Author response:

General Statements

We are grateful for constructive reviewers’ comments and criticisms and have thoroughly addressed all major and minor comments in the revised manuscript.

Summary of new data.

We have performed the following additional experiments to support our concept:

(1) The kinetcs of ROS production in B6 and B6.Sst1S macrophages after TNF stimulation (Fig. 3I and J, Suppl. Fig. 3G);

(2) Time course of stress kinase activation (Fig.3K) that clearly demonstrated the persistent stress kinase (phospho-ASK1 and phospho-cJUN) activation exclusively in. the B6.Sst1S macrophages;

(3) New Fig.4 C-E panels include comparisons of the B6 and B6.Sst1S macrophage responses to TNF and effects of IFNAR1 blockade in both backgrounds.

(4) We performed new experiments demonstrating that the synthesis of lipid peroxidation products (LPO) occurs in TNF-stimulated macrophages earlier than the IFNβ super-induction (Suppl.Fig.4A and B).

(5) We demonstrated that the IFNAR1 blockade 12, 24 and 32 h after TNF stimulation still reduced the accumulation of LPO product (4-HNE) in TNF-stimulated B6.Sst1S BMDMs (Suppl.Fig.4 E-G).

(6) We added comparison of cMyc expression between the wild type B6 and B6.Sst1S BMDMs during TNF stimulation for 6-24 h (Fig.5I-J).

(7) New data comparing 4-HNE levels in Mtb-infected B6 wild type and B6.Sst1S macrophages and quantification of replicating Mtb was added (Fig.6B, Suppl.Fig.7C and D).

(8) In vivo data described in Fig.7 was thoroughly revised and new data was included. We demonstrated increased 4-HNE loads in multibacillary lesions (Fig.7A, Suppl. Fig.9A) and the 4-HNE accumulation in CD11b+ myeloid cells (Fig.7B and Suppl.Fig.9B). We demonstrated that the Ifnb – expressing cells are activated iNOS+ macrophages (Fig.7D and Suppl.Fig.13A). Using new fluorescent multiplex IHC, we have shown that stress markers phopho-cJun and Chac1 in TB lesions are expressed by Ifnb- and iNOS-expressing macrophages (Fig.7E and Suppl.Fig.13D-F).

(9) We performed additional experiment to demonstrate that naïve (non-BCG vaccinated) lymphocytes did not improve Mtb control by Mtb-infected macrophages in agreement with previously published data (Suppl.Fig.7H).

Summary of updates

Following reviewers requests we updated figures to include isotype control antibodies, effects of inhibitors on non-stimulated cells, positive and negative controls for labile iron pool, additional images of 4-HNE and live/dead cell staining.

Isotype control for IFNAR1 blockade were included in Fig.3M, Fig.4C -E, Fig.6L-M Suppl.Fig.4F-G, 7I.

Positive and negative controls for labile iron pool measurements were added to Fig.3E, Fig.5D, Suppl.Fig.3B

Cell death staining images were added Suppl.Fig.3H

Co-staining of 4-HNE with tubulin was added to Suppl.Fig.3A.

High magnification images for Figure 7 were added in Suppl.Fig.8 to demonstrate paucibacillary and multibacillary image classification.

Single-channel color images for individual markers were provided in Fig.7E and Suppl.Fig.13B-F.

Inhibitor effects on non-stimulated cells were included in Fig.5 D-H, Suppl.Fig.6A and B. Titration of CSF1R inhibitors for non-toxic concentration determination are included in Suppl.Fig.6D.

In addition, we updated the figure legends in the revised manuscript to include more details about the experiments. We also clarified our conclusions in the Discussion. Responses to every major and minor comment of the reviewers are provided below.

Point-by-point description of the revisions

Reviewer #1 (Evidence, reproducibility and clarity:

Summary

The study by Yabaji et al. examines macrophage phenotypes B6.Sst1S mice, a mouse strain with increased susceptibility to M. tuberculosis infection that develops necrotic lung lesions. Extending previous work, the authors specifically focus on delineating the molecular mechanisms driving aberrant oxidative stress in TNF-activated B6.Sst1S macrophages that has been associated with impaired control of M. tuberculosis. The authors use scRNAseq of bone marrow-derived macrophages to further characterize distinctions between B6.Sst1S and control macrophages and ascribe distinct trajectories upon TNF stimulation. Combined with results using inhibitory antibodies and small molecule inhibitors in in vitro experimentation, the authors propose that TNF-induced protracted c-Myc expression in B6.Sst1S macrophages disables the cellular defense against oxidative stress, which promotes intracellular accumulation of lipid peroxidation products, fueled at least in part by overexpression of type I IFNs by these cells. Using lung tissue sections from M. tuberculosis-infected B6.Sst1S mice, the authors suggest that the presence of a greater number of cells with lipid peroxidation products in lung lesions with high counts of stained M. tuberculosis are indicative of progressive loss of host control due to the TNF-induced dysregulation of macrophage responses to oxidative stress. In patients with active tuberculosis disease, the authors suggest that peripheral blood gene expression indicative of increased Myc activity was associated with treatment failure.

Major comments

The authors describe differences in protein expression, phosphorylation or binding when referring to Fig 2A-C, 2G, 3D, 5B, 5C. However, such differences are not easily apparent or very subtle and, in some cases, confounded by differences in resting cells (e.g. pASK1 Fig 3L; c-Myc Fig 5B) as well as analyses across separate gels/blots (e.g. Fig 3K, Fig 5B). Quantitative analyses across different independent experiments with adequate statistical analyses are required to strengthen the associated conclusions.

We updated our Western blots as follows:

(1) Densitometery of normalized bands is included above each lane (Fig.2A-C; Fig.3C-D and 3K; Fig.4A-B; Fig.5B,C,I,J). New data in Fig.3K is added to highlight differences between B6 and B6.Sst1S at individual timepoints after TNF stimulation. In Fig.5I we added new data comparing Myc levels in B6 and B6.Sst1S with and without JNK inhibitor and updated the results accordingly. New Fig.3K clearly demonstrates the persistent activation of p-cJun and pAsk1 at 24 and 36h of TNF stimulation. In Fig.5B we clearly demonstrate that Myc levels were higher in B6.Sst1S after 12 h of TNF stimulation. At 6h, however, the basal differences in Myc levels are consistently higher in B6.Sst1S and the induction by TNF is 1.6-fold similar in both backgrounds. We noted this in the text.

(2) A representative experiment is shown in individual panels and the corresponding figure legend contains information on number of biological repeats. Each Western blot was repeated 2 – 4 times.

The representative images of fluorescence microscopy in Fig 3H, 4H, 5H, S3C, S3I, S5A, S6A seem to suggest that under some conditions the fluorescence signal is located just around the nucleus rather than absent or diminished from the cytoplasm. It is unclear whether this reflects selective translocation of targets across the cell, morphological changes of macrophages in culture in response to the various treatments, or variations in focal point at which images were acquired. Control images (e.g. cellular actin, DIC) should be included for clarification. If cell morphology changes depending on treatments, how was this accounted for in the quantitative analyses? In addition, negative controls validating specificity of fluorescence signals would be warranted.

Our conclusion of higher LPO production is based on several parameters: 4-HNE staining, measurements of MDA in cell lysates and oxidized lipids using BODIPY C11. Taken together they demonstrate significant and reproducible increase in LPO accumulation in TNFstimulated B6.Sst1S macrophages. This excludes imaging artefact related to unequal 4-HNE distribution noted by the reviewer. In fact, we also noted that the 4-HNE was spread within cell body of B6.Sst1S macrophages and confirmed it using co-staining with tubulin, as suggested by the reviewer (new Suppl.Fig.3A). Since low molecular weight LPO products, such as MDA and 4-HNE, traverse cell membranes, it is unlikely that they will be strictly localized to a specific membrane bound compartment. However, we agree that at lower concentrations, there might be some restricted localization, explaining a visible perinuclear ring of 4-HNE staining in B6 macrophages. This phenomenon may be explained just by thicker cytoplasm surrounding nucleus in activated macrophages spread on adherent plastic surface or by proximity to specific organelles involved in generation or clearance of LPO products and definitively warrants further investigation.

We also included images of non-stimulated cells in Fig.3H, Suppl.Fig.3A and 3E. We used multiple fields for imaging and quantified fluorescence signals (Suppl. Fig.3D and 3F, Suppl.Fig.4G, Suppl.Fig.6A and B).

We used negative controls without primary antibodies for the initial staining optimization, but did not include it in every experiment.

To interpret the evaluation on the hierarchy of molecular mechanisms in B6.Sst1S macrophages, comparative analyses with B6 control cells should be included (e.g. Fig 4C-I, Fig 5, Fig 6B, E-M, S6C, S6E-F). This will provide weight to the conclusions that the dysregulated processes are specifically associated with the susceptibility of B6.Sst1S macrophages.

Understanding the sst1-mediated effects on macrophage activation is the focus of our previously published studies Bhattacharya et al., JCI, 2021) and this manuscript. The data comparing B6 and B6.Sst1S macrophage are presented in Fig.1, Fig.2, Fig.3, Fig.4, Fig.5A-C, I and J, Fig.6A-C, 6J and corresponding supplemental figures 1, 2, 3, 4A and B, Suppl.Fig.5, Suppl.Fig.6C, Suppl.Fig.7A-D,7F.

Once we identified the aberrantly activated pathways in the B6.Sst1S, we used specific inhibitors to correct the aberrant response in B6.Sst1S.

All experiments using inhibitory antibodies require comparison to the effect of a matched isotype control in the same experiment (e.g. Fig 3J, 4F, G, I; 6L, 6M, S3G, S6F).

Isotype control for IFNAR1 blockade were included in Fig.3M, Fig.4C-E, Fig.6L-M Suppl.Fig.4F-G, 7I.

Experiments using inhibitors require inclusion of an inhibitor-only control to assess inhibitor effects on unstimulated cells (e.g. Fig 4I, 5D-I)

Inhibitor effects on non-stimulated cells were included in Fig.5 D-H, Suppl.Fig.6A and B.

Fig 3K and Fig 5J appear to contain the same images for p-c-Jun and b-tubulin blots.

Fig.3K and 5J partially overlapped but had different focus – 3K has been updated to reflect the time course of stress kinase activation. Fig.5J is updated (currently Fig.5I and J) to display B6 and B6.Sst1S macrophage data including cMyc and p-cJun levels.

Data of TNF-treated cells in Fig 3I appear to be replotted in Fig 3J.

Currently these data is presented in Fig.3L and 3M and has been updated to include comparison of B6 and B6.Sst1S cells (Fig.3L) and effects of inhibitors in Fig.3M.

It is stated that lungs from 2 mice with paucibacillary and 2 mice with multi-bacillary lesions were analyses. There is contradicting information on whether these tissues were collected at the same time post infection (week 14?) or whether the pauci-bacillary lesions were in lungs collected at earlier time points post infection (see Fig S8A). If the former, how do the authors conclude that multi-bacillary lesions are a progression from paucibacillary lesions and indicative of loss of M. tuberculosis control, especially if only one lesion type is observed in an individual host? If the latter, comparison between lesions will likely be dominated by temporal differences in the immune response to infection.

In either case, it is relevant to consider density, location, and cellular composition of lesions (see also comments on GeoMx spatial profiling). Is the macrophage number/density per tissue area comparable between pauci-bacillary and multi-bacillary lesions?

We did not collect lungs at the same time point. As described in greater detail in our preprints (Yabaji et al., https://doi.org/10.1101/2025.02.28.640830 and https://doi.org/10.1101/2023.10.17.562695) pulmonary TB lesions in our model of slow TB progression are heterogeneous between the animals at the same timepoint, as observed in human TB patients and other chronic TB animal models. Therefore, we perform analyses of individual TB lesions that are classified by a certified veterinary pathologist in a blinded manner based on their morphology (H&E) and acid fast staining of the bacteria, as depicted in Suppl.Fig.8. Currently it is impossible to monitor progression of individual lesions in mice. However, in mice TB is progressive disease and no healing and recovery from the disease have been observed in our studies or reported in literature. Therefore, we assumed that paucibacillary lesions preceded the multibacillary ones, and not vice versa, thus reflecting the disease progression. In our opinion, this conclusion most likely reflects the natural course of the disease. However, we edited the text : instead of disease progression we refer to paucibacillary and multibacillary lesions.

Does 4HNE staining align with macrophages and if so, is it elevated compared to control mice and driven by TNF in the susceptible vs more resistant mice?

We performed additional staining and analyses to demonstrate the 4-HNE accumulation in CD11b+ myeloid cells of macrophage morphology. Non-necrotic lesions contain negligible proportion of neutrophils (Fig.7B, Suppl.Fig.9B). B6 mice do not develop advanced multibacillary TB lesions containing 4-HNE+ cells. Also, 4-HNE staining was localized to TB lesions and was not found in uninvolved lung areas of the infected mice, as shown in Suppl.Fig.9A (left panel).

It is well established that TNF plays a central role in the formation and maintenance of TB granulomas in humans and in all animal models. Therefore, TNF neutralization would lead to rapid TB progression, rapid Mtb growth and lesions destruction in both B6 and B6.Sst1S genetic backgrounds.

Pathway analysis of spatial transcriptomic data (Suppl.Fig.11) identified TNF signaling via NFkB among dominant pathways upregulated in multibacillary lesions, suggesting that the 4-HNE accumulation paralleled increased TNF signaling. In addition, in vivo other cytokines, including IFN-I, could activate macrophages and stimulate production of reactive oxygen and nitrogen species and lead to the accumulation of LPO products as shown in this manuscript.

It would be relevant to state how many independent lesions per host were sampled in both the multiplex IHC as well as the GeoMx data. Can the authors show the selected regions of interest in the tissue overview and in the analyses to appreciate within-host and across-host heterogeneity of lesions. The nature of the spatial transcriptomics platform used is such that the data are derived from tissue areas that contain more than just Iba1+ macrophages. At later stages of infection, the cellular composition of such macrophage-rich areas will be different when compared to lesions earlier in the infection process. Hence, gene expression profiles and differences between tissue regions cannot be attributed to macrophages in this tissue region but are more likely a reflection of a mix of cellular composition and per-cell gene expression.

We used Iba1 staining to identify macrophages in TB lesions and programmed GeoMx instrument to collect spatial transcriptomics probes from Iba1+ cells within ROIs. Also, we selected regions of interest (ROI) avoiding necrotic areas (depicted in Suppl.Fig.10). We agree that Iba1+ macrophage population is heterogenous – some Iba1+ cells are activated iNOS+ macrophages, other are iNOS-negative (Fig.7C and D, and Suppl.Fig.13A). Multibacillary lesions contain larger areas occupied by activated (iNOS+) macrophages (Fig.7D,

Suppl.Fig.13B and 13F). Although the GeoMx spatial transcriptomic platform does not provide single cell resolution, it allowed us to compare populations of Iba1+ cells in paucibacillary and multibacillary TB lesions and to identify a shift in their overall activation pattern.

It is stated that loss of control of M. tuberculosis in multibacillary lesions was associated with "downregulation of IFNg-inducible genes". If the authors base this on the tissue expression of individual genes, this requires further investigation to support such conclusion (also see comment on GeoMx above). Furthermore, how might this conclusion be compatible with significantly elevated iNOS+ cells (Fig 7D) in multibacillary lesions?

We demonstrated that Ciita gene expression is specifically induced by IFN-gamma and is suppressed by IFN-I (Fig.6M). The expression of Ciita in paucibacillary lesions suggest the presence of the IFN-gamma activated cells and its disappearance in the multibacillary lesion is consistent with massive activation of IFN-I pathway (Fig.7C).

It is appreciated that the human blood signature analyses contain Myc-signatures but the association with treatment failure is not very strong based on the data in Fig 13B and C (Suppl.Fig.15B and C now). The authors indicate that they have no information on disease severity, but it should perhaps not be assumed that treatment failure is indicative of poor host control of the infection. Perhaps independent analyses in separate cohort/data set can add strength and provide -additional insights (e.g. PMID: 35841871; PMID: 32451443, PMID: 17205474, PMID: 22872737). In addition, the human data analyses could be strengthened by extension to additional signatures such as IFN, TNF, oxidative stress. Details of the human study design are not very clear and are lacking patient demographics, site of disease, time of blood collection relative to treatment onset, approving ethics committees.

X axis of Suppl.Fig.15A represent pre-defined molecular signature gene sets (MSigDB) in Gene Set Enrichment Analysis (GSEA) database (https://www.gseamsigdb.org/gsea/msigdb). On Y axis is area under curve (AUC) score for each gene set. The Myc upregulated gene set myc_up was identified among top gene sets associated with treatment failure using unbiased ssGSEA algorithm. The upregulation of Myc pathway in the blood transcriptome associated with TB treatment failure most likely reflects greater proportion of immature cells in peripheral blood, possibly due to increased myelopoiesis.

Pathway analysis of the differentially expressed genes revealed that treatment failures were associated with the following pathways relevant to this study: NF-kB Signaling, Flt3 Signaling in Hematopoietic Progenitor Cells (indicative of common myeloid progenitor cell proliferation), SAPK/JNK Signaling and Senescence (indicative of oxidative stress). The upregulation of these pathways in human patients with poor TB treatment outcomes correlates with our findings in TB susceptible mice. The detailed analysis of differentially regulated pathways in human TB patients is beyond the scope of this study and is presented in another manuscript entitled “ Tuberculosis risk signatures and differential gene expression predict individuals who fail treatment” by Arthur VanValkenburg et al., submitted for publication.

Blood collection for PBMC gene expression profiling of TB patients was prior to TB treatment or within a first week of treatment commencement. Boxplot of bootstrapped ssGSEA enrichment AUC scores from several oncogene signatures ranked from lowest to highest AUC score, with myc_up and myc_dn genes highlighted in red.

We agree with the reviewer that not every gene in the myc_up gene set correlates with the treatment outcome. But the association of the gene set is statistically significant, as presented in Suppl.Fig.15B – C.

We updated the details of the study, including study sites and the ethics committee approval statement and references describing these cohorts.

Other comments

It is excellent that the authors provide individual data points. Choosing a colour other than black would increase clarity when black bars are used.

We followed this useful suggestion and selected consistent color codes for B6 and B6.Sst1S groups to enhance clarity throughout the revised manuscript.

Error bars are inconsistently depicted as either bi-directional or just unidirectional.

We used bi-directional error bars in the revised manuscript.

Fig 1E, G, H - please include a scale to clarify what the heat map is representing.

We have included the expression key in Fig.1E,G and H and Suppl.Fig.1C and D in the revised version.

Fig 2K, Fig S10A gene information cannot be deciphered.

We increased the font in previous Fig.2K and moved to supplement to keep larger fonts (current Suppl.Fig.2G).

Fig S4A,B please add error bars.

These data are presented as Suppl.Fig.5 in the revised version. We performed one experiment to test the hypothesis. Because the data indicated no clear increase in transposon small RNAs in the sst1S macrophages, we did not pursue this hypothesis further, and therefore, the error bars were not included. However, we decided to include these negative data because it rejects a very attractive and plausible hypothesis.

Please use gene names as per convention (e.g. Ifnb1) to distinguish gene expression from protein expression in figures and text.

We addressed the comment in the revised manuscript.

Fig S8B. Contrary to the description of results, there seems to be minimal overlap between the signal for YFP and the Ifnb1 probe. Is the Ifnb1 reporter mouse a legacy reporter? If so, it is worth stating this and including such considerations in the data interpretation.

The YFP reporter expresses YFP protein under the control of the Ifnb1 promoter. The YFP protein accumulates within the cells and while Ifnb protein is rapidly secreted and does not accumulate in the producing cells in appreciable amounts. So YFP is not a lineage tracing reporter, but its accumulation marks the Ifnb1 promoter activity in cells, although the YFP protein half-life is longer than that of the Ifnb1 mRNA that is rapidly degraded (Witt et al., BioRxiv, 2024; doi:10.1101/2024.08.28.61018). Therefore, there is no precise spatiotemporal coincidence of these readouts.

Please clarify what is meant by "normal interstitium" ? If the tissue is from uninfected mice, please state clearly.

In this context we refer to the uninvolved lung areas of the infected lungs. In every sample we compare uninvolved lung areas and TB lesions of the same animal. Also, we performed staining of lung of non-infected mice as additional controls.

If macrophage cultures underwent media changes every 48h, how was loss of liberated Mtb taken into account especially if differences in cell density/survival were noted? The assessment of M. tuberculosis load by qPCR is not well described. In particular, the method of normalization applied within the experiments (not within the qPCR) here remains unclear, even with reference to the authors' prior publication.

Our lab has many years of experience working with macrophage monolayers infected with virulent Mtb and uses optimized protocols to avoid cell losses and related artifacts. Recently we published a detailed protocol for this methodology in STAR Protocols (Yabaji et al., 2022; PMID 35310069). In brief, it includes preparation of single cell suspensions of Mtb by filtration to remove clumps, use of low multiplicity of infection, preparation of healthy confluent monolayers and use of nutrient rich culture medium and medium change every 2 days. We also rigorously control for cell loss using whole well imaging and quantification of cell numbers and live/dead staining.

Please add citation for the limma package.

The references has been added (Ritchie et al, NAR 2015; PMID 25605792).

The description of methodology relating to the "oncogene signatures" is unclear.

This signature was described in Bild etal, Nature, 2006 and McQuerry JA, et al, 2019 “Pathway activity profiling of growth factor receptor network and stemness pathways differentiates metaplastic breast cancer histological subtypes”. BMC Cancer 19: 881 and is cited in Methods section Oncogene signatures

Please clearly state time points post infection for mouse analyses.

We collected lung samples from Mtb infected mice 12 – 20 weeks post infection. The lesions were heterogeneous and were individually classified using criteria described above.

Reference is made to "a list of genes unique to type I [interferon] genes [....]" (p29). Can the authors indicate the source of the information used for compiling this list?

The lists were compiled from Reactome, EMBL's European Bioinformatics Institute and GSEA databases. The links for all datasets are provided in Suppl.Table 8 “Expression of IFN pathway genes in Iba1+ cells from pauci- and multi-bacillary lesions of Mtb infected B6.Sst1S mouse lungs” in the “Pool IFN I & II gene sets” worksheet.

The discussion at present is very long, contains repetition of results and meanders on occasion.

Thank you for this suggestion, We critically revised the text for brevity and clarity.

Reviewer #1 (Significance):  

Strengths and limitations  

Strengths: multi-pronged analysis approaches for delineating molecular mechanisms of macrophage responses that might underpin susceptibility to M. tuberculosis infection; integration of mouse tissues and human blood samples  

Weaknesses: not all conclusions supported by data presented; some concerns related to experimental design and controls; links between findings in human cohort and the mechanistic insights gained in mouse macrophage model uncertain

The revised manuscript addresses every major and minor comment of the reviewers, including isotype controls and naïve T cells, to provide additional support for our conclusions. Our study revealed causal links between Myc hyperactivity with the deficiency of anti-oxidant defense and type I interferon pathway hyperactivity. We have shown that Myc hyperactivity in TNF-stimulated macrophages compromises antioxidant defense leading to autocatalytic lipid peroxidation and interferon-beta superinduction that in turn amplifies lipid peroxidation, thus, forming a vicious cycle of destructive chronic inflammation. This mechanism offers a plausible mechanistic explanation of for the association of Myc hyperactivity with poorer treatment outcomes in TB patients and provide a novel target for host-directed TB therapy.

Advance

The study has the potential to advance molecular understanding of the TNF-driven state of oxidative stress previously observed in B6.Sst1S macrophages and possible implications for host control of M. tuberculosis in vivo.

Audience

Experts seeking understanding of host factors mediating M. tuberculosis control, or failure thereof, with appreciation for the utility of the featured mouse model in assessing TB diseases progression and severe manifestation. Interest is likely extended to audience more broadly interested in TNF-driven macrophage (dys)function in infectious, inflammatory, and autoimmune pathologies.

Reviewer expertise

In preparing this review, I am drawing on my expertise in assessing macrophage responses and host defense mechanisms in bacterial infections (incl. virulent M. tuberculosis) through in vitro and in vivo studies. This includes but is not limited to macrophage infection and stimulation assays, microscopy, intra-macrophage replication of M. tuberculosis, analyses of lung tissues using multi-plex IHC and spatial transcriptomics (e.g. GeoMx). I am familiar with the interpretation of RNAseq analyses in human and mouse cells/tissues, but can provide only limited assessment of appropriateness of algorithms and analysis frameworks.

Reviewer #2 (Evidence, reproducibility and clarity):

Yabaji et al. investigated the effects of BMDMs stimulated with TNF from both WT and B6.Sst1S mice, which have previously been identified to contain the sst1 locus conferring susceptibility to Mycobacterium tuberculosis. They identified that B6.Sst1S macrophages show a superinduction of IFNß, which might be caused by increased c-Myc expression, expanding on the mechanistic insights made by the same group (Bhattacharya et al. 2021). Furthermore, prolonged TNF stimulation led to oxidative stress, which WT BMDMs could compensate for by the activation of the antioxidant defense via NRF2. On the other hand, B6.Sst1S BMDMs lack the expression of SP110 and SP140, co-activators of NRF2, and were therefore subjected to maintained oxidative stress. Yabaji et al. could link those findings to in vivo studies by correlating the presence of stressed and aberrantly activated macrophages within granulomas to the failure of Mtb control, as well as the progression towards necrosis. As the knowledge regarding Mtb progression and necrosis of granulomas is not yet well understood, findings that might help provide novel therapy options for TB are crucial. Overall, the manuscript has interesting findings with regard to macrophage responses in Mycobacteria tuberculosis infection.

However, in its current form there are several shortcomings, both with respect to the precision of the experiments and conclusions drawn.

In particular a) important controls are often missing, e.g. T-cells form non-immune mice in Fig. 6J, in F, effectivity of BCG in B6 mice in 6N; b) single experiments are shown throughout the manuscript, in particular western blots and histology without proper quantification and statistics, this is absolutely not acceptable; c) very few repetitions are shown in in vitro experiments, where there is no evidence for limitation in resources (usually not more than 3), it is not clear what "independent experiment means" - i.e. the robustness of the findings is questionable; d) data are often normalized multiple times, e.g. in the case of qPCR, and the methods of normalization are not clear (what house-keeping gene exactly?);

Moreover, experiments regarding IFN I signaling (e.g. short term TNF treatment of BMDMs to analyze LPO, making sure that the reporter mouse for IFNß works in vivo) and c-Myc (e.g. the increase after M-CSF addition might impact on other analysis as well and the experiments should be adjusted to control for this effect; MYC expression in the human samples) should be carefully repeated and evaluated to draw correct conclusions.

In addition, we would like to strongly encourage the authors to more precisely outline the experimental set-ups and figure legends, so that the reader can easily understand and follow them. In other words: The legends are - in part very - incomplete. In addition, the authors should be mindful of gene names vs. protein names and italicize where appropriate.

We appreciate a very thorough evaluation of our manuscript by this reviewer. Their insightful comments helped us improve the manuscript. As outlined below in point-by-point responses (1) we added important controls including isotype control antibodies in IFNAR blocking experiments and non-vaccinated T cells in T cell – macrophage interactions experiments; updated figure legends to indicate number of repeated experiment where a representative experiment is shown, numbers of mouse lungs and individual lesions, methods of data normalization, where it was missing. We also explained our in vitro experimental design and how we analyzed and excluded effects of media change and fresh CSF1 addition, by using a rest period before TNF stimulation and Mtb infection. The data shown in Suppl. Fig. 6C (previously Suppl. Fig. 5B) demonstrate that Myc levels induced by CSF1 return to the basal level at 12 h after media change. Our detailed in vitro protocol that contains these details has been published (Yabaji et al., STAR Protocols, 2022). We added new data demonstrating the ROS and LPO production at 6h of TNF stimulation, while the Ifnb1 mRNA super-induction occurred at 16 – 18 h, and edited the text to highlight these dynamics. The upregulation of Myc pathway in human samples does not necessarily mean the upregulation of Myc itself, it could be due to the dysregulation of downstream pathways. The upregulation of Myc pathway in the blood transcriptome associated with TB treatment failure most likely reflects greater proportion of immature cells in peripheral blood, possibly due to increased myelopoiesis. The detailed analysis of this cell populations in human patients is suggested by our findings but it is beyond the scope of this study.

The reviewer’s comments also suggested that a summary of our findings was necessary. The main focus of our study was to untangle connections between oxidative stress and Ifnb1 superinduction. It revealed that Myc hyperactivity caused partial deficiency of antioxidant defense leading to type I interferon pathway hyperactivity that in turn amplifies lipid peroxidation, thus establishing a vicious cycle driving inflammatory tissue damage.

Our laboratory worked on mechanisms of TB granuloma necrosis over more than two decades using genetic, molecular and immunological analyses in vitro and in vivo. It provided mechanistic basis for independent studies in other laboratories using our mouse model and further expanding our findings, thus supporting the reproducibility and robustness of our results and our lab’s expertise.

Specific comments to the experiments and data:

- Fig. 1E: Evaluation of differences in up- and downregulation between B6 and B6.Sst1S cells should highlight where these cells are within the heatmap, as it is only labelled with the clusters, or it should be depicted differently (in particular for cluster 1 and 2). Furthermore, a more simple labelling of the pathways would increase the readability of the data.

For our scRNAseq data presentation, we used formats accepted by computational community. To clarify Fig.1E, we added labels above B6 and B6.Sst1S-specific clusters.

- Fig. 2D, E: The staining legend is missing. For the quantification it is not clear what % total means. Is this based on the intensity or area? What do the dots represent in the bar chart? Is one data point pooled from several pictures? If not, the experiments need to be repeated, as three pictures might not be representative for evaluation.

- Fig. 2E: Statistics comparing B6/ B6,SsT1S with TNF (different) is required: Absence of induction is not a proof for a difference!

We included staining with NRF2-specific antibodies and performed area quantification per field using ImageJ to calculate the NRF2 total signal intensity per field. Each dot in the graph represents the average intensity of 3 fields in a representative experiment. The experiment was repeated 3 times. We included pairwise comparison of TNF-stimulated B6 and B6.Sst1S macrophages and updated the figure legend.

- Fig. 3E: Positive and negative control need to be depicted in the figure (see legend).

We have added the positive and negative controls for the determination of labile iron pool to the data in Fig. 3E and related Suppl. Fig. 3B and to Fig. 5D that also demonstrates labile iron determination.

- Fig. 3I: A quantification by flow cytometry or total cell counts are important, as 6% cell death in cell culture is a very modest observation. Otherwise, confocal images of the quantification would be a good addition to judge the specificity of the viability staining.

To validate the specificity of the viability staining method, we have provided fluorescent images as Suppl.Fig.3H. The main point of this experiment was to demonstrate a modest, but reproducible, increase in cell death in the sst1-mutant macrophages that suggested an IFNdependent oxidative damage. In our study, we did not focus on mechanisms of cell death, but on a state of chronic oxidative stress in the sst1 mutant live cells during TNF stimulation.

- Fig. 3I, J: What does one dot represent?

We performed this assay in 96 well format and each dot represent the % cell death in an individual well.

- Fig. 3K,L: For the B6 BMDMs it seems that p-cJun is highly increased at 12h in (L), while it is not in (K). On the other hand, for the B6.Sst1S BMDMs it peaks at 24h in (K), while in (L) it seems to at 12h. According to the data in (L) it seems that p-cJun is rather earlier and stronger activated in B6 BMDMs and has a weakened but prolonged activation in the B6.Sst1S BMDMs, which would not fit with your statement in the text that B6.Sst1S BMDMs show an upregulation.

These experiments need repetitions and quantification and statistiscs.

Fig. 3L: ASK1 seems to be higher at 12h for the B6 BMDMs and similar for both lines at 24h, which is not fitting to the statement in the text. ("Also, the ASK1 - JNK - cJun stress kinase axis was upregulated in B6.Sst1S macrophages, as compared to B6, after 12 - 36 h of TNF stimulation")

These experiments were repeated, and new data were added to highlight differences in ASK1 and c-Jun phosphorylation between B6 and B6.Sst1S at individual timepoints after TNF stimulation (presented in new Fig.3K). It demonstrated that after TNF stimulation the activation of stress kinases ASK1 and c-Jun initially increased in both genetic backgrounds. However, their upregulation was maintained exclusively in the sst1-susceptible macrophages from 24 to 36 h of TNF stimulation, while in the resistant macrophages their upregulation was transient. Thus, during prolonged TNF stimulation, B6.Sst1S macrophages experience stress that cannot be resolved, as evidenced by this kinetic analysis. The quantification of the band intensity was added to Western blot images above individual lanes.

Reviewer 2 pointed to missing isotype control antibodies in Fig.3 and Fig.4:

- Figure 3J: the isotype control for the IFNAR antibody is missing

- Figure 4E: It seems the isotype control itself has already an effect in the reduction of IFNb.

- Fig. 4H: It seems that the Isotype control antibody had an effect to increase 4-HNE (compared to TNF stimulated only).

We always include isotype control antibodies in our experiments because antibodies are known to modulate macrophage activation via binding to Fc receptor. To address the reviewer’s comments, we updated all panels that present the effects of IFNAR1 blockade with isotypematched non-specific control antibodies in the revised manuscript. Specifically, we included isotype control in Fig. 3M (previously Fig.3J), Fig.4I, Suppl.4E-G, Fig.6L-M), Suppl.Fig.7I (previously Suppl.Fig.6F).

- Fig.4A - C: "IFNAR1 blockade, however, did not increase either the NRF2 and FTL protein levels, or the Fth, Ftl and Gpx1 mRNA levels above those treated with isotype control antibodies"

Maybe not above the isotype but it is higher than the TNF alone stimulation at least for NRF2 at 8h and for Ftl at both time points. Why does the isotype already cause stimulation/induction of the cells? !These experiments need repetitions and quantification and statistics!

To determine specific effects of IFNAR blockade we compared effects of non-specific isotype control and IFNAR1-specific antibodies. In our experiments, the isotype control antibody modestly increased of Nrf2 and Ftl protein levels and the Fth and Ftl mRNA levels, but their effects were similar to the effect of IFNAR-specific antibody. The non-IFN -specific effects of antibodies, although are of potential biological significance, are modest in our model and their analysis is beyond the scope of this study.

- Fig.4H Was the AB added also at 12h post stimulation? Figure legend should be adjusted.

The IFNAR1 blocking antibodies and isotype control antibodies were added at 2 h after TNF stimulation in Fig.4H and 4I, as described in the corresponding figure legend. The data demonstrating effects of IFNAR blockade after 12, 24,and 33h of TNF stimulation are presented in Suppl.Fig.4 E-G.

- Figure 4I: How was the data measured here, i.e. what is depicted? The isotype control is missing. It seems a two-way ANOVA was used, yet it is stated differently. The figure legend should be revised, as Dunnett's multiple comparison would only check for significances compared to the control.

The microscopy images and bar graphs were updated to include isotype control and presented in Suppl. Fig.4E - G of the revised version. We also revised the statistical analysis to include correction for multiple comparisons.

- Figure 4C and subsequent: How exactly was the experiment done (house-keeping gene)?

We included the details in the figure legends of revised version. We quantified the gene expression by DDCt method using b-actin (for Fig. 4C-E) and 18S (For Fig. 4F and G) as internal controls.

- Figure 4D,E: Information on cells used is missing. Why the change in stimulation time? Did it not work after 12h? Then the experiments in A-C should be repeated for 16h.

The updated Fig. 4D and E present comparison of B6 and B6.Sst1S BMDMs clearly demonstrating significant difference between these macrophages in Ifnb1 mRNA expression 16 h after TNF stimulation, in agreement with our previous publication(Bhattacharya, et al., 2021). There we studied the time course of responses of B6 and B6.Sst1S macrophages to TNF at 2h intervals and demonstrated the divergence between their activation trajectories starting at 12 h of TNF stimulation Therefore, to reveal the underlying mechanisms we focus our analyses on this critical timepoint, i.e. as close to the divergence as possible. However, the difference between the strains in Ifnb1 mRNA expression achieved significance only by 16h of TNF stimulation. That is why we have used this timepoint for the Ifnb1 and Rsad2 analyses. It clearly shows that the superinduction was not driven by the positive feedback via IFNAR, as has been shown by the Ivashkiv lab for B6 wild type macrophages previously PMID 21220349.

- Figure 4E: It would be helpful to see if these transcripts are actually translated into protein levels, e.g. perform an ELISA. Authors state that IFNAR blockages does not alter the expression but you statistic says otherwise.

- The data for Ifnb expression (or better protein level) should be provided for B6 BMDMs as well.

We have previously reported the differences in Ifnb protein secretion (He et al., Plos Pathogens, 2013 and Bhattacharya et al., JCI 2021). We use mRNA quantification by qRT-PCR as a more sensitive and direct measurement of the sst1-mediated phenotype. The revised Fig.4D and E include responses of B6 in addition to the B6.Sst1S to demonstrate that the IFNAR blockade does not reduce the Ifnb1 mRNA levels in TNF-stimulated B6.Sst1S mutant to the B6 wild type levels. A slight reduction can be explained by a known positive feedback loop in the IFN-I pathway (see above). In this experiment we emphasized that the effect of the sst1 locus is substantially greater, as compared to the effect of the IFNAR blockade (Fig.4D), and updated the text accordingly.

- Fig. 4F: To what does the fold induction refer to? If it is again to unstimulated cells, then why is the induction now so much higher than in (E) where it was only 50x (now to 100x).

- Figure 4G: Again to what is the fold induction referring to? It seems your Fer-1 treatment only contains 2 data points. This needs to be fixed.

Yes, the fold induction was calculated by normalizing mRNA levels to untreated control incubated for the same time. Regarding the variation in Ifnb1 mRNA levels - a two-fold variation is not unusual in these experiments that may result in the Ifnb1 mRNA superinduction ranging from 50 -200-fold at this timepoint (16h). The graph in Fig.4G was modified to make all datapoints more visible.

- "These data suggest that type I IFN signaling does not initiate LPO in our model but maintains and amplifies it during prolonged TNF stimulation that, eventually, may lead to cell death". Data for a short term TNF stimulation are not shown, however, so it might impact also on the initiation of LPO.

- The overall conclusion drawn from Fig. 3 and 4 is not really clear with regard that IFN does not initiate LPO. Where is that shown? Data on earlier stimulation time points should be added to make this clear.

We demonstrated ROS production (new Suppl.Fig.3G) and the rate of LPO biosynthesis (new Suppl.Fig.4E-F) at 6 h post TNF stimulation, while the Ifnb1 superinduction occurs between 12-18 h post TNF stimulation. This temporal separation supports our conclusion that IFN-β superinduction does not initiate LPO. We clarified it in the text:

“Thus, Ifnb1 super-induction and IFN-I pathway hyperactivity in B6.Sst1S macrophages follow the initial LPO production, and maintain and amplify it during prolonged TNF stimulation”. (Previously: These data suggest that type I IFN signaling does not initiate LPO in our model). We also edited the conclusion in this section to explain the hierarchy of the sst1-regulated AOD and IFN-I pathways better:

“Taken together, the above experiments allowed us to reject the hypothesis that IFN-I hyperactivity caused the sst1-dependent AOD dysregulation. In contrast, they established that the hyperactivity of the IFN-I pathway in TNF-stimulated B6.Sst1S macrophages was itself driven by the initial dysregulation of AOD and iron-mediated lipid peroxidation. During prolonged TNF stimulation, however, the IFN-I pathway was upregulated, possibly via ROS/LPOdependent JNK activation, and acted as a potent amplifier of lipid peroxidation”.

We believe that these additional data and explanation strengthen our conclusions drawn from Figures 3 and 4.

- "A select set of mouse LTR-containing endogenous retroviruses (ERV's) (Jayewickreme et al, 2021), and non-retroviral LINE L1 elements were expressed at a basal level before and after TNF stimulation, but their levels in the B6.Sst1S BMDMs were similar to or lower than those seen in B6". This sentence should be revised as the differences between B6 and B6.Sst1S BMDMs seem small and are not there after 48h anymore. Are these mild changes really caused by the mutation or could they result from different housing conditions and/or slowly diverging genetically lines. How many mice were used for the analysis? Is there already heterogeneity between mice from the same line?

We agree with the reviewer that the data presented in Suppl.Fig.4 (Suppl.Fig.5 in the revised version) indicated no increase in single- and double-stranded transposon RNAs in the B6.Sst1S macrophages. The purpose of these experiment was to test the hypothesis that increased transposon expression might be responsible for triggering the superinduction of type I interferon response in TNF-stimulated B6.Sst1S macrophages. In collaboration with a transposon expert Dr. Nelson Lau (co-author of this manuscript) we demonstrated that transposon expression was not increased above the B6 level and, thus, rejected this attractive hypothesis. We explained the purpose of this experiment in the text and adequately described our findings as “the levels in the B6.Sst1S BMDMs were similar to or lower than those seen in B6”…and concluded that ” the above analyses allowed us to exclude the overexpression of persistent viral or transposon RNAs as a primary mechanism of the IFN-I pathway hyperactivity” in the sst1-mutant macrophages.

- Fig. 5A: Indeed, it even seems that Myc is upregulated for the mutant BMDMs. Yet, there are only 2 data points for B6 12h.

These experiments need repetitions and quantification and statistics.

We observed these differences in c-Myc mRNA levels by independent methods: RNAseq and qRT-PCR. The qRT-PCR experiments were repeated 3 times. A representative experiment in Fig.5A shows 3 data points for each condition. We reformatted the panel to make all data points clearly visible.

- Fig. 5B: Why would the protein level decrease in the controls over 6h of additional cultivation? Is this caused by fresh M-CSF? In this case maybe cells should be left to settle for one day before stimulating them to properly compare c-Myc induction. Comment on two c-Myc bands is needed. At 12h only the upper one seems increased for TNF stimulated mutant BMDMs compared to B6 BMDMs.

We agree with the reviewer’s point that cells need to be rested after media change that contains fresh CSF-1. Indeed, in Suppl.Fig.6C, we show that after media change containing 10% L929 supernatant (a source of CSF1) there is an increase in c-Myc protein levels that takes approximately 12 hours to return to baseline.

Our protocol includes resting period of 18-24 h after medium change before TNF stimulation.

We updated Methods to highlight this detail. Thus, the increase in c-Myc levels we observe at 12 h of TNF stimulation (Fig.5B) is induced by TNF, not the addition of growth factors, as further discussed in the text.

The two c-Myc bands observed in Fig.5B,I and J, are similar to patterns reported in previous studies that used the same commercial antibodies (PMIDs: 24395249, 24137534, 25351955). Whether they correspond to different c-Myc isoforms or post-translational modifications is unknown.

- Fig. 5A,B: It seems that not all the RNA is translated into protein, as c-Myc at 12h in the mutant BMDMs seems to be lower than at 6h, while the gene expression implicates it vice versa.

In addition to Fig.5B, the time course of Myc protein expression up to 24 h is presented in new panels Fig. 5I-5J. It demonstrates the gradual decrease of Myc protein levels. The observed dissociation between the mRNA and protein levels in the sst1-mutant BMDMs at 12 and 24 h is most likely due to translation inhibition as a result of the development of the integrated stress response, ISR (as shown in our previous publication by Bhattacharya et al., JCI, 2021). Translation of Myc is known to be particularly sensitive to the ISR (PMID18551192, PMID25079319, PMID28490664). Perhaps, the IFN-driven ISR may serve as a backup mechanism for Myc downregulation. We are planning to investigate these regulatory mechanisms in greater detail in the future.

- Fig. 5J: Indeed, the inhibitor seems to cause the downregulation of the proteins. Explanation?

This experiment was repeated twice and the average normalized densitometry values are presented in the updated Fig.5J. The main question addressed in this experiment was whether hyperactivity of JNK in TNF-stimulated sst1 mutant macrophages contributed to Myc upregulation, as had been previously shown in cancer. Comparing effects of JNK inhibition on phospho-cJun and c-Myc protein levels in TNF stimulated B6.Sst1S macrophages (updated Fig.5J), we rejected the hypotghesis that JNK activity might have a major role in c-Myc upregulation in sst1 mutant macrophages.

- "TNF stimulation tended to reduce the LPO accumulation in the B6 macrophages and to increase it in the B6.Sst1S ones" However, this is not apparent in Sup. Fig. 6B. Here it seems that there might be a significant increase.

Suppl.Fig.6B (currently Suppl.Fig.7B) shows the 4-HNE accumulation at day 3 post infection. The data obtained after 5 days of Mtb infection are shown in Fig.6A. We clarified this in the text: “By day 5 post infection, TNF stimulation induced significant LPO accumulation only in the B6.Sst1S macrophages (Fig.6A)”.

- Fig. 6B: Mtb and 4-HNE should be shown in two different channels in order to really assign each staining correctly.

What time point is this? Are the mycobacteria cleared at MOI1, since it looks that there are fewer than that? How does this look like for the B6 BMDMs? Are there even less mycobacteria?

We included B6 infection data to the updated Fig.6B and added Suppl.Fig.7C and 7D that address this reviewer’s comment. The data represent day 5 of Mtb infection as indicated in the updated Fig.6B and Suppl.Fig.7C and 7D legends. New Suppl.Fig.7D shows quantification of replicating Mtb using Mtb replication reporter stain expressing single strand DNA binding protein GFP fusion, as described in Methods. We observed fewer Mtb and a lower percentage of replicating Mtb in B6 macrophages, but we did not observe a complete Mtb elimination in either background.

We used red fluorescence for both Mtb::mCherry and 4-HNE staining to clearly visualize the SSB-GFP puncta in replicating Mtb DNA. In the revised manuscript, we have included the relevant channels in Suppl. Fig.7C and D to demonstrate clearly distinct patterns of Mtb::mCherry and 4-HNE signals. We did not aim to quantify the 4-HNE signal intensity in this experiment. For the 4-HNE quantification we use Mtb that expressed no reporter proteins (Fig.6A-B and Suppl.Fig.7A-B).

- Fig 6E: In the context of survival a viability staining needs to be included, as well as the data from day 0. Then it needs to be analyzed whether cell numbers remain the same from D0 or if there is a change.

We updated Fig.6 legend to indicate that the cell number percentages were calculated based on the number of cells at Day 0 (immediately after Mtb infection). We routinely use fixable cell death staining to enumerate cell death to exclude artifacts due to cell loss. Brief protocol containing this information is included in Methods section. The detailed protocol including normalization using BCG spike has been published – Yabaji et al, STAR Protocols, 2022. Here we did not present dead cell percentage as it remained low and we did not observe damage to macrophage monolayers. The fold change of Mtb was calculated after normalization using Mtb load at Day 0 after infection and washes.

"The 3D imaging demonstrated that YFP-positive cells were restricted to the lesions, but did not strictly co-localize with intracellular Mtb, i.e. the Ifnb promoter activity was triggered by inflammatory stimuli, but not by the direct recognition of intracellular bacteria. We validated the IFNb reporter findings using in situ hybridization with the Ifnb probe, as well as anti-GFP antibody staining (Suppl.Fig.8B - E)." The colocalization is not present within the tissue sections. It seems that the reporter line does not show the same staining pattern in vivo as the IFNß probe or the anti GFP antibody staining. The reporter line has to be tested for the specificity of the staining. Furthermore, to state that it was restricted to the lesions, an uninvolved tissue area needs to be depicted.

The Ifnb secreting cells are notoriously difficult to detect in vivo using direct staining of the protein. Therefore, lineage tracing of reporter expression are used as surrogates. The Ifnb reporter used in our study has been developed by the Locksley laboratory (Scheu et al., PNAS, 2008, PMID: 19088190) and has been validated in many independent studies. The reporter mice express the YFP protein under the control of the Ifnb1 promoter. The YFP protein accumulates within the cells, while Ifnb protein is rapidly secreted and does not accumulate in the producing cells in appreciable amounts. Also, the kinetics of YFP protein degradation is much slower as compared to the endogenous Ifnb1 mRNA that was detected using in situ hybridization. Thus, there is no precise spatiotemporal coincidence of these readouts in Ifnb expressing cells in vivo. However, this methodology more closely reflect the Ifnb expressing cells in vivo, as compared to a Cre-lox mediated lineage tracing approach. In the revised manuscript we demonstrate that both YFP and mRNA signals partially overlap (Suppl.Fig.12B). In Suppl.Fig.12B. we also included a new panel showing no YFP expression in the uninvolved area of the reporter mice infected with Mtb. The YFP expression by activated macrophages is demonstrated by co-staining with Iba1- and iNOS-specific antibodies (new Fig.7D and Suppl.Fig.13A). Our specificity control also included TB lesions in mice that do not carry the YFP reporter and did not express the YFP signal, as reported elsewhere (Yabaji et al., BioRxiv, https://doi.org/10.1101/2023.10.17.562695).

- Are paucibacillary and multibacillary lesions different within the same animal or does one animal have one lesion phenotype? If that is the case, what is causing the differences between mice? Bacterial counts for the mice are required.

The heterogeneity of pulmonary TB lesions has been widely acknowledged in clinic and highlighted in recent experimental studies. In our model of chronic pulmonary TB (described in detail in Yabaji et al., https://doi.org/10.1101/2025.02.28.640830 and https://doi.org/10.1101/2023.10.17.562695) the development of pulmonary TB lesions is not synchronized, i.e. the lesions are heterogeneous between the animals and within individual animals at the same timepoint. Therefore, we performed a lesion stratification where individual lesions were classified by a certified veterinary pathologist in a blinded manner based on their morphology (H&E) and acid fast staining of the bacteria, as depicted in Suppl.Fig.8.

- "Among the IFN-inducible genes upregulated in paucibacillary lesions were Ifi44l, a recently described negative regulator of IFN-I that enhances control of Mtb in human macrophages (DeDiego et al, 2019; Jiang et al, 2021) and Ciita, a regulator of MHC class II inducible by IFNy, but not IFN-I (Suppl.Table 8 and Suppl.Fig.10 D-E)." Why is Sup. Fig. 10 D, E referred to? The figure legend is also not clear, e.g. what means "upregulated in a subset of IFN-inducible genes"? Input for the hallmarks needs to be defined.

These data is now presented in Suppl.Fig.11 and following the reviewer’s comment, we moved reference to panels 11D – E up to previous paragraph in the main text, where it naturally belongs . We also edited the figure legend to refer to the list of IFN-inducible genes compiled from the literature that is discussed in the text. We appreciate the reviewer’s suggestion that helped us improve the text clarity. The inputs for the Hallmark pathway analysis are presented in Suppl.Tables 7 and 8, as described in the text.

- Fig. 7C: Single channel pictures are required as it is hard to see the differences in staining with so many markers. Why is there no iNOS expression in the bottom row? What does the rectangle indicate on the bottom right? As black is chosen for DAPI, it is not visible at all. In case the signal is needed a visible a color should be chosen.

We thoroughly revised this figure to address the reviewer’s concern about the lack of clarity. We provide individual channels for each marker in Fig.7D – E and Suppl.Fig.13F. We have to use DAPI in these presentation in gray scale to better visualize other markers.

- "In the advanced lesions these markers were primarily expressed by activated macrophages (Iba1+) expressing iNOS and/or Ifny (YFP+)(Fig.7D)" Iba1 is needed in the quantification. Based on the images, iNOS seems to be highly produced in Iba1 negative cells. Which cells do produce it then? Flow cytometry data for this quantification are required. This would allow you to specifically check which cells express the markers and allow for a more precise analysis of double positive cells.

Currently these data demonstrating the co-localization of stress markers phospho-c-Jun and Chac1 with YFP are presented in Fig.7E (images) and Suppl.Fig.13D (quantification). The co-localization of stress markers phospho-cJun and Chac1 with iNOS is presented in Suppl.Fig.13F (images) and Suppl.Fig.13E (quantification). We agree that some iNOS+ cells are Iba1-negative (Fig.7D). We manually quantified percentages of Iba1+iNOS+ double positive cells and demonstrated that they represent the majority of the iNOS+ population(Suppl.Fig.13A). Regarding the required FACS analysis, we focus on spatial approaches because of the heterogeneity of the lesions that would be lost if lungs are dissociated for FACS. We are working on spatial transcriptomics at a single cell resolution that preserves spatial organization of TB lesions to address the reviewer’s comment and will present our results in the future.

- Results part 6: In general, can you please state for each experiment at what time point mice were analyzed? You should include an additional macrophage staining (e.g. MerTK, F4/80), as alveolar macrophages are not staining well for Iba1 and you might therefore miss them in your IF microscopy. It would be very nice if you could perform flow cytometry to really check on the macrophages during infection and distinguish subsets (e.g. alveolar macrophages, interstitial macrophages, monocytes).

We have included the details of time post infection in figure legends for Fig.7, Suppl.Figures 8, 9, 12B, 13, 14A of the revised manuscript. We have performed staining with CD11b, CD206 and CD163 to differentiate the recruited and lung resident macrophages and determined that in chronic pulmonary TB lesions in our model the vast majority of macrophages are recruited CD11b+, but not resident (CD206+ and CD163+) macrophages. These data is presented in another manuscript (Yabaji et al., BioRxiv https://doi.org/10.1101/2023.10.17.562695).

- Spatial sequencing: The manuscript would highly profit from more data on that. It would be very interesting to check for the DEGs and show differential spatial distribution. Expression of marker genes should be inferred to further define macrophage subsets (e.g. alveolar macrophages, interstitial macrophages, recruited macrophages) and see if these subsets behave differently within the same lesion but also between the lesions. Additional bioinformatic approaches might allow you to investigate cell-cell interactions. There is a lot of potential with such a dataset, especially from TB lesions, that would elevate your findings and prove interesting to the TB field.

- "Thus, progression from the Mtb-controlling paucibacillary to non-controlling multibacillary TB lesions in the lungs of TB susceptible mice was mechanistically linked with a pathological state of macrophage activation characterized by escalating stress (as evidenced by the upregulation phospho-cJUN, PKR and Chac1), the upregulation of IFNβ and the IFN-I pathway hyperactivity, with a concurrent reduction of IFNγ responses." To really show the upregulation within macrophages and their activation, a more detailed IF microscopy with the inclusion of additional macrophage markers needs to be provided. Flow cytometry would enable analysis for the differences between alveolar and interstitial macrophages, as well as for monocytes. As however, it seems that the majority of iNOS, as well as the stress associated markers are not produced by Iba1+ cells. Analyzing granulocytes and T lymphocytes should be considered.

We appreciate the reviewer’s suggestion. Indeed, our model provides an excellent opportunity to investigate macrophage heterogeneity and cell interactions within chronic TB lesions. We are working on spatial transcriptomics at a single cell resolution that would address the reviewer’s comment and will present our results in the future.

In agreement with classical literature the overwhelming majority of myeloid cells in chronic pulmonary TB lesions is represented by macrophages. Neutrophils are detected at the necrotic stage, but our study is focused on pre-necrotic stages to reveal the earlier mechanisms predisposing to the necrotization. We never observed neutrophils or T cells expressing iNOS in our studies.

- It's mentioned in the method section that controls in the IF staining were only fixed for 10min, while the infected cells were fixed for 30min. Consistency is important as the PFA fixation might impact on the fluorescence signal. Therefore, controls should be repeated with the same fixation time.

We have carefully considered the impact of fixation time on fluorescence and have separately analyzed the non-infected and infected samples to address this concern. For the non-infected samples, we examined the effect of TNF in both B6 and B6.Sst1S backgrounds, ensuring that a consistent fixation protocol (10 min) was applied across all experiments without Mtb infection.

For the Mtb infection experiments, we employed an optimized fixation protocol (30 min) to ensure that Mtb was killed before handling the plates, which is critical for preserving the integrity of the samples. In this context, we compared B6 and B6.Sst1S samples to evaluate the effects of fixation and Mtb infection on lipid peroxidation (LPO) induction.

We believe this approach balances the need for experimental consistency with the specific requirements for handling infected cells, and we have revised the manuscript to reflect this clarification.

- Reactive oxygen species levels should be determined in B6 and B6.Sst1S BMDMs (stimulated and unstimulated), as they are very important for oxidative stress.

We have conducted experiments to measure ROS production in both B6 and B6.Sst1S BMDMs and demonstrated higher levels of ROS in the susceptible BMDMs after prolonged TNF stimulation (new Fig.3I-J and Suppl. Fig. 3G). Additionally, we have previously published a comparison of ROS production between B6 and B6.Sst1S by FACS (PMID: 33301427), which also supports the findings presented here.

- Sup. Fig 2C: The inclusion of an unstimulated control would be advisable in order to evaluate if there are already difference in the beginning.

We have included the untreated control to the Suppl. Fig. 2C (currently Suppl. Fig. 2D) in the revised manuscript.

- Sup. Fig. 3F: Why is the fold change now lower than in Fig. 4D (fold change of around 28 compared to 120 in 4D)?

The data in Fig.4D (Fig.4E in the revised manuscript) and Suppl.Fig.3F (currently Suppl.Fig.4C) represent separate experiments and this variation between experiments is commonly observed in qRT-PCR that is affected by slight variations in the expression in unsimulated controls used for the normalization and the kinetics of the response. This 2-4 fold difference between same treatments in separate experiments, as compared to 30 – 100 fold and higher induction by TNF does not affect the data interpretation.

- Sup. Fig. 5C, D: The data seems very interesting as you even observe an increase in gene expression. Data for the B6 mice should be evaluated for increase to a similar level as the TNF treated mutants. Data on the viability of the cells are necessary, as they no longer receive MCSF and might be dying at this point already.

To ensure that the observed effects were not confounded by cytotoxicity, we determined non-toxic concentrations of the CSF1R inhibitors during 48h of incubation and used them in our experiments that lasted for 24h. To address this valid comment, we have included cell viability data in the revised manuscript to confirm that the treatments did not result in cell death (Suppl. Fig. 6D). This experiment rejected our hypothesis that CSF1 driven Myc expression could be involved in the Ifnb superinduction. Other effects of CSF1R inhibitors on type I IFN pathway are intriguing but are beyond the scope of this study.

- Sup. Fig 12: the phospho-c-Jun picture for (P) is not the same as in the merged one with Iba1. Double positive cells are mentioned to be analyzed, but from the staining it appears that P-c-Jun is expressed by other cells. You do not indicate how many replicates were counted and if the P and M lesions were evaluated within the same animal. What does the error bar indicate? It seems unlikely from the plots that the double positive cells are significant. Please provide the p values and statistical analysis.

We thank the reviewer for bringing this inadvertent field replacement in the single phospho-cJun channel to our attention. However, the quantification of Iba1+phospho-cJun+ double positive cells in Suppl.Fig.12 and our conclusions were not affected. In the revised manuscript, images and quantification of phospho-cJun and Iba1 co-expression are shown in new Suppl.Fig.13B and C, respectively. We have also updated the figure legends to denote the number of lesions analyzed and statistical tests. Specifically, lesions from 6–8 mice per group (paucibacillary and multibacillary) were evaluated. Each dot in panels Suppl.Fig.13 represent individual lesions.

- Sup. Fig. 13D (suppl.Fig.15D now): What about the expression of MYC itself? Other parts of the signaling pathway should be analyzed(e.g. IFNb, JNK)?

The difference in MYC mRNA expression tended to be higher in TB patients with poor outcomes, but it was not statistically significant after correction for multiple testing. The upregulation of Myc pathway in the blood transcriptome associated with TB treatment failure most likely reflects greater proportion of immature cells in peripheral blood, possibly due to increased myelopoiesis. Pathway analysis of the differentially expressed genes revealed that treatment failures were associated with the following pathways relevant to this study: NF-kB Signaling, Flt3 Signaling in Hematopoietic Progenitor Cells (indicative of common myeloid progenitor cell proliferation), SAPK/JNK Signaling and Senescence (possibly indicative of oxidative stress). The upregulation of these pathways in human patients with poor TB treatment outcomes correlates with our findings in TB susceptible mice.

- In the mfIHC you he usage of anti-mouse antibodies is mentioned. Pictures of sections incubated with the secondary antibody alone are required to exclude the possibility that the staining is not specific. Especially, as this data is essential to the manuscript and mouse-antimouse antibodies are notorious for background noise.

We are well aware of the technical difficulties associated with using mouse on mouse staining. In those cases, we use rabbit anti-mouse isotype specific antibodies specifically developed to avoid non-specific background (Abcam cat#ab133469). Each antibody panel for fluorescent multiplexed IHC is carefully optimized prior to studies. We did not use any primary mouse antibodies in the final version of the manuscript and, hence, removed this mention from the Methods.

- In order to tie the story together, it would be interesting to treat infected mice with an INFAR antibody, as well as perform this experiment with a Myc antibody. According to your data, you might expect the survival of the mice to be increased or bacterial loads to be affected.

In collaboration with the Vance laboratory, we tested effects of type I IFN pathway inhibition in B6.Sst1S mice on TB susceptibility: either type I receptor knockout or blocking antibodies increased their resistance to virulent Mtb (published in Ji et al., 2019; PMID 31611644). Unfortunately, blocking Myc using neutralizing antibodies in vivo is not currently achievable. Specifically blocking Myc using small molecule inhibitors in vivo is notoriously difficult, as recognized in oncology literature. We consider using small molecule inhibitors of either Myc translation or specific pathways downstream of Myc in the future.

- It is surprising that you not even once cite or mention your previous study on bioRxiv considering the similarity of the results and topic (https://doi.org/10.1101/2020.12.14.422743). Is not even your Figure 1I and Figure 2 J, K the same as in that study depicted in Figure 4?

The reviewer refers to the first version of this manuscript uploaded to BioRxiv, but it has never been published. We continued this work and greatly expanded our original observations, as presented in the current manuscript. Therefore, we do not consider the previous version as an independent manuscript and, therefore, do not cite it.

- Please revise spelling of the manuscript and pay attention to write gene names in italics

Thank you, we corrected the gene and protein names according to current nomenclature.

Minor points:

- Fig. 1: Please provide some DEGs that explain why you used this resolution for the clustering of the scRNAseq data and that these clusters are truly distinct from each other.

Differential gene expression in clusters is presented in Suppl.Fig.1C (interferon response) and Suppl.Fig.1D (stress markers and interferon response previously established in our studies).

- Fig. 1F: What do the two lines represent (magenta, green)?

The lines indicate pseudotime trajectories of B6 (magenta) and B6.Sst1S (green) BMDMs.

- Fig. 1F, G: Why was cluster 6 excluded?

This cluster was not different between B6 and B6.Sst1S, so it was not useful for drawing the strain-specific trajectories.

- Fig. 1E, G, H: The intensity scales are missing. They are vital to understand the data.

We have included the scale in revised manuscript (Fig.1E,G,H and Suppl.Fig.1C-D).

- Fig. 2G-I: please revise order, as you first refer to Fig. 2H and I

We revised the panels’ order accordingly

- Fig. 5: You say the data represents three samples but at least in D and E you have more. Please revise. Why do you only include at (G) the inhibitor only control?

We added the inhibitor only controls to Fig. 5D - H. We also indicated the number of replicates in the updated Fig.5 legend.

- Figure 7A, Sup. Fig. 8: Are these maximum intensity projection? Or is one z-level from the 3D stack depicted?

The Fig. 7A shows 3D images with all the stacks combined.

- Fig. 7B: What do the white boxes indicate?

We have removed this panel in the revised version and replaced it with better images.

- Sup. Fig. 1A: The legend for the staining is missing

The Suppl. Fig.1A shows the relative proportions of either naïve (R and S) or TNFstimulated (RT and ST) B6 or B6.Sst1S macrophages within individual single cell clusters depicted in Fig.1B. The color code is shown next to the graph on the right.

- Sup. Fig. 1B: The feature plots are not clear: The legend for the expression levels is missing. What does the heading means?

We updated the headings, as in Fig.1C. The dots represent individual cells expressing Sp110 mRNA (upper panels) and Sp140 mRNA (lower panels).

- Sup. Fig. 3C: The scale bar is barely visible.

We resized the scale bar to make it visible and presented in Suppl. Fig.3E (previously Suppl. Fig.3C).

- Sup. Fig. 3D: There is not figure legend or the legend to C-E is wrong.

- Sup. Fig. 3F, G: You do not state to what the data is relative to.

We identified an error in the Suppl.Fig.3 legend referring to specific panels. The Suppl.Fig.3 legend has been updated accordingly. New panels were added and Suppl.Fig.3-G panels are now Suppl.Fig.4C-D.

- Sup. Fig. 3H: It seems you used a two-way ANOVA, yet state it differently. Please revise the figure legend, as Dunnett's multiple comparison would only check for significances compared to the control.

Following the reviewer’s comment, we repeated statistical analysis to include correction for multiple comparisons and revised the figure and legend accordingly.

- Sup. Fig. 4A, B: It is not clear what the lines depict as the legend is not explained. Names that are not required should be changed to make it clear what is depicted (e.g. "TE@" what does this refer to?)

This previous Sup. Fig 4 is now Sup. Fig. 5. The “TE@” is a leftover label from the bioinformatics pipeline, referring to “Transposable Element”. We apologize for this confusion and have removed these extraneous labels. We have also added transposon names of the LTR (MMLV30 and RTLV4) and L1Md to Suppl.Fig.5A and 5B legend, respectively.

- Sup. 4B: What does the y-scale on the right refer to?

We apologize for the missing label for the y-scale on the right which represents the mRNA expression level for the SetDB1 gene, which has a much lower steady state level than the LINE L1Md, so we plotted two Y-scales to allow both the gene and transposon to be visualized on this graph.

- Sup. 4C: Interpretation of the data is highly hindered by the fact that the scales differ between the B6 and B6.Sst1. The scales are barely visible.

We apologize for the missing labels for the y-scales of these coverage plots, which were originally meant to just show a qualitative picture of the small RNA sequencing that was already quantitated by the total amounts in Sup. 4B. We have added thee auto-scaled Y-scales to Sup. 4C and improved the presentation of this figure.

- Sup. Fig. 5A, B: Is the legend correct? Did you add the antibody for 2 days or is the quantification from day 3?

We recognize that the reviewer refers to Suppl.Fig.6A-B (Suppl.Fig.7A-B in the revised manuscript). We did not add antibodies to live cells. The figure legend describes staining with 4HNE-specific antibodies 3 days post Mtb infection.

- Sup. Fig. 8A: Are the "early" and "intermediate" lesions from the same time points? What are the definitions for these stages?

We discussed our lesion classification according to histopathology and bacterial loads above. Of note, in the revised manuscript we simplified our classification to denote paucibacillary and multibacillary lesions only. We agree with reviewers that designation lesions as early, intermediate and advanced lesions were based on our assumptions regarding the time course of their progression from low to high bacterial loads.

- Sup. Fig. 8E: You should state that the bottom picture is an enlargement of an area in the top one. Scale bars are missing.

We replaced this panel with clearer images in Suppl.Fig.12B.

- Sup. Fig. 11A: The IF staining is only visible for Iba and iNOS. Please provide single channels in order to make the other staining visible.

Suppl.Fig.11A (now Suppl.Fig.13B) shows the low-magnification images of TB lesions. In the Fig. 7 and Suppl. Fig. 13F of the revised manuscript we provided images for individual markers.

- Sup. Fig. 13A (Suppl.Fig.15A now): Your axis label is not clear. What do the numbers behind the genes indicate? Why did you choose oncogene signatures and not inflammatory markers to check for a correlation with disease outcome?

X axis of Suppl.Fig.15A represent pre-defined molecular signature gene sets MSigDB) in Gene Set Enrichment Analysis (GSEA) database (https://www.gseamsigdb.org/gsea/msigdb). On Y axis is area under curve (AUC) score for each gene set.

- Sup. 13D(Suppl.Fig.15D now): Maybe you could reorder the patients, so that the impression is clearer, as right now only the top genes seem to show a diverging gene signature, while the rest gives the impression of an equal distribution.

The Myc upregulated gene set myc_up was identified among top gene sets associated with treatment failure using unbiased ssGSEA algorithm. We agree with the reviewer that not every gene in the myc_up gene set correlates with the treatment outcome. But the association of the gene set is statistically significant, as presented in Suppl.Fig.15B – C.

- The scale bars for many microscopy pictures are missing.

We have included clearly visible scale bars to all the microscopy images in the revised version.

- The black bar plots should be changed (e.g. in color), since the single data points cannot be seen otherwise.

- It would be advisable that a consistent color scheme would be used throughout the manuscript to make it easier to identify similar conditions, as otherwise many different colours are not required and lead right now rather to confusion (e.g. sometimes a black bar refers to BMDMs with and sometimes without TNF stimulation, or B6 BMDMs). Furthermore, plot sizes and fonts should be consistent within the manuscript (including the supplemental data)

We followed this useful suggestion and selected consistent color codes for B6 and B6.Sst1S groups to enhance clarity throughout the revised manuscript.

Within the methods section:

- At which concentration did you use the IFNAR antibody and the isotype?

We updated method section by including respective concentrations in the revised manuscript.

- Were mice maintained under SPF conditions? At what age where they used?

Yes, the mice are specific pathogen free. We used 10 - 14 week old mice for Mtb infection.

- The BMDM cultivation is not clear. According to your cited paper you use LCCM but can you provide how much M-CSF it contains? How do you make sure that amounts are the same between experiments and do not vary? You do not mention how you actually obtain this conditioned medium. Is there the possibility of contamination or transferred fibroblasts that would impact on the data analysis? Is LCCM also added during stimulation and inhibitor treatment?

We obtain LCCM by collecting the supernatant from L929 cell line that form confluent monolayer according to well-established protocols for LCCM collection. The supernatants are filtered through 0.22 micron filters to exclude contamination with L929 cells and bacteria. The medium is prepared in 500 ml batches that are sufficient for multiples experiments. Each batch of L929-conditioned medium is tested for biological activity using serial dilutions.

- How was the BCG infection performed? How much bacteria did you use? Which BCG strain was used?

We infected mice with M. bovis BCG Pasteur subcutaneously in the hock using 10⁶ CFU per mouse.

- At what density did you seed the BMDMs for stimulation and inhibitor experiments?

In 96 well plates, we seed 12,000 cells per well and allow the cells to grow for 4 days to reach confluency (approximately 50,000 cells per well). For a 6-well plate, we seed 2.5 × 10⁵ cells per well and culture them for 4 days to reach confluency. For a 24-well plate, we seed 50,000 cells per well and keep the cells in media for 4 days before starting any treatments. This ensures that the cells are in a proliferative or near-confluent state before beginning the stimulation or inhibitor treatments. Our detailed protocol is published in STAR Protocols (Yabaji et al., 2022; PMID 35310069).

- What machine did you use to perform the bulk RNA sequencing? How many replicates did you include for the sequencing?

For bulk sequencing we used 3 RNA samples for each condition. The samples were sequenced at Boston University Microarray & Sequencing Resource service using Illumina NextSeq^TM 2000 instrument.

- How many replicates were used for the scRNA sequencing? Why is your threshold for the exclusion of mitochondrial DNA so high? A typical threshold of less than 5% has been reported to work well with mouse tissue.

We used one sample per condition. For the mitochondrial cutoff, we usually base it off of the total distribution. There is no "universal" threshold that can be applied to all datasets. Thresholds must be determined empirically.

- You do not mention how many PCAs were considered for the scRNA sequencing analysis.

We considered 50 PCAs, this information was added to Methods

- You should name all the package versions you used for the scRNA sequencing (e.g. for the slingshot, VAM package)

The following package versions were used: Seurat v4.0.4, VAM v1.0.0, Slingshot v2.3.0, SingleCellTK v2.4.1, Celda v1.10.0, we added this information to Methods.

- You mention two batches for the human samples. Can you specify what the two batches are?

Human blood samples were collected at five sites, as described in the updated Methods section and two RNAseq batches were processed separately that required batch correction.

- At which temperature was the IF staining performed?

We performed the IF at 4oC. We included the details in revised version.

Reviewer #2 (Significance):

Overall, the manuscript has interesting findings with regard to macrophage responses in Mycobacteria tuberculosis infection.

However, in its current form there are several shortcomings, both with respect to the precision of the experiments and conclusions drawn.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary

The authors use a mouse model designed to be more susceptible to M.tb (addition of sst1 locus) which has granulomatous lesions more similar to human granulomas, making this mouse highly relevant for M.tb pathogenesis studies. Using WT B6 macrophages or sst1B6 macrophages, the authors seek to understand the how the sst1 locus affects macrophage response to prolonged TNFa exposure, which can occur during a pro-inflammatory response in the lungs. Using single cell RNA-seq, revealed clusters of mutant macrophages with upregulated genes associated with oxidative stress responses and IFN-I signaling pathways when treated with TNF compared to WT macs. The authors go on to show that mutant macrophages have decreased NRF2, decreased antioxidant defense genes and less Sp110 and Sp140. Mutant macrophages are also more susceptible to lipid peroxidation and ironmediated oxidative stress. The IFN-I pathway hyperactivity is caused by the dysregulation of iron storage and antioxidant defense. These mutant macrophages are more susceptible to M.tb infection, showing they are less able to control bacterial growth even in the presence of T cells from BCG vaccinated mice. The transcription factor Myc is more highly expressed in mutant macs during TNF treatment and inhibition Myc led to better control of M.tb growth. Myc is also more abundant in PBMCs from M.tb infected humans with poor outcomes, suggesting that Myc should be further investigated as a target for host-directed therapies for tuberculosis.

Major Comments

Isotypes for IF imaging and confocal IF imaging are not listed, or not performed. It is a concern that the microscopy images throughout the manuscript do not have isotype controls for the primary antibodies.

Fig 4 (and later) the anti-IFNAR Ab is used along with the Isotype antibody, Fig 4I does not show the isotype. Use of the isotype antibody is also missing in later figures as well as Fig 3J. Why was this left off as the proper control for the Ab?

We addressed the comment in revised manuscript as described above in summary and responses to reviewers 1 and 2. Isotype controls for IFNAR1 blockade were included in Fig.3M (previously 3J), Fig. 4I, Suppl.Fig.4G (previously Fig.4I), and updated Fig.4C-E, Fig.6L-M, Suppl.Fig.4F-G, 7I.

Conclusions drawn by the authors from some of the WB data are worded strongly, yet by eye the blots don't look as dramatically different as suggested. It would be very helpful to quantify the density of bands when making conclusions. (for example, Fig 4A).

We added the densitometry of Western blot values after normalization above each lane in Fig.2A-C, Fig.3C-D and 3K; Fig.4A-B, Fig.5B,C,I,J.

Fig 5A is not described clearly. If the gene expression is normalized to untreated B6 macs, then the level of untreated B6 macs should be 1. In the graph the blue bars are slightly below 1, which would not suggest that levels "initially increased and subsequently downregulated" as stated in the text. It seems like the text describes the protein expression but not the RNA expression. Please check this section and more clearly describe the results.

We appreciate the reviewer’s comment and modified the text to specify the mRNA and protein expression data, as follows:

“We observed that Myc was regulated in an sst1-dependent manner: in TNF-stimulated B6 wild type BMDMs, c-Myc mRNA was downregulated, while in the susceptible macrophages c-Myc mRNA was upregulated (Fig.5A). The c-Myc protein levels were also higher in the B6.Sst1S cells in unstimulated BMDMs and 6 – 12 h of TNF stimulation (Fig.5B)”.

