than a filter for a later representation for more efficient decision making and planning. A fuller discussion of whether the current model and data can distinguish between these frameworks would benefit readers.

(3) Lateralization of attention: The analysis considers whether relevant information is distributed bilaterally or unilaterally across the visual display, but does not sufficiently address evidence for attentional asymmetries across the left and right visual fields due to hemispheric specialization (e.g., Bartolomeo & Seidel Malkinson, 2019). Whether effects differ for left versus right hemifield arrangements is not made explicit in the presented findings.

(4) Individual differences: Individual differences in attentional modulation are a strength of the work, but similar analyses exploring individual variation in lateralization effects could provide further insight, and the lack of such analyses may mask important effects.

(5) Distinction between overt and covert attention: The current report at times equates eye movement patterns with the locus of attention. However, attention can be covertly shifted without corresponding gaze changes (see, for example, Pooresmaeili & Roelfsema, 2014).

The implications for interpreting the relationship between eye movement, memory, and attention in this setting are not fully addressed. The potential dynamics of attention along a maze trajectory and their impact on lateralization analysis would benefit from further clarification.

Appraisal of Aims and Results:

The study sets out to determine how spatial attention shapes the construction of task representations in planning contexts. The authors provide evidence that spatial proximity and arrangement influence which environmental features are incorporated into internal models used for navigation, and that accounting for these effects improves model predictions. There is clear documentation of individual variation, with some participants showing greater attentional spillover and more sparse awareness profiles.

However, some conceptual and methodological aspects would be clearer with greater engagement with the broader literature on attention dynamics, a more explicit justification of operational choices, and more targeted lateralization analyses.

Reviewer #2 (Public review):

Summary:

Castanheira et al. investigate the role of spatial attention for planning during three maze navigation experiments (one new experiment and two existing datasets). Effective planning in complex situations requires the construction of simplified representations of the task at hand. The authors find that these mental representations (as assessed by conscious awareness) of a given stimulus are influenced by (spatially) surrounding stimuli. Individual participants varied in the degree to which attention influenced their task representations, and this attentional effect correlated with the sparsity of representations (as measured by the range of awareness reports across all stimuli). Spatially grouping task-relevant information on either the left or right side of the maze led to mental representations more similar to optimal representations predicted by the value-guided construal (VGC) model - a normative model describing a theoretical approach to simplifying complex task information. Finally, the authors propose an update to this model, incorporating an attentional spotlight component; the revised descriptive model predicts empirical task representations better than the original (normative) VGC model.

Strengths:

The novelty of this study lies in the proposal and investigation of a cognitive mechanism through which a normative model like value-guided construal can enable human planning. After proposing attention as this mechanism, the authors make concrete hypotheses about mismatches between the VGC predictions and real human behavior, which are experimentally validated. Thus, not only does this study describe a possible mechanism for simplification of task information for planning, but the authors also propose a descriptive model, revising VGC to incorporate this attentional component.

A strength of this paper is the variety of investigative approaches: analysis of existing data, novel experiment, and a computational approach to predict experimental findings from a theoretical model. Analyzing pre-existing datasets increases the size of the participant cohort and strengthens the authors' conclusions. Meanwhile, comparing the predictions of the existing normative model and the authors' own refined model is a clever approach to substantiate their claims. In addition, the authors describe several crucial controls, which are key to the interpretability of their results. In particular, the eye tracking results were critical.

In summary, this paper constitutes an important step toward a more complete understanding of the human ability to plan.

Weaknesses:

(1) There is a critical conceptual gap in the study and its interpretation, mainly due to the reliance on a self-report metric of awareness (rather than an objective measure of behavioral performance).

a. Awareness is tested by a 9-point self-report scale. It is currently unclear why awareness of task-irrelevant obstacles in this task would necessarily compromise optimal planning. There is no indication of whether self-reported awareness affects performance (e.g., navigation path distance, time to complete the maze, number of errors). Such behavioral evidence of planning would be more compelling.

b. Relatedly, it would have been more convincing to have an objective measure of awareness, for instance, how the presence or absence of a "task-irrelevant" obstacle affects performance (e.g., change navigation path distance or time to complete the maze), or whether participants can accurately recall the location of obstacles.

c. Consequently, I'm not sure that we can conclude that the spatial context does impact participants' ability to plan spatial navigation or to "incorporate task-relevant information into their construal". We know that the spatial context affects subjective (self-reported) awareness, but the authors do not present evidence that spatial context affects behavioral performance.

d. Another concern that may complicate interpretation is the following: Figure 3c shows improved VGC model predictions (steeper slope) for mazes with greater lateralization. However, there are notable outliers in these plots, where a high lateralization index does not correspond to good model performance. There is currently no discussion/explanation of these cases.

(2) I noticed an issue with clarity regarding task-relevance. It is currently not fully clear which obstacles are "task irrelevant". Also, the term is used inconsistently, sometimes conflating with "awareness". For example, in the "Attentional spotlight model of task representations" section, the authors state that "task-relevant information becomes less relevant when surrounded by task-irrelevant information". But they really mean that participants become less aware of those task-relevant obstacles. I assume task-relevance is an objective characteristic related to maze organization, not to a participant's construal. Indeed, the following paragraph provides evidence of model predictions of awareness.

(3) The behavioral paradigm has some distinct disadvantages, and the validity of the task is not backed up by behavioral data.

a. I understand the need for central fixation, but it also makes the task less naturalistic.

b. The task with its top-down grid view does not seem to mimic real human navigation. Though this grid may be similar to mental maps we form for navigation, the sensory stimuli corresponding to possible paths and to spatial context during real-life navigation are very different.

c. Behavioral performance is not reported, so it is unknown whether participants are able to properly complete the task. The task seems pretty difficult to navigate, especially when the obstacles disappear, and in combination with the central fixation.

d. There is no discussion of whether/how this navigation task generalizes to other forms of planning.

Reviewer #3 (Public review):

Summary:

The authors build on a recent computational model of planning, the "value-guided construal" framework by Ho et al. (2022), which proposes that people plan by constructing simple models of a task, such as by attending to a subset of obstacles in a maze. They analyze both published experimental data and new experimental data from a task in which participants report attention to objects in mazes. The authors find that attention to objects is affected by spatial proximity to other objects (i.e., attentional overspill) as well as whether relevant objects are lateralized to the same hemifield. To account for these results, the authors propose a "spotlight-VGC" model, in which, after calculating attention scores based on the original VGC model, attention to objects is enhanced based on distance. They find that this model better explains participant responses when objects are lateralized to different hemifields. These results demonstrate complex interactions between filtering of task-relevant information and more classical signatures of attentional selection.

Strengths:

(1) The paper builds on existing modeling work in a novel manner and integrates classic results on attention into the computational framework.

(2) The authors report new and extensive analyses of existing data that shed light on additional sources of systematic variability in responses related to attentional spillover effects

(3) They collect new data using new stimuli in the original paradigm that directly test predictions related to the lateralization of task-relevant information, including eye tracking data that allows them to control for possible confounds.

(4) The extended model (spotlight-VGC) provides a formal account of these new results.

Weaknesses:

(1) The spotlight-VGC model has a free parameter - the "width" of the attentional spotlight. This seems to have been fixed to be 3 squares. It would be good if the authors could describe a more principled procedure for selecting the width so that others can use the model in other contexts.

(2) Have the authors considered other ways in which factors such as attentional spillover and lateralization could be incorporated into the model? The spotlight-VGC model, as presented, involves first computing VGC predictions and only afterwards computing spillover. This seems psychologically implausible, since it supposes that the "optimal" representation is first formed and then it gets corrupted. Is there a way to integrate these biases directly into the VGC framework, perhaps as a prior on construals? The authors gesture towards this when they talk about "inductive biases", but this is not formalized.

(3) Can the authors rule out that the lateralization effects are the result of memory biases since the main measure used is a self-report of attention?

Question 1) (How / many) How many siblings does she have?

Question 2) (Where) Where do your parents live?

Question 3) (Who) Who was your role model growing up?

Question 4) (How / much) How much does a black coffee without milk cost?

Question 5) (Why) Why did you choose Loughborough University?

Reviewer #1 (Public review):

This work provides a valuable toolkit for endogenous isolation of projection neuron subtypes. With further validation, it could present a solid method for low-input ribosome affinity purification using a ribosomal RNA (rRNA) antibody. The experimental evidence for the distinct ribosomal complexes is limited to this method and indirect support from complementary analyses of pre-existing data. However, with additional experimental data to support the specificity of ribosomal complex pulldown and confirmation of the putative ribosomal complex proteins of interest, the study would provide compelling evidence for translation regulation of neuronal development through compositional ribosome heterogeneity. This work would be of interest to neuroscientists, developmental biologists, and those studying translational networks underlying gene regulation.

Strengths

(1) This in vivo labeling of specific projection neurons and ribosomal rRNA affinity purification method accommodates a low input of <100K somata per replicate, which is useful for the study of neuronal subtypes with limited input. In principle, this set of techniques could work across different cell types with limited input, depending on the molecule used for cell type labeling.