Also, why look at RNA through 24h but protein only through 12h? If c-myc transcripts continue to increase through 24h, it would be interesting to see if protein levels also increase at this later time point.

The time-course of Myc expression up to 24 h is presented in new panels Fig. 5I-5J It demonstrates the decrease of Myc protein levels at 24 h. In the wild type B6 BMDMs the levels of Myc protein significantly decreased in parallel with the mRNA suppression presented in Fig.5A. In contrast , we observed the dissociation of the mRNA and protein levels in the _sst1_mutant BMDMs at 12 and 24 h, most likely, because the mutant macrophages develop integrated stress response (as shown in our previous publication by Bhattacharya et al., JCI, 2021) that is known to inhibit Myc mRNA translation.

Fig 5J the bands look smaller after D-JNK1 treatment at 6 and 12h though in the text is says no change. Quantifying the bands here would be helpful to see if there really is no difference.

This experiment was repeated twice, and the average normalized densitometry values are presented in the updated Fig.5J. The main question addressed in this experiment was whether the hyperactivity of JNK in TNF-stimulated sst1 mutant macrophages contributed to Myc upregulation, as was previously shown in cancer. Comparing effects of JNK inhibition on phospho-cJun and c-Myc protein levels in TNF stimulated B6.Sst1S macrophages (updated Fig.5J), we concluded that JNK did not have a major role in c-Myc upregulation in this context.

Section 4, third paragraph, the conclusion that JNK activation in mutant macs drives pathways downstream of Myc are not supported here. Are there data or other literature from the lab that supports this claim?

This statement was based on evidence from available literature where JNK was shown to activate oncogens, including Myc. In addition, inhibition of Myc in our model upregulated ferritin (Fig.Fig.5C), reduced the labile iron pool, prevented the LPO accumulation (Fig.5D - G) and inhibited stress markers (Fig.5H). However, we do not have direct experimental evidence in our model that Myc inhibition reduces ASK1 and JNK activities. Hence, we removed this statement from the text and plan to investigate this in the future.

Fig 6N Please provide further rationale for the BCG in vivo experiment. It is unclear what the hypothesis was for this experiment.

In the current version BCG vaccination data is presented in Suppl.Fig.14B. We demonstrate that stressed BMDMs do not respond to activation by BCG-specific T cells (Fig.6J) and their unresponsiveness is mediated by type I interferon (Fig.6L and 6M). The observed accumulation of the stressed macrophages in pulmonary TB lesions of the sst1-susceptible mice (Fig.7E, Suppl.Fig.13 and 14A) and the upregulation of type I interferon pathway (Fig.1E,1G, 7C), Suppl.Fig.1C and 11) suggested that the effect of further boosting T lymphocytes using BCG in Mtb-infected mice will be neutralized due to the macrophage unresponsiveness. This experiment provides a novel insight explaining why BCG vaccine may not be efficient against pulmonary TB in susceptible hosts.

The in vitro work is all concerning treatment with TNFa and how this exposure modifies the responses in B6 vs sst1B6 macrophages; however, this is not explored in the in vivo studies. Are there differences in TNFa levels in the pauci- vs multi-bacillary lesions that lead to (or correlate with) the accumulation of peroxidation products in the intralesional macrophages. How to the experiments with TNFa in vitro relate back to how the macrophages are responding in vivo during infection?

Our investigation of mechanisms of necrosis of TB granulomas stems from and supported by in vivo studies as summarized below.

This work started with the characterization necrotic TB granulomas in C3HeB/FeJ mice in vivo followed by a classical forward genetic analysis of susceptibility to virulent Mtb in vivo.

That led to the discovery of the sst1 locus and demonstration that it plays a dominant role in the formation of necrotic TB granulomas in mouse lungs in vivo. Using genetic and immunological approaches we demonstrated that the sst1 susceptibility allele controls macrophage function in vivo (Yan, et al., J.Immunol. 2007) and an aberrant macrophage activation by TNF and increased production of Ifn-b in vitro (He et al. Plos Pathogens, 2013). In collaboration with the Vance lab we demonstrated that the type I IFN receptor inactivation reduced the susceptibility to intracellular bacteria of the sst1-susceptible mice in vivo (Ji et al., Nature Microbiology, 2019). Next, we demonstrated that the Ifnb1 mRNA superinduction results from combined effects of TNF and JNK leading to integrated stress response in vitro (Bhattacharya, JCI, 2021). Thus, our previous work started with extensive characterization of the in vivo phenotype that led to the identification of the underlying macrophage deficiency that allowed for the detailed characterization of the macrophage phenotype in vitro presented in this manuscript. In a separate study, the Sher lab confirmed our conclusions and their in vivo relevance using Bach1 knockout in the sst1-susceptible B6.Sst1S background, where boosting antioxidant defense by Bach1 inactivation resulted in decreased type I interferon pathway activity and reduced granuloma necrosis. We have chosen TNF stimulation for our in vitro studies because this cytokine is most relevant for the formation and maintenance of the integrity of TB granulomas in vivo as shown in mice, non-human primates and humans. Here we demonstrate that although TNF is necessary for host resistance to virulent Mtb, its activity is insufficient for full protection of the susceptible hosts, because of altered macrophages responsiveness to TNF. Thus, our exploration of the necrosis of TB granulomas encompass both in vitro and extensive in vivo studies.

Minor comments

Introduction, while well written, is longer than necessary. Consider shortening this section. Throughout figures, many graphs show a fold induction/accumulation/etc, but it is rarely specified what the internal control is for each graph. This needs to be added.

Paragraph one, authors use the phrase "the entire IFN pathway was dramatically upregulated..." seems to be an exaggeration. How do you know the "entire" IFN pathway was upregulated in a dramatic fashion?

(1) We shortened the introduction and discussion; (2) verified that figure legends internal controls that were used to calculate fold induction; (3) removed the word “entire” to avoid overinterpretation.

Figures 1E, G and H and supp fig 1C, the heat maps are missing an expression key Section 2 second paragraph refers to figs 2D, E as cytoplasmic in the text, but figure legend and y-axis of 2E show total protein.

The expression keys were added to Fig.1E,G,H, Fig.7C, Suppl.Fig.1C and 1D and Suppl.Fig.11A of the revised manuscript.

Section 3 end of paragraph 1 refers to Fig 3h. Does this also refer to Supp Fig 3E?

Yes, Fig.3H shows microscopy of 4-HNE and Suppl.Fig.3H shows quantification of the image analysis. In the revised manuscript these data are presented in Fig.3H and Suppl.Fig.3F. The text was modified to reflect this change.

Supplemental Fig 3 legend for C-E seems to incorrectly also reference F and G.

We corrected this error in the figure legend. New panels were added to Suppl.Fig.3 and previous Suppl.Fig.3F and G were moved to Suppl.Fig.4 panels C and D of the revise version.

Fig 3K, the p-cJun was inhibited with the JNK inhibitor, however it’s unclear why this was done or the conclusion drawn from this experiment. Use of the JNK inhibitor is not discussed in the text.

The JNK inhibitor was used to confirm that c-Jun phosphorylation in our studies is mediated by JNK and to compare effects of JNK inhibition on phospho-cJun and Myc expression. This experiment demonstrated that the JNK inhibitor effectively inhibited c-Jun phosphorylation but not Myc upregulation, as shown in Fig.5I-J of the revised manuscript.

Fig 4 I and Supp Fig 3 H seem to have been swapped? The graph in Fig 4I matches the images in Supp Fig 3I. Please check.

We reorganized the panels to provide microscopy images and corresponding quantification together in the revised the panels Fig. 4H and Fig. 4I, as well as in Suppl. Fig. 4F and Suppl. Fig. 4G.

Fig 6, it is unclear what % cell number means. Also for bacterial growth, the data are fold change compared to what internal control?

We updated Fig.6 legend to indicate that the cell number percentages were calculated based on the number of cells at Day 0 (immediately after Mtb infection). We routinely use fixable cell death staining to enumerate cell death. Brief protocol containing this information is included in Methods section. The detailed protocol including normalization using BCG spike has been published – Yabaji et al, STAR Protocols, 2022. Here we did not present dead cell percentage as it remained low and we did not observe damage to macrophage monolayers. This allows us to exclude artifacts due to cell loss. The fold change of Mtb was calculated after normalization using Mtb load at Day 0 after infection and washes.

Fig 7B needs an expression key

The expression keys was added to Fig.7C (previously Fig. 7B).

Supp Fig 7 and Supp Fig 8A, what do the arrows indicate?

In Suppl.Fig.8 (previously Suppl.Fig.7) the arrows indicate acid fast bacilli (Mtb). In figures Fig.7A and Suppl.Fig.9A arrows indicate Mtb expressing fluorescent reporter mCherry. Corresponding figure legends were updated in the revised version.

Supp Fig 9A, two ROI appear to be outlined in white, not just 1 as the legend says Methods:

We updated the figure legend.

Certain items are listed in the Reagents section that are not used in the manuscript, such as necrostatin-1 or Z-VAD-FMK. Please carefully check the methods to ensure extra items or missing items does not occur.

These experiments were performed, but not included in the final manuscript. Hence, we removed the “necrostatin-1 or Z-VAD-FMK” from the reagents section in methods of revised version.

Western blot, method of visualizing/imaging bands is not provided, method of quantifying density is not provided, though this was done for fig 5C and should be performed for the other WBs.

We used GE ImageQuant LAS4000 Multi-Mode Imager to acquire the Western blot images and the densitometric analyses were performed by area quantification using ImageJ. We included this information in the method section. We added the densitometry of Western blot values after normalization above each lane in Fig.2A-C, Fig.3C-D and 3K; Fig.4A-B, Fig.5B,C,I,J.

Reviewer #3 (Significance):

The work of Yabaji et al is of high significance to the field of macrophage biology and M.tb pathogenesis in macrophages. This work builds from previously published work (Bhattacharya 2021) in which the authors first identified the aberrant response induced by TNF in sst1 mutant macrophages. Better understanding how macrophages with the sst1 locus respond not only to bacterial infection but stimulation with relevant ligands such as TNF will aid the field in identifying biomarkers for TB, biomarkers that can suggest a poor outcome vs. "cure" in response to antibiotic treatment or design of host-directed therapies.

This work will be of interest to those who study macrophage biology and who study M.tb pathogenesis and tuberculosis in particular. This study expands the knowledge already gained on the sst1 locus to further determine how early macrophage responses are shaped that can ultimately determine disease progression.

Strengths of the study include the methodologies, employing both bulk and single cell-RNA seq to answer specific questions. Data are analyze using automated methods (such as HALO) to eliminated bias. The experiments are well planned and designed to determine the mechanisms behind the increased iron-related oxidative stress found in the mutant macrophages following TNF treatment. Also, in vivo studies were performed to validate some of the in vitro work. Examining pauci-bacillary lesions vs multi-bacillary lesions and spatial transcriptomics is a significant strength of this work. The inclusion of human data is another strength of the study, showing increased Myc in humans with poor response to antibiotics for TB.

Limitations include the fact that the work is all done with BMDMs. Use of alveolar macrophages from the mice would be a more relevant cell type for M.tb studies. AMs are less inflammatory, therefore treatment with TNF of AMs could result in different results compared to BMDMs. Reviewer's field of expertise: macrophage activation, M.tb pathogenesis in human and mouse models, cell signaling.

Limitations: not qualified to evaluate single cell or bulk RNA-seq technical analysis/methodology or spatial transcriptomics analysis.

eLife Assessment

This useful study shows that stimuli of a certain size elicit theta oscillations in V1 neurons both in spikes and local field potentials, and monkeys performing a dot detection task on these stimuli show theta rhythmicity in their response times. This replicates previous findings showing rhythmic theta activity in V4 and behaviour when stimuli are presented in the receptive field along with a surrounding flanker stimulus. However, there is incomplete evidence that rhythmicity in neural activity is related to the rhythmicity in behavior, and the mechanisms underlying these oscillations remain unclear.

Reviewer #1 (Public review):

Summary:

The authors add to the body of evidence showing theta rhythmic modulations of neuronal activity and behavior.

Strengths:

Precise characterization of the effects of visual stimulation on theta-induced neuronal oscillations of spiking neurons in V1 and its relevance for behavior.

The manuscript is well-written and clearly presented,

Weaknesses:

The advances are limited over the established body of evidence. Both theta-induced visual oscillations and their relevance for behavior have been firmly established by prior work, including prior work from the authors. There is no major new technique, data, finding, or insight that extends our knowledge in a majorly significant way beyond existing knowledge, in my opinion. I would suggest that the authors re-evaluate the body of existing work to more strongly place their work in the context of existing work. A study that targets fundamental holes or open questions in the field would have been viewed as more impactful.

Reviewer #2 (Public review):

Summary:

Schmid & colleagues test an interesting hypothesis that V1 neurons might act as theta-tuned filters to incoming sensory information, and thereby influence downstream processing and detection performance.

Strengths:

The authors report that circular stimuli elicit theta oscillations in V1 single units and population activity. They also report that the phase of the theta oscillations influences performance in a change detection task.

Weaknesses:

The results are reported in terms of specific stimulus sizes. To truly reflect general-purpose spatial computations in the primary visual cortex, it will be important to establish a relationship between stimulus size and receptive field size.

I have several major concerns that I would like the authors to address:

(1) First paragraph of Results: The results are presented at very specific stimulus sizes: 0.3-degree, 1-degree, 4-degree, and so on. A key missing piece of information is the size of the receptive fields (RFs) that were recorded from. A related missing information is at what eccentricity these RFs were recorded from. Since there is nothing magical about a 1-degree stimulus, any general-purpose computation in the primary visual cortex has to establish a relationship between RF size and stimulus size.

(2) Second paragraph of Results: The authors state that "specific stimulus sizes consistently induced strong theta rhythmic activity: 1{degree sign} in MUA and 2{degree sign} in LFP". What is the interpretation of these specific sizes? Given that the LFP and MUAe reflect different aspects of neural activity, how does one interpret the discrepancy?

(3) Third paragraph of Results: Again related to (1), what is the relationship between the stimulus size that elicited the largest theta peaks and RF size at the population level? (1)-(3) taken together, there seems to be an opportunity to reveal something more fundamental about V1 processing that the authors might have missed here.

(4) Change detection task: It was not clear to me whether the timing of the luminance change, which varied from 500ms to 1500ms, was drawn from an exponential distribution or a uniform distribution. Only an exponential distribution has the property of a flat hazard function, which will be important to establish that the animal could not anticipate the timing of the upcoming change.

(5) Figure 3D: Have the authors tried to fit the data separately for each animal? There seems to be an inconsistency in the results between the 2 animals. The circular data points ('AL') seem positively correlated, similar to the overall trend, but the diamond data points ('DP') seem to have a negative slope.

Reviewer #3 (Public review):

Summary:

This paper investigates changes in brain oscillations in V1 in response to experimentally manipulating visual stimulus features (size, contrast at optimal size) and examines whether these effects are of perceptual relevance. The results reveal prominent stimulus-related theta oscillations in V1 that match in frequency the rhythms of behavioural performance (response speed in detecting targets in the visual display). Phase analyses relate these fluctuations of detection performance more formally to opposite theta phase angles in V1.

Strengths:

The non-human primate model provides unique findings on how brain oscillations relate to rhythms in perception (in two rhesus monkeys) that align well with findings from human studies (as occurring in the theta band). However, theta rhythms in humans are typically associated with fronto-parietal activity in the domain of spatial orienting, attentional sampling, while here the focus is on V1. Importantly, microsaccade-controls seem to speak against a spatial orienting/ attentional sampling mechanism to explain the observed effects (at least regarding overt attention).

Weaknesses:

This study provides interesting clues on perceptually relevant brain oscillations. Despite the microsaccade-control, I believe it remains an open question whether the V1 rhythmicity is of pure V1 origin, or driven by top-down input, as it is conceivable that specific stimuli capture attention differently (and hence induce specific covert attentional (re)orienting patterns). For perceptually relevant (yet beta) rhythmicity over occipital areas that are top-down generated, see e.g., Veniero et al., 2019.

eLife Assessment

In this useful study, ectopic expression and knockdown strategies were used to assess the effects of increasing and decreasing Cyclic di-AMP on the developmental cycle in Chlamydia. The authors convincingly demonstrate that overexpression of the dacA-ybbR operon results in increased production of c-di-AMP and early expression of the transitionary gene hctA and late gene omcB. Whilst the authors have attempted to revise the submission, the model proposed in the revised manuscript is still not fully supported by the data presented.

Reviewer #2 (Public review):

This manuscript describes the role of the production of c-di-AMP on the chlamydial developmental cycle. The main findings remain the same. The authors show that overexpression of the dacA-ybbR operon results in increased production of c-di-AMP and early expression of transitionary and late genes. The authors also knocked down the expression of the dacA-ybbR operon and reported a modest reduction in the expression of both hctA and omcB. The authors conclude with a model suggesting the amount of c-di-AMP determines the fate of the RB, continued replication, or EB conversion.

Overall, this is a very intriguing study with important implications however the data is very preliminary and the model is very rudimentary. The data support the observation that dramatically increased c-di-AMP has an impact on transitionary gene expression and late gene expression suggesting dysregulation of the developmental cycle. This effect goes away with modest changes in c-di-AMP (detaTM-DacA vs detaTM-DacA (D164N)). However, the model predicts that low levels of c-di-AMP delays EB production is not not well supported by the data. If this prediction were true then the growth rate would increase with c-di-AMP reduction and the data does not show this. The levels of of c-di-AMP at the lower levels need to be better validated as it seems like only very high levels make a difference for dysregulated late gene expression. However, on the low end it's not clear what levels are needed to have an effect as only DacAopMut and DacAopKD show any effects on the cycle and the c-di-AMP levels are only different at 24 hours.

The data still do not support the overall model.

In Figure 1 the authors show at 24 hpi.

DacA overexpression increases cdiAMP to ~4000 pg/ml

DacAmut overexpression reduces cdiAMP dramatically to ~256 pg/ml)

DacATM overexpression increases cdiAMP to ~4000 pg/ml.

DacAmutTM overexpression does not seem to change cdiAMP ~1500 pg/ml .

dacAKD decreases cdiAMP to ~300 pg/ml .

dacAKDcom increased cdiAMP to ~8000 pg/ml.

DacA-ybbRop overexpression increased cdiAMP to ~500,000 pg/ml.

DacA-ybbRopmut ~300 pg/ml.

However in Figure 2 the data show that overexpression of DacA (cdiAMP ~4000 pg/ml) did not have a different phenotype than over expression of the mutant (cdiAMP ~256 pg/ml). HctA expression down, omcB expression down, euo not much change, replication down, and IFUs down. Additionally, Figure 3 shows no differences in anything measured although cdiAMP levels were again dramatically different. DacATM overexpression (~4000 pg/ml) and DacAmutTM (~1500). This makes it unclear what cdiAMP is doing to the developmental cycle.

In Figure 4 the authors knockdown dacA (dacA-KD) and complement the knockdown (dacA-KDcom) dacAKD decreases cdiAMP (~300) while DacA-KDcom increases cdiAMP much above wt (~8000).<br /> KD decreased hctA and omcB at 24hpi. Complementation resulted in a moderate increase in hctA at a single time point but not at 24 hpi and had no effect on euo or omcB expression. Importantly, complementation decreased the growth rate. Based on the proposed model, growth rate should increase as the chlamydia should all be RBs and replicating and not exiting the cell cycle to become EBs (not replicating). Interestingly reducing cdiAMP levels by over expressing DacAmut (~256 pg/ml) did not have an effect on the cycle but the reduction in cdiAMP by knockdown of dacA (~300 pg/ml) did have a moderate effect on the cycle.

For Figure 5 DacA-ybbRop was overexpressed and this increased cdiAMP dramatically ~500,000 pg/ml as compared to wt ~1500. This increased hctA only at an early timepoint and not at 24hpi and again had no effect on omcB or euo. Overexpression of the operon with the mutation DacA-ybbRopmut reduced cdiAMP to ~300 pg/ml and this showed a reduction in growth rate similar to dacAmut but a more dramatic decrease in IFUs.

Overall:

DacA overexpression increases cdiAMP to ~4000 pg/ml (decreased everything except euo)

DacAmut overexpression reduces cdiAMP dramatically (~256 pg/ml). (decreased everything except euo)

DacATM overexpression increases cdiAMP to ~4000 pg/ml (no changes noted)

DacAmutTM overexpression does not seem to change cdiAMP ~1500 pg/ml (no changes noted)

dacAKD decrease cdiAMP to ~300 pg/ml (decreased everything except euo)

dacAKDcom increased cdiAMP to ~8000 pg/ml (decreases growth rate, increase hctA a little but not omcB)

DacA-ybbRop overexpression increased cdiAMP to ~500,000 pg/ml (decreases growth rate, increase hctA a little but not omcB)

DacA-ybbRopmut ~300 pg/ml (decreased everything except euo)

Overall, the data show that increasing cdiAMP only has a phenotype if it is dramatically increased, no effect at 4000 pg/ml. Decreasing cdiAMP has a consistent effect, decreased growth rate, IFU, hctA expression and omcB expression. However, if their proposed model was correct and low levels of cdiAMP blocked EB conversion then more chlamydial cells would be RBs (dividing cells) and the growth rate should increase. Conversely, if cdiAMP levels were dramatically raised then all RBs would all convert and the growth rate would be very low. When cdiAMP was raised to ~4000 pg/ml there was no effect on the growth rate. However, an increase to ~8000 pg/ml resulted in a significant decrease but growth continued. Increasing cdAMP to ~500,000 pg/ml had less of an impact on the growth rate. Overall, the data does not cleanly support the proposed model.

Author response:

The following is the authors’ response to the current reviews

Reviewer #2 (Public review): 

This manuscript describes the role of the production of c-di-AMP on the chlamydial developmental cycle. The main findings remain the same. The authors show that overexpression of the dacA-ybbR operon results in increased production of c-di-AMP and early expression of transitionary and late genes. The authors also knocked down the expression of the dacA-ybbR operon and reported a modest reduction in the expression of both hctA and omcB. The authors conclude with a model suggesting the amount of c-di-AMP determines the fate of the RB, continued replication, or EB conversion. 

Overall, this is a very intriguing study with important implications however the data is very preliminary and the model is very rudimentary. The data support the observation that dramatically increased c-di-AMP has an impact on transitionary gene expression and late gene expression suggesting dysregulation of the developmental cycle. This effect goes away with modest changes in c-di-AMP (detaTM-DacA vs detaTM-DacA (D164N)). However, the model predicts that low levels of c-di-AMP delays EB production is not not well supported by the data. If this prediction were true then the growth rate would increase with c-di-AMP reduction and the data does not show this. The levels of of c-di-AMP at the lower levels need to be better validated as it seems like only very high levels make a difference for dysregulated late gene expression. However, on the low end it's not clear what levels are needed to have an effect as only DacAopMut and DacAopKD show any effects on the cycle and the c-di-AMP levels are only different at 24 hours. 

These appear to be the same comments the reviewer presented last time, so we will reiterate our prior points here and elsewhere. We do not think and nor do we predict that low c-di-AMP levels should increase growth rate (as measured by gDNA levels), and this conclusion cannot be drawn from our data. Rather, we predict that the inability to accumulate c-di-AMP should delay production of EBs, and this is what the data show. The reviewer has applied their own subjective (and erroneous) interpretation to the model. The asynchronicity of the normal developmental cycle means RBs continue to replicate as EBs are forming, so gDNA levels cannot be used as the sole metric for determining RB levels. We show that reduced c-di-AMP levels reduce EB levels as well as transcripts associated with late stages of development. The parsimonious interpretation of these data support that low c-di-AMP levels delay progression through the developmental cycle consistent with our model.

The data still do not support the overall model.

We disagree.  We have presented quantified data that include appropriate controls and statistical tests, and the reviewer has not disputed that or pointed to additional experiments that need to be performed.  The reviewer has imposed a subjective interpretation of our model based on their own biases.  A reader is free, of course, to disagree with our model, but a reviewer should not block a manuscript based on such a disagreement if no experimental flaws have been identified. 

In Figure 1 the authors show at 24 hpi. 

We also showed data from 16hpi, which is a more relevant timepoint for assessing premature transition to EBs.  In contrast, the 24hpi is more important for assessing developmental effects of reduced c-di-AMP levels.

DacA overexpression increases cdiAMP to ~4000 pg/ml 

DacAmut overexpression reduces cdiAMP dramatically to ~256 pg/ml) 

DacATM overexpression increases cdiAMP to ~4000 pg/ml. 

DacAmutTM overexpression does not seem to change cdiAMP ~1500 pg/ml . 

dacAKD decreases cdiAMP to ~300 pg/ml . 

dacAKDcom increased cdiAMP to ~8000 pg/ml. 

DacA-ybbRop overexpression increased cdiAMP to ~500,000 pg/ml. 

DacA-ybbRopmut ~300 pg/ml. 

However in Figure 2 the data show that overexpression of DacA (cdiAMP ~4000 pg/ml) did not have a different phenotype than over expression of the mutant (cdiAMP ~256 pg/ml). HctA expression down, omcB expression down, euo not much change, replication down, and IFUs down. Additionally, Figure 3 shows no differences in anything measured although cdiAMP levels were again dramatically different. DacATM overexpression (~4000 pg/ml) and DacAmutTM (~1500). This makes it unclear what cdiAMP is doing to the developmental cycle. 

As we have explained in the text and in response to reviewer comments on previous rounds of review, overexpressing the full-length WT or mutant DacA is detrimental to developmental cycle progression for reasons that have nothing to do with c-di-AMP levels (likely disrupting membrane function), since, as the reviewer notes, the WT DacA deltaTM strain had similar c-di-AMP levels but no negative effects on growth/development. If we had not presented the effects of overexpressing the individual isoforms, then a reviewer would surely have requested such, which is why we present these data even though they don’t seem to support our model.  This is an honest representation of our findings.  The reviewer seems intent on nitpicking a minor datapoint that seems to contradict the rest of the manuscript while ignoring or not carefully reading the rest of the manuscript.

In Figure 4 the authors knockdown dacA (dacA-KD) and complement the knockdown (dacA-KDcom) 

dacAKD decreases cdiAMP (~300) while DacA-KDcom increases cdiAMP much above wt (~8000). 

KD decreased hctA and omcB at 24hpi. Complementation resulted in a moderate increase in hctA at a single time point but not at 24 hpi and had no effect on euo or omcB expression.

By 24hpi, late gene transcripts are being maximally produced during a normal developmental cycle. It is unclear why the reviewer thinks that these transcripts should be elevated above this level in any of our strains that prematurely transition to EBs. There is no basis in the literature to support such an assumption. As we noted in the text, the dacA-KDcom strain phenocopied the dacAop OE strain, and we showed RNAseq data and EB production curves for the latter that support our conclusions of the effect of increased c-di-AMP levels on developmental progression.

Importantly, complementation decreased the growth rate.

Yes, since the c-di-AMP levels breached the “EB threshold” at 16hpi, it causes premature transition to EBs, which do not replicate their gDNA, at an earlier stage of the cycle when fewer organisms are present. Therefore, the gDNA levels are decreased at 24hpi, which is consistent with our model.

Based on the proposed model, growth rate should increase as the chlamydia should all be RBs and replicating and not exiting the cell cycle to become EBs (not replicating).

This is a spurious conclusion from the reviewer. As we clearly showed, the dacA-KDcom did not restore a wild-type phenotype and instead mimicked the dacAop OE strain. This was commented on in the text.

Interestingly reducing cdiAMP levels by over expressing DacAmut (~256 pg/ml) did not have an effect on the cycle but the reduction in cdiAMP by knockdown of dacA (~300 pg/ml) did have a moderate effect on the cycle. 

This is again a spurious conclusion from the reviewer. The dacAMut and dacA-KD strains are distinct. As noted in the text and above for DacA WT OE, overexpressing the DacAMut similarly disrupts organism morphology, which is different from dacA-KD. These strains should not be directly compared because of this. This point has been previously highlighted in the text (in Results and Discussion).

For Figure 5 DacA-ybbRop was overexpressed and this increased cdiAMP dramatically ~500,000 pg/ml as compared to wt ~1500. This increased hctA only at an early timepoint and not at 24hpi and again had no effect on omcB or euo.

As we explained in prior reviews, our RNAseq data more comprehensively assessed transcripts for the dacAop OE strain. These data show convincingly that late gene transcripts (not just hctA and omcB) are elevated earlier in the developmental cycle. Again, it is not clear why the reviewer should expect that late gene transcripts should be higher in these strains than they are during a normal developmental cycle. This is not part of our model and appears to be a bias that the reviewer has imposed that is not supported by the literature.

Overexpression of the operon with the mutation DacA-ybbRopmut reduced cdiAMP to ~300 pg/ml and this showed a reduction in growth rate similar to dacAmut but a more dramatic decrease in IFUs. 

As we described in the text, in earlier revisions, and above, the dacAMut OE strain has distinct effects unrelated to c-di-AMP levels and, therefore, should not be compared to other strains in terms of linking its c-di-AMP levels to its phenotype.

Overall: 

DacA overexpression increases cdiAMP to ~4000 pg/ml (decreased everything except euo) 

DacAmut overexpression reduces cdiAMP dramatically (~256 pg/ml). (decreased everything except euo) 

DacATM overexpression increases cdiAMP to ~4000 pg/ml (no changes noted) 

DacAmutTM overexpression does not seem to change cdiAMP ~1500 pg/ml (no changes noted) 

dacAKD decrease cdiAMP to ~300 pg/ml (decreased everything except euo) 

dacAKDcom increased cdiAMP to ~8000 pg/ml (decreases growth rate, increase hctA a little but not omcB) 

DacA-ybbRop overexpression increased cdiAMP to ~500,000 pg/ml (decreases growth rate, increase hctA a little but not omcB) <br /> DacA-ybbRopmut ~300 pg/ml (decreased everything except euo) 

Overall, the data show that increasing cdiAMP only has a phenotype if it is dramatically increased, no effect at 4000 pg/ml.

Yes, this clearly shows there is a threshold - as we hypothesize!  However, these thresholds are more important at the 16hpi timepoint not 24hpi (which the reviewer is referencing) when assessing premature transition to EBs.  We specifically highlighted in our prior revision in Figure 1E this EB threshold to make this point clearer for the reader.  Once the threshold is breached, then the overall c-di-AMP levels become irrelevant as the RBs have begun their transition to EBs.

Decreasing cdiAMP has a consistent effect, decreased growth rate, IFU, hctA expression and omcB expression. However, if their proposed model was correct and low levels of cdiAMP blocked EB conversion then more chlamydial cells would be RBs (dividing cells) and the growth rate should increase.

The only effect should be normal gDNA levels, which is what we see in the dacA-KD.  Given the asynchronicity of a normal developmental cycle in which RBs continue to replicate as EBs are still forming, there is no basis to assume gDNA levels should increase under these conditions for the dacA-KD strain at 24hpi.

Conversely, if cdiAMP levels were dramatically raised then all RBs would all convert and the growth rate would be very low.

We agree. This is what is reflected by the dacAop OE and dacA-KDcom strains, with reduced gDNA levels at 24hpi since organisms have transitioned to EBs at an earlier time post-infection.

When cdiAMP was raised to ~4000 pg/ml there was no effect on the growth rate.

Yes, because it had not breached the EB threshold at 16hpi – consistent with our model!  The reviewer is confusing effects of elevated c-di-AMP at 24hpi when they should be assessed at the 16hpi timepoint for strains overproducing this molecule.

However, an increase to ~8000 pg/ml resulted in a significant decrease but growth continued.

If the reviewer is referring to the dacA-KDcom strain, then this is not accurate. gDNA levels were decreased in this strain at 24hpi when the c-di-AMP levels were increased compared to the WT (mCherry OE) control at 16hpi, indicating this strain had breached the “EB threshold” and initiated conversion to EBs at an earlier timepoint post-infection when fewer organisms were present.

Increasing cdAMP to ~500,000 pg/ml had less of an impact on the growth rate.

It is not clear what this conclusion is based on and what the reviewer is comparing to.  This is a subjective assessment not based on our data.

Overall, the data does not cleanly support the proposed model.

It is an unfortunate aspect of biology, particularly for obligate intracellular bacteria – a challenging experimental system on which to work, that the data are not always “clean”.  The overall effects of increased c-di-AMP levels on chlamydial developmental cycle progression we have documented support our model, and we think the reader, as always, should make their own assessment.

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

Reviewer #2 (Public review): 

This manuscript describes the role of the production of c-di-AMP on the chlamydial developmental cycle. The main findings remain the same. The authors show that overexpression of the dacA-ybbR operon results in increased production of c-di-AMP and early expression of transitionary and late genes. The authors also knocked down the expression of the dacA-ybbR operon and reported a modest reduction in the expression of both hctA and omcB. The authors conclude with a model suggesting the amount of c-di-AMP determines the fate of the RB, continued replication, or EB conversion. 

Overall, this is a very intriguing study with important implications however, the data is very preliminary, and the model is very rudimentary. The data support the observation that dramatically increased c-di-AMP has an impact on transitionary gene expression and late gene expression suggesting dysregulation of the developmental cycle. This effect goes away with modest changes in c-di-AMP (detaTM-DacA vs detaTM-DacA (D164N)). However, the model predicts that low levels of c-di-AMP delays EB production is not not well supported by the data. If this prediction were true then the growth rate would increase with c-di-AMP reduction and the data does not show this.

Thank you for the comments. We have apparently not adequately communicated our predictions and the model. We do not think and nor do we predict that low c-di-AMP levels should increase growth rate, and there is no basis in any of our data to support that. Rather, we predict that the inability to accumulate c-di-AMP should delay production of EBs, and this is what the data show. We have clarified this in the text (line 89 paragraph).

The levels of c-di-AMP at the lower levels need to be better validated as it seems like only very high levels make a difference for dysregulated late gene expression. However, on the low end it's not clear what levels are needed to have an effect as only DacAopMut and DacAopKD show any effects on the cycle and the c-di-AMP levels are only different at 24 hours.

Our hypothesis is that increasing concentrations of c-di-AMP within a given RB is a signal for it to undergo secondary differentiation to the EB, and the data support this as noted by the reviewers. Again, we stress that low levels of c-di-AMP are irrelevant to the model. We have revised Figure 1E to indicate the level of c-di-AMP in the control strain at the 24hpi timepoint that coincides with increased EB levels. We hope this will further clarify the goals of our study. That a given strain might be below the EB control is not relevant to the model beyond indicating that it has not reached the necessary threshold for triggering secondary differentiation.

The authors responded to reviewers' critiques by adding the overexpression of DacA without the transmembrane region. This addition does not really help their case. They show that detaTM-DacA and detaTM-DacA (D164N) had the same effects on c-di-AMP levels but the figure shows no effects on the developmental cycle.

As it relates directly to the reviewer’s point, the delta-TM strains did not show the same level of c-di-AMP. It may be that the reviewer misread the graph. The purpose of testing these strains was to show that the negative effects of overexpressing full-length WT DacA were due to its membrane localization. Both the FL and deltaTM-DacA (WT) overexpression had equivalent c-di-AMP levels even though the delta-TM overexpression looked like the mCherry-expressing strain based on the measured parameters. This shows that the c-di-AMP levels were irrelevant to the phenotypes observed when overexpressing these WT isoforms. For the mutant isoforms, the delta-TM looked like the mCherry-expressing control while the FL isoform was negatively impacted for reasons we described in the Discussion (e.g., dominant negative effect). In addition, at 16hpi, neither delta-TM strain had c-di-AMP levels that approached the 24h control as denoted in Figure 1E (dashed line) and in the text, which explains why these strains did not show increased late gene transcripts at an earlier timepoint like the dacAop and dacA-KDcom strains.

Describing the significance of the findings: 

The findings are important and point to very exciting new avenues to explore the important questions in chlamydial cell form development. The authors present a model that is not quantified and does not match the data well. 

We respectfully disagree with this assessment as noted above in response to the reviewer’s critique. All of our data are quantified and support the hypothesis as stated.

Describing the strength of evidence: 

The evidence presented is incomplete. The authors do a nice job of showing that overexpression of the dacA-ybbR operon increases c-di-AMP and that knockdown or overexpression of the catalytically dead DacA protein decreases the c-di-AMP levels. However, the effects on the developmental cycle and how they fit the proposed model are less well supported. 

Overall this is a very intriguing finding that will require more gene expression data, phenotypic characterization of cell forms, and better quantitative models to fully interpret these findings. 

It is not clear what quantitative models the reviewer would prefer, but, ultimately, it is up to the reader to decide whether they agree or not with the model we present. The data are the data, and we have tried to present them as clearly as possible. We would emphasize that, with the number of strains we have analyzed, we have presented a huge amount of data for a study with an obligate intracellular bacterium. As a comparison, most publications on Chlamydia might use a handful of transformant strains, if any. Given the cost and time associated with performing such studies, it is prohibitive to attempt all the time points that one might like to do, and it is not clear to us that further studies will add to or alter the conclusions of the current manuscript.

Reviewer #2 (Recommendations for the authors): 

Minor critiques 

The graphs have red and blue lines but the figure legends are red and black. It would be better if these matched. 

Changed.

For Figure 1C. The labels are not very helpful. It's not clear what is HeLa vs mCherry. I believe it is uninfected vs Chlamydia infected.

Changed.

eLife Assessment

This valuable study revisits the effects of substitution model selection on phylogenetics by comparing reversible and non-reversible DNA substitution models. The authors provide solid evidence that 1) it can be beneficial to include non-time-reversible models in addition to general time-reversible models when inferring phylogenetic trees out of simulated viral genome sequence data sets, and that 2) non time-reversible models may fit the real data better than the reversible substitution models commonly used in phylogenetics, a finding consistent with previous work.

Reviewer #1 (Public review):

Summary:

This is a contribution to the field of developmental bioelectricity. How do changes of resting potential at the cell membrane affect downstream processes? Zhou et al. reported in 2015 that phosphatidylserine and K-Ras cluster upon plasma membrane depolarization and that voltage-dependent ERK activation occurs when constitutively active K-RasG12V mutants are overexpressed. In this paper, the authors advance the knowledge of this phenomenon by showing that membrane depolarization up-regulates mitosis and that this process is dependent on voltage-dependent activation of ERK. ERK activity's voltage-dependence is derived from changes in the dynamics of phosphatidylserine in the plasma membrane and not by extracellular calcium dynamics. This paper reports an interesting and important finding. It is somewhat derivative of Zhou et al., 2015. (https://www.science.org/doi/full/10.1126/science.aaa5619). The main novelty seems to be that they find quantitatively different conclusions upon conducting similar experiments, albeit with a different cell line (U2OS) than those used by Zhou et al. Sasaki et al. do show that increased K+ levels increase proliferation, which Zhou et al. did not look at. The data presented in this paper are a useful contribution to a field often lacking such data.

Strengths:

Bioelectricity is an important field for areas of cell, developmental, and evolutionary biology, as well as for biomedicine. Confirmation of ERK as a transduction mechanism and a characterization of the molecular details involved in the control of cell proliferation are interesting and impactful.

Weaknesses:

The authors lean heavily on the assumption that the Nernst equation is an accurate predictor of membrane potential based on K+ level. This is a large oversimplification that undermines the author's conclusions, most glaringly in Figure 2C. The author's conclusions should be weakened to reflect that the activity of voltage gated ion channels and homeostatic compensation are unaccounted for.

There are grammatical tense errors are made throughout the paper (ex line 99 "This kinetics should be these kinetics")

Line 71: Zhou et al. use BHK, N2A, PSA-3 cells, this paper uses U2OS (osteosarcoma) cells. Could that explain the differences in bioelectric properties that they describe? In general, there should be more discussion of the choice of cell line. Why were U2OS cells chosen? What are the implications of the fact that these are cancer cells, and bone cancer cells in particular? Does this paper provide specific insights for bone cancers? And crucially, how applicable are findings from these cells to other contexts?

Line 115: The authors use EGF to calibrate 'maximal' ERK stimulation. Is this level near saturation? Either way is fine, but it would be useful to clarify.

Line 121: Starting line 121 the authors say "Of note, U2OS cells expressed wild-type K-Ras but not an active mutant of K-Ras, which means voltage dependent ERK activation occurs not only in tumor cells but also in normal cells". Given that U2OS cells are bone sarcoma cells, is it appropriate to refer to these as 'normal' cells in contrast to 'tumor' cells?

Line 101: These normalizations seem reasonable, the conclusions sufficiently supported and the requisite assumptions clearly presented. Because the dish-to-dish and cell-to-cell variation may reflect biologically relevant phenomena it would be ideal if non-normalized data could be added in supplemental data where feasible.

Figure 2C is listed as Figure 2D in the text

There is no Figure 2F (Referenced in line 148)

Reviewer #2 (Public review):

Sasaki et al. use a combination of live-cell biosensors and patch-clamp electrophysiology to investigate the effect of membrane potential on the ERK MAPK signaling pathway, and probe associated effects on proliferation. This is an effect that has long been proposed, but a convincing demonstration has remained elusive, because it is difficult to perturb membrane potential without disturbing other aspects of cell physiology in complex ways. The time-resolved measurements here are a nice contribution to this question, and the perforated patch clamp experiments with an ERK biosensor are fantastic - they come closer to addressing the above difficulty of perturbing voltage than any prior work. It would have been difficult to obtain these observations with any other combination of tools.

However, there are still some concerns as detailed in specific comments below:

Specific comments:

(1) All the observations of ERK activation, by both high extracellular K+ and voltage clamp, could be explained by cell volume increase (more discussion in subsequent comments). There is a substantial literature on ERK activation by hypotonic cell swelling (e.g. https://doi.org/10.1042/bj3090013, https://doi.org/10.1002/j.1460-2075.1996.tb00938.x, among others). Here are some possible observations that could demonstrate that ERK activation by volume change is distinct from the effects reported here:

i) Does hypotonic shock activate ERK in U2OS cells?

ii) Can hypotonic shock activate ERK even after PS depletion, whereas extracellular K+ cannot?

iii) Does high extracellular K+ change cell volume in U2OS cells, measured via an accurate method such as fluorescence exclusion microscopy?

iv) It would be helpful to check the osmolality of all the extracellular solutions, even though they were nominally targeted to be iso-osmotic.

(2) Some more details about the experimental design and the results are needed from Figure 1:

i) For how long are the cells serum-starved? From the Methods section, it seems like the G1 release in different K+ concentration is done without serum, is this correct? Is the prior thymidine treatment also performed in the absence of serum?

ii) There is a question of whether depolarization constitutes a physiologically relevant mechanism to regulate proliferation, and how depolarization interacts with other extracellular signals that might be present in an in vivo context. Does depolarization only promote proliferation after extended serum starvation (in what is presumably a stressed cell state)? What fraction of total cells are observed to be mitotic (without normalization), and how does this compare to the proliferation of these cells growing in serum-supplemented media? Can K+ concentration tune proliferation rate even in serum-supplemented media?

(3) In Figure 2, there are some possible concerns with the perfusion experiment:

i) Is the buffer static in the period before perfusion with high K+, or is it perfused? This is not clear from the Methods. If it is static, how does the ERK activity change when perfused with 5 mM K+? In other words, how much of the response is due to flow/media exchange versus change in K+ concentration?

ii) Why do there appear to be population-average decreases in ERK activity in the period before perfusion with high K+ (especially in contrast to Fig. 3)? The imaging period does not seem frequent enough for photobleaching to be significant.

(4) Figure 3 contains important results on couplings between membrane potential and MAPK signaling. However, there are a few concerns:

i) Does cell volume change upon voltage clamping? Previous authors have shown that depolarizing voltage clamp can cause cells to swell, at least in the whole-cell configuration:

https://www.cell.com/biophysj/fulltext/S0006-3495(18)30441-7 . Could it be possible that the clamping protocol induces changes in ERK signaling due to changes in cell volume, and not by an independent mechanism?

ii) Does the -80 mV clamp begin at time 0 minutes? If so, one might expect a transient decrease in sensor FRET ratio, depending on the original resting potential of the cells. Typical estimates for resting potential in HEK293 cells range from -40 mV to -15 mV, which would reach the range that induces an ERK response by depolarizing clamp in Fig. 3B. What are the resting potentials of the cells before they are clamped to -80 mV, and why do we not see this downward transient?

(5) The activation of ERK by perforated voltage clamp and by high extracellular K+ are each convincing, but it is unclear whether they need to act purely through the same mechanism - while additional extracellular K+ does depolarize the cell, it could also be affecting function of voltage-independent transporters and cell volume regulatory mechanisms on the timescales studied. To more strongly show this, the following should be done with the HEK cells where there is already voltage clamp data:

i) Measure resting potential using the perforated patch in zero-current configuration in the high K+ medium. Ideally this should be done in the time window after high K+ addition where ERK activation is observed (10-20 minutes) to minimize the possibility of drift due to changes in transporter and channel activity due to post-translational regulation.

ii) Measure YFP/CFP ratio of the HEK cells in the high K+ medium (in contrast to the U2OS cells from Fig. 2 where there is no patch data).

iii) The assertion that high K+ is equivalent to changes in Vmem for ERK signaling would be supported if the YFP/CFP change from K+ addition is comparable to that induced by voltage clamp to the same potential. This would be particularly convincing if the experiment could be done with each of the 15 mM, 30 mM, and 145 mM conditions.

(6) Line 170: "ERK activity was reduced with a fast time course (within 1 minute) after repolarization to -80 mV." I don't see this in the data: in Fig. 3C, it looks like ERK remains elevated for > 10 min after the electrical stimulus has returned to -80 mV

Comments on revisions:

The authors have done a good job addressing the comments on the previous submission.

Reviewer #3 (Public review):

Summary:

This paper demonstrates that membrane depolarization induces a small increase in cell entry into mitosis. Based on previous work from another lab, the authors propose that ERK activation might be involved. They show convincingly using a combination of assays that ERK is activated by membrane depolarization. They show this is Ca2+ independent and is a result of activation of the whole K-Ras/ERK cascade which results from changed dynamics of phosphatidylserine in the plasma membrane that activates K-Ras. Although the activation of the Ras/ERK pathway by membrane depolarization is not new, linking it to an increase in cell proliferation is novel.

Strengths

A major strength of the study is the use of different techniques - live imaging with ERK reporters, as well as Western blotting to demonstrate ERK activation as well as different methods for inducing membrane depolarization. They also use a number of different cell lines. Via Western blotting the authors are also able to show that the whole MAPK cascade is activated.

Weaknesses

A weakness of the study is the data in Figure 1 showing that membrane depolarization results in an increase of cells entering mitosis. There are very few cells entering mitosis in their sample in any condition. This should be done with many more cells to increase the confidence in the results. The study also lacks a mechanistic link between ERK activation by membrane depolarization and increased cell proliferation.

The authors did achieve their aims with the caveat that the cell proliferation results could be strengthened. The results, for the most par,t support the conclusions.

This work suggests that alterations in membrane potential may have more physiological functions than action potential in the neural system as it has an effect on intracellular signalling and potentially cell proliferation.

In the revised manuscript, the authors have now addressed the issues with Figure 1, and the data presented are much clearer. They did also attempt to pinpoint when in the cell cycle ERK is having its activity, but unfortunately, this was not conclusive.

Author response:

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

Reviewer #1 (Public review):

Summary:

This is a contribution to the field of developmental bioelectricity. How do changes of resting potential at the cell membrane affect downstream processes? Zhou et al. reported in 2015 that phosphatidylserine and K-Ras cluster upon plasma membrane depolarization and that voltage-dependent ERK activation occurs when constitutive active K-RasG12V mutants are overexpressed. In this paper, the authors advance the knowledge of this phenomenon by showing that membrane depolarization up-regulates mitosis and that this process is dependent on voltage-dependent activation of ERK. ERK activity's voltage-dependence is derived from changes in the dynamics of phosphatidylserine in the plasma membrane and not by extracellular calcium dynamics.

Strengths:

Bioelectricity is an important field for areas of cell, developmental, and evolutionary biology, as well as for biomedicine. Confirmation of ERK as a transduction mechanism, and a characterization of the molecular details involved in control of cell proliferation, is interesting and impactful.

Weaknesses:

The functional cell division data need to be stronger. They show that increasing K+ increases proliferation and argue that since a MEK inhibitor (U0126) reduces proliferation in K+ treated cells, K+ induces cell division via ERK. But I don't see statistics to show that the rescue is significant, and I don't see a key U0126-only control. If the U0126 alone reduces proliferation, the combined effect wouldn't prove much.

We thank the reviewer for constructive feedback. We repeated the experiment including the U0126-only control (5K+U). We updated Fig.1, presenting the newly obtained data with statistical analysis.

Also, unless I'm missing something, it looks like every sample in their control has exactly the same number of mitotic cells. I understand that they are normalizing to this column, but shouldn't they be normalizing to the mean, with the independent values scattering around 1? It doesn't seem like it can be paired replicates since there are 6 replicates in the control and 4 replicates in one of the conditions? 

We apologize for the unclear description. As the reviewer pointed out, the experiments were not paired replicates due to the limited number of conditions that can be conducted as a single experiment. To overcome this problem, we always included a control condition (i.e. 5K) based on which normalization was performed. This is the reason the data in 5K is always 1 and the sample size of 5K is the largest. Data include 100-900 mitotic cells within the imaging frame of 6 hrs. We re-wrote the figure legend (Fig1) and the main text, which hopefully clarified our experimental framework.

Reviewer #2 (Public review):

Sasaki et al. use a combination of live-cell biosensors and patch-clamp electrophysiology to investigate the effect of membrane potential on the ERK MAPK signaling pathway, and probe associated effects on proliferation. This is an effect that has long been proposed, but convincing demonstration has remained elusive, because it is difficult to perturb membrane potential without disturbing other aspects of cell physiology in complex ways. The time-resolved measurements here are a nice contribution to this question, and the perforated patch clamp experiments with an ERK biosensor are fantastic - they come closer to addressing the above difficulty of perturbing voltage than any prior work. It would have been difficult to obtain these observations with any other combination of tools.

However, there are still some concerns as detailed in specific comments below:

Specific comments:

(1) All the observations of ERK activation, by both high extracellular K+ and voltage clamp, could be explained by cell volume increase (more discussion in subsequent comments). There is a substantial literature on ERK activation by hypotonic cell swelling (e.g. https://doi.org/10.1042/bj3090013, https://doi.org/10.1002/j.1460-2075.1996.tb00938.x, among others). Here are some possible observations that could demonstrate that ERK activation by volume change is distinct from the effects reported here:

(i) Does hypotonic shock activate ERK in U2OS cells?

(ii) Can hypotonic shock activate ERK even after PS depletion, whereas extracellular K+ cannot?

(iii) Does high extracellular K+ change cell volume in U2OS cells, measured via an accurate method such as fluorescence exclusion microscopy?

(iv) It would be helpful to check the osmolality of all the extracellular solutions, even though they were nominally targeted to be iso-osmotic.

This is an important point. We conducted several experiments and provided explanations to rule out the possibility that ERK activation can be explained solely by cell volume change. We measured the osmolarity of all solutions used in this paper, which were 296-305 mOsm/L. This information was added to the Material and Methods section (line 387). Under our experimental conditions, ERK activation was not observed with hypotonic 70 % nor 50% osmolarity solution (Fig.S2).

It is therefore unlikely that the main cause of ERK activation upon high K⁺ perfusion is due to cell volume change. We would like to pursue this issue further when we obtain capacity to measure accurate cell volume change in the future.

(2) Some more details about the experimental design and the results are needed from Figure 1:

(i) For how long are the cells serum-starved? From the Methods section, it seems like the G1 release in different K+ concentration is done without serum, is this correct? Is the prior thymidine treatment also performed in the absence of serum?

Only the high K⁺ incubation phase was serum free. We added the following sentence in the main text (line 63) and an experimental diagram was added as Fig1A. “Cells were incubated in the presence of serum except for the phase with altered K⁺ concentration. “

(ii) There is a question of whether depolarization constitutes a physiologically relevant mechanism to regulate proliferation, and how depolarization interacts with other extracellular signals that might be present in an in vivo context.

This is a very important point. However, the significance of membrane depolarization for cell proliferation in vivo is beyond the scope of this study. This important question will be addressed in the future.

Does depolarization only promote proliferation after extended serum starvation (in what is presumably a stressed cell state)?

Cells were cultured in the presence of serum prior to the high K⁺ incubation phase as described above. We added a new figure (Fig1A).

What fraction of total cells are observed to be mitotic (without normalization), and how does this compare to the proliferation of these cells growing in serum-supplemented media? Can K+ concentration tune proliferation rate even in serum-supplemented media?

We included data recorded in serum-supplemented conditions (Fig.1), which showed a high mitotic rate. This is presumably due to the growth factors included in serum. There is no significant difference between 5K+FBS and 15K+FBS.

(3) In Figure 2, there are some possible concerns with the perfusion experiment:

(i) Is the buffer static in the period before perfusion with high K+, or is it perfused? This is not clear from the Methods. If it is static, how does the ERK activity change when perfused with 5 mM K+? In other words, how much of the response is due to flow/media exchange versus change in K+ concentration?

The buffer was static prior to high K perfusion. We confirmed that perfusion alone does not activate ERK (Fig.S2). We added the following sentence to the main text. “We also confirmed that the effect of perfusion was negligible, as ERK activation was not observed upon start of the 5K⁺ perfusion” (line 150).

(ii) Why do there appear to be population-average decreases in ERK activity in the period before perfusion with high K+ (especially in contrast to Fig. 3)? The imaging period does not seem frequent enough for photo bleaching to be significant.

Although we don’ t have a clear answer to this question, we speculate that several aspects of the experimental setup may have contributed to the difference. The cell lines and imaging systems used in Fig.2 and Fig.3 were different. The expression level may be different between U2OS cells and HEK 293 cells: transient expression in U2OS cells in contrast to stable expression in HEK 293 cells. This difference may lead to the different signal-to-noise ratio. The imaging system used in Fig.2 is an epi-illumination microscope excited with a 439/24 bandpass filter and detected with 483/32 (CFP) and 542/27 (YFP), while the imaging system used in Fig.3 is a confocal microscope excited with 458 nm laser and detected with 475-525 (DFP) and LP530 (YFP). These optical setups may also contribute to the different population-average properties before stimulation.

(4) Figure 3 contains important results on couplings between membrane potential and MAPK signaling. However, there are a few concerns:

(i) Does cell volume change upon voltage clamping? Previous authors have shown that depolarizing voltage clamp can cause cells to swell, at least in the whole-cell configuration: https://www.cell.com/biophysj/fulltext/S0006-3495(18)30441-7 . Could it be possible that the clamping protocol induces changes in ERK signaling due to changes in cell volume, and not by an independent mechanism?

We do not know whether cell volume is altered in the perforated-patch configuration. As discussed above, however, the effect of cell volume changes on ERK activity seemed to be negligible, because ERK activation was not observed with hypotonic 70 % nor 50% osmolarity solution (Fig.S2)

(ii) Does the -80 mV clamp begin at time 0 minutes? If so, one might expect a transient decrease in sensor FRET ratio, depending on the original resting potential of the cells. Typical estimates for resting potential in HEK293 cells range from -40 mV to -15 mV, which would reach the range that induces an ERK response by depolarizing clamp in Fig. 3B. What are the resting potentials of the cells before they are clamped to -80 mV, and why do we not see this downward transient?

We set the potential to -80mV immediately after the giga-seal formation and waited for at least 5 minutes to allow pore formation by gramicidin. We started imaging only after membrane potential was expected to have reached a steady state at -80 mV. We now included this sentence in the ‘Material and Methods’ section (line 398).

(5) The activation of ERK by perforated voltage clamp and by high extracellular K+ are each convincing, but it is unclear whether they need to act purely through the same mechanism - while additional extracellular K+ does depolarize the cell, it could also be affecting function of voltage-independent transporters and cell volume regulatory mechanisms on the timescales studied. To more strongly show this, the following should be done with the HEK cells where there is already voltage clamp data:

(i) Measure resting potential using the perforated patch in zero-current configuration in the high K+ medium. Ideally this should be done in the time window after high K+ addition where ERK activation is observed (10-20 minutes) to minimize the possibility of drift due to changes in transporter and channel activity due to post-translational regulation.

We measured membrane potential in the perforated patch configuration and confirmed that there is negligible potential drift within 20 minutes of perfusion with 145 K+ (only 1~5 mV change during perfusion).

(ii) Measure YFP/CFP ratio of the HEK cells in the high K+ medium (in contrast to the U2OS cells from Fig. 2 where there is no patch data).

YFP/CFP ratio data in HEK cells are shown in Fig.S1. As the signal-to-noise level is affected by the expression level of the probe, it is difficult to compare between cells with different expression levels. A higher YFP/CFP value with HEK cells compared to HeLa cells and A431 cells (Sup1) does not necessarily mean that HEK cells have higher ERK activity.

(iii) The assertion that high K+ is equivalent to changes in Vmem for ERK signaling would be supported if the YFP/CFP change from K+ addition is comparable to that induced by voltage clamp to the same potential. This would be particularly convincing if the experiment could be done with each of the 15 mM, 30 mM, and 145 mM conditions.

The experimental system using fluorescent biosensor cannot measure absolute ERK activity and can only measure the amount of change after a specific stimulus compared to the period before the stimulus. In electrophysiology experiments, the pre-stimulation membrane potential was clamped to -80 mV, whereas in the perfusion experiment, the membrane potential was variable in individual cells (-35 to -15 mV). It is therefore difficult to compare the results of electrophysiology experiments with those of the perfusion system. Unlike ion channels, it is currently not possible to plot absolute ERK activity with respect to the overall membrane potential. In the present study, we therefore discussed the change rather than the absolute value of ERK activity.

(6) Line 170: "ERK activity was reduced with a fast time course (within 1 minute) after repolarization to -80 mV." I don't see this in the data: in Fig. 3C, it looks like ERK remains elevated for > 10 min after the electrical stimulus has returned to -80 mV

Thank you for pointing out that our description was confusing. We changed the sentence to clarify the point we wanted to make. It now reads as follows. “ERK activity showed signs of reduction within 1 minute after repolarization to -80 mV.” (line 174)

Reviewer #3 (Public review):

Summary:

This paper demonstrates that membrane depolarization induces a small increase in cell entry into mitosis. Based on previous work from another lab, the authors propose that ERK activation might be involved. They show convincingly using a combination of assays that ERK is activated by membrane depolarization. They show this is Ca2+ independent and is a result of activation of the whole K-Ras/ERK cascade which results from changed dynamics of phosphatidylserine in the plasma membrane that activates K-Ras. Although the activation of the Ras/ERK pathway by membrane depolarization is not new, linking it to an increase in cell proliferation is novel.

Strengths

A major strength of the study is the use of different techniques - live imaging with ERK reporters, as well as Western blotting to demonstrate ERK activation as well as different methods for inducing membrane depolarization. They also use a number of different cell lines. Via Western blotting the authors are also able to show that the whole MAPK cascade is activated.

Weaknesses

A weakness of the study is the data in Figure 1 showing that membrane depolarization results in an increase of cells entering mitosis. There are very few cells entering mitosis in their sample in any condition. This should be done with many more cells to increase confidence in the results.

We apologize that that description was not clear. Due to the limited number of conditions that can be conducted as a single experiment, we always included control condition (i.e. 5K) and performed normalization by comparing with the control condition of the initial 1.5 hrs. Data were from 100-900 mitotic cell counts within 6hr of the imaging time window. We re-wrote the figure legend (Fig1) and the main text.

The study also lacks a mechanistic link between ERK activation by membrane depolarization and increased cell proliferation.

The present study focused on the link between membrane potential and the ERK activity; the mechanistic link between ERK activity and cell proliferation is beyond the scope of the present study. This important topic will be pursued further in subsequent studies.

The authors did achieve their aims with the caveat that the cell proliferation results could be strengthened. The results for the most part support the conclusions.

This work suggests that alterations in membrane potential may have more physiological functions than action potential in the neural system as it has an effect on intracellular signalling and potentially cell proliferation.

Reviewer #1 (Recommendations for the authors):

minor typo:

ERK activity has voltage-dependency with the physiological rang of membrane potential should be "range"

Corrected

Reviewer #2 (Recommendations for the authors):

Small points:

Line 82: rang -> range

Corrected

Line 102: ". they were stimulated" -> ". The cells were stimulated"

Corrected

Figs. 2C, 2D show exactly the same data points and the same information. Please cut one of these figures.

We deleted 2C and added the information in 2D and made new Fig.2C.

For all figs: Please indicate # of cells and # of independent dishes used in each experiment, and make clear whether individual data-points correspond to cells, dishes, or some other unit of measure.

We added the information in figure legends.

Reviewer #3 (Recommendations for the authors):

The authors should repeat the cell proliferation experiments with more cells to strengthen the data. They could also use alternative assays like phosphorylated histone H3 staining for cells in M phase, that might to easier to quantitate.

We repeated the experiment and Fig.1 was replaced with the new Fig.1

The authors should investigate how the upregulation of ERK is driving cells into mitosis. At what point in the cell cycle is activated ERK induced by membrane depolarization having the effect. Is it entry into mitosis or earlier in the cell cycle?

The cells were incubated with a high K+ solution 8-9 hr after G1 release, which is supposed to correspond to G2. These data suggest that mitotic activity is stimulated when ERK is activated at G2. However, we lack conclusive data at present to show the consequence of ERK activation during G2. We therefore cannot pinpoint the stage of cell cycle where depolarization-activated ERK exerts its effect.

The authors refer a lot to the work of Zhou et al 2015 throughout the paper. This is not necessary and is a bit distracting.

We deleted several sentence from the manuscript.

eLife Assessment

This useful paper presents evidence from several experimental approaches that suggest that changes in membrane potential directly affect ERK signaling to regulate cell division. This result is relevant because it supports an ion channel-independent pathway by which changes in membrane voltage can affect cell growth. The reviewers point out that while some experimental results and interpretations are compelling, the strength of evidence is still incomplete and changes to the manuscript are needed to rule out other possible interpretations of the data.

eLife Assessment

This is a fundamental study providing molecular insight into how cross-talk between histone modifications regulates the histone H3K36 methyltransferase SETD2. The manuscript contains excellent quality data, and the conclusions are convincing and justified. This work will be of interest to many biochemists working in the field of chromatin biology and epigenetics.

Reviewer #1 (Public review):

Summary:

In this manuscript, Mack and colleagues investigate the role of posttranslational modifications, including lysine acetylation and ubiquitination, in methyltransferase activity of SETD2 and show that this enzyme functions as a tumor suppressor in a KRASG12C-driven lung adenocarcinoma. In contrast to H3K36me2-specific oncogenic methyltransferases, the deletion of SETD2, which is capable of H3K36 trimethylation, increases lethality in a KRASG12C-driven lung adenocarcinoma mouse tumor model. In vitro, the authors demonstrate that polyacetylation of histone H3, particularly of H3K27, H3K14 and H3K23, promotes the catalytic activity of SETD2, whereas ubiquitination of H2A and H2B has no effect.

Strengths:

Overall, this is a well-designed study that addresses an important biological question regarding the functioning of the essential chromatin component. The manuscript contains excellent quality data, and the conclusions are convincing and justified. This work will be of interest to many biochemists working in the field of chromatin biology and epigenetics.

Comments on revisions:

All previous comments are well addressed, and I enthusiastically support publication.

Reviewer #2 (Public review):

Summary:

Human histone H3K36 methyltransferase Setd2 has been previously shown to be a tumor suppressor in lung and pancreatic cancer. In this manuscript by Mack et al., the authors first use a mouse KRASG12D-driven lung cancer model to confirm in vivo that Setd2 depletion exacerbates tumorigenesis. They then investigate the enzymatic regulation of the Setd2 SET domain in vitro, demonstrating that H2A, H3, or H4 acetylation stimulates Setd2-SET activity, with specific enhancement by mono-acetylation at H3K14ac or H3K27ac. In contrast, histone ubiquitination has no effect. The authors propose that H3K27ac may regulate Setd2-SET activity by facilitating its binding to nucleosomes. This work provides insight into how cross-talk between histone modifications regulates Setd2 function.

Comments on revisions:

(1) Regarding New Figure 2F lane 1, please reference PMID: 33972509 Fig 4D bottom. Setd2-SET is a well-known robust K36 trimethylase. Why, under the authors' conditions, do WT nucleosomes show a significant amount of K36me1 and K36me2 accumulation, whereas K36me3 is not as pronounced? As a comparison, the authors should also report the evidence for the efficiency of each chemical modification that generates K36 methylation mimic.

(2) The bottom panel of Figure 2B does not match the top one; the number of repeats should be indicated in the figure legends.

(3) In Figure 4E, the differences between Setd2-bound WT and acetylated nucleosomes are minimal, as judged by both the decreasing trend of unbound nucleosomes and the increasing trend of bound fractions. This experiment needs to be quantified based on multiple repeats.

Author response:

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

Reviewer #1 (Public review):

(1) Labels should be added in the Figures and should be uniform across all Figures (some are distorted).

We thank the Reviewer for pointing out this issue. As requested, labels have been edited to ensure they are legible and are consistent in font, size, and style.  

Reviewer #2 (Public review):

(1) As for Figure 2F, Setd2-SET activity on WT rNuc (H3) appears to be significantly lower compared to what is extensively reported in the literature. This is particularly puzzling given that Figure 2B suggests that using 3H-SAM, H3-nuc are much better substrates than K36me1, whereas in Figure 3F, rH3 is weaker than K36me1. It is recommended for the authors to perform additional experimental repeats and include a quantitative analysis to ensure the consistency and reliability of these findings.  

We appreciate the Reviewer’s points. We respectfully suggest that these comments may reflect potential confusion around interpreting how different assays detect in vitro methylation, what data can and cannot be compared, and the nature of the different substrates used. 

With respect to point 1 (Western signal significantly lower compared to extensive literature): To the best of our knowledge, it would be extremely challenging to make a quantitative argument comparing the strength of the Western signal in Figure 2F with results reported in the literature. Specifically, comparing our results with previous studies would require (1) all the studies to have used the exact same antibodies as antibody signal intensities vary depending on the specific activity and selectively of a particular antibody and even its lot number, (2) similar in vitro methylation reaction condition, (3) the same type of recombinant nucleosomes used, and so on. Further, given that these are Western blots, we do not understand how one could interpret an absolute activity level. In the figure, all we can conclude is that in in vitro methylation reactions, our recombinant SETD2 protein methylates rNucs to generate mono-, di-, and tri-methylation at K36 (using vetted antibodies (see Fig. 2e)). If there is a specific paper within the extensive literature that the Reviewer highlights, we could look more into the details of why the signals are different (our guess is that any difference would largely be due to the use of different antibodies). We add that it might be challenging to find a similar experiment performed in the literature; we are not aware of a similar experiment. 

With respect to comparing Figure 2B and 2F: We do not understand how one can meaningfully compare incorporation of radiolabeled SAM to antibody-based detection on film using an antibody against specific methyl states. In particular, regarding the question regarding comparing rH3 vs H3K36me1 nucleosomes, we point out that in using recombinant nucleosomes installed with native modifications (e.g. H3K36me1), in which the entire population of the starting material is mono-methylated, then naturally the Western signal with an anti-H3K36me1 antibody will be strong. In Fig. 2b, the assay is incorporation of radiolabeled methyl, which is added to the preexiting mono-methylated substrate. In other words, the results are entirely consistent if one understands how the methylation reactions were performed, how methylation was detected, and the nature of the reagents.

(2) The additional bands observed in Figure 4B, which appear to be H4, should be accompanied by quantification of the intensity of the H3 bands to better assess K36me3 activity. Additionally, the quantification presented in Figure 4C for SAH does not seem accurate as it potentially includes non-specific methylation activity, likely from H4. This needs to be addressed for clarity and accuracy. 

We thank the reviewer for this comment. The additional bands observed in Figure 4B represent degradation products of histone H3, not H4 methylation. This is commonly seen in in vitro reactions using recombinant nucleosomes, where partial proteolysis of H3 can occur under the assay conditions.  

(3) In Figure 4E, the differences between bound and unbound substrates are not sufficiently pronounced. Given the modest differences observed, authors might want to consider repeating the assay with sufficient replicates to ensure the results are statistically robust.

In Figure 4E, we observe a clear difference between the bound and unbound substrate. To aid interpretation, we have clarified in the figure where the bound complex migrates on the gel, while the unbound nucleosomes migrate at the bottom of the gel. The differences are indeed subtle, which we highlight in the text.  

(4) Regarding labeling, there are multiple issues that need correction: In the depiction of Epicypher's dNuc, it is crucial to clearly mark H2B as the upper band, rather than ambiguously labeling H2A/H2B together when two distinct bands are evident. In Figure 3B and D, the histones appear to be mislabeled, and the band corresponding to H4 has been cut off. It would be beneficial to refer to Figure 3E for correct labeling to maintain consistency and accuracy across figures. 

Thank you for pointing this out. To avoid any confusion, we have delineated the H2B and H2A markers and indicate the band corresponding to H4.

(5) There are issues with the image quality in some blots; for instance, Figure 2EF and Figure 2D exhibit excessive contrast and pixelation, respectively. These issues could potentially obscure or misrepresent the data, and thus, adjustments in image processing are recommended to provide clearer, more accurate representations. 

Contrast adjustments were applied uniformly across each entire image and were not used to modify any specific region of the blot. We have corrected the issue of increased pixelation in Figure 2D. 

(6) The authors are recommended to provide detailed descriptions of the materials used, including catalog numbers and specific products, to allow for reproducibility and verification of experimental conditions. 

We have added the missing product specifications and catalog numbers to ensure clarity and reproducibility of the experiments.

(7) The identification of Setd2 as a tumor suppressor in KrasG12C-driven LUAD is a significant finding. However, the discussion on how this discovery could inspire future therapeutic approaches needs to be more balanced. The current discussion (Page 10) around the potential use of inhibitors is somewhat confusing and could benefit from a clearer explanation of how Setd2's role could be targeted therapeutically. It would be beneficial for the authors to explore both current and potential future strategies in a more structured manner, perhaps by delineating between direct inhibitors, pathway modulators, and other therapeutic modalities. 

SETD2 is a tumor suppressor in lung cancer (as we show here and many others have clearly established in the literature) and thus we would recommend avoiding a SETD2 inhibitor to treat solid tumors, as it could have a very much unwanted affect.  Our discussion addresses a different point regarding the relative importance of the enzymatic activity versus other, nonenzymatic functions of SETD2. We believe that a detailed exploration of the therapeutic potential of inhibiting SETD2 would be better suited in a review or a more therapy-focused manuscript.

eLife Assessment

This study identifies novel approaches to improving transgene expression in the injured mammalian myocardium through a combination of a tissue regeneration enhancer element and engineered AAVs - specifically, a liver-detargeting capsid, AAV.cc84, and an in vivo library screen-selected AAV-IR41. The evidence is convincing, and the AAV vectors are of fundamental value to the field of cardiac gene therapy. Future research exploring how to combine the features of AAV.cc84 and AAV-IR41 could yield an even more promising vector for therapeutic use.

Reviewer #1 (Public review):

In this manuscript, Wolfson and co-authors demonstrate a combination of an injury-specific enhancer and engineered AAV that enhances transgene expression in injured myocardium. The authors characterize spatiotemporal dynamics of TREE-directed AAV expression in the injured heart using a non-invasive longitudinal monitoring system. They show that transgene expression is drastically increased 3 days post-injury, driven by 2ankrd1a. They reported a liver-detargeted capsid, AAV cc.84, with decreased viral entry into the liver while maintaining TREE transgene specificity. They further identified the IR41 serotype with enhanced transgene expression in injured myocardium from AAV library screening. This is an interesting study that optimizes the potential application of TREE delivery for cardiac repair.

Comments on revisions:

The authors are responsive and have addressed my concerns.

Reviewer #2 (Public review):

Summary:

In this manuscript by Wolfson et al., various adeno-associated viruses (AAVs) were delivered to mice to assess the cardiac-specificity, injury border-zone cardiomyocyte transduction rate, and temporal dynamics in the goal to find better AAVs for gene therapies targeting the heart. The authors delivered tissue regeneration enhancer elements (TREEs) controlling luciferase expression and used IVIS imaging to examine transduction in the heart and other organs. They found that luciferase expression increased in the first week after injury when using AAV9-TREE-Hsp68 promoter, waning to baseline levels by 7 weeks. However, AAV9 vectors transduced the liver, which was significantly reduced by using an AAV.cc84 liver de-targeting capsid. The authors then performed in vivo screening of AAV9 capsids and found AAV-IR41 to preferentially transduce injured myocardium when compared to AAV9. Finally, the authors combined TREEs with AAV-IR41 to show improved luciferase expression compared to AAV9-TREE at 7, 14 and 21 days after injury.

Overall, this manuscript provides insights into TREE expression dynamics when paired with various heart-targeting capsids, which can be useful for researchers studying ischemic injury of murine hearts. While the authors have shown the success of using AAV9-TREEs in porcine hearts, it is unknown whether the expression dynamics would be similar in pigs or humans, as mentioned in the limitations.

Strengths:

Important contribution to the AAV gene therapy literature.

Comments on revised version:

My concerns have been adequately addressed.

Reviewer #3 (Public review):

Summary:

The tissue regeneration enhancer elements (TREEs) identified in zebrafish have been shown to drive injury-activated temporal-spatial gene expression in mice and large animals. These findings increase the translational potential of findings in zebrafish to mammals. In this manuscript, the authors tested TREEs in combination with different adeno-associated viral (AAV) vectors using in vivo luciferase bioluminescent imaging that allows for longitudinal tracking. The TREE-driven luciferase delivered by a liver de-targeted AAV.cc84 decreased off-target transduction in liver. They further screened an AAV library to identify capsid variants that display enhanced transduction for infarcted myocardium post ischemia reperfusion and myocardial infarction. A new capsid variant, AAV.IR41, was found to show increased transduction post I/R and MI.

Strengths:

The authors injected AAV-cargo several days after ischemia/reperfusion (I/R) injury as a clinically relevant approach. Overall, this study is significant in that it identifies new AAV vectors that can be used to deliver promising genes as potential new gene therapies in the future. The manuscript is well-written and the data are also of high quality.

Weaknesses:

The authors have addressed my previous concerns.

Author response:

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

Reviewer #1 (Public review):

In this manuscript, Wolfson and co-authors demonstrate a combination of an injury-specific enhancer and engineered AAV that enhances transgene expression in injured myocardium. The authors characterize spatiotemporal dynamics of TREE-directed AAV expression in the injured heart using a non-invasive longitudinal monitoring system. They show that transgene expression is drastically increased 3 days post-injury, driven by 2ankrd1a. They reported a liver-detargeted capsid, AAV cc.84, with decreased viral entry into the liver while maintaining TREE transgene specificity. They further identified the IR41 serotype with enhanced transgene expression in injured myocardium from AAV library screening. This is an interesting study that optimizes the potential application of TREE delivery for cardiac repair. However, several concerns were raised prior to publication:

Major Concerns:

(1) In Figure 1, the authors demonstrated that 2andkrd1aEN is not responsive to sham injury after AAV delivery, but Figure 3 shows a strong response to sham when AAV is delivered after injury. The authors do not provide an explanation for this observation.

This discrepancy is due to the timing of AAV delivery. In Figure 1, AAV was delivered 60 days prior to IVIS imaging and cardiac injury, allowing time for the baseline level of AAV transgene expression to reach a plateau. From this baseline level, we were able to measure fold change in luminescence signal before and after cardiac injury. In Figure 3, AAV was delivered 4 days after cardiac injury. Luminescence in the heart was measured 3 days later (day 7), when the baseline of AAV transgene expression is still building. The data from Figure 1C-D inform us that the 2ankrd1aEN response to cardiac injury peaks within the first week and returns to baseline levels after 5-7 weeks. In Figure 3E, we show that 2ankrd2aEN provides a baseline level of expression that is present in sham hearts and reaches its plateau after 6 weeks. In contrast, I/R injured hearts show enhanced expression in the first 3-4 weeks, corresponding with the dynamics of 2ankrd1aEN’s response to injury observed in Figure 1C. We have now included a phrase in the revised manuscript on p. 7, paragraph 1 to clarify.

(2) In Figure 4, a higher GFP signal is observed in all areas of the heart of the IR41-treated mouse compared to AAV9. The authors should compare GFP expression between AAV9 and IR41 in uninjured hearts and provide insights into enhanced cardiac tropism to confirm that IR41 is MI injury enriched, not Sham as well.

We sought to address this question with the experiments presented in Figure 5. We treated sham mice with AAV9 and IR41 containing 2ankrd1aEN. Figure 5D showed IR41 delivered more vector genomes to the sham heart on average, though not with a p-value less than 0.05 compared with AAV9. In Supplemental Figure 5B, IR41 also provided higher luminescence at day 7 post-sham but was comparable at day 14 and day 21. These data suggest IR41 might increase heart tropism in healthy hearts, but IR41’s effect is most dramatic when delivered to injured hearts, where cardiac vector genomes are highest (Figure 5D). We have now included a sentence in the revised manuscript on p. 8, paragraph 2 to clarify.

(3) The authors should clarify which model is being used between myocardial infarction (MI) and Ischemia-reperfusion (IR) throughout the figures, as the experimental schemes and figure legends did not match with each other (MI or IR in Figure 1A, 1D, 3A, and 3E). Both models cause different types of injuries. The authors should explain the difference in TREE expression in both models.

We have revised the figures to specify the model, where I/R or MI is used.

(4) In Figure 2, the authors use REN instead of 2ankrd1aEN to demonstrate liver-detargeting using AAV cc.84. Is there a specific reason?

Our data in Figure 1 informed us that off-target liver expression is more specifically an issue for REN compared to 2ankrd1aEN. Baseline levels of luminescence in the heart could not be as clearly marked due to off-target expression in the liver, which was showcased in Figure 2B with AAV9 delivery to sham mice. As discussed above, 2ankrd1aEN provided stronger baseline levels of expression of the heart which could be more clearly marked in IVIS images for tracking fold changes over time. For these reasons, we sought to explore how incorporation of the AAV.cc84 capsid could be utilized to minimize off-target liver expression. We have now included a sentence in the revised manuscript on p. 5, paragraph 3 to clarify.

Reviewer #2 (Public review):

In this manuscript by Wolfson et al., various adeno-associated viruses (AAVs) were delivered to mice to assess the cardiac-specificity, injury border-zone cardiomyocyte transduction rate, and temporal dynamics, with the goal of finding better AAVs for gene therapies targeting the heart. The authors delivered tissue regeneration enhancer elements (TREEs) controlling luciferase expression and used IVIS imaging to examine transduction in the heart and other organs. They found that luciferase expression increased in the first week after injury when using AAV9-TREE-Hsp68 promoter, waning to baseline levels by 7 weeks. However, AAV9 vectors transduced the liver, which was significantly reduced by using an AAV.cc84 liver de-targeting capsid. The authors then performed in vivo screening of AAV9 capsids and found AAV-IR41 to preferentially transduce injured myocardium when compared to AAV9. Finally, the authors combined TREEs with AAV-IR41 to show improved luciferase expression compared to AAV9-TREE at 7, 14, and 21 days after injury.

Overall, this manuscript provides insights into TREE expression dynamics when paired with various heart-targeting capsids, which can be useful for researchers studying ischemic injury of murine hearts. While the authors have shown the success of using AAV9-TREEs in porcine hearts, it is unknown whether the expression dynamics would be similar in pigs or humans, as mentioned in the limitations.

The following questions and concerns can be addressed to improve the manuscript:

(1) From the IVIS data, it seems that the Hsp68 promoter might not be "normally silent in mouse tissues," specifically in the liver (Figure S1B). Are there any other promoters that can be combined with TREEs to induce cardiac-injury specific expression while minimizing liver expression? This could simplify capsid design to focus on delivery to injured areas.

Indeed we found the Hsp68 promoter does provide low levels of baseline expression, especially in the liver of mice. The Hsp68 promoter was initially chosen due to its permissive nature allowing for assessment of expression directed by TREEs. Many or most groups use the Hsp68 promoter for enhancer tests in mice, but we agree that other permissive promoters might have lower baseline levels of expression and might have the benefit of smaller size. We have not rigorously tested other permissive promoters in our experiments.

(2) Why is it that AAV9-TREE-Hsp68-Luc wane in expression (Figure 1C and 1D), whereas AAV.cc84-TREE-Hsp68-Luc expresses stably for over 2 months (3E)? This has important implications for the goal of transience in gene delivery.

Please see our response to reviewer 1’s comment #1 above.

(3) AAV-IR41 was found to transduce cardiomyocytes in the injured zone. However, this capsid also shows a very strong off-target liver expression. From a capsid design perspective, is it possible to combine AAV-cc84 and AAV-IR41?

This approach is in theory possible as these epitopes are structurally distinct. However, since the mechanism (receptor usage) is currently unknown, it would not be possible to predict whether the properties are mutually exclusive. Further, we would need to ensure that combining modifications does not impact vector yield. We can explore such features with next generation candidates as we continue to improve the platform. We have now included a sentence in the revised manuscript on p. 9, paragraph 3, mentioning the possibility of combining the two capsid mutations.

(4) It would be helpful to see immunostaining for the various time points in Figure 5. Is it possible to use an anti-luciferase antibody (or AAV-TREE-Hsp68-eGFP) to compare the two TREE capsids?

We were not able to do immunostaining of luciferase expression, because the biopsied hearts were used to quantify vector genomes via qPCR. We have previously reported results of immunostaining of EGFP expression directed by 2ankrd1aEN in I/R-injured mouse hearts (Yan et al., 2023), which we expect to match the expression seen in these experiments.

Reviewer #3 (Public review):

Summary:

The tissue regeneration enhancer elements (TREEs) identified in zebrafish have been shown to drive injury-activated temporal-spatial gene expression in mice and large animals. These findings increase the translational potential of findings in zebrafish to mammals. In this manuscript, the authors tested TREEs in combination with different adeno-associated viral (AAV) vectors using in vivo luciferase bioluminescent imaging that allows for longitudinal tracking. The TREE-driven luciferase delivered by a liver de-targeted AAV.cc84 decreased off-target transduction in the liver. They further screened an AAV library to identify capsid variants that display enhanced transduction for myocardium post-myocardial infarction. A new capsid variant, AAV.IR41, was found to show increased transduction at the infarct border zones.

Strengths:

The authors injected AAV-cargo several days after ischemia/reperfusion (I/R) injury as a clinically relevant approach. Overall, this study is significant in that it identifies new AAV vectors for potential new gene therapies in the future. The manuscript is well-written, and their data are also of high quality.

Weaknesses:

The authors might be using MI (myocardial infarction) and I/R injury interchangeably in their text and labels. For instance, "We systemically transduced mice at 4 days after permanent left coronary artery ligation with either AAV9 or IR41 harboring a 2ankrd1aEN-Hsp68::fLuc transgene. IVIS imaging revealed higher expression levels in animals transduced with IR41 compared to AAV9, in both sham and I/R groups (Fig. 5A)". They should keep it consistent. There is also no description for the MI model.

We have adjusted figure labels and main text to ensure the injury model is described correctly.

We have also addressed all additional Recommendations for the authors, which requested minor modifications to figures like error bars and image annotation.

eLife Assessment

This important study provides a conceptual advance in our understanding of how membrane geometry modulates the balance between specific and non-specific molecular interactions, reversing multiphase morphologies in postsynaptic protein assemblies. Using a mesoscale simulation framework grounded in experimental binding affinities, the authors successfully recapitulate key experimental observations in both solution and membrane-associated systems, providing novel mechanistic insight into how spatial constraints regulate postsynaptic condensate organization. The conclusions are supported by solid strength of evidence and the findings are of broad significance for both computational and experimental biologists

Reviewer #2 (Public review):

This is a timely and insightful study aiming to explore the general physical principles for the sub-compartmentalization--or lack thereof--in the phase separation processes underlying the assembly of postsynaptic densities (PSDs), especially the markedly different organizations in three-dimensional (3D) droplets on one hand and the two-dimensional (2D) condensates associated with a cellular membrane on the other. Simulation of a highly simplified model (one bead per protein domain) is apparently carefully executed. Based on a thorough consideration of various control cases, the main conclusion regarding the trade-off between repulsive excluded volume interactions and attractive interactions among protein domains in determining the structures of 3D vs 2D model PSD condensates is quite convincing. The novel results in this manuscript should be published.

Comment on the revised manuscript:

The authors have adequately addressed all my previous concerns. The manuscript is now much improved, ready for publication as a version of record.

Reviewer #3 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

The biggest weakness of the study, in my opinion, has been a lack of more in-depth and quantitative physical insights about phase separation theories. In the revised version, the authors have added text to point the interested reader to the respective theories, and have included a qualitative assessment of their findings in the light of said theories. This better positions their discussion. I still believe the role of entropic effects need more attention, which can be the subject of future studies.

The authors have revised their Introduction and added text to the Discussion, to enrich their view on the attractive and repulsive forces as well as mixing entropy. This version better covers the physics of phase separation.

I appreciate the added discussion about the different diffusive behavior in the membrane in contrast to the bulk (i.e. the Saffman-Delbrück model). This paves the way for future studies, including realistic kinetics of the studied system.

Author response:

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

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

We thank the reviewer for his/her time and effort to our manuscript. We agree with the point that the contribution of other synaptic components should be addressed. We have included a discussion of the effects of environmental factors such as protein and ion concentrations, as well as other omitted postsynaptic components (SAPAP, Shank, and Homer) on phase morphology. In the middle of the 2^nd paragraph of Discussion, we added: 

“While these in vivo results contain additional scaffold and cytoskeletal elements omitted in our model, such as SAPAP, Shank and Homer, nearly all proteins in the middle and lower layers of the PSD associate directly or indirectly with PSD-95 in the upper PSD layer. Consequently, it is probable that other scaffold proteins contribute to the mobility of AMPAR-containing and NMDAR-containing nanodomains indistinguishably. They may increase the stability of the AMPAR and NMDAR clusters but are unlikely to have a distinct effect to reverse the phase-separation phenomenon.”

Also, as the reviewer pointed out, we agree with that physiological factors such as ion concentration may influence the phase. However, conditions such as ion concentration are implicitly implemented as the specific and nonspecific interactions in this model, which makes it difficult to estimate the effect of each physiological condition individually. We added the variability potential of physiological conditions to the discussion section as a limitation of this model. To investigate parameter sensitivity in more detail, we performed additional MD simulations with weakened membrane constraints to account for the behavior between 3D and 2D. We added:

“First, our results did not provide direct insights to physiological conditions, such as ion concentrations. Since such factors are implicitly implemented in our model, it is difficult to estimate these effects individually. This suggests the need for future implementation of environmental factors and validation under a broader range of in vivo-like settings.”

Reviewer #2 (Public review):

This is a timely and insightful study aiming to explore the general physical principles for the sub-compartmentalization--or lack thereof--in the phase separation processes underlying the assembly of postsynaptic densities (PSDs), especially the markedly different organizations in three-dimensional (3D) droplets on one hand and the twodimensional (2D) condensates associated with a cellular membrane on the other. Simulation of a highly simplified model (one bead per protein domain) is carefully executed. Based on a thorough consideration of various control cases, the main conclusion regarding the trade-off between repulsive excluded volume interactions and attractive interactions among protein domains in determining the structures of 3D vs 2D model PSD condensates is quite convincing. The results in this manuscript are novel; however, as it stands, there is substantial room for improvement in the presentation of the background and the findings of this work. In particular,

(i) conceptual connections with prior works should be better discussed 

(ii) essential details of the model should be clarified, and

(iii) the generality and limitations of the authors' approach should be better delineated.

We appreciate the reviewer for his/her time and effort on our manuscript and for encouraging comments and helpful suggestions. We answered every technical comment the reviewer mentioned below.

Specifically, the following items should be addressed (with the additional references mentioned below cited and discussed):

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

Thank you for this comment. We have substituted the words “excluded volume interactions” for words of similar meaning. However, we have left the expression of “non-specific interactions” as they are referring to explicit interactions that are given as force fields in the model, rather than in the general meaning of excluded volume effect.

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

We appreciate the reviewer’s insightful comment. We have now included a more detailed discussion on excluded volume effect in the revised manuscript, which provides important context for our findings. Furthermore, we have cited the references to support and enrich the discussion, as recommended.

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

We agree that phosphorylation effect on phase separation is an important and interesting aspect to consider. Some experimental results have shown that activation of CaMKII can lead to phosphorylation of various proteins and make PSD condensate more stable by altering their interactions. We included the sentence below in limitations:

“In this context, we also do not explicitly account for downstream phosphorylation events. Although such proteins are not included in the current components, they will regulate PSD-95, affecting its binding valency, or diffusion coefficient. This is a subject worthy of future research.”

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

We thank the reviewer for the helpful recommendation. We have revised the manuscript to include membrane-mimicking potential on main text. Furthermore, we also think that exploring the shape of the 3D/2D condensate phase due to the sensitivity of confinement is a very interesting point. We have additionally performed MD simulations with smaller/larger membrane constraints and included the results in supporting information as Figure S5. The following parts are added:

“We further attempted to mimic intermediate conditions between 3D and 2D systems in two different manners. First, we applied a weaker membrane constraint in 2D system. Even when the strength of membrane constraints is reduced by a factor of 1000, NMDARs are located on the inner side when the CaMKII was active, as well as the result in 2D system (Fig.S5ABC). Second, to weaken further the effect of membrane constraints, we artificially altered the membrane thickness from 5 nm to 50 nm, in addition to reducing the membrane constraints by 1000. As a result, NMDAR clusters move to the bottom and surround AMPAR (Fig.S5DEF). In this artificial intermediate condition, both states in which the NMDARs are outside (corresponding to 3D) and in which the NMDARs are inside (corresponding to 2D) are observed, depending on the strength of the membrane constraint.”

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

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

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

We sincerely appreciate the reviewer’s comments. According to the recommendation, we have changed the diagram in Figure 1B into interaction matrix with each mesoscale molecular representation and the expression in main text to be clearer about AMPAR and TARP, and about the relationship between NMDAR and GluN2Bc. Former diagram of the pairs of specific interaction is moved to supplementary figure. 

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

We thank the reviewer for the comment. As pointed out, the multiphase morphology change observed in this study can be attributed to a decrease in coordination number in 2D compared to 3D. We have included the physicochemical rationalization in the discussion.  

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

We are grateful to the reviewer for highlighting this important point. We agree with that the real PSD forms 3D condensates beneath the 2D membrane. Some lower PSD components under the membrane (i.e. SAPAP, Shank, and Homer) are omitted in our system, which may cause a weak condensation. To emphasize this, we have added the following sentence:

“While these in vivo results contain additional scaffold and cytoskeletal elements omitted in our model, such as SAPAP, Shank and Homer, nearly all proteins in the middle and lower layers of the PSD associate directly or indirectly with PSD-95 in the upper PSD layer. Consequently, it is probable that other scaffold proteins contribute to the mobility of AMPAR-containing and NMDAR-containing nanodomains indistinguishably. They may increase the stability of the AMPAR and NMDAR clusters but are unlikely to have a distinct effect to reverse the phase-separation phenomenon.”

However, we believe that the clusters formed on the 2D membrane are not a robust “phase” because they do not follow scaling law. In fact, in our previous study of PSD system with AMPAR(TARP)₄ and PSD-95, we have already reported that phase separation is less likely to occur in 2D than in 3D. The previous result suggests that phase separation on membrane may be difficult to achieve, which is consistent with the results of this study.

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

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

We thank the reviewer for the helpful recommendation. We have added the recommended references in each relevant part in introduction, respectively.

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

We thank you for your comment. We replaced the word “vertical” with “perpendicular" in the main text and caption.

Reviewer #3 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

The biggest weakness of the study, in my opinion, has to do with a lack of more in-depth physical insight about phase separation. For example, the authors express surprise about similar interactions between components resulting in different phase separation in 2D and 3D. This is not surprising at all, as in 3D, higher coordination numbers and more available volume translate to lower free energy, which easily explains phase separation. The role of entropy is also significantly missing from the analyses. When interaction strengths are small, entropic effects play major roles. In the introduction, the authors present an oversimplified view of associative and segregative phase transitions based on the attractive and repulsive interactions, and I'm afraid that this view, in which all the observed morphologies should have clear pairwise enthalpic explanations, diffuses throughout the analysis. Meanwhile, I believe the authors correctly identify some relevant effects, where they consider specific/nonspecific interactions, or when they investigate the reduced valency of CaMKII in the 2D system.

We thank the reviewer for the insightful and constructive comments. Regarding the difference in phase behavior between 2D and 3D systems, we appreciate the reviewer’s clarification that differences in coordination number and entropy in higher dimensions can account for the observed morphology of the phases. While it may be clear that entropy decreases due to the decrease of coordination number, our objective was to uncover how such an isotropic entropy reduction regulates the behavior of each phase driven by different interactions, which remains largely unknown. To emphasize this, we modified the introduction and have now included a discussion of the entropic contributions to phase behavior in both 2D and 3D systems, and we have made this clearer in the revised manuscript by referencing relevant theoretical frameworks. In the Discussion, we added the sentence below:

“Generally, phase separation can be explained by the Flory-Huggins theory and its extensions: phase separation can be favored by the difference in the effective pairwise interactions in the same phase compared to those across different phases, and is disfavored by mixing entropy. The effective interactions contain various molecular interactions, including direct van der Waals and electrostatic interactions, hydrophobic interactions, and purely entropic macromolecular excluded volume interactions. For the latter, Asakura-Oosawa depletion force can drive the phase separation. Furthermore, the demixing effect was explicitly demonstrated in previous simulations and field theory (61). Importantly, we note that the effective pairwise interactions scale with the coordination number z. The coordination number is a clear and major difference between 3D and 2D systems. In 3D systems, large z allows both relatively strong few specific interactions and many weak non-specific interactions. While a single specific interaction is, by definition, stronger than a single non-specific interaction, contribution of the latter can have strong impact due to its large number. On the other hand, a smaller z in the membrane-bound 2D system limits the number of interactions. In case of limited competitive binding, specific interactions tend to be prioritized compared to non-specific ones. In fact, Fig. 3A clearly shows that number of specific interactions in 2D is similar to that in 3D, while that of non-specific interactions is dramatically reduced in 2D. In the current PSD system, CaMKII is characterized by large valency and large volume. In the 3D solution system, non-specific excluded volume interactions drive CaMKII to the outer phase, while this effect is largely reduced in 2D, resulting in the reversed multiphase.   

Also, I sense some haste in comparing the findings with experimental observations. For example, the authors mention that "For the current four component PSD system, the product of concentrations of each molecule in the dilute phase is in good agreement with that of the experimental concentrations (Table S2)." But the data used here is the dilute phase, which is the remnant of a system prepared at very high concentrations and allowed to phase separate. The errors reported in Table S2 already cast doubt on this comparison. 

We thank the reviewer for the insightful comment. In the validation process, we adjusted the parameters so that the number of molecules in dilute phase is consistent with the experimental lower limit of phase separation, based on the assumption that phase-separated dilute phase is the same concentration as the critical concentration. That is why we focus on comparing dilute phase concentration in Table S2. However, in our simulations, the number of protein molecules is relatively small since it is based on the average number per synapse spine. For example, there are only about 60 CaMKII molecules at most, and its presence in the dilute phase is highly sensitive to concentration, as the reviewer pointed out. This is one of the limitations, so we have added a description to the Limitations section. We added:

“Second, parameter calibration contains some uncertainty. Previous in vitro study results used for parameter validation are at relatively high concentrations for phase separation, which may shift critical thresholds compared to that in in vivo environments. Also, since the number of molecules included in the model is small, the difference of a single molecule could result in a large error during this validation process.”

Or while the 2D system is prepared via confining the particles to the vicinity of the membrane, the different diffusive behavior in the membrane, in contrast to the bulk (i.e., the Saffman-Delbrück model), is not considered. This would thus make it difficult to interpret the results of a coupled 2D/3D system and compare them to the actual system.

We appreciate the reviewer’s helpful comment. We agree with that there is a concern that the Einstein-Stokes equation does not adequately reproduce the diffusion of membrane-embedded particles. We recalculated the diffusion coefficients for every membrane particle used in this model using the Saffman-Delbrück model and found that diffusion coefficients for receptor cores (AMPAR and NMDAR) were approximately three times larger. These values are still about ~10 times smaller than that of molecules diffusing under the cytoplasm. Additionally, since this study focuses on the morphology of the phase/cluster at the thermodynamic equilibrium, we think that the magnitude of the diffusion coefficient has little influence on the final structure of the cluster. However, we will incorporate the membrane-embedded diffusion as a future improvement item for better modelling and implementation. We added:

“Third, we estimated all the diffusion coefficients from the Einstein-Stokes equation, which may oversimplify membrane-associated dynamics. Applying the Saffmann-Delbrück model to membrane-embedded particles would be desired although the resulting diffusion coefficients remain of the same order of magnitude. These limitations highlight the need for further research, yet they do not undermine the core significance of the present findings in advancing our understanding of multiphase morphologies.”

eLife Assessment

Kin selection and inclusive fitness have generated significant controversy. This paper reconsiders the general form of Hamilton's rule in which benefits and costs are defined as regression coefficients, with higher-order coefficients being added to accommodate non-linear interactions. The paper is a landmark contribution to the field with compelling, systematic analysis, giving clarity to long-standing debates.

Joint Public Review:

This manuscript reconsiders the "general form" of Hamilton's rule, in which "benefit" and "cost" are defined as regression coefficients. It points out that there is no reason to insist on Hamilton's rule of the form -c+br>0, and that, in fact, arbitrarily many terms (i.e. higher-order regression coefficients) can be added to Hamilton's rule to reflect nonlinear interactions. Furthermore, it argues that insisting on a rule of the form -c+br>0 can result in conditions that are true but meaningless and that statistical considerations should be employed to determine which form of Hamilton's rule is meaningful for a given dataset or model.

Comments on latest version:

The authors have provided a robust, valuable and detailed response to the previous reviews.

Comments from Reviewer #1: I have nothing further to add.

Comments from Reviewer #2: I appreciate the clarifications the author has made to the manuscript regarding (i) "sample covariance" terminology, (ii) the generality of the "generalized Price equation", and (iii) the distinction between the covariance and regression forms of the Price equation. I also appreciate that the ms now engages more deeply with some of the previous literature on regression-based Hamilton's rules (e.g. Smith et al., 2010; Rousset 2015). I feel these revisions make this contribution more valuable, and also more technically sound, since the term "sample covariance" is no longer used incorrectly.

I also add that I agree with the substance of the authors' response to Reviewer #3. That is, the original submission was very clear that the regression-based Hamilton's rule is already completely general in the range of situations to which it applies, and that the added "generality" in the present ms refers to the variety of regression models that can be applied to these situations. In this way, the original ms already anticipates and addresses the criticism that Reviewer #3 raises.

Reviewer #3 did not provide comments on the revised version.

eLife Assessment

The ratio of nuclei to cell volume is a well-controlled parameter in eukaryotic cells. This study now reports important findings that expand our understanding of the regulatory relationship between cell size and number of nuclei. The evidence supporting the conclusions is convincing obtained by applying appropriate and validated methodology in line with current state-of-the-art. The paper will be of broad interest for cell biologists and fungal biotechnologists seeking to understand mechanisms determining cell size and number of nuclei and why this knowledge might also be of importance for the production of enzymes and thus production strains not only of Aspergillus oryzae but also other industrially used fungi.

Reviewer #1 (Public review):

Filamentous fungi are established work horses in biotechnology with Aspergillus oryzae as a prominent example with a thousand-year of history. Still the cell biology and biochemical properties of the production strains is not well understood. The paper of the Takeshita group describes the change in nuclear numbers and correlate it to different production capacities. They used microfluidic devices to really correlate the production with nuclear numbers. In addition, they used microdissection to understand expression profile changes and found an increase of ribosomes. The analysis of two genes involved in cell volume control in S. pombe did not reveal conclusive answers to explain the phenomenon. It appears that it is a multi-trait phenotype. Finally, they identified SNPs in many industrial strains and tried to correlate them to the capability of increasing their nuclear numbers.

The methods used in the paper range from high quality cell biology, Raman spectroscopy to atomic force and electron microscopy and from laser microdissection to the use of microfluidic devices to study individual hyphae.

This is a very interesting, biotechnologically relevant paper with the application of excellent cell biology.

Comments on revised version:

The authors addressed all suggestions satisfactorily.

Reviewer #2 (Public review):

Summary:

In the study presented by Itani and colleagues it is shown that some strains of Aspergillus oryzae - especially those used industrially for the production of sake and soy sauce - develop hyphae with a significantly increased number of nuclei and cell volume over time. These thick hyphae are formed by branching from normal hyphae and grow faster and therefore dominate the colonies. The number of nuclei positively correlates with the thicker hyphae and also the amount of secreted enzymes. The addition of nutrients such as yeast extract or certain amino acids enhanced this effect. Genome and transcriptome analyses identified genes, including rseA, that are associated with the increased number of nuclei and enzyme production. The authors conclude from their data involvement of glycosyltransferases, calcium channels and the tor regulatory cascade in regulation of cell volume and number of nuclei. Thicker hyphae and an increased number of nuclei was also observed in high-production strains of other industrially used fungi such as Trichoderma reesei and Penicillium chrysogenum, leading to the hypothesis that the mentioned phenotypes are characteristic of production strains which is of significant interest for fungal biotechnology.

Strengths:

The study is very comprehensive and involves application of divers state-of-the-art cell biological, biochemical and genetical methods. Overall, the data are properly controlled and analyzed, figures and movies are of excellent quality.<br /> The results are particularly interesting with regard to the elucidation of molecular mechanisms that regulate the size of fungal hyphae and their number of nuclei. For this, the authors have discovered a very good model: (regular) strains with a low number of nuclei and strains with high number of nuclei. Also, the results can be expected to be of interest for the further optimization of industrially relevant filamentous fungi.

In the revision the authors addressed all my comments and as a result produced an even stronger study.

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:

Although the image analysis and data interpretation is convincing, the genetic data supporting the author's model is somewhat more speculative and will likely require additional investigation.

Overall, the authors have achieved their aims in that they are able to clearly document the presence of two distinct hyphal forms in A. oryzae and other Aspergillus species, and to correlate the presence of the thicker rapidly growing form with enhanced enzyme secretion. The image analysis is convincing. The discovery that addition of yeast extract and specific amino acids can stimulate formation of the novel hyphal form is also notable. Although the conclusions are generally supported by the results, this is perhaps less so for the genetic analysis as it remains unclear how direct the role of RseA and the calcium transporters might be in supporting the formation of the thicker hyphae.

The results presented here will impact the field. The complexity of hyphal morphology and how it affects secretion are not well understood despite the importance of these processes for the fungal lifestyle. In addition, the description of approaches that can be used to facilitate the study of these different hyphal forms (i.e., stimulation using yeast extract or specific animo acids) will benefit future efforts to understand the molecular basis of their formation.

Author response:

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

Reviewer #1 (Public review): 

Filamentous fungi are established workhorses in biotechnology, with Aspergillus oryzae as a prominent example with a thousand-year history. Still, the cell biology and biochemical properties of the production strains is not well understood. The paper of the Takeshita group describes the change in nuclear numbers and correlates it to different production capacities. They used microfluidic devices to really correlate the production with nuclear numbers. In addition, they used microdissection to understand expression profile changes and found an increase in ribosomes. The analysis of two genes involved in cell volume control in S. pombe did not reveal conclusive answers to explain the phenomenon. It appears that it is a multi-trait phenotype. Finally, they identified SNPs in many industrial strains and tried to correlate them to the capability of increasing their nuclear numbers. 

The methods used in the paper range from high-quality cell biology, Raman spectroscopy, to atomic force and electron microscopy, and from laser microdissection to the use of microfluidic devices to

study individual hyphae. 

This is a very interesting, biotechnologically relevant paper with the application of excellent cell biology. I have only minor suggestions for improvement. 

We sincerely appreciate your fair and positive evaluation of our work. Thank you for your suggestions for improvement. We respond to each of them appropriately.

Reviewer #2 (Public review): 

Summary: 

In the study presented by Itani and colleagues, it is shown that some strains of Aspergillus oryzae - especially those used industrially for the production of sake and soy sauce - develop hyphae with a significantly increased number of nuclei and cell volume over time. These thick hyphae are formed by branching from normal hyphae and grow faster and therefore dominate the colonies. The number of nuclei positively correlates with the thicker hyphae and also the amount of secreted enzymes. The addition of nutrients such as yeast extract or certain amino acids enhanced this effect. Genome and transcriptome analyses identified genes, including rseA, that are associated with the increased number of nuclei and enzyme production. The authors conclude from their data involvement of glycosyltransferases, calcium channels, and the tor regulatory cascade in the regulation of cell volume and number of nuclei. Thicker hyphae and an increased number of nuclei were also observed in high-production strains of other industrially used fungi such as Trichoderma reesei and Penicillium chrysogenum, leading to the hypothesis that the mentioned phenotypes are characteristic of production strains, which is of significant interest for fungal biotechnology. 

Strengths: 

The study is very comprehensive and involves the application of diverse state-of-the-art cell biological, biochemical, and genetic methods. Overall, the data are properly controlled and analyzed, figures and

movies are of excellent quality. 

The results are particularly interesting with regard to the elucidation of molecular mechanisms that regulate the size of fungal hyphae and their number of nuclei. For this, the authors have discovered a very good model: (regular) strains with a low number of nuclei and strains with a high number of nuclei. Also, the results can be expected to be of interest for the further optimization of industrially relevant filamentous

fungi. 

Weaknesses: 

There are only a few open questions concerning the activity of the many nuclei in production strains (active versus inactive), their number of chromosomes (haploid/diploid), and whether hyper-branching always leads to propagation of nuclei. 

We are very grateful for your recognition of our findings, the proposed model, and their significance for future applications. We are grateful for the questions, which contribute to a more accurate understanding. 

Our responses to each are provided below.  

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: 

There are aspects of the methods that would benefit from the inclusion of more detail on how experiments were performed and data interpreted. 

Overall, the authors have achieved their aims in that they are able to clearly document the presence of two distinct hyphal forms in A. oryzae and other Aspergillus species, and to correlate the presence of the thicker, rapidly growing form with enhanced enzyme secretion. The image analysis is convincing. The discovery that the addition of yeast extract and specific amino acids can stimulate the formation of the novel hyphal form is also notable. Although the conclusions are generally supported by the results, this is perhaps less so for the genetic analysis as it remains unclear how direct the role of RseA and the calcium transporters might be in supporting the formation of the thicker hyphae. 

The results presented here will impact the field. The complexity of hyphal morphology and how it affects secretion is not well understood despite the importance of these processes for the fungal lifestyle. In addition, the description of approaches that can be used to facilitate the study of these different hyphal forms (i.e., stimulation using yeast extract or specific amino acids) will benefit future efforts to understand the molecular basis of their formation. 

We are very grateful for your fair and thoughtful evaluation of our work. We agree that the genetic analysis in the latter part is relatively weaker compared to the imaging analysis in the first half. Rather than a single mutation causing a dramatic phenotypic change, we believe that the accumulation of various mutations through breeding leads to the observed phenotype, making it difficult to clearly demonstrate causality. Since transcriptome and SNP analyses have revealed key pathways and phenotypes, it would be gratifying if these insights could contribute to future applications utilizing filamentous fungi.

Reviewer #1 (Recommendations for the authors): 

I was wondering what happens if thick hyphae were taken as inoculum for a new colony or thin hyphae. Is it possible to enrich for one or the other type of hyphae? Perhaps in the presence of yeast extract or certain amino acids. 

Added an explanation in the discussion.

L304-306. When thick hyphae were cultured on fresh medium, thin hyphae initially emerged, suggesting that sustained metabolic activity is required for the formation of thick hyphae with a high number of nuclei.    

L120-121. In some cases, thick hyphae emerged by branching from thick hyphae (Fig. 2D, left), while in other cases, thin hyphae emerged from thick hyphae (Fig. 2D, right). Thin hyphae emerge in the early stage of cultivation even in the presence of yeast extract or certain amino acids.

In the Discussion, they hypothesize that the primary effect could be on cell wall rigidity. I am wondering if that hypothesis could be tested by adding, for instance, sublethal concentrations of cytochalasin to hyphae of A. nidulans to weaken the cell wall. 

The question is reasonable. To ensure accurate understanding, we moved Fig. S6 to Fig. 6 and revised the discussion as follows. 

L294-295. In our model, cell wall loosening at a branching site and regulation of cell volume by turgor pressure constitute necessary conditions for increasing cell volume and maintaining thick hyphae. L306-309. Weakening the cell wall by treatment with a low concentration of calcofluor white did not lead to hyphal thickening or an increase in nuclear number. On the contrary, thick hyphae have thicker cell walls (Fig. 2H-K), which are necessary to maintain the increased cell volume.

I recommend including some older literature. It was described already 20 years ago that A. nigerdifferentiates hyphae with different capacities to secrete proteins (PMID: 16238620). In addition, there are old reports in A. nidulans reporting high numbers of nuclei (https://doi.org/10.1099/00221287-60-1-133). Perhaps it is worth trying to reproduce those cultural conditions. At least this should be discussed. In the same line, the number of nuclei increases a lot in the stalk of conidiophores in A. nidulans. These observations could be used as examples that the phenomenon observed in A. oryzae may be of general importance. 

Thank you for the suggestion. It is a very interesting proposal. We checked the nuclei distribution of A. nidulans on the media and added the following discussion.

L328-334. A previous study reported an increase in the number of nuclei in A. nidulans (62, 63). Here, we examined the nuclear distribution of A. nidulans grown on the culture media, however, did not find class III hyphae as observed in A. oryzae. Even in A. nidulans, conidiophore stalks contain a high number of nuclei. It has been shown that A. oryzae has a taller conidiophore stalk (64). In the thick hyphae of A. oryzae, the expression level of flbA, an early regulator of conidiophore development (65), was elevated. This suggests that differentiation to aerial hyphae may be involved in the increase of hyphal volume and nuclear number. 

(62) Clutterbuck A.J. Synchronous Nuclear Division and Septation in Aspergillus nidulans. J Gen Microbiol 60, 133-135 (1970).

(63) Vinck, A., Terlou, M., Pestman, W.R., Martens, E.P., Ram, A.F., van den Hondel, C.A., Wösten, H.A. Hyphal differentiation in the exploring mycelium of Aspergillus niger. Mol Microbiol 58, 693-9 (2005).

(64) Wada R, Maruyama J, Yamaguchi H, Yamamoto N, Wagu Y, Paoletti M, Archer DB, Dyer PS, Kitamoto K. Presence and functionality of mating type genes in the supposedly asexual filamentous fungus Aspergillus oryzae. Appl Environ Microbiol 78, 2819-29 (2012).

(65) Lee, B.N., Adams, T.H. Overexpression of flbA, an early regulator of Aspergillus asexual sporulation, leads to activation of brlA and premature initiation of development. Mol Microbiol 14, 323-34 (1994).

Reviewer #2 (Recommendations for the authors): 

I suggest addressing the following questions to strengthen the manuscript: 

(1) Do the authors have an explanation for their result that with an increase in the number of nuclei the individual nucleus is smaller? Have the authors checked whether all the nuclei are haploid or diploid?

Thank you for the very important question. We added new results to Fig. S5D and S5E and the following discussion.

L335-340. We investigated whether the reduction in nuclear size observed in thick hyphae was due to a change from diploid to haploid status. However, no difference in GFP-histone fluorescence intensity was detected between thick and thin hyphae (Fig. S5D). In both RIB40 and RIB915 strains, no significant difference in conidial spore size was observed despite the large difference in the number of nuclei within the hyphae (Fig. S5E). These results suggest that both thick and thin hyphae remain haploid, and that the smaller nuclear size observed in thick hyphae is likely due to a higher nuclear density.

(2) In this context, the biological relevance of the increase in the number of nuclei should also be discussed in more detail. It remains to be clarified whether in hyphae with a high number of nuclei all nuclei are functionally active or whether many nuclei are possibly "inactive". Studies on the transcriptional activity of individual nuclei or on DNA replication (e.g., by EdU labeling) could clarify this. 

Added the explanation below.

L102-105. The transcriptional activity of each nucleus is unknown. However, a previous study (Yasui et al., FBB 2020) demonstrated that nuclear division is synchronized even when there are more than 200 nuclei. This suggests that DNA replication occurs similarly in most nuclei. Furthermore, since the germination rate of conidia and the colonies formed from individual conidia show no significant abnormalities, it is suggested that nearly all nuclei possess normal genomes and chromosomes.

(3) It becomes not entirely clear what the underlying signal is that causes a thin hypha to branch into a thick multinucleated cell. This needs to be discussed in more detail. 

Thanks for the suggestion. We clarified the signal to increase nuclear number and cell volume.

L294-309. Although it is speculative, we propose a model to aid interpretation in the discussion. We have clarified that both genetic potential and environmental signals such as nutrients are important.

(4) Is increased branching always correlated with an increased number of nuclei? 

It is not an increase in branching, but rather the thickening of hyphae and an increase in cell volume that is consistently associated with an increase in nuclear number. Approximately 40 hours after inoculation, within 400 μm from the tip, the number of branches was 3.4 (SD=2.4) in thin hyphae and 2.6 (SD=0.5) in thick hyphae, suggesting that branching does not increase (n=4). Since thick hyphae elongate faster, it seems that fewer branches are present near the tip, even if the branching frequency itself remains unchanged.

(5) The abstract does not summarize the many findings of the manuscript in an adequate way. 

abstract change

Minor: 

(1) Lines 49-50: Why italics? 

corrected.

(2) Line 179: process. 

corrected.

(3) Lines 313-314: Do not forget (and discuss) in this context mycorrhiza fungi with up to thousands of nuclei that were apparently selected during evolution for this high number of nuclei. 

Thank you for the very interesting suggestion. We have added the following discussion.

L339-351. The regulation of nuclear number and its ecological strategy are intriguing in other fungi such as N. crassa, which rapidly spreads after wildfires (68), and arbuscular mycorrhiza fungi that form symbiotic relationships with plants and contain thousands of nuclei within hyphae lacking septa (69).

(68) Jacobson, D. J. et al. Neurospora in temperate forests of western North America. Mycologia 96, 66–74 (2004).

(69) Kokkoris V, Stefani F, Dalpé Y, Dettman J, Corradi N. Nuclear Dynamics in the Arbuscular Mycorrhizal Fungi. Trends Plant Sci. 25, 765-778 (2020).

(4) Lines 356-358: many typos.

corrected.

Reviewer #3 (Recommendations for the authors): 

Specific suggestions or clarifications for the authors include: 

(1) Lines 49-50: Is this sentence italicized for a reason? 

It was a mistake, so we have corrected it.

(2) Line 83: More detail on the specific characteristics of the different classes of hyphae would be helpful. Perhaps include a schematic drawing that emphasizes the differences between class I,II, and III hyphae. 

L398-400. The classification is described in the Methods section: Class I – nuclei are distributed at regular intervals without overlapping; Class II – nuclei are aligned but occasionally overlap; Class III – nuclei are scattered throughout the hyphae without alignment. Representative images are shown in a previous study (Yasui et al., FBB 2020). 

L82-84. We have added this information to clarify the classification.

(3) Lines 102-103: It was not very clear how this experiment was done. Are you counting nuclei within 100 um of the tip? Are these all in one hyphal compartment? These details could be provided in a drawing that would make it easier for the reader to understand how this was done. 

L109. Due to variation in the distance from the hyphal tip to the septum, we counted the number of nuclei within 100 μm from the hyphal tip. When septa were present, nuclei were counted in the same manner, so multiple compartments may be included. Changed the explanation.

(4) Lines 134-140: Is there a way to calibrate levels of secreted protein or amylase activity per nucleus? That is, if the ratio of cytoplasmic volume per nucleus is constant, does the same apply to the secreted product? Knowing this would help to clarify whether the key feature in enhanced secretion is nuclear (e.g., gene expression) versus a cytoplasmic trait (e.g., vesicle trafficking). 

Enzyme activity was measured across the entire mycelium, which includes a mixture of hyphae with high and low numbers of nuclei. Therefore, it is difficult to assess the correlation between enzyme activity and nuclear number. Enzyme activity was normalized by fungal biomass. The size of each colony is shown in Fig. 1B. Additionally, the correlation between the proportion of hyphae with increased nuclear number and enzyme activity is shown in Fig. 3H. In the experiment where enzyme activity was measured in a single hypha, we attempted to measure the number of nuclei; however, we could not use the nuclear GFP strain because the substrate exhibits green fluorescence. DAPI staining also failed due to limited dye access to the microfluidic channel. Changed the section title, ‘Increase in nuclear number and enzyme secretion’ from ‘Correlation between nuclear number and enzyme secretion’.

(5) Line 151 and Figure 3F: YE also triggered a ~5-fold enhancement of secretion in A. nidulans without a concomitant increase in hyphal width. This merits some comment in the text.  

Added an explanation, L156-157.

In A. nidulans, the addition of yeast extract did not cause a dramatic increase in nuclear number, but hyphal width increased by 1.4-times and protein secretion increased by 5.1-times.

(6) Line 252: Were nimE levels detected or altered in thick hyphae? The levels of this cycling might play a more important role in a shortened cell cycle than the authors have considered, especially as NimE functions during both G1 and G2. 

Added an explanation below, L260-262.

The expression level of nimE (AO090003000993) was low in both thick and thin hyphae, with no significant difference observed. As known in other organisms, its function is likely regulated through phosphorylation and the protein degradation.

(7) Line 254: Please provide a citation for the statement that branches emerge as a result of cell wall loosening. 

rephrased and added citation, L263.

Branching is thought to occur through the degradation and reconstruction of the cell wall at the branching site (54).

Harris SD. Branching of fungal hyphae: regulation, mechanisms and comparison with other branching systems. Mycologia 100, 823-32 (2008).   

(8) Lines 275-277: It would be interesting to know whether the addition of rapamycin also suppressed the ability of amino acids to trigger greater numbers of class III hyphae. 

We added new results at Fig. S2G.

L168. Rapamycin decreased the ratio of hyphae with increased nuclei even in the medium with yeast extract (Fig. S2G).

(9) Lines 282-289: My sense is that this model is too speculative at this time. The role of RseA seems very broad based on the strong deletion phenotype. How would the removal of RseA be regulated to limit its effect to the branch site? Also, the msyA deletion phenotype isn't entirely consistent with what you would expect if it were necessary to maintain thick hyphae. Lastly, the authors do not show that translational capacity is enhanced in thick hyphae. I would suggest that these statements be tempered to some degree. 

Thank you for your comment. We agree that it was too speculative, whereas we believe that some explanatory interpretation is necessary. Therefore, we have revised the text as follows, L294-300. In our model, cell wall loosening during branching and regulation of cell volume by turgor pressure constitute necessary conditions for increasing cell volume and maintaining thick hyphae. RseA and MsyA may be involved in these processes. At the same time, enhanced translational capacity by increased expression of ribosomal genes, possibly due to associated with TOR activation by specific amino acids, and mechanisms that accelerate the cell cycle represent another essential condition that enables an increase in nuclear number.

(10) General: how do the authors reconcile the observation that YE and amino acids stimulate the formation of thicker hyphae, yet the time lapse imaging (Figure 2E) suggests that these hyphae arise at a later time during colony development when these resources might be limiting? The authors should consider providing some insight into this in the Discussion. 

L300-305. Added a discussion below.

Both genetic potential and nutritional environmental signals are likely required for the formation of thick hyphae with a high number of nuclei. When thick hyphae were cultured on fresh medium, thin hyphae initially emerged, suggesting the necessity of sustained high metabolic activity.

eLife Assessment

This important study reports that an oncogenic population in an epithelium can either be repressed or spread, depending on the tissues. This is explained based on the differential interfacial tension hypothesis, and supported by pharmacological perturbations and numerical simulations using the vertex model. The study conveys a key message, but, as it stands, the strength of evidence is incomplete, and a more detailed analysis of the mechanistic origin of the different tensions and better comparison between experiments and simulations would strongly strengthen the message.

Reviewer #1 (Public review):

Summary:

The behaviour of cells expressing constitutively active HRas is examined in mosaic monolayers, both in MCF10a breast epithelial and Beas2b bronchial epithelial cell lines, mimicking the potential initial phase of development of carcinoma. Single HRas-positive cells are excluded from MCF10a but not Beas2b monolayers. Most interestingly, however, when in groups, these cells are not excluded, but rather sharply segregated within a MCF10a monolayer. In contrast, they freely mix with wt Beas2b cells. Biophysical analysis identifies high tension at heterotypic interfaces between HRas and wild-type cells as the likely reason for segregation of MCF10a cells. The hypothesis is supported experimentally, as myosin inhibition abolishes segregation. The probable reason for the lack of segregation in the bronchial epithelium is to be found in the different intrinsic properties of these cells, which form a looser tissue with lower basal actomyosin activity. The behaviour of single cells and groups is recapitulated in a vortex model based on the principle of differential interfacial tension, under the condition of high heterotypic interfacial tension.

Strengths:

Despite being long recognized as a crucial event during cancer development, segregation of oncogenic cells has been a largely understudied question. This nice work addresses the mechanics of this phenomenon through a straightforward experimental design, applying the biophysical analytical approaches established in the field of morphogenesis. Comparison between two cell types provides some preliminary clues on the diversity of effects in various cancers.

Weaknesses:

Although not calling into question the main message of this study, there are a few issues that one may want to address:

(1) One may be careful in interpreting the comparison between MCF10a and Beas2b cells as used in this study. The conditions may not necessarily be representative of the actual properties of breast and bronchial epithelia. How much of the epithelial organization is reconstituted under these experimental conditions remains to be established. This is particularly obvious for bronchial cells, which would need quite specific culture conditions to build a proper bronchial layer. In this study, they seemed to be on the verge of a mesenchymal phenotype (large gaps, huge protrusions, cells growing on top of each other, as mentioned in the manuscript).

As an alternative to Beas2b, comparison of MCF10a with another cell line capable of more robust in vitro epithelial organization, but ideally with different adhesive and/or tensile properties, would be highly interesting, as it may narrow down the parameters involved in segregation of oncogenic cells.

(2) While the seminal description of tissue properties based on interfacial tensions (Brodland 2002) is clearly key to interpreting these data, the actual "Differential Interfacial Tension Hypothesis" poses that segregation results from global differences, i.e., juxtaposition of two tissues displaying different intrinsic tensions. On the contrary, the results of the present work support a different scenario, where what counts is the actual difference in tension ALONG the tissue boundary, in other words, that segregation is driven by high HETEROTYPIC interfacial tension. This is an important distinction that should be clarified.

(3) Related: The fact that actomyosin accumulates at the heterotypic interface is key here. It would be quite informative to better document the pattern of this accumulation, which is not clear enough from the images of the current manuscript: Are we talking about the actual interface between mutant and wt cells (membrane/cortex of heterotypic contacts)? Or is it more globally overactivated in the whole cell layer along the border? Some better images and some quantification would help.

(4) In the case of Beas2b cells, mutant cells show higher actin than wt cells, while actin is, on the contrary, lower in mutant MCF10a cells (Figure 2b). Has this been taken into account in the model? It may be in line with the idea that HRas may have a different action on the two cell types, a possibility that would certainly be worth considering and discussing.

In conclusion, the study conveys an important message, but, as it stands, the strength of evidence is incomplete. It would greatly benefit from a more detailed and complete analysis of the experimental data, a better fit between this analysis and the corresponding vertex model, and a more in-depth discussion of biological and biophysical aspects. These revisions should be rather easily done, and would then make the evidence much more solid.

Reviewer #2 (Public review):

Summary:

The authors investigate the behavior of oncogenic cells in mammary and bronchial epithelia. They observe that individual oncogenic cells are preferentially excluded from the mammary epithelium, but they remain integrated in the bronchial epithelium. They also observe that clusters of oncogenic cells form a compact cluster in the mammary epithelium, but they disperse in the bronchial epithelium. The authors demonstrate experimentally and in the vertex model simulations that the difference in observed behavior is due to the differential tension between the mutant and wild-type cells due to a differential expression of actin and myosin.

Strengths:

(1) Very detailed analysis of experiments to systematically characterize and quantify differences between mammary and bronchial epithelia.

(2) Detailed comparison between the experiments and vertex model simulations to identify the differential cell line tension between the oncogenic and wild-type cells as one of the key parameters that are responsible for the different behavior of oncogenic cells in mammary and bronchial epithelia

Weaknesses:

(1) It is unclear what the mechanistic origin of the shape-tension coupling is, which is used in the vertex model, and how important that coupling is for the presented results. The authors claim that the shape-tension coupling is due to the anisotropic distribution of stress fibers when cells are under external stress. It is unclear why the stress fibers should affect an effective line tension on the cell boundaries and why the stress fibers should be sensitive to the magnitude of the internal isotropic cell pressure. In experiments, it makes sense that stress fibers form when cells are stretched. Similar stress fibers form when the cytoskeleton or polymer networks are stretched. It is unclear why the stress fibers should be sensitive to the magnitude of internal isotropic cell pressure. If all the surrounding cells have the same internal pressure, then the cell would not be significantly deformed due to that pressure, and stress fibers would not form. The authors should better justify the use of the shape-tension coupling in the model and also present simulation results without that coupling. I expect that most of the observed behavior is already captured by the differential tension, even if there is no shape-tension coupling.

(2) The observed difference of shape indices between the interfacial and bulk cells in simulations in the absence of differential line tension is concerning. This suggests that either there are not enough statistics from the simulations or that something is wrong with the simulations. For all presented simulation results, the authors should repeat multiple simulations and then present both averages and standard deviations. This way, it would be easier to determine whether the observed differences in simulations are statistically significant.

(3) The authors should also analyze the cell line tension data in simulations and make a comparison with experiments.

eLife Assessment

In this important study, the authors use computational modeling to explore how fast learning can be reconciled with the accumulation of stable memories in the olfactory bulb, where adult neurogenesis is prominent. Their model demonstrates that changes in excitability, plasticity, and susceptibility to apoptosis during the maturation of adult-born granule cells can help resolve the flexibility-stability dilemma. These compelling results provide a coherent picture of a neurogenesis-dependent learning process that is consistent with diverse experimental observations and may serve as a foundation for further experimental and computational studies.

Reviewer #1 (Public review):

Summary:

Sakelaris and Riecke used computational modeling to explore how neurogenesis and sequential integration of new neurons into a network support memory formation and maintenance. They focus on the integration of granule cells in the olfactory bulb, a brain area where adult neurogenesis is prominent. Experimental results published during recent years provide an excellent basis to address the question at hand by biologically constrained models. The study extends previous computational models and provides a coherent picture of how multiple processes may act in concert to enable rapid learning, high stability of memories, and high memory capacity. This computational model generates experimentally testable predictions and is likely to be valuable to understand roles of neurogenesis and related phenomena in memory. One of the key findings is that important features of the memory system depend on transient properties of adult-born granule cells such as enhanced excitability and apoptosis during specific phases the development of individual neurons. The model can explain many experimental observations, and suggests specific functions for different processes (e.g., importance of apoptosis for continual learning). While this model is obviously a massive simplification of the biological system, it conceptualizes diverse experimental observations into a coherent picture, it generates testable predictions for experiments, and it and will likely inspire further modeling and experimental studies.

Strengths:

- The model can explain diverse experimental observations

- The model directly represents the biological network

Weaknesses:

- As many other models of biological networks, this model contains major simplifications.

Reviewer #2 (Public review):

Summary:

The authors propose a mechanism to provide flexibility to learn new information while preserving stability in neural networks by combining structural plasticity and synaptic plasticity.

Strengths:

An intriguing idea, well embedded in experimental data.

Authors have done a great job addressing reviewers' concerns

Weaknesses:

None

Reviewer #3 (Public review):

The manuscript is focused on local bulbar mechanisms to solve the flexibility-stability dilemma in contrast to long range interactions documented in other systems (hippocampus-cortex). The network performance is assessed in a perceptual learning task: the network is presented with alternating, similar artificial stimuli (defined as enrichment) and the authors assess its ability to discriminate between these stimuli by comparing the mitral cell representations quantified by Fisher discriminant analysis. The authors use enhancement in discriminability between stimuli as function of the degree of specificity of connectivity in the network to quantify the formation of an odor-specific network structure which as such has memory - they quantify memory as the specificity of that connectivity.

The focus on neurogenesis, excitability and synaptic connectivity of abGCs is topical, and the authors systematically built their model, clearly stating their assumptions and setting up the questions and answers. In my opinion, the combination of latent dendritic representations, excitability and apoptosis in an age-dependent manner is interesting and as the authors point out leads to experimentally testable hypotheses.

In the revised manuscript, the authors have systematically addressed my previous concerns. In particular, they now refer to previous work on granule cells-mitral cell interactions more generally, they explain the pros and cons for usage of specificity in connectivity as a proxy for memory capacity, and the biological plausibility of the model.

eLife Assessment

This important work sets out to identify the neural substrates of associative fear responses in adult zebrafish. Through a compelling and innovative paradigm and analysis, the authors suggest brain regions associated with individual differences in fear memory. While several findings are well supported, aspects of the interpretation and presentation are partially incomplete, and the manuscript would benefit from adjusting key claims or including additional experiments. Nonetheless, this study showcases the strength of zebrafish for systems-level neuroscience and will be of broad interest to the neuroscience community.

Reviewer #1 (Public review):

Summary:

This work provides a comprehensive analysis of how adult zebrafish show fear responses to conspecific alarm substances (CAS) and retain their associative memory. It shows that freezing is a more reliable measure of fear response and memory compared to evasive swimming, and that the reactivity and the type of responses depend on the zebrafish strain. It further suggests neuronal substrates of different fear responses based on c-Fos mapping.

Strengths:

The behavioral part is the most comprehensive and detailed yet in the zebrafish field, providing strong support for the authors' claim. The flow from Figure 1 to Figure 4 is very smooth. They provide extremely detailed, yet complementary and necessary, analyses of how different categories of behavior emerge over time during the CAS exposure and memory retrieval. I'm convinced that neuro researchers who study fear/stress responses will always refer to this paper to plan and interpret their future experiments.

Weaknesses:

The neural analysis part is very comprehensive. Figure 5 and Figure 6 are independent but complement each other very well. They together support that the cerebellar system is the key brain component for a freezing response. Their extreme focus on high-level analyses, however, came at the expense of biological intuitions. I suggest adding some figure panels and result/discussion paragraphs to help with that aspect.

Reviewer #2 (Public review):

In this study, Fontana et al. develop a paradigm for associative conditioning by pairing exposure to an alarm substance with a novel tank. Exposure to conspecific alarm substance (CAS) in the novel tank triggers freezing and what they characterize as evasive swimming behaviour, which is subsequently seen in a re-exposure to the novel tank without the CAS present. Importantly, these states are identified via automated processes, including postural tracking and a random forest classification process, which could be very useful tools for subsequent studies.

In their experiments, they focus on the differences in behaviour among strains of zebrafish (both males and females), and among individual zebrafish. For males and females of different strains, they find some differences, though the clearest message seems to be that the most robust measure of the behaviour in response to both the CAS and in the memory trials is the freezing behaviour, while evasive behaviour is more variable. and not always seen. This may relate to their observation of significant "evasiveness" in vehicle control experiments (discussed further below).

Moving on to individual variation from within this multi-strain male/female dataset, they first examine transition matrices between states and find tthat his is not dramatically altered by stimulus exposure. They then use clustering to identify 4 different "classes" of zebrafish that differ in their expression (or not) of two types of behaviour: freezing and/or evasive behaviour. They show that over the three exposure epochs of the experiment, this classification is somewhat stable in an individual fish, though many fish change their behaviour - e.g., evading + freezing -> only freezing.

In the final set of experiments, the authors move beyond behavioural analyses and perform whole-brain cFos mapping of these individual zebrafish. They perform analyses aimed at identifying correlations between individual behavioural expression and the number of cFos-positive cells in different brain regions. Using partial least squares analysis, they find areas associated with two types of behavioural contrasts, which differ in their weighting of different behavioural expression during the Memory trials. Covariation and network structure analysis within different classes of larvae also find some differences in covariation among brain areas, providing hypotheses as to underlying network effects that may govern the expression of freezing and/or evasive behavior in the memory trial phases.

Overall, I find this to be an interesting study that employs state of the are methods of behavioural analyses and whole-brain cFos analyses, but I am left a little bit confused as to what the take home message is and what can be concluded from this complex study that mixes in analyses of strain, sex, and individuality within a quite complex assay with multiple behavioural parameters.

My suggestions are as follows:

(1) My first concern relates to the claim in the abstract that "We found that fear memory behavior fell into four distinct groups: non-reactive, evaders, evading freezers, and freezers".

In my opinion, the "freezing" aspect is well supported as being both triggered by the CAS and for memory effect upon re-exposure to the tank, but I am less convinced about the "evasive" behaviour. In Figure 2, it appears that "evasiveness" is generally not increased in both the Exposure or Memory phases for many groups, and in Figure 5, it appears that "evasiveness" is expressed by nearly 50% of the fish in the pre-exposure condition before CAS addition and in all phases in the vehicle condition. Therefore, it appears that most of the expression of this behaviour is independent of any memory-based effect.

(2) My second concern relates to the claim in the abstract that "background strain and sex influenced how fish respond to CAS, with males more likely to increase evasive behaviors than females and the TU strain more likely to be non-reactive."

My understanding, based on the introduction and on the methods, is that it is likely important that the CAS be prepared from conspecifics of the same strain and sex, and for this reason, they prepared different CAS specific for each strain and each sex. Therefore, the "CAS" that is applied is necessarily different for each condition, and I am concerned about if the differences observed could relate more to variation in the quality, purity, concentration, etc. of the specific CAS samples for different groups, rather than their reactivity to the substance or their ability to form memories based on such experiences.

(3) My third concern relates to the interpretation of the cFos data.

As I mentioned above, I feel as though the behavioural analysis is perhaps more complex than is warranted via the inclusion of evasiveness, and I wonder if the conclusions from the experiments would be simpler if analyzed only from the perspective of freezing.

But considering the presented analyses: while I dont think there is anything wrong with the partial least squares approach and the network analyses, I am concerned that the simple messaging in the text does not reflect the complexity of this analysis combining different weightings of different behavioural characteristics in a behavioural contrast, or covariations among many regions and what such analyses mean at the level of brain function. For these reasons, I feel like statements along the lines of "Behavioral variation is driven by differences in the activity of brain regions outside the telencephalon, such as the cerebellum, preglomerular nuclei, preoptic area and hypothalamus" are not well supported.

Reviewer #3 (Public review):

Summary:

This manuscript by Fontana et al. sets out to fill a critical gap in our understanding of how individuality in fear responses corresponds to changes in brain activity. Previous work has shown in myriad species that fear behaviors are highly variable, and these variabilities correlate with sex and strain, with epigenetic modifications, and neural activity in specific regions of the brain, such as the amygdala. However, a whole-brain functional assessment of whether activity in different regions of the brain is associated with fear behavior has been difficult to assess, in part due to the large size and opacity of the brain. The Kenney group overcomes these limitations using the zebrafish, together with powerful behavioral and brain imaging approaches pioneered by their lab. To overcome the technical obstacles of delivering a reproducible unconditioned stimulus in water and quantifying nuanced behavioral responses, the authors developed a three-day conditioning paradigm in which fish were repeatedly exposed to CAS in one tank context and to control water in another. Leveraging automated cluster analysis across over 300 individuals from four inbred strains, they identified four distinct memory-recall phenotypes - non-reactive, evaders, evading freezers, and freezers - demonstrating both the robustness of their assay and the influence of genetic background and sex on fear learning. Finally, whole-brain imaging using the AZBA atlas (Kenney et al. eLife) and cfos mapping coupled with multivariate analysis revealed that although all fish reengaged telencephalic regions during recall, high-freezing phenotypes uniquely recruited cerebellar, preglomerular, and pretectal nuclei, whereas mixed evasion-freezing fish showed preferential activation of preoptic and hypothalamic areas - a finding that lays the groundwork for dissecting the distributed neural substrates of associative fear in zebrafish.

Strengths:

The strengths of the study lie in the use of zeberarish and the innovative behavioral, modeling, and brain imaging tools applied to address this question. The question of how brain-wide activity correlates with variations in fear behavior is fundamental, and arguably, this system is the only system that could be used to address this. The statistics are appropriate, and the study is well reasoned. Overall, I like this manuscript very much and think it adds invaluable information to the field of fear/anxiety.

Weaknesses:

I have a few questions and suggestions.

(1) The three-day contextual fear paradigm, as implemented - one CAS pairing on day 2 followed by a single recall test on day 3 - inevitably conflates acquisition and long-term memory, making it impossible to know whether strains like TU truly recall the association poorly or simply learn it more slowly. For example, given that TU fish extinguish fear faster than AB or TL strains in extended protocols, they may simply require additional or repeated CAS pairings to achieve the same asymptotic performance. To disentangle learning kinetics from recall strength, the assay could be revised to include multiple acquisition trials (e.g., conditioning on two or more consecutive days) with an immediate post-conditioning probe to assess acquisition independent of consolidation, and continuous measurement of freezing and evasive behaviors across each trial to fit learning curves for each strain. Such refinements - even if on a subset of the strains - would reveal whether "non-reactive" phenotypes reflect genuine recall deficits or merely delayed acquisition.

(2) My second major question is with respect to Figure 3 panel B. This is a complex figure, and I can understand the gist of what the authors are attempting to show, but it is difficult to understand as it is. Can this be represented in a way that is clearer and explained a bit more easily?

(3) The brain mapping is by far one of the most interesting aspects of this study, and the methods that the group used are interesting. The brain mapping, however, relies on generating "contrasting" groups (Figure 6A), and I was not clear as to how these two groups were formed. Could the authors elaborate a bit?

eLife Assessment

This valuable study focuses on defining how the HSP70 chaperone system utilizes J-domain proteins to regulate the heat shock response-associated transcription factor HSF1. Using a combination of orthogonal techniques in yeast, this manuscript provides compelling evidence that the J-domain protein Apj1 facilitates attenuation of HSF1 transcriptional activity through a mechanism involving its dissociation from heat shock gene promoter regions. This work generates new insight into the mechanism of HSF1 transcriptional regulation and is a significant contribution of broad interest to cell biologists interested in proteostasis, chaperone networks, and stress-responsive signaling.

Reviewer #1 (Public review):

Summary:

In this study, the authors present a thorough mechanistic study of the J-domain protein Apj1 in Saccharomyces cerevisiae, establishing it as a key repressor of Hsf1 during the attenuation phase of the heat shock response (HSR). The authors integrate genetic, transcriptomic (ribosome profiling), biochemical (ChIP, Western), and imaging data to dissect how Apj1, Ydj1 and Sis1 modulate Hsf1 activity under stress and non-stress conditions. The work proposes a model where Apj1 specifically promotes displacement of Hsf1 from DNA-bound heat shock elements, linking nuclear PQC to transcriptional control.

Strengths:

Overall, the work is highly novel-this is the first detailed functional dissection of Apj1 in Hsf1 attenuation. It fills an important gap in our understanding of how Hsf1 activity is fine-tuned after stress induction, with implications for broader eukaryotic systems. I really appreciate the use of innovative techniques including ribosome profiling and time-resolved localization of proteins (and tagged loci) to probe Hsf1 mechanism. The overall proposed mechanism is compelling and clear-the discussion proposes a phased control model for Hsf1 by distinct JDPs, with Apj1 acting post-activation, while Sis1 and Ydj1 suppress basal activity.

The manuscript is well-written and will be exciting for the proteostasis field and beyond.

Comments on revised version:

The authors have addressed all my concerns,

Reviewer #2 (Public review):

Summary:

Overall, the work is exceptionally well done and controlled and the results properly and appropriately interpreted. While several of the approaches, while powerful, are somewhat indirect (i.e., following gene expression via ribosomal profiling) additional experiments utilizing traditional gene expression assays added in revision combine to ultimately provide a compelling answer to the main questions being asked.

The key finding from this work is the discovery that Apj1 regulates Hsf1 attenuation in a manner that includes Hsp70. That finding is strongly supported by the experimental data. While it would be ideal to also demonstrate Apj1-controlled differential binding of Ssa1/2 to Hsf1 at either the N- or C-terminal binding sites during attenuation, the Hsp70-Hsf1 interactions are difficult to reproducibly assess in cell extracts and are likely beyond the scope of this study. However, this work paves the way in the future for potential biochemical reconstitution assays that could elucidate both Hsp70-Hsf1 interactions as well as the distinct JDP-Hsf1 interactions reported here.

This discovery raises additional new questions about JDP specificity in HSR regulation and the role of JDPs in navigating protein aggregation and sensing of proteostatic challenge in the nucleus, thus advancing the field and opening new, exciting avenues for exploration.

Reviewer #3 (Public review):

Summary:

The heat shock response (HSR) is an inducible transcriptional program that has provided paradigmatic insight into how stress cues feed information into the control of gene expression. The recent elucidation that the chaperone Hsp70 controls the DNA binding activity of the central HSR transcription factor Hsf1 by direct binding has spurred the question how such a general chaperone obtains specificity. This study has addressed the next logical question, how J-domain proteins execute this task in budding yeast, the leading cell model for studying the HSR. While an involvement and in part overlapping function of general class A and B J-domain proteins, Ydj1 and Sis1 are indicated by the genetic analysis a highly specific role for the class A Apj1 in displacing Hsf1 from the promoters is found unveiling specificity in the system.

Strengths

The central strong point of the paper is the identification of class A J-domain protein Apj1 as a specific regulator of the attenuation of the HSR by removing Hsf1 from HSEs at the promoters. The genetic evidence and the ChIP data strongly support this claim. This identification of a specific role for a lowly expressed nuclear J-domain protein changes how the wiring of the HSR should be viewed. It also raises important questions regarding the model of chaperone titration, the concept that a chaperone with limiting availability is involved in a thug of war involving competing interactions with misfolded protein substrates and regulatory interactions with Hsf1. Perhaps Apj1 with its low levels and interactions with misfolded and aggregated proteins in the nucleus is the titrated Hsp70 (co)chaperone that determines the extent of the HSR? This would mean that Apj1 is at the nexus of the chaperone titration mechanism. Although Apj1 is not a highly conserved J domain protein among eukaryotes the strength of the study is that is provides a conceptual framework for what may be required for chaperone titration in other eukaryotes: One or more nuclear J-domain proteins with low nuclear levels that has an affinity for Hsf1 and that can become limiting due to interactions with misfolded Hsp70 proteins. The provides a pathway for how these may be identified using for example ChIP-seq.

Weakness

A built-in challenge when studying the mechanism of the HSR is the general role of Hsp70 chaperone system and its J domain proteins. Indeed, a weakness of the study is that it is unclear what of the phenotypic effects have to do with directly recruiting Hsp70 to Hsf1 dependent on a J domain protein and what instead is an indirect effect of protein misfolding caused by the mutation. This interpretation problem is clearly and appropriately dealt with in the manuscript text and in experiments but is of such fundamental nature that it cannot easily be fully ruled out.

eLife Assessment

This important study provides compelling evidence that fever-like temperatures enhance the export of Plasmodium falciparum transmembrane proteins, including the cytoadherence protein PfEMP1 and the nutrient channel PSAC, to the red blood cell surface, thereby increasing cytoadhesion. Using rigorous and well-controlled experiments, the authors convincingly demonstrate that this effect results from accelerated protein trafficking rather than changes in protein production or parasite development. These findings significantly advance our understanding of parasite virulence mechanisms and offer insights into how febrile episodes may exacerbate malaria severity.

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

All the experiments investigating changes resulting from increased temperature were conducted after an increase in temperature from 16 to 24 hours, with sampling or assays conducted at the 24 hr mark. While this provided consistency throughout the study, this is a time point relatively early in the export of proteins to the RBC surface, as shown in Figure 1E. At 24 hrs, only approximately 50% of wildtype parasites are positive for PfEMP1, while at 32 hrs this approaches 80%. Since the authors only checked the effect of heat stress at 24 hrs, it is not possible to determine if the changes they observe reflect an overall increase in protein trafficking or instead a shift to earlier (or an accelerated) trafficking. In other words, if a second time point had been considered (for example, 32 hrs or later), would the parasites grown in the absence of heat stress catch up?

Reviewer #2 (Public review):

This manuscript describes experiments characterising how malaria parasites respond to physiologically relevant heat-shock conditions. The authors show, quite convincingly, that moderate heat-shock appears to increase cytoadherance, likely by increasing trafficking of surface proteins involved in this process.

While generally of a high quality and including a lot of data, I have a few small questions and comments, mainly regarding data interpretation.

(1) The authors use sorbitol lysis as a proxy for trafficking of PSAC components. This is a very roundabout way of doing things and does not, I think, really show what they claim. There could be a myriad of other reasons for this increased activity (indeed, the authors note potential PSAC activation under these conditions). One further reason could be a difference in the membrane stability following heat shock, which may affect sorbitol uptake, or the fragility of the erythrocytes to hypotonic shock. I really suggest that the authors stick to what they show (increased PSAC) without trying to use this as evidence for increased trafficking of a number of non-specified proteins that they cannot follow directly.

(2) Supplementary Figure 6C/D: The KAHRP signal does not look like it should. In fact, it doesn't look like anything specific. The HSP70-X signal is also blurry and overexposed. These pictures cannot be used to justify the authors' statements about a lack of colocalisation in any way.

(3) Figure 6: This experiment confuses me. The authors purport to fractionate proteins using differential lysis, but the proteins they detect are supposed to be transmembrane proteins and thus should always be found associated with the pellet, whether lysis is done using equinatoxin or saponin. Have they discovered a currently unknown trafficking pathway to tell us about? Whilst there is a lot of discussion about the trafficking pathways for TM proteins through the host cell, a number of studies have shown that these proteins are generally found in a membrane-bound state. The authors should elaborate, or choose an experiment that is capable of showing compartment-specific localisation of membrane-bound proteins (protease protection, for example).

(4) The red blood cell contains, in addition to HSP70-X, a number of human HSPs (HSP70 and HSP90 are significant in this current case). As the name suggests, these proteins non-specifically shield exposed hydrophobic domains revealed upon partial protein unfolding following thermal insult. I would thus have expected to find significantly more enrichment following heat shock, but this is not the case. Is it possible that the physiological heat shock conditions used in this current study are not high enough to cause a real heat shock?

Reviewer #3 (Public review):

Summary:

In this paper, it is established that high fever-like 39{degree sign}C temperatures cause parasite-infected red blood cells to become stickier. It is thought that high temperatures might help the spleen to destroy parasite-infected cells, and they become stickier in order to remain trapped in blood vessels, so they stop passing through the spleen.

Strengths:

The strength of this research is that it shows that fever-like temperatures can cause parasite-infected red blood cells to stick to surfaces designed to mimic the walls of small blood vessels. In a natural infection, this would cause parasite-infected red blood cells to stop circulating through the spleen, where the parasites would be destroyed by the immune system. It is thought that fevers could lead to infected red blood cells becoming stiffer and therefore more easily destroyed in the spleen. Parasites respond to fevers by making their red blood cells stickier, so they stop flowing around the body and into the spleen. The experiments here prove that fever temperatures increase the export of Velcro-like sticky proteins onto the surface of the infected red blood cells and are very thorough and convincing.

Weaknesses:

A minor weakness of the paper is that the effects of fever on the stiffness of infected red blood cells were not measured. This can be easily done in the laboratory by measuring how the passage of infected red blood cells through a bed of tiny metal balls is delayed under fever-like temperatures.

Author response:

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

All the experiments investigating changes resulting from increased temperature were conducted after an increase in temperature from 16 to 24 hours, with sampling or assays conducted at the 24 hr mark. While this provided consistency throughout the study, this is a time point relatively early in the export of proteins to the RBC surface, as shown in Figure 1E. At 24 hrs, only approximately 50% of wildtype parasites are positive for PfEMP1, while at 32 hrs this approaches 80%. Since the authors only checked the effect of heat stress at 24 hrs, it is not possible to determine if the changes they observe reflect an overall increase in protein trafficking or instead a shift to earlier (or an accelerated) trafficking. In other words, if a second time point had been considered (for example, 32 hrs or later), would the parasites grown in the absence of heat stress catch up?

We did not assess cytoadhesion at later stages, but in the supplementary figures we show that at 40 hours post infection both heat stress and control conditions have comparable proportions of VAR2CSA-positive iRBCs, whilst they differ at 24h. This is true for the DMSO (control wildtype resembling) HA-tagged lines of HSP70x and PF3D7_072500 (Supplementary Figures 9 and 12 respectively). In the light that protein levels appear not changed, we conclude that trafficking is accelerated during these earlier timepoints, but remains comparable at later stages. This would still increase the overall bound parasite mass as parasites start to adhere earlier during or after a heat stress.

Reviewer #2 (Public review):

This manuscript describes experiments characterising how malaria parasites respond to physiologically relevant heat-shock conditions. The authors show, quite convincingly, that moderate heat-shock appears to increase cytoadherance, likely by increasing trafficking of surface proteins involved in this process.

While generally of a high quality and including a lot of data, I have a few small questions and comments, mainly regarding data interpretation.

(1) The authors use sorbitol lysis as a proxy for trafficking of PSAC components. This is a very roundabout way of doing things and does not, I think, really show what they claim. There could be a myriad of other reasons for this increased activity (indeed, the authors note potential PSAC activation under these conditions). One further reason could be a difference in the membrane stability following heat shock, which may affect sorbitol uptake, or the fragility of the erythrocytes to hypotonic shock. I really suggest that the authors stick to what they show (increased PSAC) without trying to use this as evidence for increased trafficking of a number of non-specified proteins that they cannot follow directly.