(2) The authors are also able to isolate endogenous neurons with minimal perturbation up to the point of collection, preserving the native state for the neuron in vivo as long as possible prior to processing.

(3) This study identified over a dozen potential non-ribosomal proteins associated with SCPN ribosomal complexes, as well as a ribosomal protein enriched in CPN.

Limitations

(1) In this study, the authors address the advantages of their ribosomal complex isolation method in SCPN and CPN against RPL22-HA affinity purification. While this does show more pull-down of the ribosomal RNA by the Y10B rRNA antibody, the authors claim this method identifies cell-type-specific ribosomal complex proteins without demonstrating a positive control for the method's specificity. There are very limited experiments to truly delineate how "specific" this method is working and whether there could be contamination from other complexes bound by the antibody. I see this as the major limitation that should be addressed. To boost their claims of capturing cell-type-specific ribosomal complexes, the authors could consider applying their rRNA affinity purification pipeline to compare cell types with well-characterized ribosome-associated proteins, like mouse embryonic stem cells and HELA cells. The reviewer can completely appreciate the elegance in the neural characterization here, but it seems there needs to be a solid foothold on the specificity of the method, perhaps facilitated by cell types that can be more readily scaled up and tested.

(2) The authors followed up on their differentially enriched ribosomal complex proteins by analyzing the ribosome association of these proteins in external datasets. While this analysis supports the ribosome-association of these proteins, there is limited experimental validation of physical association with the ribosome, much less any functional characterization. The reciprocal pulldown of PRKCE is promising; however, I would recommend orthogonal validation of several putative ribosomal complex proteins to increase confidence. Specifically, the authors could use sucrose gradient fractionation of SCPN and CPN, followed by a western blot to identify the putative interaction with the 80S monosome or polysomes. This would also provide evidence towards the pulldown capturing association with mature ribosome species, which is currently unclear. This experiment would provide substantial evidence for the direct association of these non-ribosomal proteins with subtype-specific ribosomal complexes.

(3) The authors state interest in learning more about the differences underlying translational regulation of projection neuron development. This method only captures neuronal somata, which will only capture ribosomes in the main cell body. There are also ribosomes regulating local translation in the axons, which may also play a critical role in axonal circuit establishment and activity. These ribosomal complex interactions may also be rather transient and difficult to capture at only one developmental stage. Therefore, this method is currently limited to a single developmental snapshot of ribosomal complexes at P3 within the main cell body. It would be exciting to see the extended utility of this method to sample neurites and additional developmental stages to gain further resolution on the developmental translation regulation of these projection neurons.

Likely impact of the work on the field, and the utility of the methods and data to the community:

The authors introduce a unique pipeline of techniques to identify cell-type-specific ribosomal complex compositions. With more validation, there is certainly potential for those studying neuronal translation to leverage this method in limited primary cells as an alternative to existing methods that do not rely on ribosomal protein tagging, such as ARC-MS (Bartsch et al., 2023), RAPIDASH (Susanto and Hung et al., 2024), and RAPPL (Nature Communications, 2025).

Having a sense of direction is important when trying to convey an idea or information to the reader.

Yeah as a high school student I think that my teachers have given me a baseline and overview of everything and college is where I get to build on that foundation and make something

It is important that we know the different forms of writing, otherwise, we can make mistakes.

purpose of compositions courses

Everyone has there different way of writing up a esay or even a noval so when it comes to having your own style its common it what makes you differnt and possibly even a great writer

I was really interested to read about how women in these societies held social power because they controlled food distribution—it surprised me, since I usually think of ancient cultures as male-dominated. It makes me wonder how common matrilineal or more egalitarian systems were in other parts of the world, especially in early farming communities. Could some of these arrangements have influenced the development of later social hierarchies, or were they mostly lost as agriculture and patriarchy expanded? I wish the textbook gave more examples of specific ancient societies outside North America that might have had similar gender dynamics.

This is a perfect way to word exactly how I view Nature vs nurture both are equally as important and impactful when it comes to shaping a person especially in early childhood.

1. Teachers were not involved in the process--they did not provide suggestions or had any other input. 2. Teachers were not provided any training on how to use the tech. 3. Technology was introduced in the classroom, but methods on how to implement the tech were not given. SUGGESTIONS: 1. Involve teaches in the process from beginning to end--show them the benefits of using tech in the classroom. 2. Allow them to give input on what tech to use and the process of implementing it. 3. Train them on teaching processes and how to use the technology.

This is just about acceptance and not really conforming into certain views

Differences in power consumption per rack

This difference requires liquid cooling versus air cooling.

1. Snuggling down to sleep smiling
2. Cuddling a soft toy
3. Having a good cry when things turn out bad

important

ojo con la numeración de títulos

numeración títulos

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Reply to the reviewers

Manuscript number: RC-2025-02922

Corresponding author(s): Christian Specht

[Please use this template only if the submitted manuscript should be considered by the affiliate journal as a full revision in response to the points raised by the reviewers.

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If you wish to submit a preliminary revision with a revision plan, please use our "Revision Plan" template. It is important to use the appropriate template to clearly inform the editors of your intentions.]

1. General Statements [optional]

This section is optional. Insert here any general statements you wish to make about the goal of the study or about the reviews.

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We thank the reviewers for their thorough and constructive evaluation of our work. We have revised the manuscript carefully and addressed all the criticisms raised, in particular the issues mentioned by several of the reviewers (see point-by-point response below). We have also added a number of explanations in the text for the sake of clarity, while trying to keep the manuscript as concise as possible.

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In our view, the novelty of our research is two-fold. From a neurobiological point of view, we provide conclusive evidence for the existence of glycine receptors (GlyRs) at inhibitory synapses in various brain regions including the hippocampus, dentate gyrus and sub-regions of the striatum. This solves several open questions and has fundamental implications for our understanding of the organisation and function of inhibitory synapses in the telencephalon. Secondly, our study makes use of the unique sensitivity of single molecule localisation microscopy (SMLM) to identify low protein copy numbers. This is a new way to think about SMLM as it goes beyond a mere structural characterisation and towards a quantitative assessment of synaptic protein assemblies.

2. Point-by-point description of the revisions

This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *

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__Reviewer #1 (Evidence, reproducibility and clarity (Required)): __

In this manuscript, the authors investigate the nanoscopic distribution of glycine receptor subunits in the hippocampus, dorsal striatum, and ventral striatum of the mouse brain using single-molecule localization microscopy (SMLM). They demonstrate that only a small number of glycine receptors are localized at hippocampal inhibitory synapses. Using dual-color SMLM, they further show that clusters of glycine receptors are predominantly localized within gephyrin-positive synapses. A comparison between the dorsal and ventral striatum reveals that the ventral striatum contains approximately eight times more glycine receptors and this finding is consistent with electrophysiological data on postsynaptic inhibitory currents. Finally, using cultured hippocampal neurons, they examine the differential synaptic localization of glycine receptor subunits (α1, α2, and β). This study is significant as it provides insights into the nanoscopic localization patterns of glycine receptors in brain regions where this protein is expressed at low levels. Additionally, the study demonstrates the different localization patterns of GlyR in distinct striatal regions and its physiological relevance using SMLM and electrophysiological experiments. However, several concerns should be addressed.

The following are specific comments:

1. Colocalization analysis in Figure 1A. The colocalization between Sylite and mEos-GlyRβ appears to be quite low. It is essential to assess whether the observed colocalization is not due to random overlap. The authors should consider quantifying colocalization using statistical methods, such as a pixel shift analysis, to determine whether colocalization frequencies remain similar after artificially displacing one of the channels. *Following the suggestion of reviewer 1, we re-analysed CA3 images of Glrbeos/eos hippocampal slices by applying a pixel-shift type of control, in which the Sylite channel (in far red) was horizontally flipped relative to the mEos4b-GlyRβ channel (in green, see Methods). As expected, the number of mEos4b-GlyRβ detections per gephyrin cluster was markedly reduced compared to the original analysis (revised__ Fig. 1B__), confirming that the synaptic mEos4b detections exceed chance levels (see page 5). *

Inconsistency between Figure 3A and 3B. While Figure 3B indicates an ~8-fold difference in the number of mEos4b-GlyRβ detections per synapse between the dorsal and ventral striatum, Figure 3A does not appear to show a pronounced difference in the localization of mEos4b-GlyRβ on Sylite puncta between these two regions. If the images presented in Figure 3A are not representative, the authors should consider replacing them with more representative examples or providing an expanded images with multiple representative examples. Alternatively, if this inconsistency can be explained by differences in spot density within clusters, the authors should explain that.

*The pointillist images in Fig. 3A are essentially binary (red-black). Therefore, the density of detections at synapses cannot be easily judged by eye. For clarity, the original images in Fig. 3A have been replaced with two other examples that better reflect the different detection numbers in the dorsal and ventral striatum. *

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Quantification in Figure 5. It is recommended that the authors provide quantitative data on cluster formation and colocalization with Sylite puncta in Figure 5 to support their qualitative observations.