This is a valid point, however, uninfected RBCs do not lyse following heat stress, nor do much younger iRBCs, indicating that the observed effect is specific to infected RBCs at a defined stage. The sorbitol sensitivity assay is performed at 37°C under normal conditions after cells are returned to non–heat stress temperatures, so the effect is not due to transient changes in membrane permeability at elevated temperature. 

Planned experiment: However, to increase the strength of our conclusions and further test our hypothesis, we will perform sorbitol sensitivity assays on >20 hours post infection iRBCs following heat stress in the presence and absence of furosemide, a PSAC inhibitor. If iRBC lysis is abolished with furosemide present, this would confirm that the effect is PSAC-dependent. However, the effect could also possibly be due to altered PSAC activity during heat stress which is maintained at lower temperatures, as outlined in the discussion.

(2) Supplementary Figure 6C/D: The KAHRP signal does not look like it should. In fact, it doesn't look like anything specific. The HSP70-X signal is also blurry and overexposed. These pictures cannot be used to justify the authors' statements about a lack of colocalisation in any way.

Planned experiment: We agree that the IFAs are not the best as presented and will include better quality supplementary images in a revised version.

(3) Figure 6: This experiment confuses me. The authors purport to fractionate proteins using differential lysis, but the proteins they detect are supposed to be transmembrane proteins and thus should always be found associated with the pellet, whether lysis is done using equinatoxin or saponin. Have they discovered a currently unknown trafficking pathway to tell us about? Whilst there is a lot of discussion about the trafficking pathways for TM proteins through the host cell, a number of studies have shown that these proteins are generally found in a membrane-bound state. The authors should elaborate, or choose an experiment that is capable of showing compartment-specific localisation of membrane-bound proteins (protease protection, for example).

We do not believe we identified a novel trafficking pathway, but that we capture trafficking intermediates of PfEMP1 between the PVM and the RBC periphery, in either small vesicles, and/ or possibly Maurer’s clefts. These would still be membrane embedded, but because of their small size, not be pelleted using the centrifugation speeds in our study (we did not use ultracentrifugation). This explanation, we believe, is in line with the current hypothesis of PfEMP1 and other exported TMD protein trafficking to the periphery or the Maurer’s clefts.

(4) The red blood cell contains, in addition to HSP70-X, a number of human HSPs (HSP70 and HSP90 are significant in this current case). As the name suggests, these proteins non-specifically shield exposed hydrophobic domains revealed upon partial protein unfolding following thermal insult. I would thus have expected to find significantly more enrichment following heat shock, but this is not the case. Is it possible that the physiological heat shock conditions used in this current study are not high enough to cause a real heat shock?

As noted by the reviewer, we do not see enrichment of red blood cell heat shock proteins following heat stress, either with FIKK10.2-TurboID or in the phosphoproteome. We used a physiologically relevant heat stress that significantly modifies the iRBC, as shown by our functional assays. While a higher temperature might induce an association of red blood cell heat shock proteins, such conditions may not accurately reflect the most commonly found context of malaria infection.

Reviewer #3 (Public review):

Summary:

In this paper, it is established that high fever-like 39 C temperatures cause parasite-infected red blood cells to become stickier. It is thought that high temperatures might help the spleen to destroy parasite-infected cells, and they become stickier in order to remain trapped in blood vessels, so they stop passing through the spleen.

Strengths:

The strength of this research is that it shows that fever-like temperatures can cause parasite-infected red blood cells to stick to surfaces designed to mimic the walls of small blood vessels. In a natural infection, this would cause parasite-infected red blood cells to stop circulating through the spleen, where the parasites would be destroyed by the immune system. It is thought that fevers could lead to infected red blood cells becoming stiffer and therefore more easily destroyed in the spleen. Parasites respond to fevers by making their red blood cells stickier, so they stop flowing around the body and into the spleen. The experiments here prove that fever temperatures increase the export of Velcro-like sticky proteins onto the surface of the infected red blood cells and are very thorough and convincing.

Weaknesses:

A minor weakness of the paper is that the effects of fever on the stiffness of infected red blood cells were not measured. This can be easily done in the laboratory by measuring how the passage of infected red blood cells through a bed of tiny metal balls is delayed under fever-like temperatures.

Previous work by Marinkovic et al. (cited in this manuscript) reported that all RBCs, both infected and uninfected, increase in stiffness at 41 °C compared with 37 °C, with trophozoites and schizonts exhibiting a particularly pronounced increase. We agree that it would be interesting to determine whether similar changes occur at physiological fever-like temperatures, and whether this increase in stiffness coincides with the period of elevated protein trafficking. However, since we have already demonstrated enhanced protein export using multiple complementary approaches, we have chosen to address these questions in a follow-up study.

eLife Assessment

This study provides important insights into how the EBH domain of microtubule end-binding protein 1 (EB1) interacts with SxIP peptides derived from the MACF plus-end tracking protein. The revised manuscript includes convincing ITC and NMR experiments that clarify the role of flanking residues and address the influence of dimerization and cooperativity on binding. While some mechanistic aspects remain difficult to resolve experimentally, the data and analysis now more clearly justify the proposed "dock-and-lock" model and its interpretive value. This work will be of interest to structural biologists and biophysicists studying microtubule-associated protein interactions.

Reviewer #1 (Public review):

Summary:

In this article, Almeida and colleagues use a combination of NMR and ITC to study the interaction of the EBH domain of microtubule end-binding protein 1 (EB1) with SxIP peptides derived from the MACF plus-end tracking protein. EBH forms a dimer and in isolation has previously been shown to have a disordered C-terminal tail. Here, the authors use NMR to determine a solution structure of the EBH dimer bound to 11-mer SxIP peptides derived from MACF, and observe that the disordered C-terminal of EBH is recruited by residues C-terminal to the SxIP motif to fold into the final complex. By comparison of binding in different length peptides, and of EBH lacking the C-terminal tail, they show that these additional contacts increase binding affinity by an order of magnitude, greatly stabilising the interaction, in a binding mode they term 'dock-and-lock'.

The authors also use their new structural knowledge to design peptides with higher affinities, and show in a cell model that these can be weakly recruited to microtubule ends - although a dimeric construct is necessary for efficient recruitment. Ultimately, by demonstrating the feasibility of targeting these proteins, this work points towards the possibility of designing small-molecules to block the interactions.

Reviewer #2 (Public review):

Summary:

The C-terminal region of EB1 is responsible for protein-protein interactions, thereby recruiting the binding partners of EB1 to microtubules; the coiled-coil region (EBH) and the acidic tail are critical for their binding partners. The authors demonstrated by using NMR that the binding mode of EBH with the SxIP motif, which is a two-step process termed "dock-and-lock". The ITC analysis supports the results obtained from NMR. The initial version of the manuscript contained ambiguities on the ITC data; however, the results of the revised manuscript are convincing and support the two-step binding model.

Strength:

The authors propose a novel model of "dock-and-lock" by using multiple methods of NMR, ITC and cell biology.

Author response:

The following is the authors’ response to the original reviews

We would like to express our sincere gratitude to the reviewers for their thorough analysis of the manuscript and their extremely helpful comments. We have taken all the suggestions into consideration and conducted a range of additional experiments to address the points raised. We have also extensively revised the manuscript to clarify descriptions, correct inaccuracies and remove inconsistencies. We have modified the figures for clarity and content.

Overall, we expanded the description of the EBH structure to emphasise its dimeric nature and the impact of the two binding sites on interpreting the binding data, including cooperativity. Using ITC, we tested the effect of the pre-SxIP residues on the binding affinity with additional peptides. We found that these residues had a significant effect, albeit much smaller than that of the post-SxIP residues. We analysed the binding of the 11MACF-VLL mutant with EBH-ΔC and evaluated the exchange rates. In agreement with our model, we found that the EBH affinity for the SxIP peptide from CK5P2 (KKSRLPRILIKRSR), which has a C-terminal sequence similar to that of the 11MACF-VLLRK mutant, is 21nM, which is similar to the affinity of the mutant itself. This demonstrates the significant variation in affinity observed among natural SxIP ligands, as predicted by our study. Our responses to the specific points raised by the reviewers are provided below.

Reviewer #1 (Public Review):

There is no direct experimental evidence for independent dock and lock steps. The model is certainly plausible given their structural data, but all titration and CEST measurements are fully consistent with a simple one-step binding mechanism. Indeed, it is acknowledged that the results for the VLL peptide are not consistent with the predictions of this model, as affinity and dissociation rates do not co-vary. The model may still be a helpful way to interpret and discuss their results, and may indeed be the correct mechanism, but this has not yet been proven.

Unfortunately, it is not possible to obtain direct experimental evidence because the folding of the C-terminus is too fast to influence the NMR parameters. However, as the reviewer pointed out, our structural data support the two-step model, since folding of the C-terminus is only possible once the ligand containing the post-SxIP residues has bound. By adopting a mechanistically supported model, we can analyse the contributions to binding and relate them to the structural characteristics of the complex. This provides a clearer insight into the roles of the various regions in the interaction and allows to modify them rationally to enhance the ligand affinity.

In the revised version, we restate the equations in terms of comparing the on-rates. This provides a clearer view of the effect of the additional stage, which cannot increase the overall on-rate since the two stages are sequential. If the forward rate of the second stage is comparable to or slower than the off-rate of the first stage, the overall on-rate decreases. Conversely, if the forward rate is much faster, the overall on-rate remains unchanged. For the wild-type 11MACF peptide, we observed that the presence of the EBH C-terminus does not affect the on-rate of binding, which is in perfect agreement with the two-step model and indicates that the C-terminus folds very quickly.

Additionally, we evaluated the binding of the 11MACF-VLL mutant to EBH-ΔC and observed a twofold decrease in Kd compared to WT 11MAC, primarily due to an increase in the on-rate. Interestingly, this rate is approximately twice as low as the overall on-rate for EBH/11MACF-VLL binding, contradicting the sequential two-step model. This suggests a more complex binding process where binding is accelerated by additional hydrophobic interactions with the unfolded C-terminus. However, given the difficulty of quantifying very slow exchange rates, it is more likely that the discrepancy is due to the accuracy of the rate measurements. Therefore, the model allows the rational analysis of changes in binding parameters due to mutations.

There is little discussion of the fact that binding occurs to EBH dimers -  either in terms of the functional significance of this or in the  acquisition and analysis of their data. There is no discussion of  cooperation in binding (or its absence), either in the analysis of NMR  titrations or in ITC measurements. Complete ITC fit results have not  been reported so it is not possible to evaluate this for oneself.

We added information about the dimer to the introduction, emphasising its role in enhancing interaction with microtubules (MTs) and its structural role in SxIP binding. The ITC data do not exhibit any biphasic behaviour and can be fitted to a single-site model with 1:1 stoichiometry relative to the EB1c monomer. This corresponds to two independent binding sites in the dimer. We have added the stoichiometry to Table 1 and the description. The NMR titration data for the 11MACF and 11MACF-VLL interactions were fitted to the TITAN dimer model, which includes cooperativity parameters. For WT 11MACF, both cooperativity parameters were zero, corresponding to independent binding sites in the ITC model. For 11MACF-VLL, the fitting suggests weak negative cooperativity, with a ~3-fold increase in Kd for binding to the second site and no change in the off-rate. This difference in Kd is likely to be too small to induce a biphasic shape to the ITC curve. As the cooperativity effect on the NMR spectra is small and absent in the ITC, we used the independent sites model for data analysis, as there is insufficient justification for introducing extra parameters into the model. Crucially, fitting to this model did not alter the off-rate value obtained by NMR or affect the conclusions. We added a description of cooperativity to the results and discussion.

Three peptides are used to examine the role of C-terminal residues in SxIP motifs: 4-MACF (SKIP), 6-MACF (SKIPTP), and 11-MACF (KPSKIPTPQRK). The 11-mer demonstrates the strongest binding, but this has added residues to the N-terminal as well. It has also introduced charges at both termini, further complicating the interpretation of changes in binding affinities. Given this, I do not believe the authors can reasonably attribute increased affinities solely to post-SxIP residues.

We tested the 9MACF peptide SKIPTPQRK, which has the same N-terminus as the 4- and 6-MACF peptides, and found that its binding affinity is ~10-fold weaker than that of 11MACF. This demonstrates the contribution of both the pre- and post-SxIP residues. This is likely due to electrostatic interactions between the positively charged N-terminus and the negatively charged EBH surface, similar to those involving the positive charges at the peptide C-terminus. Although significant, the contribution of the N-terminal peptide region is approximately one order of magnitude lower than that of the post-SxIP residues, meaning the post-SxIP region is the main affinity modulator. We have added the binding data on 9MACF and a discussion of the contributions to the manuscript.

Experimental uncertainties are, with exceptions, not reported.

Uncertainties added to the number in Table 1 and the text. Information on how uncertainties were calculated added to Table 1.

Reviewer #1 (Recommendations For The Authors):

(1) Have you tested the binding of the WT dimer in your cell model?

We haven’t tested the WT dimer because it has already been reported in the 2009 Cell paper by Honappa et al. In the cell experiments, our main focus was on recruiting the high-affinity mutant to MTs. The low level of recruitment, despite the mutant's high affinity, highlights the importance of dimerisation or additional contributions to binding.

(2) Please deposit all NMR dynamics measurements (relaxation rates and derived model-free parameters) alongside structural data in the BMRB.

The relaxation data have been submitted to BMRB, IDs 53187 and 53188

(3) Please report complete fitting results, e.g. for ITC, including stoichiometries. Clarify what this means for binding to a dimer, and if there is any evidence of cooperativity. Figure 3C, right hand panel, shows an unusual stoichiometry, can the authors comment on this?

We have added more information on stoichiometry and cooperativity; please refer to our response to the above comment for details. We repeated the titration for the VLLRK mutant using fresh peptide stock. As expected, the stoichiometry was close to 1:1 relative to the EB1c monomer. The new data are now included in the table and figure.

(4) Please report uncertainties for all measurements of Kd, koff, kon, ∆G, ∆H, ∆S, and explain whether these are determined from statistical analysis, technical or biological repeats (and where reported, clarify between standard deviation/standard error). Please also be aware of standard guidelines for reporting significant figures for data with uncertainties, as these have not been followed in Table 1.

Uncertainties added to the number in Table 1 and the text. Information on how uncertainties were calculated added to Table 1.

(5) The construct design for the cell model is unclear - given the importance of flanking residues, please report and discuss how the sequences are attached to venus: which termini is attached, and what is the linker composition?

We cloned the peptides at the C-terminus of mTFP, after the GS linker of the vector. The peptide itself contains a GS sequence at the N-terminus, creating a highly flexible GSGS linker that separates the SxIP region from mTFP and minimises the potential effect of mTFP on binding. We followed the design of Honappa et al. to enable direct comparison with the published results. We have added this information to the 'Methods' section..

(6) Which HSQC pulse sequence was used for 2D lineshape analysis? The authors mention non-linear chemical shift changes, presumably associated with the dimer interface - this would be useful to expand upon and clarify.

For the lineshape analysis, we used the standard Bruker sequence hsqcfpf3gpphwg with soft-pulse watergate water suppression and flip-back. This sequence is included in the TITAN model. We added the description of the non-linear chemical shift changes and connection of these changes to the allosteric effect of the binding to the supplementary information describing details of the lineshape analysis.

(7) Figure 1A could usefully highlight the dimer interface in the surface representation also.

We believe that including the interface would make the figure too complicated. The dimer configuration is shown in different colours for the two subunits, clearly demonstrating their involvement in forming the binding site.

(8) Figures 1C and 1D could usefully show a secondary structure schematic to assist the reader. The x-axis in these figures is not linear and this should be corrected. The calculation of combined chemical shift perturbations should be described.

Thank you for the helpful suggestion. We changed the scale of the figures and added the diagram of the secondary structure.

(9) Units are missing from many figure axes.

We added missing units to the axes. Thank you for highlighting this.

(10) What peptide concentrations are used in Figure 1C? Presumably, these should be reported at saturation for this to be a fair comparison, this should be clarified.

The protein concentration was 50 µM. Peptides 4MACF and 6MACF were added at a 100-fold molar excess and peptide 11MACF was added at a 4-fold excess. Saturation was achieved for 11MACF. This was impossible for the short peptides due to their mM affinity. This information has been added to the figure legend. The figure's main aim is to illustrate the differences in the chemical shift perturbation profiles, which can be achieved even if full saturation is not attained. Although the absolute value of the chemical shifts is proportional to the degree of saturation, the distribution of the largest chemical shift changes is independent of this degree. Therefore, we can draw conclusions about the distribution of changes by comparing under non-saturation conditions.

(11) The presentation of raw peak intensities in Figure 1D shows primarily the flexibility of the C-terminal region associated with high intensities. Beyond this, when comparing the binding of peptides it would be much more informative to show relative peak intensities. Residues around 210-225 appear to show strong broadening in the presence of peptide, but this is masked by the low initial intensity. Can the authors clarify and discuss this? Also, what peptide concentrations were used for this comparison? For a fair comparison, it should be close to saturation - particularly to exclude exchange broadening contributions.

The protein concentration was 50 µM. 6MACF and 6MACF peptides were added at a 100-fold excess and 11MACF at a 4-fold excess. Saturation was achieved for 11MACF. This was impossible to achieve for the short peptide due to its mM affinity. This information has been added to the figure legend. Upon checking the data, we found a small systematic offset in the coiled-coil region of some of the complexes, as the integral intensity had been used in the initial plot. While this does not change the conclusion regarding the high dynamics of the C-terminus, it does create an inaccurate perception of the relative intensities of the folded regions in the different complexes, as noted by the reviewer. We have now plotted the amplitudes at the maximum of the peaks, which do not exhibit any systematic offset as they are much less susceptible to baseline distortions. We are grateful to the reviewer for highlighting this apparent discrepancy.

(12) Figure 2 - the scale for S2 order parameters appears to be backwards, given the caption, but its range should be indicated. Similarly, the range of values for Rex should also be indicated. These data should also be tabulated/plotted in supporting information.

We have corrected the figure legend and added S2 and Rex plots to the supplementary material. The figure aims to highlight regions of increased mobility, while the plots provide full quantitative information on the values. We thank the reviewer for pointing out the error in the figure legend and for the suggestions regarding the plots.

(13) The scale in Figure 3B is illegible. Indeed, the whole structure is quite small and could usefully be expanded.

We increased the size of the structure panels and added a scale.

(14) Figure 4 does not show a decrease in exchange rates, as per the caption - no comparison of exchange rates is shown, only thermodynamic information in panel E. Panel C shows CEST measurements, but it is not clear what system this is for - please clarify, and consider showing the comparable data for the ∆C construct for comparison.

We have amended the figure legend to clarify that the figure shows binding parameters. We added information about the CEST profiles for the EBH/11MACF interaction to the figure legend (Figure 4C). Exchange with the ∆C construct is too fast for CEST measurements. We used lineshape analysis to evaluate the exchange rates for this construct.

(15) The schematics shown in Figure 4D, and elsewhere, are really quite difficult to understand. They may pose additional challenges to colourblind readers. Please consider ways that this could be clarified.

We simplified the colour scheme in the model to make the colours easier to see and to highlight SxIP and non-SxIP regions. We believe that this improved the clarity of the figure.

(16) Figures S1D/E - the x-axes are unclear and units are missing from the y-axes.

We re-labelled the axes to clarify the scale and units. Thank you for pointing this.

Reviewer #2 (Public Review):

The C-terminal tail of EB1, which is adjacent to EBH and is not analyzed in this study, is highly acidic and plays an important role in protein interactions. If the authors discuss the C-terminus of EB1, they should analyze the whole C-terminus of EB1, which would strengthen the conclusion they have made.

Honapa et al., Cell, 2009, reported chemical shift perturbations (CSPs) on the peptide binding for the full EB1c fragment, which includes the negatively charged C-terminus. Similar to our study, they observed significant CSPs in the FVIP region but negligible CSPs at the negatively charged EEY end. They concluded that the final eight EB1c residues did not contribute to binding and used a truncated EB1c construct for their structural analysis. Building on that study, we used the same EEY-truncated construct to analyse the contribution of the C-terminus in more detail. We believe that conducting additional experiments with the full C-terminus with respect to SxIP binding would be superfluous, as it would merely replicate the findings of Honapa EA. We have added the rationale for selecting the truncated EB1c construct to the text, referencing Honapa et al.

Reviewer #2 (Recommendations For The Authors):

(1) Figure 2C: The authors can analyze the 11MACF peptide as well, to provide more assurance to their argument. It would be easier to distinguish the sequences of "SKIP" and "FVIP" by changing their colors.

Our relaxation analysis (Fig. 2C) focuses on the dynamics of the unstructured C-terminal region in both the free and complex forms. Further relaxation analysis of the peptide would not provide additional information on this, and would be complicated by the presence of free peptide in solution.

(2) Figure 3B: Acidic residues in EBH should be labeled.<br /> Page 6, line 11: If the authors insist that the acidic patch will influence the interactions between EB1 and the peptide, the data of the analysis using the entire EB1 C-terminus should be included, given that the C-terminal tail of EB1 is highly acidic.

To test the contribution of charge to binding, we conducted an ITC experiment at increasing salt concentrations. We observed a significant increase in Kd values when the concentration of NaCl increased from 50 to 150 mM, which supports our conclusion regarding the significant electrostatic contribution. This conclusion is independent of the presence or absence of the C-terminus.

As we explained earlier, Honapa et al., Cell 2009, conducted an NMR experiment on the full EB1c and observed no CPSs in the EEY region, indicating a negligible contribution from the EEY region to SxIP binding. Therefore, we think that additional experiments involving the entire C-terminus are unnecessary, as they would simply replicate the results of Honapa et al. We have added the rationale for selecting the truncated EB1c to the text, referencing Honapa et al.

It would be very difficult to label the acidic residues without enlarging 3B considerably. However, we do not think this is necessary as we are not discussing any specific residues. The current figure shows the distribution of the surface charge, which is sufficient for our purposes.

(3) Figure 2B (Page 4, line 27): The side chain of S5477 should be drawn. The authors should include a figure of the crystal structure of EBH and SxIP as a comparison (Honnappa et al., Cell, 2009). In their paper, Honnappa et al. performed chemical shift perturbation titrations by NMR. From their analysis, I imagine that the EB1 tail may not be critical for the EB1 C-terminus:SxIP interactions, since the signals in the tail are not significantly perturbed. The authors should cite this paper.

We are grateful to the reviewer for highlighting this. CSP analysis of the Honapa EA revealed significant changes in the FVIP region, which we also observed. They also reported negligible CSPs at the EEY end, demonstrating that this part of the tail is non-critical and can be removed. We have added text to the manuscript to highlight the similarity between CSPs and those observed in Honapa EA. Figure 2B shows the side chains for the residues with the strongest detected contacts. These do not include S5477.

(4) Figure 3C (ITC data): The stoichiometric ratios in the ITC data look strange. EBH vs KPSKIPVLLRKRK, is it 1:1?

We repeated the ITC experiments using a new stock of the peptide and a new batch of the protein, checking the concentrations using UV spectroscopy. The new experiments produced a stoichiometry close to 1, as shown in the table.

(5) Page 10, line 27: "The TPQ sequence of 11MACF is not optimal...": What is the meaning of "optimal"? The transient interaction between EB1 and its binding partner is responsible for the dynamics of the microtubule cytoskeleton. In a sense, the relatively weak interaction is "optimal" for the system. The authors should rephrase the word.

We agree that weak interactions are optimal from a functional perspective, as they have been selected through evolution. In our case, 'optimal' refers to the hydrophobic interaction with the C-terminus. We replaced 'optimal' with 'ideal' to draw more attention to the second part of the sentence, which clarifies the context.

(6) Page 11, line 2: "small number of comets enriched in the peptide that were too faint for the quantitative analysis, comparable to the reported previously (Honnappa, Gouveia et al. 2009)." Honnappa et al. used EGFP-fusion constructs in their study: EGFP forms a weak dimer, which presumably gave different results from the authors' mTFP-constructs. The authors can note this point in the text.

We are grateful to the reviewer for highlighting this. This aligns well with our conclusion that dimerisation is important for localisation to comets. We have added this point to the text.

(7) Page 10, line 21: The authors calculate the free energy of complex formation between EBH and MACF peptide and explain in the text, but it is hard to follow.

We simplified and clarified the description of the energy contributions by focusing on the SxIP and non-SxIP regions of the peptide, as well as the EBH C-terminus.

Minor points:

Page 2, line 9: IP motifs are not usually located in the C-terminus. For example, SxIP in Tastin is located in the N-terminal region, and SxIPs in CLASP are in the middle.

We corrected this statement, removing C-terminal.

Page 3, line 4: The authors should note the residue numbers of SKIP.

We think that in this context the residue number of the SxIP region are not important and would be distracting.

Figure 3D and Figure S3F: Make the colors and the order the same between the two figures.

We changed the colour scheme and the order of ITC parameters in S3F to match the main figure.

Figure 1A, 2B, Figure S5: Change the color of SKIP from other residues in the same chain, otherwise the readers cannot distinguish. Likewise, change the color of FVIP in Figure 2B.

We think that changing the colours will complicate the figures unnecessary. The corresponding residues are clearly labelled in the figures.

Figure 3, Figure S5, S6, S7: Box the letters of SKIP for clarity.

We boxed the SxIP region in S5 (new S6) and underlined in S6 (new S7). In S7 (new S8) the location of SxIP is very clear from the homology.

Figure 3B; Figure S2: Hard to recognize the peptide (MACF in green).

We increased the size of 3D and S2, making it easier to see the peptide.

Figure 1C and D: Make the residual numbers of the x-axes the same between the two graphs.

We made new plots with a linear scale for the residue numbers.

Figure 2A: The structures shown are not EB1. It should be described as EBH or EB1(191-260 a.a.).

Corrected.

Page 5, line 17: "the S2 values of the C-terminus" should be "the S2 values of the C-terminal loop in EBH", otherwise it is confusing.

Corrected.

Page 6, line 27; Figure S3C and S6: Please indicate the assignments of the resonances from "253FVI255" in the Figures.

We labelled the peaks corresponding to the 253FVI255 region in figure S6 (new S7). Figure S3 shows EBH-ΔC that does not include this region.

Page 7, line 25: Figure S7 should be S8.

Corrected

Page 12, line 6: "sulfatrahsferases" must by a typo.

Corrected.

eLife Assessment

This useful study develops an individual-based model to investigate the evolution of division of labor in vertebrates, comparing the contributions of group augmentation and kin selection. The model incorporates several biologically relevant features, including age-dependent task switching and separate manipulation of relatedness and group-size benefits. However, the evidence remains inadequate to support the authors' central claim that group augmentation is the primary driver of vertebrate division of labor. Key modelling assumptions-such as floater dominance advantages, the absence of task synergy, and the narrow parameter space explored-restrict the potential for kin selection to produce division of labor, thereby limiting the generality of the conclusions.

Reviewer #1 (Public review):

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

This is an interesting model, and there is much to like about the complexity that is built in. Individual-based simulations like this can be a valuable tool to explore the complex interaction of life history and social traits. Yet, models like this also have to take care of both being very clear on their construction and exploring how some of the ancillary but potentially consequential assumptions affect the results, including robust exploration of the parameter space. I think the current manuscript falls short in these areas, and therefore, I am not yet convinced of the results.

In this round, the authors provided some clarity, but some questions still remain, and I remain unconvinced by a main assumption that was not addressed.

Based on the authors' response, if I understand the life history correctly, dispersers either immediately join another group (with 1-the probability of dispersing), or remain floaters until they successfully compete for a breeder spot or die? Is that correct? I honestly cannot decide because this seems implicit in the first response but the response to my second point raises the possibility of not working while floating but can work if they later join a group as a subordinate. If it is the case that floaters can have multiple opportunities to join groups as subordinates (not as breeders; I assume that this is the case for breeding competition), this should be stated, and more details about how.

So there is still some clarification to be done, and more to the point, the clarification that happened only happened in the response. The authors should add these details to the main text. Currently, the main text only says vaguely that joining a group after dispersing " is also controlled by the same genetic dispersal predisposition" without saying how.

In response to my query about the reasonableness of the assumption that floaters are in better condition (in the KS treatment) because they don't do any work, the authors have done some additional modeling but I fail to see how that addresses my point. The additional simulations do not touch the feature I was commenting on, and arguably make it stronger (since assuming a positive beta_r -which btw is listed as 0 in Table 1- would make floaters on average be even more stronger than subordinates). It also again confuses me with regard to the previous point, since it implies that now dispersal is also potentially a lifetime event. Is that true?

Meanwhile, the simplest and most convincing robustness check, which I had suggested last round, is not done: simply reduce the increase in the R of the floater by age relative to subordinates. I suspect this will actually change the results. It seems fairly transparent to me that an average floater in the KS scenario will have R about 15-20% higher than the subordinates (given no defense evolves, y_h=0.1 and H_work evolves to be around 5, and the average lifespan for both floaters and subordinates are in the range of 3.7-2.5 roughly, depending on m). That could be a substantial advantage in competition for breeding spots, depending on how that scramble competition actually works. I asked about this function in the last round (how non-linear is it?) but the authors seem to have neglected to answer.

More generally, I find that the assumption (and it is an assumption) floaters are better off than subordinates in a territory to be still questionable. There is no attempt to justify this with any data, and any data I can find points the other way (though typically they compare breeders and floaters, e.g.: https://bioone.org/journals/ardeola/volume-63/issue-1/arla.63.1.2016.rp3/The-Unknown-Life-of-Floaters--The-Hidden-Face-of/10.13157/arla.63.1.2016.rp3.full concludes "the current preliminary consensus is that floaters are 'making the best of a bad job'."). I think if the authors really want to assume that floaters have higher dominance than subordinates, they should justify it. This is driving at least one and possibly most of the key results, since it affects the reproductive value of subordinates (and therefore the costs of helping).

Regarding division of labor, I think I was not clear so will try again. The authors assume that the group reproduction is 1+H_total/(1+H_total), where H_total is the sum of all the defense and work help, but with the proviso that if one of the totals is higher than "H_max", the average of the two totals (plus k_m, but that's set to a low value, so we can ignore it), it is replaced by that. That means, for example, if total "work" help is 10 and "defense" help is 0, total help is given by 5 (well, 5.1 but will ignore k_m). That's what I meant by "marginal benefit of help is only reduced by a half" last round, since in this scenario, adding 1 to work help would make total help go to 5.5 vs. adding 1 to defense help which would make it go to 6. That is a pretty weak form of modeling "both types of tasks are necessary to successfully produce offspring" as the newly added passage says (which I agree with), since if you were getting no defense by a lot of food, adding more food should plausibly have no effect on your production whatsoever (not just half of adding a little defense). This probably explains why often the "division of labor" condition isn't that different than the no DoL condition.

Reviewer #2 (Public review):

Summary:

This paper formulates an individual-based model to understand the evolution of division of labor in vertebrates. The model considers a population subdivided in groups, each group has a single asexually-reproducing breeder, other group members (subordinates) can perform two types of tasks called "work" or "defense", individuals have different ages, individuals can disperse between groups, each individual has a dominance rank that increases with age, and upon death of the breeder a new breeder is chosen among group members depending on their dominance. "Workers" pay a reproduction cost by having their dominance decreased, and "defenders" pay a survival cost. Every group member receives a survival benefit with increasing group size. There are 6 genetic traits, each controlled by a single locus, that control propensities to help and disperse, and how task choice and dispersal relate to dominance. To study the effect of group augmentation without kin selection, the authors cross-foster individuals to eliminate relatedness. The paper allows for the evolution of the 6 genetic traits under some different parameter values to study the conditions under which division of labour evolves, defined as the occurrence of different subordinates performing "work" and "defense" tasks. The authors envision the model as one of vertebrate division of labor.

The main conclusion of the paper is that group augmentation is the primary factor causing the evolution of vertebrate division of labor, rather than kin selection. This conclusion is drawn because, for the parameter values considered, when the benefit of group augmentation is set to zero, no division of labor evolves and all subordinates perform "work" tasks but no "defense" tasks.

Strengths:

The model incorporates various biologically realistic details, including the possibility to evolve age polytheism where individuals switch from "work" to "defence" tasks as they age or vice versa, as well as the possibility of comparing the action of group augmentation alone with that of kin selection alone.

Weaknesses:

The model and its analysis is limited, which makes the results insufficient to reach the main conclusion that group augmentation and not kin selection is the primary cause of the evolution of vertebrate division of labor. There are several reasons.

First, the model strongly restricts the possibility that kin selection is relevant. The two tasks considered essentially differ only by whether they are costly for reproduction or survival. "Work" tasks are those costly for reproduction and "defense" tasks are those costly for survival. The two tasks provide the same benefits for reproduction (eqs. 4, 5) and survival (through group augmentation, eq. 3.1). So, whether one, the other, or both tasks evolve presumably only depends on which task is less costly, not really on which benefits it provides. As the two tasks give the same benefits, there is no possibility that the two tasks act synergistically, where performing one task increases a benefit (e.g., increasing someone's survival) that is going to be compounded by someone else performing the other task (e.g., increasing that someone's reproduction). So, there is very little scope for kin selection to cause the evolution of labour in this model. Note synergy between tasks is not something unusual in division of labour models, but is in fact a basic element in them, so excluding it from the start in the model and then making general claims about division of labour is unwarranted. I made this same point in my first review, although phrased differently, but it was left unaddressed.

Second, the parameter space is very little explored. This is generally an issue when trying to make general claims from an individual-based model where only a very narrow parameter region has been explored of a necessarily particular model. However, in this paper, the issue is more evident. As in this model the two tasks ultimately only differ by their costs, the parameter values specifying their costs should be varied to determine their effects. Instead, the model sets a very low survival cost for work (yh=0.1) and a very high survival cost for defense (xh=3), the latter of which can be compensated by the benefit of group augmentation (xn=3). Some very limited variation of xh and xn is explored, always for very high values, effectively making defense unevolvable except if there is group augmentation. Hence, as I stated in my previous review, a more extensive parameter exploration addressing this should be included, but this has not been done. Consequently, the main conclusion that "division of labor" needs group augmentation is essentially enforced by the limited parameter exploration, in addition to the first reason above.

Third, what is called "division of labor" here is an overinterpretation. When the two tasks evolve, what exists in the model is some individuals that do reproduction-costly tasks (so-called "work") and survival-costly tasks (so-called "defense"). However, there are really no two tasks that are being completed, in the sense that completing both tasks (e.g., work and defense) is not necessary to achieve a goal (e.g., reproduction). In this model there is only one task (reproduction, equation 4,5) to which both "tasks" contribute equally and so one task doesn't need to be completed if the other task compensates for it. So, this model does not actually consider division of labor.

eLife Assessment

This study introduces a novel and potentially valuable metric-phenological lag-to quantify the gap between observed and expected phenological shifts under climate warming. While the dataset is extensive and the framework is clearly defined, key assumptions (e.g., base temperature, linear forcing response) are not empirically tested, and the analysis underexplores key spatial and climatic gradients. The strength of evidence is mostly solid but would benefit from further validation and deeper analysis.

Reviewer #1 (Public review):

Jiang et al. present a measure of phenological lag by quantifying the effects of abiotic constraints on the differences between observed and expected phenological changes, using a combination of previously published phenology change data for 980 species, and associated climate data for study sites. They found that, across all samples, observed phenological responses to climate warming were smaller than expected responses for both leafing and flowering spring events. They also show that data from experimental studies included in their analysis exhibited increased phenological lag compared to observational studies, possibly as a result of reduced sensitivity to climatic changes. Furthermore, the authors present evidence that spatial trends in phenological responses to warming may differ than what would be expected from phenological sensitivity, due to the seasonal timing of when warming occurs. Thus, climate change may not result in geographic convergences of phenological responses. This study presents an interesting way to separate the individual effects of climate change and other abiotic changes on the phenological responses across sites and species.

Strengths:

A straightforward mathematical definition of phenological lag allows for this method to potentially be applied in different geographic contexts. Where data exists, other researchers can partition the effects of various abiotic forcings on phenological responses that differ from those expected from warming sensitivity alone.

Identifying phenological lag, and associated contributing factors, provides a method by which more nuanced predictions of phenological responses to climate change can be made. Thus, this study could improve ecological forecasting models.

Weaknesses:

The analysis here could be more robust. A more thorough examination of phenological lag would provide stronger evidence that the framework presented has utility. The differences in phenologica lag by study approach, species origin, region, and growth form are interesting, and could be expanded. For example, the authors have the data to explore the relationships between phenological lag and the quantitative variables included in the final model (altitude, latitude, mean annual temperature) and other spatial or temporal variables. This would also provide stronger evidence for the author's claims about potential mechanisms that contribute to phenological lag.

The authors include very little data visualizations, and instead report results and model statistics in tables. This is difficult to interpret and may obscure underlying patterns in the data. Including visual representations of variable distributions and between-variable relationships, in addition to model statistics, provides stronger evidence than model statistics alone.

Reviewer #3 (Public review):

Summary:

The authors developed a new phenological lag metric and applied this analytical framework to a global dataset to synthesize shifts in spring phenology and assess how abiotic constraints influence spring phenology.

Strengths:

The dataset developed in this study is extensive, and the phenological lag metric is valuable.

Weaknesses:

The stability of the method used in this study needs improvement, particularly in the calculation of forcing requirements. In addition, the visualization of the results (such as Table 1) should be enhanced.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Jiang et al. present a measure of phenological lag by quantifying the effects of abiotic constraints on the differences between observed and expected phenological changes, using a combination of previously published phenology change data for 980 species, and associated climate data for study sites. They found that, across all samples, observed phenological responses to climate warming were smaller than expected responses for both leafing and flowering spring events. They also show that data from experimental studies included in their analysis exhibited increased phenological lag compared to observational studies, possibly as a result of reduced sensitivity to climatic changes. Furthermore, the authors present compelling evidence that spatial trends in phenological responses to warming may differ from what would be expected from phenological sensitivity, due to the seasonal timing of when warming occurs. Thus, climate change may not result in geographic convergences of phenological responses. This study presents an interesting way to separate the individual effects of climate change and other abiotic changes on the phenological responses across sites and species.

Greater phenological lag with experimental studies results in reduced sensitivity to climatic changes, not other way around.

Strengths:

A clearly defined and straightforward mathematical definition of phenological lag allows for this method to be applied in different scientific contexts. Where data exists, other researchers can partition the effects of various abiotic forcings on phenological responses that differ from those expected from warming sensitivity alone.

Sensitivity does not tell the magnitude of phenological changes, nor does it provide indications of mechanisms responsible for changes in spring phenology. Because of uneven warming, the same average temperature change (annual or spring temperatures) can have greater (greater warming prior to budburst) or smaller (smaller warming prior to budburst) phenological change than that with even warming. When average temperature change is close to zero, uneven warming can lead to infinite sensitivity values, either advanced (warmer temperatures prior to budburst) or delayed (cooler temperatures prior to budburst) spring phenology.

It is not clear why sensitivity is so popularly used in phenological research.

Identifying phenological lag and associated contributing factors provides a method by which more nuanced predictions of phenological responses to climate change can be made. Thus, this study could improve ecological forecasting models.

Weaknesses:

The authors include very few data visualizations, and instead report results and model statistics in tables. This is difficult to interpret and may obscure underlying patterns in the data. Including visual representations of variable distributions and between-variable relationships, in addition to model statistics, provides stronger evidence than model statistics alone.

The use of stepwise, automated regression may be less suitable than a hypothesis-driven approach to model selection, combined with expanded data visualization. The use of stepwise regression may produce inappropriate models based on factors of the sample data that may preclude or require different variable selection.

We used two statistical methods, variance analysis to examine differential phenological responses (Figure 2) and regression analysis to determine the relative importance of forcing change, budburst temperature, and physiological lag, the drivers of changes in spring phenology (Table 2). Our objective was to understand why plants show differential responses by research approach, species origin, climatic region, and growth form identified in previous research. Variable selection may affect minor (altitude, latitude, MAT, and average spring temperature change) or insignificant (photoperiod and long-term precipitation) variables, but not those related to drivers of spring phenology. We are not sure how hypothesis-driven approach can help with our objective.

Reviewer #2 (Public review):

Summary:

This is a meta-analysis of the relative contributions of spring forcing temperature, winter chilling, photoperiod and environmental variables in explaining plant flowering and leafing phenology. The authors develop a new summary variable called phenology lag to describe why species might have different responses than predicted by spring temperature.

Strengths:

The summary statistic is used to make a variety of comparisons, such as between observational studies and experimental studies.

Weaknesses:

By combining winter chilling effects, photoperiod effects, and environmental stresses that might affect phenology, the authors create a new variable that is hard to interpret. The authors do not provide information in the abstract about new insights that this variable provides.

Phenological lag contains effects of all constraints that may include chilling effects, photoperiod effects, and environmental stresses and is, indeed, hard to interpret without investigation of individual constraints. In our synthesis, spring phenology (or photoperiod effect) is not significant across all studies complied. It is also unlikely that lack of winter chilling causes the systemic differences in phenological lag between observational and experimental studies or between native and exotic species (see discussion at lines 335-339). At individual study level, the contribution of different constraints to the overall lag effect can be specifically determined if moisture stresses, species chilling and photoperiod effects, or cold hardiness are known from on-site monitoring or previous research.

The meaning of phenological lag is described at lines 34-38 in the abstract.

Comments:

It would be useful to have a map showing the sites of the studies.

A map showing the sites of the studies was added as supplementary Figure S1.

The authors should provide a section in which the strengths and weaknesses of the approach are discussed. Is it possible that mixing different types of data, studies, sample sizes, number of years, experimental set-ups, and growth habits results in artifacts that influence the results?

Both strengths and weaknesses are discussed at various places throughout the paper. The weakness of our method, as indicated by the reviewer, is the inclusion of different constraints in the phenological lag and has been described at lines 34-38 in the abstract and lines 80-86 in the introduction of the concept. We have also expanded Conclusion section to discuss possible caveats at lines 369-393.

As in all data analyses, the results can change with addition of more/different data, especially when sample size is relatively small. Ideally, comparisons are made among levels of fixed effects while controlling variations of other conditions. In phenological studies, however, climatic, phenological, and biological conditions all vary. For example, observational and experimental studies differ not only in the nature of warming (natural climate change vs artificial warming), but also in levels of warming (greater warming with experimental studies) and climatic, phenological, and biological conditions (Table 1). All phenological syntheses (or meta-analyses) have to make do with this uncontrolled nature of phenological data.

Now that the authors have created this new variable, phenological lag, which of the components that contribute to it has the most influence on it? Or which components are most influential in which circumstances? For example, what are some examples where photoperiod causes a phenological lag?

Any of the phenological constraints identified can contribute alone or in combination with others to the overall effect of phenological lag. Across all studies with this synthesis, the lack of significance with spring phenology rules out photoperiod effect, while the association of longer phenological lags with longer accumulation of winter chilling does not suggest general chilling shortage with the current extent of climate change.

Although spring phenology is not significant across all studies, photoperiod effect can be influential at individual studies where changes in spring phenology are large. However, reported photoperiod effects in the literature are mostly confounding effects with temperatures, i.e., longer photoperiods are associated with longer hours of high daytime temperatures (see Chu et al., 2021). Other than European beech under an unlikely scenario of climate change (growth resumes at beginning of winter), there has been not clear evidence showing the effect of photoperiod in constraining spring phenology.

Another confounding effect with photoperiod is extra heating effect with artificial light sources in warming experiments. Some early studies have shown that leaf temperature can be several degrees above the ambient air, due to long-wave radiation with artificial light sources. It is hard to believe the constraining effect of photoperiod on spring phenology if phenological changes are within inter-annual variations (can be a few weeks), although photoperiod effect has been increasingly discussed recently.

Recommendations for the authors:

Reviewing Editor:

A key methodological concern is the inconsistent definition of growth temperature across observations. It is calculated over the interval between the baseline phenological date and the expected date under warming - a window that varies by species, site, and treatment. This variability limits comparability across observations and may introduce circularity, as growth temperature is derived from the same modelled expectation (i.e., the expected phenological advance) that it is later used to explain.

The term “growth temperature” has been replaced with “budburst temperature” to indicate temperatures at species events. Budburst temperature is the average temperature within the window of expected response with the warmer climate and, as indicated by the editor, varies by species, sites, and treatments. This species-specific temperature provides an opportunity to compare among species, sites, and treatments and helps explain differences in observed responses, as demonstrated in the discussion of results in this synthesis.

Forcing change, budburst temperature, and expected response are related. High budburst temperatures are associated with smaller expected responses, which helps explain smaller observed responses with late season species and areas of warm climates that have been often attributed to chilling or photoperiod effect.

Additionally, the use of degree days above 0 {degree sign}C as a universal metric for spring forcing oversimplifies species' temperature responses. This approach assumes not only a fixed base temperature but also a linear response to temperature accumulation, which overlooks well-established nonlinear or species-specific thermal response curves. To improve the robustness and interpretability of the phenological lag framework, we encourage the authors to consider these limitations and explore ways to test or justify these modelling assumptions more explicitly.

The use of 0 degree base temperature may not be the best choice for some species. Except for some early work, there has been few experimental research on physiological aspects of chilling and forcing processes. A popular alternative is modelling using assumed temperature response models. As variables influencing chilling and forcing processes are not controlled, the determined base temperatures and temperature response models may be OK with the species studied under particular conditions but would be inappropriate for applications beyond. It is hard to believe that species, in a study, all have different base temperature for accumulation of spring forcing and optimum temperature for winter chilling. Apparently, this is the result of model fitting, not actual dynamics of chilling and forcing processes.

Two base temperatures are commonly used, 0 and 5 oC, although choice is not generally justified. It is known for long time that temperatures above 0oC contribute to spring forcing. My personal experience at tree nursery suggests that seedlings will flush after winter cold storage, even at forcing temperatures ≤ 5 oC in the dark. The use of 5 oC is rather the choice of tradition (5 oC is commonly used to define growing season) than scientific justification. The use of high base temperatures may not make much difference at high temperatures due to short forcing duration but will underestimate forcing at low temperatures due to long forcing duration and large proportions of forcing between 0 and base temperatures. We are not aware of any experimental studies that demonstrate non-zero base temperatures.

Within the dominant range of spring temperatures (e.g., between 5 and 25 oC), the forcing responses to temperatures can be approximated with linear models. Again, we are not aware of any non-linear forcing models that can be safely applied beyond the species studied under particular conditions.

Regardless, the uses of different base temperatures or forcing models would not affect the partitioning of phenological changes, simply because temperature response models reflect physiological aspects of chilling and forcing processes and would not change with climate warming.

The authors introduce a new metric, phenological lag, to assess how phenological constraints influence spring phenology, offering new insights into phenological research. However, there are several concerns. First, the research question and the study's aim are not clearly presented. The authors primarily analyzed phenological lag and simply compared it across different groups, but additional analyses are needed to adequately address the research question. In addition, the broader importance of this study is not clearly explained - why this research is necessary and what it contributes to the field should be explicitly stated.

The research question is outlined at lines 92-108. We added “Our objective was to determine how phenological responses differ among different groups and how differential responses are related to drivers of spring phenology, i.e., forcing change, budburst temperature, and phenological lag” at lines 106-108.

(1) Abstract: The methodological improvements and more key results should be included.

Growth temperature has been replaced with “budburst temperature” to indicate temperatures at time of budburst. More results are added at lines 40-48.

(2) Line 32: Terms such as "sensitivity analysis" and "phenological lag" need clearer definitions.

We added at lines 32-33 to define sensitivity analysis “that is based on rates of phenological changes, not on drivers of spring phenology”. Phenological lag is defined at lines 34-38.

(3) Lines 38-47: Further results and the urgency or importance of the study should be conveyed.

More results are added at lines 40-48. The importance of this study is described at lines 48-50.

(4) Line 57-58: This sentence is unclear - please clarify.

The sentence is modified to “difficult using sensitivity analysis that is based on rates of phenological changes, not on drivers of spring phenology".

(5) Line 60: break "endodormancy".

Breaking dormancy would mean endodormancy.

(6) Line 67: What does "growth temperature" refer to?

Growth temperature has been replaced with “budburst temperature” to indicate temperatures at time of budburst. It is calculated as the average temperature within the window of expected response with the warmer climate.

(7) Lines 87-94: The specific purpose of the study is vague. Why is this method needed, and how will it serve future research?

We have modified the paragraph at lines 92-108 to provide justification and objective of the study.

(8) Lines 163-164: The rationale for exploring differences in observed responses and phenological lag needs to be better justified.

We added explanations at lines 179-182 why observed responses and phenological lag were chosen in the analysis.

(9) Lines 178-183: Tables and figures should be properly cited within the text.

Table S3 was added at line 197.

(10) Lines 195-198: Clarify whether variables were scaled before model analysis.

We clarified at line 192 “variables were not standardized prior to regression analysis”.

(11) Line 206-207: The observed response is presented as the number of advanced days, while temperature sensitivity refers to the response of spring phenology to temperature - these are different variables and should not be conflated.

The two variables are related but show different aspects of phenological changes. Observed response divided by average temperature change gives temperature sensitivity. Observed response is the total changes in number of days observed, while temperature sensitivity is the change in number of days per unit change in average temperature (oC). Sensitivity may reflects rates of phenological change with temperature (see responses to reviewer 1).

(12) In the discussion section, the authors compared phenological responses among different groups separately. This section requires substantial improvement to more clearly answer the research question.

These discussions are related to our objective “how phenological responses differ among different groups identified in previous research (i.e., research approach, species origin, climatic region, and growth form) and how these differential responses are related to drivers of spring phenology, i.e., forcing change, budburst temperature, and phenological lag”.

eLife Assessment

This paper presents a valuable software package, named "Virtual Brain Inference" (VBI), that enables faster and more efficient inference of parameters in dynamical system models of whole-brain activity, grounded in artificial network networks for Bayesian statistical inference. The authors have provided convincing evidence, across several case studies, for the utility and validity of the methods using simulated data from several commonly used models, but more thorough benchmarking could be used to demonstrate the practical utility of the toolkit. This work will be of interest to computational neuroscientists interested in modelling large-scale brain dynamics.

Reviewer #1 (Public review):

This work provides a new Python toolkit for combining generative modeling of neural dynamics and inversion methods to infer likely model parameters that explain empirical neuroimaging data. The authors provided tests to show the toolkit's broad applicability, accuracy, and robustness; hence, it will be very useful for people interested in using computational approaches to better understand the brain.

Strengths:

The work's primary strength is the tool's integrative nature, which seamlessly combines forward modelling with backward inference. This is important as available tools in the literature can only do one and not the other, which limits their accessibility to neuroscientists with limited computational expertise. Another strength of the paper is the demonstration of how the tool can be applied to a broad range of computational models popularly used in the field to interrogate diverse neuroimaging data, ensuring that the methodology is not optimal to only one model. Moreover, through extensive in-silico testing, the work provided evidence that the tool can accurately infer ground-truth parameters even in the presence of noise, which is important to ensure results from future hypothesis testing are meaningful.

Weaknesses

The paper still lacks appropriate quantitative benchmarking relative to non-Bayesian-based inference tools, especially with respect to performance accuracy and computational complexity and efficiency. Without this benchmarking, it is difficult to fully comprehend the power of the software or its ability to be extended to contexts beyond large-scale computational brain modelling.

Reviewer #2 (Public review):

Summary:

Whole-brain network modeling is a common type of dynamical systems-based method to create individualized models of brain activity incorporating subject-specific structural connectome inferred from diffusion imaging data. This type of model has often been used to infer biophysical parameters of the individual brain that cannot be directly measured using neuroimaging but may be relevant to specific cognitive functions or diseases. Here, Ziaeemehr et al introduce a new toolkit, named "Virtual Brain Inference" (VBI), offering a new computational approach for estimating these parameters using Bayesian inference powered by artificial neural networks. The basic idea is to use simulated data, given known parameters, to train artificial neural networks to solve the inverse problem, namely, to infer the posterior distribution over the parameter space given data-derived features. The authors have demonstrated the utility of the toolkit using simulated data from several commonly used whole-brain network models in case studies.

Strength:

- Model inversion is an important problem in whole-brain network modeling. The toolkit presents a significant methodological step up from common practices, with the potential to broadly impact how the community infers model parameters.<br /> - Notably, the method allows the estimation of the posterior distribution of parameters instead of a point estimation, which provides information about the uncertainty of the estimation, which is generally lacking in existing methods.<br /> - The case studies were able to demonstrate the detection of degeneracy in the parameters, which is important. Degeneracy is quite common in this type of models. If not handled mindfully, they may lead to spurious or stable parameter estimation. Thus, the toolkit can potentially be used to improve feature selection or to simply indicate the uncertainty.<br /> - In principle, the posterior distribution can be directly computed given new data without doing any additional simulation, which could improve the efficiency of parameter inference on the artificial neural network is well-trained.

Weaknesses:

- The z-scores used to measure prediction error are generally between 1-3, which seems quite large to me. It would give readers a better sense of the utility of the method if comparisons to simpler methods, such as k-nearest neighbor methods, are provided in terms of accuracy.<br /> - A lot of simulations are required to train the posterior estimator, which is computationally more expensive than existing approaches. Inferring from Figure S1, at the required order of magnitudes of the number of simulations, the simulation time could range from days to years, depending on the hardware. The payoff is that once the estimator is well-trained, the parameter inversion will be very fast given new data. However, it is not clear to me how often such use cases would be encountered. It would be very helpful if the authors could provide a few more concrete examples of using trained models for hypothesis testing, e.g., in various disease conditions.

eLife Assessment

This important study identifies and partially characterises two proteins optimised for coordinated peptidoglycan degradation during two spore morphogenesis programs in the bacterium Myxococcus xanthus. The evidence supporting the conclusions is solid, although the description of the data is somewhat overstated. After some editing, the paper will be of interest to those studying peptidoglycan synthesis and reorganisation, which is a central aspect of microbial cell biology.

Reviewer #1 (Public review):

Summary:

Ramirez Carbo et al. use the powerful M. xanthus spore morphogenesis model to address fundamental mechanisms in coordinated peptidoglycan remodeling and degradation. As peptidoglycan is an essential macromolecule and difficult to study in vivo, the authors use indirect but important methodology. The authors first identify two lytic transglycosylase (Ltg) enzymes necessary for spore morphogenesis using mutant phenotypic studies. They characterize these mutants for their role in coordinating spore morphogenesis induced either in fruiting bodies (starvation-dependent) or in liquid-rich media conditions (chemical-dependent). They conclude from these phenotypic and epistatic analyses that LtgA is necessary for morphogenesis during chemical-induced sporulation, and LtgB appears to be necessary to coordinate LtgA activity by interfering with LtgA function. Under starvation-induced sporulation, the absence of LtgB interferes with the building of fruiting bodies. LtgA does not appear to play a primary role in promoting aggregation into fruiting bodies, nor in degradation of peptidoglycan as assayed by loss of signal in anti-PG immunofluorescence. The authors demonstrate that the purified periplasmic domain of LtgA is highly active in degrading purified PG sacculi in vitro, while that of LtgB is highly reduced (relative to LtgA or lysozyme). The authors use photoactivated mCherry Lyt fusions and PALM to track the fusion protein mobility, which they state correlates with activity as immobilization results from PG binding. They demonstrate that in vegetative cells, a greater proportion of LtgA-PAmCh is more immobile (more active) than LtgB-PAmCh, but that directly after chemical-induction of sporulation, LtgB-PAmCh becomes more immobile (active). These analyses in the partner mutant backgrounds suggest that LtgA-PAmCh is more immobile (less active) in the absence of LtgB, but the reverse is not observed. Finally, the authors demonstrate that overexpression of LtgA in vegetative conditions leads to cell rounding, likely because of uncontrolled PG degradation, while overexpression of LtgB displays no phenotype.

Strengths:

This paper capitalizes on a novel spore morphogenesis mechanism to define proteins and mechanisms involved in peptidoglycan reorganization. The authors use the powerful PALM microscopy technique to assess Ltg activity in vivo by assaying for immobility as a proxy for PG binding. The authors elucidate a novel mechanism by which two Ltg's function together- with one (LtgB) seeming to regulate the activity of the other (the primary Ltg).

Despite some weaknesses, there is no question that this study provides important insight into mechanisms of peptidoglycan remodeling- a difficult but highly impactful area of study with implications for the development of novel therapeutics and the discovery of mechanisms of fundamental bacterial physiology.

Weaknesses:

In many places, the authors do not adequately justify interpretations of their assays, leading to some apparently unjustified conclusions. Many of these are minor and may just require citations to demonstrate that the interpretations are justified by previous studies (detailed in recommendations below), but two bigger concerns are as follows:

(1) It is not clear how the muropeptides listed in Figure 1 were assigned, and it is missing in the methods. In the sporulating conditions, the spectra look like combinations of multiple peaks, and the data, as stated, is not convincing to the non-specialist eye.

(2) The observation that the lytB mutant prevents appropriate aggregation into fruiting bodies does not allow the interpretation that the absence of LytB prevents PG morphogenesis in the starvation-induced sporulation pathway, per se. It is more likely that in the lytB mutant, the morphogenesis program is not even triggered. This is because signaling proteins and regulators (specifically, C-signal accumulation/activated FruA), which are dependent on increased cell-cell signaling in the fruiting body, do not accumulate appropriately in shallow aggregates. C-signal/FruA are necessary to trigger the sporulation program in FBs. BTW: A hypothesis to explain the indirect effect of ltgB absence on aggregation could be that UDP-precursors are not regulated appropriately (unregulated LtyA??), so polysaccharides necessary for motility are not properly produced.

Along these lines, fruiting body formation does not equal sporulation, and even "darkened" fruiting bodies can be misleading, as some mutants form polysaccharide-rich fruiting bodies (that appear dark under certain light conditions in the stereomicroscope) but do not sporulate efficiently. The wording in the text suggests that the authors assume that sporulation levels are normal because fruiting bodies are produced (see specific comments for details).

(3) The authors repeatedly state that production of spore coat polysaccharides likely affects the PG IP staining (see below), but this is not well justified. A citation is needed if this has already been directly shown, or the language needs to be softened.

(4) Better justification for the immobility of Lyt proteins in vivo as an assay for activity may be required. If this is well known in the field, it should be explicitly stated. The authors address this better in the discussion - but still state it is a correlation.

Reviewer #2 (Public review):

Summary:

The authors' initial goal was to demonstrate loss of PG during the slow sporulation process of Myxococcus xanthus, with examination of the PG degradation products in order to implicate possible enzymes involved. Upon finding a predominance of LGT products, they examined sporulation in strains lacking each of the 14 candidate LGTs encoded in the genome, leading to the identification of two sporulation-linked LGTs. An extensive characterization of the roles played by these LGTs. One LGT is responsible for the slow sporulation PG degradation, while another is required for the rapid sporulation process. Interestingly, the "slow" LGT seems to provide an important regulatory brake on the rapid enzyme. Single-molecule fluorescent tracking of these enzymes was used to develop a model for their interaction with PG that mimics their observed activity. The rate of PG synthesis activity was also shown to impact the rate of PG degradation, suggesting potential interplay between the synthetic and degradative enzymes.

Strengths:

The genetic analysis to identify sporulation-linked LGTs and their effects on growth, sporulation, and spore properties was well done and productive. The fluorescence microscopy to track LGT mobility, presumably tied to activity, produced a convincing argument about the mechanism of regulation of one LGT by another.

Weaknesses:

While the impact of LGTs on sporulation was clearly demonstrated, the PG analysis that resulted from the study of LGTs raised some important unanswered questions. The analyses suggest that the PG is degraded to quite small fragments, which would normally be lost during the purification of PG. How these small fragments were thus detected is unclear, and this suggests a more complex story concerning PG metabolism during sporulation. An anti-PG antibody is used to quantify PG in the spores, but it is not made clear what the specificity of this antibody is, and thus whether it would recognize the LGT-altered PG of the spore. The authors suggest a "new mechanism of sporulation" when they have actually simply identified an important factor (PG degradation by LGTs) within a complex "process of sporulation".

eLife Assessment

In this manuscript, Chen et al. used cryo-ET and in vitro reconstituted system to demonstrate that the autoinhibited form of LRRK2 can also assemble into filaments on the microtubule surface, with a new interface involving the N-terminal repeats that were disordered in the previous active-LRRK2 filament structure. The structure obtained in this study is the highest resolution of LRRK2 filaments done by subtomogram averaging, representing a major technical advance compared to the previous paper from the same group. This is an important study, especially considering the pharmacological implications of the effect of inhibitors of the protein. The strengths of the data are convincing, but the study would be considerably strengthened if the authors explored the physiological significance of the new interfaces and the incomplete decoration of microtubules described here.

Reviewer #1 (Public review):

Summary:

In this manuscript, Chen et al. use cryo-electron tomography and an in vitro reconstitution system to demonstrate that the autoinhibited form of LRRK2 can assemble into filaments that wrap around microtubules. These filaments are generally shorter and less ordered than the previously characterized active-LRRK2 filaments. The structure reveals a novel interface involving the N-terminal repeats, which were disordered in the earlier active filament structure. Additionally, the autoinhibited filaments exhibit distinct helical parameters compared to the active form.

Strengths:

This study presents the highest-resolution structure of LRRK2 filaments obtained via subtomogram averaging, marking a significant technical advance over the authors' previous work published in Cell. The data are well presented, with high-quality visualizations, and the findings provide meaningful insights into the structural dynamics of LRRK2.

Weaknesses and Suggestions:

The revised manuscript by Chen et al. has fully addressed all of my previous suggestions regarding the rearrangement of the main figures.

Reviewer #2 (Public review):

The authors of this paper have done much pioneering work to decipher and understand LRRK2 structure and function and uncover the mechanism by which LRRK2 binds to microtubules and to study the roles that this may play in biology. Their previous data demonstrated that LRRK2 in the active conformation (pathogenic mutation or Type I inhibitor complex) bound to microtubule filaments in an ordered helical arrangement. This they showed induced a "roadblock" in the microtubule impacting vesicular trafficking. The authors have postulated that this is a potentially serious flaw with Type 1 inhibitors and that companies should consider generating Type 2 inhibitors in which the LRRK2 is trapped in the inactive conformation. Indeed the authors have published much data that LRRK2 complexed to Type 2 inhibitors does not seem to associate with microtubules and cause roadblocks in parallel experiments to those undertaken with type 1 inhibitors published above.

In the current study the authors have undertaken an in vitro reconstitution of microtubule bound filaments of LRRK2 in the inactive conformation, which surprisingly revealed that inactive LRRK2 can also interact with microtubules in its auto-inhibited state. The authors' data shows that while the same interphases are seen with both the active LRRK2 and inactive microtubule bound forms of LRRK2, they identified a new interphase that involves the WD40-ARM-ANK- domains that reportedly contributes to the ability of the inactive form of LRRK2 to bind to microtubule filaments. The structures of the inactive LRRK2 complexed to microtubules are of medium resolution and do not allow visualisation of side chains.

This study is extremely well written and the figures incredibly clear and well presented. The finding that LRRK2 in the inactive autoinhibited form can associate with microtubules is an important observation that merits further investigation. This new observation makes an important contribution to the literature and builds upon the pioneering research that this team of researchers has contributed to the LRRK2 fields.

Comments on revised version:

The authors have adequately addressed my questions and those of the other Reviewers in my opinion.

Reviewer #3 (Public review):

Summary:

The manuscript by Chen et al examines the structure of the inactive LRRK2 bound to microtubules using cryo-EM tomography. Mutations in this protein have been shown to be linked to Parkinson's Disease. It is already shown that the active-like conformation of LRRK2 binds to the MT lattice, but this investigation shows that full-length LRRk2 can oligomerize on MTs in its autoinhibited state with different helical parameters than were observed with active-like state. The structural studies suggest that the autoinhibited state is less stable on MTs.

Strengths:

The protein of interest is very important biomedically and a novel conformational binding to microtubules in proposed

The authors have addressed my original critique.

eLife Assessment

This is an important study that demonstrates that blood pressure variability impairs myogenic tone and diminishes baroreceptor reflex. The study also provides evidence that blood pressure variability blunts functional hyperemia and contributes to cognitive decline. The evidence is compelling whereby the authors use appropriate and validated methodology in line with or more rigorous than the current state-of-the-art.

Reviewer #1 (Public review):

This study examined the effect of blood pressure variability on brain microvascular function and cognitive performance. By implementing a model of blood pressure variability using intermittent infusion of AngII for 25 days, the authors examined different cardiovascular variables, cerebral blood flow and cognitive function during midlife (12-15-month-old mice). Key findings from this study demonstrate that blood pressure variability impairs baroreceptor reflex and impairs myogenic tone in brain arterioles, particularly at higher blood pressure. They also provide evidence that blood pressure variability blunts functional hyperemia and impairs cognitive function and activity. Simultaneous monitoring of cardiovascular parameters, in vivo imaging recordings, and the combination of physiological and behavioral studies reflect rigor in addressing the hypothesis. The experiments are well designed, and data generated are clear.

A number of issues raised earlier were addressed by the authors in the revised manuscript. The responses are convincing. These included circadian rhythm considerations, baroreflex findings, BP fluctuations driven by animal movement, and data presentation.

Overall, this is a solid study with huge physiological implications. I believe that it will be of great benefit to the field.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

This study examined the effect of blood pressure variability on brain microvascular function and cognitive performance. By implementing a model of blood pressure variability using an intermittent infusion of AngII for 25 days, the authors examined different cardiovascular variables, cerebral blood flow, and cognitive function during midlife (12-15-month-old mice). Key findings from this study demonstrate that blood pressure variability impairs baroreceptor reflex and impairs myogenic tone in brain arterioles, particularly at higher blood pressure. They also provide evidence that blood pressure variability blunts functional hyperemia and impairs cognitive function and activity. Simultaneous monitoring of cardiovascular parameters, in vivo imaging recordings, and the combination of physiological and behavioral studies reflect rigor in addressing the hypothesis. The experiments are well-designed, and the data generated are clear. I list below a number of suggestions to enhance this important work:

(1) Figure 1B: It is surprising that the BP circadian rhythm is not distinguishable in either group. Figure 2, however, shows differences in circadian rhythm at different timepoints during infusion. Could the authors explain the lack of circadian effect in the 24-h traces?

The circadian rhythm pattern is apparent in Figure 2 (Active BP higher than Inactive BP), where BP is presented as 12hour averages. When the BP data is expressed as one-hour averages (rather than minute-to-minute) over 24hours, now included in the revised manuscript as Supplemental Figure 3C-D, the circadian rhythm becomes noticeable. In addition, we have included one-hour average BP data for all mice in the control and BPV groups, Supplemental Figure 3A-B.

Notably, the Ang-II induced pulsatile BP pattern remains evident in the one-hour averages for the BPV group, Supplemental Figure 3B. To minimize bias and validate variability, pump administrations start times were randomized for both control and BPV groups, Supplemental Figure 3A-B. Despite these adjustments, the circadian rhythm profile of BP is consistently maintained across individual mice and in the collective dataset, Supplemental Figure 3C-D.

(2) While saline infusion does not result in elevation of BP when compared to Ang II, there is an evident "and huge" BP variability in the saline group, at least 40mmHg within 1 hour. This is a significant physiological effect to take into consideration, and therefore it warrants discussion.

Thank you for this comment. The large variations in BP in the raw traces during saline infusion reflects transient BP changes induced by movement/activity, which is now included in Figure 1B (maroon trace). The revised manuscript now includes Line 222 “Note that dynamic activity-driven BP changes were apparent during both saline- and Ang II infusions, Figure 1B”.

(3) The decrease in DBP in the BPV group is very interesting. It is known that chronic Ang II increases cardiac hypertrophy, are there any changes to heart morphology, mass, and/or function during BPV? Can the decrease in DBP in BPV be attributed to preload dysfunction? This observation should be discussed.

The lower DBP in the BPV group was already present at baseline, while both groups were still infused with saline, and was a difference beyond our control. However, this is an important and valid consideration, particularly considering the minimal yet significant increase in SBP within the BPV group (Figure 1D). Our goal was to induce significant transient blood pressure responses (BPV) and investigate the impact on cardiovascular and neurovascular outcomes in the absence of hypertension. We did not anticipate any major cardiac remodeling at this early time point (considering the absence of overt hypertension) and thus cardiac remodeling was not assessed and this is now discussed in the revised manuscript (Line 443-453).

(4) Examining the baroreceptor reflex during the early and late phases of BPV is quite compelling. Figures 3D and 3E clearly delineate the differences between the two phases. For clarity, I would recommend plotting the data as is shown in panels D and E, rather than showing the mathematical ratio. Alternatively, plotting the correlation of ∆HR to ∆SBP and analyzing the slopes might be more digestible to the reader. The impairment in baroreceptor reflex in the BPV during high BP is clear, is there any indication whether this response might be due to loss of sympathetic or gain of parasympathetic response based on the model used?

We appreciate the reviewer’s suggestion and have accordingly generated new figures displaying scatter plots of SBP vs HR with linear regression analysis (Figure 3D-G). Our goal is to further investigate which branch of the autonomic nervous system is affected in this model. The loss of a bradycardic response suggests either an enhancement of sympathetic activity, a reduction in parasympathetic activity, or a combination of both. This is briefly discussed in the revised manuscript (Line 486-496).

Heart rate variability (HRV) serves as an index of neurocardiac function and dynamic, non-linear autonomic nervous system processes, as described in Shaffer and Ginsber[1]. However, given that our data was limited to BP and HR readings collected at one-minute intervals, our primary assessment of autonomic function is limited to the bradycardic response. Further studies will be necessary to fully characterize the autonomic parameters influenced by chronic BPV.

(5) Figure 3B shows a drop in HR when the pump is ON irrespective of treatment (i.e., independent of BP changes). What is the underlying mechanism?

We apologize for any lack of clarity. These observed heart rate (HR) changes occurred during Ang II infusion, when blood pressure (BP) was actively increasing. In the control group, the pump solution was switched to Ang II during specific periods (days 3-5 and 21-25 of the treatment protocol) to induce BP elevations and a baroreceptor response, allowing direct comparisons between the control and BPV group.

To clarify this point, we have revised Line 260-263 of the manuscript: “To compare pressure-induced bradycardic responses between BPV and control mice at both early and later treatment stages, a cohort of control mice received Ang II infusion on days 3-5 (early phase) (Supplemental Figure 4) and days 21-25 (late phase) thereby transiently increasing BP”.

Additionally, a detailed description has been added to the Methods section (Line 96-101): “Controls receiving Ang II: To facilitate between-group comparisons (control vs BPV), a separate cohort of control mice were subjected to the same pump infusion parameters as BPV mice but for a brief period receiving Ang II infusions on days 3-5 and 21-25 for experiments assessing pressure-evoked responses, including bradycardic reflex, myogenic response, and functional hyperemia at high BP.”

(6) The correlation of ∆diameter vs MAP during low and high BP is compelling, and the shift in the cerebral autoregulation curve is also a good observation. I would strongly recommend that the authors include a schematic showing the working hypothesis that depicts the shift of the curve during BPV.

Thank you for this insightful comment. The increase in vessel reactivity to BP elevations in parenchymal arterioles of BPV mice suggests that chronic BPV induces a leftward shift and a potential narrowing of the cerebral autoregulation range (lower BP thresholds for both the upper and lower limits of autoregulation). This has been incorporated (and discussed) into the revised manuscript (see Figure 5N).

One potential explanation for these changes is that the absence of sustained hypertension, a prominent feature in most rodent models of hypertension, limits adaptive processes that protect the cerebral microcirculation from large BP fluctuations (e.g., vascular remodeling). While this study does not specifically address arteriole remodeling, the lack of such adaptation may reduce pressure buffering by upstream arterioles, thereby rendering the microcirculation more vulnerable to significant BP fluctuations.

The unique model allows for measurements of parenchymal arteriole reactivity to acute dynamic changes in BP (both an increase and decrease in MAP). Our findings indicate that chronic BPV enhances the reactivity of parenchymal arterioles to BP changes—both during an increase in BP and upon its return to baseline, Supplemental Figure 5C, F. The data suggest an increased myogenic response to pressure elevation, indicative of heightened contractility, a common adaptive process observed in rodent models of hypertension[2-4]. However, our model also reveals a notable tendency for greater dilation when the BP drops, Supplemental Figure 5F. This intriguing observation may suggest ischemia during the vasoconstriction phase (at higher BP), leading to enhanced release of dilatory signals, which subsequently manifest as a greater dilation upon BP reduction. This phenomenon bears similarities to chronic hypoperfusion models[5,6], where vasodilatory mechanisms become more pronounced in response to sustained ischemic conditions. Future studies investigating the effects of BPV on myogenic responses and brain perfusion will be a priority for our ongoing research.

(7) Functional hyperemia impairment in the BPV group is clear and well-described. Pairing this response with the kinetics of the recovery phase is an interesting observation. I suggest elaborating on why BPV group exerts lower responses and how this links to the rapid decline during recovery.

Based on the heightened reactivity of BPV parenchymal arterioles to intravascular pressure (Figure 5), we anticipate that the reduction of sensory-evoked dilations results from an increased vasoconstrictive activity and/or a decreased availability of vasodilatory signaling pathways (NO, EETs, COX-derived prostaglandins)[7,8]. Consequently, the magnitude of the FH response is blunted during periods of elevated BP in BPV mice.

Additionally, upon termination of the stimulus-induced response−when vasodilatory signals would typically dominate−vasoconstrictive mechanisms are rapidly engaged (or unmasked), leading to quicker return to baseline. This shift in the balance between vasodilatory and vasoconstrictive forces favors vasoconstriction, contributing to the altered recovery kinetics observed in BPV mice. This has been included in the Discussion section of the revised manuscript.

(8) The experimental design for the cognitive/behavioral assessment is clear and it is a reasonable experiment based on previous results. However, the discussion associated with these results falls short. I recommend that the authors describe the rationale to assess recognition memory, short-term spatial memory, and mice activity, and explain why these outcomes are relevant in the BPV context. Are there other studies that support these findings? The authors discussed that no changes in alternation might be due to the age of the mice, which could already exhibit cognitive deficits. In this line of thought, what is the primary contributor to behavioral impairment? I think that this sentence weakens the conclusion on BPV impairing cognitive function and might even imply that age per se might be the factor that modulates the various physiological outcomes observed here. I recommend clarifying this section in the discussion.

We thank the reviewer for this comment. Clinical studies have demonstrated that patients with elevated BPV exhibit impairments across multiple cognitive domains, including declines in processing speed[9] and episodic memory[10]. To evaluate memory function, we utilized behavioral tests: the novel object recognition (NOR) task to assess episodic memory[11] and the spontaneous Y-maze to evaluate short-term spatial memory[12].

Previous research indicates that older C57Bl6 mice (14-month-old) exhibit cognitive deficits compared to younger counterparts (4- and 9-month-old)[13]. To ensure rigorous selection for behavioral testing, we conducted preliminary NOR assessment, evaluating recognition memory at the one-hour delay but observing failures at the four-, and 24-hour delays, indicating age-related deficits. Based on these results, animals failing recognition criteria were excluded from subsequent behavioral assessment. However, because no baseline cognitive testing was conducted for the spontaneous Y-maze, it is possible that some mice with aged-related deficits were included in this test, which may have influenced data interpretation.

Additionally, the absence of differences in the Y-maze performance may suggest that short-term spatial memory remains intact following 25 days of BPV, a point that is now discussed in the revised manuscript.

(9) Why were only male mice used?

We appreciate this comment and acknowledge the importance of conducting experiments in both male and female mice. Studies involving female mice are currently ongoing, with telemetry data collection approximately halfway completed and two-photon imaging studies on functional hyperemia also partially completed. However, using middleaged mice for these experiments has proven challenging due to high mortality rates following telemetry surgeries. As a result, we initially limited our first cohort to male mice.

(10) In the results for Figure 3: "Ang II evoked significant increases in SBP in both control and BPV groups;...". Also, in the figure legend: "B. Five-minute average HR when the pump is OFF or ON (infusing Ang II) for control and BPV groups...." The authors should clarify this as the methods do not state a control group that receives Ang II.

Please refer to response to comment 5.

Reviewer #2 (Public review):

Summary:

Blood pressure variability has been identified as an important risk factor for dementia. However, there are no established animal models to study the molecular mechanisms of increased blood pressure variability. In this manuscript, the authors present a novel mouse model of elevated BPV produced by pulsatile infusions of high-dose angiotensin II (3.1ug/hour) in middle-aged male mice. Using elegant methodology, including direct blood pressure measurement by telemetry, programmable infusion pumps, in vivo two-photon microscopy, and neurobehavioral tests, the authors show that this BPV model resulted in a blunted bradycardic response and cognitive deficits, enhanced myogenic response in parenchymal arterioles, and a loss of the pressure-evoked increase in functional hyperemia to whisker stimulation.

Strengths:

As the presentation of the first model of increased blood pressure variability, this manuscript establishes a method for assessing molecular mechanisms. The state-of-the-art methodology and robust data analysis provide convincing evidence that increased blood pressure variability impacts brain health.

Weaknesses:

One major drawback is that there is no comparison with another pressor agent (such as phenylephrine); therefore, it is not possible to conclude whether the observed effects are a result of increased blood pressure variability or caused by direct actions of Ang II.

We acknowledge this limitation and have attempted to address the concern by introducing an alternative vasopressor, norepinephrine (NE), Figure 4. A subcutaneous dose of 45 µg/kg/min was titrated to match Ang II-induced transient BP pulse (Systolic BP ~150-180 mmHg), Figure 4A. Similar to Ang II treated mice, NE-treated mice exhibited no significant changes in average mean arterial pressure (MAP) throughout the 20-day treatment period (Figure 4B). Although there was a trend (P=0.08) towards increased average real variability (ARV) (Figure 4C left), it did not reach statistical significance. The coefficient of variation (CV) (Figure 4C right) was significantly increased by day 3-4 of treatment (P=0.02).

Notably, unlike the bradycardic response observed during Ang II-induced BP elevations, NE infusions elicited a tachycardic response (Figure 4A), likely due to β-1 adrenergic receptor activation. However, significant mortality was observed within the NE cohort: three of six mice died prematurely during the second week of treatment, and two additional mice required euthanasia on days 18 and 20 due to lethargy, impaired mobility, and tachypnea.

While we recognize the importance of comparing results across vasopressors, further investigation using additional vasopressors would require a dedicated study, as each agent may induce distinct off-target effects, potentially generating unique animal models. Alternatively, a mechanical approach−such as implanting a tethered intra-aortic balloon[14] connected to a syringe pump−could be explored to modulate blood pressure variability without pharmacological intervention. However, such an approach falls beyond the scope of the present study.

Ang II is known to have direct actions on cerebrovascular reactivity, neuronal function, and learning and memory. Given that Ang II is increased in only 15% of human hypertensive patients (and an even lower percentage of non-hypertensive), the clinical relevance is diminished. Nonetheless, this is an important study establishing the first mouse model of increased BPV.

We agree that high Ang II levels are not a predominant cause of hypertension in humans, which is why it is critical that our pulsatile Ang II dosing did not cause overt hypertension, (no increase in 24-hour MAP). Ang II was solely a tool to produce controlled, transient increases in BP to yield a significant increase in BPV.

Regarding BPV specifically, prior studies indicate that primary hypertensive patients with elevated urinary angiotensinogen-to-creatinine ratio exhibit significantly higher mean 24-hour systolic ARV compared to those with lower ratios[15]. However, the fundamental mechanisms driving these harmful increases in BPV remain poorly defined. A central theme across clinical BPV studies is impaired arterial stiffness, which has been proposed to contribute to BPV through reduced arterial compliance and diminished baroreflex sensitivity. Moreover, increased BPV can exert mechanical stress on arterial walls, leading to arterial remodeling and stiffness−ultimately perpetuating a detrimental feed-forward cycle[16].

In our model, male BPV mice exhibited a minimal yet significant elevation in SBP without corresponding increases in DBP, potentially reflecting isolated systolic hypertension, which is strongly associated with arterial stiffness[17,18]. Our initial goal was to establish controlled rapid fluctuations in BP, and Ang II was selected as the pressor due to its potent vasoconstrictive properties and short half-life[19].

We appreciate the reviewer’s insightful comment and acknowledge the necessity of exploring alternative mechanisms underlying BPV, and independent of Ang II. It is our long-term goal to investigate these factors in further studies.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) How was the dose of Ang II determined? It seems that this dose (3.1ug/hr) is quite high.

The Ang II dose was titrated in a preliminary study to one that induced a significant and transient BP response without increasing 24-hour blood pressure (i.e. no hypertension).

Ang II was delivered subcutaneously at 3.1 μg/hr, a concentration comparable to high-dose Ang II administration via mini-osmotic pumps (~1700 ng/kg/min)[20], with one-hour pulses occurring every 3-4 hours. With 6 pulses per day, the total daily dose equates to 18.6 µg/day in a ~30 gram mouse.

For comparison, if the same 18.6 µg/day dose were administered continuously via a mini-osmotic pump (18.6 µg/0.03kg/1440min), the resulting dosage would be approximately 431 ng/kg/min[21,22], aligning with subpressor dose levels. Thus, while the total dose may appear high, it is not delivered in a constant manner but rather intermittently, allowing for controlled, rapid variations in blood pressure.

(2) Were behavioral studies performed on the same mice that were individually housed? Individual housing causes significant stress in mice that can affect learning and memory tasks (PMC6709207). It's not a huge issue since the control mice would have been housed the same way, but it is something that could be mentioned in the discussion section.

Behavioral studies were performed on mice that were individually housed following the telemetry surgery. The study was started once BP levels stabilized, as mice required several days to achieve hemodynamic stability post-surgery. Consequently, all mice were individually housed for several days before undergoing behavioral assessment.

To account for potential cognitive variability, earlier novel object recognition (NOR) tests were conducted to established cognitive capacity, and mice that did not meet criteria were excluded from further behavioral testing. However, we acknowledge that individual housing induces stress, which can influence learning and memory, and this is a factor we were unable to fully control. Given that both experimental and control groups experienced the same housing conditions, this stress effect should be comparable across cohorts. A discussion on this limitation is now included in the text.

(3) It looks like one control mouse that was included in both Figures 1 and 2 (control n=12) but was excluded in Table 1 (control n=11), this isn't mentioned in the text - please include the exclusion criteria in the manuscript.

We apologize for the typo−12 control animals were consistently utilized across Figure 1-2, Table 1, Supplemental Table 1, Figure 6C, and Supplemental Figure 2B. Since the initial submission, one control mouse was completed and included into the telemetry control cohort. Thus, in the updated manuscript, we have corrected the control sample size to 13 mice across these figures ensuring consistency.

Additionally, exclusion criteria have now been explicitly included in the manuscript (Line 173-175). Mice were excluded from the study if they died prematurely (died prior to treatment onset) or mice exhibited abnormally elevated pressure while receiving saline, likely due to complications from telemetry surgery.

(4) Please include a statement on why female mice were not included in this study.

As discussed in our response to Reviewer #1, our initial intention was to include both male and female mice in this study. However, high mortality rates following telemetry surgeries significantly constrained our ability to advance all aspects of the study. As a result, we limited our first cohort to males to establish the basics of the model. A statement is now included in the manuscript, Line 50-53: “Female mice were not included in the present study due to high post-surgery mortality observed in 12-14-month-old mice following complex procedures. To minimized confounding effects of differential survival and to establish foundational data for this model, we restricted the investigation to male mice.”

Potential sex differences might be complex and warrants a separate future research to comprehensively assess sex as a biological variable, which are currently ongoing.

(5) On page 14, "experiments from control vs experimental mice were not equally conducted in the same season raising the possibility for a seasonal effect" - does this mean that control experiments were not conducted at the same time as the Ang II infusions in BPV mice? This has huge implications on whether the effects observed are induced by treatment or just batch seasonal effects.

We fully acknowledge the reviewer’s concern, and our statement aims to provide transparency regarding the study’s limitations. Several challenges contributed to this outcome, including high mortality rates following surgeries (primarily telemetry implantation) and technical issues related to instrumentation, particularly telemetry functionality.

Differences between BPV and saline mice emerge primarily due to mortality or telemetry failures−some mice did not survive post-surgery, while others remain healthy but had non-functional telemeters. This issue was particularly pronounced in 14-month-old mice, as their fragile vasculature occasionally prevented proper BP readings.

Each experiment required a minimum of two and a half months per mouse to complete, with a cost (also per mouse) exceeding $1500 USD ($300 pump, $175 mouse, $900 telemeters, per diem, drugs, reagents etc.). Despite our best effort to ensure comparable seasonal/batch data, these logistical and technical constraints prevented perfect synchronization.

To evaluate whether seasonal differences influenced our results, we incorporated additional telemetry data into the control cohort. Of the seven included control mice, six underwent the same treatment but were allocated to a separate branch of the study, which endpoints did not require a chronic cranial window. We found no significant differences in 24-hour average MAP during the baseline period between control mice with or without a cranial window, Supplemental Figure 2A. Additionally, we grouped mice into seasonal categories based on Georgia’s climate: “Spring-Summer” (May-September) and “Fall-Winter” (October-April) but observed no BP differences between these periods, Supplemental Figure 2B.

Given the absence of seasonal effects on BP and the fact that mice were sourced from two independent suppliers (Jackson Laboratory and NIA), we anticipate that the observed results are driven by treatment rather than seasonal or batch effects.

(6) Methods, two-photon imaging: did the authors mean "retro-orbital" instead of "intra-orbital" injection of the Texas red dye? Also, is this a Texas red-dextran? If so, what molecular weight?

Thank you for this comment. The correct terminology is “retro-orbital” rather than “intra-orbital” injection. Additionally, we utilized Texas Red-dextran (70 kDa, 5% [wt/vol] in saline) for the imaging experiments. These details have now been incorporated into the Methods section.

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eLife Assessment

This study offers a valuable contribution to our understanding of the role of layer 6b cortical neurons in sleep-wake regulation, providing new insight into how this understudied neural population may regulate cortical arousal via orexin signaling. The evidence supporting these findings is solid, although somewhat constrained by limitations in the specificity of the genetic targeting strategy. Nonetheless, the work introduces new avenues for uncovering how the classical wake-promoting peptide, orexin, exerts its effects on the cortex.

Reviewer #1 (Public review):

Summary:

Meijer et al. sought to investigate the role of cortical layer 6b (L6b) neurons in modulating sleep-wake states and cortical oscillations under baseline and sleep deprived conditions and in response to orexin A and B. Using chronic EEG recordings in mice with silencing of Drd1a+ neurons (via constitutive Cre-dependent knockout of SNAP25), the authors report that while overall baseline sleep-wake architecture and response to sleep deprivation minimal/unchanged, "L6b silencing" leads to a slowing of theta activity during wakefulness and REM sleep, and a reduction in EEG power during NREM sleep. Additionally, orexin B-induced increases in theta activity were attenuated in L6b silenced mice, which the authors state suggests a modulatory role for L6b in orexin-mediated arousal regulation. The manuscript is generally well written with clarity and transparency. However, a major concern is the lack of specificity in the genetic manipulation, which targets Drd1a+ neurons not exclusive to L6b, undermining the attribution of observed effects solely to L6b. Verification of neuronal silencing is also unclear, and statistical inconsistencies between the main text and figures/tables make it difficult to effectively evaluate the text and stated outcomes.

Strengths:

(1) The text is well written.

(2) The authors are transparent about methodological details.

(3) The stated sleep, circadian, and orexin infusion experiments appear to be well designed, executed, and analyzed (with the exceptions of some statistical analyses detailed below).

Weaknesses:

(1) All outcomes are attributed specifically to L6b neurons, but the genetic manipulation is not specific to L6b neurons. The authors acknowledge this as a limitation, but in my view, this global manipulation is more than a limitation - it affects the overall interpretations of the data. The Hoerder-Suabedissen et al., 2018 paper shows sparse, but also dense, expression of Drd1a+ neurons in brain regions outside of the L6b. Given this issue, the results are largely overstated throughout the paper.

(2) It is not clear to me that the "silencing" of Drd1a+ neurons was verified.

(3) There were various discrepancies (and potentially misattributions) between the stated significant differences in Supplementary Table T1 data and Figure 3a & S2 spectral plots. This issue makes it difficult to effectively evaluate the main text and stated outcomes.

Related, the authors stated that post hoc comparisons of EEG spectral frequency bins were not corrected for multiple testing. Instead, significance was only denoted if changes in at least two consecutive frequency bins were significant. However, there are multiple plots in which a single significance marker is placed over an isolated bin (i.e., 4c, 6, S5, S6). Unless each marker is equivalent to 2 consecutive frequency bins, these markers should be removed from the plots. Otherwise, please define the frequency and size of these markers in the main text.

(4) A rainbow color scale, as in Figure 3, we've now learned, can be misleading and difficult to interpret. The viridis color scale or a different diverging color scale are good alternatives.

(5) How much time elapsed between vehicle/orexin A & B infusions?

(6) For Figure 6, there are statistical discrepancies between the main text and the plots (pg. 10):

a) The text claims post hoc differences for relative ORXA frontal EEG, but there are no significance markers on the plot.<br /> b) The text states that there were no post hoc differences for the relative ORXA occipital EEG, but significance markers are on the plot.<br /> c) The main test for the relative ORXB frontal EEG was not significant, but there are post hoc significance markers on the plot.<br /> d) For relative ORXB occipital EEG, there are significant markers on the plot outside of the stated range in the text.

(7) Some important details are only available in figure captions, making it difficult to understand the main text. For example, when describing Figure 3c in the main text on page 7, it is not clear what type of transitions are being discussed without reading the figure caption. Likewise, a "decrease," "shift," and "change" are mentioned, but relative to what? Similar comment for the EEG theta activity description on pages 7 - 8. Please add relevant details to the main text.

(8) Statistical comparisons for data in Figure 3e, post hoc analyses for data in Figure S7a-b REM data, and post hoc analyses for Figure S7c (not b) occipital EEG should be included to support differences claims. Please denote these differences on the respective plots.

(9) In the subsection titled "Layer 6b mediates effects of orexin on vigilance states (pg. 8)," there does not seem to be any stated differences between control and L6b silenced mice. A more accurate subtitle is needed.

Reviewer #2 (Public review):

Summary:

In this manuscript, Meijer and colleagues investigated the effects of inactivation (conditional silencing) of cortical layer 6b neurons on sleep-wake states and EEG spectral power under the following three conditions: during natural sleep-wake states, after sleep deprivation, or after intracerebroventricular administration of orexin A and B. The authors report that silencing of L6b neurons did not have a significant effect on the total time spent in sleep-wake states, duration, or number of state epochs, or the response to sleep deprivation. However, silencing of L6b neurons did slow down theta-frequency (6-9 Hz) during wake and REM sleep, and reduced the total EEG power during NREM sleep. Infusion of orexin A in the mice in which cortical layer 6b neurons were inactivated produced an increase in wakefulness. A similar effect was observed after infusion of orexin A in the mice in which these neurons were not silenced, but the effect (i.e., increase in wakefulness) was of a smaller magnitude. Silencing of cortical layer 6b neurons attenuated the effect of orexin B in increasing theta activity, as was observed in the control mice. The authors conclude that the cortical neurons in layer 6b play an essential role in state-dependent dynamics of brain activity, vigilance state control, and sleep regulation.

Strengths:

(1) A focus on cortical layer 6b neurons, which are an understudied neuronal population, especially in the context of brain and behavioral state transitions.

(2) The authors used a well-established mouse model to study the effect of inactivation of cortical layer 6b neurons.

Weaknesses:

(1) Although the authors used a highly selective approach to silence layer 6b neurons, the observed changes in EEG oscillations cannot be solely attributed to layer 6b neurons because of the ICV route for orexin administration.

(2) The rationale for using only male rats is not provided.

Author response:

Public Reviews:

Reviewer #1 (Public review):

(1) All outcomes are attributed specifically to L6b neurons, but the genetic manipulation is not specific to L6b neurons. The authors acknowledge this as a limitation, but in my view, this global manipulation is more than a limitation - it affects the overall interpretations of the data. The Hoerder-Suabedissen et al., 2018 paper shows sparse, but also dense, expression of Drd1a+ neurons in brain regions outside of the L6b. Given this issue, the results are largely overstated throughout the paper.

We appreciate the reviewer’s careful reading and concern that some of our statements may have overstated the implications of our data. The Drd1a Cre mouse model used (FK164) has a relatively selective expression of Drd1a Cre in cortex, especially in layer 6b, but indeed some expression is seen in layer 6a and subcortically. We will nuance our claims throughout the paper to ensure that the conclusions are supported by our findings, and further discuss the impact of this limitation on the overall interpretation of our results. Specifically, we will discuss the potential contribution of relevant subcortical areas and layer 6a in the effects we observed.

(2) It is not clear to me that the "silencing" of Drd1a+ neurons was verified.

In our previous publications, we showed confirmation of the loss of regulated synaptic vesicle release from the Cre positive neuronal population (Marques-Smith et al., 2016; Hoerder-Suabedissen et al., 2018; Messore et al., 2024), which validates our approach to “silence” cortical neurons. We will discuss this further in the revised manuscript.

(3) There were various discrepancies (and potentially misattributions) between the stated significant differences in Supplementary Table T1 data and Figure 3a & S2 spectral plots. This issue makes it difficult to effectively evaluate the main text and stated outcomes.

We thank the reviewer for spotting the inconsistencies in how the statistical comparisons were presented: indeed, in the text we described two-way ANOVAs with posthoc tests but in the figures significance markers were positioned based on multiple t-tests. We have revised Supplementary Table T1, Figure 3a and S2 to ensure that all statistics are presented consistently throughout the manuscript, i.e. with two-way ANOVAs and accompanying posthoc tests.

Related, the authors stated that post hoc comparisons of EEG spectral frequency bins were not corrected for multiple testing. Instead, significance was only denoted if changes in at least two consecutive frequency bins were significant. However, there are multiple plots in which a single significance marker is placed over an isolated bin (i.e., 4c, 6, S5, S6). Unless each marker is equivalent to 2 consecutive frequency bins, these markers should be removed from the plots. Otherwise, please define the frequency and size of these markers in the main text.

In line with the previous comment, we have adjusted markers to reflect the results from posthoc tests after two-way ANOVAs in Figures 6 and supplementary figures S5 and S6. 

We thank the reviewer for pointing out that in our comparisons of EEG spectra, in some cases single isolated frequency bins, where p-value reached 0.05 were shown as significantly different, which indeed could have occurred by chance given that, in line with previous literature, we have not employed multiple testing comparison. In the revised manuscript we will use an unbiased approach by plotting actual p-values for all bins, and moderate our conclusions accordingly, while giving the readers the opportunity to evaluate the magnitude and extent of the differences directly, rather than relying on an arbitrary threshold for significance.

(4) A rainbow color scale, as in Figure 3, we've now learned, can be misleading and difficult to interpret. The viridis color scale or a different diverging color scale are good alternatives.

Thank you for pointing this out, we have adjusted the colour scale.

(5) How much time elapsed between vehicle/orexin A & B infusions?

There were 2-4 non-infusions days between infusions. We will add this information to methods when revising the manuscript.

(6) For Figure 6, there are statistical discrepancies between the main text and the plots (pg. 10):

a) The text claims post hoc differences for relative ORXA frontal EEG, but there are no significance markers on the plot.

b) The text states that there were no post hoc differences for the relative ORXA occipital EEG, but significance markers are on the plot.

c) The main test for the relative ORXB frontal EEG was not significant, but there are post hoc significance markers on the plot.

d) For relative ORXB occipital EEG, there are significant markers on the plot outside of the stated range in the text.

Thank you for your careful observations, these issues reflect the same inconsistency as raise above, where the text describes two-way ANOVAs and the figures refers to results obtained with multiple t tests. We shall adjust the markers in the figures to be only shown when the ANOVA is significant and show the results of posthoc tests after ANOVAs instead of the results of multiple t tests.

(7) Some important details are only available in figure captions, making it difficult to understand the main text. For example, when describing Figure 3c in the main text on page 7, it is not clear what type of transitions are being discussed without reading the figure caption. Likewise, a "decrease," "shift," and "change" are mentioned, but relative to what? Similar comment for the EEG theta activity description on pages 7 - 8. Please add relevant details to the main text.

We will adjust the wording in the main text to reflect more precisely which comparisons are shown in the figures.

(8) Statistical comparisons for data in Figure 3e, post hoc analyses for data in Figure S7a-b REM data, and post hoc analyses for Figure S7c (not b) occipital EEG should be included to support differences claims. Please denote these differences on the respective plots.

We have added the statistical comparisons for Figure 3e to the results section.

We have added the statistical comparisons for Figure S7A to the results section.

We have added the statistical comparison for Figure S7b to the results section.

In Figure S7c, there was an overall genotype difference, but there was not a time x genotype interaction, so we have not performed posthoc tests and did not plot posthoc significance markers for this figure. We have adjusted the wording in the results section to make this clearer.

We have adjusted the reference to the figure S7c which was incorrect, thank you for your careful attention.

(9) In the subsection titled "Layer 6b mediates effects of orexin on vigilance states (pg. 8)," there does not seem to be any stated differences between control and L6b silenced mice. A more accurate subtitle is needed.

We shall change the subtitle to: “The effects of orexin on vigilance states in L6b silenced mice”. The main finding described in this section is that the increase in EEG theta frequency after ORXB infusion is attenuated in L6b silenced mice, so a statement summarizing this finding could be an alternative title. However, then it would not accurately reflect other, less conspicuous, yet potentially important findings described in this section (during NREM sleep, only in L6b silenced animals there is an increase in power in the lower frequency bins in the frontal derivation; in the occipital derivation, levels of relative SWA during NREM sleep after ORXA infusion were lower in L6b silenced than in control animals).

Reviewer #2 (Public review):

Weaknesses:

(1) Although the authors used a highly selective approach to silence layer 6b neurons, the observed changes in EEG oscillations cannot be solely attributed to layer 6b neurons because of the ICV route for orexin administration.

We completely agree, and did not want to imply that orexin administered through the ICV route reaches cortical Drd1a Cre expressing neurons only. We will re-word the corresponding sentences accordingly throughout the manuscript.

(2) The rationale for using only male rats is not provided.

We agree that this is an important limitation and will acknowledge and discuss it further in the revised manuscript. Unfortunately, our experimental protocol precluded the possibility of monitoring accurately the oestrous cycle, which as well-known has an influence on sleep-wake architecture, brain oscillations as well as orexin signalling and receptor abundance. We therefore decided to use male mice only for the current study, but planning to use both sexes in our follow up work.

eLife Assessment

In this valuable study, the authors use a cutting-edge method to perform voltage imaging of CA1 pyramidal cells in head-fixed mice running on a track while local field potentials (LFPs) were recorded in the contralateral hemisphere. The authors provide solid evidence of synchronous ensembles of CA1 pyramidal neurons that are associated with contralaterally recorded theta rhythms but not with contralaterally recorded sharp wave-ripples during exploration of a novel environment. The paper will be of interest to scientists who are interested in hippocampal neuronal coding of novel environments, particularly those with experimental questions that can benefit from this cutting-edge imaging technique.

Joint Public Review:

Summary:

There has been extensive electrophysiological research investigating the relationship between local field potential patterns and individual cell spike patterns in the hippocampus. In this study, the authors used innovative imaging techniques to examine spike synchrony of hippocampal cells during locomotion and immobility states. The authors report that hippocampal place cells exhibit prominent synchronous spikes that co-occur with theta oscillations during exploration of novel environments.

Strengths:

The single cell voltage imaging used in this study is a highly novel method that may allow recordings that were not previously possible using traditional methods.

Weaknesses:

Local field potential recordings were obtained from the contralateral hemisphere for technical reasons, which limits some of the study's claims.

Author response:

The following is the authors’ response to the previous reviews

Joint Public Review:

Summary:

For many years, there has been extensive electrophysiological research investigating the relationship between local field potential patterns and individual cell spike patterns in the hippocampus. In this study, using innovative imaging techniques, they examined spike synchrony of hippocampal cells during locomotion and immobility states. The authors demonstrated that hippocampal place cells exhibit prominent synchronous spikes locked to theta oscillations.

Strengths:

The single cell voltage imaging used in this study is a highly novel method that may allow recordings that were not previously possible using existing methods.

We thank the reviewer for recognizing the strengths of our study.

Weaknesses:

The strength of evidence remains incomplete because of the main claim that synchronous events are not associated with ripples. As was mentioned in previous rounds of review, ripples emerge locally and independently in the two hemispheres. Thus, obtaining ripple recordings from the contralateral hemisphere does not provide solid evidence for this claim. The papers the authors are citing to make the claim that "Additionally, we implanted electrodes in the contralateral CA1 region to monitor theta and ripple oscillations, which are known to co-occur across hemispheres (29-31)" do not support this claim. For example, reference 29 contains the following statement: "These findings suggest that ripples emerge locally and independently in the two hemispheres".

In our previous revisions, we took care to limit our claim to what our data directly supported: that synchronous ensembles of CA1 neurons were not associated with ripple oscillations recorded in the contralateral hippocampus. To address reviewer concerns, we changed the Title, modified the Abstract, adjusted relevant text in the Results, and explicitly acknowledged the methodological limitations in the Discussion. 

In this round, we further revised the manuscript to directly address the editor’s and reviewer’s remaining concerns: 

(1) We replaced the word “surprisingly” with a more neutral “Moreover” to avoid implying that the observed dissociation was unexpected given the use of contralateral recordings.

Introduction (line 67-69):

“Moreover, these synchronous ensembles occurred outside of contralateral ripples (c-ripples) …”

(2) We removed the clause stating that ripples “co-occur across hemispheres”, along with the associated citation to Buzsaki et al. (2003), to avoid potential misinterpretation. The sentence now simply states that we recorded ripple and theta oscillations in the contralateral CA1.

Introduction (line 63-64):

“Additionally, we implanted electrodes in the contralateral CA1 region to monitor theta and ripple oscillations.” (co-occurrence claim removed)

(3) We carefully replaced all mentions of “ripples” in the manuscript with “c-ripples” (i.e., contralateral ripples) to ensure that the scope of our findings is clearly defined and cannot be misinterpreted.

(4) We strengthened the acknowledgment of the methodological limitations in the Discussion. 

Discussion (line 528-533): 

“While contralateral LFP recordings can capture large-scale hippocampal theta and ripple oscillations, they do not fully reflect ipsilateral-specific dynamics, such as variation in theta phase alignment or locally generated ripple events (Buzsaki et al., 2003; Szabo et al., 2022; Huang et al., 2024). Given that ripple oscillations can emerge locally and independently in each hemisphere, interpretations based on contralateral recordings must be made with caution. Further studies incorporating simultaneous ipsilateral field potential recordings will be essential to more precisely understand local-global network interactions.”

These revisions ensure that our manuscript now presents a consistent and appropriately limited interpretation across all sections. We hope these clarifications address all remaining concerns and accurately reflect the scope of our findings.

eLife Assessment

This paper reports a valuable discovery that specific-mode electroacupuncture (EA) transiently opens the blood-brain barrier (BBB) in rats. The evidence is solid but lacks functional validation of BBB permeability changes. The work will be of interest to medical scientists working in the field of electroacupuncture and drug delivery.

Reviewer #1 (Public review):

Summary:

The work from this paper successfully mapped transcriptional landscape and identified EA-responsive cell types (endothelial, microglia). Data suggest EA modulates BBB via immune pathways and cell communication. However, claims of "BBB opening" are not directly proven (no permeability data).

Strengths:

First scRNA-seq atlas of EA effects on BBB, revealing 23 cell clusters and 8 cell types. High cell throughput (98,338 cells), doublet removal, and robust clustering (Seurat, SingleR). Comprehensive bioinformatics (GO/KEGG, CellPhoneDB for ligand-receptor interactions). Raw data were deposited in GEO (GSE272895) and can be accessed.

Weaknesses:

(1) No in vivo/in vitro assays confirm BBB permeability changes (e.g., Evans blue leakage, TEER).

(2) Only male rats were used, ignoring sex-specific BBB differences.

(3) Pericytes and neurons, critical for the BBB, were not captured, likely due to dissociation artifacts.

(4) Protein-level validation (Western blot, IHC) absent for key genes (e.g., LY6E, HSP90).

(5) Fixed stimulation protocol (2/100 Hz, 40 min); no dose-response or temporal analysis.

Reviewer #2 (Public review):

Summary:

This study uses single-cell RNA sequencing to explore how electroacupuncture (EA) stimulation alters the brain's cellular and molecular landscape after blood-brain barrier (BBB) opening. The authors aim to identify changes in gene expression and signaling pathways across brain cell types in response to EA stimulation using single-cell RNA sequencing. This direction holds promise for understanding the consequences of noninvasive methods of BBB opening for therapeutic drug delivery across the BBB.

Strengths:

(1) The study addresses an emerging and potentially important application of noninvasive stimulation methods to manipulate BBB permeability.

(2) The dataset provides broad transcriptional profiling across multiple brain cell types using single-cell resolution, which could serve as a valuable community resource.

(3) Analyses of receptor-ligand signaling and cell-cell communication are included and have the potential to offer mechanistic insight into BBB regulation.

Weaknesses:

(1) The work falls short in its current form. The experimental design lacks a clear justification, and readers are not provided with sufficient background information on the extent, timing, or regional specificity of BBB opening in this EA model. These details, established in prior work, are critical to understanding the rationale behind the current transcriptomic analyses.

(2) Further, the results are often presented with minimal context or interpretation. There is no model of intercellular or molecular coordination to explain the BBB-opening process, despite the stated goal of identifying such mechanisms. The statement that EA induces a "unique frontal cortex-specific transcriptome signature" is not supported, as no data from other brain regions are presented. Biological interpretation is at times unclear or inaccurate - for instance, attributing astrocyte migration effects to endothelial cell clusters or suggesting microglial tight junction changes without connecting them meaningfully to endothelial function.

(3) The study does include analyses of receptor-ligand signaling and cell-cell communication, which could be among its most biologically rich outputs. However, these are relegated to supplementary material and not shown in the leading figures. This choice limits the utility of the manuscript as a hypothesis-generating resource.

(4) Overall, while the dataset may be of interest to BBB researchers and those developing technologies for drug delivery across the BBB, the manuscript in its current form does not yet fulfill its interpretive goals. A more integrated and biologically grounded analysis would be beneficial.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The work from this paper successfully mapped transcriptional landscape and identified EA-responsive cell types (endothelial, microglia). Data suggest EA modulates BBB via immune pathways and cell communication. However, claims of "BBB opening" are not directly proven (no permeability data).

(1) No in vivo/in vitro assays confirm BBB permeability changes (e.g., Evans blue leakage, TEER).  

(2) Only male rats were used, ignoring sex-specific BBB differences.

(3) Pericytes and neurons, critical for the BBB, were not captured, likely due to dissociation artifacts.

(4) Protein-level validation (Western blot, IHC) absent for key genes (e.g., LY6E, HSP90).

(5) Fixed stimulation protocol (2/100 Hz, 40 min); no dose-response or temporal analysis.

(1) We sincerely apologize for the oversight regarding the description of changes in blood-brain barrier permeability. In fact, our team conducted a series of preliminary studies that verified this aspect, but we did not provide a more detailed introduction in the introduction section. We will address and improve this in the revised manuscript. (2) We are very grateful to the reviewers for pointing out the important and meaningful issue of "gender-specific BBB differences." We will make this a focal point in our future research.

(2) As for pericytes and neurons, we acknowledge their importance in the function of the blood-brain barrier. We acknowledge the importance of pericytes and neurons in the blood-brain barrier. However, neurons are absent because our sample processing method involves dissociation. During the dissociation procedure, neuronal axons, which are relatively long, are filtered out during the frequent cell suspension steps and cannot enter the downstream microfluidic system for analysis, so they are not present in our data. Since this experiment is primarily focused on non-neuronal cells, we did not choose to use nucleus extraction for sample processing. As for pericytes, we believe they are not captured because their proportion in our samples is extremely low, which is why they are not present in the data. Further research may require single-nucleus transcriptomics or the separate isolation of these two cell types for study. Of course, in our current mechanistic studies, we are also fully considering the important roles these two cell types play in BBB function.

(3) In addition, for verification at the protein level, we have recently conducted some experiments and will include these results in the revised version.

(5) Lastly, regarding our electroacupuncture intervention model, we actually conducted a series of parameter optimization experiments during the preliminary exploration phase. This part is indeed lacking in our current introduction, and we will add it to the research background and introduction.

Reviewer #2 (Public review):

Summary:

This study uses single-cell RNA sequencing to explore how electroacupuncture (EA) stimulation alters the brain's cellular and molecular landscape after blood-brain barrier (BBB) opening. The authors aim to identify changes in gene expression and signaling pathways across brain cell types in response to EA stimulation using single-cell RNA sequencing. This direction holds promise for understanding the consequences of noninvasive methods of BBB opening for therapeutic drug delivery across the BBB.

(1) The work falls short in its current form. The experimental design lacks a clear justification, and readers are not provided with sufficient background information on the extent, timing, or regional specificity of BBB opening in this EA model. These details, established in prior work, are critical to understanding the rationale behind the current transcriptomic analyses.

(2) Further, the results are often presented with minimal context or interpretation. There is no model of intercellular or molecular coordination to explain the BBB-opening process, despite the stated goal of identifying such mechanisms. The statement that EA induces a "unique frontal cortex-specific transcriptome signature" is not supported, as no data from other brain regions are presented. Biological interpretation is at times unclear or inaccurate - for instance, attributing astrocyte migration effects to endothelial cell clusters or suggesting microglial tight junction changes without connecting them meaningfully to endothelial function.<br /> (3) The study does include analyses of receptor-ligand signaling and cell-cell communication, which could be among its most biologically rich outputs. However, these are relegated to supplementary material and not shown in the leading figures. This choice limits the utility of the manuscript as a hypothesis-generating resource.

(4) Overall, while the dataset may be of interest to BBB researchers and those developing technologies for drug delivery across the BBB, the manuscript in its current form does not yet fulfill its interpretive goals. A more integrated and biologically grounded analysis would be beneficial.

(1) It was indeed our mistake that we did not pay attention to the importance of research background factors such as the degree, timing, or regional specificity of BBB opening for the rationale and purpose of this experimental design. In our revision, we will thoroughly elaborate on the relevant previous studies.

(2) Our current study is actually based on previous findings that electroacupuncture can open the BBB, with a more pronounced effect observed in the frontal lobe (this aspect should be further described in the research background). Building on this foundation, our aim is to delineate the potential biological mechanisms involved. Therefore, we selected frontal lobe tissue as our primary choice for sequencing and have not yet investigated differences across other brain regions, although this may become a focus of future research. Additionally, we recognize that the mechanism underlying BBB opening is complex, and at present, we cannot determine whether it is driven by a single direct factor or by coordinated actions between cells or molecules. As such, our results are presented only briefly for now, and we will carefully consider whether to supplement our findings by incorporating insights from other studies.

(3) Thank you very much for bringing this to our attention. We will include the key results of the receptor-ligand signaling and cell-cell communication analysis in the main manuscript.

(4) Indeed, our current dataset and analysis tend to present objective data results. We are also conducting a series of validations that may be related to the biology of the blood-brain barrier, and we look forward to sharing and discussing any future research findings with you and everyone.

eLife Assessment

This study presents valuable computational findings on the neural basis of learning new motor memories without interfering with previously learned behaviours using recurrent neural networks. The evidence supporting the claims of the authors is solid, but it would benefit from stronger and clearer links with experimental findings. This work will be of interest to computational and experimental neuroscientists working in motor learning.

Reviewer #1 (Public review):

Summary:

This work investigates the neural basis of continual motor learning, specifically how brains might accommodate new motor memories without interfering with previously learned behaviours. Mainly drawing inspiration from recent experimental studies in monkeys (Losey et al. and Sun, O'Shea et al.), the authors use recurrent neural networks (RNNs) to model sequential learning and examine the emergence and properties of two proposed neural signatures of motor memory: the "uniform shift" observed in preparatory activity and the "memory trace" observed in execution activity.

Strengths:

The work's main contribution is demonstrating that both uniform shifts and memory traces emerge in RNN models trained on a sequential BCI task, without requiring explicit additional mechanisms. The work explores the relationship between these signatures and behavioural savings, finding that the memory trace correlates with immediate retention savings in networks without context, while the uniform shift does not. The study also investigates how properties of the new task perturbation (within- vs. outside-manifold) and the presence of explicit context cues affect these signatures and their relationship to savings, generally finding that context signals and outside-manifold perturbations reduce savings by decreasing the inherent overlap in the neural strategies used to solve the task.

Weaknesses:

A primary weakness is the lack of clear definitions of the uniform shift and the memory trace, which are quite different metrics. Another primary weakness is that the task modelled is well-matched to the Losey et al. BCI paradigm, but not well-matched to the Sun, O'Shea et al.'s curl field paradigm, which is likely impacting some of the results, primarily the lack of a relationship between the uniform shift and motor memories. While there are improvements that could be made in this work, we think it is a demonstration that modeling learning in neural activity using neural network models continues to be a valuable tool, moving the field forward.

Reviewer #2 (Public review):

Summary:

Chang et al. develop an RNN model of a BCI sequential learning task to examine the emergence of motor memory in the network. They use this system to quantify signatures of memory in continual learning, comparing their model with experimental observations from monkeys in prior publications. They show that the RNN model has signatures of shifts associated with sequential learning without any non-standard learning rules. This convincing study contributes to the knowledge of how motor memories are formed and shaped so that they are flexible in acquiring multiple behaviors.

Strengths:

This paper describes a well-designed numerical experiment that comes to a clear interpretation of a set of neural BCI experiments. The learning signatures the authors describe are interesting and well laid out, and the paper is well written. I find it insightful that the neural signature of motor learning emerges in a trained network without special learning rules.

Weaknesses:

The paper could be stronger if it made a stronger interpretation of how memory traces and uniform shifts are related. These two observations are taken from the BCI sequential learning literature and introduced by two different prior experimental papers on two different tasks, so it seems like there is an opportunity here to use the RNN model to unite these concepts, or define another metric for signatures of learning from a more normative approach.

Reviewer #3 (Public review):

Summary:

The authors build and analyze recurrent neural network (RNN) models of brain-computer interface (BCI) multi-task learning, developing a valuable theoretical understanding of learning-related neural population phenomena ("memory traces" and "uniform shifts") that have been reported in recent experimental studies of BCI and motor learning. The authors find that both phenomena emerge in their RNN models, and both correlate in some manner to learning-related behavioral phenomena ("savings" and "forgetting"). The authors also reveal that RNN training details, in particular, incorporating a task-indicating contextual input, can impact these population-level signatures of learning in RNN activity and their relation to those behavioral phenomena.

Strengths:

The text is well written, and the figures are clearly composed to convey the core concepts and findings. The RNN studies are elegant in their ability to recapitulate the memory trace and uniform shift phenomena, and further allow evaluations of novel scenarios that were not tested in the original corpus of the modeled animal experiments. The authors assess the sensitivity of their results to multiple approaches to RNN training, including training connectivity within a model of motor cortex, training only an upstream model that provides inputs to the motor cortex model, and providing task-indicating contextual inputs.

Weaknesses:

(1) It is unclear to what extent these RNN models operate in regimes relevant to biological neural networks (e.g., motor cortex), even at the neural-population level of abstraction studied here. Can the authors speak to how sensitive their results are to details that might speak to these operating regimes (e.g., signal-to-noise ratios or dimensionality of the RNN activities)?

(2) The work could be further strengthened by analyses demonstrating a more direct link between the neural population phenomena (memory trace and uniform shift) and the behavioral phenomena (savings, forgetting, etc). While in animal experiments, it can be exceedingly difficult to demonstrate links beyond correlative effects, the promise of a model is the relative tractability of implementing manipulations that might establish something closer to a causal link between phenomena. Is it the case that the memory trace is a task-dependent, mean-preserving rotation of the across-target task-relevant activity space? And that the uniform shift is a translation (non-mean-preserving) of that space? If so, could the authors design regularization schemes that specifically target each of these effects, enabling a more direct test of the functional role the effects play in driving behavioral phenomena?

Minor Comments:

The current study is based on BCI learning of center-out tasks, analogous to the Losey et al. task that initially reported the memory trace phenomena. However, a rather different behavioral task - involving arm movements through curl force fields - was employed by the Sun, O'Shea, et al. study that originally reported the uniform shift phenomena. How should readers interpret the current study's findings related to the uniform shift? To what extent might the behavioral implications of the uniform shift depend on the demands of the task, e.g., the biomechanics, day-to-day experiencing of different curl-field perturbations, etc.?

Author response:

We thank the reviewers for their thoughtful comments, and we plan to implement many of their suggestions to improve the paper. We agree that the paper can benefit from clearer links between the two neural signatures (memory traces and uniform shifts) themselves, and between the neural signatures and behavioral phenomena. We will address these limitations in multiple ways. First, as the reviewers noted, RNN models have the potential to probe these relationships, so we plan to perform further analyses and modeling experiments to uncover any causal relationships. Second, we will also establish clearer definitions of the neural signatures and explore how these signatures can be unified using our models. Finally, we will compare the experimental paradigms between Losey et al and Sun, O’Shea et al, and discuss how differences between the paradigms may have impacted our observations, particularly in the context of other experimental and modeling papers.

eLife Assessment

This important study introduces the Life Identification Number (LIN) coding system as a powerful and versatile approach for classifying Neisseria gonorrhoeae lineages. The authors show that LIN codes capture both previously defined lineages and their relationships in a way that aligns with the species' phylogenetic structure. The compelling evidence presented, together with its integration into the PubMLST platform, underscores its strong potential to enhance epidemiological surveillance and advance our understanding of gonococcal population biology.

Reviewer #1 (Public review):

Summary:

Bacterial species that frequently undergo horizontal gene transfer events tend to have genomes that approach linkage equilibrium, making it challenging to analyze population structure and establish the relationships between isolates. To overcome this problem, researchers have established several effective schemes for analyzing N. gonorrhoeae isolates, including MLST and NG-STAR. This report shows that Life Identification Number (LIN) Codes provide for a robust and improved discrimination between different N. gonorrhoeae isolates.

Strengths:

The description of the system is clear, the analysis is convincing, and the comparisons to other methods show the improvements offered by LIN Codes.

Weaknesses:

No major weaknesses were identified by this reviewer.

Reviewer #2 (Public review):

Summary:

This paper describes a new approach for analyzing genome sequences.

Strengths:

The work was performed with great rigor and provides much greater insights than earlier classification systems.

Weaknesses:

A minor weakness is that the clinical application of LIN coding could be articulated in a more in-depth way. The LIN coding system is very impressive and is certainly superior to other protocols. My recommendation, although not necessary for this paper, is that the authors expand their analysis to noncoding sequences, especially those upstream of open reading frames. In this respect, important cis-acting regulatory mutations that might help to further distinguish strains could be identified.

Reviewer #3 (Public review):

Summary:

In this well-written manuscript, Unitt and colleagues propose a new, hierarchical nomenclature system for the pathogen Neisseria gonorrhoeae. The proposed nomenclature addresses a longstanding problem in N. gonorrhoeae genomics, namely that the highly recombinant population complicates typing schemes based on only a few loci and that previous typing systems, even those based on the core genome, group strains at only one level of genomic divergence without a system for clustering sequence types together. In this work, the authors have revised the core genome MLST scheme for N. gonorrhoeae and devised life identification numbers (LIN) codes to describe the N. gonorrhoeae population structure.

Strengths:

The LIN codes proposed in this manuscript are congruent with previous typing methods for Neisseria gonorrhoeae, like cgMLST groups, Ng-STAR, and NG-MAST. Importantly, they improve upon many of these methods as the LIN codes are also congruent with the phylogeny and represent monophyletic lineages/sublineages.

The LIN code assignment has been implemented in PubMLST, allowing other researchers to assign LIN codes to new assemblies and put genomes of interest in context with global datasets.

Weaknesses:

The authors correctly highlight that cgMLST-based clusters can be fused due to "intermediate isolates" generated through processes like horizontal gene transfer. However, the LIN codes proposed here are also based on single linkage clustering of cgMLST at multiple levels. It is unclear if future recombination or sequencing of previously unsampled diversity within N. gonorrhoeae merges together higher-level clusters, and if so, how this will impact the stability of the nomenclature.

The authors have defined higher resolution thresholds for the LIN code scheme. However, they do not investigate how these levels correspond to previously identified transmission clusters from genomic epidemiology studies. It would be useful for future users of the scheme to know the relevant LIN code thresholds for these investigations.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

Bacterial species that frequently undergo horizontal gene transfer events tend to have genomes that approach linkage equilibrium, making it challenging to analyze population structure and establish the relationships between isolates. To overcome this problem, researchers have established several effective schemes for analyzing N. gonorrhoeae isolates, including MLST and NG-STAR. This report shows that Life Identification Number (LIN) Codes provide for a robust and improved discrimination between different N. gonorrhoeae isolates.

Strengths:

The description of the system is clear, the analysis is convincing, and the comparisons to other methods show the improvements offered by LIN Codes.

Weaknesses:

No major weaknesses were identified by this reviewer.

We thank the reviewer for their assessment of our paper.

Reviewer #2 (Public review):

Summary:

This paper describes a new approach for analyzing genome sequences.

Strengths:

The work was performed with great rigor and provides much greater insights than earlier classification systems.

Weaknesses:

A minor weakness is that the clinical application of LIN coding could be articulated in a more in-depth way. The LIN coding system is very impressive and is certainly superior to other protocols. My recommendation, although not necessary for this paper, is that the authors expand their analysis to noncoding sequences, especially those upstream of open reading frames. In this respect, important cis-acting regulatory mutations that might help to further distinguish strains could be identified.

We thank the reviewer for their comments. LIN code could be applied clinically, for example in the analysis of antibiotic resistant isolates, or to investigate outbreaks associated with a particular lineage. We will update the text to describe this more thoroughly.

In regards to non-coding sequences: unfortunately, intergenic regions are generally unsuitable for use in typing systems as (i) they are subject to phase variation, which can occlude relationships based on descent; (ii) they are inherently difficult to assemble and therefore can introduce variation due to the sequencing procedure rather than biology. For the type of variant typing that LIN code represents, which aims to replicate phylogenetic clustering, protein encoding sequences are the best choice for convenience, stability, and accuracy. This is not to say that it is not a valid object to base a nomenclature on intergenic regions, which might be especially suitable for predicting some phenotypic characters, but this will still be subject to problem (ii), depending on the sequencing technology used.  Such a nomenclature system should stand beside, rather than be combined with or used in place of, phylogenetic typing. However, we could certainly investigate the relationship between an isolates LIN code and regulatory mutations in the future.

Reviewer #3 (Public review):

Summary:

In this well-written manuscript, Unitt and colleagues propose a new, hierarchical nomenclature system for the pathogen Neisseria gonorrhoeae. The proposed nomenclature addresses a longstanding problem in N. gonorrhoeae genomics, namely that the highly recombinant population complicates typing schemes based on only a few loci and that previous typing systems, even those based on the core genome, group strains at only one level of genomic divergence without a system for clustering sequence types together. In this work, the authors have revised the core genome MLST scheme for N. gonorrhoeae and devised life identification numbers (LIN) codes to describe the N. gonorrhoeae population structure.

Strengths:

The LIN codes proposed in this manuscript are congruent with previous typing methods for Neisseria gonorrhea, like cgMLST groups, Ng-STAR, and NG-MAST. Importantly, they improve upon many of these methods as the LIN codes are also congruent with the phylogeny and represent monophyletic lineages/sublineages.

The LIN code assignment has been implemented in PubMLST, allowing other researchers to assign LIN codes to new assemblies and put genomes of interest in context with global datasets.

Weaknesses:

The authors correctly highlight that cgMLST-based clusters can be fused due n to "intermediate isolates" generated through processes like horizontal gene transfer. However, the LIN codes proposed here are also based on single linkage clustering of cgMLST at multiple levels. It is unclear if future recombination or sequencing of previously unsampled diversity within N. gonorrhoeae merges together higher-level clusters, and if so, how this will impact the stability of the nomenclature.

The authors have defined higher resolution thresholds for the LIN code scheme. However, they do not investigate how these levels correspond to previously identified transmission clusters from genomic epidemiology studies. It would be useful for future users of the scheme to know the relevant LIN code thresholds for these investigations.

We thank the reviewer for their insightful comments. LIN codes do use multi-level single linkage clustering to define the cluster number of isolates. However, unlike previous applications of simple single linkage clustering such as N. gonorrhoeae core genome groups (Harrison et al., 2020), once assigned in LIN code, these cluster numbers are fixed within an unchanging barcode assigned to each isolate. Therefore, the nomenclature is stable, as the addition of new isolates cannot change previously established LIN codes.

Cluster stability was considered during the selection of allelic mismatch thresholds. By choosing thresholds based on natural breaks in population structure (Figure 3), applying clustering statistics such as the silhouette score, and by assessing where cluster stability has been maintained within the previous core genome groups nomenclature, we can have confidence that the thresholds which we have selected will form stable clusters. For example, with core genome groups there has been significant group fusion with clusters formed at a threshold of 400 allelic differences, while clustering at a threshold of 300 allelic differences has remained cohesive over time (supported by a high silhouette score) and so was selected as an important threshold in the gonococcal LIN code. LIN codes have now been applied to >27000 isolates in PubMLST, and the nomenclature has remained effective despite the continual addition of new isolates to this collection. The manuscript will be revised to emphasise these points.

Work is in progress to explore what LIN code thresholds are generally associated with transmission chains. These will likely be the last 7 thresholds (25, 10, 7, 5, 3, 1, 0) as previous work has suggested that isolates linked by transmission within one year are associated with <14 single nucleotide polymorphism differences (De Silva et al., 2016). The results of this analysis will be described in a future article, currently in preparation.

Harrison, O.B., et al. Neisseria gonorrhoeae Population Genomics: Use of the Gonococcal Core Genome to Improve Surveillance of Antimicrobial Resistance. The Journal of Infectious Diseases 2020.

De Silva, D., et al. Whole-genome sequencing to determine transmission of Neisseria gonorrhoeae: an observational study. The Lancet Infectious Diseases 2016;16(11):1295-1303.

eLife Assessment

This study provides valuable insights into microtubule remodeling during liver-stage Plasmodium berghei development, demonstrating that deletion of the alpha-tubulin C-terminal tail impairs parasite growth in mosquitoes and abolishes infection in HeLa cells. The work is technically ambitious, employing advanced microscopy, genetic mutants, and pharmacological approaches. However, key claims are only partially supported due to incomplete evidence linking tubulin modifications to microtubule dynamics and uncertain antibody-based PTM detection.

Reviewer #1 (Public review):

The authors try to investigate how the population of microtubules (LSPMB) that originate from sporozoite subpellicular microtubules (SSPM) and are remodelled during liver-stage development of malaria parasites. These bundles shrink over time and help form structures needed for cell division. The authors have used expansion microscopy, live-cell imaging, genetically engineered mutants, and pharmacological perturbation to study parasite development with liver cells.

A major strength of the manuscript is the live cell imaging and expansion microscopy to study this challenging liver stage of parasite development. It gives important knowledge that PTMs of α-tubulin, such as polyglutamylation and tyrosination/detyrosination, are crucial for microtubule stability. Mutations in α-tubulin reduce the parasite's ability to move and proliferate in the liver cells. The drug oryzalin, which targets microtubules, also blocks parasite development, showing how important dynamic microtubules are at this stage.

The major problem in the manuscript was the way it flows, as the authors keep shifting from the liver stage to the sporogony stages and then back to the liver stages. It was very confusing at times to know what the real focus of the study is, whether sporozoite development or liver stage development. The flow of the manuscript could be improved. Some of the findings reported here substantiate the previous electron microscopy.

Overall, the study represents an important contribution towards understanding cytoskeletal remodelling during liver stage infection. The study suggests that tubulin modifications are key for the parasite's survival in the liver and could be targets for new malaria treatments. This is also the stage that has been used for vaccine development, so any knowledge of how parasites proliferate in the liver cells will be beneficial towards intervention approaches.

Reviewer #2 (Public review):

Summary:

The authors investigated microtubule distribution and their possible post-translational modifications (PTM) in Plasmodium berghei during development of the liver stage, using either hepatocytes or HeLa cells as models. They used conventional immunofluorescence assays and expansion microscopy with various antibodies recognising tubulin and, in the second part of the work, its candidate PTMs, as well as markers of Plasmodium, in addition to live imaging with a fluorescent marker for tubulin. In the third part of the study, they generated 3 mutants deprived of either the last four residues or the last 11 residues, or where a candidate polyglutamylation site was substituted by an alanine residue.

Strengths:

In the first part, microtubules are monitored by a combination of two approaches (IFA and live), revealing nicely the evolution of the sporozoite subpellicular microtubules (SSPM, the sporozoite is the developmental stage present in salivary glands of the mosquitoes and that infects hepatocytes) into a different structure termed liver-stage parasite microtubule bundle (LSPMB). The LSPMB shrinks during the course of parasite development and finally disappears while hemi-spindles emerge over time. Contact points between these two structures are observed frequently in live cells and occasionally in fixed cells, suggesting the intriguing possibility that tubulin might be recycled from the LSPMB to contribute to hemi-spindle formation.

In the second part, antibodies recognising (1) the final tyrosine found at the C-terminal tail and (2) a stretch of 3 glutamate residues in a side chain are used to monitor these candidate PTMs. Signals are positive at the SSPM, and while it remains positive for polyglutamylation, it becomes negative for the final tyrosine at the LSPM, while a positive signal emerges at hemi-spindles at later stages of development.

In the last part, the three mutants are fed to mosquitoes, where they show reduced development, the one lacking the alpha-tubulin tail even failing to reach the salivary glands. However, the two other mutants infect HeLa cells normally, whereas sporozoites with the C-terminal tail deletion recovered from the haemolymph did not develop in these cells.

The first part provides convincing evidence that microtubules are extensively remodelled during the infection of hepatocytes and HeLa cells, in agreement with the spectacular Plasmodium morphogenetic changes accompanying massive and rapid proliferation. The third part brings further confirmation that the C-terminal tail of alpha-tubulin is essential for multiple stages of parasite development, in agreement with previous work (50). Since it is the region where several post-translational modifications take place in other organisms (detyrosination, polyglutamylation, glycylation), it makes sense to propose that the essential function is related to these PTMs also in Plasmodium.

Weaknesses:

The significance of tubulin PTM relies on two antibodies whose reactivity to Plasmodium tubulins is unclear (see below). The interpretation of the literature on detyrosination and polyglutamylation is confusing in several places, meaning that the statements about the possible role of these PTMs need to be carefully revisited.

The authors use the term "tyrosination" but the alpha1-tubulin studied here possesses the final tyrosine when it is synthesised, so it is "tyrosinated" by default. It could potentially be removed by a tyrosine carboxypeptidase of the vasoinhibin family (VASH) as reported in other species. After removal, this tyrosine can be added again by a tubulin-tyrosine ligase (TTL) enzyme. It is therefore more appropriate to talk about detyrosination-retyrosination rather than tyrosination (this confusion is unfortunately common in the literature, see Janke & Magiera, 2020).

The difficulty here is that there is so far no evidence that detyrosination takes place in Plasmodium. Neither VASH nor TTL could be identified in the Plasmodium genome (ref 31, something we can confirm with our unsuccessful BLAST analyses), and mass spectrometry studies of purified tubulin, albeit from blood stages, did not find evidence for detyrosination (reference 43). Western blots using an antibody against detyrosinated tubulin did not produce a positive signal, neither on purified tubulin, nor on whole parasites (43). Of course, the situation could be different in liver stages, but the question of the detyrosinating enzyme is still there. The existence of a unique Plasmodium system for detyrosination cannot be formally ruled out, but given the high degree of conservation of these PTMs and their associated enzymes, it sounds difficult to imagine.

The fact that the anti-tyrosinated antibody still produced a signal in the cell line where the final tyrosine is deleted raises issues about its specificity. A cross-reactivity with beta-tubulin is proposed, but the Plasmodium beta-tubulin does not carry a final tyrosine, further raising concerns about antibody specificity.

The interpretation of these results should therefore be considered carefully. There also seems to be some confusion in the function of detyrosination cited from the literature. It is said in line 229 that "tyrosination has been associated with stable microtubules" (33, 34, 50, 55). References 33 and 34 actually show that tyrosinated microtubules turn over faster in neurons or in epithelial cells, respectively, while references 50 and 55 do not study de/retyrosination. The general consensus is that tyrosinated microtubules are more dynamic (see reference 24).

The situation is a bit different for polyglutamylation since several candidate poly- or mono-glutamylases have been identified in the Plasmodium genome, and at least mono-glutamylation of beta-tubulin has been formally proven, still in bloodstream stages (ref 43). The authors propose that the residue E445 is the polyglutamylation site. To our knowledge, this has not been demonstrated for Plasmodium. This residue is indeed the favourite one in several organisms such as humans and trypanosomes (Eddé et al., Science 1990; Schneider et al., JCS, 1997), and it is tempting to propose it would be the same here. However, TTLLs bind the tubulin tails from their C-terminal end like a glove on a finger (Garnham et al., Cell, 2015), and the presence of two extra residues in Plasmodium tubulins would mean that the reactive glutamate might be in position E447 rather than E445. This is worth discussing.<br /> On the positive side, it is encouraging to see that signals for both anti-tyrosinated tail and poly-glutamylated side chain are going down in the various mutants, but this would need validation with a comparison for alpha-tubulin signal.

Line 316: polyglutamylation "is commonly associated with dynamic microtubule behavior (78-80)". Actually, references 78 and 79 show the impact of this PTM on interaction with spastin, and reference 80 discusses polyglutamylation as a marker of stable microtubules in the context of cilia and flagella. The consensus is that polyglutamylated microtubules tend to be more stable (ref24).

Conclusion:

The first and the third parts of this manuscript - evolution of microtubules and importance of the C-terminal tails for Plasmodium development - are convincing and well supported by data. However, the presence and role of tubulin PTM should be carefully reconsidered.

Plasmodium tubulins are more closely related to plant tubulins and are sensitive to inhibitors that do not affect mammalian microtubules. They therefore represent promising drug targets as several well-characterised compounds used as herbicides are available. The work produced here further defines the evolution of the microtubule network in sporozoites and liver stages, which are the initial and essential first steps of the infection. Moreover, Plasmodium has multiple specificities that make it a fascinating organism to study both for cell biology and evolution. The data reported here are elegant and will attract the attention of the community working on parasites but also on the cytoskeleton at large. It will be interesting to have the feedback of other people working on tubulin PTMs to figure out the significance of this part of the work.

Reviewer #3 (Public review):

Summary:

The manuscript by Atchou et al. investigates the role of the microtubule cytoskeleton in sporozoites of Plasmodium berghei, including possible functions of microtubule post-translational modifications (tyrosination and polyglutamylation) in the development of sporozoites in the liver. They also assessed the development of sporozoites in the mosquito. Using cell culture models and in vivo infections with parasites that contain tubulin mutants deficient in certain PTMs, they show that may aspects of the life cycle progression are impaired. The main conclusion is that microtubule PTMs play a major role in the differentiation processes of the parasites.

However, there are a number of major and minor points of criticism that relate to the interpretation of some of the data.

Comments:

(1) The first paragraph of "Results" almost suggests that the presence of a subpellicular MT-array in sporozoites is a new discovery. This is not the case, see e.g. the recent publication by Ferreira et al. (Nature Communications, 2023).

(2) Why were HeLa cells and not hepatocytes (as in Figure 3) used for measuring infection rates of the mutants in Figure 5H and 5L? As I understand, HeLa cells are not natural host cells for invading sporozoites. HeLa cells are epithelial cells derived from a cervical tumour. I am not an expert in Plasmodium biology, but is a HeLa infection an accepted surrogate model for liver stage development?

(3) The tubulin staining in Figures 1A and 1B is confusing and doesn't seem to make sense. Whereas in 1A the antibody nicely stains host and parasite tubulin, in 1B, only parasite tubulin is visible. If the same antibody and the same host cells have been used, HeLa cytoplasmic microtubules should be visible in 1B. In fact, they should be the predominant antigen. The same applies to Figure 2, where host microtubules are also not visible.

(4) In Figures 2A and B, the host nuclei appear to have very different sizes in the DMSO controls and in the drug-treated cells. For example, in the 20 µM (-) image (bottom right), the nuclei are much larger than in the DMSO (-) control (top left). If this is the case, expansion microscopy hasn't worked reproducibly, and therefore, quantification of fluorescence is problematic. The scalebar is the same for all panels.

(5) I don't quite follow the argument that spindles and the LSPMB are dynamic structures (e.g., lines 145, 174). That is a trivial statement for the spindle, as it is always dynamic, but beyond that, it has only been shown that the structure is sensitive to oryzalin. That says little about any "natural" dynamic behaviour. Any microtubule structure can be destroyed by a particular physical or chemical treatment, but that doesn't mean all structures are dynamic. It also depends on the definition of "dynamic" in a particular context, for example, the time scale of dynamic behaviour (changes within seconds, minutes, or hours).

(6) I am not sure what part in the story EB1 plays. The data are only shown in the Supplements and don't seem to be of particular relevance. EB1 is a ubiquitous protein associated with microtubule plus ends. The statement (line 192) that it "may play a broader role..." is unsubstantiated and cannot be based merely on the observation that it is expressed in a particular life cycle stage.

(7) Line 196 onwards: The antibody IN105 is better known in the field as polyE. Maybe that should be added in Materials and Methods. Also, the antibody T9028 against tyrosinated tubulin is poorly validated in the literature and rarely used. Usually, researchers in this field use the monoclonal antibody YL1/2. I am not sure why this unusual antibody was chosen in this study. In fact, has its specificity against tyrosinated α-tubulin from Plasmodium berghei ever been shown? The original antigen was human and had the sequence EGEEY. The Plasmodium sequence is YEADY and hence very different. It is stated that the LSPMB is both polyglutamylated and tyrosinated. This is unusual because polyglutamylated microtubules are usually indicative of stable microtubules, whereas tyrosinated microtubules are found on freshly polymerised and dynamic microtubules. However, a co-localisation within the same cell has not been attempted. This is, however, possible since polyE is a rabbit antibody and T9028 is a mouse antibody. I suspect that differences or gradients along the LSPMB would have been noticed. Also, in lines 207/208, it is said that tyrosination disappears after hepatocyte invasion, which is shown in Figure 3. However, in Figure 3A, quite a lot of positive signals for tyrosination are visible in the 54 and 56 hpi panels.

(8) In line 229, it is stated that tyrosination "has previously been associated with stable microtubule in motility". This statement is not correct. In fact, none of the cited references that apparently support this statement show that this is the case. On the contrary, stable microtubules, such as flagellar axonemes, are almost completely detyrosinated. Therefore, tyrosination is a marker for dynamic microtubules, whereas detyrosinated microtubules are indicative of stable microtubules. This is an established fact, and it is odd that the authors claim the opposite.

(9) Line 236 onwards: Concerning the generation of tubulin mutants, I think it is necessary to demonstrate successful replacement of the wild-type allele by the mutant allele. I am sure the authors have done this by amplification and subsequent sequencing of the genomic locus using PCR primers outside the plasmid sequences. I suggest including this information, e.g., by displaying the chromatograph trace in a supplementary figure. Or are the sequences displayed in Figure S3B already derived from sequenced genomic DNA? This is not described in the Legend or in Materials and Methods. The left PCR products obtained for Figure S3 B would be a suitable template for sequencing.

(10) It is also important to be aware of the fact that glutamylation also occurs on β-tubulin. This signal will also be detected by polyE (IN105). Therefore, it is surprising that IN105 immunofluorescence is negative on the C-term Δ cells (Figure S3 D). Is there anything known about confirmed polyglutamylation sites on both α- and β-tubulins in Plasmodium, e.g., by MS? In Toxoplasma, both α- and β-tubulin have been shown to be polyglutamylated.

(11) Figure S3 is very confusing. In the legend, certain intron deletions are mentioned. How does this relate to posttranslational tubulin modifications? The corresponding section in Results (lines 288-292) is also not very helpful in understanding this.

(12) Figure 4E doesn't look like brightfield microscopy but like some sort of fluorescent imaging. In Figure 4C, were the control (NoΔ) cells with an integrated cassette, but no mutations, or non-transgenic cells?

(13) It is difficult to understand why the TyΔ and the CtΔ mutants still show quite a strong signal using the anti-tyrosination antibody. If the mutants have replaced all wild-type alleles, the signal should be completely absent, unless the antibody (see my comment above concerning T9028) cross-reacts with detyrosinated microtubules. Therefore, the quantitation in Figures 5F and 5G is actually indicative of something that shouldn't be like that. The quantitation of 5F is at odds with the microscopy image in 5D. If this image is representative, the anti-Ty staining in TyΔ is as strong as in the control NoΔ.

(14) The statement that the failure of CtΔ mutants to generate viable sporozoites is due to the lack of microtubule PTMs (lines 295-296) is speculative. The lack of the entire C-terminal tail could have a number of consequences, such as impaired microtubule assembly or failure to recruit and bind associated proteins. This is not necessarily linked to PTMs. Also, it has been shown in yeast that for microtubules to form properly and exquisite regulation (proteostasis) of the ratio between α- and β-tubulin is essential (Wethekam and Moore, 2023). I am not sure, but according to Materials and Methods (line 423), the gene cassettes for replacing the wild-type tubulin gene with the mutant versions contain a selectable marker gene for pyrimethamine selection. Are there qPCR data that show that expression levels of mutant α-tubulin are more or less the same as the wild-type levels?

(15) In the Discussion, my impression is that two recent studies, the superb Expansion Microscopy study by Bertiaux et al. (2021) and the cryo-EM study by Ferreira et al. (2023), are not sufficiently recognised (although they are cited elsewhere in the manuscript). The latter study includes a detailed description of the microtubule cytoskeleton in sporozoites. However, the present study clearly expands the knowledge about the structure of the cytoskeleton in liver stage parasites and is one of the few studies addressing the distribution and function of microtubule post-translational modifications in Plasmodium.

(16) I somewhat disagree with the statement of a co-occurrence of polyglutamylated and tyrosinated microtubules. I think the resolution is too low to reach that conclusion. As this is a bold claim, and would be contrary to what is known from other organisms, it would require a more rigorous validation. Given the apparent problems with the anti-Ty antibody (signal in the TyΔ mutant), one should be very cautious with this claim.

(17) In the Discussion (lines 311 and 377), it is again claimed that tyrosinated microtubules are "a well-known marker of stable microtubules". This statement is completely incorrect, and I am surprised by this serious mistake. A few lines later, the authors say that polyglutamylated is "commonly associated with dynamic microtubule behaviour". Again, this is completely incorrect and is the opposite of what is firmly established in the literature. Polyglutamylation and detyrosination are markers of stable microtubules.

(18) In line 339, the authors interpret the residual antibody staining after the introduction of the mutant tubulin as a compensatory mechanism. There is no evidence for this. More likely explanations are firstly the quality of the anti-Ty-antibody used (see comment above), and the fact that also β-tubulin carries C-terminal polyglutamylation sites, which haven't been investigated in this study. PTMs on β-tubulin are not compensatory, but normal PTMs, at least in all other organisms where microtubule PTMs have been investigated.

Author response:

Public Reviews:

Reviewer #1 (Public review):

The authors try to investigate how the population of microtubules (LSPMB) that originate from sporozoite subpellicular microtubules (SSPM) and are remodelled during liver-stage development of malaria parasites. These bundles shrink over time and help form structures needed for cell division. The authors have used expansion microscopy, live-cell imaging, genetically engineered mutants, and pharmacological perturbation to study parasite development with liver cells.

A major strength of the manuscript is the live cell imaging and expansion microscopy to study this challenging liver stage of parasite development. It gives important knowledge that PTMs of α-tubulin, such as polyglutamylation and tyrosination/detyrosination, are crucial for microtubule stability. Mutations in α-tubulin reduce the parasite's ability to move and proliferate in the liver cells. The drug oryzalin, which targets microtubules, also blocks parasite development, showing how important dynamic microtubules are at this stage.

The major problem in the manuscript was the way it flows, as the authors keep shifting from the liver stage to the sporogony stages and then back to the liver stages. It was very confusing at times to know what the real focus of the study is, whether sporozoite development or liver stage development. The flow of the manuscript could be improved. Some of the findings reported here substantiate the previous electron microscopy.

Overall, the study represents an important contribution towards understanding cytoskeletal remodelling during liver stage infection. The study suggests that tubulin modifications are key for the parasite's survival in the liver and could be targets for new malaria treatments. This is also the stage that has been used for vaccine development, so any knowledge of how parasites proliferate in the liver cells will be beneficial towards intervention approaches.

We would like to express our sincere gratitude to Reviewer #1 for the positive and encouraging feedback on our manuscript. We are delighted that the reviewer found our experimental design and methodologies appropriate and that our study represents an important contribution to understanding cytoskeletal remodelling during liver stage infection, a critical phase for vaccine development. We are also grateful to the reviewer for highlighting the issue with the manuscript's flow. We acknowledge this limitation and will significantly improve the narrative structure and logical progression in the revised manuscript to ensure clarity and avoid any potential confusion. Thank you again for your thoughtful and constructive comments.

Reviewer #2 (Public review):

Summary:

The authors investigated microtubule distribution and their possible post-translational modifications (PTM) in Plasmodium berghei during development of the liver stage, using either hepatocytes or HeLa cells as models. They used conventional immunofluorescence assays and expansion microscopy with various antibodies recognising tubulin and, in the second part of the work, its candidate PTMs, as well as markers of Plasmodium, in addition to live imaging with a fluorescent marker for tubulin. In the third part of the study, they generated 3 mutants deprived of either the last four residues or the last 11 residues, or where a candidate polyglutamylation site was substituted by an alanine residue.

Strengths:

In the first part, microtubules are monitored by a combination of two approaches (IFA and live), revealing nicely the evolution of the sporozoite subpellicular microtubules (SSPM, the sporozoite is the developmental stage present in salivary glands of the mosquitoes and that infects hepatocytes) into a different structure termed liver-stage parasite microtubule bundle (LSPMB). The LSPMB shrinks during the course of parasite development and finally disappears while hemi-spindles emerge over time. Contact points between these two structures are observed frequently in live cells and occasionally in fixed cells, suggesting the intriguing possibility that tubulin might be recycled from the LSPMB to contribute to hemi-spindle formation.

In the second part, antibodies recognising (1) the final tyrosine found at the C-terminal tail and (2) a stretch of 3 glutamate residues in a side chain are used to monitor these candidate PTMs. Signals are positive at the SSPM, and while it remains positive for polyglutamylation, it becomes negative for the final tyrosine at the LSPM, while a positive signal emerges at hemi-spindles at later stages of development.

In the last part, the three mutants are fed to mosquitoes, where they show reduced development, the one lacking the alpha-tubulin tail even failing to reach the salivary glands. However, the two other mutants infect HeLa cells normally, whereas sporozoites with the C-terminal tail deletion recovered from the haemolymph did not develop in these cells.

The first part provides convincing evidence that microtubules are extensively remodelled during the infection of hepatocytes and HeLa cells, in agreement with the spectacular Plasmodium morphogenetic changes accompanying massive and rapid proliferation. The third part brings further confirmation that the C-terminal tail of alpha-tubulin is essential for multiple stages of parasite development, in agreement with previous work (50). Since it is the region where several post-translational modifications take place in other organisms (detyrosination, polyglutamylation, glycylation), it makes sense to propose that the essential function is related to these PTMs also in Plasmodium.

Weaknesses:

The significance of tubulin PTM relies on two antibodies whose reactivity to Plasmodium tubulins is unclear (see below). The interpretation of the literature on detyrosination and polyglutamylation is confusing in several places, meaning that the statements about the possible role of these PTMs need to be carefully revisited.

The authors use the term "tyrosination" but the alpha1-tubulin studied here possesses the final tyrosine when it is synthesised, so it is "tyrosinated" by default. It could potentially be removed by a tyrosine carboxypeptidase of the vasoinhibin family (VASH) as reported in other species. After removal, this tyrosine can be added again by a tubulin-tyrosine ligase (TTL) enzyme. It is therefore more appropriate to talk about detyrosination-retyrosination rather than tyrosination (this confusion is unfortunately common in the literature, see Janke & Magiera, 2020).

The difficulty here is that there is so far no evidence that detyrosination takes place in Plasmodium. Neither VASH nor TTL could be identified in the Plasmodium genome (ref 31, something we can confirm with our unsuccessful BLAST analyses), and mass spectrometry studies of purified tubulin, albeit from blood stages, did not find evidence for detyrosination (reference 43). Western blots using an antibody against detyrosinated tubulin did not produce a positive signal, neither on purified tubulin, nor on whole parasites (43). Of course, the situation could be different in liver stages, but the question of the detyrosinating enzyme is still there. The existence of a unique Plasmodium system for detyrosination cannot be formally ruled out but given the high degree of conservation of these PTMs and their associated enzymes, it sounds difficult to imagine.

The fact that the anti-tyrosinated antibody still produced a signal in the cell line where the final tyrosine is deleted raises issues about its specificity. A cross-reactivity with beta-tubulin is proposed, but the Plasmodium beta-tubulin does not carry a final tyrosine, further raising concerns about antibody specificity.

The interpretation of these results should therefore be considered carefully. There also seems to be some confusion in the function of detyrosination cited from the literature. It is said in line 229 that "tyrosination has been associated with stable microtubules" (33, 34, 50, 55). References 33 and 34 actually show that tyrosinated microtubules turn over faster in neurons or in epithelial cells, respectively, while references 50 and 55 do not study de/retyrosination. The general consensus is that tyrosinated microtubules are more dynamic (see reference 24).