*This is an important point that was also raised by the other reviewers. We have performed additional experiments to increase the data volume for analysis. For quantification, we used two approaches. First, we counted the percentage of infected cells in which synaptic localisation of the recombinant receptor subunit was observed (Fig. 5C). We found that mEos4b-GlyRa1 consistently localises at synapses, indicating that all cells express endogenous GlyRb. When neurons were infected with mEos4b-GlyRb, fewer cells had synaptic clusters, meaning that indeed, GlyR alpha subunits are the limiting factor for synaptic targeting. In cultures infected with mEos4b-GlyRa2, only very few neurons displayed synaptic localisation (as judged by epifluorescence imaging). We think this shows that GlyRa2 is less capable of forming heteromeric complexes than GlyRa1, in line with our previous interpretation (see pp. 9-10, 13). *

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Secondly, we quantified the total intensity of each subunit at gephyrin-positive domains, both in infected neurons as well as non-infected control cultures (Fig. 5D). We observed that mEos4b-GlyRa1 intensity at gephyrin puncta was higher than that of the other subunits, again pointing to efficient synaptic targeting of GlyRa1. Gephyrin cluster intensities (Sylite labelling) were not significantly different in GlyRb and GlyRa2 expressing neurons compared to the uninfected control, indicating that the lentiviral expression of recombinant subunits does not fundamentally alter the size of mixed inhibitory synapses in hippocampal neurons. Interestingly, gephyrin levels were slightly higher in hippocampal neurons expressing mEos4b-GlyRa1. In our view, this comes from an enhanced expression and synaptic targeting of mEos4b-GlyRa1 heteromers with endogenous GlyRb, pointing to a structural role of GlyRa1/b in hippocampal synapses (pp. 10, 13).

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The new data and analyses have been described and illustrated in the relevant sections of the manuscript.

Potential for pseudo replication. It's not clear whether they're performing stats tests across biological replica, images, or even synapses. They often quote mean +/- SEM with n = 1000s, and so does that mean they're doing tests on those 1000s? Need to clarify.

All experiments were repeated at least twice to ensure reproducibility (N independent experiments). Statistical tests were performed on pooled data across the biological replicates; n denotes the number of data points used for testing (e.g., number of synaptic clusters, detections, cells, as specified in each case). We have systematically given these numbers in the revised manuscript (n, N, and other experimental parameters such as the number of animals used, coverslips, images or cells). Data are generally given as mean +/- SEM or as mean +/- SD as indicated.

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Does mEoS effect expression levels or function of the protein? Can't see any experiments done to confirm this. Could suggest WB on homogenate, or mass spec?

The Glrbeos/eos knock-in mouse line has been characterised previously and does not to display any ultrastructural or functional deficits at inhibitory synapses (Maynard et al. 2021 eLife). GlyRβ expression and glycine-evoked responses were not significantly different to those of the wild-type. The synaptic localisation of mEos4b-GlyRb in KI animals demonstrates correct assembly of heteromeric GlyRs and synaptic targeting. Accordingly, the animals do not display any obvious phenotype. We have clarified this in the manuscript (p. 4). In the case of cultured neurons, long-term expression of fluorescent receptor subunits with lentivirus has proven ideal to achieve efficient synaptic targeting. The low and continuous supply of recombinant receptors ensures assembly with endogenous subunits to form heteropentameric receptor complexes (e.g. [Patrizio et al. 2017 Sci Rep]). In the present study, lentivirus infection did not induce any obvious differences in the number or size of inhibitory synapses compared to control neurons, as judged by Sylite labelling of synaptic gephyrin puncta (new__ Fig. 5D__).

Quantification of protein numbers is challenging with SMLM. Issues include i) some of FP not correctly folded/mature, and ii) dependence of localisation rate on instrument, excitation/illumination intensities, and also the thresholds used in analysis. Can the authors compare with another protein that has known expression levels- e.g. PSD95? This is quite an ask, but if they could show copy number of something known to compare with, it would be useful.

We agree that absolute quantification with SMLM is challenging, since the number of detections depends on fluorophore maturation, photophysics, imaging conditions, and analysis thresholds (discussed in Patrizio & Specht 2016, Neurophotonics). For this reason, only very few datasets provide reliable copy numbers, even for well-studied proteins such as PSD-95. One notable exception is the study by Maynard et al. (eLife 2021) that quantified endogenous GlyRb-containing receptors in spinal cord synapses using SMLM combined with correlative electron microscopy. The strength of this work was the use of a KI mouse strain, which ensures that mEos4b-GlyRb expression follows intrinsic regional and temporal profiles. The authors reported a stereotypic density of ~2,000 GlyRs/µm² at synapses, corresponding to ~120 receptors per synapse in the dorsal horn and ~240 in the ventral horn, taking into account various parameters including receptor stoichiometry and the functionality of the fluorophore. These values are very close to our own calculations of GlyR numbers at spinal cord synapses that were obtained slightly differently in terms of sample preparation, microscope setup, imaging conditions, and data analysis, lending support to our experimental approach. Nevertheless, the obtained GlyR copy numbers at hippocampal synapses clearly have to be taken as estimates rather than precise figures, because the number of detections from a single mEos4b fluorophore can vary substantially, meaning that the fluorophores are not represented equally in pointillist images. This can affect the copy number calculation for a specific synapse, in particular when the numbers are low (e.g. in hippocampus), however, it should not alter the average number of detections (Fig. 1B) or the (median) molecule numbers of the entire population of synapses (Fig. 1C). We have discussed the limitations of our approach (p. 11).

Rationale for doing nanobody dSTORM not clear at all. They don't explain the reason for doing the dSTORM experiments. Why not just rely on PALM for coincidence measurements, rather than tagging mEoS with a nanobody, and then doing dSTORM with that? Can they explain? Is it to get extra localisations- i.e. multiple per nanobody? If so, localising same FP multiple times wouldn't improve resolution. Also, no controls for nanobody dSTORM experiments- what about non-spec nb, or use on WT sections?

*As discussed above (point 6), the detection of fluorophores with SMLM is influenced by many parameters, not least the noise produced by emitting molecules other than the fluorophore used for labelling. Our study is exceptional in that it attempts to identify extremely low molecule numbers (down to 1). To verify that the detections obtained with PALM correspond to mEos4b, we conducted robust control experiments (including pixel-shift as suggested by the reviewer, see point 1, revised__ Fig. 1B__). The rationale for the nanobody-based dSTORM experiments was twofold: (1) to have an independent readout of the presence of low-copy GlyRs at inhibitory synapses and (2) to analyse the nanoscale organisation of GlyRs relative to the synaptic gephyrin scaffold using dual-colour dSTORM with spectral demixing (see p. 6). The organic fluorophores used in dSTORM (AF647, CF680) ensure high photon counts, essential for reliable co-localisation and distance analysis. PALM and dSTORM cannot be combined in dual-colour mode, as they require different buffers and imaging conditions. *

The specificity of the anti-Eos nanobody was demonstrated by immunohistochemistry in spinal cord cultures expressing mEos4b-GlyRb and wildtype control tissue (Fig. S3). In response to the reviewer's remarks, we also performed a negative control experiment in Glrbeos/eos slices (dSTORM), in which the nanobody was omitted (new__ Fig. S4F,G__). Under these conditions, spectral demixing produced a single peak corresponding to CF680 (gephyrin) without any AF647 contribution (Fig. S4F). The background detection of "false" AF647 detections at synapses was significantly lower than in the slices labelled with the nanobody. We conclude that the fluorescence signal observed in our dual-colour dSTORM experiments arises from the specific detection of mEos4b-GlyRb by the nanobody, rather than from background, cross-reactivity or wrong attribution of colour during spectral demixing. We have added these data and explanations in the results (p. 7) and in the figure legend of Fig. S4F,G.

What resolutions/precisions were obtained in SMLM experiments? Should perform Fourier Ring Correlation (FRC) on SR images to state resolutions obtained (particularly useful for when they're presenting distance histograms, as this will be dependent on resolution). Likewise for precision, what was mean precision? Can they show histograms of localisation precision.

This is an interesting question in the context of our experiments with low-copy GlyRs, since the spatial resolution of SMLM is limited also by the density of molecules, i.e. the sampling of the structure in question (Nyquist-Shannon criterion). Accordingly, the priority of the PALM experiments was to improve the sensibility of SMLM for the identification of mEos4b-GlyRb subunits, rather than to maximize the spatial resolution. The mean localisation precision in PALM was 33 +/- 12 nm, as calculated from the fitting parameters of each detection (Zeiss, ZEN software), which ultimately result from their signal-to-noise ratio. This is a relatively low precision for SMLM, which can be explained by the low brightness of mEos4b compared to organic fluorophores together with the elevated fluorescence background in tissue slices.

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In the case of dSTORM, the aim was to study the relative distribution of GlyRs within the synaptic scaffold, for which a higher localisation precision was required (p. 6). Therefore, detections with a precision ≥ 25 nm were filtered during analysis with NEO software (Abbelight). The retained detections had a mean localisation precision of 12 +/- 5 for CF680 (Sylite) and 11 +/- 4 for AF647 (nanobody). These values are given in the revised manuscript (pp. 18, 22).