The situation is a bit different for polyglutamylation since several candidate poly- or mono-glutamylases have been identified in the Plasmodium genome, and at least mono-glutamylation of beta-tubulin has been formally proven, still in bloodstream stages (ref 43). The authors propose that the residue E445 is the polyglutamylation site. To our knowledge, this has not been demonstrated for Plasmodium. This residue is indeed the favourite one in several organisms such as humans and trypanosomes (Eddé et al., Science 1990; Schneider et al., JCS, 1997), and it is tempting to propose it would be the same here. However, TTLLs bind the tubulin tails from their C-terminal end like a glove on a finger (Garnham et al., Cell, 2015), and the presence of two extra residues in Plasmodium tubulins would mean that the reactive glutamate might be in position E447 rather than E445. This is worth discussing.

On the positive side, it is encouraging to see that signals for both anti-tyrosinated tail and poly-glutamylated side chain are going down in the various mutants, but this would need validation with a comparison for alpha-tubulin signal.

Line 316: polyglutamylation "is commonly associated with dynamic microtubule behavior (78-80)". Actually, references 78 and 79 show the impact of this PTM on interaction with spastin, and reference 80 discusses polyglutamylation as a marker of stable microtubules in the context of cilia and flagella. The consensus is that polyglutamylated microtubules tend to be more stable (ref24).

Conclusion:

The first and the third parts of this manuscript - evolution of microtubules and importance of the C-terminal tails for Plasmodium development - are convincing and well supported by data. However, the presence and role of tubulin PTM should be carefully reconsidered.

Plasmodium tubulins are more closely related to plant tubulins and are sensitive to inhibitors that do not affect mammalian microtubules. They therefore represent promising drug targets as several well-characterised compounds used as herbicides are available. The work produced here further defines the evolution of the microtubule network in sporozoites and liver stages, which are the initial and essential first steps of the infection. Moreover, Plasmodium has multiple specificities that make it a fascinating organism to study both for cell biology and evolution. The data reported here are elegant and will attract the attention of the community working on parasites but also on the cytoskeleton at large. It will be interesting to have the feedback of other people working on tubulin PTMs to figure out the significance of this part of the work.

We thank Reviewer #2 for the thoughtful and detailed evaluation of our manuscript. We are pleased that the reviewer found our study elegant and believe it will attract the attention of the broader scientific community, both those working on parasites and those focused on cytoskeleton biology. We also acknowledge the concerns raised regarding the specificity of the antibodies used to detect tubulin post-translational modifications (PTMs), as well as the interpretation of their signals and the current lack of identified detyrosination enzymes in the Plasmodium genome. We agree that these are important limitations, and we will address them thoroughly in the revised manuscript. This includes clarifying our interpretation of tyrosination versus detyrosination, adjusting our claims regarding polyglutamylation sites, and carefully revisiting the literature cited to ensure accurate contextualization of PTM function in microtubule stability.

We are grateful for the reviewer’s close reading and critical feedback, which will help us substantially improve the clarity, precision, and strength of our manuscript.

Reviewer #3 (Public review):

Summary:

The manuscript by Atchou et al. investigates the role of the microtubule cytoskeleton in sporozoites of Plasmodium berghei, including possible functions of microtubule post-translational modifications (tyrosination and polyglutamylation) in the development of sporozoites in the liver. They also assessed the development of sporozoites in the mosquito. Using cell culture models and in vivo infections with parasites that contain tubulin mutants deficient in certain PTMs, they show that may aspects of the life cycle progression are impaired. The main conclusion is that microtubule PTMs play a major role in the differentiation processes of the parasites.

However, there are a number of major and minor points of criticism that relate to the interpretation of some of the data.

We thank Reviewer #3 for the overall positive assessment of our study and for recognizing its contribution to advancing our understanding of Plasmodium biology and malaria pathogenesis. We appreciate the reviewer’s constructive feedback, particularly regarding the interpretation of some of our data. These comments have been very helpful in guiding our revisions, and we have worked to improve both the clarity of our presentation and the precision of our interpretations in the revised manuscript.

Below, we respond in detail to each of the reviewer’s points.

Comments:<br /> (1) The first paragraph of "Results" almost suggests that the presence of a subpellicular MT-array in sporozoites is a new discovery. This is not the case, see e.g. the recent publication by Ferreira et al. (Nature Communications, 2023).

We thank the reviewer for pointing this out and fully agree that the subpellicular microtubule (SPM) array in sporozoites is well established, as documented in earlier work (e.g., Cyrklaff et al., 2007) and more recently by Ferreira et al. (Nat. Commun., 2023). Our intention was not to suggest that the existence of the SSPM is a novel finding. Rather, our study builds on this existing knowledge by demonstrating that these sporozoite-derived microtubules are not disassembled upon hepatocyte entry but are repurposed into a newly described structure, the liver stage parasite microtubule bundle (LSPMB). This reorganization, its persistence into liver stage development, and its dynamic role in microtubule remodeling and nuclear division are, to our knowledge, novel observations. We will revise the manuscript to make this distinction clearer in the introduction and the results section.

(2) Why were HeLa cells and not hepatocytes (as in Figure 3) used for measuring infection rates of the mutants in Figure 5H and 5L? As I understand, HeLa cells are not natural host cells for invading sporozoites. HeLa cells are epithelial cells derived from a cervical tumour. I am not an expert in Plasmodium biology, but is a HeLa infection an accepted surrogate model for liver stage development?

We appreciate the opportunity to clarify our experimental model. While HeLa cells are not the natural host cells, they are a well-established and validated in vitro model for studying Plasmodium berghei liver stage development in our lab and others. In this system, the parasite completes its full development and generates infectious merozoites. Numerous studies have successfully used HeLa cells as a liver stage infection model, with key findings subsequently validated in primary hepatocytes or in vivo, confirming its utility as a representative model. We employed this cell line primarily to reduce animal usage in accordance with the 3Rs principles (Replacement, Reduction, Refinement). Importantly, to ensure the biological relevance of our discoveries in HeLa cells, we validated our key findings in primary mouse hepatocytes, as shown in Figure 3. Furthermore, we confirmed the in vivo infectivity of mutant parasite lines that produced typical salivary gland sporozoites through an in vivo infection assay, presented in Figure S4C.

(3) The tubulin staining in Figures 1A and 1B is confusing and doesn't seem to make sense. Whereas in 1A the antibody nicely stains host and parasite tubulin, in 1B, only parasite tubulin is visible. If the same antibody and the same host cells have been used, HeLa cytoplasmic microtubules should be visible in 1B. In fact, they should be the predominant antigen. The same applies to Figure 2, where host microtubules are also not visible.

We thank the reviewer for this careful observation regarding the α-tubulin staining in Figures 1A and 1B. The same host cell type (HeLa) and α-tubulin antibody were indeed used in both experiments. Figure 1A shows results from conventional immunofluorescence assays, where both host and parasite microtubules are clearly stained. In contrast, Figure 1B shows the outcome of ultrastructure expansion microscopy (U-ExM), where parasite microtubules appear prominently, while host microtubules are less visible.

This effect appears to be a technical outcome of the U-ExM protocol, which can differentially preserve or reveal microtubule epitopes. We consistently observed stronger parasite signal across various cell types, including primary hepatocytes (Figure 3A,B). The lack of visible host microtubules in some U-ExM images does not reflect their absence, but rather reduced signal intensity relative to the parasite structures. This is not observed with all antibodies, e.g., host microtubules stain strongly with anti-tyrosinated α-tubulin (Figure 3B), likely reflecting their high tyrosination state.

To overcome this limitation, we employed PS-ExM and combined PS-ExM/U-ExM approaches (as described in reference 56), which allowed simultaneous high-resolution visualization of both host and parasite microtubule networks. These combined methods are now being used in follow-up studies to investigate host–parasite microtubule interactions in more detail.

We will clarify this point in the revised manuscript to avoid confusion.

(4) In Figures 2A and B, the host nuclei appear to have very different sizes in the DMSO controls and in the drug-treated cells. For example, in the 20 µM (-) image (bottom right), the nuclei are much larger than in the DMSO (-) control (top left). If this is the case, expansion microscopy hasn't worked reproducibly, and therefore, quantification of fluorescence is problematic. The scalebar is the same for all panels.

The expansion microscopy methods used in this study have been rigorously validated for both reproducibility and isotropicity. However, as the reviewer rightly notes, host cell nuclei can vary in size due to several factors, including cell cycle stage, infection status, and the extent of parasite development, all of which can influence host nuclei morphology and size.

Importantly, the quantifications relevant to our conclusions were focused specifically on parasite structures. We did not rely on host nuclear size or host fluorescence intensity as a quantitative readout in this context. While we acknowledge the observed variability in host nuclear dimensions, it does not compromise the accuracy or reproducibility of the parasite specific measurements central to our study.

We will clarify this point in the revised figure legend and manuscript.

(5) I don't quite follow the argument that spindles and the LSPMB are dynamic structures (e.g., lines 145, 174). That is a trivial statement for the spindle, as it is always dynamic, but beyond that, it has only been shown that the structure is sensitive to oryzalin. That says little about any "natural" dynamic behaviour. Any microtubule structure can be destroyed by a particular physical or chemical treatment, but that doesn't mean all structures are dynamic. It also depends on the definition of "dynamic" in a particular context, for example, the time scale of dynamic behaviour (changes within seconds, minutes, or hours).

We agree that sensitivity to chemical depolymerization alone does not necessarily indicate dynamic behavior, particularly in the absence of data on turnover kinetics or temporal changes.

Our interpretation was based on two observations: first, that the LSPMB, which derives from the highly stable sporozoite subpellicular microtubules (known to be drug-resistant), becomes susceptible to depolymerization during the liver stage; and second, that the LSPMB gradually shrinks over time during parasite development. These features suggested a transition toward a more dynamic state compared to its origin. However, we fully agree that “dynamic” is a context-dependent term and that direct evidence such as turnover rates or structural changes on short time scales, is required to rigorously define microtubule dynamics.

We will revise the manuscript to clarify our use of this term and explicitly acknowledge the need for further studies to characterize the timescale and mechanisms underlying LSPMB remodeling.

(6) I am not sure what part in the story EB1 plays. The data are only shown in the Supplements and don't seem to be of particular relevance. EB1 is a ubiquitous protein associated with microtubule plus ends. The statement (line 192) that it "may play a broader role..." is unsubstantiated and cannot be based merely on the observation that it is expressed in a particular life cycle stage.

We agree that EB1 is a ubiquitous microtubule plus-end binding protein and that its presence alone does not imply a novel function. Previous studies (e.g., Maurer et al., 2023; Yang et al., 2023; Zeeshan et al., 2023) have focused on its role during Plasmodium sexual stages, while its expression during liver and mosquito stages has not been previously documented.

Our data extend this knowledge by showing that EB1 is also expressed during liver stage development, particularly during the highly mitotic schizont phase. While we agree that this observation alone does not prove functional involvement, it raises the possibility of a broader role for EB1 in regulating microtubule dynamics beyond sexual stages. To avoid overinterpretation, we have presented these findings in the supplementary material and will revise the manuscript to tone down speculative statements and clearly frame this as a preliminary observation that warrants further investigation.

(7) Line 196 onwards: The antibody IN105 is better known in the field as polyE. Maybe that should be added in Materials and Methods. Also, the antibody T9028 against tyrosinated tubulin is poorly validated in the literature and rarely used. Usually, researchers in this field use the monoclonal antibody YL1/2. I am not sure why this unusual antibody was chosen in this study. In fact, has its specificity against tyrosinated α-tubulin from Plasmodium berghei ever been shown? The original antigen was human and had the sequence EGEEY. The Plasmodium sequence is YEADY and hence very different. It is stated that the LSPMB is both polyglutamylated and tyrosinated. This is unusual because polyglutamylated microtubules are usually indicative of stable microtubules, whereas tyrosinated microtubules are found on freshly polymerised and dynamic microtubules. However, a co-localisation within the same cell has not been attempted. This is, however, possible since polyE is a rabbit antibody and T9028 is a mouse antibody. I suspect that differences or gradients along the LSPMB would have been noticed. Also, in lines 207/208, it is said that tyrosination disappears after hepatocyte invasion, which is shown in Figure 3. However, in Figure 3A, quite a lot of positive signals for tyrosination are visible in the 54 and 56 hpi panels.

First, we acknowledge that the IN105 antibody is more widely known as "polyE" in the field. We will update the Materials and Methods section accordingly to reflect this nomenclature.

Regarding the use of the T9028 antibody against tyrosinated α-tubulin: we agree that this monoclonal antibody is less commonly used than YL1/2, and we appreciate the reviewer drawing attention to this. The original antigen for T9028 is based on the mammalian C-terminal sequence EGEEY, which differs from the Plasmodium α1-tubulin sequence (YEADY). Like many in the field, we face the challenge that most available antibodies are raised against mammalian epitopes, and specificity in Plasmodium can vary. Nonetheless, the literature (e.g., Hirst et al., 2022; Fennell et al., 2008) has demonstrated that tyrosination occurs in Plasmodium α1-tubulin, using anti-tyrosination antibodies including YL1/2.

Following the reviewer’s excellent suggestion, we are currently repeating the key experiments using the YL1/2 antibody to compare staining patterns directly with those obtained using T9028. We will include these results in the revised manuscript.

Concerning the potential co-localization of polyglutamylation and tyrosination on the LSPMB: we agree that this is an interesting and testable hypothesis. In the current manuscript, Figures 3A and 3B were generated from independent experiments, and thus co-localization was not assessed. However, as the reviewer correctly notes, polyE and T9028 antibodies are raised in rabbit and mouse, respectively, making co-staining feasible. We will follow up on this experimentally and, if feasible within our revision timeline, include data in the revised version or highlight this as a future direction.

Finally, with regard to Figure 3 and the observation that tyrosination appears to persist at 54 and 56 hpi (Figure 3B): the reviewer is correct that tyrosination signal is still detectable at these time points. Our statement that tyrosination “disappears after hepatocyte invasion” was intended to refer to an overall decrease in signal intensity during early liver stage development, with a reappearance at later stages (e.g., cytomere formation). We will rephrase this section for greater clarity and ensure that figure annotations and legends unambiguously reflect the dynamics observed.

(8) In line 229, it is stated that tyrosination "has previously been associated with stable microtubule in motility". This statement is not correct. In fact, none of the cited references that apparently support this statement show that this is the case. On the contrary, stable microtubules, such as flagellar axonemes, are almost completely detyrosinated. Therefore, tyrosination is a marker for dynamic microtubules, whereas detyrosinated microtubules are indicative of stable microtubules. This is an established fact, and it is odd that the authors claim the opposite.

We fully agree that in canonical eukaryotic systems, tyrosinated microtubules are generally markers of dynamic microtubule populations, whereas detyrosinated microtubules are typically associated with stability particularly in structures such as flagellar axonemes.

Our original statement will be corrected. In our study, we observed that tyrosinated microtubules are prevalent in invasive stages (sporozoites and merozoites), while detyrosinated forms become more prominent during intracellular liver stage development. This pattern is consistent with the established link between tyrosination and dynamic microtubules.

What is particularly intriguing in Plasmodium is the apparent cycling of tyrosination despite the absence of known tubulin tyrosine ligase (TTL) homologs in the genome. This suggests either a highly divergent enzyme or the involvement of host cell factors, a hypothesis supported by the reappearance of tyrosinated microtubules during liver stage schizogony (Figure 3B).

We will revise the relevant text and the Discussion section to reflect these mechanistic considerations more accurately and to avoid misrepresenting established principles of microtubule biology.

(9) Line 236 onwards: Concerning the generation of tubulin mutants, I think it is necessary to demonstrate successful replacement of the wild-type allele by the mutant allele. I am sure the authors have done this by amplification and subsequent sequencing of the genomic locus using PCR primers outside the plasmid sequences. I suggest including this information, e.g., by displaying the chromatograph trace in a supplementary figure. Or are the sequences displayed in Figure S3B already derived from sequenced genomic DNA? This is not described in the Legend or in Materials and Methods. The left PCR products obtained for Figure S3 B would be a suitable template for sequencing.

Indeed, these data are presented in Figure 4B and the corresponding sequence data are shown in Figure S3B. We appreciate the reviewer’s suggestion, which will help improve the transparency and reproducibility of our methodology.

(10) It is also important to be aware of the fact that glutamylation also occurs on β-tubulin. This signal will also be detected by polyE (IN105). Therefore, it is surprising that IN105 immunofluorescence is negative on the C-term Δ cells (Figure S3 D). Is there anything known about confirmed polyglutamylation sites on both α- and β-tubulins in Plasmodium, e.g., by MS? In Toxoplasma, both α- and β-tubulin have been shown to be polyglutamylated.

Indeed, polyglutamylation is known to occur not only on α-tubulin but also on β-tubulin in many organisms, including Toxoplasma gondii, and the polyE (IN105) antibody is expected to detect polyglutamylation on both tubulin isoforms.

The parasites shown in Figure S3D correspond to mutant lines originally generated by Spreng et al. (2019): the IntronΔ mutant (with deletion of introns in the Plasmodium α1-tubulin gene) and the C-termΔ mutant (with deletion of the final three C-terminal residues: ADY). As the reviewer correctly notes, this particular C-terminal deletion does not include the predicted polyglutamylation site (E445 or E447, depending on alignment), and thus should not abolish all polyglutamylation. However, in our experiments, the IN105 signal is substantially reduced in this mutant. This may suggest that structural alterations in the tubulin tail affect accessibility of the polyglutamylation epitope or influence the modification itself though we cannot exclude other possibilities, including changes in antibody recognition.

To date, polyglutamylation sites in Plasmodium tubulins have not been definitively confirmed by mass spectrometry. However, a recent MS-based study (reference 43) detected monoglutamylation on β-tubulin in blood stage parasites. Direct MS evidence for polyglutamylation of either α- or β-tubulin in Plasmodium liver stages is still lacking. We will clarify these points in the revised manuscript to avoid potential confusion and to highlight the need for future biochemical validation of PTM sites.

(11) Figure S3 is very confusing. In the legend, certain intron deletions are mentioned. How does this relate to posttranslational tubulin modifications? The corresponding section in Results (lines 288-292) is also not very helpful in understanding this.

The parasite lines shown in Figure S3D were originally generated by Spreng et al. (2019) and are not directly part of the main set of PTM-targeted mutants described in our study. Specifically, the IntronΔ line carries deletions in introns of the Plasmodium α1-tubulin gene, while the C-termΔ line lacks the final three C-terminal residues (ADY). These lines were included for comparative purposes to explore whether structural changes in α-tubulin could impact polyglutamylation signal, as detected by the polyE (IN105) antibody.

We acknowledge that the figure legend and corresponding text (lines 288–292) did not adequately explain the rationale for including these control lines. We will revise both the legend and Results section to more clearly describe the origin, purpose, and relevance of these mutants to the overall study.

(12) Figure 4E doesn't look like brightfield microscopy but like some sort of fluorescent imaging. In Figure 4C, were the control (NoΔ) cells with an integrated cassette, but no mutations, or non-transgenic cells?

The reviewer is absolutely correct: Figure 4E shows a fluorescent image acquired using widefield microscopy and not a brightfield image. We will revise the figure legend accordingly to avoid confusion. The “BF” (brightfield) label applies only to the left panel in Figure 4C, which depicts oocysts imaged using transmitted light.

Regarding the controls labeled "NoΔ" in Figure 4C, we confirm that these parasites contain the integrated selection cassette but do not harbor any mutations in the target gene. They serve as proper integration controls, allowing us to distinguish the effects of the point mutations or deletions introduced in the experimental lines.

(13) It is difficult to understand why the TyΔ and the CtΔ mutants still show quite a strong signal using the anti-tyrosination antibody. If the mutants have replaced all wild-type alleles, the signal should be completely absent, unless the antibody (see my comment above concerning T9028) cross-reacts with detyrosinated microtubules. Therefore, the quantitation in Figures 5F and 5G is actually indicative of something that shouldn't be like that. The quantitation of 5F is at odds with the microscopy image in 5D. If this image is representative, the anti-Ty staining in TyΔ is as strong as in the control NoΔ.

We agree that the persistence of anti-tyrosination signal in the TyΔ and CtΔ mutant lines is unexpected, given that all wild-type alleles were replaced. This discrepancy has led us to further investigate the specificity of the T9028 antibody, as raised in the reviewer’s earlier comment. To address this concern, we are currently repeating the key experiments using the well-established YL1/2 monoclonal antibody, which is widely accepted for detecting tyrosinated α-tubulin in other systems.

We also acknowledge that Figure 5F shows residual tyrosination signal, and the reviewer is correct that this should not occur if the modified residues are the exclusive PTM sites. One possible explanation is that adjacent residues or even alternative tubulin isoforms may serve as substrates. While α1-tubulin is the dominant isoform in Plasmodium, low-level expression of α2-tubulin has been detected in liver stages based on transcriptomic data, and it may contribute to the observed signal.

Regarding the apparent discrepancy between the quantification in Figure 5F and the representative image in Figure 5D, we will revise the figure legend to clarify that image selection aimed to show detectable signal, not necessarily the average phenotype. We will also reassess and, if needed, repeat the quantification with improved image sets to ensure accuracy and consistency.

We will revise the manuscript to reflect these points and include a more nuanced interpretation of the residual staining in the mutant lines.

(14) The statement that the failure of CtΔ mutants to generate viable sporozoites is due to the lack of microtubule PTMs (lines 295-296) is speculative. The lack of the entire C-terminal tail could have a number of consequences, such as impaired microtubule assembly or failure to recruit and bind associated proteins. This is not necessarily linked to PTMs. Also, it has been shown in yeast that for microtubules to form properly and exquisite regulation (proteostasis) of the ratio between α- and β-tubulin is essential (Wethekam and Moore, 2023). I am not sure, but according to Materials and Methods (line 423), the gene cassettes for replacing the wild-type tubulin gene with the mutant versions contain a selectable marker gene for pyrimethamine selection. Are there qPCR data that show that expression levels of mutant α-tubulin are more or less the same as the wild-type levels?

We agree that attributing the developmental failure of the CtΔ mutants solely to the absence of microtubule post-translational modifications (PTMs) is speculative. As the reviewer rightly points out, deletion of the entire C-terminal tail may have multiple effects, including impaired microtubule assembly, altered α/β-tubulin stoichiometry, or disruption of interactions with essential microtubule-associated proteins (MAPs). These consequences may arise independently of PTMs.

That said, we note that PTMs particularly polyglutamylation, can modulate MAP binding by altering the surface charge of microtubules (Genova et al., 2023; Mitchell et al., 2010). Therefore, while PTM loss may be a contributing factor, we acknowledge that the phenotype likely results from a combination of mechanisms. We will revise the relevant section of the manuscript to present a more cautious and balanced interpretation.

Regarding the reviewer’s question on expression levels: although the replacement constructs include a pyrimethamine resistance cassette, we have not yet quantified α-tubulin transcript levels by qPCR. In the interim, the study by Spreng et al. (2019) (reference 50) on a related α1-tubulin nutations provides valuable insight. They observed no difference in mRNA levels in day 12 oocysts, yet reported fainter microtubule staining and shorter sporozoites, suggesting a post-transcriptional mechanism affecting protein expression or function in later stages. Furthermore, the phenotypic spectrum across their mutant panel (Suppl. Fig. 3 D and E) implies that robust α-tubulin regulation is highly sensitive to specific sequences.

We acknowledge this as a current limitation in our study and will address it in the revised manuscript, noting that direct measurement of transcript levels is a key area for future investigation.

(15) In the Discussion, my impression is that two recent studies, the superb Expansion Microscopy study by Bertiaux et al. (2021) and the cryo-EM study by Ferreira et al. (2023), are not sufficiently recognised (although they are cited elsewhere in the manuscript). The latter study includes a detailed description of the microtubule cytoskeleton in sporozoites. However, the present study clearly expands the knowledge about the structure of the cytoskeleton in liver stage parasites and is one of the few studies addressing the distribution and function of microtubule post-translational modifications in Plasmodium.

Indeed, our work builds upon the established knowledge from Bertiaux et al. (2021) and the cryo-EM study by Ferreira et al. (2023), as rightly mentioned by the reviewer. We agree that these foundational studies, combined with our findings, will significantly expand the understanding of Plasmodium biology and cytoskeleton dynamics across its life cycle and will open the door for further investigations. We are grateful for this suggestion and will ensure these key studies are appropriately acknowledged in the revised manuscript.

(16) I somewhat disagree with the statement of a co-occurrence of polyglutamylated and tyrosinated microtubules. I think the resolution is too low to reach that conclusion. As this is a bold claim, and would be contrary to what is known from other organisms, it would require a more rigorous validation. Given the apparent problems with the anti-Ty antibody (signal in the TyΔ mutant), one should be very cautious with this claim.

This is a very important point to clarify. As mentioned previously, the initial experiments for these modifications were performed independently. It is established that sporozoite subpellicular microtubules exhibit both tyrosination and polyglutamylation. We will revise the manuscript to temper this statement and clearly indicate that the co-occurrence of these PTMs remains a hypothesis that requires more rigorous validation. As suggested, we are now conducting additional co-staining experiments using the better validated YL1/2 antibody to re-express and directly compare the distribution of both PTMs within the same cell. These follow-up experiments will help clarify whether both modifications occur simultaneously on the same microtubule structures in Plasmodium liver stages.

(17) In the Discussion (lines 311 and 377), it is again claimed that tyrosinated microtubules are "a well-known marker of stable microtubules". This statement is completely incorrect, and I am surprised by this serious mistake. A few lines later, the authors say that polyglutamylated is "commonly associated with dynamic microtubule behaviour". Again, this is completely incorrect and is the opposite of what is firmly established in the literature. Polyglutamylation and detyrosination are markers of stable microtubules.

Indeed, in canonical eukaryotic systems, tyrosinated microtubules are generally considered markers of dynamic microtubule populations, whereas detyrosinated and polyglutamylated microtubules are more commonly associated with stability.

We acknowledge this mistake and will revise the Discussion to correct these statements accordingly. In the context of Plasmodium, our observations suggest an unusual regulation of microtubule dynamics, which may reflect parasite-specific adaptations. For example, we observed tyrosinated α-tubulin in the stable subpellicular microtubules of sporozoites structures typically known for their exceptional stability. This atypical association implies either non-canonical roles for tyrosination or parasite-specific mechanisms for modulating microtubule properties. Additionally, the presence of both PTMs at different stages of development and on different microtubule populations suggests tightly regulated spatial and temporal modulation of microtubule function.

We will carefully revise the relevant sections of the manuscript to remove incorrect generalizations and ensure accurate representation of the current consensus in the field, while emphasizing the possibility of Plasmodium-specific adaptations that merit further study.

(18) In line 339, the authors interpret the residual antibody staining after the introduction of the mutant tubulin as a compensatory mechanism. There is no evidence for this. More likely explanations are firstly the quality of the anti-Ty-antibody used (see comment above), and the fact that also β-tubulin carries C-terminal polyglutamylation sites, which haven't been investigated in this study. PTMs on β-tubulin are not compensatory, but normal PTMs, at least in all other organisms where microtubule PTMs have been investigated.

As mentioned above, we are currently repeating the key experiments with the [YL1/2] antibody, as suggested. Furthermore, we fully agree with the reviewer's point regarding polyglutamylation on β-tubulin. The C-terminal tail of β-tubulin does indeed contain polyglutamylation sites. As we noted in the manuscript (Lines 340-352), this aspect has not been investigated in the present study, and we acknowledge it as a valuable direction for future research. We will revise the text accordingly to avoid overinterpretation and to more accurately reflect the limitations of our current data.

eLife Assessment

This important work shows that fine particulate matter exposure to the lungs led to nociceptor-dependent neutrophilic inflammation. Likely macrophage-neuronal crosstalk, via release of artemin from macrophages and activation of Gfra3 on the JNC neuron, potentiated the response. The data convincingly strengthens links between pollutants, immune and neural interactions.

Reviewer #1 (Public review):

Summary:

In the presented study, the authors aim to explore the role of nociceptors in the fine particulate matter (FPM) mediated Asthma phenotype, using rodent models of allergic airway inflammation. This manuscript builds on previous studies, and identify transciptomic reprogramming and an increased sensitivity of the jugular nodose complex (JNC) neurons, one of the major sensory ganglion for the airways, on exposure to FPM along with Ova during the challenge phase. The authors then use OX-314 a selectively permeable form of lidocaine, and TRPV1 knockouts to demonstrate that nociceptor blocking can reduce airway inflammation in their experimental setup.

The authors further identify the presence of Gfra3 on the JNC neurons, a receptor for the protein Artemin, and demonstrate their sensitivity to Artmein as a ligand. They further show that alveolar macrophages release Artemin on exposure to FPM.

Strengths:

The study builds on results available from multiple previous works, and presents important results which allow insights into the mixed phenotypes of Asthma seen clinically. In addition, by identifying the role of nociceptors, they identify potential therapeutic targets which bear high translational potential.

Weaknesses:

While the results presented in the study are highly relevant, there is a need for further mechanistic dissection to allow better inferences. Currently, certain results seem associative. Also, certain visualisations and experimental protocols presented in the manuscript need careful assessment and interpretation.

While Asthma is a chronic disease, the presented results are particularly important to explore Asthma exacerbations in response to acute exposure to air pollutants. This is relevant in today's age of increasing air pollution and increasing global travel.

Comments on revisions:

Thank you for addressing the suggestions. No further comments.

Reviewer #2 (Public review):

Summary:

The authors sought to investigate the role of nociceptor neurons in the pathogenesis of pollution-mediated neutrophilic asthma. The authors overall achieved the aim of demonstrating that nociceptor neurons are important to the pathogenesis of pollution-exacerbated asthma. Their results support their conclusions overall, although there are ways the study findings can be strengthened. This work further evaluates how nociceptor neurons contribute to asthma pathogenesis important for consideration while proposing treatment strategies for under treated asthma endotypes.

Strengths:

The authors utilize TRPV1 ablated mice to confirm the effects of intranasally administered QX-314 utilized to block sodium currents.

Use of intravital microscopy to track alveolar macrophage and neutrophil motility in their model

The authors demonstrate that via artemin, which is upregulated in alveolar macrophages in response to pollution, sensitizes JNC neurons thereby increasing their responsiveness to pollution. Ablation or inactivity of nociceptor neurons prevented the pollution induced increase in inflammation.

Weaknesses:

While neutrophilic, unclear of the endotype of asthma represented by the model

Comments on revisions:

The authors have addressed or commented on all concerns.

Reviewer #3 (Public review):

Asthma is a complex disease that includes endogenous epithelial, immune and neural components that respond to environmental stimuli. Small airborne particles with diameters in the range of 2.5 micrometers or less, so-called PM2.5, are thought to contribute to some forms of asthma. These forms of asthma may have neutrophils, eosinophils and macrophages in bronchoalveolar lavage. Here, Wang and colleagues build on a recent model that incorporated PM2.5 which was found to have a neutrophilic component. Wang altered the model to provide an extra kick via the incorporation of ovalbumin. The major strength of this work is that silencing TRPV1-expressing neurons either pharmacologically or genetically, modulated inflammation and the motility of neutrophils. By examining bronchoalveolar lavage fluid, they found not only that levels of a number of cytokines were increased, but also that artemin, a protein that supports neuronal development and function, was elevated, which did not occur in nociceptor- ablated mice. Their data strengthens links between pollutants, immune and neural interactions.

Comments on revisions:

The manuscript has been revised extensively, including the addition of new experiments, such as intravital microscopy. Did the comments from the reviewers, manifest by additional experiments and modifying how some of the data was presented, result in any changes in the hypotheses or the interpretation of such?

eLife Assessment

CCL2 is a chemokine with immune cell chemoattractant properties, and it appears to play a role in several chronic inflammatory diseases. The RNA-binding protein HuR controls the stability and translation of CCL2 mRNA. This paper presents convincing evidence that a relatively common genetic variant tied to several disease phenotypes affects the interaction between the mRNA of CCL2 and the RNA-binding protein HuR. While the experiments cannot definitively distinguish between effects on RNA transcription and stability, CCL2 is thought to be relevant for leukocyte migration in various conditions, including chronic inflammation and cancer, and the study presents important findings that may be relevant to a broad audience.

Reviewer #1 (Public review):

Summary:

This paper presents evidence that a relatively common genetic variant tied to several disease phenotypes affects the interaction between the mRNA of CCL2 and the RNA binding protein HuR. CCL2 is an immune cell chemoattractant protein.

Strengths:

The study is well conducted with relevant controls. The techniques are appropriate, and several approaches provided concordant results were generally supportive of the conclusions reached. The impact of this work, identifying a genetic variant that works by altering the binding of an RNA-regulatory protein, has important implications given that the HuR protein could be a drug target to improve its function and over-ride this genetic change. This could have important implications for a number of diseases where this genetic variant contributes to disease risk.

The authors have done a nice job of citing prior work. Details of the experimental protocols are well elaborated and the significance of the findings are well contextualized.

Weaknesses:

Authors have addressed prior weaknesses.

Reviewer #2 (Public review):

This study focuses on the differential binding of the RNA-binding protein HuR to CCL2 transcript (genetic variants rs13900 T or C). The study explores how this interaction influences the stability and translation of CCL2 mRNA. Employing a combination of bioinformatics, reporter assays, binding assays, and modulation of HuR expression, the study proposes that the rs13900T allele confers increased binding to HuR, leading to greater mRNA stability and higher translational efficiency. These findings indicate that rs13900T allele might contribute to heightened disease susceptibility due to enhanced CCL2 expression mediated by HuR. The study is interesting and most results are convincing, however the interpretation relative to RNA transcription and/or stability must be modified, and some data need better presentation or interpretation.

Major Points

Figure 2C:<br /> The authors describe an experiment to assess mRNA stability by labeling nascent RNA with EU for 3 hours, followed by washout of EU, and then incubation with or without actinomycin D for an additional 4 hours before measuring the remaining EU-labeled RNA. While the approach to label nascent RNA with EU is appropriate for tracking RNA decay, I have concerns regarding the use and interpretation of actinomycin D in this context.<br /> After EU washout, the pool of EU-labeled RNA is fixed and no new EU incorporation can occur. Therefore, the addition of actinomycin D at this stage should not affect the decay rate of the already labeled RNA, as transcription of EU-labeled RNA has effectively ceased. In this design, measuring the decrease in EU-labeled RNA over time reflects mRNA stability (even in absence of actinomycin D) rather than transcriptional activity.<br /> Therefore, the authors' statement that the non-actinomycin D treatment group represents transcriptional changes is not accurate here. Since EU labeling was stopped prior to the 4-hour incubation, any changes in EU-labeled RNA levels during this period reflect RNA decay, not new transcription.

In summary:<br /> To assess transcriptional changes, one would compare the amount of EU-labeled RNA synthesized during the initial labeling period (the first 3 hours), before washout.<br /> If the authors wish to use actinomycin D to block transcription, this should be done in a separate decay assay without EU labeling.<br /> In the current experimental setup, actinomycin D is unnecessary after EU washout and does not influence the decay of the labeled RNA.<br /> I recommend the authors reconsider the interpretation of their data accordingly. I recommend to remove the data points relative to the presence of actinomycin D, as the non-actinomycin D samples are already representative of post-transcriptional changes given that EU was washed out. If Authors want to assess transcriptional changes, they would have to assess the levels during the initial labeling period (before the washout). Transcriptional differences were not assessed, therefore I would modify the text accordingly.<br /> In this context, any changes observed in the actinomycin D-treated samples are likely attributable to general cellular stress induced by actinomycin D, which is known to be highly stressful for cells. This stress could indirectly influence the decay rates of already-labeled EU-RNA.

Figure 4C and 4D:<br /> The Author provided an updated gel with relative quantification - which effectively show the enhanced binding of CCL2 mRNA carrying the T variant to HuR - but they only provided it as data for reviewers (Figure R1). I highly recommend to use these data in the final manuscript instead of the data currently presented in Figure 4C and 4D. This would be important in order not to not create confusion in the reader or concerns regarding probe degradation or saturation.

Minor points<br /> For the IP, I recommend to explain in the final version why the input was not provided (lack of material) and to clarify that the specific binding of Actin was used as a loading control in absence of input. This would be highly beneficial for the readers.

eLife Assessment

In this important study, the authors engineered and characterised novel genetically encoded calcium indicators (GECIs) and an analytical tool (CaFire) capable of reporting and quantifying various sub-synaptic events, including miniature synaptic events, with a speed and sensitivity approaching that of intracellular electrophysiological recordings. While the evidence supporting the improvements in the speed and accuracy of these tools is convincing, including additional information about key imaging parameters, the Bar8f experiments, and CaFire would strengthen the study. This work will be of interest to neurobiologists studying synaptic calcium dynamics in various model systems.

Reviewer #1 (Public review):

Summary:

Chen et al. engineered and characterized a suite of next-generation GECIs for the Drosophila NMJ that allow for the visualization of calcium dynamics within the presynaptic compartment, at presynaptic active zones, and in the postsynaptic compartment. These GECIs include ratiometric presynaptic Scar8m (targeted to synaptic vesicles), ratiometric active zone localized Bar8f (targeted to the scaffold molecule BRP), and postsynaptic SynapGCaMP8m. The authors demonstrate that these new indicators are a large improvement on the widely used GCaMP6 and GCaMP7 series GECIs, with increased speed and sensitivity. They show that presynaptic Scar8m accurately captures presynaptic calcium dynamics with superior sensitivity to the GCaMP6 and GCaMP7 series and with similar kinetics to chemical dyes. The active-zone targeted Bar8f sensor was assessed for the ability to detect release-site-specific nanodomain changes, but the authors concluded that this sensor is still too slow to accurately do so. Lastly, the use of postsynaptic SynapGCaMP8m was shown to enable the detection of quantal events with similar resolution to electrophysiological recordings. Finally, the authors developed a Python-based analysis software, CaFire, that enables automated quantification of evoked and spontaneous calcium signals. These tools will greatly expand our ability to detect activity at individual synapses without the need for chemical dyes or electrophysiology.

Strengths:

(1) In this study, the authors rigorously compare their newly engineered GECIs to those previously used at the Drosophila NMJ, highlighting improvements in localization, speed, and sensitivity. These comparisons appropriately substantiate the authors' claim that their GECIs are superior to those currently in use.

(2) The authors demonstrate the ability of Scar8m to capture subtle changes in presynaptic calcium resulting from differences between MN-Ib and MN-Is terminals and from the induction of presynaptic homeostatic potentiation (PHP), rivaling the sensitivity of chemical dyes.

(3) The improved postsynaptic SynapGCaMP8m is shown to approach the resolution of electrophysiology in resolving quantal events.

(4) The authors created a publicly available pipeline that streamlines and standardizes analysis of calcium imaging data.

Weaknesses:

(1) Given the superior performance of GCaMP8m in the vesicle-tethered and postsynaptic applications, an analysis of its functionality at individual active zones ("Bar8m") would be a useful addition to this compendium, especially since the authors show that the faster kinetics of GCaMP8f are still not fast enough to resolve active zone-specific calcium dynamics.

(2) Description of the CaFire pipeline could be clearer (for example, what exactly is the role of Excel?), and the GitHub user guide could be more fleshed out (with the addition of example ImageJ scripts and analyzed images).

Reviewer #2 (Public review):

Summary

Calcium ions play a key role in synaptic transmission and plasticity. To improve calcium measurements at synaptic terminals, previous studies have targeted genetically encoded calcium indicators (GECIs) to pre- and postsynaptic locations. Here, Chen et al. improve these constructs by incorporating the latest GCaMP8 sensors and a stable red fluorescent protein to enable ratiometric measurements. In addition, they develop a new analysis platform, 'CaFire', to facilitate automated quantification. Using these tools, the authors demonstrate favorable properties of their sensors relative to earlier constructs. Impressively, by positioning postsynaptic GCaMP8m near glutamate receptors, they show that their sensors can report miniature synaptic events with speed and sensitivity approaching that of intracellular electrophysiological recordings. These new sensors and the analysis platform provide a valuable tool for resolving synaptic events using all-optical methods.

Strengths:

The authors present a rigorous characterization of their sensors using well-established assays. They employ immunostaining and super-resolution STED microscopy to confirm correct subcellular targeting. Additionally, they quantify response amplitude, rise and decay kinetics, and provide side-by-side comparisons with earlier-generation GECIs. Importantly, they show that the new sensors can reproduce known differences in evoked Ca²⁺ responses between distinct nerve terminals. Finally, they present what appears to be the first simultaneous calcium imaging and intracellular mEPSP recording to directly assess the sensitivity of different sensors in detecting individual miniature synaptic events.

Weaknesses:

Major points:

(1) While the authors rigorously compared the response amplitude, rise, and decay kinetics of several sensors, key parameters like brightness and photobleaching rates are not reported. I feel that including this information is important as synaptically tethered sensors, compared to freely diffusible cytosolic indicators, can be especially prone to photobleaching, particularly under the high-intensity illumination and high-magnification conditions required for synaptic imaging. Quantifying baseline brightness and photobleaching rates would add valuable information for researchers intending to adopt these tools, especially in the context of prolonged or high-speed imaging experiments.

(2) In several places, the authors compare the performance of their sensors with synthetic calcium dyes, but these comparisons are based on literature values rather than on side-by-side measurements in the same preparation. Given differences in imaging conditions across studies (e.g., illumination, camera sensitivity, and noise), parameters like indicator brightness, SNR, and photobleaching are difficult to compare meaningfully. Additionally, the limited frame rate used in the present study may preclude accurate assessment of rise times relative to fast chemical dyes. These issues weaken the claim made in the abstract that "...a ratiometric presynaptic GCaMP8m sensor accurately captures .. Ca²⁺ changes with superior sensitivity and similar kinetics compared to chemical dyes." The authors should clearly acknowledge these limitations and soften their conclusions. A direct comparison in the same system, if feasible, would greatly strengthen the manuscript.

(3) The authors state that their indicators can now achieve measurements previously attainable with chemical dyes and electrophysiology. I encourage the authors to also consider how their tools might enable new measurements beyond what these traditional techniques allow. For example, while electrophysiology can detect summed mEPSPs across synapses, imaging could go a step further by spatially resolving the synaptic origin of individual mEPSP events. One could, for instance, image MN-Ib and MN-Is simultaneously without silencing either input, and detect mEPSP events specific to each synapse. This would enable synapse-specific mapping of quantal events - something electrophysiology alone cannot provide. Demonstrating even a proof-of-principle along these lines could highlight the unique advantages of the new tools by showing that they not only match previous methods but also enable new types of measurements.

(4) For ratiometric measurements, it is important to estimate and subtract background signals in each channel. Without this correction, the computed ratio may be skewed, as background adds an offset to both channels and can distort the ratio. However, it is not clear from the Methods section whether, or how, background fluorescence was measured and subtracted.

(5) At line 212, the authors claim "... GCaMP8m showing 345.7% higher SNR over GCaMP6s....(Fig. 3D and E) ", yet the cited figure panels do not present any SNR quantification. Figures 3D and E only show response amplitudes and kinetics, which are distinct from SNR. The methods section also does not describe details for how SNR was defined or computed.

(6) Lines 285-287 "As expected, summed ΔF values scaled strongly and positively with AZ size (Fig. 5F), reflecting a greater number of Cav2 channels at larger AZs". I am not sure about this conclusion. A positive correlation between summed ΔF values and AZ size could simply reflect more GCaMP molecules in larger AZs, which would give rise to larger total fluorescence change even at a given level of calcium increase.

(7) Lines 313-314: "SynapGCaMP quantal signals appeared to qualitatively reflect the same events measured with electrophysiological recordings (Fig. 6D)." This statement is quite confusing. In Figure 6D, the corresponding calcium and ephys traces look completely different and appear to reflect distinct sets of events. It was only after reading Figure 7 that I realized the traces shown in Figure 6D might not have been recorded simultaneously. The authors should clarify this point.

(8) Lines 310-313: "SynapGCaMP8m .... striking an optimal balance between speed and sensitivity", and Lines 314-316: "We conclude that SynapGCaMP8m is an optimal indicator to measure quantal transmission events at the synapse." Statements like these are subjective. In the authors' own comparison, GCaMP8m is significantly slower than GCaMP8f (at least in terms of decay time), despite having a moderately higher response amplitude. It is therefore unclear why GCaMP8m is considered 'optimal'. The authors should clarify this point or explain their rationale for prioritizing response amplitude over speed in the context of their application.

Reviewer #3 (Public review):

Genetically encoded calcium indicators (GECIs) are essential tools in neurobiology and physiology. Technological constraints in targeting and kinetics of previous versions of GECIs have limited their application at the subcellular level. Chen et al. present a set of novel tools that overcome many of these limitations. Through systematic testing in the Drosophila NMJ, they demonstrate improved targeting of GCaMP variants to synaptic compartments and report enhanced brightness and temporal fidelity using members of the GCaMP8 series. These advancements are likely to facilitate more precise investigation of synaptic physiology.

This is a comprehensive and detailed manuscript that introduces and validates new GECI tools optimized for the study of neurotransmission and neuronal excitability. These tools are likely to be highly impactful across neuroscience subfields. The authors are commended for publicly sharing their imaging software.

This manuscript could be improved by further testing the GECIs across physiologically relevant ranges of activity, including at high frequency and over long imaging sessions. The authors provide a custom software package (CaFire) for Ca2+ imaging analysis; however, to improve clarity and utility for future users, we recommend providing references to existing Ca2+ imaging tools for context and elaborating on some conceptual and methodological aspects, with more guidance for broader usability. These enhancements would strengthen this already strong manuscript.

eLife Assessment

This important study describes a non-canonical role for IκBα in regulating mouse embryonic stem cell pluripotency and differentiation, independent of the classical NF-κB pathway. The conclusions are convincingly supported through orthogonal approaches and separation of function mutants. The findings add new insight into pluripotency regulation in mouse cells.

Reviewer #1 (Public review):

Summary:

This study probes the role of the NF-κB inhibitor IκBa in the regulation of pluripotency in mouse embyronic stem cells (mESCs). It follows from previous work that identified a chromatin-specific role for IκBa in the regulation of tissue stem cell differentiation. The work presented here shows that a fraction of IκBa specifically associates with chromatin in pluripotent stem cells. Using three Nfkbia-knockout lines, the authors show that IκBa ablation impairs the exit from pluripotency, with embryonic bodies (an in vitro model of mESC multi-lineage differentiation) still expressing high levels of pluripotency markers after sustained exposure to differentiation signals. The maintenance of aberrant pluripotency gene expression under differentiation conditions is accompanied by pluripotency-associated epigenetic profiles of DNA methylation and histone marks. Using elegant separation of function mutants identified in a separate study, the authors generate versions of IκBa that are either impaired in histone/chromatin binding or NF-κB binding. They show that the provision of the WT IκBa, or the NF-κB-binding mutant can rescue the changes in gene expression driven by loss of IκBa, but the chromatin-binding mutant can not. Thus the study identifies a chromatin-specific, NF-κB-independent role of IκBa as a regulator of exit from pluripotency.

Strengths:

The strengths of the manuscript lie in:<br /> (a) the use of several orthogonal assays to support the conclusions on the effects of exit from pluripotency;<br /> (b) the use of three independent clonal Nfkbia-KO mESC lines (lacking IκBa), which increase confidence in the conclusions; and<br /> (c) the use of separation of function mutants to determine the relative contributions of the chromatin-associated and NF-κB-associated IκBa, which would otherwise be very difficult to unpick.

Weaknesses:

No notable weaknesses remain in this revised version.

Reviewer #2 (Public review):

Summary:

This manuscript investigates the role of IκBα in regulating mouse embryonic stem cell (ESC) pluripotency and differentiation. The authors demonstrate that IκBα knockout impairs the exit from the naïve pluripotent state during embryoid body differentiation. Through mechanistic studies using various mutants, they show that IκBα regulates ESC differentiation through chromatin-related functions, independent of the canonical NF-κB pathway.

Strengths:

The authors nicely investigate the role of IκBα in pluripotency exit, using embryoid body formation and complementing the phenotypic analysis with a number of genome-wide approaches, including transcriptomic, histone marks deposition, and DNA methylation analyses. Moreover, they generate a first-of-its-kind mutant set that allows them to uncouple IκBα's function in chromatin regulation versus its NF-κB-related functions. This work contributes to our understanding of cellular plasticity and development, potentially interesting a broad audience including developmental biologists, chromatin biology researchers, and cell signaling experts.

Weaknesses:

Future experiments will likely help establish a more direct mechanistic link between IκBα activity and the chromatin remodeling events observed in pluripotent cells.

Reviewer #1 (Public review):

Summary:

The authors define the principles that, based on first principles, should be guiding the optimisation of transcription factors with intrinsically disordered regions (IDR). The authors introduce an original search process, coined "octopusing", that involves transcription factor IDR and their binding affinities to optimise search times and binding affinities. The first part concerns the optimal strategies to define binding affinities to the genome in the receiving region that is called the "antenna", highlighting the following: (i) reduce the target to IDR-binding distance on the genome, (ii) optimise the distance between the DNA binding domain and the binding sites on the IDR to be as close as possible to the distance between their binding sites on the genome; (iii) keep the same number of binding sites and their targets and modulate this number with binding strength, reducing them with increased strength; (iv) modulate the binding strength to be above a threshold that depends on the proportion of IDR binding sites in the antenna. The second part concerns the scaling of the search time in function of key parameters such as the volume of the nucleus, and the size of the antenna, derived as a combination of 3D search and 1D "octopusing". The third part focuses on validation, where the current results are compared to binding probability data from a single experiment, and new experiments are proposed to further validate the model as well as testing designed transcription factors.

Strengths:

The strength of this work is that it provides simple, interpretable and testable theoretical conclusions. This will allow the derived design principles to be understood, evaluated and improved in the future. The theoretical derivations are rigorous. The authors provide a comparison to experiments, and also propose new experiments to be performed in the future. This is a great value in the paper since it will set the stage and inspire new experimental techniques. Further, the field needs inspiration and motivation to develop these techniques, since they are required to benchmark the transcription factors designed with the methods presented in this paper, as well as to develop novel data based or in vivo methods that would greatly benefit the field. As such, this paper is a fundamental contribution to the field.

Weaknesses:

The model presents many first principles to drive the design of transcription factors, but arguably, other principles and mechanisms might also play a role by being beneficial to the search and binding process. These other principles are mentioned at the end of the discussion part of the paper. On the other hand, an important task left to do, is to critically consider these principles altogether, and analyse the available data to quantify which role is predominant among transcription factors IDRs functions. Further, since one function doesn't exclude another, a theoretical investigation of possible crosstalk, interaction, and cooperativity of those different hypothetical functions is still missing.

Reviewer #2 (Public review):

Summary:

This is an interesting theoretical exploration of how a flexible protein domain, which has multiple DNA-binding sites along it, affects the stability of the protein-DNA complex. It proposes a mechanism ("octopusing") for protein doing a random walk while bound to DNA which simultaneously enables exploration of the DNA strand and stability of the bound state.

Strengths:

Stability of the protein-DNA bound state and the ability of the protein to perform 1d diffusion along the DNA are two properties of a transcription factor that are usually seen as being in opposition of each other. The octopusing mechanism is an elegant resolution of the puzzle of how both could be accommodated. This mechanism has interesting biological implications for the functional role of intrinsically disordered domains in transcription factor (TF) proteins. They show theoretically how these domains, if flexible and able to make multiple weak contacts with the DNA, can enhance the ability of the TF to efficiently find their binding site on the DNA from which they exert control over the transcription of their target gene. The paper concludes with a comparison of model predictions with experimental data which gives further support to the proposed mechanism. Overall, this is an interesting and well-executed theoretical paper that proposes an interesting idea about the functional role for IDR domains in TFs.

Weaknesses:

It is not clear how ubiquitous among eukaryotic transcription factors are the DNA binding sites for multiple subdomains along the IDR, which are assumed by the model. These assumptions though, provide interesting points of departure for further experiments.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Summary:

The authors define the principles that, based on first principles, should be guiding the optimisation of trascription factors with intrinsically disordered regions (IDR). The first part of the study defines the following principles to optimize the binding affinities to the genome in the receiving region that is called the ”antenna”: (i) reduce the target to IDR-binding distance on the genome, (ii) optimise the distance betwee the DNA binding domain and the binding sites on the IDR to be as close as possible to the distance between their binding sites on the genome; (iii) keep the same number of binding sites and their targets and modulate this number with binding strength, reducing them with increased strenght; (iv) modulate the binding strenght to be above a threshold that depends on the proportion of IDR binding sites in the antenna. The second part defines the scaling of the seach time in function of key parameters such as the volume of the nucleus, and the size of the antenna, derived as a combination of 3D search of the antenna and 1D ”octopusing” on the antenna. The third part focuses on validation, where the current results are compared to binding probabilith data from a single experiment, and new experiment are proposed to further validate the model as well as testing designed transcription factors.

Strengths:

The strength of this work is that it provides simple, interpretable and testable theoretical conclusions. This will allow the derived design principles to be understood, evaluated and improved in the future. The theoretical derivations are rigorous. The authors provides a comparison to experiments, and also propose new experiments to be performed in the future, this is a great value in the paper since it will set the stage and inspire new experimental techniques. Further, the field needs inspiration and motivations to develop these techniques, since they are required to benchmark the transcription factors designed with the methods presented in this paper, as well as to develop novel data based or in vivo methods that would greatly benefit the field. As such, this paper is a fundamental contribution to the field.

Weaknesses:

The model assumption that the interaction between the transcription factor and the DNA outside of the antenna region is negligible is probably too strong for many/most transcription factors, particularly in organisms with a longer genome than yeasts. The model presents many first principles to drive the design of transcription factor, but arguably, other principles and mechanisms might also play a role by being beneficial to the search and binding process. Specifically: (i) a role of the IDR in complex formation and cooperativity between multiple trascription factors, (ii) ability of the IDR to do parallel searching based on multiple DNA binding sites spaced by disordered regions, (iii) affinity of the IDR to specific compartmentalisations in the nucleus reducing the search time, etc. The paper would be improved by a discussion over alternative mechanisms.

We thank the reviewer for highlighting that our work delivers simple, interpretable and rigorously derived conclusions, backed by experimental comparison and concrete proposals for future studies.

Regarding interactions outside the antenna region, Supplementary S10 shows that the non-specific IDR–DNA interactions (on the order of 1 kBT) only slightly alter the 3D diffusion coefficient and thus do not affect our conclusions regarding the optimal search process.

We have also added sentences in the discussion section regarding the alternative mechanism.

Reviewer #2 (Public review):

Summary:

This is an interesting theoretical exploration of how a flexible protein domain, which has multiple DNAbinding sites along it, affects the stability of the protein-DNA complex. It proposes a mechanism (”octopusing”) for protein doing a random walk while bound to DNA which simultaneously enables exploration of the DNA strand and stability of the bound state.

Strengths:

Stability of the protein-DNA bound state and the ability of the protein to perform 1d diffusion along the DNA are two properties of a transcription factor that are usually seen as being in opposition of each other. The octopusing mechanism is an elegant resolution of the puzzle of how both could be accommodated. This mechanism has interesting biological implications for the functional role of intrinsically disordered domains in transcription factor (TF) proteins. They show theoretically how these domains, if flexible and able to make multiple weak contacts with the DNA, can enhance the ability of the TF to efficiently find their binding site on the DNA from which they exert control over the transcription of their target gene. The paper concludes with a comparison of model predictions with experimental data which gives further support to the proposed model. Overall, this is an interesting and well executed theoretical paper that proposes an interesting idea about the functional role for IDR domains in TFs.

Weaknesses:

IDR domains are assumed flexible which I believe is not always the case. Also, I’m not sure how ubiquitous are the assumed binding sites on the DNA for multiple subdomains along the IDR. These assumptions though seem like interesting points of departure for further experiments.

We thank the reviewer for their careful and insightful evaluation of our work. In particular, we appreciate your emphasis on the inherent trade-off between binding stability and one-dimensional diffusion, and your recognition of how the octopusing mechanism elegantly reconciles these conflicting requirements.

To address the flexibility of TFs with IDRs, we incorporated the spring’s rest length—effectively introducing tunable rigidity—in Supplementary Section S1, and we show that our design principles for binding probability remain robust. Indeed, this is a highly interesting point; a comprehensive study will require more detailed modeling alongside experimental validation.

We acknowledge that the current evidence for IDR-directed DNA binding is primarily derived from a limited number of well-studied cases, particularly Msn2 in yeast, and the ubiquity of this mechanism across diverse transcription factors remains to be established.

Reviewer #1 (Recommendations for the authors):

The paper jumps to fast to the results, an larger introduction might improve the paper, the current introduction jumps too fast to results. Further, line 50, I don’t think that the figure is properly referenced. The formula 2 is confusing since what is the target volume V1 is not explained in the context of the formula, please expand the explanations.

We appreciate the reviewer’s valuable recommendations. We have expanded the Introduction, clarified V₁, and updated the line 50.

Reviewer #2 (Recommendations for the authors):

I have some mostly minor suggestions to the authors for improving the manuscript:

In the abstract and introduction on at least two occasions the authors talk about IDRs as though they’re necessarily flexible. My understanding is that, while this is a very reasonable assumption, I don’t think this is something we know with any certainty for most IDRs. If the authors agree with my assessment I think they should reflect this uncertainty in the writing.

Thank you for the recommendations. We revised the wording to reflect the uncertainty, changing it to: “... commonly assumed to behave as a long, flexible...” and “...can be assumed as flexible....”.

It took me a bit of time to figure out what’s going on in Figure 1b. To help the reader I would suggest labeling the DBD targets (yellow square) and the IDR targets (gray squares) as such. The figure also left me guessing whether the DBD domain can bind to the IDR targets non-specifically? (I presume not.) This also brought a slightly bigger question into focus for me, wouldn’t the presence of the IDR binding ”sites” (since these ”sites” are on the protein I think the term ”domains” instead of ”sites” ) mean that this would increase the time the protein is bound non-specifically somewhere far from the target thereby increasing the search time. Or is the ability of the protein to bind specifically to DNA away from the DBD target ignored?

We have labeled the DBD targets and IDR targets in the figure. ‘Domains’ usually refers to structured parts; we keep using ‘sites’ and clarify that they correspond to short linear motifs.

The reviewer is correct. Our model omits any non-specific binding between the DBD and IDR-binding targets, as well as between the TF and other DNA regions. If such interactions were to substantially lengthen the search time, they would effectively revert our mechanism to the classical bacterial facilitateddiffusion model, which is generally considered inappropriate for IDR-mediated TF search in eukaryotic cells. However, Supplementary Figure S10 demonstrates that non-specific IDR–DNA interactions induce only marginal changes in the effective three-dimensional diffusion coefficient within complex chromatin environments, and therefore do not alter our conclusions regarding the optimal search process.

In Equation 2 and the text that follows I was left wondering what is the target volume V1. Also, I think it would be helpful to the reader to give them a sense of scale for the dimension full quantities appearing in Equation 2. This is done later when comparing the theory to experimental data, but I think it would be helpful to give a sense of size earlier in the manuscript.

V₁ denotes the volume of the IDR–binding target region, which is on the order of bp³. f(d,l₀) has units of inverse volume. We have included the units and specified the order of magnitude of V₁ after Equation 2.

The binding energy EB is discussed a number of times but it wasn’t clear to me that this quantity referred to the energy per IDR site on the DNA or the total energy when the IDR is bound to DNA. In Figure 1 it would seem that the model allows only one IDR domain bound at a given time but I think the model allows for multiple IDR domains to be bound to the IDR target sites simultaneously. Right? Maybe make this clear in the Figure and the text.

E_B denotes the binding energy per binding site, where each site corresponds to a short linear motif. Yes, we allow for multiple IDR domains to be bound to the IDR target sites simultaneously. We have clarified the definition of E_B and adjusted the figure slightly to avoid any misunderstanding.

After Eq 4 the discussion suggests that for ϕ << 1 the threshold energy is much greater than kBT, but that’s hard to imagine given that the logarithmic dependence of the latter on the former. Also in Figure 2d it seems that the threshold energy is about 8 kBT. Clearly this is not a big deal, just thought the authors might want to revise the language.

Thank you. We now clarify the sentence using the representative values of ϕ and E_th after Equation 4.

Right after Figure 2 there is a discussion of the different parameters that the authors vary. I suggest having a figure that illustrates these parameters (possibly in Figure 1b) to make it easier to follow the discussion.

We have added explanations of the relevant parameters in Figure 1 for clarity.

When discussing the dynamics of search the result stated is that the search time is minimum for a specific value of R. I think it would be useful to translate this into a TF concentration. Also, if R represents the radius of the cells nucleus 1/6 um is almost an order of magnitude smaller than the size of a typical nucleus. Is this a worry? Either way some clarification of this number would be helpful.

Thank you for the suggestion. As noted later in this section, we have translated R into an equivalent TF concentration, and we clarify that we assume the scaling of the minimum search time remains unchanged when extrapolated to the size of a typical nucleus.

There is a comment regarding the role of the DNA persistence length and how it was not accounted for. It would be helpful if the authors could add a sentence or two explains how a folded DNA conformation, as is the case in the nucleus, would affect their calculation. (So that the reader gets an idea without having to get into the details described in the Supplement).

Thank you. We have revised the sentence to: “We have verified that reducing the DNA persistence length, which promotes increased DNA coiling, results in only a modest increase in mean search time. Even under extreme coiling conditions, the increase remains below 30% of the baseline value, as detailed in Supplementary S9.”.

eLife Assessment

This valuable work shows that subcortically-generated behaviors, like grooming, can have widespread representations in cortical activity. While the evidence is solid, additional analyses are necessary to strengthen the claims associated with outsized cortical representations of grooming onsets, as well as to address atypical grooming events. This work will be of interest to neuroscientists interested in how subcortically-generated behaviors are represented across the cortex.

Reviewer #1 (Public review):

In their manuscript, Michelson et al use a combination of mesoscopic 1p and single-cell resolution 2p imaging to characterise cortical encoding of grooming behaviour. Despite their subcortical locus of control (and non-reliance on cortex), the authors report that grooming movements are accompanied by widespread activation of dorsal cortex. Different grooming movements elicit distinct spatiotemporal cortical activity patterns. They find that cortical engagement is greater at the beginning of grooming episodes than at their end. They also report greater cortical activation for atypical unilateral grooming movements seen under head-restraint in comparison to cortical activity during bilateral movements typical of unrestrained or spontaneous grooming.

While this is not the first study to report cortical representations of subcortically controlled behaviours, and the authors themselves cite many previous reports of cortical activation during locomotion and even grooming (Sjöbom et al 2020), the value of the present study lies in their use of imaging to reveal the widespread nature of cortical activation during execution of a complex, innate behaviour. I also appreciate the systematic approach used by the authors to break down grooming episodes into their constituent movements and reveal their transition structure.

I do have concerns, however, that some of the authors' claims are insufficiently supported by their results, and more analysis is required to convincingly rule out alternative interpretations.

(1) One possible explanation for the gradual decline in cortical activity is that unilateral movements associated with greater cortical activation dominate early in grooming episodes, whereas bilateral movements that elicit weaker cortical activity dominate later (Figure 3G and 2C). The authors could check whether cortical activity associated with the *same* grooming movement is constant or declines during such episodes. A related point: doesn't the regression analysis shown in Figure 3, Supplement 2, assume that a stationary relationship between movement and spatiotemporal patterns of cortical activity?

(2) From the decline in cortical responses during long grooming episodes, the authors suggest that "mesoscale cortical activity mostly reflects the initiation of subcortically-mediated behaviors, rather than the behavior itself". The authors have taken a lot of trouble to come up with a rich, detailed segmentation and clustering of the grooming behaviour into its constituent movements (Figure 1). Therefore, I am somewhat surprised that they make this claim solely from analysis of averaged cortical activity during nearly minute-long grooming episodes rather than a higher time resolution analysis of transitions between distinct grooming movements (like the prior study by Sjöbom et al and related work in striatal encoding of innate movement sequences by Markowitz et al).

(3) The authors find that unilateral, atypical grooming movements elicit cortical activity that is distinct from the more naturalistic bilateral movements. They interpret this as reflecting the temporal transition structure of the behaviour. However, an alternative explanation is that the differences (or similarities) in evoked activity simply reflect differences (or similarities) in the kinematics of these movements, with bilateral movements appearing more similar to each other than to unilateral movements. A related point: there is little description of the "non-grooming forelimb movements". Were these kinematically similar to the unilateral forelimb movements, which may explain why they cluster together in Figure 4H?

(4) Page 13, last paragraph: the authors suggest that similar encoding of non-grooming forelimb movements and unilateral grooming movements may reflect a shared reliance on the cortex. This is rather speculative. Several studies have demonstrated that voluntary unilateral movements employed for reaching or lever pressing are not generally reliant on the cortex (Whishaw et al, Beh Brain Res, 1991; Kawai et al, 2015). There isn't, in my opinion, a broad consensus for the authors' statement that "reaching for food is a cortex-dependent action". Rather than extrapolating from past studies, could the authors not experimentally assess whether unilateral grooming movements are more sensitive to cortical silencing than bilateral ones, possibly revealing a cortical locus of control?

Reviewer #2 (Public review):

Summary:

In this manuscript, Michelson, Gupta, and Murphy use calcium imaging to map the distribution of neural activity across the cerebral cortex of grooming, head-restrained mice. Animals groomed spontaneously and in response to wetting of the face. Individual movement elements, such as bilateral strokes across the face, resembled those observed in freely-moving animals. Sequencing of movement elements was structured, but did not consist of full "syntactic grooming chains." Widefield imaging across the cortex revealed distinct patterns of activity for distinct movement elements. Individual neurons responded strongly during movement and had largely similar properties across cortical areas.

Strengths:

In my opinion, this is a solid paper that will be of interest to the mouse sensorimotor neuroscience community. The experiments are technically sound, the text is well-written, and the figures are clear. The activity maps are presented in standardized Allen Atlas coordinates, and I expect they will be very useful for future studies of orofacial and limb movement.

Weaknesses:

While the manuscript provides a valuable description of cortical activity during head-restrained grooming, I think it could engage a bit more with contemporary theories and debates in cortical physiology and motor control. The Abstract nicely highlights an apparent paradox: the motor cortex sends strong projections to the spinal cord, and is strongly modulated during behaviors like grooming. Nevertheless, blocking corticospinal traffic by inactivating or lesioning the motor cortex leaves such behaviors intact. There are several potential resolutions to this paradox. First, cortical activity during grooming could be confined to an "output-null" subspace that is responsible for monitoring sensorimotor events and preparing voluntary movements, but does not drive muscle activity (c.f. work in the macaque: Kaufman et al., Nature Neuroscience 2014; Churchland & Shenoy, Nature Reviews Neuroscience 2024). Second, cortical activity during grooming could be transmitted to lower centers, but gated out through inhibition. Third, it is possible that cortical activity in intact animals does contribute to muscle activation during grooming, but following a lesion or inactivation, other descending pathways compensate for the cortical deficit. The authors might wish to discuss their findings in light of these considerations.

In the first paragraph of the Introduction, it could be made clearer which results are specific to mice. The Niell & Stryker finding, for example, holds in mice, but not marmosets (Liska et al., eLife 2024).

The "hotspots" in Figure 3G appear to be more anterior during bilateral elliptical than unilateral elliptical movements. How do the authors interpret this finding?

The distribution of single-neuron responses looks relatively similar across cortical areas, including forelimb, hindlimb, and trunk somatosensory cortex, and primary and secondary forelimb motor cortex. What do the authors make of this?

Reviewer #3 (Public review):

Summary:

The authors use a combination of a head-fixed grooming paradigm, single-photon mesoscale, and wide-field-of-view two-photon calcium imaging to characterize cortical activity patterns during evoked grooming. Previous work has shown that grooming behavior does not require cortex, but that there are neuronal representations of grooming in motor cortex. The authors extend these findings by showing cortex-wide activation patterns at the meso-scale that relate to distinct grooming elements. This activation is strongest at grooming onset, but declines over the course of extended grooming periods. They also find similar activity patterns during licking/drinking behavior. Two-photon imaging further revealed that individual neurons across the cortex are preferentially activated by grooming. While their activity also declines after grooming onset, they remain active throughout grooming periods. This work extends previous findings by revealing that grooming and other subcortically-generated behaviors may be represented not only in motor cortex, but across dorsal cortex, both on the mesoscale and single neuron levels. These findings may lead to further investigation into the role of cortical activity during subcortically generated behaviors.

Strengths:

(1) Detailed characterization of grooming behavior in a head-fixed paradigm.

(2) Combination of single photon mesoscale and two-photon wide field-of-view imaging to characterize grooming (and licking)-related activity across dorsal cortex on multiple levels

Weaknesses:

(1) The behavior observed in the head-fixed grooming paradigm only partially resembles spontaneous grooming, lacking typical elements of the syntactic chain, while additionally evoking non-typical behaviors, resembling unilateral reaches, making the interpretation of the observations and their relevance to natural behaviors difficult. Furthermore, the nature of the non-typical movements (which may be cortex-dependent while typical grooming is not) is not explored.

(2) Two important findings in relation to the neural representations of individual grooming behaviors remain unclear:

a) The authors state that individual grooming behaviors did not have distinct neuronal representations (except unilateral grooming; Figure 4G) - it remains unclear how this fits with the observation of distinct activation maps during the different grooming behaviors. Should this differential activation not also correspond to distinct activation patterns of 'grooming' neurons across the cortex? Or do they mean that the activity in the 'grooming' neurons is not consistent across grooming instances and therefore no distinct representation can be detected?

b) The authors state that the 'typical' grooming behaviors do not have consistent activation patterns across animals (Figure 3 and supplements). It remains, therefore, unclear what the averaged activation maps really represent. Furthermore, this observation leaves several open questions: Are the activation patterns consistent in individual animals? Do differences across animals emerge due to differences in their behavior? And most importantly, can the actual behavior be decoded from the activation patterns?

(3) Multiple statements/conclusions are not supported by quantification of the data, but only by qualitative assessments, e.g.: lines 433-435: "In general, the maximally activated networks involved in licking and unilateral grooming behaviors 'appeared' to be the most consistent across animals compared to the bilateral grooming movements (Figure 3G)."; 436-437: "Averaged cortical activation maps associated with licking and elliptical behaviors were 'qualitatively similar' between evoked and spontaneous sessions, where the water drop was not applied".; 480-482: "The unique explained variance maps for the licking behavior 'differed' in the drinking context compared to the grooming context (Figure 3-figure supplement 3F)." The lack of quantification leaves the significance of these observations unclear.

(4) It remains unclear what the ongoing activity in 'grooming' neurons represents, since there is no detailed analysis of the relationship between activity and the detailed kinematics of the grooming movements.

The authors show that neuronal representations of grooming and other subcortical behaviors can be found across dorsal cortex and that these representations are at least to some degree specific to distinct behavioral elements. While this study does not reveal functional insights into the role of cortical representations of subcortically-generated behaviors, it is a step towards more in-depth studies. In the future, it will be important to determine whether these representations are efference copies or sensory-driven, or whether they affect the behavior, and if so, under which circumstances.

eLife Assessment

This valuable study applies transcranial direct current stimulation (tCDS) to the prefrontal cortex of non-human primates during two states: (1) propofol-induced unconsciousness; and (2) wakeful performance of a fixation task. The analysis offers incomplete evidence to indicate that the effect of tDCS on brain dynamics, as recorded with functional magnetic resonance imaging, is contingent on the state of consciousness during which the stimulation is applied. The findings will be of interest to researchers interested in brain stimulation and consciousness.

Reviewer #2 (Public review):

General comments

We thank the reviewers and editor for their thoughtful feedback. We are glad that the minor comments appear resolved. In this revision, we added subject-specific analyses, further FC comparisons, and clarified our rationale for stimulation parameters. We acknowledge that two concerns remain: (1) the 1 mA-2 mA sequence may introduce confounds, and (2) electric field modeling was not included due to technical limitations. We now explicitly note these as limitations in the manuscript and provide justification and discussion accordingly.

Major comments

R.2.1. For the anesthetized monkeys, the anode location differs between subjects, with the electrode positioned to stimulate the left DLFPC in monkey R and the right DLPFC in monkey N. The authors mention that this discrepancy does not result in significant differences in the electric field due to the monkeys' small head size. However, this is incorrect, as placing the anode on the left hemisphere would result in a much lower EF in the right DLPFC than placing the anode on the right side. Running an electric field simulation would confirm this. Additionally, the small electrode size suggested by the Easy cap configuration for NHP appears sufficient to stimulate the targeted regions focally. If this interpretation is correct, the authors should provide additional evidence to support their claim, such as a computational simulation of the EF distribution.

R.2.1 Authors' answer: We thank the Reviewer for the comments. First, regarding the reviewer's statement that placing the anode on the left hemisphere would result in a much lower EF in the right DLPFC than placing the anode on the right side, we would like to clarify that we did not use a typical 4 x 1 concentric ring high-definition setup (which consists of a small centre electrode surrounded by four return electrodes), but a two-electrode montage, with one electrode over the left or right PFC and the other one over the contralateral occipital cortex. According to EF modelling papers, a 4 x 1 high-definition setup would produce an EF that is focused and limited to the cortical area circumscribed by the ring of the return electrodes (Datta et al. 2009; Alam et al. 2016). Therefore, targeting the left or right DLPFC with a 4 x 1 setup would produce an EF confined to the targeted hemisphere of the PFC. In contrast, we expect the brain current flow generated with our 2-electrode setup to be broader, despite the small size of the electrodes, because there is no constraint from return electrodes. Thus, with our setup, the current is expected to flow between the PFC and the occipital cortex (see also our responses to comments R3.3., R.E.C.#2.1. and R.E.C.#2.2.).

Second, we would like to point out that in awake experiments, in which we stimulated the right PFC of both monkeys, there was no gross evidence of left or right asymmetry in the computed functional connectivity patterns (Figure 3A, Figure 3 - figure supplement 2A; Figure 5A). These results, showing that our stimulation montages did not induce asymmetric dynamic FC changes in NHPs, support the idea that our setups did not generate EFs that were spatially focused enough to alter brain activity in one hemisphere substantially more than the other.

Third, it is also worth noting that current evidence suggests that human brains are significantly more lateralized than those of macaques. Macaque monkeys have been found to have some degree of lateralized networks, but these are of lower complexity, and the lateralization is less pronounced and functionally organized than in humans. (Whey et al., 2014; Mantini et al., 2013). This suggests that, even if the stimulation were focal enough to stimulate the left or the right part of the PFC only, the behavioural effects would likely be similar.

Follow-up comment: Thank you for the detailed response and for referencing both experimental data and prior literature. While I appreciate the discussion on the lack of functional asymmetry and reduced lateralization in macaques, my original concern was about the physical distribution of the electric field (EF) due to different anode placements. Functional connectivity outcomes do not necessarily reflect EF symmetry, and without EF modeling, it's difficult to determine whether the stimulation affected both hemispheres equally. I understand the challenges of NHP-specific modeling, but even a simplified simulation or acknowledgment of this limitation in the manuscript would help clarify the interpretability of your results.

R.2.2. For the anesthetized monkeys, the authors applied 1 mA tDCS first, followed by 2 mA tDCS. A 20-minute stimulation duration of 1 mA tDCS is strong enough to produce after-effects that could influence the brain state during the 2 mA tDCS. This raises some concerns. Previous studies have shown that 1 mA tDCS can generate EF of over 1 V/m in the brain, and the effects of stimulation are sensitive to brain state (e.g., eye closed vs. eye open). How do the authors ensure that there are no after-effects from the 1 mA tDCS? This issue makes it challenging to directly compare the effects of 1 mA and 2 mA stimulation.<br /> R.2.2 Authors' answer: We agree with the reviewer's comment that 1 mA tDCS may induce aftereffects, as has been observed in several human studies (e.g., (Jamil et al. 2017, 2020). Although the differences between the 1 mA post-stimulation and baseline conditions were not significant in our analyses, it's still possible that the stimulation produced some effects below the threshold of significance that may contribute, albeit weakly, to the changes observed during

Follow-up comment: Thank you for the clarification and for acknowledging the potential for 1 mA after-effects. While I appreciate the authors' transparency and the amendment to the manuscript, I still find it important that the limitation be clearly stated in the Discussion section. The fact that 2 mA stimulation always followed 1 mA introduces a potential confound, making it difficult to attribute observed changes uniquely to 2 mA. If a counterbalanced design was not feasible, I would recommend explicitly noting this as a limitation in the interpretation of dose-dependent effects.

R.2.3. The occurrence rate of a specific structural-functional coupling pattern among random brain regions shows significant effects of tDCS. However, these results seem counterintuitive. It is generally understood that non-invasive brain stimulation tends to modulate functional connectivity rather than structural or structural-functional connectivity. How does the occurrence rate of structural-functional coupling patterns provide a more suitable measure of the effectiveness of tDCS than functional connectivity alone? I would recommend that the authors present the results based on functional connectivity itself. If there is no change in functional connectivity, the relevance of changes in structural-functional coupling might not translate into a meaningful alteration in brain function, making it unclear how significant this finding is without corresponding functional evidence.

R.2.3. Authors' answer: First of all, we would like to make it clear that the occurrence rate of patterns as a function of their SFC is not intended to be used or seen as a 'better' measure of the efficacy of tDCS. Instead, it is one aspect of the effects of tDCS on whole-brain functional cortical dynamics, obtained from refined measures (phase-coherences), that specifically addresses the coupling between structure and function. This type of analysis is further motivated by its increasing use in the literature due to its suspected relationship to wakefulness (e.g., (Barttfeld et al. 2015, Demertzi et al. 2019; Castro et al. 2023)). Also, in our analysis, the structure is kept constant: the connectivity matrix used to correlate the functional brain states is always the same (CoCoMac82). Thus, the influence of tDCS on the structure-function side can only be explained by modulating the functional aspects, as suggested by intuition and previous results.

Then, we agree with the reviewer that studying the functional changes induced by tDCS alone could be valuable. However, usual metrics used in FC analysis are usually done statistically: FC-states are either computed through averaging spatial correlations over time, then analyzed through graph-theoretical properties for instance (or by just directly computing the element-wise differences), or either by considering the properties of the different visited FC-states by computing spatial correlations over a sliding time-window, and then similar analysis can be done as previously explained. But these are static metrics, if the states visited are essentially the same (which is expected from non-invasive neuromodulations that haven't already demonstrated strong and/or characteristic impact), but the dynamical process of visiting said states changes, one would see no difference in that regard. As such, in the case of resting-state fMRI, differences in FCs are hard to interpret given that between-sessions within-condition differences are usually found with some degree of variance for the respective conditions. Trying then to interpret between-condition differences is quite tricky in the case of subtle modulations of the system's activity. On the other hand, more subtle differences can be captured by considering more detailed analysis, such as using phase-based methods like we did, by incorporating some statistical learning component with regard to the dynamicity of the system (supervised learning for instance like we did followed by temporal & transition-based methodology), and by adding some dimensions along which one will be able to give some interpretation to the analysis. In our case we were interested in characterizing resting-state differences between stimulation conditions, which have nuanced and subtle interactions with the biological system. As such, classical measures of differences between FC states are likely to not be refined and precise enough. In fact, we propose additional files investigating those classically used measures such as differences in average FC matrices, or changes in functional graph properties (like modularity, efficiency and density) of the visited FC states. These figures show that, for the first case, comparing region-to-region specific FCs provides very few statistically significant results. With respect to the second part, we show that virtually no differences are observed in the properties of the functional states visited. These results suggest, as expected, that the actual brain states visited across the different stimulation conditions are topologically quite similar, and that only very few region-specific pairwise functional connectivities are particularly modulated by specific tDCS montages while, on the other hand, the actual dynamical process dictating how the brain activity passes from one state to another is in fact being influenced as shown by the dynamical analysis presented in the main figures in a more apparent and meaningful way (in that it is dependent on the montage, somewhat consistent with regard to the post-stimulations conditions, and can be made sense of by considering the theoretical effect of near-anodal versus near-cathodal neuromodulatory effects).

Actions in the text: We have added new supplementary files showing the effects of the stimulations on FC matrices and on classical functional graph properties in awake and anesthesia datasets (Supplementary Files 3 & 4). We have added new sentences about these new analyses on the effects of the stimulations on FC matrices and on classical functional graph properties in the Results section:<br /> Follow-up comment: Thank you for the detailed and comprehensive response. The clarification regarding the use of SFC dynamics and the additional analyses provided are convincing.

R2.4. The authors recorded data from only two monkeys, which may limit the investigation of the group effects of tDCS. As the number of scans for the second monkey in each consciousness condition is lower than that in the first monkey, there is a concern that the main effects might primarily reflect the data from a single monkey. I suggest that the authors should analyze the data for each monkey individually to determine if similar trends are observed in both subjects.

R.2.4. Authors' answer: We agree that the small number of subjects is a limitation of our study. However, we have already addressed these aspects by reporting statistical analyses that consider them, using linear models of such variables, and running them through ANOVA tests. In addition, we experimentally ensured that we recorded a relatively high number of sessions over a period of several years. Regardless, we agree that our study would benefit from further investigation into this matter. We have therefore prepared complementary figures showing the main analysis performed separately for the two monkeys as proposed, as well as further investigations into the inter-condition variability outmatching the inter-individual variability, itself being also outmatched by intra-individual changes.

Actions in the text: We have added a supplementary file showing the main analyses performed separately for the two monkeys (Supplementary File 2) and further investigations into the inter-condition variability (Supplementary Files 3 & 4). We have added new sentences about these analyses performed separately for the two monkeys in the Results section:

Follow-up comment: Thank you for addressing this concern and for providing the individual monkey analysis. The additional figures and statistical explanations are helpful and appreciated.

R2.5. Anodal tDCS was only applied to anesthetized monkeys, which limits the conclusion that the authors are aiming for. It raises questions about the conclusion regarding brain state dependency. To address this, it would be better to include the cathodal tDCS session for anesthetized monkeys. If cathodal tDCS changes the connectivity during anesthesia, it becomes difficult to argue that the effects of cathodal tDCS vary depending on the state of consciousness as discussed in this paper. On the other hand, if cathodal tDCS would not produce any changes, the conclusion would then focus on the relationship between the polarity of tDCS and consciousness. In that case, the authors could maintain their conclusion but might need to refine it to reflect this specific relationship more accurately.

R.2.5. Authors' answer: We agree with the reviewer that it would have been interesting to investigate the effects of cathodal tDCS in anesthetized monkeys. However, due to the challenging nature of the experimental procedures under anesthesia, we had to limit the investigations to only one stimulation modality. We chose to deliver anodal stimulation because, from a translational point of view, we aimed to provide new information on the effects of tDCS under anesthesia as a model for disorders of consciousness. It also made much more sense to increase the cortical excitability of the prefrontal cortex in an attempt to wake up the sedated monkeys rather than doing the opposite.

Actions in the text: We have added a new sentence in the Results section:

"Due to the challenging nature of the experimental procedures under anesthesia, we limited the investigations to only one stimulation modality. We chose to deliver anodal stimulation to provide new information on the effects of tDCS under anesthesia as a model for disorders of consciousness and to increase the cortical excitability of the PFC in an attempt to wake up the sedated monkeys."

Follow-up comment: Thank you for clarifying the rationale behind applying only anodal stimulation under anesthesia. While I appreciate the experimental constraints and the translational motivation, I would still encourage the authors to explicitly acknowledge in the Discussion that the absence of a cathodal condition under anesthesia limits the ability to dissociate polarity-specific effects from state-dependent effects. This clarification would help temper the conclusions and better reflect the scope of the current dataset.

Reviewer #3 (Public review):

Summary:

This study used transcranial direct current stimulation administered using small 'high definition' electrodes to modulate neural activity within the non-human primate prefrontal cortex during both wakefulness and anaesthesia. Functional magnetic resonance imaging (fMRI) was used to assess neuromodulatory effects of stimulation. The authors report on modification of brain dynamics during and following anodal and cathodal stimulation during wakefulness and following anodal stimulation at two intensities (1 mA, 2 mA) during anaesthesia. This study provides some support that prefrontal direct current stimulation can alter neural activity patterns across wakefulness and sedation in monkeys.

Strengths and Weaknesses:

A key strength of this work is the use of fMRI-based methods to track changes in brain activity with good spatial precision. Another strength is the exploration of stimulation effects across wakefulness and sedation, which has the potential to provide novel information on the impact of electrical stimulation across states of consciousness. The authors should be commended for undertaking this challenging and important work.

The lack of a sham stimulation condition is a limitation of the study, as it somewhat restricts the certainty with which the results can be attributed to the active stimulation as opposed to other external factors such as drowsiness or fatigue as a result of the experimental procedure? Nevertheless, I acknowledge the demanding nature of performing this work in non-human primates and that only runs with high fixation rates were included, which should have helped reduce any fatigue-related effects.

In the anaesthesia condition, the authors investigated the effects of two intensities of stimulation (1 mA and 2 mA). However, it is possible that the initial 1 mA stimulation block might have caused some level of plasticity-related changes in neural activity that could have potentially interfered with the following 2 mA block due to the lack of a sufficient wash-out period. This potentially limits the findings from the 2 mA block as they cannot be interpreted as completely separate to the initial 1 mA stimulation period, given that they were administered consecutively. However, I do acknowledge the author's point that differences between the 1 mA post-stimulation and baseline conditions were not significantly different, which provides some evidence against this possibility.

The different electrode placement for the two anaesthetised monkeys (i.e., Monkey R: F3/O2 montage, Monkey N: F4/O1 montage) is potentially problematic, as it might have resulted in stimulation over different brain regions. Electric field models of brain current flow for the monkeys would really be needed to understand with reasonable certainty, however, I recognise that these models are generally designed for human studies making their integration into non-human primate studies challenging.

Finally, the sample size is obviously small. However, I realise this is often a limitation in non-human primate research, which can be both expensive and labour intensive.

Assessment:

This manuscript presents some novel insights into the effects of transcranial direct current stimulation on functional brain dynamics in awake and anaesthetised monkeys using MRI-based connectivity indices. Overall, the study presents several interesting and potentially impactful findings regarding stimulation-induced changes in brain activity. There are some limitations, such as the small sample size, lack of a sham stimulation control, and lack of electric field models, which, if included, would have, in my view, further helped improve the rigour of the study. Nevertheless, the manuscript presents several important findings, which warrant further analysis in future work.

Author response:

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

Reviewer #1 (Public review): 

Summary: 

In this work, the authors apply TDCS to awake and anesthetized macaques to determine the effect of this modality on dynamic connectivity measured by fMRI. The question is to understand the extent to which TDCS can influence conscious or unconscious states. Their target was the PFC. During the conscious states, the animals were executing a fixation task. Unconsciousness was achieved by administering a constant infusion of propofol and a continuous infusion of the muscle relaxant cisatracurium. They observed the animals while awake receiving anodal or cathodal hd-TDCS applied to the PFC. During the cathodal stimulation, they found disruption of functional connectivity patterns, enhanced structure-function correlations, a decrease in Shannon entropy, and a transition towards patterns that were more commonly anatomically based. In contrast under propofol anesthesia anodal hd-TDCS stimulation appreciably altered the brain connectivity patterns and decreased the correlation between structure and function. The PFC stimulations altered patterns associated with consciousness as well as those associated with unconsciousness.

Strengths: 

The authors carefully executed a set of very challenging experiments that involved applying tDCS in awake and anesthetized non-human primates while conducting functional imaging.

We thank the Reviewer for summarising our study and for his appreciation of the highly challenging experiments we performed.

Weaknesses:

The authors show that tDCS can alter functional connectivity measured by fMRI but they do not make clear what their studies teach the reader about the effects of tDCS on the brain during different states of consciousness. No important finding is stated contrary to what is stated in the abstract. It is also not clear what the work teaches us about how tDCS works nor is it clear what are the "clinical implications for disorders of consciousness." The deep anesthesia is akin to being in a state of coma. This was not discussed.  

While the authors have executed a set of technically challenging experiments, it is not clear what they teach us about how tDCS works, normal brain neurophysiology, or brain pathological states such as disorders of consciousness.

We thank the reviewer for his comments. We agree that we could better highlight the value and implications of our work, and we take this opportunity to improve our manuscript according to the suggestions.

Actions in the text: We have added several new paragraphs in the Discussion section, considering these comments and other related remarks from the Reviewing Editor (see below our answer to the first comment of the Reviewing Editor: REC#1).

Reviewer #2 (Public review): 

General comments: 

The authors investigated the effects of tDCS on brain dynamics in awake and anesthetized monkeys using functional MRI. They claim that cathodal tDCS disrupts the functional connectivity pattern in awake monkeys while anodal tDCS alters brain patterns in anesthetized monkeys. This study offers valuable insight into how brain states can influence the outcomes of noninvasive brain stimulation. However, there are several aspects of the methods and results sections that should be improved to clarify the findings.

We thank the Reviewer for the summary and appreciation of our study.  

Major comments 

For the anesthetized monkeys, the anode location differs between subjects, with the electrode positioned to stimulate the left DLFPC in monkey R and the right DLPFC in monkey N. The authors mention that this discrepancy does not result in significant differences in the electric field due to the monkeys' small head size. However, this is incorrect, as placing the anode on the left hemisphere would result in a much lower EF in the right DLPFC than placing the anode on the right side. Running an electric field simulation would confirm this. Additionally, the small electrode size suggested by the Easy cap configuration for NHP appears sufficient to stimulate the targeted regions focally. If this interpretation is correct, the authors should provide additional evidence to support their claim, such as a computational simulation of the EF distribution.

We thank the Reviewer for the comments. First, regarding the reviewer’s statement that placing the anode on the left hemisphere would result in a much lower EF in the right DLPFC than placing the anode on the right side, we would like to clarify that we did not use a typical 4 x 1 concentric ring high-definition setup (which consists of a small centre electrode surrounded by four return electrodes), but a two-electrode montage, with one electrode over the left or right PFC and the other one over the contralateral occipital cortex. According to EF modelling papers, a 4 x 1 high-definition setup would produce an EF that is focused and limited to the cortical area circumscribed by the ring of the return electrodes (Datta et al. 2009; Alam et al. 2016). Therefore, targeting the left or right DLPFC with a 4 x 1 setup would produce an EF confined to the targeted hemisphere of the PFC. In contrast, we expect the brain current flow generated with our 2-electrode setup to be broader, despite the small size of the electrodes,  because there is no constraint from return electrodes. Thus, with our setup, the current is expected to flow between the PFC and the occipital cortex (see also our responses to comments R3.3., R.E.C.#2.1. and R.E.C.#2.2.). 

Second, we would like to point out that in awake experiments, in which we stimulated the right PFC of both monkeys, there was no gross evidence of left or right asymmetry in the computed functional connectivity patterns (Figure 3A, Figure 3 - figure supplement 2A; Figure 5A). These results, showing that our stimulation montages did not induce asymmetric dynamic FC changes in NHPs, support the idea that our setups did not generate EFs that were spatially focused enough to alter brain activity in one hemisphere substantially more than the other.

Third, it is also worth noting that current evidence suggests that human brains are significantly more lateralized than those of macaques. Macaque monkeys have been found to have some degree of lateralized networks, but these are of lower complexity, and the lateralization is less pronounced and functionally organized than in humans. (Whey et al., 2014; Mantini et al., 2013). This suggests that, even if the stimulation were focal enough to stimulate the left or the right part of the PFC only, the behavioural effects would likely be similar.

We strongly agree with the reviewer that conducting an EF simulation would be valuable to confirm our expectations and to gain a comprehensive view of the characteristics of the EFs generated with our different setups in NHPs. However, the challenge is in the fact that EF computational models have been developed for humans, and their use in NHPs is not straightforward due to significant anatomical differences. For example, macaque monkeys are distinct from humans in terms of brain size, shape and cortical organisation, skull thickness, and the presence of muscles, as well as different tissue conductivities (Lee et al. 2015; Datta et al.2016; Mantell et al. 2023). We plan to address this in future work.

Actions in the text: In the Materials and Methods section, we have modified the sentence: “Because of the small size of the monkey's head and because we did not use return electrodes to restrict the current flow (as is achieved with typical high-definition montages (Datta et al. 2009; Alam et al. 2016)), we expected that tDCS stimulation with the two symmetrical montages would result in nearly equivalent electric fields across the monkey’s head and produce roughly similar effects on brain activity.” 

We also added a new sentence about EF simulation: 

“This would need to be confirmed by running an electric field simulation. However, computational electric field models have been developed for humans, and their use in NHPs is not straightforward due to anatomical specificities. Indeed, monkeys differ from humans in terms of brain size, shape and cortical organization, skull thickness, tissue conductivities and the presence of muscles (Lee et al. 2015; Datta et al. 2016; Mantell et al. 2023). Modelling of EFs generated with the specific tDCS montages employed in this study will be performed in future work.”

For the anesthetized monkeys, the authors applied 1 mA tDCS first, followed by 2 mA tDCS. A 20-minute stimulation duration of 1 mA tDCS is strong enough to produce after-effects that could influence the brain state during the 2 mA tDCS. This raises some concerns. Previous studies have shown that 1 mA tDCS can generate EF of over 1 V/m in the brain, and the effects of stimulation are sensitive to brain state (e.g., eye closed vs. eye open). How do the authors ensure that there are no after-effects from the 1 mA tDCS? This issue makes it challenging to directly compare the effects of 1 mA and 2 mA stimulation.

We agree with the reviewer's comment that 1 mA tDCS may induce aftereffects, as has been observed in several human studies (e.g., (Jamil et al. 2017, 2020). Although the differences between the 1 mA post-stimulation and baseline conditions were not significant in our analyses, it's still possible that the stimulation produced some effects below the threshold of significance that may contribute, albeit weakly, to the changes observed during and after 2 mA stimulation. We have, therefore, amended the paper in line with the reviewer's comments.

Actions in the text: We have added the following text in the Result section: 

“While several human studies have reported that 1 mA transcranial stimulation induces aftereffects (e.g., (Jamil et al. 2017, 2020; Monte-Silva et al. 2010), the differences between the 1 mA post-stimulation and baseline conditions were not significant in our analyses. However, it is still possible that the 1 mA stimulation produced some effects below the threshold of significance that may contribute to the changes observed during and after the 2 mA stimulation.”

The occurrence rate of a specific structural-functional coupling pattern among random brain regions shows significant effects of tDCS. However, these results seem counterintuitive. It is generally understood that noninvasive brain stimulation tends to modulate functional connectivity rather than structural or structural-functional connectivity. How does the occurrence rate of structural-functional coupling patterns provide a more suitable measure of the effectiveness of tDCS than functional connectivity alone? I would recommend that the authors present the results based on functional connectivity itself. If there is no change in functional connectivity, the relevance of changes in structural-functional coupling might not translate into a meaningful alteration in brain function, making it unclear how significant this finding is without corresponding functional evidence.

First, of all, we would like to make it clear that the occurrence rate of patterns as a function of their SFC is not intended to be used or seen as a ‘better’ measure of the efficacy of tDCS. Instead, it is one aspect of the effects of tDCS on whole-brain functional cortical dynamics, obtained from refined measures (phase-coherences), that specifically addresses the coupling between structure and function. This type of analysis is further motivated by its increasing use in the literature due to its suspected relationship to wakefulness (e.g., (Barttfeld et al. 2015, Demertzi et al. 2019; Castro et al. 2023)). Also, in our analysis, the structure is kept constant: the connectivity matrix used to correlate the functional brain states is always the same (CoCoMac82). Thus, the influence of tDCS on the structure-function side can only be explained by modulating the functional aspects, as suggested by intuition and previous results.

Then, we agree with the reviewer that studying the functional changes induced by tDCS alone could be valuable. However, usual metrics used in FC analysis are usually done statistically: FC-states are either computed through averaging spatial correlations over time, then analyzed through graph-theoretical properties for instance (or by just directly computing the element-wise differences), or either by considering the properties of the different visited FC-states by computing spatial correlations over a sliding time-window, and then similar analysis can be done as previously explained. But these are static metrics, if the states visited are essentially the same (which is expected from non-invasive neuromodulations that haven’t already demonstrated strong and/or characteristic impact), but the dynamical process of visiting said states changes, one would see no difference in that regard. As such, in the case of resting-state fMRI, differences in FCs are hard to interpret given that between-sessions within-condition differences are usually found with some degree of variance for the respective conditions. Trying then to interpret between-condition differences is quite tricky in the case of subtle modulations of the system’s activity. On the other hand, more subtle differences can be captured by considering more detailed analysis, such as using phase-based methods like we did,  by incorporating some statistical learning component with regard to the dynamicity of the system (supervised learning for instance like we did followed by temporal & transition-based methodology), and by adding some dimensions along which one will be able to give some interpretation to the analysis.  In our case we were interested in characterizing resting-state differences between stimulation conditions, which have nuanced and subtle interactions with the biological system. 

As such, classical measures of differences between FC states are likely to not be refined and precise enough. In fact, we propose additional files investigating those classically used measures such as differences in average FC matrices, or changes in functional graph properties (like modularity, efficiency and density) of the visited FC states. These figures show that, for the first case, comparing region-to-region specific FCs provides very few statistically significant results. With respect to the second part, we show that virtually no differences are observed in the properties of the functional states visited. 

These results suggest, as expected, that the actual brain states visited across the different stimulation conditions are topologically quite similar, and that only very few region-specific pairwise functional connectivities are particularly modulated by specific tDCS montages while, on the other hand, the actual dynamical process dictating how the brain activity passes from one state to another is in fact being influenced as shown by the dynamical analysis presented in the main figures in a more apparent and meaningful way (in that it is dependent on the montage, somewhat consistent with regard to the post-stimulations conditions, and can be made sense of by considering the theoretical effect of near-anodal versus near-cathodal neuromodulatory effects).

Actions in the text: We have added new supplementary files showing the effects of the stimulations on FC matrices and on classical functional graph properties in awake and anesthesia datasets (Supplementary Files 3 & 4).

We have added new sentences about these new analyses on the effects of the stimulations on FC matrices and on classical functional graph properties in the Results section:

“In addition, we performed the main analyses separately for the two monkeys, explored the inter-condition variability (Supplementary File 2), and computed classical measures of functional connectivity such as average FC matrices and functional graph properties (modularity, efficiency and density) of the visited FC states (Supplementary File 3).... In contrast, classical FC metrics did not show significant differences across stimulation conditions, highlighting the value of dynamic FC metrics to capture the neuromodulatory effects of tDCS.”

“Analyses of the two monkeys separately showed that the changes in slope and Shannon entropy were bigger in one of the two monkeys but went in the same direction (Supplementary File 2), while classical FC metrics did not capture any statistical differences between the different stimulation conditions (Supplementary File 3).”

The authors recorded data from only two monkeys, which may limit the investigation of the group effects of tDCS. As the number of scans for the second monkey in each consciousness condition is lower than that in the first monkey, there is a concern that the main effects might primarily reflect the data from a single monkey. I suggest that the authors should analyze the data for each monkey individually to determine if similar trends are observed in both subjects.

We agree that the small number of subjects is a limitation of our study. However, we have already addressed these aspects by reporting statistical analyses that consider them, using linear models of such variables, and running them through ANOVA tests. In addition, we experimentally ensured that we recorded a relatively high number of sessions over a period of several years. Regardless, we agree that our study would benefit from further investigation into this matter. We have therefore prepared complementary figures showing the main analysis performed separately for the two monkeys as proposed, as well as further investigations into the inter-condition variability outmatching the inter-individual variability, itself being also outmatched by intra-individual changes. 

Actions in the text: We have added a supplementary file showing the main analyses performed separately for the two monkeys (Supplementary File 2) and further investigations into the inter-condition variability (Supplementary Files 3 & 4).

We have added new sentences about these analyses performed separately for the two monkeys in the Results section:

“In addition, we performed the main analyses separately for the two monkeys, explored the inter-condition variability (Supplementary File 2), and computed classical measures of functional connectivity such as average FC matrices and functional graph properties (modularity, efficiency and density) of the visited FC states (Supplementary File 3). The separate analyses showed that the changes in slope and Shannon entropy were substantially more pronounced in one of the two monkeys, corroborating some of the effects captured in the ANOVA tests.”

“Analyses of the two monkeys separately showed that the changes in slope and Shannon entropy were bigger in one of the two monkeys but went in the same direction (Supplementary

File 2)”.

Anodal tDCS was only applied to anesthetized monkeys, which limits the conclusion that the authors are aiming for. It raises questions about the conclusion regarding brain state dependency. To address this, it would be better to include the cathodal tDCS session for anesthetized monkeys. If cathodal tDCS changes the connectivity during anesthesia, it becomes difficult to argue that the effects of cathodal tDCS vary depending on the state of consciousness as discussed in this paper. On the other hand, if cathodal tDCS would not produce any changes, the conclusion would then focus on the relationship between the polarity of tDCS and consciousness. In that case, the authors could maintain their conclusion but might need to refine it to reflect this specific relationship more accurately. 

We agree with the reviewer that it would have been interesting to investigate the effects of cathodal tDCS in anesthetized monkeys. However, due to the challenging nature of the experimental procedures under anesthesia, we had to limit the investigations to only one stimulation modality. We chose to deliver anodal stimulation because, from a translational point of view, we aimed to provide new information on the effects of tDCS under anesthesia as a model for disorders of consciousness. It also made much more sense to increase the cortical excitability of the prefrontal cortex in an attempt to wake up the sedated monkeys rather than doing the opposite.

Actions in the text: We have added a new sentence in the Results section:

“Due to the challenging nature of the experimental procedures under anesthesia, we limited the investigations to only one stimulation modality. We chose to deliver anodal stimulation to provide new information on the effects of tDCS under anesthesia as a model for disorders of consciousness and to increase the cortical excitability of the PFC in an attempt to wake up the sedated monkeys.”

Reviewer #3 (Public review): 

Summary: 

This study used transcranial direct current stimulation administered using small 'high-definition' electrodes to modulate neural activity within the non-human primate prefrontal cortex during both wakefulness and anaesthesia. Functional magnetic resonance imaging (fMRI) was used to assess the neuromodulatory effects of stimulation. The authors report on the modification of brain dynamics during and following anodal and cathodal stimulation during wakefulness and following anodal stimulation at two intensities (1 mA, 2 mA) during anaesthesia. This study provides some possible support that prefrontal direct current stimulation can alter neural activity patterns across wakefulness and sedation in monkeys. However, the reported findings need to be considered carefully against several important methodological limitations. 

Strengths: 

A key strength of this work is the use of fMRI-based methods to track changes in brain activity with good spatial precision. Another strength is the exploration of stimulation effects across wakefulness and sedation, which has the potential to provide novel information on the impact of electrical stimulation across states of consciousness.

We thank the Reviewer for the summary and for highlighting the strengths of our study. 

Weaknesses: 

The lack of a sham stimulation condition is a significant limitation, for instance, how can the authors be sure that results were not affected by drowsiness or fatigue as a result of the experimental procedure?

We agree with the reviewer that adding control conditions could have strengthened our study. Control conditions usually consist of a sham condition or active control conditions. However, as mentioned in response to one of Reviewer 2 comments (R.2.5), we had to make choices as we could not perform as many experiments due to their demanding nature, especially under anesthesia. 

In the awake state, we acquired data with two experimental conditions; the monkeys were exposed to either anodal (F4/O1) or cathodal (O1/F4) PFC tDCS. As anodal tDCS of the PFC induced only minor changes in brain dynamics, it could be considered as an active control condition for the cathodal condition, which had striking effects on the cortical dynamics. It is also worth noting that doubts have been raised about the neurobiological inertia of certain sham protocols. Indeed, different sham protocols have been employed in the literature, some of which may produce unintended effects (Fonteneau et al. 2019). Therefore, active control conditions, such as reversing the polarity of the stimulation or targeting a different brain region, have been proposed to provide better control (Fonteneau et al. 2019). Furthermore, in the context of experiments performed under anesthesia, the relevance of a sham control condition typically used to achieve adequate blinding is questionable. 

With regard to drowsiness and fatigue as a result of the experimental procedure, we agree with the reviewer that this is a common problem in functional imaging due to the length of the recording sessions. We assumed, as was done in previous work (Uhrig, Dehaene, and Jarraya 2014; Wang et al. 2015), that the monkeys' performance on the fixation task during acquisition would capture these periods of fatigue. Therefore, only sessions with fixation rates above 85% were included in our analysis. 

Actions in the text: We have now specified, in the Materials and Methods section, the fact that only runs with a high fixation rate (> 85%) were included in the study: 

“To ensure that the results were not biased by fatigue or drowsiness due to the lengthy

In the anaesthesia condition, the authors investigated the effects of two intensities of stimulation (1 mA and 2 mA). However, a potential confound here relates to the possibility that the initial 1 mA stimulation block might have caused plasticity-related changes in neural activity that could have interfered with the following 2 mA block due to the lack of a sufficient wash-out period. Hence, I am not sure any findings from the 2 mA block can really be interpreted as completely separate from the initial 1 mA stimulation period, given that they were administered consecutively. Several previous studies have shown that same-day repeated tDCS stimulation blocks can influence the effects of neuromodulation (e.g., Bastani and Jaberzadeh, 2014, Clin Neurophysiol; Monte-Silva et al., J. Neurophysiology). 

We agree with the reviewer’s comment that the initial 1 mA stimulation block might have induced changes in neural activity and that the 20-minute post 1 mA block would not be long enough to wash out these changes. This comment is very similar to the second comment made by Reviewer 2 (R.2.2). Although our experimental data do not support this possibility (as the differences between the 1 mA post-stimulation and baseline conditions were not significant), it is still conceivable that the stimulation produced some effects below the threshold of significance and that these might weakly contribute to the changes observed during and after the 2 mA stimulation. 

Actions in the text: We have modified the paper according to the reviewers' comments (please see our answer and actions in the text to R.2.2.).

The different electrode placement for the two anaesthetised monkeys (i.e., Monkey R: F3/O2 montage, Monkey N: F4/O1 montage) is problematic, as it is likely to have resulted in stimulation over different brain regions. The authors state that "Because of the small size of the monkey's head, we expected that tDCS stimulation with these two symmetrical montages would result in nearly equivalent electric fields across the monkey's head and produce roughly similar effects on brain activity"; however, I am not totally convinced of this, and it really would need E-field models to confirm. It is also more likely that there would in fact be notable differences in the brain regions stimulated as the authors used HD-tDCS electrodes, which are generally more focal.

We thank the Reviewer for the remark, which is very similar to the second comment from Reviewer 2. Please see our answer to the first comment of Reviewer 2 

Actions in the text: We have modified the paper according to the reviewers' comments (please see the actions taken in response to R.2.1.).

Given the very small sample size, I think it is also important to consider the possibility that some results might also be impacted by individual differences in response to stimulation. For instance, in the discussion (page 9, paragraph 2) the authors contrast findings observed in awake animals versus anaesthetised animals. However, different monkeys were examined for these two conditions, and there were only two monkeys in each group (monkeys J and Y for awake experiments [both male], and monkeys R and N [male and female] for the anaesthesia condition). From the human literature, it is well known that there is a considerable amount of inter-individual variability in response to stimulation (e.g., Lopez-Alonso et al., 2014, Brain Stimulation; Chew et al., 2015, Brain Stimulation), therefore I wonder if some of these differences could also possibly result from differences in responsiveness to stimulation between the different monkeys? At the end of the paragraph, the authors also state "Our findings also support the use of tDCS to promote rapid recovery from general anesthesia in humans...and suggest that a single anodal prefrontal stimulation at the end of the anesthesia protocol may be effective." However, I'm not sure if this statement is really backed-up by the results, which failed to report "any behavioural signs of awakening in the animals" (page 7)?

We thank the Reviewer for this comment. Because working with non-human primates is expensive and labor intensive, the sample sizes in classical macaque experiments are generally small (typically 2-4 subjects per experiment). Our sample size (i.e. 2 rhesus macaques in awake experiments and 2 macaques under sedation, 11 +/- 9 scan sessions per animal, 288 and 136 runs in the awake and anesthesia state, respectively) is comparable to other previous work in non-human primates using fMRI (Milham et al. 2018; Yacoub et al. 2020; Uchimura, Kumano, and Kitazawa 2024). In addition, we would like to point out that the baseline cortical dynamics we found before stimulation, whether in the awake or sedated state, are comparable to previous studies (Barttfeld et al. 2015; Uhrig et al. 2018; Tasserie et al. 2022). This suggests our results are reproducible across datasets, despite the small sample size.

That being said, we agree with the reviewer that inter-individual variability in response to stimulation can be considerable, as shown by a large body of literature in the field. It seems possible that the two monkeys studied in each condition responded differently to the stimulation. But even if that’s the case, our results suggest that at least in one of the two monkeys, cathodal PFC stimulation in the awake state and anodal PFC stimulation under propofol anesthesia induced striking changes in brain dynamics, which we believe is a significant contribution to the field. 

In fact, supplementary analysis, as proposed by Reviewer 2 (cf R2.4), investigating how the different measurables we’ve used were differently affected by tDCS show that indeed monkey Y’s case is more apparent and significant than monkey J’s. Still, the effects observed in monkey J’s case are still congruent with what is observed in monkey Y’s and at the population level (though less flagrant). We also show that these inter-individual variabilities are outmatched by the inter-condition variability, (as indicated by our initially strong statistical results at the population levels), thus showing that, even though we have different responses depending on the subject, the effects observed at the population level cannot be only accounted for by the differences in subjects’ specificities.

Lastly, the Reviewer questioned whether our results support that a single anodal prefrontal stimulation at the end of the anesthesia protocol could effectively promote rapid recovery from general anesthesia, because the stimulation did not wake the animals in our experiments. It should be emphasized that in our case, the monkeys were stimulated while they were still receiving continuous propofol perfusion. In contrast, during the recovery process from anesthesia, the delivery of the anesthetic drug is stopped. It is therefore conceivable that anodal PFC tDCS, which successfully enriched brain dynamics in sedated monkeys in our experiments, may accelerate the recovery from anesthesia when the drug is no longer administered. 

Actions in the text: We have added a line in the Materials and Methods to compare to other studies:

“Our sample size is comparable to previous work in NHP using fMRI (Milham et al. 2018; Yacoub et al. 2020; Uchimura, Kumano, and Kitazawa 2024).”

Reviewing Editor Comments: 

In some cases, authors opt to submit a revised manuscript. Should you choose to do so, please be aware that the reviewers have indicated that their appraisal is unlikely to change unless some of the suggested field modelling is incorporated into the work. This may change the evaluation of the strength of evidence, but the final wording will be subject to reviewer discretion. Details for responding to the reviews are provided at the bottom of this email.

Reviewer #1 (Recommendations for the authors): 

The work should discuss the implications of their experiments for using tDCS to arouse a patient from a coma. The anesthetized animal is effectively in a drug-induced coma. While they observed connectivity changes, these changes did not map nicely onto behavioral changes. 

I would suggest that the authors spell out more clearly what they view as the clinical implications of their work in terms of new insights into how tDCS may be used to either understand and or treat disorders of consciousness.

We thank the Reviewer for his thoughtful comments. We appreciate the opportunity to clarify and expand on the key findings and implications of our work, particularly regarding the new insights into how tDCS can be used to understand and treat disorders of consciousness. We therefore provide a broader perspective on the clinical implications of our experiments regarding coma and disorders of consciousness. We also agree with the Reviewer that the absence of behavioral changes but the presence of functional differences should be more clearly addressed. 

Actions in the text: We have added a few lines about the relevance of anesthesia as a model for disorders of consciousness in the Introduction part:

“Anesthesia provides a unique model for studying consciousness, which, similarly to DOC, is characterized by the disruption or even  the loss of consciousness (Luppi 2024). Additionally, anesthesia mechanisms involve several subcortical nuclei that are key components of the brain's sleep and arousal circuits (Kelz and Mashour 2019).”

In the Discussion section, we have modified and expanded a paragraph about the effects of tDCS in DOC patients and how this technique could be further used to study consciousness: From another clinical perspective, our results demonstrating that 2 mA anodal PFC tDCS decreased the structure-function correlation and modified the dynamic repertoire of brain patterns during anesthesia (Figures 6 and 7) are consistent with the beneficial effects of such stimulation in DOC patients (Thibaut et al., 2014; Angelakis et al., 2014; Thibaut et al., 2017; Zhang et al., 2017; Martens et al., 2018; Cavinato et al., 2019; Wu et al., 2019; Hermann et al., 2020; Peng et al., 2022; Thibaut et al., 2023). Although some clinical trials investigated the effects of stimulating other brain regions, such as the motor cortex (Martens et al., 2019; Straudi et al., 2019) or the parietal cortex (Huang et al., 2017; Guo et al., 2019; Zhang et al., 2022; Wan et al., 2023; Wang et al., 2020), the DLPFC appears to be the most effective target for patients with a minimally conscious state (Liu et al., 2023). In terms of neuromodulatory effects in DOC patients, DLPFC tDCS has been reported to increase global excitability (Bai et al., 2017), increase the P300 amplitude (Zhang et al., 2017; Hermann et al., 2020), improve the fronto-parietal coherence in the theta band (Bai et al., 2018), enhance the putative EEG markers of consciousness (Bai et al., 2018; Hermann et al., 2020) and reduce the incidence of slow-waves in the resting state (Mensen et al., 2020). Our findings further support the PFC as a relevant target for modulating consciousness level and align with growing evidence showing that the PFC plays a key role in conscious access networks (Mashour, Pal, and Brown 2022; Panagiotaropoulos 2024). Nevertheless, we hypothesize that other brain targets for tDCS may be of interest for consciousness restoration, potentially using multi-channel tDCS (Havlík et al., 2023). Among transcranial electrical stimulation techniques, tDCS has the great advantage of facilitating either excitation or inhibition of brain regions, depending on the polarity of the stimulation (Sdoia et al., 2019) exploited this advantage to investigate the causal involvement of the DLPFC in conscious access to a visual stimulus during an attentional blink paradigm. While conscious access was enhanced by anodal stimulation of the left DLPFC compared to sham stimulation, opposite effects were found with cathodal stimulation compared to sham over the same locus. Finally, this literature and our findings suggest that tDCS constitutes a non-invasive, reversible, and powerful tool for studying consciousness.”

We have added a new paragraph about patients with cognitive-motor dissociation and dissociation between consciousness and behavioral responsiveness:

“Changes in the state of consciousness are generally closely associated with changes in behavioural responsiveness, although some rare cases of dissociation have been described. Cognitive-motor dissociation (CMD) is a condition observed in patients with severe brain injury, characterized by behavior consistent with unresponsive wakefulness syndrome or a minimally conscious state minus (Thibaut et al., 2019). However, in these patients, specific cortical brain areas activate in response to mental imagery tasks (e.g., imagining playing tennis or returning home) in a manner indistinguishable from that of healthy controls, as shown through fMRI or EEG (Thibaut et al., 2019; Owen et al., 2006; Monti et al., 2010; Bodien et al., 2024). Thus, although CMD patients are behaviorally unresponsive, they demonstrate cognitive awareness that is not outwardly apparent. It is worth noting that both the structure-function correlation and the rate of the pattern closest to the anatomy were shown to be significantly reduced in unresponsive patients showing command following during mental imagery tasks compared to those who do not show command following (Demertzi et al., 2019). These observations would be compatible with our findings in anesthetized macaques exposed to 2 mA anodal PFC tDCS. The richness of the brain dynamics would be recovered (at least partially, in our experiments), but not the behaviour. This hypothesis also fits with a recent longitudinal fMRI study on patients recovering from coma (Crone et al., 2020). The researchers examined two groups of patients: one group consisted of individuals who were unconscious at the acute scanning session but regained consciousness and improved behavioral responsiveness a few months later, and the second group consisted of patients who were already conscious from the start and only improved behavioral responsiveness at follow-up. By comparing these two groups, the authors could distinguish between the recovery of consciousness and the recovery of behavioral responsiveness. They demonstrated that only initially conscious patients exhibited rich brain dynamics at baseline. In contrast, patients who were unconscious in the acute phase and later regained consciousness had poor baseline dynamics, which became more complex at follow-up. Complete recovery of both consciousness and responsiveness under general anesthesia is possible through electrical stimulation of the central thalamus (Redinbaugh et al., 2020; Tasserie et al., 2022).”

Reviewer #2 (Recommendations for the authors): 

Method 

(1) The authors mentioned that they used HD-tDCS in their experiments; however, they used 1 x 1 tDCS, which is not HD-tDCS but rather single-channel tDCS.

We thank the Reviewing Editor for pointing out this ambiguous wording. We understand that "HD-tDCS", which we used in our paper to refer to high-density 1x1 tDCS (because we used small carbon electrodes instead of the large sponge electrodes employed in conventional tDCS), may cause some confusion with high-definition tDCS, which uses compact ring electrodes and most commonly refers to a 4x1 montage (1 active central electrode over the target area and 4 return electrodes placed around the central electrode).

Therefore, to avoid any confusion, we will use the term "tDCS" rather than “HD-tDCS” to qualify the technique used in this paper and suppress mentions of high-density or high-definition tDCS.

Actions in the text: We have replaced the abbreviation “HD-tDCS” with “tDCS” throughout the paper. We have also suppressed the sentence about high-definition tDCS in the Introduction (“While conventional tDCS relies on the use of relatively large rectangular pad electrodes, high-density tDCS (HD-tDCS) utilizes more compact ring electrodes, allowing for increased focality, stronger electric fields, and presumably, greater neurophysiological changes (Datta et al. 2009; Dmochowski et al. 2011)”) and the two related citations in the References section.

(2) Please provide the characteristics of electrodes, including their size, shape, and thickness.

We thank the Reviewing Editor for this recommendation. We now provide the complete characteristics of the tDCS electrodes used in the paper.

Actions in the text: We have added a sentence describing the characteristics of the tDCS electrodes in the Materials and Methods section:

“We used a 1x1 electrode montage with two carbon rubber electrodes (dimensions: 1.4 cm x 1.85 cm, 0.93  cm thick) inserted into Soterix HD-tES MRI electrode holders (base diameter: 25 mm; height: 10.5 mm), which are in contact with the scalp. These electrodes (2.59 cm2) are smaller than conventional tDCS sponge electrodes (typically 25 to 35 cm²).”

(3) Could the authors clarify why they chose to stimulate the right DLPFC? Is there a specific rationale for this choice? Additionally, could the authors explain how they ensured that the stimulation targeted the DLPFC, given that the monkey cap might differ from human configurations? In many NHP studies, structural MRI is used to accurately determine electrode placement. Considering that a single channel F4 - O2 montage was used, even a small displacement of the frontal electrode laterally could result in the electric field not adequately covering the DLPFC. Could the authors provide structural MRI images and details of electrode positioning to help readers better understand targeting accuracy?

We thank the Reviewing Editor for the thoughtful comments and recommendations. We appreciate the opportunity to further clarify our rationale for stimulating the right DLPFC and also the suggestion to provide structural MRI images and details of electrode positioning, which we think will improve the quality of the paper by showing targeting accuracy.

First, we would like to clarify that our initial decision to stimulate the right PFC in most animals was driven by experimental constraints. Indeed, we had limited access to the left PFC in three of the four macaques, either due to the presence of cement (spreading asymmetrically from the centre of the head) used to fix the head post in awake animals or due to a scar in one of the two animals studied under anesthesia. 

Second, we agree with the Reviewing Editor on the importance of showing details of electrode positioning and evidence of targeting accuracy across MRI sessions. Therefore, we now provide structural images showing the positions of anodal and cathodal electrodes in almost all acquired sessions: 10 sessions (out of 10) under anesthesia and 30 sessions in the awake state (out of 34 sessions, because we could not acquire structural images in four sessions). These images show that, in anesthesia experiments, the anodal electrode was positioned over the dorsal prefrontal cortex and the cathodal electrode was placed over the contralateral occipital cortex (at the level of the parieto–occipital junction) in both monkeys. In the awake state, the montage still targeted the prefrontal cortex and the occipital cortex, but with a slightly different placement. One of the electrodes was placed over the prefrontal cortex, closer to the premotor cortex than in anesthesia experiments, while the other one was placed over the occipital cortex (V1), slightly more posterior than in anesthesia experiments. These images therefore show that the placement was relatively accurate across sessions and reproducible between monkeys in each of the two arousal conditions.

Actions in the text: We have added a supplementary file showing electrode positioning in 40 of the 44 acquired MRI sessions (Supplementary File 1). We have also added a new supplement figure (Figure 1 - figure supplement 1) showing electrode positioning in representative MRI sessions of the awake and anesthetized experiments in the main manuscript. 

We added a few sentences referring to these figures in the Result section: 

“Representative structural images showing electrode placements on the head of the two awake monkeys are shown in Figure 1 - figure supplement 1A). Supplementary File 1 displays the complete set of structural images, showing that the two electrodes were accurately placed over the prefrontal cortex and the occipital cortex in a reproducible manner across awake sessions.”

Figure 1 - figure supplement 1. Structural images displaying electrode placements on the head of monkeys. A) Awake experiments. Representative sagittal, coronal and transverse MRI sections, and the corresponding skin reconstruction images showing the position of the prefrontal and the occipital electrodes on the head of monkeys J. and Y. B) Anesthesia experiments. Representative sagittal, coronal and transverse MRI sections, and the corresponding skin reconstruction images showing the position of the prefrontal and occipital electrodes over the occipital cortex on the head of monkeys R. and N.

Supplementary File 1 (see attached file). Structural images showing the position of the tDCS electrodes on the monkey's head across sessions. Sagittal, coronal and transverse MRI sections, and corresponding skin reconstruction images showing the position of the prefrontal and occipital electrodes on the monkey's head for each MRI session (except for 4 sessions in which no anatomical scan was acquired). The two electrodes were accurately placed over the prefrontal cortex and the occipital cortex in a reproducible manner across sessions and between the two monkeys studied in each arousal state. In anesthesia experiments, the anodal electrode was placed over the dorsal prefrontal cortex, while the cathodal electrode was positioned over the parieto-occipital junction. In awake experiments, the prefrontal electrode was positioned over the dorsal prefrontal cortex/pre-motor cortex, while the occipital electrode was placed over the visual area 1. The position of the two electrodes differed slightly between the anesthetized and awake experiments due to different body positions (the prone position of the sedated monkeys prevented a more posterior position of the occipital electrode) and also due to the presence of a headpost on the head of the two monkeys in awake experiments (the monkeys we worked with in anesthesia experiments did not have an headpost).

(4) If the authors did not analyze the data for the passive event-related auditory response, it may be helpful to remove the related sentence to avoid potential confusion for readers.

We thank the Reviewing Editor for the comment. Although we understand the reviewer’s point of view, we decide to keep this information in the paper to inform the reader that the macaques were passively engaged in an auditory task, as this could have some influence on the brain state. In the Materials and Methods section, we already mentioned that the analysis of the cerebral responses to the auditory paradigm is not part of the paper. We have modified the sentence to make it clearer and to avoid potential confusion for readers.

Actions in the text: We have modified the sentence referring to the passive event-related auditory response in the Materials and Methods section:

“All fMRI data were acquired while the monkeys were engaged in a passive event-related auditory task, the local-global paradigm, which is based on local and global deviations from temporal regularities (Bekinschtein et al. 2009; Uhrig, Dehaene, and Jarraya 2014). The present paper does not address how tDCS perturbs cerebral responses to local and global deviants, which will be the subject of future work.”

(5) Could the authors clarify what x(t) represents in the equation? Additionally, it would be better to number the equations.

We apologize for the confusion,  x(t) represents the evolution of the BOLD signals over time. We have numbered the equations as suggested. 

Actions in the text: We have added explanations about the notation and numerotation of equations.

(6) It would be much better to provide schematic illustrations to explain what the authors did for analyzing fMRI data.

We thank the Reviewing Editor for the suggestion and now provide a new figure as suggested.  

Actions in the text: We have added a new figure (Figure 2) graphically showing the overall analysis performed. We have added a sentence about the new Figure 2 in the Results section:  “A graphical overview of the overall analysis is shown in Figure 2.” We have renumbered Figure 2 - supplement figures accordingly.

Figure 2. fMRI Phase Coherence analysis. A) Left) Animals were scanned before, during and after PFC tDCS stimulation in the awake state (two macaques) or under deep propofol anesthesia (two macaques). Right) Example of Z-scored filtered BOLD time series for one macaque, 111 time points with a TR of 2.4 s. B) Hilbert transform of the z-scored BOLD signal of one ROI into its time-varying amplitude A(t) (red) and the real part of the phase φ (green). In blue, we recover the original z-scored BOLD signal as A(t)cos(φ). C) Example of the phase of the Hilbert transform for each brain region at one TR. D) Symmetric matrix of cosines of the phase differences between all pairs of brain regions. E) We concatenated the vectorized form of the triangular superior of the phase difference matrices for all TRs for all participants, in all the conditions for both datasets separately obtaining using the K-means algorithm, the brain patterns whose statistics are then analyzed in the different conditions.

Results 

(1) In Figures 3A, 5A, and 6A showing brain connectivity, it is difficult to relate the connectivity variability among the brain regions. Instead of displaying connection lines for nodes, it would be more effective if the authors highlighted significant, strong connectivity within specific brain regions using additional methods, such as bootstrapping.

We thank the Reviewing Editor for the comment and suggestion. The connection lines indeed represent all the synchronizations above 0.5 and all the anti-synchronization below -0.5 between all pairs of brain regions. As suggested, another element we haven’t addressed is the heterogeneity in coherences between individual brain regions. We hence propose additional supplementary figures showing, for all centroids mentioned in main figures, the variance in phase-based connectivity of the distributions of coherence of all brain regions to the rest of the brain. High value would then indicate a wide range of values of coherence, while low would indicate the different coherence a region has with the rest of the brain have similar values. Thus, a brain with uniform color would indicate high homogeneity in coherence among brain regions, while sharp changes in colors would reveal that certain regions are more subject to high variance in their coherence distributions. We expect this new figure to more clearly expose the connectivity variability among the brain regions.

Actions in the text: We have added new figures showing, for all centroids mentioned in the main figures, the variances in phase-based connectivity of the distributions of coherence  (Figure 3 - figure supplement 3;  Figure 5 - figure supplement 2; Figure 6 - figure supplement 3; Figure 7 - figure supplement 2). One of them is shown below for the only awake analysis (Figure 3 - figure supplement 3).

Figure 3 - figure supplement 3. Variance in inter-region phase coherences of brain patterns. Low values (red and light red) indicate that the distribution of synchronizations between a brain region and the rest of the brain has relatively low variance, while high values (blue and light blue) indicate relatively high variance. Are displayed both supra (top) and subdorsal (bottom) views for each brain pattern from the main figure, ordered similarly as previously: from left (1) to right (6) as their respective SFC increases. 

We added a few sentences about variances in phase-based connectivity of the distributions of coherence in the Result section: 

“Further investigation of the variances in inter-region phase coherences of brain patterns, presented in Figure 3 - figure supplement 3, revealed two main findings. First, all the patterns exhibited some degree of lateral symmetry. Second, except for the pattern with the highest SFC, most patterns displayed high heterogeneity in their coherence variances and striking inter-pattern differences. These observations reflect both the segmentation of distinct functional networks across patterns and a topological organization within the patterns themselves: some regions showed a broader spectrum of synchrony with the rest of the brain, while others exhibited narrower distributions of coherence variances. For instance, unlike other brain patterns, pattern 5 was characterized by a high coherence variance in the frontal premotor areas and low variance in the occipital cortex, whereas pattern 3 had a high variance in the frontal and orbitofrontal regions. In addition, we performed the main analyses separately for the two monkeys, explored the inter-condition variability (Supplementary File 2), and computed classical measures of functional connectivity such as average FC matrices and functional graph properties (modularity, efficiency and density) of the visited FC states (Supplementary File 3).”

“The variance in inter-regional phase coherence across brain patterns showed notably that pattern 4, in contrast to most other patterns, was characterized by a high variance in frontal premotor areas and a low variance in the occipital cortex (Figure 5 - figure supplement 2)." 

“The variance in inter-region phase coherences of the brain patterns is displayed in Figure 6 - figure supplement 3 and showed a striking heterogeneity between the patterns. For example, pattern 5 had a low overall variance (except in the frontal cortex), while pattern 1 was the only pattern with a high variance in the occipital cortex.”

“The variance in inter-region phase coherences of brain patterns is displayed in Figure 6 - figure supplement 2.”

(2) For both conditions, only 2 to 3 out of 6 patterns showed significant effects of tDCS on the occurrence rate. Is it sufficient to claim the authors' conclusion?

We thank the Reviewer Editor for the comment. We would like to point out that similar kinds of differences in the occurrence rates of specific brain patterns (particularly in patterns at the extremities of the SFC scale) have already been reported previously. Prior works in patients suffering from disorders of consciousness, in healthy humans or in non-human primates,  have shown, by using a similar method of analysis, that not all brain states are equally disturbed by loss of consciousness, even in different modalities of unconscious transitioning (Luppi et al. 2021; Z. Huang et al. 2020; Demertzi et al. 2019; Castro et al. 2023; Golkowski et al. 2019; Barttfeld et al. 2015). Therefore, yes we believe that our conclusions are still supported by the results.

(3) If the authors want to assert that the brain state significantly influences the effects of tDCS as discussed in the manuscript, further analysis is necessary. First, it would be great to show the difference in connectivity between two consciousness conditions during the baseline (resting state) to see how resting state connectivity or structural connectivity varies. Second, demonstrating the difference in connectivity between the awake and anesthetized conditions (e.g., awake during cathodal vs. anesthetized cathodal) to show how the connectivity among the brain regions was changed by the brain state during tDCS. This would strengthen the authors' conclusion.

We thank the reviewer for this comment. Firstly, we’d like to clarify that the structural connectivity doesn’t change from one session to another in the same animal and minimally between subjects. Secondly, we agree with the Reviewing Editor that it is informative to show the differences between the baselines and this is what we have done. The results are shown in Figures 5 and 7. Regarding the comparison of the stimulating conditions across arousal levels, the only contrast that we could make is to compare 2 mA anodal awake with 2 mA anodal anesthetized (during and post-stimulation). However, as 2 mA anodal stimulation in the awake state did not affect the connectivity much (compared to the awake baseline), the results would be almost similar to the comparison of the awake baseline with 2 mA anodal anesthetized, which is shown in Figure 7. Therefore, we believe that this would result in minimal informative gains and even more redundancy. 

Reviewer #3 (Recommendations for the authors): 

Introduction, par 2: HD-tDCS does not necessarily produce stronger electric fields (E-fields) in the brain. The E-field is largely montage-dependent, and some configurations such as the 4x1 configuration can actually have weaker E-fields compared to conventional tDCS designs (i.e., with two sponge electrodes) as electrodes are often closer together resulting in more current being shunted by skull, scalp, and CSF. I would consider re-phrasing this section.

We agree with the Reviewer Editor that high-definition tDCS does not necessarily produce stronger electric fields in the brain and apologize for the confusion caused by our use of HD-tDCS to refer to high-density tDCS. To avoid any confusion, we have removed the sentence mentioning that HD-tDCS produces stronger electric fields. 

Actions in the text: We have removed the sentence about high-definition tDCS in the Introduction (“While conventional tDCS relies on the use of relatively large rectangular pad electrodes, high-density tDCS (HD-tDCS) utilizes more compact ring electrodes, allowing for increased focality, stronger electric fields, and presumably, greater neurophysiological changes (Datta et al. 2009; Dmochowski et al. 2011)”) and the two related citations in the References section.

eLife Assessment

This interesting study presents important information on how human cytomegalovirus (HCMV) infection disrupts the activity of the TEAD1 transcription factor, leading to widespread chromatin alterations. The strength of evidence in revised manuscript is convincing, and includes additional functional data teasing out how TEAD1-driven chromatin changes might influence HCMV replication. This work will be of interest to the virology, chromosome biology and transcriptional co-regulation fields.

Reviewer #1 (Public review):

The manuscript by Sayeed et al. uses a comprehensive series of multi-omics approaches to demonstrate that late-stage human cytomegalovirus (HCMV) infection leads to a marked disruption of TEAD1 activity, a concomitant loss of TEAD1-DNA interactions, and extensive chromatin remodeling. The data are thoroughly presented and provide evidence for the role of TEAD1 in the cellular response to HCMV infection.

However, a key question remains unresolved: is the observed disruption of TEAD1 activity a direct consequence of HCMV infection, or could it be secondary to the broader innate antiviral response? In this respect, the study would benefit from more in-depth experiments that assess the effect of TEAD1 overexpression or knockdown/deletion on HCMV replication dynamics. The new data provided by the authors in Reviewer Response Figures 1 and 2 suggest that the presence of constitutively expressed TEAD1 does not substantially impact HCMV replication and gene expression as assessed at 72 and 96 hours post-infection. However, this does not discount the fact that HCMV infection induces significant TEAD1-related chromatin changes that may impact other cellular functions.

Reviewer #2 (Public review):

Summary:

This work uses genomic and biochemical approaches for HCMV infection in human fibroblasts and retinal epithelial cell lines, followed by comparisons and some validations using strategies such as immunoblots. Based on these analyses, they propose several mechanisms that could contribute to the HCMV-induced diseases, including closing of TEAD1-occupying domains and reduced TEAD1 transcript and protein levels, decreased YAP1 and phospho-YAP1 levels, and exclusion of TEAD1 exon 6. Some functional assays, using over-expression of TEAD1, are provided.

Strengths:

The genomics experiments were done in duplicates and data analyses show good technical reproducibility. Data analyses are performed to show changes at the transcript and chromatin level changes, followed by some Western blot validations.

Weaknesses:

For readers who are outside the field, some clarifications of the system and design would be helpful.

eLife Assessment

This paper is important in demonstrating a requirement for sulfation in organizing apical ECM (aECM) during tubulogenesis in Drosophila melanogaster. The authors identify and characterize the organization of some of the first known components of the non-chitinous aECM in the Drosophila salivary gland tube, and these findings are supported by convincing data. This study would be of interest to developmental and cell biologists.

[Editors' note: this paper was reviewed by Review Commons.]

Reviewer #1 (Public review):

Summary:

There is growing appreciation for the important of luminal (apical) ECM in tube development, but such matrices are much less well understood than basal ECMs. Here the authors provide insights into the aECM that shapes the Drosophila salivary gland (SG) tube and the importance of PAPSS-dependent sulfation in its organization and function.

The first part of the paper focuses on careful phenotypic characterization of papss mutants, using multiple markers and TEM. This revealed reduced markers of sulfation and defects in both apical and basal ECM organization, Golgi (but not ER) morphology, number and localization of other endosomal compartments, plus increased cell death. The authors focus on the fact that papss mutants have an irregular SG lumen diameter, with both narrowed regions and bulged regions. They address the pleiotropy, showing that preventing the cell death and resultant gaps in the tube did not rescue the SG luminal shape defects and discussing similarities and differences between the papss mutant phenotype and those caused by more general trafficking defects. The analysis uses a papss nonsense mutant from an EMS screen - I appreciate the rigorous approach the authors took to analyze transheterozygotes (as well as homozygotes) plus rescued animals in order to rule out effects of linked mutations. Importantly, the rescue experiments also demonstrated that sulfation enzymatic activity is important.

The 2nd part of the paper focuses on the SG aECM, showing that Dpy and Pio ZP protein fusions localize abnormally in papss mutants and that these ZP mutants (and Np protease mutants) have similar SG lumen shaping defects to the papss mutants. A key conclusion is that SG lumen defects correlate with loss of a Pio+Dpy-dependent filamentous structure in the lumen. These data suggest that ZP protein misregulation could explain this part of the papss phenotype.

Overall, the text is very well written and clear. Figures are clearly labeled. The methods involve rigorous genetic approaches, microscopy, and quantifications/statistics and are documented appropriately. The findings are convincing.

Significance:

This study will be of interest to researchers studying developmental morphogenesis in general and specifically tube biology or the aECM. It should be particularly of interest to those studying sulfation or ZP proteins (which are broadly present in aECMs across organisms, including humans).

This study adds to the literature demonstrating the importance of luminal matrix in shaping tubular organs and greatly advances understanding of the luminal matrix in the Drosophila salivary gland, an important model of tubular organ development and one that has key matrix differences (such as no chitin) compared to other highly studied Drosophila tubes like the trachea.

The detailed description of the defects resulting from papss loss suggests that there are multiple different sulfated targets, with a subset specifically relevant to aECM biology. A limitation is that specific sulfated substrates are not identified here (e.g. are these the ZP proteins themselves or other matrix glycoproteins or lipids?); therefore, it's not clear how direct or indirect the effects of papss are on ZP proteins. However, this is clearly a direction for future work and does not detract from the excellent beginning made here.

Comments on revised version:

Overall, I am pleased with the authors' revisions in response to my original comments and those of the other reviewers

Reviewer #2 (Public review):

Summary

This study provides new insights into organ morphogenesis using the Drosophila salivary gland (SG) as a model. The authors identify a requirement for sulfation in regulating lumen expansion, which correlates with several effects at the cellular level, including regulation of intracellular trafficking and the organization of Golgi, the aECM and the apical membrane. In addition, the authors show that the ZP proteins Dumpy (Dpy) and Pio form an aECM regulating lumen expansion. Previous reports already pointed to a role for Papss in sulfation in SG and the presence of Dpy and Pio in the SG. Now this work extends these previous analyses and provides more detailed descriptions that may be relevant to the fields of morphogenesis and cell biology (with particular focus on ECM research and tubulogenesis). This study nicely presents valuable information regarding the requirements of sulfation and the aECM in SG development.

Strengths

-The results supporting a role for sulfation in SG development are strong. In addition, the results supporting the involvement of Dpy and Pio in the aECM of the SG, their role in lumen expansion, and their interactions, are also strong.

-The authors have made an excellent job in revising and clarifying the many different issues raised by the reviewers, particularly with the addition of new experiments and quantifications. I consider that the manuscript has improved considerably.

-The authors generated a catalytically inactive Papss enzyme, which is not able to rescue the defects in Papss mutants, in contrast to wild type Papss. This result clearly indicates that the sulfation activity of Papss is required for SG development.

Weaknesses

-The main concern is the lack of clear connection between sulfation and the phenotypes observed at the cellular level, and, importantly, the lack of connection between sulfation and the Pio-Dpy matrix. Indeed, the mechanism/s by which sulfation affects lumen expansion are not elucidated and no targets of this modification are identified or investigated. A direct (or instructive) role for sulfation in aECM organization is not clearly supported by the results, and the connection between sulfation and Pio/Dpy roles seems correlative rather than causative. As it is presented, the mechanisms by which sulfation regulates SG lumen expansion remains elusive in this study.

-In my opinion the authors overestimate their findings with several conclusions, as exemplified in the abstract:

"In the absence of Papss, Pio is gradually lost in the aECM, while the Dpy-positive aECM structure is condensed and dissociates from the apical membrane, leading to a thin lumen. Mutations in dpy or pio, or in Notopleural, which encodes a matriptase that cleaves Pio to form the luminal Pio pool, result in a SG lumen with alternating bulges and constrictions, with the loss of pio leading to the loss of Dpy in the lumen. Our findings underscore the essential role of sulfation in organizing the aECM during tubular organ formation and highlight the mechanical support provided by ZP domain proteins in maintaining luminal diameter."

The findings leading to conclude that sulfation organizes the aECM and that the absence of Papss leads to a thin lumen due to defects in Dpy/Pio are not strong. The authors certainly show that Papss is required for proper Pio and Dpy accumulation. They also show that Pio is required for Dpy accumulation, and that Pio and Dpy form an aECM required for lumen expansion. However, the absence of Pio and Dpy do not fully recapitulate Papss mutant defects (thin lumen). I wonder whether other hypothesis and models could account for the observed results. For instance, a role for Papss affecting secretion, in which case sulfation would have an indirect role in aECM organization. This study does not address the mechanical properties of Dpy in normal and mutant salivary glands.

-Minor issues relate to the genotype/phenotype analysis. It is surprising that the authors detect only mild effects on sulfation in Papss mutants using an anti-sulfoTyr antibody, as Papss is the only Papss synthathase. Generating germ line clones (which is a feasible experiment) would have helped to prove that this minor effect is due to the contribution of maternal product. The loss of function allele used in this study seems problematic, as it produces effects in heterozygous conditions difficult to interpret. Cleaning the chromosome or using an alternative loss of function condition (another allele, RNAi, etc...) would have helped to present a more reliable explanation.

Author response:

General Statements:

The formation of three-dimensional tubes is a fundamental process in the development of organs and aberrant tube size leads to common diseases and congenital disorders, such as polycystic kidney disease, asthma, and lung hypoplasia. The apical (luminal) extracellular matrix (ECM) plays a critical role in epithelial tube morphogenesis during organ formation, but its composition and organization remain poorly understood. Using the Drosophila embryonic salivary gland as a model, we reveal a critical role for the PAPS Synthetase (Papss), an enzyme that synthesizes the universal sulfate donor PAPS, as a critical regulator of tube lumen expansion. Additionally, we identify two zona pellucida (ZP) domain proteins, Piopio (Pio) and Dumpy (Dpy) as key apical ECM components that provide mechanical support to maintain a uniform tube diameter.

The apical ECM has a distinct composition compared to the basal ECM, featuring a diverse array of components. Many studies of the apical ECM have focused on the role of chitin and its modification, but the composition of the non-chitinous apical ECM and its role, and how modification of the apical ECM affects organogenesis remain elusive. The main findings of this manuscript are listed below.

(1) Through a deficiency screen targeting ECM-modifying enzymes, we identify Papss as a key enzyme regulating luminal expansion during salivary gland morphogenesis. 

(2) Our confocal and transmission electron microscopy analyses reveal that Papss mutants exhibit a disorganized apical membrane and condensed aECM, which are at least partially linked to disruptions in Golgi structures and intracellular trafficking. Papss is also essential for cell survival and basal ECM integrity, highlighting the role of sulfation in regulating both apical and basal ECM.

(3) Salivary gland-specific overexpression of wild-type Papss rescues all defects in Papss mutants, but the catalytically inactive mutant form does not, suggesting that defects in sulfation are the underlying cause of the phenotypes.

(4) We identify two ZP domain proteins, Piopio (Pio) and Dumpy (Dpy), as key components of the salivary gland aECM. In the absence of Papss, Pio is progressively lost from the aECM, while the Dpy-positive aECM structure is condensed and detaches from the apical membrane, resulting in a narrowed lumen. 

(5) Mutations in pio or dpy, or in Notopleural (Np), which encodes a matriptase that cleaves Pio, cause the salivary gland lumen to develop alternating bulges and constrictions. Additionally, loss of pio results in loss of Dpy in the salivary gland lumen, suggesting that the Dpycontaining filamentous structures of the aECM is critical for maintaining luminal diameter, with Pio playing an essential role in organizing this structure.

(6) We further reveal that the cleavage of the ZP domain of Pio by Np is critical for the role of Pio in organizing the aECM structure.

Overall, our findings underscore the essential role of sulfation in organizing the aECM during tubular organ formation and highlight the mechanical support provided by ZP domain proteins in maintaining tube diameter. Mammals have two isoforms of Papss, Papss1 and Papss2. Papss1 shows ubiquitous expression, with higher levels in glandular cells and salivary duct cells, suggesting a high requirement for sulfation in these cell types. Papss2 shows a more restricted expression, such as in cartilage, and mutations in Papss2 have been associated with skeletal dysplasia in humans. Our analysis of the Drosophila Papss gene, a single ortholog of human Papss1 and Papss2, reveals its multiple roles during salivary gland development. We expect that these findings will provide valuable insights into the function of these enzymes in normal development and disease in humans. Our findings on the key role of two ZP proteins, Pio and Dpy, as major components of the salivary gland aECM also provide valuable information on the organization of the non-chitinous aECM during organ formation.

We believe that our results will be of broad interest to many cell and developmental biologists studying organogenesis and the ECM, as well as those investigating the mechanisms underlying human diseases associated with conserved mutations.

Point-by-point description of the revisions:

We are delighted that all three reviewers were enthusiastic about the work. Their comments and suggestions have improved the paper. The details of the changes we have made in response to each reviewer’s comments are included in italicized text below.

Reviewer #1 (Evidence, reproducibility and clarity):

PAPS is required for all sulfotransferase reactions in which a sulfate group is covalently attached to amino acid residues of proteins or to side chains of proteoglycans. This sulfation is crucial for properly organizing the apical extracellular matrix (aECM) and expanding the lumen in the Drosophila salivary gland. Loss of Papss potentially leads to decreased sulfation, disorganizing the aECM, and defects in lumen formation. In addition, Papss loss destabilizes the Golgi structures.

In Papss mutants, several changes occur in the salivary gland lumen of Drosophila. The tube lumen is very thin and shows irregular apical protrusions. There is a disorganization of the apical membrane and a compaction of the apical extracellular matrix (aECM). The Golgi structures and intracellular transport are disturbed. In addition, the ZP domain proteins Piopio (Pio) and Dumpy (Dpy) lose their normal distribution in the lumen, which leads to condensation and dissociation of the Dpy-positive aECM structure from the apical membrane. This results in a thin and irregularly dilated lumen.

(1) The authors describe various changes in the lumen in mutants, from thin lumen to irregular expansion. I would like to know the correct lumen diameter, and length, besides the total area, by which one can recognize thin and irregular.

We have included quantification of the length and diameter of the salivary gland lumen in the stage 16 salivary glands of control, Papss mutant, and salivary gland-specific rescue embryos (Figure 1J, K). As described, Papss mutant embryos have two distinct phenotypes, one group with a thin lumen along the entire lumen and the other group with irregular lumen shapes. Therefore, we separated the two groups for quantification of lumen diameter. Additionally, we have analyzed the degree of variability for the lumen diameter to better capture the range of phenotypes observed (Figure 1K’). These quantifications enable a more precise assessment of lumen morphology, allowing readers to distinguish between thin and irregular lumen phenotypes.

(2) The rescue is about 30%, which is not as good as expected. Maybe the wrong isoform was taken. Is it possible to find out which isoform is expressed in the salivary glands, e.g., by RNA in situ Hyb? This could then be used to analyze a more focused rescue beyond the paper.

Thank you for this point, but we do not agree that the rescue is about 30%. In Papss mutants, about 50% of the embryos show the thin lumen phenotype whereas the other 50% show irregular lumen shapes. In the rescue embryos with a WT Papss, few embryos showed thin lumen phenotypes. About 40% of the rescue embryos showed “normal, fully expanded” lumen shapes, and the remaining 60% showed either irregular (thin+expanded) or slightly overexpanded lumen. It is not uncommon that rescue with the Gal4/UAS system results in a partial rescue because it is often not easy to achieve the balance of the proper amount of the protein with the overexpression system. 

To address the possibility that the wrong isoform was used, we performed in situ hybridization to examine the expression of different Papss spice forms in the salivary gland. We used probes that detect subsets of splice forms: A/B/C/F/G, D/H, and E/F/H, and found that all probes showed expression in the salivary gland, with varying intensities. The original probe, which detects all splice forms, showed the strongest signals in the salivary gland compared to the new probes which detect only a subset. However, the difference in the signal intensity may be due to the longer length of the original probe (>800 bp) compared to other probes that were made with much smaller regions (~200 bp). Digoxigenin in the DIG labeling kit for mRNA detection labels the uridine nucleotide in the transcript, and the probes with weaker signals contain fewer uridines (all: 147; ABCFG, 29; D, 36; EFH, 66). We also used the Papss-PD isoform, for a salivary gland-specific rescue experiment and obtained similar results to those with Papss-PE (Figure 1I-L, Figure 4D and E). 

Furthermore, we performed additional experiments to validate our findings. We performed a rescue experiment with a mutant form of Papss that has mutations in the critical rescues of the catalytic domains of the enzyme, which failed to rescue any phenotypes, including the thin lumen phenotype (Figure 1H, J-L), the number and intensity of WGA puncta (Figure 3I, I’), and cell death (Figure 4D, E). These results provide strong evidence that the defects observed in Papss mutants are due to the lack of sulfation.  

(3) Crb is a transmembrane protein on the apicolateral side of the membrane. Accordingly, the apicolateral distribution can be seen in the control and the mutant. I believe there are no apparent differences here, not even in the amount of expression. However, the view of the cells (frame) shows possible differences. To be sure, a more in-depth analysis of the images is required. Confocal Z-stack images, with 3D visualization and orthogonal projections to analyze the membranes showing Crb staining together with a suitable membrane marker (e.g. SAS or Uif). This is the only way to show whether Crb is incorrectly distributed. Statistics of several papas mutants would also be desirable and not just a single representative image. When do the observed changes in Crb distribution occur in the development of the tubes, only during stage 16? Is papss only involved in the maintenance of the apical membrane? This is particularly important when considering the SJ and AJ, because the latter show no change in the mutants.

We appreciate your suggestion more thoroughly analyze Crb distribution. We adapted a method from a previous study (Olivares-Castiñeira and Llimargas, 2017) to quantify Crb signals in the subapical region and apical free region of salivary gland cells. Using E-Cad signals as a reference, we marked the apical cell boundaries of individual cells and calculated the intensity of Crb signals in the subapical region (along the cell membrane) and in the apical free region. We focused on the expanded region of the SG lumen in Papss mutants for quantification, as the thin lumen region was challenging to analyze. This quantification is included in Figure 2D. Statistical analysis shows that Crb signals were more dispersed in SG cells in Papss mutants compared to WT.

(4) A change in the ECM is only inferred based on the WGA localization. This is too few to make a clear statement. WGA is only an indirect marker of the cell surface and glycosylated proteins, but it does not indicate whether the ECM is altered in its composition and expression. Other important factors are missing here. In addition, only a single observation is shown, and statistics are missing.