Why were DBSCAN parameters selected? How can they rule out multiple localisations per fluor? If low copy numbers (

Multiple detections of the same fluorophore are intrinsic to dSTORM imaging and have not been eliminated from the analysis. Small clusters of detections likely represent individual molecules (e.g. single receptors in the extrasynaptic regions, Fig. 2A). DBSCAN is a robust clustering method that is quite insensitive to minor changes in the choice of parameters. For dSTORM of synaptic gephyrin clusters (CF680), a relatively low length (80 nm radius) together with a high number of detections (≥ 50 neighbours) were chosen to reconstruct the postsynaptic domain with high spatial resolution (see point 8). In the case of the GlyR (nanobody-AF647), the clustering was done mostly for practical reasons, as it provided the coordinates of the centre of mass of the detections. The low stringency of this clustering (200 nm radius, ≥ 5 neighbours) effectively filters single detections that can result from background noise or incorrect demixing. An additional reference explaining the use of DBSCAN including the choice of parameters is given on p. 22 (see also R2 point 4).

For microscopy experiment methods, state power densities, not % or "nominal power".

*Done. We now report the irradiance (laser power density) instead of nominal power (pp. 18, 21). *

In general, not much data presented. Any SI file with extra images etc.?

*The original submission included four supplementary figures with additional data and representative images that should have been available to the reviewer (Figs. S1-S4). The SI file has been updated during revision (new Fig. S4E-G). *

Clarification of the discussion on GlyR expression and synaptic localization: The discussion on GlyR expression, complex formation, and synaptic localization is sometimes unclear, and needs terminological distinctions between "expression level", "complex formation" and "synaptic localization". For example, the authors state:"What then is the reason for the low protein expression of GlyRβ? One possibility is that the assembly of mature heteropentameric GlyR complexes depends critically on the expression of endogenous GlyR α subunits." Does this mean that GlyRβ proteins that fail to form complexes with GlyRα subunits are unstable and subject to rapid degradation? If so, the authors should clarify this point. The statement "This raises the interesting possibility that synaptic GlyRs may depend specifically on the concomitant expression of both α1 and β transcripts." suggests a dependency on α1 and β transcripts. However, is the authors' focus on synaptic localization or overall protein expression levels? If this means synaptic localization, it would be beneficial to state this explicitly to avoid confusion. To improve clarity, the authors should carefully distinguish between these different aspects of GlyR biology throughout the discussion. Additionally, a schematic diagram illustrating these processes would be highly beneficial for readers.

We thank the reviewer to point this out. We are dealing with several processes; protein expression that determines subunit availability and the assembly of pentameric GlyRs complexes, surface expression, membrane diffusion and accumulation of GlyRb-containing receptor complexes at inhibitory synapses. We have edited the manuscript, particularly the discussion and tried to be as clear as possible in our wording.

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We chose not to add a schematic illustration for the time being, because any graphical representation is necessarily a simplification. Instead, we preferred to summarise the main numbers in tabular form (Table 1). We are of course open to any other suggestions.

Interpretation of GlyR localization in the context of nanodomains. The distribution of GlyR molecules on inhibitory synapses appears to be non-homogeneous, instead forming nanoclusters or nanodomains, similar to many other synaptic proteins. It is important to interpret GlyR localization in the context of nanodomain organization.

The dSTORM images in Fig. 2 are pointillist representations that show individual detections rather than molecules. Small clusters of detections are likely to originate from a single AF647 fluorophore (in the case of nanobody labelling) and therefore represent single GlyRb subunits. Since GlyR copy numbers are so low at hippocampal synapses (≤ 5), the notion of nanodomain is not directly applicable. Our analysis therefore focused on the integration of GlyRs within the postsynaptic scaffold, rather than attempting to define nanodomain structures (see also response to point 8 of R1). A clarification has been added in the revised manuscript (p. 6).

__Reviewer #1 (Significance (Required)): __

The paper presents biological and technical advances. The biological insights revolve mostly on the documentation of Glycine receptors in particular synapses in forebrain, where they are typically expressed at very low levels. The authors provide compelling data indicating that the expression is of physiological significance. The authors have done a nice job of combining genetically-tagged mice with advanced microscopy methods to tackle the question of distributions of synaptic proteins. Overall these advances are more incremental than groundbreaking.

We thank the reviewer for acknowledging both the technical and biological advances of our study. While we recognize that our work builds upon established models, we consider that it also addresses important unresolved questions, namely that GlyRs are present and specifically anchored at inhibitory synapses in telencephalic regions, such as the hippocampus and striatum. From a methodological point of view, our study demonstrates that SMLM can be applied not only for structural analysis of highly abundant proteins, but also to reliably detect proteins present at very low copy numbers. This ability to identify and quantify sparse molecule populations adds a new dimension to SMLM applications, which we believe increases the overall impact of our study beyond the field of synaptic neuroscience.

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __

In their manuscript "Single molecule counting detects low-copy glycine receptors in hippocampal and striatal synapses" Camuso and colleagues apply single molecule localization microscopy (SMLM) methods to visualize low copy numbers of GlyRs at inhibitory synapses in the hippocampal formation and the striatum. SMLM analysis revealed higher copy numbers in striatum compared to hippocampal inhibitory synapses. They further provide evidence that these low copy numbers are tightly linked to post-synaptic scaffolding protein gephyrin at inhibitory synapses. Their approach profits from the high sensitivity and resolution of SMLM and challenges the controversial view on the presence of GlyRs in these formations although there are reports (electrophysiology) on the presence of GlyRs in these particular brain regions. These new datasets in the current manuscript may certainly assist in understanding the complexity of fundamental building blocks of inhibitory synapses.

However I have some minor points that the authors may address for clarification:

1) In Figure 1 the authors apply PALM imaging of mEos4b-GlyRß (knockin) and here the corresponding Sylite label seems to be recorded in widefield, it is not clearly stated in the figure legend if it is widefield or super-resolved. In Fig 1 A - is the scale bar 5 µm? Some Sylite spots appear to be sized around 1 µm, especially the brighter spots, but maybe this is due to the lower resolution of widefield imaging? Regarding the statistical comparison: what method was chosen to test for normality distribution, I think this point is missing in the methods section.

*This is correct; the apparent size of the Sylite spots does not reflect the real size of the synaptic gephyrin domain due to the limited resolution of widefield imaging including the detection of out-of-focus light. We have clarified in the legend of Fig. 1A that Sylite labelling was with classic epifluorescence microscopy. The scale bar in Fig. 1A corresponds to 5 µm. Since the data were not normally distributed, nonparametric tests (Kruskal- Wallis one-way ANOVA with Dunn’s multiple comparison test or Mann-Whitney U-test for pairwise comparisons) were used (p. 23). *

Moreover I would appreciate a clarification and/or citation that the knockin model results in no structural and physiological changes at inhibitory synapses, I believe this model has been applied in previous studies and corresponding clarification can be provided.

The Glrbeos/eos mouse model has been described previously and does not exhibit any structural or physiological phenotypes (Maynard et al. 2021 eLife). The issue was also raised by reviewer R1 (point 5) and has been clarified in the revised manuscript (p. 4).

2) In the next set of experiments the authors switch to demixing dSTORM experiments - an explanation why this is performed is missing in the text - I guess better resolution to perform more detailed distance measurements? For these experiments: which region of the hippocampus did the authors select, I cannot find this information in legend or main text.

Yes, the dSTORM experiments enable dual-colour structural analysis at high spatial resolution (see response to R1 point 7). An explanation has been added (p. 6).

3) Regarding parameters of demixing experiments: the number of frames (10.000) seems quite low and the exposure time higher than expected for Alexa 647. Can the authors explain the reason for chosing these particular parameters (low expression profile of the target - so better separation?, less fluorophores on label and shorter collection time?) or is there a reference that can be cited? The laser power is given in the methods in percentage of maximal output power, but for better comparison and reproducibility I recommend to provide the values of a power meter (kW/cm2) as lasers may change their maximum output power during their lifetime.

Acquisition parameters (laser power, exposure time) for dSTORM were chosen to obtain a good localisation precision (~12 nm; see R1 point 8). The number of frames is adequate to obtain well sampled gephyrin scaffolds in the CF680 channel. In the case of the GlyR (nanobody-AF647), the concept of spatial resolution does not really apply due to the low number of targets (see R1, point 13). Power density (irradiance) values have now been given (pp. 18, 21).

4) For analysis of subsynaptic distribution: how did the authors decide to choose the parameters in the NEO software for DBSCAN clustering - was a series of parameters tested to find optimal conditions and did the analysis start with an initial test if data is indeed clustered (K-ripley) or is there a reference in literature that can be provided?

DBSCAN parameters were optimised manually, by testing different values. Identification of dense and well-delimited gephyrin clusters (CF680) was achieved with a small radius and a high number of detections (80 nm, ≥ 50 neighbours), whereas filtering of low-density background in the AF647 channel (GlyRs) required less stringent parameters (200 nm, ≥ 5) due to the low number of target molecules. Similar parameters were used in a previous publication (Khayenko et al. 2022, Angewandte Chemie). The reference has been provided on p. 22 (see also R1 point 9).

5) A conclusion/discussion of the results presented in Figure 5 is missing in the text/discussion.

*This part of the manuscript has been completely overhauled. It includes new experimental data, quantification of the data (new Fig.5), as well as the discussion and interpretation of our findings (see also R1, point 3). In agreement with our earlier interpretation, the data confirm that low availability of GlyRa1 subunits limits the expression and synaptic targeting of GlyRa1/b heteropentamers. The observation that GlyRa1 overexpression with lentivirus increases the size of the postsynaptic gephyrin domain further points to a structural role, whereby GlyRs can enhance the stability (and size) of inhibitory synapses in hippocampal neurons, even at low copy numbers (pp. 13-14). *

6) in line 552 "suspension" is misleading, better use "solution"

Done.

__Reviewer #2 (Significance (Required)): __

Significance: The manuscript provides new insights to presence of low-copy numbers by visualizing them via SMLM. This is the first report that visualizes GlyR optically in the brain applying the knock-in model of mEOS4b tagged GlyRß and quantifies their copy number comparing distribution and amount of GlyRs from hippocampus and striatum. Imaging data correspond well to electrophysiological measurements in the manuscript.

Field of expertise: Super-Resolution Imaging and corresponding analysis

__Reviewer #4 (Evidence, reproducibility and clarity (Required)): __

In this study, Camuso et al., make use of a knock-in mouse model expressing endogenously mEos4b-tagged GlyRβ to detect endogenous glycine receptors using single-molecule localization microscopy. The main conclusion from this study is that in the hippocampus GlyRβ molecules are barely detected, while inhibitory synapses in the ventral striatum seem to express functionally relevant GlyR numbers.

I have a few points that I hope help to improve the strength of this study.

• In the hippocampus, this study finds that the numbers of detections are very low. The authors perform adequate controls to indicate that these localizations are above noise level. Nevertheless, it remains questionable that these reflect proper GlyRs. The suggestion that in hippocampal synapses the low numbers of GlyRβ molecules "are important in assembly or maintenance of inhibitory synaptic structures in the brain" is on itself interesting, but is not at all supported. It is also difficult to envision how such low numbers could support the structure of a synapse. A functional experiment showing that knockdown of GlyRs affects inhibitory synapse structure in hippocampal neurons would be a minimal test of this.

*It is not clear what the reviewer means by “it remains questionable that these reflect proper GlyRs”. The PALM experiments include a series of stringent controls (see R1, point 1) demonstrating the existence of low-copy GlyRs at inhibitory synapses in the hippocampus (Fig. 1) and in the striatum (Fig. 3), and are backed up by dSTORM experiments (Fig. 2). We have no reason to doubt that these receptors are fully functional (as demonstrated for the ventral striatum (Fig. 4). However, due to their low number, a role in inhibitory synaptic transmission is clearly limited, at least in the hippocampus and dorsal striatum. *

• *

We therefore propose a structural role, where the GlyRs could be required to stabilise the postsynaptic gephyrin domain in hippocampal neurons. This is based on the idea that the GlyR-gephyrin affinity is much higher than that of the GABAAR-gephyrin interaction (reviewed in Kasaragod & Schindelin 2018 Front Mol Neurosci). Accordingly, there is a close relationship between GlyRs and gephyrin numbers, sub-synaptic distribution, and dynamics in spinal cord synapses that are mostly glycinergic (Specht et al. 2013 Neuron; Maynard et al. 2021 eLife; Chapdelaine et al. 2021 Biophys J). It is reasonable to assume that low-copy GlyRs could play a similar structural role at hippocampal synapses. A knockdown experiment targeting these few receptors is technically very challenging and beyond the scope of this study. However, in response to the reviewer's question we have conducted new experiments in cultured hippocampal neurons (new__ Fig. 5__). They demonstrate that overexpression of GlyRa1/b heteropentamers increases the size of the postsynaptic domain in these neurons, supporting our interpretation of a structural role of low-copy GlyRs (p. 14).

• The endogenous tagging strategy is a very strong aspect of this study and provides confidence in the labeling of GlyRβ molecules. One caveat however, is that this labeling strategy does not discriminate whether GlyRβ molecules are on the cell membrane or in internal compartments. Can the authors provide an estimate of the ratio of surface to internal GlyRβ molecules?

Gephyrin is known to form a two-dimensional scaffold below the synaptic membrane to which inhibitory GlyRs and GABAARs attach (reviewed in Alvarez 2017 Brain Res). The majority of the synaptic receptors are therefore thought to be located in the synaptic membrane, which is supported by the close relationship between the sub-synaptic distribution of GlyRs and gephyrin in spinal cord neurons (e.g. Maynard et al. 2021 eLife). To demonstrate the surface expression of GlyRs at hippocampal synapses we labelled cultured hippocampal neurons expressing mEos4b-GlyRa1 with anti-Eos nanobody in non-permeabilised neurons (see Figure below for the reviewer only). The close correspondence between the nanobody (AF647) and the mEos4b signal confirms that the majority of the GlyRs are indeed located in the synaptic membrane.

• *

Figure (for the reviewer only).* Left: Lentivirus expression of mEos4b-GlyRa1 in fixed and non-permeabilised hippocampal neurons (mEos4b signal). Right: Surface labelling of the recombinant subunit with anti-Eos nanoboby (AF647). *

• 'We also estimated the absolute number of GlyRs per synapse in the hippocampus. The number of mEos4b detections was converted into copy numbers by dividing the detections at synapses by the average number of detections of individual mEos4b-GlyRβ containing receptor complexes'. In essence this is a correct method to estimate copy numbers, and the authors discuss some of the pitfalls associated with this approach (i.e., maturation of fluorophore and detection limit). Nevertheless, the authors did not subtract the number of background localizations determined in the two negative control groups. This is critical, particularly at these low-number estimations.

We fully agree that background subtraction can be useful with low detection numbers. In the revised manuscript, copy numbers are now reported as background-corrected values. Specifically, the mean number of detections measured in wildtype slices was used to calculate an equivalent receptor number, which was then subtracted from the copy number estimates across hippocampus, spinal cord and striatum. This procedure is described in the methods (p. 20) and results (p. 5, 8), and mentioned in the figure legends of Fig. 1C, 3C. The background corrected values are given in the text and Table 1.

Furthermore, the authors state that "The advantage of this estimation is that it is independent of the stoichiometry of heteropentameric GlyRs". However, if the stoichometry is unknown, the number of counted GlyRβ subunits cannot simply be reported as the number of GlyRs. This should be discussed in more detail, and more carefully reported throughout the manuscript.

*The reviewer is right to point this out. There is still some debate about the stoichiometry of heteropentameric GlyRs. Configurations with 2a:3b, 3a:2b and 4a:1b subunits have been advanced (e.g. Grudzinska et al. 2005 Neuron; Durisic et al. 2012 J Neurosci; Patrizio et al. 2017 Sci Rep; Zhu & Gouaux 2021 Nature). We have therefore chosen a quantification that is independent of the underlying stoichiometry. Since our quantification is based on very sparse clusters of mEos4b detections that likely originate from a single receptor complex (irrespective of its stoichiometry), the reported values actually reflect the number of GlyRs (and not GlyRb subunits). We have clarified this in the results (p. 5) and throughout the manuscript (Table 1). *

• The dual-color imaging provides insights in the subsynaptic distribution of GlyRβ molecules in hippocampal synapses. Why are similar studies not performed on synapses in the ventral striatum where functionally relevant numbers of GlyRβ molecules are found? Here insights in the subsynaptic receptor distribution would be of much more interest as it can be tight to the function.

This is an interesting suggestion. However, the primary aim of our study was to identify the existence of GlyRs in hippocampal regions. At low copy numbers, the concept of sub-synaptic domains (SSDs, e.g. Yang et al. 2021 EMBO Rep) becomes irrelevant (see R1 point 13). It should be pointed out that the dSTORM pointillist images (Fig. 2A) represent individual GlyR detections rather than clusters of molecules. In the striatum, our specific purpose was to solve an open question about the presence of GlyRs in different subregions (putamen, nucleus accumbens).

• It is unclear how the experiments in Figure 5 add to this study. These results are valid, but do not seem to directly test the hypothesis that "the expression of α subunits may be limiting factor controlling the number of synaptic GlyRs". These experiments simply test if overexpressed α subunits can be detected. If the α subunits are limiting, measuring the effect of α subunit overexpression on GlyRβ surface expression would be a more direct test.

Both R1 and R2 have also commented on the data in Fig. 5 and their interpretation. We have substantially revised this section as described before (see R1 point 3) including additional experiments and quantification of the data (new Fig. 5). The findings lend support to our earlier hypothesis that GlyR alpha subunits (in particular GlyRa1) are the limiting factor for the expression of heteropentameric GlyRa/b in hippocampal neurons (pp. 13-14). Since the GlyRa1 subunit itself does not bind to gephyrin (Patrizio et al. 2017 Sci Rep), the synaptic localisation of the recombinant mEos4b-GlyRa1 subunits is proof that they have formed heteropentamers with endogenous GlyRb subunits and driven their membrane trafficking, which the GlyRb subunits are incapable of doing on their own.