We understand your concern that WGA localization alone may not be sufficient to conclude changes in the ECM. However, we observed that luminal WGA signals colocalize with Dpy-YFP in the WT SG (Figure 5-figure supplement 2C), suggesting that WGA detects the aECM structure containing Dpy. The similar behavior of WGA and Dpy-YFP signals in multiple genotypes further supports this idea. In Papss mutants with a thin lumen phenotype, both WGA and Dpy-YFP signals are condensed (Figure 5E-H), and in pio mutants, both are absent from the lumen (Figure 6B, D). We analyzed WGA signals in over 25 samples of WT and Papss mutants, observing consistent phenotypes. We have included the number of samples in the text. While we acknowledge that WGA is an indirect marker, our data suggest that it is a reliable indicator of the aECM structure containing Dpy. 

(5) Reduced WGA staining is seen in papss mutants, but this could be due to other circumstances. To be sure, a statistic with the number of dots must be shown, as well as an intensity blot on several independent samples. The images are from single confocal sections. It could be that the dots appear in a different Z-plane. Therefore, a 3D visualization of the voxels must be shown to identify and, at best, quantify the dots in the organ.

We have quantified cytoplasmic punctate WGA signals. Using spinning disk microscopy with super-resolution technology (Olympus SpinSR10 Sora), we obtained high-resolution images of cytoplasmic punctate signals of WGA in WT, Papss mutant, and rescue SGs with the WT and mutant forms of Papss-PD. We then generated 3D reconstructed images of these signals using Imaris software (Figure 3E-H) and quantified the number and intensity of puncta. Statistical analysis of these data confirms the reduction of the number and intensity of WGA puncta in Papss mutants (Figure 3I, I’). The number of WGA puncta was restored by expressing WT Papss but not the mutant form. By using 3D visualization and quantification, we have ensured that our results are not limited to a single confocal section and account for potential variations in Z-plane localization of the dots.

(6) A colocalization analysis (statistics) should be shown for the overlap of WGA with ManII-GFP.

Since WGA labels multiple structures, including the nuclear envelope and ECM structures, we focused on assessing the colocalization of the cytoplasmic WGA punctate signals and ManIIGFP signals. Standard colocalization analysis methods, such as Pearson’s correlation coefficient or Mander’s overlap coefficient, would be confounded by WGA signals in other tissues. Therefore, we used a fluorescent intensity line profile to examine the spatial relationship between WGA and ManII-GFP signals in WT and Papss mutants (Figure 3L, L’). 

(7) I do not understand how the authors describe "statistics of secretory vesicles" as an axis in Figure 3p. The TEM images do not show labeled secretory vesicles but empty structures that could be vesicles.

Previous studies have analyzed “filled” electron-dense secretory vesicles in TEM images of SG cells (Myat and Andrew, 2002, Cell; Fox et al., 2010, J Cell Biol; Chung and Andrew, 2014, Development). Consistent with these studies, our WT TEM images show these vesicles. In contrast, Papss mutants show a mix of filled and empty structures. For quantification, we specifically counted the filled electron-dense vesicles (now Figure 3W). A clear description of our analysis is provided in the figure legend.

(8) The quality of the presented TEM images is too low to judge any difference between control and mutants. Therefore, the supplement must present them in better detail (higher pixel number?).

We disagree that the quality of the presented TEM images is too low. Our TEM images have sufficient resolution to reveal details of many subcellular structures, such as mitochondrial cisternae. The pdf file of the original submission may not have been high resolution. To address this concern, we have provided several original high-quality TEM images of both WT and Papss mutants at various magnifications in Figure 2-figure supplement 2. Additionally, we have included low-magnification TEM images of WT and Papss mutants in Figure 2H and I to provide a clearer view of the overall SG lumen morphology. 

(9) Line 266: the conclusion that apical trafficking is "significantly impaired" does not hold. This implies that Papss is essential for apical trafficking, but the analyzed ECM proteins (Pio, Dumpy) are found apically enriched in the mutants, and Dumpy is even secreted. Moreover, they analyze only one marker, Sec15, and don't provide data about the quantification of the secretion of proteins.

We agree and have revised our statement to “defective sulfation affects Golgi structures and multiple routes of intracellular trafficking”. 

(10) DCP-1 was used to detect apoptosis in the glands to analyze acellular regions. However, the authors compare ST16 control with ST15 mutant salivary glands, which is problematic. Further, it is not commented on how many embryos were analyzed and how often they detect the dying cells in control and mutant embryos. This part must be improved.

Thank you for the comment. We agree and have included quantification. We used stage 16 samples from WT and Papss mutants to quantify acellular regions. Since DCP-1 signals are only present at a specific stage of apoptosis, some acellular regions do not show DCP-1 signals. Therefore, we counted acellular regions regardless of DCP-1 signals. We also quantified this in rescue embryos with WT and mutant forms of Papss, which show complete rescue with WT and no rescue with the mutant form, respectively. The graph with a statistical analysis is included (Figure 4D, E).

(11) WGA and Dumpy show similar condensed patterns within the tube lumen. The authors show that dumpy is enriched from stage 14 onwards. How is it with WGA? Does it show the same pattern from stage 14 to 16? Papss mutants can suffer from a developmental delay in organizing the ECM or lack of internalization of luminal proteins during/after tube expansion, which is the case in the trachea.

Dpy-YFP and WGA show overlapping signals in the SG lumen throughout morphogenesis. DpyYFP is SG enriched in the lumen from stage 11, not stage 14 (Figure 5-figure supplement 2). WGA is also detected in the lumen throughout SG morphogenesis, similar to Dpy. In the original supplemental figure, only a stage 16 SG image was shown for co-localization of Dpy-YFP and WGA signals in the SG lumen. We have now included images from stage 14 and 15 in Figure 5figure supplement 2C. 

Given that luminal Pio signals are lost at stage 16 only and that Dpy signals appear as condensed structures in the lumen of Papss mutants, it suggests that the internalization of luminal proteins is not impaired in Papss mutants. Rather, these proteins are secreted but fail to organize properly. 

(12) Line 366. Luminal morphology is characterized by bulging and constrictions. In the trachea, bulges indicate the deformation of the apical membrane and the detachment from the aECM. I can see constrictions and the collapsed tube lumen in Fig. 6C, but I don't find the bulges of the apical membrane in pio and Np mutants. Maybe showing it more clearly and with better quality will be helpful.

Since the bulging phenotype appears to vary from sample to sample, we have revised the description of the phenotype to “constrictions” to more accurately reflect the consistent observations. We quantified the number of constrictions along the entire lumen in pio and Np mutants and included the graph in Figure 6F.

(13) The authors state that Papss controls luminal secretion of Pio and Dumpy, as they observe reduced luminal staining of both in papss mutants. However, the mCh-Pio and Dumpy-YFP are secreted towards the lumen. Does papss overexpression change Pio and Dumpy secretion towards the lumen, and could this be another explanation for the multiple phenotypes? 

Thank you for the comment. To clarify, we did not observe reduced luminal staining of Pio and Dpy in Papss mutants, nor did we state that Papss controls luminal secretion of Pio and Dpy. In Papss mutants, Pio luminal signals are absent specifically at stage 16 (Figure 5H), whereas strong luminal Pio signals are present until stage 15 (Figure 5G). For Dpy-YFP, the signals are not reduced but condensed in Papss mutants from stages 14-16 (Figure 5D, H). 

It remains unclear whether the apparent loss of Pio signals is due to a loss of Pio protein in the lumen or due to epitope masking resulting from protein aggregation or condensation. As noted in our response to Comment 11 internalization of luminal proteins seems unaffected in Papss mutants; proteins like Pio and Dpy are secreted into the lumen but fail to properly organize. Therefore, we have not tested whether Papss overexpression alters the secretion of Pio or Dpy.

In our original submission, we incorrectly stated that uniform luminal mCh-Pio signals were unchanged in Papss mutants. Upon closer examination, we found these signals are absent in the expanded luminal region in stage 16 SG (where Dpy-YFP is also absent), and weak mCh-Pio signals colocalize with the condensed Dpy-YFP signals (Figure 5C, D). We have revised the text accordingly. 

Regulation of luminal ZP protein level is essential to modulate the tube expansion; therefore, Np releases Pio and Dumpy in a controlled manner during st15/16. Thus, the analysis of Pio and Dumpy in NP overexpression embryos will be critical to this manuscript to understand more about the control of luminal ZP matrix proteins.

Thanks for the insightful suggestion. We overexpressed both the WT and mutant form of Np using UAS-Np.WT and UAS-Np.S990A lines (Drees et al., 2019) and analyzed mCh-Pio, Pio antibody, and Dpy-YFP signals. It is important to note that these overexpression experiments were done in the presence of the endogenous WT Np. 

Overexpression of Np.WT led to increased levels of mCh-Pio, Pio, and Dpy-YFP signals in the lumen and at the apical membrane. In contrast, overexpression of Np.S990A resulted in a near complete loss of luminal mCh-Pio signals. Pio antibody signals remained strong at the apical membrane but was weaker in the luminal filamentous structures compared to WT. 

Due to the GFP tag present in the UAS-Np.S990A line, we could not reliably analyze Dpy-YFP signals because of overlapping fluorescent signals in the same channel. However, the filamentous Pio signals in the lumen co-localized with GFP signals, suggesting that these structures might also include Dpy-YFP, although this cannot be confirmed definitively. 

These results suggest that overexpressed Np.S990A may act in a dominant-negative manner, competing with endogenous Np and impairing proper cleavage of Pio (and mCh-Pio). Nevertheless, some level of cleavage by endogenous Np still appears to occur, as indicated by the residual luminal filamentous Pio signals. These new findings have been incorporated into the revised manuscript and are shown in Figure 6H and 6I.

(14) Minor:

Fig. 5 C': mChe-Pio and Dumpy-YFP are mixed up at the top of the images.

Thanks for catching this error.  It has been corrected.

Sup. Fig7. A shows Pio in purple but B in green. Please indicate it correctly.

It has been corrected.

Reviewer #1 (Significance):

In 2023, the functions of Pio, Dumpy, and Np in the tracheal tubes of Drosophila were published. The study here shows similar results, with the difference that the salivary glands do not possess chitin, but the two ZP proteins Pio and Dumpy take over its function. It is, therefore, a significant and exciting extension of the known function of the three proteins to another tube system. In addition, the authors identify papss as a new protein and show its essential function in forming the luminal matrix in the salivary glands. Considering the high degree of conservation of these proteins in other species, the results presented are crucial for future analyses and will have further implications for tubular development, including humans.

Reviewer #2 (Evidence, reproducibility and clarity):

Summary:

There is growing appreciation for the important of luminal (apical) ECM in tube development, but such matrices are much less well understood than basal ECMs. Here the authors provide insights into the aECM that shapes the Drosophila salivary gland (SG) tube and the importance of PAPSS-dependent sulfation in its organization and function.

The first part of the paper focuses on careful phenotypic characterization of papss mutants, using multiple markers and TEM. This revealed reduced markers of sulfation (Alcian Blue staining) and defects in both apical and basal ECM organization, Golgi (but not ER) morphology, number and localization of other endosomal compartments, plus increased cell death. The authors focus on the fact that papss mutants have an irregular SG lumen diameter, with both narrowed regions and bulged regions. They address the pleiotropy, showing that preventing the cell death and resultant gaps in the tube did not rescue the SG luminal shape defects and discussing similarities and differences between the papss mutant phenotype and those caused by more general trafficking defects. The analysis uses a papss nonsense mutant from an EMS screen - I appreciate the rigorous approach the authors took to analyze transheterozygotes (as well as homozygotes) plus rescued animals in order to rule out effects of linked mutations.

The 2nd part of the paper focuses on the SG aECM, showing that Dpy and Pio ZP protein fusions localize abnormally in papss mutants and that these ZP mutants (and Np protease mutants) have similar SG lumen shaping defects to the papss mutants. A key conclusion is that SG lumen defects correlate with loss of a Pio+Dpy-dependent filamentous structure in the lumen. These data suggest that ZP protein misregulation could explain this part of the papss phenotype.

Overall, the text is very well written and clear. Figures are clearly labeled. The methods involve rigorous genetic approaches, microscopy, and quantifications/statistics and are documented appropriately. The findings are convincing, with just a few things about the fusions needing clarification.

Minor comments

(1) Although the Dpy and Qsm fusions are published reagents, it would still be helpful to mention whether the tags are C-terminal as suggested by the nomenclature, and whether Westerns have been performed, since (as discussed for Pio) cleavage could also affect the appearance of these fusions.

Thanks for the comment. Dpy-YFP is a knock-in line in which YFP is inserted into the middle of the dpy locus (Lye et al., 2014; the insertion site is available on Flybase). mCh-Qsm is also a knock-in line, with mCh inserted near the N-terminus of the qsm gene using phi-mediated recombination using the qsm^MI07716 line (Chu and Hayashi, 2021; insertion site available on Flybase). Based on this, we have updated the nomenclature from Qsm-mCh to mCh-Qsm throughout the manuscript to accurately reflect the tag position. To our knowledge, no western blot has been performed on Dpy-YFP or mCh-Qsm lines. We have mentioned this explicitly in the Discussion.  

(2) The Dpy-YFP reagent is a non-functional fusion and therefore may not be a wholly reliable reporter of Dpy localization. There is no antibody confirmation. As other reagents are not available to my knowledge, this issue can be addressed with text acknowledgement of possible caveats.

Thanks for raising this important point. We have added a caveat in the Discussion noting this limitation and the need for additional tools, such as an antibody or a functional fusion protein, to confirm the localization of Dpy.

(3) TEM was done by standard chemical fixation, which is fine for viewing intracellular organelles, but high pressure freezing probably would do a better job of preserving aECM structure, which looks fairly bad in Fig. 2G WT, without evidence of the filamentous structures seen by light microscopy. Nevertheless, the images are sufficient for showing the extreme disorganization of aECM in papss mutants.

We agree that HPF is a better method and intent to use the HPF system in future studies. We acknowledge that chemical fixation contributes to the appearance of a gap between the apical membrane and the aECM, which we did not observe in the HPF/FS method (Chung and Andrew, 2014). Despite this, the TEM images still clearly reveal that Papss mutants show a much thinner and more electron-dense aECM compared to WT (Figure 2H, I), consistent to the condensed WGA, Dpy, and Pio signals in our confocal analyses. As the reviewer mentioned, we believe that the current TEM data are sufficient to support the conclusion of severe aECM disorganization and Golgi defects in Papss mutants.

(4) The authors may consider citing some of the work that has been done on sulfation in nematodes, e.g. as reviewed here: https://pubmed.ncbi.nlm.nih.gov/35223994/ Sulfation has been tied to multiple aspects of nematode aECM organization, though not specifically to ZP proteins.

Thank you for the suggestion. Pioneering studies in C. elegans have highlighted the key role of sulfation in diverse developmental processes, including neuronal organization, reproductive tissue development, and phenotypic plasticity. We have now cited several works.  

Reviewer #2 (Significance):

This study will be of interest to researchers studying developmental morphogenesis in general and specifically tube biology or the aECM. It should be particularly of interest to those studying sulfation or ZP proteins (which are broadly present in aECMs across organisms, including humans).

This study adds to the literature demonstrating the importance of luminal matrix in shaping tubular organs and greatly advances understanding of the luminal matrix in the Drosophila salivary gland, an important model of tubular organ development and one that has key matrix differences (such as no chitin) compared to other highly studied Drosophila tubes like the trachea.

The detailed description of the defects resulting from papss loss suggests that there are multiple different sulfated targets, with a subset specifically relevant to aECM biology. A limitation is that specific sulfated substrates are not identified here (e.g. are these the ZP proteins themselves or other matrix glycoproteins or lipids?); therefore it's not clear how direct or indirect the effects of papss are on ZP proteins. However, this is clearly a direction for future work and does not detract from the excellent beginning made here.

My expertise: I am a developmental geneticist with interests in apical ECM

Reviewer #3 (Evidence, reproducibility and clarity):

In this work Woodward et al focus on the apical extracellular matrix (aECM) in the tubular salivary gland (SG) of Drosophila. They provide new insights into the composition of this aECM, formed by ZP proteins, in particular Pio and Dumpy. They also describe the functional requirements of PAPSS, a critical enzyme involved in sulfation, in regulating the expansion of the lumen of the SG. A detailed cellular analysis of Papss mutants indicate defects in the apical membrane, the aECM and in Golgi organization. They also find that Papss control the proper organization of the Pio-Dpy matrix in the lumen. The work is well presented and the results are consistent.

Main comments

- This work provides a detailed description of the defects produced by the absence of Papss. In addition, it provides many interesting observations at the cellular and tissular level. However, this work lacks a clear connection between these observations and the role of sulfation. Thus, the mechanisms underlying the phenotypes observed are elusive. Efforts directed to strengthen this connection (ideally experimentally) would greatly increase the interest and relevance of this work.

Thank you for this thoughtful comment. To directly test whether the phenotypes observed in Papss mutants are due to the loss of sulfation activity, we generated transgenic lines expressing catalytically inactive forms of Papss, UAS-PapssK193A, F593P, in which key residues in the APS kinase and ATP sulfurylase domains are mutated. Unlike WT UAS-Papss (both the Papss-PD or Papss-PE isoforms), the catalytically inactive UAS-Papssmut failed to rescue any of the phenotypes, including the thin lumen phenotype (Figure 1I-L), altered WGA signals (Figure I, I’) and the cell death phenotype (Figure 4D, E). These findings strongly support the conclusion that the enzymatic sulfation activity of Papss is essential for the developmental processes described in this study.  

- A main issue that arises from this work is the role of Papss at the cellular level. The results presented convincingly indicate defects in Golgi organization in Papss mutants. Therefore, the defects observed could stem from general defects in the secretion pathway rather than from specific defects on sulfation. This could even underly general/catastrophic cellular defects and lead to cell death (as observed).

This observation has different implications. Is this effect observed in SGs also observed in other cells in the embryo? If Papss has a general role in Golgi organization this would be expected, as Papss encodes the only PAPs synthatase in Drosophila.

Can the authors test any other mutant that specifically affect Golgi organization and investigate whether this produces a similar phenotype to that of Papss?

Thank you for the comment. To address whether the defects observed in Papss mutants stem from general disruption of the secretory pathway due to Golgi disorganization, we examined mutants of two key Golgi components: Grasp65 and GM130. 

In Grasp65 mutants, we observed significant defects in SG lumen morpholgy, including highly irregular SG lumen shape and multiple constrictions (100%; n=10/10). However, the lumen was not uniformly thin as in Papss mutants. In contrast, GM130 mutants–although this line was very sick and difficult to grow–showed relatively normal salivary glands morphology in the few embryos that survived to stage 16 (n=5/5). It is possible that only embryos with mild phenotypes progressed to this stages, limiting interpretation. These data have now been included in Figure 3-figure supplement 2. Overall, while Golgi disruption can affect SG morphology, the specific phenotypes seen in Papss mutants are not fully recapitulated by Grasp65 or GM130 loss. 

- A model that conveys the different observations and that proposes a function for Papss in sulfation and Golgi organization (independent or interdependent?) would help to better present the proposed conclusions. In particular, the paper would be more informative if it proposed a mechanism or hypothesis of how sulfation affects SG lumen expansion. Is sulfation regulating a factor that in turn regulates Pio-Dpy matrix? Is it regulating Pio-Dpy directly? Is it regulating a

product recognized by WGA?

For instance, investigating Alcian blue or sulfotyrosine staining in pio, dpy mutants could help to understand whether Pio, Dpy are targets of sulfation.

Thank you for the comment. We’re also very interested in learning whether the regulation of the Pio-Dpy matrix is a direct or indirect consequence of the loss of sulfation on these proteins. One possible scenario is that sulfation directly regulates the Pio-Dpy matrix by regulating protein stability through the formation of disulfide bonds between the conserved Cys residues responsible for ZP module polymerization. Additionally, the Dpy protein contains hundreds of EGF modules that are highly susceptible to O-glycosylation. Sulfation of the glycan groups attached to Dpy may be critical for its ability to form a filamentous structure. Without sulfation, the glycan groups on Dpy may not interact properly with the surrounding materials in the lumen, resulting in an aggregated and condensed structure. These possibilities are discussed in the Discussion.

We have not analyzed sulfation levels in pio or dpy mutants because sulfation levels in mutants of single ZP domain proteins may not provide much information. A substantial number of proteoglycans, glycoproteins, and proteins (with up to 1% of all tyrosine residues in an organism’s proteins estimated to be sulfated) are modified by sulfation, so changes in sulfation levels in a single mutant may be subtle. Especially, the existing dpy mutant line is an insertion mutant of a transposable element; therefore, the sulfation sites would still remain in this mutant. 

- Interpretation of Papss effects on Pio and Dpy would be desired. The results presented indicate loss of Pio antibody staining but normal presence of cherry-Pio. This is difficult to interpret. How are these results of Pio antibody and cherry-Pio correlating with the results in the trachea described recently (Drees et al. 2023)?

In our original submission, we stated that the uniform luminal mCh-Pio signals were not changed in Papss mutants, but after re-analysis, we found that these signals were actually absent from the expanded luminal region in stage 16 SG (where Dpy-YFP is also absent), and weak mCh-Pio signals colocalize with the condensed Dpy-YFP signals (Figure 5C, D). We have revised the text accordingly. 

After cleavages by Np and furin, the Pio protein should have three fragments. The Nterminal region contains the N-terminal half of the ZP domain, and mCh-Pio signals show this fragment. The very C-terminal region should localize to the membrane as it contains the transmembrane domain. We think the middle piece, the C-terminal ZP domain, is recognized by the Pio antibody. The mCh-Pio and Pio antibody signals in the WT trachea (Drees et al., 2023) are similar to those in the SG. mCh-Pio signals are detected in the tracheal lumen as uniform signals, at the apical membrane, and in cytoplasmic puncta. Pio antibody signals are exclusively in the tracheal lumen and show more heterogenous filamentous signals. 

In Papss mutants, the middle fragment (the C-terminal ZP domain) seems to be most affected because the Pio antibody signals are absent from the lumen. The loss of Pio antibody signals could be due to protein degradation or epitope masking caused by aECM condensation and protein misfolding. This fragment seems to be key for interacting with Dpy, since Pio antibody signals always colocalize with Dpy-YFP. The N-terminal mCh-Pio fragment does not appear to play a significant role in forming a complex with Dpy in WT (but still aggregated together in Papss mutants), and this can be tested in future studies.

In response to Reviewer 1’s comment, we performed an additional experiment to test the role of Np in cleaving Pio to help organize the SG aECM. In this experiment, we overexpressed the WT and mutant form of Np using UAS-Np.WT and UAS-Np.S990A lines (Drees et al., 2019) and analyzed mCh-Pio, Pio antibody, and Dpy-YFP signals. Np.WT overexpression resulted in increased levels of mCh-Pio, Pio, and Dpy-YFP signals in the lumen and at the apical membrane. However, overexpression of Np.S990A resulted in the absence of luminal mCh-Pio signals. Pio antibody signals were strong at the apical membrane but rather weak in the luminal filamentous structures. Since the UAS-Np.S990A line has the GFP tag, we could not reliably analyze Dpy-YFP signals due to overlapping Np.S990A.GFP signals in the same channel. However, the luminal filamentous Pio signals co-localized with GFP signals, and we assume that these overlapping signals could be Dpy-YFP signals. 

These results suggest that overexpressed Np.S990A may act in a dominant-negative manner, competing with endogenous Np and impairing proper cleavage of Pio (and mCh-Pio). Nevertheless, some level of cleavage by endogenous Np still appears to occur, as indicated by the residual luminal filamentous Pio signals. These new findings have been incorporated into the revised manuscript and are shown in Figure 6H and 6I. 

A proposed model of the Pio-Dpy aECM in WT, Papss, pio, and Np mutants has now been included in Figure 7.

-  What does the WGA staining in the lumen reveal? This staining seems to be affected differently in pio and dpy mutants: in pio mutants it disappears from the lumen (as dpy-YFP does), but in dpy mutants it seems to be maintained. How do the authors interpret these findings? How does the WGA matrix relate to sulfated products (using Alcian blue or sulfotyrosine)?

WGA binds to sialic acid and N-acetylglucosamine (GlcNAc) residues on glycoproteins and glycolipids. GlcNAc is a key component of the glycosaminoglycan (GAG) chains that are covalently attached to the core protein of a proteoglycan, which is abundant in the ECM. We think WGA detects GlcNAc residues in the components of the aECM, including Dpy as a core component, based on the following data. 1) WGA and Dpy colocalize in the lumen, both in WT (as thin filamentous structures) and Papss mutant background (as condensed rod-like structures), and 2) are absent in pio mutants. WGA signals are still present in a highly condensed form in dpy mutants. That’s probably because the dpy mutant allele (dpyov1) has an insertion of a transposable element (blood element) into intron 11 and this insertion may have caused the Dpy protein to misfold and condense. We added the information about the dpy allele to the Results section and discussed it in the Discussion.

Minor points:

- The morphological phenotypic analysis of Papss mutants (homozygous and transheterozygous) is a bit confusing. The general defects are higher in Papss homozygous than in transheterozygotes over a deficiency. Maybe quantifying the defects in the heterozygote embryos in the Papss mutant collection could help to figure out whether these defects relate to Papss mutation.

We analyzed the morphology of heterozygous Papss mutant embryos. They were all normal. The data and quantifications have now been added to Figure 1-figure supplement 3. 

- The conclusion that the apical membrane is affected in Papss mutants is not strongly supported by the results presented with the pattern of Crb (Fig 2). Further evidences should be provided. Maybe the TEM analysis could help to support this conclusion

We quantified Crb levels in the sub-apical and medial regions of the cell and included this new quantification in Figure 2D. TEM images showed variation in the irregularity of the apical membrane, even in WT, and we could not draw a solid conclusion from these images.

- It is difficult to understand why in Papss mutants the levels of WGA increase. Can the authors elaborate on this?

We think that when Dpy (and many other aECM components) are condensed and aggregated into the thin, rod-like structure in Papss mutants, the sugar residues attached to them must also be concentrated and shown as increased WGA signals.   

- The explanation about why Pio antibody and mcherry-Pio show different patterns is not clear. If the antibody recognizes the C-t region, shouldn't it be clearly found at the membrane rather than the lumen?

The Pio protein is also cleaved by furin protease (Figure 5B). We think the Pio fragment recognized by the antibody should be a “C-terminal ZP domain”, which is a middle piece after furin + Np cleavages. 

- The qsm information does not seem to provide any relevant information to the aECM, or sulfation.

Since Qsm has been shown to bind to Dpy and remodel Dpy filaments in the muscle tendon (Chu and Hayashi, 2021), we believe that the different behavior of Qsm in the SG is still informative. As mentioned briefly in the Discussion, the cleaved Qsm fragment may localize differently, like Pio, and future work will need to test this. We have shortened the description of the Qsm localization in the manuscript and moved the details to the figure legend of Figure 5-figure supplement 3.

Reviewer #3 (Significance):

Previous reports already indicated a role for Papss in sulfation in SG (Zhu et al 2005). Now this work provides a more detailed description of the defects produced by the absence of Papss. In addition, it provides relevant data related to the nature and requirements of the aECM in the SG. Understanding the composition and requirements of aECM during organ formation is an important question. Therefore, this work may be relevant in the fields of cell biology and morphogenesis.

eLife Assessment

This valuable study combines anatomical tracing and slice physiology to examine how anterior thalamic and retrosplenial inputs converge in the presubiculum, a key region in the navigation circuit. The authors show that near-simultaneous co-activation of retrosplenial and thalamic inputs drives supra-linear presubiculum responses, revealing a potential cellular mechanism for anchoring the brain's head direction system to external visual landmarks. Their thorough experimental approach and analyses provide convincing evidence for the cellular basis of how the brain's internal compass may be anchored to the external world, laying the groundwork for future experimental testing in vivo.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors use anatomical tracing and slice physiology to investigate the integration of thalamic (ATN) and retrosplenial cortical (RSC) signals in the dorsal presubiculum (PrS). This work will be of interest to the field, as postsubiculum is thought to be a key region for integrating internal head direction representations with external landmarks. The main result is that ATN and RSC inputs drive the same L3 PrS neurons, which exhibit superlinear summation to near-coincident inputs. Moreover, this activity can induce bursting in L4 PrS neurons, which can pass the signals LMN (perhaps gated by cholinergic input).

Strengths:

The slice physiology experiments are carefully done. The analyses are clear and convincing, and the figures and results are well composed. Overall, these results will be a welcome addition to the field.

Weaknesses:

The conclusions about the circuit-level function of L3 PrS neurons sometimes outstrip the data, and their model of the integration of these inputs is unclear. I would recommend some revision of the introduction and discussion. I also had some minor comments about the experimental details and analysis.

Specific major comments:

(1) I found that the authors' claims sometimes outstrip their data, given that there were no in vivo recordings during behavior. For example, in the abstract that their results indicate "that layer 3 neurons can transmit a visually matched HD signal to medial entorhinal cortex", and in the conclusion they state "[...] cortical RSC projections that carry visual landmark information converge on layer 3 pyramidal cells of the dorsal presubiculum". However, they never measured the nature of the signals coming from ATN and RSC to L3 PrS (or signals sent to downstream regions). Their claim is somewhat reasonable with respect to ATN, where the majority of neurons encode HD, but neurons in RSC encode a vast array of spatial and non-spatial variables other than landmark information (e.g., head direction, egocentric boundaries, allocentric position, spatial context, task history to name a few), so making strong claims about the nature of the incoming signals is unwarranted.

(2) Related to the first point, the authors hint at, but never explain, how coincident firing of ATN and RSC inputs would help anchor HD signals to visual landmarks. Although the lesion data (Yoder et al. 2011 and 2015) support their claims, it would be helpful if the proposed circuit mechanism was stated explicitly (a schematic of their model would be helpful in understanding the logic). For example, how do neurons integrate the "right" sets of landmarks and HD signals to ensure a stable anchoring? Moreover, it would be helpful to discuss alternative models of HD-to-landmark anchoring, including several studies that have proposed that the integration may (also?) occur in RSC (Page & Jeffrey, 2018; Yan, Burgess, Bicanski, 2021; Sit & Goard, 2023). Currently, much of the Discussion simply summarizes the results of the study, this space could be better used in mapping the findings to the existing literature on the overarching question of how HD signals are anchored to landmarks.

Comments on revised version:

The authors addressed all of my major points and most of my minor points in the revised submission.

Reviewer #2 (Public review):

Richevaux et al investigate how anterior thalamic (AD) and retrosplenial (RSC) inputs are integrated by single presubicular (PrS) layer 3 neurons. They show that these two inputs converge onto single PrS layer 3 principal cells. By performing dual wavelength photostimulation of these two inputs in horizontal slices, the authors show that in most layer 3 cells, these inputs summate supra-linearly. They extend the experiments by focusing on putative layer 4 PrS neurons and show that they do not receive direct anterior thalamic nor retrosplenial inputs; rather, they are (indirectly) driven to burst firing in response to strong activation of the PrS network.

This is a valuable study, which investigates an important question - how visual landmark information (possibly mediated by retrosplenial inputs) converges and integrates with HD information (conveyed by the AD nucleus of the thalamus) within PrS circuitry. The data indicate that near-coincident activation of retrosplenial and thalamic inputs leads to non-linear integration in target layer 3 neurons, thereby offering a potential biological basis for landmark + HD binding.

Main limitations relate to the anatomical annotation of 'putative' PrS L4 neurons, and to the presentation of retrosplenial / thalamic input modularity. Specifically, more evidence should be provided to convincingly demonstrate that the 'putative L4 neurons' of the PrS are not distal subicular neurons (as the authors' anatomy and physiology experiments seem to indicate). The modularity of thalamic and retrosplenial inputs could be better clarified in relation to the known PrS modularity.

Reviewer #3 (Public review):

Summary:

The authors sought to determine, at the level of individual presubiculum pyramidal cells, how allocentric spatial information from retrosplenial cortex was integrated with egocentric information from the anterior thalamic nuclei. Employing a dual opsin optogenetic approach with patch clamp electrophysiology, Richevaux and colleagues found that around three quarters of layer 3 pyramidal cells in presubiculum receive monosynaptic input from both brain regions. While some interesting questions remain (e.g. the role of inhibitory interneurons in gating the information flow and through different layers of presubiculum, this paper provides valuable insights into the microcircuitry of this brain region and the role that it may play in spatial navigation.

Strengths:

One of the main strengths of this manuscript was that the dual opsin approach allowed the direct comparison of different inputs within an individual neuron, helping to control for what might otherwise have been an important source of variation. The experiments were well-executed and the data rigorously analysed. The conclusions were appropriate to the experimental questions and were well-supported by the results. These data will help to inform in vivo experiments aimed at understanding the contribution of different brain regions in spatial navigation and could be valuable for computational modelling.

Weaknesses:

Some attempts were made to gain mechanistic insights into how inhibitory neurotransmission may affect processing in presubiuclum (e.g. figure 5) but these experiments were a little underpowered and the analysis carried out could have been more comprehensively undertaken, as was done for other experiments in the manuscript.

Comments on revised version:

The authors have addressed all of my comments and I have nothing further to add. Well done for an interesting and valuable contribution!

eLife Assessment

This study presents a useful set of experiments to explore how a salivary protein might facilitate planthopper-transmitted rice stripe virus infection by interfering with callose deposition and if fully validated, these findings would significantly advance our understanding of tripartite virus-vector-plant interactions and could be of broad interest to plant science research. The authors provide additional data supporting protein-protein interactions and clarify the transient presence of LssaCA in plants. However, the mechanistic framework remains incomplete, particularly regarding the temporal dynamics of callose function and the sustained effect of LssaCA after virus inoculation. Evidence for the tripartite interaction's functional relevance is still limited, and several critical phenotypic and biochemical details require further substantiation.

Reviewer #1 (Public review):

In this study, the authors identified an insect salivary protein LssaCA participating viral initial infection in plant host. LssaCA directly bond to RSV nucleocapsid protein and then interacted with a rice OsTLP that possessed endo-β-1,3-glucanase activity to enhance OsTLP enzymatic activity and degrade callose caused by insects feeding. The manuscript suffers from fundamental logical issues, making its central narrative highly unconvincing.

(1) These results suggested that LssaCA promoted RSV infection through a mechanism occurring not in insects or during early stages of viral entry in plants, but in planta after viral inoculation. As we all know that callose deposition affects the feeding of piercing-sucking insects and viral entry, this is contradictory to the results in Fig. S4 and Fig 2. It is difficult to understand callose functioned in virus reproduction in 3 days post virus inoculation. And authors also avoided to explain this mechanism.

(2) Missing significant data. For example, the phenotypes of the transgenic plants, the RSV titers in the transgenic plants (OsTLP OE, ostlp). The staining of callose deposition were also hard to convince. The evidence about RSV NP-LssaCA-OsTLP tripartite interaction to enhance OsTLP enzymatic activity is not enough.

(3) Figure 4a, there was the LssaCA signal in the fourth lane of pull-down data. Did MBP also bind LsssCA? The characterization of pull-down methods was rough a little bit. The method of GST pull-down and MBP pull-down should be characterized more in more detail.

Author response:

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

Reviewer #1 (Public Review):

In this study, the authors identify an insect salivary protein participating viral initiate infection in plant host. They found a salivary LssaCA promoting RSV infection by interacting with OsTLP that could degrade callose in plants. Furthermore, RSV NP bond to LssaCA in salivary glands to form a complex, which then bond to OsTLP to promote degradation of callose.

The story focus on tripartite virus-insect vector-plant interaction and is interesting. However, the study is too simple and poor-conducted. The conclusion is also overstated due to unsolid findings.

We thank the reviewer for their constructive feedback. We have conducted additional experiments to strengthen our results and conclusions as detailed below:

(1) The comparison between vector inoculation and microinjection involves multiple confounding factors that could affect the experimental results, including salivary components, RSV inoculation titers, and the precision of viral deposition. The differential outcomes could be attributed to these various factors rather than definitively demonstrating the necessity of salivary factors. Therefore, we have removed this comparison from the revised manuscript and instead focused on elucidating the specific mechanisms by which LssaCA facilitates viral infection.

(2) We conducted new experiments to assess the function of LssaCA enzymatic activity in mediating RSV infection. Additional experiments revealed that OsTLP enzymatic activity is highly pH-dependent, with increased activity as pH decreases from 7.5 to 5.0 (Fig. 3H). However, the LssaCA-OsTLP interaction at pH 7.4 significantly enhanced OsTLP enzymatic activity without requiring pH changes. These results demonstrate that LssaCA-OsTLP protein interactions are crucial for mediating RSV infection. In contrast to pH-dependent mechanisms, our study demonstrated that LssaCA's biological function in mediating RSV infection is at least partially, if not completely, independent of its enzymatic activity. We have added these new resulted into the revised manuscript (Lines 220-227). We have also added a comprehensive discussion comparing the aphid CA mechanism described by Guo et al. (2023 doi.org/10.1073/pnas.2222040120) with our findings in the revised manuscript (Lines 350-371).

(3) We have repeated majority of callose deposition experiments, providing clearer images (Figures 5-6). In addition to aniline blue staining, we quantified callose concentrations using a plant callose ELISA kit to provide more precise measurements (Figure 5A, I, 6A, C and S8A). We utilized RT-qPCR to measure callose synthase expression in both feeding and non-feeding areas, confirming that callose synthesis was induced specifically in feeding regions, leading to localized callose deposition (Figures 5D-G and S8B-E). For sieve plate visualization, we examined longitudinal sections, which revealed callose deposition in sieve plates during SBPH feeding and RSV infection (Figure S7).

(4) We generated OsTLP mutant rice seedlings (ostlp) and use this mutant to directly demonstrate that LssaCA mediates callose degradation in planta through enhancement of OsTLP enzymatic activity (Lines 288-302 and Figure 6).

(5) We produced LssaCA recombinant proteins in sf9 cells to ensure full enzymatic activity and constructed a comprehensive CA mutant protein, in which all seven residues constituting the enzymatic active center mutated (LssaCA^H111D,LssaCA^N139H,LssaCA^H141D, LssaCA^H143D, LssaCA^E153H, LssaCA^H166D, LssaCA^T253E) (Fig. S1B). This LssaCA mutant protein demonstrated complete loss of enzymatic activity (Fig. 1C).

Major comments:

(1) The key problem is that how long the LssCA functioned for in rice plant. Author declared that LssCA had no effect on viral initial infection, but on infection after viral inoculation. It is unreasonable to conclude that LssCA promoted viral infection based on the data that insect inoculated plant just for 2 days, but viral titer could be increased at 14 days post-feeding. How could saliva proteins, which reached phloem 12-14 days before, induce enough TLP to degrade callose to promote virus infection? It was unbelievable.

We appreciate your insightful comment and acknowledge that our initial description may have been unclear. We agree that salivary proteins would not present in plant tissues for two weeks post-feeding or post-injection. Our intention was to clarify that when salivary proteins enhance RSV infection, this initial enhancement leads to sustained high viral loads. We measured viral burden at 14 days post-feeding or post-injection because this is the common measurement time point when viral titers are sufficiently high for reliable detection by qRT-PCR or western blotting. We have clarified this rationale in the revised manuscript (Lines 155-157).

To determine the actual persistence of LssaCA in plant tissues, we conducted additional experiments where insects were allowed to feed on a defined aera of rice seedlings for two days. We then monitored LssaCA protein levels at 1 and 3 days after removing the insects. Western blotting analysis revealed that LssaCA protein levels decreased post-feeding and remained detectable at 3 days post-feeding. These results are presented in Figure 2H and described in detail in Lines 184-193.

(2) Lines 110-116 and Fig. 1, the results of viruliferous insect feeding and microinjection with purified virus could not conclude the saliva factor necessary of RSV infection, because these two tests are not in parallel and comparable. Microinjection with salivary proteins combined with purified virus is comparable with microinjection with purified virus.

We thank the reviewer’s insightful comment. We agree that “the results of viruliferous insect feeding and microinjection with the purified virus could not conclude the saliva factor necessary of RSV infection”. However, due to the technical difficulty in collecting sufficient quantities of salivary proteins to conduct the microinjection experiment, we have removed these results from the revised manuscript.

(3) The second problem is how many days post viruliferous insect feeding and microinjection with purified virus did author detect viral titers? in Method section, authors declared that viral titers was detected at 7-14 days post microinjection. Please demonstrate the days exactly.

We thank the reviewer’s insightful comment. We typically measured RSV infection levels at both 7- and 14-days post-microinjection. However, since the midrib microinjection experiments have been removed from the revised manuscript, this methodology has also been removed accordingly.

(4) The last problem is that how author made sure that the viral titers in salivary glands of insects between two experiments was equal, causing different phenotype of rice plant. If not, different viral titers in salivary glands of insects between two experiments of course caused different phenotype of rice plant.

We thank the reviewer’s comment. When we compared the effects of LssaCA deficiency on RSV infection of rice plants, we have compared the viral titers in the insect saliva and salivary glands. The results indicated that the virus titers in both tissues have not changed by LssaCA deficiency, suggesting that the viruses inoculated into rice phloem by insects of different treatments were comparable. Please refer to the revised manuscript Figures 2D-G and Lines 161-173.

(5) The callose deposition in phloem can be induced by insect feeding. In Fig. 5H, why was the callose deposition increased in the whole vascular bundle, but not phloem? Could the transgenic rice plant directional express protein in the phloem? In Fig. 5, why was callose deposition detected at 24 h after insect feeding? In Fig. 6A, why was callose deposition decreased in the phloem, but not all the cells of the of TLP OE plant? Also in Fig.6A and B, expression of callose synthase genes was required.

We thank the reviewer for these insightful comments.

(1) Figure 5. The callose deposition increased in multiple cells within the vascular bundle, including sieve tubes, parenchymatic cells, and companion cells. While callose deposition was detected in other parts of the vascular bundle, no significant differences were observed between treatments in these regions, indicating that in response to RSV infection and other treatments, altered callose deposition mainly occurred in phloem cells. Please refer to the revised 5B, 5J, 6B, and 6D.

(2) Transgenic plant expression. The OsTLP-overexpressing transgenic rice plants express TLP proteins in various cells under the control of CaMV 35S promoter, rather than being directionally expressed in the phloem. However, since TLP proteins are secreted, they are potentially transported and concentrated in the phloem where they can degrade callose.

(3) Figure 5. The 24-hour time point for callose deposition detection was selected based on established protocols from previous studies. According to Hao et al. (Plant Physiology 2008), callose deposition increased during the first 3 days of planthopper infestation and decreased after 4 days. Additionally, Ellinger and Voigt (Ann Bot 2014) demonstrated that callose visualization typically begins 18-24 hours after treatment, making 24 hours an optimal detection time point.

(4) Figure 6, Phloem-specific changes. Similar to Figure 5, while callose deposition was detected in other parts of vascular bundle, significant differences between treatments were mainly observed in phloem cells, indicating that RSV infection specifically affects callose deposition in phloem tissue.

(5) Callose synthase gene expression. We performed RT-qPCR analysis to measure the expression levels of callose synthase genes. The results indicated that OsTLP overexpression did not significantly alter the mRNA levels of these genes, regardless of RSV infection status in SBPH.

Reviewer #2 (Public Review):

There is increasing evidence that viruses manipulate vectors and hosts to facilitate transmission. For arthropods, saliva plays an essential role for successful feeding on a host and consequently for arthropod-borne viruses that are transmitted during arthropod feeding on new hosts. This is so because saliva constitutes the interaction interface between arthropod and host and contains many enzymes and effectors that allow feeding on a compatible host by neutralizing host defenses. Therefore, it is not surprising that viruses change saliva composition or use saliva proteins to provoke altered vector-host interactions that are favorable for virus transmission. However, detailed mechanistic analyses are scarce. Here, Zhao and coworkers study transmission of rice stripe virus (RSV) by the planthopper Laodelphax striatellus. RSV infects plants as well as the vector, accumulates in salivary glands and is injected together with saliva into a new host during vector feeding.

The authors present evidence that a saliva-contained enzyme - carbonic anhydrase (CA) - might facilitate virus infection of rice by interfering with callose deposition, a plant defense response. In vitro pull-down experiments, yeast two hybrid assay and binding affinity assays show convincingly interaction between CA and a plant thaumatin-like protein (TLP) that degrades callose. Similar experiments show that CA and TLP interact with the RSV nuclear capsid protein NT to form a complex. Formation of the CA-TLP complex increases TLP activity by roughly 30% and integration of NT increases TLP activity further. This correlates with lower callose content in RSV-infected plants and higher virus titer. Further, silencing CA in vectors decreases virus titers in infected plants.

(1) Interestingly, aphid CA was found to play a role in plant infection with two non-persistent non-circulative viruses, turnip mosaic virus and cucumber mosaic virus (Guo et al. 2023 doi.org/10.1073/pnas.2222040120), but the proposed mode of action is entirely different.

We appreciate the reviewer’s insightful comment and have carefully examined the cited publication. The study by Guo et al. (2023) elucidates a distinct mechanism for aphid-mediated transmission of non-persistent, non-circulative viruses (turnip mosaic virus and cucumber mosaic virus). In their model, aphid-secreted CA-II in the plant cell apoplast leads to H⁺ accumulation and localized acidification. This trigger enhanced vesicle trafficking as a plant defense response, inadvertently facilitating virus translocation from the endomembrane system to the apoplast.

In contrast to these pH-dependent mechanisms, our study demonstrated that LssaCA’s biological function in mediating RSV infection is, if not completely, at least partially independent of its enzymatic activity. We performed additional experiments to reveal that OsTLP enzymatic activity is highly pH-dependent and exhibits increased enzymatic activity as pH decreases from 7.5 to 5.0 (Fig. 3H); however, the LssaCA-OsTLP interaction occurring at pH 7.4 significantly enhanced OsTLP enzymatic activity without any change in buffer pH (Fig. 3G). These results demonstrate the crucial importance of LssaCA-OsTLP protein interactions, rather than enzymatic activity alone, in mediating RSV infection.

We have incorporated these new experimental results and added a comprehensive discussion comparing the aphid CA mechanism described by Guo et al. (2023) with our findings in the revised manuscript. Please refer to Figures 3G-H, Lines 220-227 and 350-371 for detailed information.

(2) While this is an interesting work, there are, in my opinion, some weak points. The microinjection experiments result in much lower virus accumulation in rice than infection by vector inoculation, so their interpretation is difficult.

We acknowledge the reviewer's concern regarding the lower virus accumulation observed in microinjection experiments compared to vector-mediated inoculation. We have removed these experiments from the revised manuscript. To address the core question raised by these experiments, we have conducted new experiments that directly demonstrate the importance of LssaCA-OsTLP protein-protein interactions in mediating RSV infection. These results demonstrate the crucial importance of LssaCA-OsTLP protein interactions, rather than enzymatic activity alone, in mediating RSV infection. Additionally, we have incorporated a comprehensive discussion examining carbonic anhydrase activity, pH homeostasis, and viral infection. Please refer to the detailed experimental results and discussion in the sections mentioned in our previous response (Figures 3G-H, Lines 220-227 and 350-371).

(3) Also, the effect of injected recombinant CA protein might fade over time because of degradation or dilution.

We appreciate the reviewer’s insightful comment. This is indeed a valid concern that could affect the interpretation of microinjection results. To address the temporal dynamics of CA protein presence in planta, we conducted time-course experiments to monitor the retention of naturally SBPH-secreted CA proteins in rice plants. Our analysis at 1- and 3- days post-feeding (dpf) revealed that CA protein levels decreased progressively following SBPH feeding, but could also been detected at 3dpf (Fig. 2H). Please refer to Figures 2H and lines 184-193 for detailed information.

(4) The authors claim that enzymatic activity of CA is not required for its proviral activity. However, this is difficult to assess because all CA mutants used for the corresponding experiments possess residual activity.

We appreciate the reviewer’s insightful comment. We constructed a comprehensive CA mutant protein in which all seven residues constituting the enzymatic active center mutated (LssaCA^H111D, LssaCA^N139H, LssaCA^H141D, LssaCA^H143D, LssaCA^E153H, LssaCA^H166D, LssaCA^T253E) (Fig. S1B). This LssaCA mutant protein demonstrated complete loss of enzymatic activity (Fig. 1C). However, since we have removed the recombinant CA protein microinjection experiments from the revised manuscript, we lack sufficient direct evidence to definitively demonstrate that CA enzymatic activity is dispensable for its proviral function. To address the core question raised by these experiments, we have conducted new experiments that provide direct evidence for the importance of LssaCA-OsTLP protein-protein interactions in mediating RSV infection. Additionally, we have incorporated a comprehensive discussion examining carbonic anhydrase activity, pH homeostasis, and viral infection. Please refer to the detailed experimental results and discussion in the sections mentioned in our previous response (Figures 3G-H, Lines 220-227 and 350-371).

(5) It remains also unclear whether viral infection deregulates CA expression in planthoppers and TLP expression in plants. However, increased CA and TLP levels could alone contribute to reduced callose deposition.

We have compared LssaCA mRNA levels in RSV-free and RSV-infected L.striatellus salivary glands, which indicated that RSV infection does not significantly affect LssaCA expression (Figure 1J). By using RSV-free and RSV-infected L.striatellus to feed on rice seedlings, we clarified that RSV infection does not affect TLP expression in plants (Figure 5H).

Reviewer #1: (Recommendations For The Authors):

Other comments:

(1) Most data proving viral infection and LssaCA expression were derived from qPCR assays. Western blot data are strongly required to prove the change at the protein level.

We agree that western blot data are required to prove the change at the protein level. In the revised manuscript, we have added western-blotting results (Figures 1F, 1I, 2C, 2J, and S6).

(2) Line 145, data that LssaCA was significantly downregulated should be shown.

Thank you and the data has been added to the revised manuscript. Please refer to Line 165 and Figure 2D.

(3) Lines 159-161, how did authors assure that the dose of recombinant LssCA was closed to the release level of insect feeding, but not was excessive? How did author exclude the possibility of upregulated RSV titer caused by excessive recombinant LssCA?

We appreciate this important concern regarding dosage controls. While microinjection of recombinant proteins typically yields viral infection levels significantly lower than those achieved through natural insect feeding, higher protein concentrations are often required to achieve high viral infection levels. In this experiment, we compared RSV infection levels following microinjection of BSA+RSV versus LssaCA+RSV, with the expectation that any observed upregulation in RSV titer would be specifically attributable to recombinant LssaCA rather than excessive protein dosing. However, given the low RSV infection levels observed with viral microinjection, we have removed their corresponding results from the revised manuscript.

(4) Lines 124-125, recombinantly expressed LssaCA protein should be underlined, but not the LssaCA protein itself.

We have clearly distinguished recombinantly expressed LssaCA from endogenous LssaCA protein throughout the manuscript, ensuring that all references to recombinant proteins are properly labeled as such.

(5) LssaCA expression in salivary glands of viruliferous and nonviruliferous insects is required. LssaCA accumulation in rice plant exposed to viruliferous and nonviruliferous insects is also required.

We have measured LssaCA mRNA levels in salivary glands of viruliferous and nonviruliferous insects (Figure 1J), and protein levels in rice plant exposed to viruliferous and nonviruliferous insects (Figure 1I).

(6) Fig. 4G, the enzymatic activities of OsTLP were too low compared with that in Fig. 4E and Fig. 7E. Why did the enzymatic activities of the same protein show so obvious difference?

We apologize for the error in Fig. 4G. The original data presented relative fold changes between OsTLP+BSA and OsTLP+LssaCA treatment, with OsTLP+BSA normalized to 1.0 and OsTLP+LssaCA values expressed as fold changes relative to this baseline. However, the Y-axis was incorrectly labeled as “β-1,3-glucanase (units mg^-1)”, which suggested absolute enzymatic activity values. We have now corrected the figure (revised Figure 3G) to display the actual absolute enzymatic activity values with the appropriate Y-axis label “β-1,3-glucanase (units mg^-1)”.

(7) Fig. 7E, was the LssaCA + NP and LssaCA + GST quantified?

Yes, all proteins were quantified, and enzymatic activity values were calculated and expressed as units per milligram of proteins (units mg^-1).

Minor comments:

(1) The keywords: In fact, the LssaCA functioned during initial viral infection in plant, but not viral horizontal transmission.

We appreciate the reviewer’s insightful comment. We have revised the manuscript title to “Rice stripe virus utilizes an Laodelphax striatellus salivary carbonic anhydrase to facilitate plant infection by direct molecular interaction” and changed the keyword from “viral horizontal transmission” to “viral infection of plant”.

(2) Fig. 2A, how about testes? Was this data derived from female insects? Fig. 2C, is the saliva collected from nonviruliferous insects? Fig. 2E, what is the control?

We appreciate the reviewer’s insightful comments.

(1) Fig. 2A: The data present mean and SD calculated from three independent experiments, with 5 tissue samples per experiment. Since 3^rd instar nymphs were used for feeding experiments in this study, we also used 3^rd instar RSV-free nymphs to measure gene expression in guts, salivary glands and fat bodies. R-body represents the remaining body after removing these tissues. Female insects were used to measure gene expression in ovaries, and gene expression in testes was also added. We have added this necessary information to the revised manuscript (please refer to new Figure 1F and Lines 402-403).

(2) Fig. 2C: Yes, saliva was collected from nonviruliferous insects.

(3) Fig. 2E: The control consisted of 100 mM PBS, as described in the experimental section (Lines 643-644): “A blank control consisted of 2 mL of 100 mM PBS (pH 7.0) mixed with 1 mL of 3 mM p-NPA.” In the revised manuscript, we recombinantly expressed LssaCA and its mutant proteins in both sf9 cells and E.coli. Therefore, we have used the mutant proteins as controls to demonstrate specific enzymatic activity. Please refer to Figure 1C, Lines 115-122 and 621-635 for detailed information.

(3) Some figure labeling appeared unprofessional. For example, "a-RSV", "loading" in Fig. 1, "W-saliva", "G-saliva" in Fig. 2, and so on, the related explanations were absent.

We appreciate the reviewer’s insightful comments. We have thoroughly reviewed all figures to ensure professional labels. Specifically, we have:

(1) Used proper protein names to label western blots and clearly explained the antibodies used for protein detection.

(2) Provided comprehensive explanations for all abbreviations used in figures within the corresponding figure legends.

(3) Ensured consistent and clear labeling throughout all figures.

Please refer to the revised Figures 1-3 for these corrections.

(4) Lines 83-84, please cite references on callose preventing viral movement. I do not think the present references were relevant.

We have added a more relevant reference (Yue et al., 2022, Line 82), which revealed that palmitoylated γb promotes virus cell-to-cell movement by interacting with NbREM1 to inhibit callose deposition at plasmodesmata.

(5) The background of transgenic plants of OsTLP OE should be characterized. And the overexpression of OsTLP should be shown. Which generation of OsTLP OE did authors use?

The background of transgenic plants of OsTLP OE and its generation used have been shown in the “Materials and methods” section (Line 782-786) and has been mentioned in the main text (Line 214). T² lines have been selected for further analysis (Line 789).

(6) Fig. 5A, the blank, which derived from plants without exposure to insect, was absent.

We appreciate the reviewer’s insightful comments. We have added the non- fed control in the revised Figure 5A-C.

(7) Fig. 7A, the nonviruruliferous insects were required to serve as a control.

Immunofluorescence localization of RSV and LssaCA in uninfected L. striatellus salivary glands have been added to the revised manuscript (Figure S2).

(8) The manuscript needs English language edit.

The manuscript has undergone comprehensive English language editing to improve clarity, grammar, and overall readability.

Reviewer #2 (Recommendations For The Authors):

(1) The first experiment compares vector inoculation vs microinjection of RSV in tissue. I am not sure that your claim (saliva factors are necessary for inoculation) holds, because the vector injects RSV directly into the phloem, whereas microinjection is less precise and you cannot control where exactly the virus is deposed. However, virus deposited in other tissues than the phloem might not replicate, and indeed you observe, compared to natural vector inoculation, highly reduced virus titers.

We appreciate the reviewer’s insightful comments. We agree that the comparison between vector inoculation and microinjection involves multiple confounding factors that could affect the experimental results, including salivary components, RSV inoculation titers, and the precision of viral deposition. As the reviewer correctly points out, the differential outcomes could be attributed to these various factors rather than definitively demonstrating the necessity of salivary factors. Therefore, we have removed this comparison from the revised manuscript and instead focused on elucidating the specific mechanisms by which LssaCA facilitates viral infection.

(2) Next the authors show that a carbonic anhydrase (CA) that they previously detected in saliva is functional and secreted into rice. I assume this is done with non-infected insects, but I did not find the information. Silencing the CA reduces virus titers in inoculated plants at 14 dpi, but not in infected planthoppers. At 1 dpi, there is no difference in RSV titer in plants inoculated with CA silenced planthoppers or control hoppers. To see a direct effect of CA in virus infection, purified virus is injected together with a control protein or recombinant CA into plants. At 14 dpi, there is about double as much virus in the CA-injected plants, but compared to authentic SBPH inoculation, titers are 20,000 times lower. Actually, I believe it is not very likely that the recombinant CA is active or present so long after initial injection.

We appreciate the reviewer’s insightful comments.

(1) Our previous study identified the CA proteins from RSV-free insects. We have added this information to the revised manuscript (Line 110).

(2) We acknowledge the reviewer's concern regarding the lower virus accumulation observed in microinjection experiments compared to vector-mediated inoculation. We have removed these experiments from the revised manuscript and instead focused on elucidating the specific mechanisms by which LssaCA facilitates viral infection.

(3) We didn’t intend to suggest that LssaCA proteins presented for 14 days post-injection. We measured viral titers at 14 days post-feeding or post-injection because this is the common measurement time point when viral titers are sufficiently high for reliable detection by RT-qPCR or western blotting. We have clarified this rationale in the revised manuscript (Lines 155-157). To determine the actual persistence of LssaCA in plant tissues, we monitored LssaCA protein levels at 1 and 3 dpf. Western blotting analysis revealed that LssaCA protein levels decreased post-feeding and remained detectable at 3 dpf. These results are presented in Figure 2H and described in detail in Lines 184-193.

(3) Then the authors want to know whether CA activity is required for its proviral action and single amino acid mutants covering the putative active CA site are created. The recombinant mutant proteins have 30-70 % reduced activity, but none of them has zero activity. When microinjected together with RSV into plants, RSV replication is similar as injection with wild type CA. Since no knock-out mutant with zero activity is used, it is difficult to judge whether CA activity is unimportant for viral replication, as claim the authors.

We appreciate the reviewer’s insightful comment. We constructed a comprehensive CA mutant protein in which all seven residues constituting the enzymatic active center mutated (LssaCA^H111D, LssaCA^N139H, LssaCA^H141D, LssaCA^H143D, LssaCA^E153H, LssaCA^H166D, LssaCA^T253E) (Fig. S1B). This LssaCA mutant protein demonstrated complete loss of enzymatic activity (Fig. 1C). However, since we have removed the recombinant CA proteins microinjection experiments from the revised manuscript, we lack sufficient direct evidence to definitively demonstrate that CA enzymatic activity is dispensable for its proviral function. To address the core question raised by these experiments, we have conducted new experiments that provide direct evidence for the importance of LssaCA-OsTLP protein-protein interactions in mediating RSV infection. Additionally, we have incorporated a comprehensive discussion examining carbonic anhydrase activity, pH homeostasis, and viral infection. Please refer to the detailed experimental results and discussion in the sections mentioned in our previous response (Figures 3G-H, Lines 220-227 and 350-371).

(4) Next a yeast two hybrid assay reveals interaction with a thaumatin-like rice protein (TLP). It would be nice to know whether you detected other interacting proteins as well. The interaction is confirmed by pulldown and binding affinity assay using recombinant proteins. The kD is in favor of a rather weak interaction between the two proteins.

We have added a list of rice proteins that potentially interact with LssaCA (Table S1) and have measured interactions with additional proteins (unpublished data). Despite the relatively weak binding affinity, the functional significance of the LssaCA-OsTLP interaction in enhancing TLP enzymatic activity is substantial.

(5) Then the glucanase activity of TLP is measured using recombinant TLP-MBP or in vivo expressed TLP. It is not clear to me which TLP is used in Fig. 4G (plant-expressed or bacteria-expressed). If it is plant-expressed TLP, why is its basic activity 10 times lower than in Fig. 4F?

Fig. 4G is the Fig. 3G in the revised manuscript. A E. coli-expressed TLP protein has been used. We apologize for the error in our original Fig. 4G. The original data presented relative fold changes between OsTLP+BSA and OsTLP+LssaCA treatment, with OsTLP+BSA normalized to 1.0 and OsTLP+LssaCA values expressed as fold changes relative to this baseline. However, the Y-axis was incorrectly labeled as “β-1,3-glucanase (units mg^-1)”, which suggested absolute enzymatic activity values. We have now corrected the figure to display the actual absolute enzymatic activity values with the appropriate Y-axis label “β-1,3-glucanase (units mg^-1)”.

(6) There is also a discrepancy in the construction of the transgenic rice plants: did you use TLP without signal peptide or full length TLP? If you used TLP without signal peptide, you should explain why, because the wild type TLP contains a signal peptide.

We cloned the full-length OsTLP gene including the signal peptide sequence (Line 782 in the revised manuscript).

(7) The authors find that CA increases glucanase activity of TLP. Next the authors test callose deposition by aniline blue staining. Feeding activity of RSV-infected planthoppers induces more callose deposition than does feeding by uninfected insects. In the image (Fig. 5A) I see blue stain all over the cell walls of xylem and phloem cells. Is this what the authors expect? I would have expected rather a patchy pattern of callose deposition on cell walls. Concerning sieve plates, I cannot discern any in the image; they are easier to visualize in longitudinal sections than in transversal section as presented here.

We appreciate the reviewer’s insightful comment.

(1) Callose deposition pattern: While callose deposition was detected in other parts of the vascular bundle, significant differences between treatments were mainly observed in phloem cells, indicating that phloem-specific callose deposition is the primary response to RSV infection and SBPH feeding (Figures 5B and 5J).

(2) Sieve plate visualization: We have examined longitudinal sections to visualize sieve plates, which revealed callose deposition in sieve plates during SBPH feeding and RSV infection (Figure S7).

(3) Quantitative analysis: In addition to aniline blue staining, we quantified callose concentrations using a plant callose ELISA kit to provide more precise measurements (Figure 5A, 5I and S8A).

(4) Gene expression analysis: We utilized RT-qPCR to measure callose synthase expression in both feeding and non-feeding areas, confirming that callose synthesis was induced specifically in feeding regions, leading to localized callose deposition (Figures 5D-H).

These experimental results collectively demonstrate that RSV infection induces enhanced callose synthesis and deposition, with this response occurring primarily in phloem cells, including sieve plates, within feeding sites and their immediate vicinity.

(8) I do not quite understand how you quantified callose deposition (arbitrary areas?) with ImageJ. Please indicate in detail the analysis method.

We have added more detailed information for the methods to quantify callose deposition (Lines 673-678).

(9) More callose content is also observed by a callose ELISA assay of tissue extracts and supported by increased expression of glucanase synthase genes. Did you look whether expression of TLP is changed by feeding activity and RSV infection? Silencing CA in planthoppers increases callose deposition, which is inline with the observation that CA increases TLP activity.

We measured OsTLP expression following feeding by RSV-free or RSV-infected SBPH and found that gene expression was not significantly affected by either insect feeding or RSV infection. These results have been added to the revised manuscript (Lines 275-277 and Figure 5H).

(10) Next, callose is measured after feeding of RSV-infected insects on wild type or TLP-overexpressing rice. Less callose deposition (after 2 days) and more virus (after 14 days) is observed in TLP overexpressors. I am missing a control in this experiment, that is feeding of uninfected insects on wild type or TLP overexpressing rice, where I would expect intermediate callose levels.

We appreciate the reviewer’s insightful comment and fully agree with the prediction. In the revised manuscript, we have constructed ostlp mutant plants and conducted additional experiments to further clarify how callose deposition is regulated by insect feeding, RSV infection, LssaCA levels, and OsTLP expression. Specifically: 

(1) Both SBPH feeding and RSV infection induce callose deposition, with RSV-infected insect feeding resulting in significantly higher callose levels compared to RSV-free insect feeding (Fig. 5A-C).

(2) LssaCA enhances OsTLP enzymatic activity, thereby promoting callose degradation (Fig. 5I-K).

(3) OsTLP-overexpressing (OE) plants exhibit lower callose levels than wild-type (WT) plants, while ostlp mutant plants show higher callose levels than WT (Fig. 6A-B).

(4) In ostlp knockout plants, LssaCA no longer affects callose levels, indicating that OsTLP is required for LssaCA-mediated regulation of callose (Fig. 6C-D).

These additional data address the reviewer’s concern and support the conclusion that OsTLP plays a central role in modulating callose levels in response to RSV infection and insect feeding.

(11) Next the authors test for interaction between virions and CA. Immunofluorescence shows that RSV and CA colocalize in salivary glands; in my opinion, there is partial and not complete colocalization (Fig. 7A).

We agree with the reviewer’s observation. CA is primarily produced in the small lobules of the principal salivary glands, while RSV infects nearly all parts of the salivary glands. In regions where RSV and CA colocalize within the principal glands, the CA signal appears sharper than that of RSV, likely due to the relatively higher abundance of CA compared to RSV in these areas. This may explain the partial, rather than complete, colocalization observed in our original Figure 7A. In the revised manuscript, please refer to Figure 1A.

(12) Pulldown experiments with recombinant RSV NP capsid protein and CA confirm interaction, binding affinity assays indicate rather weak interaction between CA and NP. Likewise in pull-down experiments, interaction between NP, CA and TLP is shown. Finally, in vitro activity assays show that activity of preformed TLP-CA complexes can be increased by adding NP; activity of TLP alone is not shown.

We performed two independent experiments to confirm the influence on TLP enzymatic activity by LssaCA or by the LssaCA-RSV NP complex. In the first experiment, we compared the enhancement of TLP activity by LssaCA using TLP alone as a control (Figure 3G). In the second experiment examining the LssaCA-RSV NP complex effect on TLP activity, we used the LssaCA-TLP combination as the baseline control rather than TLP alone (Figure 4B), since we had already established the LssaCA enhancement effect in the previous experiment.

(13) For all microscopic acquisitions, you should indicate the exact acquisition conditions, especially excitation and emission filter settings, kind of camera used and objectives. Use of inadequate filters or of a black & white camera could for example be the reason why you observe a homogeneous cell wall label in the aniline blue staining assays. Counterstaining cell walls with propidium iodide might help distinguish between cell wall and callose label.

Thank you for your insightful suggestions. We have added the detailed information to the revised manuscript (Lines 656-659 and 673-678).

(14) You should provide information whether CA is deregulated in infected planthoppers, as this could also modify its mode of action.\

We have compared LssaCA mRNA levels in RSV-free and RSV-infected L.striatellus salivary glands. The results indicated that RSV infection does not significantly affect LssaCA expression (Figure 1J).

(15) You should show purity of the proteins used for affinity binding measurements.

We have included SDS-PAGE results of purified proteins in the revised manuscript (Figure S3).

(16) L 39: Not all arboviruses are inoculated into the phloem.

Thank you. We have revised this description (Lines 40, 73, 95 and 97).

(17) L 76: Watery saliva is also injected in epidermis and mesophyll cells.

Thank you. We have revised this description (Line 73).

(18) L 79: What do you mean by "avirulent gene"?

Thank you for your valuable comments. We have revised this description as “certain salivary effectors may be recognized by plant resistance proteins to induce effector-triggered immunity”. Please refer to Lines 76-77 for detail.

(19) L 128: Please add delivery method.

Thank you. We have added the delivery methods (Line 134).

(20) L 195: Please explain "MST".

Explained (Line 124). Thank you.

(21) L 203: Please add the plant species overexpressing TLP.

Added (Line 214). Thank you.

(22) L 213: Callose deposition has also a role against phloem-feeding insects.

We appreciate the reviewer’s insight comment. We have added this information to the revised manuscript (Line 252).

(23) L 626: What is a "mutein"?

"mutein" is an abbreviation for mutant proteins. Since the recombinant protein microinjection experiments have been removed from the revised manuscript, the term “mutein” has also been removed. For all other instances, we now use the full term “mutant proteins”.

(24) Fig. 1E: what is "loading"? You should rather show here and elsewhere (or add to supplement) complete protein gels and Western blot membranes and not only bands of interest.

Thank you for your valuable suggestion. Although Figure 1E has been removed from the revised manuscript, we have carefully reviewed all figures to ensure that the term “loading” has been replaced with the specific protein names where appropriate.

(25) Fig. 2C: Please indicate which is the blot and which is the silver stained gel and add mass markers in kDa to the silver stained gel.

Thank you for your suggestion. We have revised figure to include labeled silver-stained gels with indicated molecular weight markers (Figure 1H in the revised manuscript).

eLife Assessment

This paper presents an analysis of demography and selection from whole-genome sequencing of 40 Faroese, with data that are useful beyond the study region. Much of the analysis is solid, but a more fine-scale analysis of demographic history could have led to more interesting findings. In addition, there are concerns about the selection analyses, given the special nature of the studied population and sampling scheme. Finally, lack of data availability limits the broader value of the paper.

Reviewer #1 (Public review):

Summary:

The paper reports an analysis of whole-genome sequence data from 40 Faroese. The authors investigate aspects of demographic history and natural selection in this population. The key findings are that the Faroese (as expected) have a small population size and are broadly of Northwest European ancestry. Accordingly, selection signatures are largely shared with other Northwest European populations, although the authors identify signals that may be specific to the Faroes. Finally, they identify a few predicted deleterious coding variants that may be enriched in the Faroes.

Strengths:

The data are appropriately quality-controlled and appear to be of high quality. Some aspects of the Faroese population history are characterized, in particular, by the relatively (compared to other European populations) high proportion of long runs of homozygosity, which may be relevant for disease mapping of recessive variants. The selection analysis is presented reasonably, although as the authors point out, many aspects, for example differences in iHS, can reflect differences in demographic history or population-specific drift and thus can't reliably be interpreted in terms of differences in the strength of selection.

Weaknesses:

The main limitations of the paper are as follows:

(1) The data are not available. I appreciate that (even de-identified) genotype data cannot be shared; however, that does substantially reduce the value of the paper. Minimally, I think the authors should share summary statistics for the selection scans, in line with the standard of the field.

(2) The insight into the population history of the Faroes is limited, relative to what is already known (i.e., they were settled around 1200 years ago, by people with a mixture of Scandinavian and British ancestry, have a small effective population size, and any admixture since then comes from substantially similar populations). It's obvious, for example, that the Faroese population has a smaller bottleneck than, say, GBR.

More sophisticated analyses (for example, ARG-based methods, or IBD or rare variant sharing) would be able to reveal more detailed and fine-scale information about the history of the populations that is not already known. PCA, ADMIXTURE, and HaplotNet analysis are broad summaries, but the interesting questions here would be more specific to the Faroes, for example, what are the proportions of Scandinavian vs Celtic ancestry? What is the date and extent of sex bias (as suggested by the uniparental data) in this admixture? I think that it is a bit of a missed opportunity not to address these questions.

(3) I don't really understand the rationale for looking at HLA-B allele frequencies. The authors write that "ankylosing spondylitis (AS) may be at a higher prevalence in the Faroe Islands (unpublished data), however, this has not been confirmed by follow-up epidemiological studies". So there's no evidence (certainly no published evidence) that AS is more prevalent, and hence nothing to explain with the HLA allele frequencies?

Reviewer #2 (Public review):

In this paper, Hamid et al present 40 genomes from the Faroe Islands. They use these data (a pilot study for an anticipated larger-scale sequencing effort) to discuss the population genetic diversity and history of the sample, and the Faroes population. I think this is an overall solid paper; it is overall well-polished and well-written. It is somewhat descriptive (as might be expected for an explorative pilot study), but does make good use of the data.

The data processing and annotation follows a state-of-the-art protocol, and at least I could not find any evidence in the results that would pinpoint towards bioinformatic issues having substantially biased some of the results, and at least preliminary results lead to the identification of some candidate disease alleles, showing that small, isolated cohorts can be an efficient way to find populations with locally common, but globally rare disease alleles.

I also enjoyed the population structure analysis in the context of ancient samples, which gives some context to the genetic ancestry of Faroese, although it would have been nice if that could have been quantified, and it is unfortunate that the sampling scheme effectively precludes within-Faroes analyses.

I am unfortunately quite critical of the selection analysis, both on a statistical level and, more importantly, I do not believe it measures what the authors think it does.

Major comments:

(1) Admixture timing/genomic scaling/localization:<br /> As the authors lay out, the Faroes were likely colonized in the last 1,000-1,500 years, i.e., 40-60 generations ago. That means most genomic processes that have happened on the Faroese should have signatures that are on the order of ~1-2cM, whereas more local patterns likely indicate genetic history predating the colonization of the islands. Yet, the paper seems to be oblivious to this (to me) fascinating and somewhat unique premise. Maybe this thought is wrong, but I think the authors miss a chance here to explain why the reader should care beyond the fact that the small populations might have high-frequency risk alleles and the Faroes are intrinsically interesting, but more importantly, it also makes me think it leads to some misinterpretations in the selection analysis

(2) ROH:<br /> Would the sampling scheme impact ROH? How would it deal with individuals with known parental coancestry? As an example of what I mean by my previous comment, 1MB is short enough in that I would expect most/many 1MB ROH-tracts to come from pedigree loops predating the colonization of the Faroes. (i.e, I am actually quite surprised that there isn't much more long ROH, which makes me wonder if that would be impacted by the sampling scheme).

(3) Selection scan:

We are talking about a bottlenecked population that is recently admixed (Faroese), compared to a population (GBR) putatively more closely related to one of its sources. My guess would be that selection in such a scenario would be possibly very hard to detect, and even then, selection signals might not differentiate selection in Faroese vs. GBR, but rather selection/allele frequency differences between different source populations. I think it would be good to spell out why XP-EHH/iHS measures selection at the correct time scale, and how/if these statistics are expected to behave differently in an admixed population.

(4) Similarly, for the discussion of LCT, I am not convinced that the haplotypes depicted here are on the right scale to reflect processes happening on the Faroes. Given the admixture/population history, it at the very least should be discussed in the context of whether the 13910 allele frequency on the Faroes is at odds with what would be expected based on the admixture sources.

(5) I am lacking information to evaluate the procedure for turning the outliers into p-values. Both iHS and XP-EHH are ratio statistics, meaning they might be heavy-tailed if one is not careful, and the central limit theorem may not apply. It would be much easier (and probably sufficient for the points being made here) to reframe this analysis in terms of empirical outliers.

(6) Oldest individual predating gene flow: It seems impossible to make any statements based on a single individual. Why is it implausible that this person (or their parents), e.g., moved to the Faroes within their lifetime and died there?