__Reviewer #4 (Significance (Required)): __

These results are based on carefully performed single-molecule localization experiments, and are well-presented and described. The knockin mouse with endogenously tagged GlyRβ molecules is a very strong aspect of this study and provides confidence in the labeling, the combination with single-molecule localization microscopy is very strong as it provides high sensitivity and spatial resolution.

The conceptual innovation however seems relatively modest, these results confirm previous studies but do not seem to add novel insights. This study is entirely descriptive and does not bring new mechanistic insights.

This study could be of interest to a specialized audience interested in glycine receptor biology, inhibitory synapse biology and super-resolution microscopy.

my expertise is in super-resolution microscopy, synaptic transmission and plasticity

As we have stated before, the novelty of our study lies in the use of SMLM for the identification of very small numbers of molecules, which requires careful control experiments. This is something that has not been done before and that can be of interest to a wider readership, as it opens up SMLM for ultrasensitive detection of rare molecular events. Using this approach, we solve two open scientific questions: (1) the demonstration that low-copy GlyRs are present at inhibitory synapses in the hippocampus, (2) the sub-region specific expression and functional role of GlyRs in the ventral versus dorsal striatum.

• *

• *

The following review was provided later under the name “Reviewer #4”. To avoid confusion with the last reviewer from above we will refer to this review as R4-2.

__Reviewer #4-2 (Evidence, reproducibility and clarity (Required)): __

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

The authors investigate the presence of synaptic glycine receptors in the telencephalon, whose presence and function is poorly understood.

Using a transgenically labeled glycine receptor beta subunit (Glrb-mEos4b) mouse model together with super-resolution microscopy (SLMM, dSTORM), they demonstrate the presence of a low but detectable amount of synaptically localized GLRB in the hippocampus. While they do not perform a functional analysis of these receptors, they do demonstrate that these subunits are integrated into the inhibitory postsynaptic density (iPSD) as labeled by the scaffold protein gephyrin. These findings demonstrate that a low level of synaptically localized glycerine receptor subunits exist in the hippocampal formation, although whether or not they have a functional relevance remains unknown.

They then proceed to quantify synaptic glycine receptors in the striatum, demonstrating that the ventral striatum has a significantly higher amount of GLRB co-localized with gephyrin than the dorsal striatum or the hippocampus. They then recorded pharmacologically isolated glycinergic miniature inhibitory postsynaptic currents (mIPSCs) from striatal neurons. In line with their structural observations, these recordings confirmed the presence of synaptic glycinergic signaling in the ventral striatum, and an almost complete absence in the dorsal striatum. Together, these findings demonstrate that synaptic glycine receptors in the ventral striatum are present and functional, while an important contribution to dorsal striatal activity is less likely.

Lastly, the authors use existing mRNA and protein datasets to show that the expression level of GLRA1 across the brain positively correlates with the presence of synaptic GLRB.

The authors use lentiviral expression of mEos4b-tagged glycine receptor alpha1, alpha2, and beta subunits (GLRA1, GLRA1, GLRB) in cultured hippocampal neurons to investigate the ability of these subunits to cause the synaptic localization of glycine receptors. They suggest that the alpha1 subunit has a higher propensity to localize at the inhibitory postsynapse (labeled via gephyrin) than the alpha2 or beta subunits, and may therefore contribute to the distribution of functional synaptic glycine receptors across the brain.

Major comments:

• Are the key conclusions convincing?

The authors are generally precise in the formulation of their conclusions.

• They demonstrate a very low, but detectable, amount of a synaptically localized glycine receptor subunit in a transgenic (GlrB-mEos4b) mouse model. They demonstrate that the GLRB-mEos4b fusion protein is integrated into the iPSD as determined by gephyrin labelling. The authors do not perform functional tests of these receptors and do not state any such conclusions.
• The authors show that GLRB-mEos4b is clearly detectable in the striatum and integrated into gephyrin clusters at a significantly higher rate in the ventral striatum compared to the dorsal striatum, which is in line with previous studies.
• Adding to their quantification of GLRB-mEos4b in the striatum, the authors demonstrate the presence of glycinergic miniature IPSCs in the ventral striatum, and an almost complete absence of mIPSCs in the dorsal striatum. These currents support the observation that GLRB-mEos4b is more synaptically integrated in the ventral striatum compared to the dorsal striatum.

• The authors show that lentiviral expression of GLRA1-mEos4b leads to a visually higher number of GLR clusters in cultured hippocampal neurons, and a co-localization of some clusters with gephyrin. The authors claim that this supports the idea that GLRA1 may be an important driver of synaptic glycine receptor localization. However, no quantification or statistical analysis of the number of puncta or their colocalization with gephyrin is provided for any of the expressed subunits. Such a claim should be supported by quantification and statistics A thorough analysis and quantification of the data in Fig.5 has been carried out as requested by all the other reviewers (e.g. R1, point 3). The new data and results have been described in the revised manuscript (pp. 9-10, 13-14).

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

One unaddressed caveat is the fact that a GLRB-mEos4b fusion protein may behave differently in terms of localization and synaptic integration than wild-type GLRB. While unlikely, it is possible that mEos4b interacts either with itself or synaptic proteins in a way that changes the fused GLRB subunit’s localization. Such an effect would be unlikely to affect synaptic function in a measurable way, but might be detected at a structural level by highly sensitive methods such as SMLM and STORM in regions with very low molecule numbers (such as the hippocampus). Since reliable antibodies against GLRB in brain tissue sections are not available, this would be difficult to test. Considering that no functional measures of the hippocampal detections exist, we would suggest that this possible caveat be mentioned for this particular experiment.

*This question has also been raised before (R1, point 5). According to an earlier study the mEos4b-GlyRb knock-in does not cause any obvious phenotypes, with the possible exception of minor loss of glycine potency (Maynard et al. 2021 eLife). The fact that the synaptic levels in the spinal cord in heterozygous animals are precisely half of those of homozygous animals argues against differences in receptor expression, heteropentameric assembly, forward trafficking to the plasma membrane and integration into the synaptic membrane as confirmed using quantitative super-resolution CLEM (Maynard et al. 2021 eLife). Accordingly, we did not observe any behavioural deficits in these animals, making it a powerful experimental model. We have added this information in the revised manuscript (p. 4). *

In addition, without any quantification or statistical analysis, the author’s claims regarding the necessity of GLRA1 expression for the synaptic localization of glycine receptors in cultured hippocampal neurons should probably be described as preliminary (Fig. 5).

As mentioned before, we have substantially revised this part (R1, point 3). The quantification and analysis in the new Fig. 5 support our earlier interpretation.

• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

The authors show that there is colocalization of gephyrin with the mEos4b-GlyRβ subunit using the Dual-colour SMLM. This is a powerful approach that allows for a claim to be made on the synaptic location of the glycine receptors. The images presented in Figure 1, together with the distance analysis in Figure 2, display the co-localization of the fluorophores. The co-localization images in all the selected regions, hippocampus and striatum, also show detections outside of the gephyrin clusters, which the authors refer to as extrasynaptic. These punctated small clusters seem to have the same size as the ones detected and assigned as part of the synapse. It would be informative if the authors analysed the distribution, density and size of these non-synaptic clusters and presented the data in the manuscript and also compared it against the synaptic ones. Validating this extrasynaptic signal by staining for a dendritic marker, such as MAP-2 or maybe a somatic marker and assessing the co-localization with the non-synaptic clusters would also add even more credibility to them being extrasynaptic.

The existence of extrasynaptic GlyRs is well attested in spinal cord neurons (e.g. Specht et al. 2013 Neuron; this study see Fig. S2). The fact that these appear as small clusters of detections in SMLM recordings results from the fact that a single fluorophore can be detected several times in consecutive image frames and because of blinking. Therefore, small clusters of detections likely represent single GlyRs (that can be counted), and not assemblies of several receptor complexes. Due to their diffusion in the neuronal membrane, they are seen as diffuse signals throughout the somatodendritic compartment in epifluorescence images (e.g. Fig. 5A). SMLM recordings of the same cells resolves this diffuse signal into discrete nanoclusters representing individual receptors (Fig. 5B). It is not clear what information co-localisation experiments with specific markers could provide, especially in hippocampal neurons, in which the copy numbers (and density) of GlyRs is next to zero.

In addition we would encourage the authors to quantify the clustering and co-localization of virally expressed GLRA1, GLRA2, and GLRB with gephyrin in order to support the associated claims (Fig. 5). Preferably, the density of GLR and gephyrin clusters (at least on the somatic surface, the proximal dendrites, or both) as well as their co-localization probability should be quantified if a causal claim about subunit-specific requirements for synaptic localization is to be made.

Quantification of the data have been carried out (new Fig.5C,D). The results have been described before (R1, point 3) and support our earlier interpretation of the data (pp. 13-14).

Lastly, even though it may be outside of the scope of such a study analysing other parts of the hippocampal area could provide additional important information. If one looks at the Allen Institute’s ISH of the beta subunit the strongest signal comes from the stratum oriens in the CA1 for example, suggesting that interneurons residing there would more likely have a higher expression of the glycine receptors. This could also be assessed by looking more carefully at the single cell transcriptomics, to see which cell types in the hippocampus show the highest mRNA levels. If the authors think that this is too much additional work, then perhaps a mention of this in the discussion would be good.

We have added the requested information from the ISH database of the Allen Institute in the discussion as suggested by the reviewer (p. 12). However, in combination with the transcriptomic data (Fig. S1) our finding strongly suggest that the expression of synaptic GlyRs depends on the availability of alpha subunits rather than on the presence of the GlyRb transcript. This is obvious when one compares the mRNA levels in the hippocampus with those in the basal ganglia (striatum) and medulla. While the transcript concentrations of GlyRb are elevated in all three regions and essentially the same, our data show that the GlyRb copy numbers *at synapses differ over more than 2 orders of magnitude (Fig. 1B, Table 1). *

• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

Since the labeling and some imaging has been performed already, the requested experiment would be a matter of deploying a method of quantification. In principle, it should not require any additional wet-lab experiments, although it may require additional imaging of existing samples.

• Are the data and the methods presented in such a way that they can be reproduced?

Yes, for the most part.

• Are the experiments adequately replicated and statistical analysis adequate?

Yes

Minor comments:

• Specific experimental issues that are easily addressable.

N/A

• Are prior studies referenced appropriately?

Yes

• Are the text and figures clear and accurate?

Yes, although quantification in figure 5 is currently not present.

A quantification has been added (see R1, point 3).

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

This paper presents a method that could be used to localize receptors and perhaps other proteins that are in low abundance or for which a detailed quantification is necessary. I would therefore suggest that Figure S4 is included into Figure 2 as the first panel, showcasing the demixing, followed by the results.

We agree in principle with this suggestion. However, the revised Fig. S4 is more complex and we think that it would distract from the data shown in Fig. 2. Given that Fig. S4 is mostly methodological and not essential to understand the text, we have kept it in the supplement for the time being. We leave the final decision on this point to the editor.

__Reviewer #4-2 (Significance (Required)): __

[This review was supplied later]

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

Using a novel and high resolution method, the authors have provided strong evidence for the presence of glycine receptors in the murine hippocampus and in the dorsal striatum. The number of receptors calculated is small compared to the numbers found in the ventral striatum. This is the first study to quantify receptor numbers in these region. In addition it also lays a roadmap for future studies addressing similar questions.

• Place the work in the context of the existing literature (provide references, where appropriate).

This is done well by the authors in the curation of the literature. As stated above, the authors have filled a gap in the presence of glycine receptors in different brain regions, a subject of importance in understanding the role they play in brain activity and function.

• State what audience might be interested in and influenced by the reported findings.

Neuroscientists working at the synaptic level, on inhibitory neurotransmission and on fundamental mechanisms of expression of genes at low levels and their relationship to the presence of the protein would be interested. Furthermore, researchers in neuroscience and cell biology may benefit from and be inspired by the approach used in this manuscript, to potentially apply it to address their own aims.

*We thank the reviewer for the positive assessment of the technical and biological implications of our work, as well as the interest of our findings to a wide readership of neuroscientists and cell biologists. *

• Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

Synaptic transmission, inhibitory cells and GABAergic synapses functionally and structurally, cortex and cortical circuits. No strong expertise in super-resolution imaging methods.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #4

Evidence, reproducibility and clarity

Summary: Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

The authors investigate the presence of synaptic glycine receptors in the telencephalon, whose presence and function is poorly understood.

Using a transgenically labeled glycine receptor beta subunit (Glrb-mEos4b) mouse model together with super-resolution microscopy (SLMM, dSTORM), they demonstrate the presence of a low but detectable amount of synaptically localized GLRB in the hippocampus. While they do not perform a functional analysis of these receptors, they do demonstrate that these subunits are integrated into the inhibitory postsynaptic density (iPSD) as labeled by the scaffold protein gephyrin. These findings demonstrate that a low level of synaptically localized glycerine receptor subunits exist in the hippocampal formation, although whether or not they have a functional relevance remains unknown.

They then proceed to quantify synaptic glycine receptors in the striatum, demonstrating that the ventral striatum has a significantly higher amount of GLRB co-localized with gephyrin than the dorsal striatum or the hippocampus. They then recorded pharmacologically isolated glycinergic miniature inhibitory postsynaptic currents (mIPSCs) from striatal neurons. In line with their structural observations, these recordings confirmed the presence of synaptic glycinergic signaling in the ventral striatum, and an almost complete absence in the dorsal striatum. Together, these findings demonstrate that synaptic glycine receptors in the ventral striatum are present and functional, while an important contribution to dorsal striatal activity is less likely.

Lastly, the authors use existing mRNA and protein datasets to show that the expression level of GLRA1 across the brain positively correlates with the presence of synaptic GLRB. The authors use lentiviral expression of mEos4b-tagged glycine receptor alpha1, alpha2, and beta subunits (GLRA1, GLRA1, GLRB) in cultured hippocampal neurons to investigate the ability of these subunits to cause the synaptic localization of glycine receptors. They suggest that the alpha1 subunit has a higher propensity to localize at the inhibitory postsynapse (labeled via gephyrin) than the alpha2 or beta subunits, and may therefore contribute to the distribution of functional synaptic glycine receptors across the brain.

Major comments: - Are the key conclusions convincing?

The authors are generally precise in the formulation of their conclusions.

1) They demonstrate a very low, but detectable, amount of a synaptically localized glycine receptor subunit in a transgenic (GlrB-mEos4b) mouse model. They demonstrate that the GLRB-mEos4b fusion protein is integrated into the iPSD as determined by gephyrin labelling. The authors do not perform functional tests of these receptors and do not state any such conclusions. 2) The authors show that GLRB-mEos4b is clearly detectable in the striatum and integrated into gephyrin clusters at a significantly higher rate in the ventral striatum compared to the dorsal striatum, which is in line with previous studies. 3) Adding to their quantification of GLRB-mEos4b in the striatum, the authors demonstrate the presence of glycinergic miniature IPSCs in the ventral striatum, and an almost complete absence of mIPSCs in the dorsal striatum. These currents support the observation that GLRB-mEos4b is more synaptically integrated in the ventral striatum compared to the dorsal striatum. 4) The authors show that lentiviral expression of GLRA1-mEos4b leads to a visually higher number of GLR clusters in cultured hippocampal neurons, and a co-localization of some clusters with gephyrin. The authors claim that this supports the idea that GLRA1 may be an important driver of synaptic glycine receptor localization. However, no quantification or statistical analysis of the number of puncta or their colocalization with gephyrin is provided for any of the expressed subunits. Such a claim should be supported by quantification and statistics

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

One unaddressed caveat is the fact that a GLRB-mEos4b fusion protein may behave differently in terms of localization and synaptic integration than wild-type GLRB. While unlikely, it is possible that mEos4b interacts either with itself or synaptic proteins in a way that changes the fused GLRB subunit's localization. Such an effect would be unlikely to affect synaptic function in a measurable way, but might be detected at a structural level by highly sensitive methods such as SMLM and STORM in regions with very low molecule numbers (such as the hippocampus). Since reliable antibodies against GLRB in brain tissue sections are not available, this would be difficult to test. Considering that no functional measures of the hippocampal detections exist, we would suggest that this possible caveat be mentioned for this particular experiment.

In addition, without any quantification or statistical analysis, the author's claims regarding the necessity of GLRA1 expression for the synaptic localization of glycine receptors in cultured hippocampal neurons should probably be described as preliminary (Fig. 5).

• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

The authors show that there is colocalization of gephyrin with the mEos4b-GlyRβ subunit using the Dual-colour SMLM. This is a powerful approach that allows for a claim to be made on the synaptic location of the glycine receptors. The images presented in Figure 1, together with the distance analysis in Figure 2, display the co-localization of the fluorophores. The co-localization images in all the selected regions, hippocampus and striatum, also show detections outside of the gephyrin clusters, which the authors refer to as extrasynaptic. These punctated small clusters seem to have the same size as the ones detected and assigned as part of the synapse. It would be informative if the authors analysed the distribution, density and size of these non-synaptic clusters and presented the data in the manuscript and also compared it against the synaptic ones. Validating this extrasynaptic signal by staining for a dendritic marker, such as MAP-2 or maybe a somatic marker and assessing the co-localization with the non-synaptic clusters would also add even more credibility to them being extrasynaptic.

In addition we would encourage the authors to quantify the clustering and co-localization of virally expressed GLRA1, GLRA2, and GLRB with gephyrin in order to support the associated claims (Fig. 5). Preferably, the density of GLR and gephyrin clusters (at least on the somatic surface, the proximal dendrites, or both) as well as their co-localization probability should be quantified if a causal claim about subunit-specific requirements for synaptic localization is to be made.

Lastly, even though it may be outside of the scope of such a study analysing other parts of the hippocampal area could provide additional important information. If one looks at the Allen Institute's ISH of the beta subunit the strongest signal comes from the stratum oriens in the CA1 for example, suggesting that interneurons residing there would more likely have a higher expression of the glycine receptors. This could also be assessed by looking more carefully at the single cell transcriptomics, to see which cell types in the hippocampus show the highest mRNA levels. If the authors think that this is too much additional work, then perhaps a mention of this in the discussion would be good.

• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

Since the labeling and some imaging has been performed already, the requested experiment would be a matter of deploying a method of quantification. In principle, it should not require any additional wet-lab experiments, although it may require additional imaging of existing samples.

• Are the data and the methods presented in such a way that they can be reproduced?

Yes, for the most part.

• Are the experiments adequately replicated and statistical analysis adequate?

Yes

Minor comments: - Specific experimental issues that are easily addressable.

N/A

• Are prior studies referenced appropriately?

Yes

• Are the text and figures clear and accurate?

Yes, although quantification in figure 5 is currently not present.

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

This paper presents a method that could be used to localize receptors and perhaps other proteins that are in low abundance or for which a detailed quantification is necessary. I would therefore suggest that Figure S4 is included into Figure 2 as the first panel, showcasing the demixing, followed by the results.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

Using a novel and high resolution method, the authors have provided strong evidence for the presence of glycine receptors in the murine hippocampus and in the dorsal striatum. The number of receptors calculated is small compared to the numbers found in the ventral striatum. This is the first study to quantify receptor numbers in these region. In addition it also lays a roadmap for future studies addressing similar questions.

• Place the work in the context of the existing literature (provide references, where appropriate).

This is done well by the authors in the curation of the literature. As stated above, the authors have filled a gap in the presence of glycine receptors in different brain regions, a subject of importance in understanding the role they play in brain activity and function.

• State what audience might be interested in and influenced by the reported findings.

Neuroscientists working at the synaptic level, on inhibitory neurotransmission and on fundamental mechanisms of expression of genes at low levels and their relationship to the presence of the protein would be interested. Furthermore, researchers in neuroscience and cell biology may benefit from and be inspired by the approach used in this manuscript, to potentially apply it to address their own aims.

• Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

Synaptic transmission, inhibitory cells and GABAergic synapses functionally and structurally, cortex and cortical circuits. No strong expertise in super-resolution imaging methods.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #3

Evidence, reproducibility and clarity

In this study, Camuso et al., make use of a knock-in mouse model expressing endogenously mEos4b-tagged GlyRβ to detect endogenous glycine receptors using single-molecule localization microscopy. The main conclusion from this study is that in the hippocampus GlyRβ molecules are barely detected, while inhibitory synapses in the ventral striatum seem to express functionally relevant GlyR numbers.

I have a few points that I hope help to improve the strength of this study.

• In the hippocampus, this study finds that the numbers of detections are very low. The authors perform adequate controls to indicate that these localizations are above noise level. Nevertheless, it remains questionable that these reflect proper GlyRs. The suggestion that in hippocampal synapses the low numbers of GlyRβ molecules "are important in assembly or maintenance of inhibitory synaptic structures in the brain" is on itself interesting, but is not at all supported. It is also difficult to envision how such low numbers could support the structure of a synapse. A functional experiment showing that knockdown of GlyRs affects inhibitory synapse structure in hippocampal neurons would be a minimal test of this.
• The endogenous tagging strategy is a very strong aspect of this study and provides confidence in the labeling of GlyRβ molecules. One caveat however, is that this labeling strategy does not discriminate whether GlyRβ molecules are on the cell membrane or in internal compartments. Can the authors provide an estimate of the ratio of surface to internal GlyRβ molecules?
• 'We also estimated the absolute number of GlyRs per synapse in the hippocampus. The number of mEos4b detections was converted into copy numbers by dividing the detections at synapses by the average number of detections of individual mEos4b-GlyRβ containing receptor complexes'. In essence this is a correct method to estimate copy numbers, and the authors discuss some of the pitfalls associated with this approach (i.e., maturation of fluorophore and detection limit). Nevertheless, the authors did not subtract the number of background localizations determined in the two negative control groups. This is critical, particularly at these low-number estimations. Furthermore, the authors state that "The advantage of this estimation is that it is independent of the stoichiometry of heteropentameric GlyRs". However, if the stoichometry is unknown, the number of counted GlyRβ subunits cannot simply be reported as the number of GlyRs. This should be discussed in more detail, and more carefully reported throughout the manuscript.
• The dual-color imaging provides insights in the subsynaptic distribution of GlyRβ molecules in hippocampal synapses. Why are similar studies not performed on synapses in the ventral striatum where functionally relevant numbers of GlyRβ molecules are found? Here insights in the subsynaptic receptor distribution would be of much more interest as it can be tight to the function.
• It is unclear how the experiments in Figure 5 add to this study. These results are valid, but do not seem to directly test the hypothesis that "the expression of α subunits may be limiting factor controlling the number of synaptic GlyRs". These experiments simply test if overexpressed α subunits can be detected. If the α subunits are limiting, measuring the effect of α subunit overexpression on GlyRβ surface expression would be a more direct test.

Significance

These results are based on carefully performed single-molecule localization experiments, and are well-presented and described. The knockin mouse with endogenously tagged GlyRβ molecules is a very strong aspect of this study and provides confidence in the labeling, the combination with single-molecule localization microscopy is very strong as it provides high sensitivity and spatial resolution.

The conceptual innovation however seems relatively modest, these results confirm previous studies but do not seem to add novel insights. This study is entirely descriptive and does not bring new mechanistic insights.

This study could be of interest to a specialized audience interested in glycine receptor biology, inhibitory synapse biology and super-resolution microscopy.

my expertise is in super-resolution microscopy, synaptic transmission and plasticity

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Referee #2

Evidence, reproducibility and clarity

In their manuscript "Single molecule counting detects low-copy glycine receptors in hippocampal and striatal synapses" Camuso and colleagues apply single molecule localization microscopy (SMLM) methods to visualize low copy numbers of GlyRs at inhibitory synapses in the hippocampal formation and the striatum. SMLM analysis revealed higher copy numbers in striatum compared to hippocampal inhibitory synapses. They further provide evidence that these low copy numbers are tightly linked to post-synaptic scaffolding protein gephyrin at inhibitory synapses. Their approach profits from the high sensitivity and resolution of SMLM and challenges the controversial view on the presence of GlyRs in these formations although there are reports (electrophysiology) on the presence of GlyRs in these particular brain regions. These new datasets in the current manuscript may certainly assist in understanding the complexity of fundamental building blocks of inhibitory synapses.

However I have some minor points that the authors may address for clarification:

1. In Figure 1 the authors apply PALM imaging of mEos4b-GlyRß (knockin) and here the corresponding Sylite label seems to be recorded in widefield, it is not clearly stated in the figure legend if it is widefield or super-resolved. In Fig 1 A - is the scale bar 5 µm? Some Sylite spots appear to be sized around 1 µm, especially the brighter spots, but maybe this is due to the lower resolution of widefield imaging? Regarding the statistical comparison: what method was chosen to test for normality distribution, I think this point is missing in the methods section. Moreover I would appreciate a clarification and/or citation that the knockin model results in no structural and physiological changes at inhibitory synapses, I believe this model has been applied in previous studies and corresponding clarification can be provided.
2. In the next set of experiments the authors switch to demixing dSTORM experiments - an explanation why this is performed is missing in the text - I guess better resolution to perform more detailed distance measurements? For these experiments: which region of the hippocampus did the authors select, I cannot find this information in legend or main text.
3. Regarding parameters of demixing experiments: the number of frames (10.000) seems quite low and the exposure time higher than expected for Alexa 647. Can the authors explain the reason for chosing these particular parameters (low expression profile of the target - so better separation?, less fluorophores on label and shorter collection time?) or is there a reference that can be cited? The laser power is given in the methods in percentage of maximal output power, but for better comparison and reproducibility I recommend to provide the values of a power meter (kW/cm2) as lasers may change their maximum output power during their lifetime.
4. For analysis of subsynaptic distribution: how did the authors decide to choose the parameters in the NEO software for DBSCAN clustering - was a series of parameters tested to find optimal conditions and did the analysis start with an initial test if data is indeed clustered (K-ripley) or is there a reference in literature that can be provided?
5. A conclusion/discussion of the results presented in Figure 5 is missing in the text/discussion.
6. in line 552 "suspension" is misleading, better use "solution"

Significance

Significance: The manuscript provides new insights to presence of low-copy numbers by visualizing them via SMLM. This is the first report that visualizes GlyR optically in the brain applying the knock-in model of mEOS4b tagged GlyRß and quantifies their copy number comparing distribution and amount of GlyRs from hippocampus and striatum. Imaging data correspond well to electrophysiological measurements in the manuscript.

Field of expertise: Super-Resolution Imaging and corresponding analysis